introduction to epidemiology (2011, mc-graw-hill_open university press)

Introduction to
Epidemiology
Second Edition
Understanding Public Health
Ilona Carneiro & Natasha Howard
Lucianne Bailey, Katerina Vardulaki,
Julia Langham & Daniel Chandramohan
IntroductiontoEpidemiologyCarneiro&Howard
Second
Edition
www.openup.co.uk
Cover design Hybert Design • www.hybertdesign.com
Introduction to Epidemiology
Second Edition
“Well structured, to the point and well documented with great
exercises. This is a remarkable book on basic epidemiology,
based on many years of experience and designed primarily for
self-learning students. It will also appeal to all those wanting a
quick and well structured introduction to epidemiology, with a
wealth of classical and more recent examples.”
Professor Christian Lengeler (MSc, PhD), Head of Unit,
Swiss Tropical and Public Health Institute, Basel, Switzerland
This popular book introduces the principles, methods and application of
epidemiology for improving health and survival. The book assists readers in
applying basic epidemiological methods to measure health outcomes, identifying
risk factors for a negative outcome, and evaluating health interventions and health
services.
The book also helps to distinguish between strong and poor epidemiological
evidence; an ability that is fundamental to promoting evidence-based health care.
This new edition has been carefully developed and includes:
Ⅲ A writing style and structure that helps the flow of learning
Ⅲ A broad range of examples and activities covering a range of
contemporary health issues including obesity, mental health and
cervical cancer
Ⅲ Additional focus on developing countries
Ⅲ Updated and additional exercises for self-testing
Ⅲ A new chapter on study design
Ⅲ A new section on the application of epidemiology for monitoring
and evaluation of health programmes
Introduction to Epidemiology 2nd edition is an ideal self-directed learning
resource for students studying epidemiology and all those who work in health-
related areas, including health economists, health policy analysts, and health
services managers.
Ilona Carneiro is a lecturer in infectious disease epidemiology at the London School of Hygiene
and Tropical Medicine (LSHTM). She is a malaria researcher with substantial experience in
teaching, developing and organising epidemiology courses.
Natasha Howard is a research fellow at LSHTM. She is a researcher on health in conflict-affected
settings and an experienced distance learning course
developer, organiser and teacher.
Lucianne Bailey, Katerina Vardulaki, Julia Langham and
Daniel Chandramohan were authors of the first edition.
Downloadedby[FacultyofNursing,ChiangmaiUniversity5.62.158.117]at[07/18/16].Copyright©McGraw-HillGlobalEducationHoldings,LLC.Nottoberedistributedormodifiedinanywaywithoutpermission.

Introduction to Epidemiology
Second edition
23346.indb i23346.indb i 22/08/2011 15:1222/08/2011 15:12

Understanding Public Health series
Series editors: Ros Plowman and Nicki Thorogood, London School of Hygiene & Tropical Medicine.
Throughout the world,there is growing recognition of the importance of public health to sustainable,safe and healthy
societies.The achievements of public health in nineteenth-century Europe were for much of the twentieth century
overshadowed by advances in personal care,in particular in hospital care.Now,as we move into the new century,there
is increasing understanding of the inevitable limits of individual healthcare and of the need to complement such ser-
vices with effective public health strategies. Major improvements in people’s health will come from controlling com-
municable diseases, eradicating environmental hazards, improving people’s diets and enhancing the availability and
quality of effective healthcare.To achieve this,every country needs a cadre of knowledgeable public health practitioners
with social,political and organizational skills to lead and bring about changes at international,national and local levels.
This is one of a series of books that provides a foundation for those wishing to join in and contribute to the regen-
eration of public health,helping to put the concerns and perspectives of public health at the heart of policy-making
and service provision.While each book stands alone, together they provide a comprehensive account of the three
main aims of public health:protecting the public from environmental hazards,improving the health of the public and
ensuring high quality health services are available to all.Some of the books focus on methods,others on key topics.
They have been written by staff at the London School of Hygiene &Tropical Medicine with considerable experience
of teaching public health to students from low, middle and high income countries. Much of the material has been
developed and tested with postgraduate students both in face-to-face teaching and through distance learning.
The books are designed for self-directed learning. Each chapter has explicit learning objectives, key terms are
highlighted and the text contains many activities to enable the reader to test their own understanding of the ideas
and material covered.Written in a clear and accessible style, the series is essential reading for students taking
postgraduate courses in public health and will also be of interest to public health practitioners and policy-makers.
Titles in the series
Analytical models for decision making: Colin Sanderson and Reinhold Gruen
Controlling communicable disease: Norman Noah
Economic analysis for management and policy: Stephen Jan, Lilani Kumaranayake, Jenny Roberts, Kara Hanson
and Kate Archibald
Economic evaluation: Julia Fox-Rushby and John Cairns (eds)
Environmental epidemiology: Paul Wilkinson (ed.)
Environmental health policy: Megan Landon and Tony Fletcher
Financial management in health services: Reinhold Gruen and Anne Howarth
Global change and health: Kelley Lee and Jeff Collin (eds)
Health care evaluation: Sarah Smith, Don Sinclair, Rosalind Raine and Barnaby Reeves
Health promotion practice: Maggie Davies,Wendy Macdowall and Chris Bonell (eds)
Health promotion theory: Maggie Davies and Wendy Macdowall (eds)
Introduction to epidemiology, second edition: Ilona Carneiro and Natasha Howard
Introduction to health economics, second edition: Lorna Guinness andVirginia Wiseman (eds)
Issues in public health, second edition: Fiona Sim and Martin McKee (eds)
Managing health services: Nick Goodwin, Reinhold Gruen andValerie Iles
Medical anthropology: Robert Pool and Wenzel Geissler
Principles of social research: Judith Green and John Browne (eds)
Public health in history:Virginia Berridge, Martin Gorsky and Alex Mold
Understanding health services: Nick Black and Reinhold Gruen
Forthcoming titles:
Conﬂict and health: Natasha Howard, Egbert Sondorp and Annemarie terVeen (eds)
Environment, health and sustainable development, second editon: Emma Hutchinson and Megan Landon
Making health policy, second edition: Kent Buse, Nicholas Mays and Gill Walt
Sexual health: a public health perspective: Kaye Wellings, Martine Collumbien,Wendy Macdowall and Kirstin
Mitchell
23346.indb ii23346.indb ii 22/08/2011 15:1222/08/2011 15:12

Introduction to
Epidemiology
Second edition
Ilona Carneiro and
Natasha Howard
Lucianne Bailey, KaterinaVardulaki,
Julia Langham and Daniel Chandramohan
23346.indb iii23346.indb iii 22/08/2011 15:1222/08/2011 15:12

Open University Press
McGraw-Hill Education
McGraw-Hill House
Shoppenhangers Road
Maidenhead
Berkshire
England
SL6 2QL
email: enquiries@openup.co.uk
world wide web: www.openup.co.uk
and Two Penn Plaza, NewYork, NY 10121-2289, USA
First published 2005
Reprinted 2010
First published in this second edition 2011
Copyright © London School of Hygiene & Tropical Medicine 2011
All rights reserved. Except for the quotation of short passages for the purposes of criticism
and review, no part of this publication may be reproduced, stored in a retrieval system, or
transmitted,in any form or by any means,electronic,mechanical,photocopying,recording or
otherwise, without the prior written permission of the publisher or a licence from the
Copyright Licensing Agency Limited. Details of such licences (for reprographic reproduc-
tion) may be obtained from the Copyright LicensingAgency Ltd of Saffron House,6–10 Kirby
Street, London, EC1N 8TS.
A catalogue record of this book is available from the British Library
ISBN-13: 978-0-33-524461-4
ISBN-10: 0-33-524461-0
eISBN: 978-0-33-524462-1
Library of Congress Cataloging-in-Publication Data
CIP data applied for
Typeset by ReﬁneCatch Limited, Bungay, Suffolk
Printed in the UK by Bell & Bain Ltd, Glasgow.
Fictitious names of companies, products, people, characters and/or data that may be used
herein (in case studies or in examples) are not intended to represent any real individual,
company, product or event.
23346.indb iv23346.indb iv 22/08/2011 15:1222/08/2011 15:12

To Ariana and Alesia Marin Carneiro
and
Alya Howard
23346.indb v23346.indb v 22/08/2011 15:1222/08/2011 15:12

23346.indb vi23346.indb vi 22/08/2011 15:1222/08/2011 15:12

Contents
List of ﬁgures ix
List of tables xi
Preface xiii
Acknowledgements xv
Overview of the book 1
Section 1: Key principles of epidemiology 3
1 Principles of epidemiology 5
2 Measuring the frequency of outcomes 17
3 Measures of association and impact 27
4 Interpreting associations 43
Section 2: Epidemiological research studies 57
5 Study design and handling data 59
6 Ecological studies 75
7 Cross-sectional studies 93
8 Cohort studies 100
9 Case-control studies 110
10 Intervention studies 118
Section 3: Epidemiology in public health 135
11 Prevention strategies 137
12 Surveillance, monitoring and evaluation 155
Glossary 171
Index 181
23346.indb vii23346.indb vii 22/08/2011 15:1222/08/2011 15:12

23346.indb viii23346.indb viii 22/08/2011 15:1222/08/2011 15:12

Figure 1.1 Main sources of epidemiological data 6
Figure 1.2 Incidence of rheumatic fever in Denmark, 1862–1962 7
Figure 1.3 Child road-traffic deaths per 100,000 population 10
Figure 1.4 Distribution of cholera deaths around Golden Square, London,
August–September 1854 12
Figure 1.5 Distribution of cases of cholera by date of onset 13
Figure 2.1 Graphical representation of person-time at risk for 9 study
participants during a 6-year study period 20
Figure 2.2 Person-months at risk of HIV in factory B in 2010 23
Figure 4.1 A normal distribution or ‘bell-shaped’ curve, illustrating the 95%
confidence interval as a dashed line 44
Figure 4.2 The relationship between an exposure, outcome and
confounder 47
Figure 5.1 (a) Histogram of the frequency distribution of haemoglobin
concentration (g/dl) values from a cross-sectional survey of
children. (b) Bar chart of the proportion of children in a
refugee camp underweight by ethnic group 68
Figure 5.2 Scatter plot of national incidence of breast cancer per
100,000 person-years, by estimated per capita alcohol
consumption for selected countries 69
Figure 5.3 Forest plot of estimates from 15 studies of the relative risk of
heterosexual HIV infection among circumcised males
compared with uncircumcised males 71
Figure 6.1 Incidence of neonatal and maternal mortality by percentage
of births without a skilled birth attendant for different regions 76
Figure 6.2 Gross Domestic Product (GDP) per capita and life expectancy
at birth in 169 countries (1975 and 2005) 78
Figure 6.3 Population age-distribution of males in Switzerland and
South Africa in 2005 81
Figure 6.4 Age-specific male cancer mortality rates for 2007 in
Switzerland and South Africa 82
Figure 6.5 (a) Annual geometric mean sulphur dioxide concentrations
in 1987. (b) Prevalence of low birthweight (<2500g) in districts
for which data were available in (a) 87
Figure 8.1 Flow-chart of numbers of participants recruited, numbers
categorized as exposed or unexposed, numbers lost-to-follow-up
in each category, and numbers with and without the outcome
in each exposure category at the end of the study 101
Figure 8.2 Kaplan-Meier survival curve from birth according to survival
status of mother 104
Figure 10.1 Schematic of stepped-wedge intervention trial design 121
List of figures
23346.indb ix23346.indb ix 22/08/2011 15:1222/08/2011 15:12

x List of figures
Figure 10.2 Flow-chart of a factorial design randomized controlled trial
of an insecticide treated net (ITN) and/or intermittent
preventive treatment in infants (IPTi) with sulphadoxine
pyrimethamine (SP) or a placebo 123
Figure 11.1 General outcome process illustrating the three levels at which
intervention for prevention can act 138
Figure 11.2 Schematic models of four different relationships between
exposure to a risk factor and risk of outcome 139
Figure 11.3 Lead-time bias effect for a disease with onset at 50 years and
death at 65 years 145
Figure 11.4 Population distribution of serum cholesterol levels in Japan
and Finland 149
Figure 12.1 Incidence of notiﬁed syphilis cases in the USA per 100,000
population by gender and year 156
Figure 12.2 Total number of AIDS cases reported to the Centers for
Disease Control in the USA between 1982 and 2002 157
Figure 12.3 Age-adjusted percentage of adults ≥20 years old who were
obese in the USA in 2007 158
Figure 12.4 Number of cases of anthrax notiﬁed by year in the USA
(1953–2008) 161
Figure 12.5 Incidence of acute lower respiratory tract infections per
100,000 cases by 3-month reporting period 163
23346.indb x23346.indb x 22/08/2011 15:1222/08/2011 15:12

Table 1.1 Water sources and cholera mortality in London, 9 July to
26 August 1854 12
Table 3.1 Standard cross-tabulation (2 × 2 table) of outcome by
exposure 28
Table 3.2 Comparison of mortality rates for two outcomes 33
Table 3.3 Cause of death and specific death rates by smoking habits of
British male doctors, 1951–71 36
Table 3.4 Incidence of tuberculosis and mid-year population by ethnic
group in country Z, 2011 37
Table 3.5 Odds of smoking in cases of myocardial infarcation (MI) and
controls 41
Table 3.6 Incidence of tuberculosis, mid-year population, incidence rate
and rate ratio by ethnic group in country Z, 2011 41
Table 5.1 Key features, advantages and disadvantages of main
epidemiological study designs 61
Table 6.1 Direct standardization of Swiss and South African (SA) 2007
male cancer mortality rates per 100,000 83
Table 6.2 Indirect age standardization of Swiss and South African (SA)
2007 male cancer mortality 84
Table 6.3 HIV-related deaths and estimated population by age group
in country Y, 2010 85
Table 6.4 Age-specific HIV-related mortality for country Z in 2010 86
Table 6.5 Age-specific mortality rates in City A and City B 86
Table 6.6 Outdoor gamma radiation and cancer incidence among
children from 69 census areas within 10 miles of a US
nuclear plant 88
Table 6.7 HIV-related deaths and estimated population by age group
in country Y, 2010 90
Table 6.8 Expected mortality for City B using rates from City A 91
Table 7.1 Numbers (%) of children from three cross-sectional
surveys, 1997–1999 96
Table 7.2 Effect of net ownership on the prevalence of anaemia and
malaria parasites 96
Table 7.3 Selected factors associated with the presence of a mental
disorder in adolescents (n = 2048) 97
Table 7.4 ITN ownership among children with and without anaemia 98
Table 7.5 Net ownership among children with and without malaria
parasites 98
Table 8.1 Lung cancer death rates per 100,000 person-years by
gender and smoking status 105
Table 8.2 Incidence of pulmonary tuberculosis (TB) by HIV status
and age 106
List of tables
23346.indb xi23346.indb xi 22/08/2011 15:1222/08/2011 15:12

xii List of tables
Table 8.3 Incidence rate ratios for lung cancer death by gender
and smoking status 108
Table 8.4 Incidence of tuberculosis (TB) by HIV status and age 109
Table 10.1 Vaccine efﬁcacy against ﬁrst episode of invasive pneumococcal
disease 129
Table 11.1 Standard cross-tabulation (2 × 2 table) of true condition by
screening/diagnostic result 141
Table 11.2 List of ten WHO criteria for assessing the appropriateness
of screening 144
Table 11.3 Comparison of methods and biases of study designs for
evaluating screening methods 145
Table 11.4 Distribution of myocardial infarction (MI) by high-risk group 148
Table 11.5 FBS test results (cut-off 6 mmol/1) by true diabetes
(GTT test) status 152
23346.indb xii23346.indb xii 22/08/2011 15:1222/08/2011 15:12

This book represents a thorough revision of the ﬁrst edition.The structure of the book
has been changed to help the ﬂow of learning. Key concepts of chance, bias, confound-
ing and causality are now introduced earlier to help student understanding.The con-
cept of standardization is introduced later to improve the pace at which new material
is covered.The chapters on risk assessment and screening methods have been com-
bined as both relate to preventive strategies. A new chapter on study design has been
written to bring together issues common to all epidemiological studies, and may be
used as a quick reference when developing a study protocol. Finally, the chapter on
surveillance includes a new section on the application of epidemiology for monitoring
and evaluation of health programmes.
We have aimed to clarify the terminology and concepts covered in the original ver-
sion, and have revised the examples and activities to cover a wider range of more
contemporary health issues,with additional focus on developing countries.The number
of activities has been increased and we have moved the feedback to the end of the
chapters for this new edition to help readers test their understanding of the material
more effectively. New material includes: measuring the secondary attack rate for out-
break investigation, the use of case-control studies for genetic epidemiology and plau-
sibility designs for intervention studies.
Preface
23346.indb xiii23346.indb xiii 22/08/2011 15:1222/08/2011 15:12

23346.indb xiv23346.indb xiv 22/08/2011 15:1222/08/2011 15:12

Acknowledgements
The authors wish to thank colleagues who have developed the original lectures and
teaching materials at the London School of Hygiene & Tropical Medicine: Lucianne
Bailey, Katerina Vardulaki, Julia Langham and Daniel Chandramahon who wrote the
ﬁrst edition; Ros Plowman, and Nicki Thorogood (Series Editors) and Julia Langham,
Daniel Chandramohan and John Carneiro for reviewing chapters in the 2nd edition.We
are grateful to the students of the Public Health Distance Learning course for their
challenging questions that have helped to improve the material, especially Peter
Simpson, Dina Khan,Aaron Hawkins, Anita Dubey and Julie Nabweteme who piloted
various chapters.
23346.indb xv23346.indb xv 22/08/2011 15:1222/08/2011 15:12

23346.indb xvi23346.indb xvi 22/08/2011 15:1222/08/2011 15:12

Introduction
This book is intended for self-directed learning. It provides a summary of the main
concepts and methods of epidemiology as a foundation for further study. It will also
introduce more advanced epidemiological and statistical concepts to broaden under-
standing.After completing the book, you should be able to apply basic epidemiological
methods and critically interpret the epidemiological findings of others.
Why study epidemiology?
Epidemiology is integral to public health.Whether your interest is in clinical or public
health medicine, the study of epidemiology is key to improving health. Neither clinical
nor public health practice can be based on experience alone; they must be based on
scientific evidence.Understanding the appropriateness of different research methods is
essential to critical appraisal of the evidence presented in scientific literature. The
ability to distinguish between strong and poor evidence is fundamental to promoting
evidence-based healthcare.This ability is important for all those who work in health-
related areas, including health economists, health policy analysts, and health services
managers. Epidemiology is central to clinical research, disease prevention, health
promotion, health protection and health services research.
Epidemiology offers rigorous methods to study the distribution, causation and
prevention of poor health in populations. It enables a better understanding of health
and the factors that influence it at individual and population-levels. Epidemiological
methods are also used to investigate the usefulness of preventive and therapeutic
interventions, and the coverage of healthcare services.The purpose of epidemiology is
to use these methods and the resulting data to improve health and survival.
Structure of the book
This book is structured around the basic concepts, practices and applications of epide-
miology and uses the conceptual framework of the basic epidemiology module taught
face-to-face at the London School of Hygiene &Tropical Medicine.It is based on mater-
ials presented in lectures and seminars, which have been adapted for distance learning.
Chapters 1–4 discuss the principles of epidemiology and introduce strategies for
measuring the frequency of health outcomes, associations and impact of exposures,
and evaluating whether an association is causal. Chapters 5–10 focus on practical
aspects of epidemiological research,including issues of study design and data collection
and the strengths and weaknesses of each of the principal epidemiological study
designs. Chapters 11–12 consider the application of epidemiology for prevention
strategies, and surveillance, monitoring and evaluation.
Overview of the book
23346.indb 123346.indb 1 22/08/2011 15:1222/08/2011 15:12

2 Overview of the book
Each chapter includes:
• an overview
• a list of learning objectives
• a range of activities
• a concluding summary
• feedback on the activities
In each chapter, some words are presented in italics to add emphasis.Words presented
in bold are described in the Glossary on p.171.You may find the index at the end of
the book useful for finding terms that you are unsure of or wish to review.
Guidance notes for activities
We recommend that you attempt the activities as they appear in the text, and refer
back to the preceding explanatory text if you find a question unclear or difficult.You
should complete the whole of each activity before reading the relevant feedback at the
end of each chapter, as this will help you assess your understanding of the material
presented. As is usual in epidemiology, most activities will include numerical calcula-
tions and require interpretation of results.
The required mathematical skills will be fairly basic, but may require the use of a
calculator. Proportions (e.g. 0.20) can be presented as percentages by multiplying by
100 (i.e. 0.20 × 100 = 20%). Except for percentages, answers should generally be
rounded to two decimal places (e.g. 0.148 reported as 0.15), and statistical probability
values are usually rounded to three decimal places (e.g. 0.0025 reported as p = 0.003).
It is important not to round numbers until the very end of a mathematical operation,
to avoid the accumulation of error due to rounding and remain as precise as possible.
23346.indb 223346.indb 2 22/08/2011 15:1222/08/2011 15:12

SECTION 1
Key principles of
epidemiology
23346.indb 323346.indb 3 22/08/2011 15:1222/08/2011 15:12

23346.indb 423346.indb 4 22/08/2011 15:1222/08/2011 15:12

Overview
Epidemiology is the cornerstone of public health. It employs rigorous methods
and a quantitative approach to study the health of populations rather than individuals.
Epidemiological methods are used to identify the causes of poor health, measure the
strength of association between causes and outcomes, evaluate interventions and
monitor changes in population health over time. The study of epidemiology
provides the evidence-base for appropriate public health policy, planning and practice.
This chapter provides an introduction to the key approaches of epidemiological
research.
Learning objectives
When you have completed this chapter you should be able to:
• describe the key aspects of epidemiology
• discuss the complex factors involved in the study of causality
• identify the basic study designs used in epidemiology
• recognize the role of epidemiology in society.
What is epidemiology?
Epidemiology is the study of the distribution and determinants of health states
or events in specified populations, and the application of this study to control health
problems (adapted from Porta and International Epidemiological Association, 2008).
Health states or events usually refer to infection, illness, disability, or death but
may equally be used to refer to a positive outcome (e.g. survival). Epidemiological
studies describe the distribution of these health outcomes in terms of frequency
and pattern. The frequency is the number of occurrences of an outcome within a
given time period, and the pattern refers to the occurrence of the outcome by
time, place and personal or population characteristics. Determinants influence
the frequency and pattern of health outcomes and are known as risk factors or
protective factors, depending on whether they result in a negative or positive health
outcome respectively.
Epidemiological research also involves the testing of preventive interventions (e.g.
vaccines, improved hygiene) and therapeutic interventions (e.g. medicines, surgery) to
improve health and survival. An intervention may be evaluated either under ideal
(research-controlled) conditions to assess its efficacy or through a routine delivery
system to assess its effectiveness.
1Principles of
epidemiology
23346.indb 523346.indb 5 22/08/2011 15:1222/08/2011 15:12

6 Key principles of epidemiology
After collecting epidemiological evidence, its application to improve health is
a natural progression. Identification of risk factors and protective interventions,
and quantification of their effects are key to informing action. Knowledge of the distri-
bution and time-trends of outcomes, risk factors, and intervention coverage may be
used for advocacy, for health promotion, and to inform public health policy and
practice.
The study of epidemiology
The two main approaches to epidemiological study are descriptive and
analytical (Figure 1.1). Descriptive epidemiology may provide information on the
distribution of health outcomes by age, population type, geography or over time.
Sources of descriptive data include routine monitoring such as registers of births and
deaths, notification systems of specific diseases or adverse treatment reactions,
and hospital or clinic records. Population censuses may also provide data on births,
deaths, and a variety of risk factors (e.g. age, gender), and there is an overlap with
demography (i.e. research on changes in the size, structure and distribution of human
populations).Population health surveys evolved from censuses and provide information
on the use of health services, coverage of interventions and the frequency of specific
outcomes.
Figure 1.1 Main sources of epidemiological data
Source: Ilona Carneiro.
Activity 1.1
Figure 1.2 shows a declining trend in the incidence of rheumatic fever in Denmark
since 1900. Briefly describe what this might suggest.
23346.indb 623346.indb 6 22/08/2011 15:1222/08/2011 15:12

Principles of epidemiology 7
Cause and effect
Analytical epidemiology aims to investigate which factors may be responsible for
increasing or decreasing the probability (‘risk’) of an outcome. Identifying the cause of
an outcome is not always simple, and can be described in terms of sufficient cause
and component causes. Sufficient cause refers to a factor or set of factors that
inevitably produces the outcome.The factors that form a sufficient cause are called
component causes. Some component causes are essential for the outcome to occur:
tuberculosis cannot occur without Mycobacterium tuberculosis, and this is known as a
necessary cause. However, some people may be infected with M. tuberculosis without
developing tuberculosis, because other components such as immune status and con-
current infections (e.g. HIV) will determine their susceptibility to the disease.
A single necessary cause is rarely sufficient to cause the outcome. While this
may make epidemiological investigation of causality more difficult to untangle, it
works to our advantage in public health, as it means that there are often several points
at which we can intervene to reduce the likelihood of an outcome. Necessary causes
may be:
1 infectious agents such as viruses, bacteria or parasites;
2 environmental agents such as sun-rays or allergens (e.g. pollen, dust-mites);
3 industrial agents such as chemicals (e.g. nicotine) or radiation (e.g. mobile phones);
4 genetic factors such as chromosomal abnormalities;
5 physical factors such as violence or car accidents;
6 psychological factors such as stress or abuse.
Figure 1.2 Incidence of rheumatic fever in Denmark, 1862–1962
Source: Taranta and Markowitz (1989) – graph re-drawn by Ilona Carneiro from Beaglehole et al. (1993).
23346.indb 723346.indb 7 22/08/2011 15:1222/08/2011 15:12

Component causes may influence an individual’s contact or response to a necessary
cause. Environmental factors tend to affect contact and may be physical (e.g. climate,
altitude), biological (e.g. vectors that transmit an agent) or structural (e.g. crowding,
sanitation). Human factors affect both contact and response, and include age, sex,
ethnicity, behaviour, genetics, and nutritional and immunological status.These environ-
mental and human factors also interact,making the whole process even more complex.
For example, people living in conditions of poor sanitation will have greater contact
with the polio virus because transmission is mainly via faecal contamination. Children
will be at greater risk of infection than adults because of their poorer sanitary practices
and also because of their lack of natural immunity or incomplete immunization.
As you may have realized, depending on the perspective we take, a cause can also be
considered as an outcome for the purpose of epidemiological investigation. For exam-
ple, human immunodeficiency virus (HIV) is a necessary cause of acquired immunode-
ficiency syndrome (AIDS). However, we might then want to consider HIV infection as
an outcome, and identify the necessary cause as unprotected sex with an infected
individual, or contact with contaminated needles.This leads us to consider other risk
factors that might increase the likelihood of HIV infection: multiple sexual partners,
sharing of intravenous drug needles or poor safety practices in health facilities.However,
while these risk factors can be component causes, they are not necessarily causal.
A person may become infected through only one sexual contact,while another person
with multiple sexual partners may not become infected at all.
Relating a causative agent or risk factor – from here on termed exposure – to an
outcome of interest is known as inferring causality. For an association to be causal,
the exposure must occur before the outcome. Other factors that support a causal
relationship include a dose–response relationship, the strength of the association seen,
a plausible biological mechanism of action, and reproducibility of the result.These and
other factors that support causality will be discussed in more detail in Chapter 4.
Alternative explanations
Analytical methods may confirm an association between an exposure and outcome, but
causality can only be inferred if alternative explanations, namely chance, bias and con-
founding,have been accounted for.Chance is the possibility that there is random error
and is usually reduced by increasing sample size, using random selection (observa-
tional studies) or randomization (intervention studies). Bias refers to systematic dif-
ferences between comparison groups, which may misrepresent the association being
investigated.Confounding is caused when another factor,independently associated with
both the outcome and exposure of interest,influences the association being investigated.
These alternative explanations for an apparent association between an outcome and
exposure, and the challenges of inferring causality, will be discussed in Chapter 4.
Analytical study designs
The main approach to investigating causal relationships is through analytical studies.An
epidemiological investigation starts with the development of a hypothesis, which
takes the form of a proposed association that can be tested.For example,‘smokers are
at a higher risk of lung cancer’.An analytical study will then aim to find out whether
there is sufficient or insufficient evidence to support this hypothesis.
23346.indb 823346.indb 8 22/08/2011 15:1222/08/2011 15:12

Analytical epidemiology takes two forms: observation or intervention (Figure 1.1).
An observational study aims to compare the frequency of the outcome in groups or
individuals with and without the exposure of interest.An intervention study is effec-
tively an experiment,and therefore restricted to evaluating the effect of reducing a risk
factor or increasing a protective factor on the frequency of an outcome. Five study
designs form the core of epidemiological research and these will be considered in
more detail in Chapters 6–10:
1 Ecological studies consider populations of individuals and aim to relate the total
frequency of an outcome to an average level of exposure by population group. For
example, differences in alcohol consumption and incidence of breast cancer by
country.
2 Cross-sectional studies collect data on outcome and exposure at one point in
time from a random sample of study subjects. For example, prevalence of HIV in
relation to male circumcision.
3 Cohort studies compare individuals with recorded differences in exposure to
measure the occurrence over time of the outcome in relation to exposure. For
example, incidence of cervical cancer in women with and without human papilloma-
virus infection.
4 Case-control studies identify individuals with and without the outcome, and exam-
ine whether they differ in relation to previous exposure.For example,mobile telephone
use among people with brain tumours compared to those without brain tumours.
5 Intervention studies allocate a protective factor to individuals or groups, and
compare the frequency of the outcome in those exposed with those unexposed.
For example, the incidence of malaria among children given an insecticide-treated
mosquito net, compared with those given an untreated mosquito net. Intervention
studies may be randomized or non-randomized.
The application of epidemiology
The data and relationships identified through epidemiological study may be used in
various ways.Descriptive epidemiological methods enable health professionals to iden-
tify the actual and potential health problems in a population. The burden of health
outcomes or associated risk factors can be quantified, related to existing health serv-
ices,and tracked to predict changes over time. An overview of the health issues affect-
ing a population, and more importantly the relative distribution of these outcomes,
enables priorities to be set and programmes to be planned. For example, Figure 1.3
shows that the incidence of road traffic deaths among children was estimated to be
greater in Africa than in Europe for 2004, highlighting the need for relevant interven-
tions in Africa.
Once a risk factor has been identified through analytical studies, health promotion
activities may be developed to reduce exposure to the outcome at the individual level
(e.g. encouraging smokers to stop smoking through education and support pro-
grammes) or population level (e.g. banning smoking in public places). Screening pro-
grammes may be implemented to increase early diagnosis and appropriate treatment
(e.g. recommended mammograms for all women over 50 years old, who are at greater
risk of breast cancer than younger women).
Monitoring and evaluation of health programmes are necessary to assess whether an
implemented intervention is safe and effective under routine conditions, and whether
23346.indb 923346.indb 9 22/08/2011 15:1222/08/2011 15:12

this can be maintained over time.This may take the form of routine surveillance for the
outcome (e.g. number of measles cases), or monitoring of specific programmatic indi-
cators (e.g. number of children receiving three doses of measles vaccine).
Activities 1.2–1.5
To help you put some of these epidemiological ideas into context,you will now look at
a famous example from the nineteenth century.
John Snow (1813–58), a distinguished physician and considered one of the fathers of
epidemiology, is best known for his studies of cholera outbreaks in London between
1848–49 and in 1854 (Snow 1936). These are the first documented epidemiological
investigations. Activities 1.2–1.5 use John Snow’s cholera studies to illustrate the
epidemiological approach, from descriptive epidemiology and hypothesis generation
(1.2), to hypothesis testing and refinement (1.3–1.4), and application of epidemiological
data (1.5).After attempting each activity you should refer to the feedback at the end of
the chapter to prepare you for the next activity. Feedback does not provide the only
true answers, as there are many accurate ways to answer these questions.
Cholera periodically swept across Europe during the nineteenth century. Cholera
was characterized by profuse painless diarrhoea and clear fluid vomit that caused rapid
dehydration, but the cause was unknown.After a severe epidemic in London in 1832,
cholera reappeared in 1848.The first definite case was a seaman, newly arrived from
Hamburg where cholera was prevalent. He died a few hours after the onset of symp-
toms on 22 September 1848 in a hotel near the River Thames.The next case was a
lodger in the same room, who developed cholera symptoms on 30 September 1848.
During the epidemic, approximately 15,000 deaths were recorded. Cholera mortality
Figure 1.3 Child road-traffic deaths per 100,000 population
Source: WHO (2008).
23346.indb 1023346.indb 10 22/08/2011 15:1222/08/2011 15:12

in this epidemic was particularly high in residential areas downstream from the hotel,
and decreased progressively upstream.
Microorganisms had not yet been discovered and one of the popular beliefs
about disease causation was the ‘miasma’ theory – that breathing bad air caused
disease. John Snow had previously documented several instances in which people
had come into contact with cases of cholera and developed the disease within a
few days. While investigating several case series of cholera, he made the following
observations:
• Cholera was more readily transmitted within poor households and to those who
had handled a case of cholera.
• Miners had suffered more than any other occupation.
• Almost no doctor who attended to cholera cases or conducted post-mortems had
developed cholera.
• Most cases of cholera developed within 24–48 hours after contact with a case of
cholera.
• Cholera was characterized by profuse painless diarrhoea and often proceeded with
so little feeling of general illness that patients did not consider themselves in danger,
or seek advice, until the illness was far advanced.
Activity 1.2
1 If you were a doctor in Snow’s time, list what hypotheses you might generate about
cholera transmission from these observations.
2 Describe how Snow might have interpreted his observations to oppose the ‘miasma
theory’ and support alternative hypotheses such as those in question 1.
3 Identify what the most plausible explanations are for the observed association
between elevation of residential area and level of mortality from cholera.
Activity 1.3
During the nineteenth century, private companies that obtained water directly from
the river Thames supplied the drinking water in London. Each company had its own
network of pipes. In some areas these networks overlapped and different companies
could supply houses along a single street.The Southwark andVauxhall (S&V) Company
and the Lambeth Company were the two major water suppliers to the cholera-affected
areas during the epidemics that John Snow investigated.
Between 1849 and 1853, when London was free of cholera, the Lambeth Company
moved its water source upstream to an area outside London, while the S&V Company
continued to draw water from a downstream source in London. Snow collected data
on the number of houses supplied by the S&V Company and the Lambeth Company.
When the cholera epidemic recurred in London in 1854, he collected data on sources
of water for households of those who died of cholera.Table 1.1 shows the number of
cholera deaths per 10,000 households,stratiﬁed by water source,during the ﬁrst seven
weeks of the epidemic.
1 Do the data presented in Table 1.1 support Snow’s hypothesis that cholera is
transmitted through water? Give reasons for your answer.
23346.indb 1123346.indb 11 22/08/2011 15:1222/08/2011 15:12

2 Are these data adequate to conclude that cholera mortality is higher in houses
supplied by the S&V Company than in houses supplied by the Lambeth Company?
Give reasons for your answer.
3 What further questions might you ask before reaching any conclusions based on
these data?
Activity 1.4
Snow investigated a severe outbreak of cholera in the Soho area of London. He
collected house addresses of all 616 recorded cholera deaths between 19 August and
30 September 1854. From these data he produced a map showing the distribution of
cholera deaths (bars) and positions of the water pumps (ﬁlled-circles) used by Soho
households (Figure 1.4).This is known as a ‘spot map’.
Table 1.1 Water sources and cholera mortality in London, 9 July to 26 August 1854
Source of water Total number of households Number of cholera deaths Deaths per 10,000 houses
S&V Company 40,046 1,263 315
Lambeth Company 26,107 98 37
Rest of London 256,423 1,422 59
Source: Adapted from John Snow (1936).
Figure 1.4 Distribution of cholera deaths around Golden Square, London, August–September 1854
presented in a ‘spot map’
Source: John Snow (1936).
23346.indb 1223346.indb 12 22/08/2011 15:1222/08/2011 15:12

Figure 1.5 Distribution of cases of cholera by date of onset (based on data from Snow, 1936)
Source: Drawn by Ilona Carneiro using data from John Snow (1936).
1 Describe the distribution of cholera deaths in relation to the position of water
pumps in Figure 1.4.
2 What might explain the differences in the distribution of deaths around water pumps
A, B, C and D?
3 Can you conclude that water from a particular pump was the source of the cholera
epidemic? Give reasons for your answer.
4 What further information do you need?
Activity 1.5
Snow discovered that a brewery was located in the two blocks with no cholera deaths
with a deep well on the premises.The brewery workers and people living nearby col-
lected water from the brewery well.Additionally,brewery workers had a daily quota of
malt liquor.This information convinced Snow that pump B was the source of the chol-
era.He persuaded the local authorities to remove the pump-handle,preventing further
use of the pump after the 8th September.
The dates of onset of symptoms of the 616 fatal cases of cholera recorded between
19 August and 30 September are shown in Figure 1.5.
1 Describe what the graph in Figure 1.5 shows.
2 Did removal of pump B end the cholera epidemic? Explain your answer.
3 What other factors might explain why the epidemic stopped?
23346.indb 1323346.indb 13 22/08/2011 15:1222/08/2011 15:12

Conclusion
Epidemiology includes both a scientiﬁc approach (evidenced-based medicine) and a
societal perspective (population-based studies and solutions) to health.You have been
introduced to several new concepts and terms that are key to the understanding of
epidemiology: descriptive epidemiology, inferring causality, analytical study designs,
interpretation of results and the applications of epidemiology.These issues are funda-
mental for those involved in clinical and public health, and will be discussed further in
subsequent chapters.
References
Beaglehole R, Bonita R and Kjellstrom T (1993) Basic Epidemiology, Geneva:World Health Organization.
Porta MS and International Epidemiological Association (eds) (2008) A Dictionary of Epidemiology, Oxford:
Oxford University Press.
Snow J (1936) Snow on Cholera (being a reprint of two papers), London: Oxford University Press.
Taranta A and Markowitz M (1989) Rheumatic fever: a guide to its recognition, prevention and cure. 2nd edn.
Lancaster: Kluwer Academic Publishers.
World Health Organization (2008) TheWorld Health Report 2008:Primary Health Care – Now MoreThan Ever,
Geneva:World Health Organization.
Feedback for activities
Activity 1.1
The graph in Figure 1.2 shows that the incidence of rheumatic fever drops particularly
sharply after 1900,having been relatively steady for the previous 40 years.This suggests
that some event might have triggered the decline in the incidence of rheumatic fever
around 1900.
Rheumatic fever is caused by haemolytic streptococcal upper respiratory tract infec-
tion, which is associated with poverty and overcrowding.Therefore, it is reasonable to
suggest that the decline in rheumatic fever was the result of improvements in socioeco-
nomic conditions in Denmark that occurred at the beginning of the twentieth century.
Activity 1.2
1 You might have listed some or all of the hypotheses that Snow developed. Based on
his observations,Snow generated the following hypotheses on the mode of transmis-
sion of cholera:
• Cholera can be transmitted from the sick to the healthy.
• Cholera is caused by some material (Snow called it ‘morbid matter’) that can
increase and multiply in the body of the person it attacks.
• The causative agent must be introduced into the alimentary canal by swallowing.
• The causative agent may be transmitted through water from the sick to the healthy.
2 To dispute the miasma theory, Snow argued that:
• The risk of transmission of cholera was high in miners and people of low socio-
economic status because these groups had poor hygiene practices and were,
therefore, more likely to have contact with faecal matter from cholera patients
than those of higher socioeconomic status.
23346.indb 1423346.indb 14 22/08/2011 15:1222/08/2011 15:12

• Few doctors developed cholera because they washed their hands after seeing
each cholera patient.
• If transmission were through the air or via a vector, the disease would have been
transmitted from cholera patients to more doctors.
• Thus, the disease was most likely caused by some causative agent transmitted by
direct contact.
3 The observed association between higher elevation of residential area and lower
mortality from cholera could support the theory of bad air causing cholera.However,
as Snow argued, the water downstream of the initial cases was more likely to be
polluted with sewage than the water upstream.Thus, the increased risk of cholera
transmission in the areas downstream also supported his theory that the causative
agent was most probably transmitted through water.
Activity 1.3
1 Yes, these data support Snow’s hypothesis that cholera is transmitted through water,
but they do not prove it. For example, no information on other possible modes of
transmission is included.
2 The risk of cholera death was 315/10,000 in houses supplied by the S&V Company,
38/10,000 in households supplied by Lambeth Company, and 55/10,000 in houses
supplied by other sources.These data suggest that the risk of cholera death was 8–9
times higher (315/38) in households supplied by the S&V Company than in house-
holds supplied by the Lambeth Company. However, they do not prove causality and
are not adequate to make ﬁrm conclusions that cholera mortality is higher in house-
holds supplied by the S&V Company.
3 Before reaching any conclusions, you would want to consider whether the number
of people per household, their socioeconomic status, and other potential factors
associated with the risk of transmission of cholera are comparable between these
two populations. For example, the S&V Company might have supplied water to
multiple-occupancy buildings while Lambeth supplied individual family houses. If this
were the case, then the risk of cholera death per house between the two popula-
tions would not be comparable since the average number of people per house
would differ between them.Since the S&V Company was drawing water from down-
stream, it is possible that households supplied by the company would have been in
downstream areas and might be poorer than households upstream.Thus, although
these data appear to support Snow’s hypothesis, more information is needed to be
convincing.
Activity 1.4
1 Figure 1.4 shows that there was a cluster (collection) of many deaths around pump
B (the Broad Street pump), very few deaths near pumps A and D, and almost no
deaths around pump C.
2 If water from all the pumps was the source of cholera, there would probably have
been similar numbers of deaths around each pump rather than more around pump
B. However, it is possible that people did not drink the water from pumps A, C and
D due to bad taste, smell, or inconvenience, or that the water from these pumps
might not have carried the cholera causative agent.
3 While pump B has the greatest spatial clustering of cholera deaths and might have
been the source, this is not sufﬁcient to conclude that pump B was the source of
23346.indb 1523346.indb 15 22/08/2011 15:1222/08/2011 15:12

cholera.Two blocks of buildings very close to pump B did not have a single death
from cholera.
4 More information is needed to explain the absence of deaths in the two blocks
nearby before implicating the water from pump B as the source of the epidemic.For
example, if it could be shown that there was no death in these blocks for reasons
such as:
• No one lived there.
• Inhabitants had alternative sources of water.
• Inhabitants had some kind of protection against cholera.
Activity 1.5
1 There appears to have been a low background number of cases (zero or one case
per day) before 30thAugust.There was an explosive rise in the number of cases over
three days,which decreased to previous levels after 12 days.The most likely explana-
tion for the sudden rise in the number of cholera deaths would be exposure of the
population to a causal agent from a common source.
2 It is unlikely that removal of the pump-handle from pump B stopped the epidemic,
because the number of cholera deaths had already dropped to almost the back-
ground level by the time the pump-handle was removed. However, removing the
pump-handle B may have prevented another outbreak of cholera if pump B still
contained the causal agent and was available for use.
3 There are several possible explanations for the end of the epidemic:
• People who lived in the epidemic area might have moved elsewhere due to fear
of contracting cholera.
• All susceptible people (those who had no form of immunity to cholera and
were therefore at-risk of infection) might have been exposed within a short time,
leaving very few susceptible individuals.
• The amount of causal agent in the water could have reduced.
Vibrio cholera,the bacterium that causes cholera,was identified by Robert Koch in 1883,
several decades after Snow identified appropriate preventive measures from his epide-
miological investigations:
I feel confident, however, that by attending the above mentioned precautions
(personal hygiene, boiling soiled bedclothes of patients, isolation and quarantine,
improved waste disposal, drainage, provision of clear water), which I consider to be
based on correct knowledge of the cause of cholera, this disease may be rendered
extremely rare, if indeed it may not be altogether banished from civilized countries.
(Snow 1936)
23346.indb 1623346.indb 16 22/08/2011 15:1222/08/2011 15:12

2
Overview
The occurrence of health outcomes (i.e. infection, illness, disability and death) will vary
between populations, geographical areas and over time. Epidemiological studies
quantify the frequency of health outcomes, which is the number of occurrences in a
defined population over a defined time-period. In this chapter you are introduced
to the epidemiological measures used to determine the frequency of outcomes:
prevalence, risk (including attack rates), odds and incidence rates.
Learning objectives
• identify and define the four common frequency measures: prevalence, risk, odds
and incidence rate
• calculate each of these frequency measures
• recognise the use of attack rates in the investigation of outbreaks
• estimate person-time at risk.
Defining a case
To measure the frequency of an outcome in a population, it is first necessary to have a
clear definition or description to identify the outcome of interest. In some situations
the outcome is obvious (e.g.all cause death),but often,standardized criteria are needed
(e.g. severe anaemia may be defined as haemoglobin less than 5 grams per decilitre).
Individuals with the outcome of interest are often referred to as ‘cases’.The criteria
used to define them form the case definition, which may not be clinically defined.
The outcome may refer to an event such as a car accident rather than an
illness. A ‘case’ may occur only once per individual (e.g. death), more than once (e.g.
pregnancy), or frequently (e.g. diarrhoeal disease). Epidemiologists count cases using
clinical assessments, diagnostic tests, registry or clinic record entries, observation, or
even self-reporting in population surveys.
Knowing the number of cases is not enough to allow any comparison or association
to be made. If you were told that there were 75 cases of tuberculosis in village A and
only 25 cases in village B, you might be tempted to conclude that tuberculosis was
more common in village A than in village B. However, without knowing how many
people live in each village, this comparison is impossible to make. Once cases have
been defined and counted, it is necessary to count the number of individuals in the
population from which cases were identified and the time-period in which the cases
occurred, to calculate frequency.
Measuring the frequency
of outcomes
23346.indb 1723346.indb 17 22/08/2011 15:1222/08/2011 15:12

Measuring disease frequency
The most common measures of disease frequency (i.e. prevalence, risk, odds, incidence
rate) vary according to how cases and time-period are considered.We will use the anal-
ogy of a children’s game of musical chairs, where everybody dances while the music is
played, and chairs are removed at regular intervals when the music stops.Those left
without a chair on which to sit have to stand to one side until the game finishes.We can
explain the measures of frequency as follows, where the outcome is ‘sitting on a chair’:
1 Prevalence counts the number of children sitting at a specific time point (e.g. at
11:30a.m.),compared with the total participants in the game (standing and sitting) at
that same time point.
2 Risk counts those sitting after a specified time-period (e.g. after 10 minutes), com-
pared with the total participants at the start of the game.
3 Odds counts those sitting after a specified time-period (e.g. after 10 minutes), com-
pared with those standing after the same time-period.
4 Incidence rate counts those sitting at any point during the game and the total time that
each individual participates,allowing for children who join the game late or leave early.
Prevalence
Prevalence is the number of existing cases in a defined population at a defined point in
time divided by the total number of people in that population at the same point in time:
Prevalence =
Number of cases at one time point
Total number of individuals in the defined population
at same time point
Prevalence is a proportion and can never be greater than one. It is dimensionless,
meaning that it has no units, so the term ‘prevalence rate’ is incorrect. Prevalence is
usually presented as a percentage by multiplying the proportion by 100. Prevalence is
sometimes referred to as point prevalence to distinguish it from period preva-
lence. Period prevalence refers to the number of existing cases identified during a
specified,usually short,period divided by the total number of people in that population
during the same period.
The prevalence of an outcome may be measured during population surveys or cross-
sectional studies. Prevalence is useful to rapidly assess the frequency of an outcome in
a community. For example, in a cross-sectional survey of 200 boys aged 5–10 years old
in a low-income setting, 60 were found to be stunted, i.e. had a height-for-age lower
than the average.The prevalence of stunting in this group would be calculated as 60 ÷
200 = 0.30, which would be presented as 0.3 × 100 = 30% of young boys in this popu-
lation being stunted (an indicator of chronic malnutrition) at the time of the survey.
Incidence
Incidence is the frequency of new (‘incident’) cases in a defined population during a
specified time-period. Incidence may be measured in ecological or cohort studies.
There are three different ways of considering incidence: risk, odds and incidence rate.
23346.indb 1823346.indb 18 22/08/2011 15:1222/08/2011 15:12

Measuring the frequency of outcomes 19
Risk
Risk is also known as cumulative incidence because it refers to the total number
of new cases in a defined ‘population at risk’ over a specified period of time:
Risk =
Number of new cases in a specified time-period
Total number of individuals at risk in the population at the
start of that time-period
This measure can be interpreted as the likelihood (‘risk’) that an individual will develop
an outcome during the specified time-period, and the ‘population at risk’ excludes
existing (‘prevalent’) cases. Risk is also a dimensionless proportion, so can never be
greater than one and has no units. However, its value can increase with the duration of
the time-period under consideration, making it essential to specify the period at
risk. For example, if a group of 100 people were studied for a year, and 75 had caught
at least one cold during that year, we could say that the risk of catching a cold was
75 ÷ 100 = 0.75 or 75% in that year in that group. However, the result would be
interpreted differently if 100 people had been studied for six months and 75 had caught
at least one cold during this six-month period; it would have to be specified as a 75%
risk over 6 months.
A specific form of risk used in disease outbreak settings is called the secondary
attack rate.This is a misnomer, as it is a proportion and not a rate (see below), but
the term is commonly accepted.The secondary attack rate is calculated as the number
of new cases among contacts of a primary case in a specified period of time:
Secondary attack rate =
Number of new cases among contacts in a
specified time-period
Total number of contacts of a primary
case in that time-period
This can be interpreted as the ‘risk’ that a contact of a case will develop the outcome
during the specified time-period.The total number of contacts is often estimated from
the household members of primary cases, but may also include school or workplace
contacts.For example,if eight children developed varicella (chicken pox) in an outbreak
at a school, and five out of a total of 15 siblings developed varicella in the subsequent
two weeks, we could estimate the secondary attack rate, or risk of developing varicella
among household contacts, as 5 ÷ 15 = 0.33 or 33% in this two-week time-period.
Odds
Odds is a different way of representing risk, and is calculated as the number of new
cases divided by the number of individuals still at risk after a specified time- period:
Odds =
Number who did not become a case during that time-period
The odds is actually a ratio of two proportions and can be greater than one. It is the
ratio of the ‘risk’ that an individual develops the outcome during a specified time-
period, to the ‘risk’ that the individual does not develop the outcome during that same
time-period. Below you can see how this simplifies mathematically to the equation
given above, as the denominator (total number at risk) is the same for both outcomes,
and cancels-out:
23346.indb 1923346.indb 19 22/08/2011 15:1222/08/2011 15:12

Odds =
Cases
÷
Non-cases
=
Cases
×
Total
=
Cases
Total Total Total Non-cases Non-cases
In the example, in which 75 people in a group of 100 caught a cold during a particular
year,the odds of catching a cold would be calculated as 75 ÷ 25 = 3.The odds of catch-
ing a cold would be 3 to 1, sometimes reported as 3:1, so that a person in that group
would be three times more likely to catch a cold as not to catch a cold during that year.
Incidence rate and person-time at risk
Both risk and odds assume that the population at risk is followed over a speciﬁed time-
period, and that all those who are included at the beginning of the time-period are
counted at the end of the time-period.This is called a closed population. However, you
might want to look at incidence in a dynamic or open population,in which people enter
and exit the population at risk at different points and are therefore at risk for different
lengths of time.Once the outcome has occurred,the individual will either no longer be
at risk or, if the outcome can recur, there will be some interval of time before the
individual is once more considered at risk. Therefore, instead of counting the total
number of people at the start of the study, the time that each individual is at risk is
calculated.This is known as the person-time at risk and is illustrated in Figure 2.1.
People may start and stop being at risk at different times, due to births and deaths,
immigration, acquiring the outcome, leaving the study population before the end
(known as ‘lost to follow-up’), or reaching the end of the observation period.
Figure 2.1 Graphical representation of person-time at risk for 9 study participants during a 6-year study
period
Source: Bailey et al. (2005).
The incidence rate allows us to account for variation in time at risk, and is
calculated as the number of new cases divided by the total person-time at risk:
23346.indb 2023346.indb 20 22/08/2011 15:1222/08/2011 15:12

Incidence rate =
Total person – time at risk during that time-period
This measure is a rate and is reported as the number of new cases per person-time at
risk. It is essential to specify the time units, for example person-days, person-months,
person-years, or more frequently 1,000 person-years at risk.
In Figure 2.1, the incidence rate is obtained by dividing the total number of cases by
the total number of person-years at risk. Four people became cases during the study,
so the incidence rate is 4 ÷ 40.5 = 0.099 cases per person-year at risk, or 99 cases per
1,000 person-years at risk (to avoid the use of too many decimal places).
In registry data or very large studies it might be difficult to know the exact person-
time at risk for each individual in the population. In this situation, the population at the
mid-point of the time-period of interest is multiplied by the period of time under
consideration to give an estimate of the person-time at risk, so long as the population
size does not change substantially over the study period. For example, data from a
cancer registry (a record of all cancer cases notified by doctors) found 750 cases of
breast cancer in a region of a politically-stable country between 2005 and 2010.
The population of that region was recorded from a census to be 10,130 in 2007–2008.
The person-time at risk is estimated as the mid-period population multiplied by the
five-year period at risk. The incidence is calculated as 750 ÷ (10,130 × 5) =
750 ÷ 50,650 = 0.015 per person-year at risk, or to reduce loss of precision due to
rounding, 0.0148 × 1,000 = 14.8 cases of breast cancer per 1,000 person-years at risk
between 2005–2010.
Activity 2.1
Investigators were asked to determine the prevalence of malaria cases in two villages in
rural Southeast Asia. There were 500 people (210 men and 290 women) in the two
villages.Investigators spent a couple of days in November testing everyone in the villages
for malaria, using rapid diagnostic tests (which detect malaria parasite-specific proteins
in blood). Investigators found that 62 men and 22 women tested positive for malaria.
1 Write a simple case definition investigators could have used in this study.
2 Define the study population.
3 Based on your case definition and study population, what is the malaria prevalence
among men and among women in the villages?
Activity 2.2
An outbreak of human monkeypox,a relatively rare orthopox viral disease similar to but
milder than smallpox,was detected in a forested province of the Democratic Republic of
Congo (DRC). Investigators found 5 secondary cases of monkeypox among 37 house-
hold contacts of a 9-year-old boy who was the first reported to have become infected.
1 Assuming all household contacts are equally at risk,what is the secondary attack rate
among household contacts?
2 Data from previous outbreaks suggests that prior smallpox vaccination confers 85%
protection from monkeypox. If all household contacts had been vaccinated against
smallpox, how would this change your secondary attack rate calculation?
23346.indb 2123346.indb 21 22/08/2011 15:1222/08/2011 15:12

Activity 2.3
Investigation of an outbreak of measles,in remote District X,found 12 cases of measles
had occurred among 350 children attending a local school over a one-month period.
Each infected child came from a different household.The total number of additional
children (i.e. household child contacts) in the 12 affected households was 67. Ten
children in the affected households had previously had measles, while 20 children were
reported to have received at least one dose of measles vaccine.However,immunization
records were poor and many children had not been fully immunized. One month
(i.e. approximately two incubation periods) later, four more children in the 12 affected
households also developed measles.
1 What was the risk of measles in the school during the initial one-month period?
2 What is the secondary attack rate among household child contacts of the 12 children?
3 What does this tell us?
Activity 2.4
Investigators conducted a survey of intestinal worm infestation among 1,000 adoles-
cent agricultural workers in CountryY.They found 620 adolescents were infested with
one or more type of worm.After treating all adolescents found positive, investigators
returned six months later and tested all 1,000 adolescents again.This time they found
390 adolescents infested.
1 Calculate the prevalence of worm infestation among adolescents in the ﬁrst survey.
2 Calculate the risk and the odds of worm infestation among adolescents during the
six-month study period.
3 What is the incidence rate of worm infestation among adolescents during the
six-month study period?
Activity 2.5
One thousand men working in factoryA were screened for HIV on 1 January 2010 and
50 of them were found to be HIV-positive.When the screening was repeated on the
same 1,000 men on 1 January 2011, 62 men were positive, including the 50 men who
were positive on the ﬁrst screening. Nobody had died or been lost to follow-up.
1 What is the prevalence of HIV in men working in factory A on 1 January 2010, and
on 1 January 2011?
2 What is the annual risk of developing HIV infection in men working in factory A
during 2010?
3 What are the odds of developing HIV infection in men working in factory A during
2010?
Activity 2.6
One thousand men in factory B were screened for HIV on 1 January 2010 and 50 men
were found to be HIV-positive.All of these men were tested for HIV at the end of each
month until 31 December 2010.Twelve men became HIV-positive during this period,
23346.indb 2223346.indb 22 22/08/2011 15:1222/08/2011 15:12

Conclusion
You have been introduced to the measures of prevalence and incidence (risk, odds and
incidence rate) that are used to quantify the occurrence of an outcome in a deﬁned
population.These epidemiological measures of frequency help in assessing the public
health importance of an outcome and planning appropriate health services. These
measures also form the basis of analytical studies to investigate the association between
exposures and outcomes.
Reference
Bailey L, Vardulaki K, Langham J and Chandramohan D (2005) Introduction to Epidemiology 1st edn.
Maidenhead: Open University Press.
Figure 2.2 Person-months at risk of HIV in factory B in 2010
while the remaining 938 men were still HIV-negative by 31 December 2010. Figure 2.2
shows when these 12 men became HIV-positive.Nobody died or was lost to follow-up
during this period.
1 What is the total number of person-months at risk of HIV infection observed in this
study?
2 What is the incidence rate of HIV infection among men working in factory B?
3 What are the odds of becoming infected with HIV in the ﬁrst six months of 2010
compared with becoming infected in the last six months of 2010?
23346.indb 2323346.indb 23 22/08/2011 15:1222/08/2011 15:12

Activity 2.1
1 You may have said that cases could have been defined as those individuals resident in
one of the two villages who tested positive for malaria by rapid diagnostic test during
the two days in November.
2 The study population includes all 500 individuals in the two study villages. There
were 210 men and 290 women.
3 The number of prevalent cases among men is 62. There were 210 men tested.
Therefore, the prevalence of malaria in men is 62/210 × 100 = 0.295 × 100 = 30%.
The number of prevalent cases among women is 22.There were 290 women tested.
Therefore,the prevalence of malaria in women is 22/290 × 100 = 0.076 × 100 = 7.6%.
Activity 2.2
1 The number of cases of monkeypox among secondary contacts = 5.The total number
of secondary household contacts = 37. Therefore, the secondary attack rate = 5 ÷ 37
× 100 = 0.135 × 100 = 13.5%.
2 The total number of secondary household contacts estimated to be unprotected by
vaccination = 37 – (37 × 0.85) = 37 – 31.45 = 5.55 (i.e.6) unprotected household con-
tacts.The number of cases of monkeypox among secondary contacts = 5.
To calculate the secondary attack rate in this scenario we divide the number of
cases among secondary contacts by the number of unprotected household contacts =
5 ÷ 5.55 × 100 = 0.90 × 100 = 90%.This would indicate a dramatically more virulent
monkeypox strain than did the first scenario.
Activity 2.3
1 The number of cases of measles among children at the school = 12.The total number
of children at the school = 350.Therefore, the incidence risk = 12 ÷ 350 × 100 =
0.34 × 100 = 3%.
2 The number of secondary cases of measles among household child contacts of
the 12 children is 4.The total number of children at risk in the affected households
= (total number of contacts – previous measles cases) = 67 – 10 = 57.Therefore,the
secondary attack rate among unvaccinated child contacts is the number of cases
among household child contacts out of those child contacts who are actually known
to be at risk (i.e. not already a case) = 4 ÷ 57 × 100 = 0.0702 × 100 = 7%.
In reality, there may be a higher number of contacts immune to measles through
vaccination or prior disease.
3 An initial risk of (3%) and a secondary attack rate of (7%) indicate that the outbreak
is increasing or that transmission is more efficient within households than within the
school.As measles can be prevented by vaccination, the increase in cases suggests
that vaccination coverage is insufficient and a mass measles vaccination campaign
should be organized.
Activity 2.4
1 The number of prevalent cases in the first survey = 620.The total number of adoles-
cents tested is 1,000.Therefore, the prevalence of infestation among adolescents in
the first survey is (620 ÷ 1,000) × 100 = 0.62 × 100 = 62%.
23346.indb 2423346.indb 24 22/08/2011 15:1222/08/2011 15:12

2 The number of incident cases in the second survey = 390. The total number of
adolescents tested is 1,000. Therefore, the risk of infestation among adolescents
during the six-month period is (390 ÷ 1,000) × 100 = 0.39 × 100 = 39%.The number
of cases in the second survey = 390. The number of adolescents who are not
cases = 1,000 – 390 = 610.Therefore, the odds of infestation among adolescents dur-
ing the six-month period are (390 ÷ 610) × 100 = 0.64 × 100 = 64%.
3 The number of incident cases in the second survey = 390.As we do not know how
many months each adolescent contributed to person-time at risk, we need to use
the mid-period population, calculated as the average of the population at start and
end of the study (i.e. (1,000 + 1,000)/2 = 1,000, thus 1,000 × 6 = 6,000 person-
months), and assume that the adolescents did not leave the study area for signiﬁcant
periods during the six-month period. Therefore, the incidence rate of infestation
among adolescents is estimated as (390 ÷ 6,000) × 1000 = 0.065 × 1000 = 65 per
1,000 person-months.
Activity 2.5
1 The number of prevalent cases at 1 January 2010 = 50.The total number of individu-
als tested in this population on 1 January 2010 = 1,000.Therefore, the prevalence at
1 January 2010 = (50 ÷ 1,000) × 100 = 5%.
The number of prevalent cases at 1 January 2011 is 62.The total number of indi-
viduals tested in this population at 1 January 2011 is 1000.Therefore, prevalence at
1 January 2011 = (62 ÷ 1000) × 100 = 6.2%.
2 The number of incident (new) cases in 2010 is 62 – 50 = 12. The number of
individuals at risk of HIV infection on 1 January 2010 = 1000 – 50 = 950.Therefore,
the annual risk of developing HIV infection in 2010 = (12 ÷ 950 ) × 100 = 1.26%.
The 50 men who were HIV-positive on 1 January 2010 are not included in the
denominator because HIV-positive individuals do not become HIV-negative.
Therefore those who were HIV-positive on 1 January 2010 were not at risk of devel-
oping HIV infection during 2010.
3 The number of incident cases during 2010 is 62 – 50 = 12.The number of individuals
at risk of HIV infection in 2010 who did not become infected is 950 – 12 = 938.
Therefore, the odds of developing HIV infection in 2010 = 12 ÷ 938 × 100 = 1.28%.
Activity 2.6
1 To calculate total person-months at risk, add total person-months contributed by
men who remained HIV-negative and total person-months contributed while they
were HIV-negative by men who subsequently became infected (as men who were
already infected at the beginning of study do not contribute any person-months
at risk).
Person-months at risk for men who remained HIV-negative throughout the study
period = 938 × 12 = 11,256. Person-months at risk for the 12 men infected during
the study period = 1 + (3 × 4) + 5 + (2 × 6) + 8 + 9 + (2 × 11) + 12 = 81.Therefore,
total person-months at risk during the study period = 11,256 + 81 = 11,337.
Another way to look at this is that, as we do not know when exactly these men
became infected, it would be more accurate to assume that ‘on average’ they con-
tributed only 0.5 months at risk for the month prior to testing HIV-positive. Using
this approach, total person-months at risk for the 12 men infected during the
study period = 0.5 + (3 × 3.5) + 4.5 + (2 × 5.5) + 7.5 + 8.5 + (2 × 10.5) + 11.5 = 75.
23346.indb 2523346.indb 25 22/08/2011 15:1222/08/2011 15:12

Using this approach, total person-months at risk during the study period would be
11,256 + 75 = 11,331. In this particular example, as the overall person-time at risk is
large, this will not make a difference to our estimate of incidence rate below.
2 To calculate an incidence rate, select an appropriate unit of person-time at risk for
the denominator. In this example, person-months is an appropriate unit, as time at
risk is already segmented into months and person-months contributed can be calcu-
lated easily from Figure 2.2.
Total number of incident cases = 12. Total person-months = 11,337. Therefore,
incidence rate = (12 ÷ 11,337) × 1,000 = 1.06 per 1,000 person-months.
3 To calculate odds, divide the number of men who became HIV-positive in the first
half of 2010 by the number who did not (i.e. who became positive in the second half
of 2010).
Number of men who became HIV-positive in the first six months of 2010 = 7.
Number of men who did not become HIV-positive during first six months = 5.
Therefore, of those who became HIV-positive in 2010, the odds of becoming HIV-
positive in the first 6 months = 7/5 = 1.4. In other words, among those who became
HIV-positive in 2010, the odds of becoming infected in the first half of the year were
40% higher (difference from an odds of 1, i.e. 1.4 – 1.0 = 0.4 or 40%) than the odds
of becoming infected in the second half of the year.
23346.indb 2623346.indb 26 22/08/2011 15:1222/08/2011 15:12

Overview
Analytical epidemiology is concerned with quantifying the association between an expo-
sure and an outcome,to establish causal relationships and identify effective interventions.
This chapter presents different ways to measure the association between an exposure
and an outcome, and you will be introduced to several new terms and formulae.
First,relative measures of association use the frequency measures you learned about in
the previous chapter to compare the frequency of outcomes in different exposure groups.
These take the form of ratios:prevalence ratio,risk ratio,odds ratio and incidence rate ratio.
Second, you will be introduced to measures of impact: attributable risk, attributable
fraction, population attributable risk and population attributable fraction. Evidence of
an association between a modifiable exposure and an outcome can be used to assess
potential impact, i.e. the additional burden of outcome due to the exposure that may
be prevented if that exposure is removed.
Learning objectives
• recognize different measures of association:prevalence ratio,risk ratio,odds ratio
and incidence rate ratio
• recognize different measures of impact: attributable risk, attributable fraction,
population attributable risk, population attributable fraction
• define, calculate and interpret each of these measures of association and impact
• identify the appropriate measure of association for a given epidemiological objective.
Relative measures of association
Relative measures estimate the extent (strength) of an association between an expo-
sure and an outcome.The relative measures that use ratios to compare the frequency
of an outcome are prevalence ratio,risk ratio,odds ratio and incidence rate ratio.These
are collectively referred to as measures of relative risk. However, it is good practice
to refer to specific relative risk measures by name,to avoid confusing the term‘relative
risk’ with the specific ‘risk ratio’ measure.
Relative risk measures indicate how much more likely it is that an exposed individual
will develop the outcome compared with an unexposed individual. If the relative risk is
greater than one, then exposed individuals are at greater risk. If the relative risk equals
one, there is no difference in risk between the exposed and unexposed. If the relative
risk is less than one, exposed individuals are at a lower risk, and the exposure can be
called a protective factor. Table 3.1 illustrates the standard format for presenting
3Measures of association
and impact
23346.indb 2723346.indb 27 22/08/2011 15:1222/08/2011 15:12

Prevalence ratio
The prevalence ratio can be calculated from cross-sectional studies or population
surveys. In practice, this is the least useful of the measures described in this chapter as
the exposure and the prevalence of the outcome are measured at the same time point,
making it difﬁcult to infer causality.We cannot distinguish whether an associated factor
has caused the outcome to occur or has simply caused it to persist as a prevalent case.
It is calculated as the prevalence in exposed individuals divided by the prevalence in
unexposed individuals:
Prevalence ratio =
Prevalence of outcome in the exposed group
Prevalence of outcome in the unexposed group
If Table 3.1 is taken to represent the number of existing cases by exposure group
detected at one time point, the overall prevalence of the outcome in the sample popu-
lation is calculated as (a+c)/(a+b+c+d).The prevalence in the exposed group is given by
a/(a + b) and the prevalence in the unexposed group is given by c/(c + d), so the preva-
lence ratio is calculated as:
Prevalence ratio =
a/(a + b)
c/(c + d)
It is not necessary to know the actual number of cases or the total number of
individuals, as long as the prevalence in each exposure group is known. For example,
you are told that the prevalence of obesity, deﬁned as body mass index greater than
30 kg/m2
, is 20% in people reporting that they do less than 2 hours of exercise per
week, and 10% in those reporting that they do at least 2 hours of exercise per week.
The prevalence ratio for obesity can be calculated as 0.10 ÷ 0.20 = 0.50 in those
‘exposed’ to at least 2 hours of exercise per week.This can be interpreted as exposed
individuals being 0.50 times or half as likely to be obese as those unexposed.The ratio
can also be inverted as 0.20 ÷ 0.10 = 2.0,such that those‘exposed’ to less than 2 hours
of exercise are twice as likely to be obese as those unexposed.
Risk ratio
The risk ratio can be calculated from ecological, cohort or intervention studies.The
risk ratio is calculated as the risk (cumulative incidence) of the outcome in the exposed
comparative data in an epidemiological study and will be used to clarify the differences
between the different measures of relative risk.
Table 3.1 Standard cross-tabulation (2 × 2 table) of
outcome by exposure
Outcome
Yes No Total
Exposed a b a + b
Unexposed c d c + d
Total a + c b + d a + b + c + d
Exposure
23346.indb 2823346.indb 28 22/08/2011 15:1222/08/2011 15:12

Measures of association and impact 29
group divided by the risk (cumulative incidence) of the outcome in the unexposed
group:
Risk ratio =
Risk of outcome in the exposed group
Risk of outcome in the unexposed group
IfTable 3.1 is taken to represent the number of new (incident) cases by exposure group
detected during a deﬁned time-period, the overall risk of the outcome in the sample
population can be calculated as (a+c)/(a+b+c+d).You will see that these equations are
identical to those for prevalence, because risk is also a proportion as discussed in the
previous chapter, but are applied to incident cases.The risk in the exposed group is
given by a/(a + b) and the risk in the unexposed group is given by c/(c + d), so the risk
ratio can be calculated as:
Risk ratio =
a/(a + b)
c/(c + d)
For example,a cohort study observed that 20 out of 50 children who regularly washed
their hands with soap after defecation had at least one episode of diarrhoea during the
study period, compared with 20 out of 40 children who did not.The risk ratio can be
calculated as (20 ÷ 50)/(20 ÷ 40) = 0.4 ÷ 0.5 = 0.80.This is interpreted as children who
practise hand washing with soap being 0.8 times as likely to have diarrhoea than those
who do not practise hand washing with soap.When the relative risk is lower than one,
we often subtract it from one to report the difference,so in this example we might say
that those who washed hands with soap have a 1 – 0.8 = 0.2 times, or 20%, lower risk
than those who did not wash hands with soap.
Odds ratio
The odds ratio can also be calculated from ecological, cohort or intervention studies.
It is calculated as the odds of the outcome in the exposed group divided by the odds
of the outcome in the unexposed group:
Odds ratio =
Odds of outcome in exposed group
Odds of outcome in unexposed group
Referring to Table 3.1, the odds of cases in the total population are calculated as
(a + c)/(b + d).The odds in the exposed group are a/b and the odds in the unexposed
group are c/d so the odds ratio can be calculated as follows:
Odds ratio =
a/b
c/d
When a fraction is divided by a fraction, it can be simpliﬁed by multiplying the top and
bottom of the equation by the denominators b and d:
Odds ratio=
a/b
×
b × d
=
ad
c/d b × d bc
A variant and more frequently used version is the odds ratio of exposure. This
is used in a case-control study because individuals are selected on the basis of their
outcome status and the incidence of the outcome cannot be measured (see Chapter
9). It is calculated as the odds of exposure in individuals with the outcome divided by
the odds of exposure in individuals without the outcome:
23346.indb 2923346.indb 29 22/08/2011 15:1222/08/2011 15:12

Odds ratio of exposure =
Odds of exposure in those with the outcome
Odds of exposure in those without the outcome
Referring to Table 3.1, the odds of exposure in those with the outcome is a/c, and the
odds of exposure in those without the outcome is b/d,so the odds ratio of exposure is:
a/c
=
a/c
×
c × d
=
ad
b/d b/d c × d bc
As you can see,the odds ratio of exposure is mathematically the same as the odds ratio
of outcome given above.The odds ratio of exposure is therefore used as an estimate
of the relative risk of an outcome in case-control studies.
However,it is important not to use the terms interchangeably,as their definitions are
very different.You can practise preparing 2×2 tables using the same format asTable 3.1,
to work through the following examples.
One thousand mothers of newborns in a Sub-Saharan African country were asked
about their level of education, of which 400 had completed primary education.After
one year, there were 16 deaths among infants ‘exposed’ to mothers who had com-
pleted primary education and 48 deaths among ‘unexposed’ infants.The odds ratio of
outcome can be calculated as (16 ÷ 384)/(48 ÷ 552) = 0.48.Again, as this is less than 1,
we calculate the difference from 1 as 1 – 0.48 = 0.52 and interpret it as 52% lower
(than 1) odds of dying in infancy among those born to mothers who had completed
primary education compared with those who had not.
In a case-control study in the same country,100 infant deaths were identified among
hospital admissions, and 100 infants who survived were selected for comparison from
admissions to the same hospital. In a questionnaire conducted at admission, 20 of
the mothers of infants who subsequently died reported that they had completed
primary education, compared with 35 of the mothers of infants who survived. The
odds ratio of exposure to maternal primary education can be calculated as (20 ÷ 80)/
(35 ÷ 65) = 0.250 ÷ 0.538 = 0.46.This can be reported as 1 – 0.46 = 0.54 or 54% lower
odds of having a mother who had completed primary education among infants who
died compared with those who survived.While we know that this is mathematically
equivalent to the odds ratio of outcome, we cannot calculate the odds ratio of
outcome.This is because we do not know the odds or likelihood of the outcome in
the study population,having specifically selected infants for the study because they died
in infancy.
Incidence rate ratio
The incidence rate ratio can be obtained from ecological, cohort or intervention
studies. It is calculated as the incidence rate of the outcome in the exposed group
divided by the incidence rate of the outcome in the unexposed group:
Incidence rate ratio =
Incidence rate of outcome in the exposed group
Incidence rate of outcome in the unexposed group
Referring again to Table 3.1, the column for ‘no outcome’ would in this instance refer
to the person-time at risk. The incidence rate of the outcome in the total sample
population can then be calculated as (a+c)/(b+d).The incidence rate in the exposed
group is a/b and the incidence rate in the unexposed group is c/d. As with the odds
ratio, the incidence rate ratio can be simplified as follows:
23346.indb 3023346.indb 30 22/08/2011 15:1222/08/2011 15:12

a/b
=
ad
c/d bc
We use incidence rate ratio in studies where people are entering and leaving the study
population or have changing levels of exposure.As an example, we might want to find
out whether miners are at a higher risk of tuberculosis.We would compare the inci-
dence rate of tuberculosis in miners (exposed group) with the incidence rate in non-
miners (unexposed group). Since the miners will have worked for different lengths of
time, the number of person-years at risk can be used to calculate the incidence rate in
each group. If the incidence of tuberculosis in miners is 3 cases per 100 person-years
and the rate for non-miners is 0.6 cases per 100 person-years, the incidence rate ratio
is calculated as 3 ÷ 0.6 = 5.This can be interpreted as the incidence of tuberculosis
being five times as high in miners as in non-miners.
Comparability of measures of association
For common diseases (e.g. most infectious diseases), the estimates obtained may differ
substantially, however, for very rare outcomes (e.g. most cancers, congenital malforma-
tions) these measures will be very similar.To demonstrate this, if we complete Table 3.1
with five cases among 5,005 exposed and 1 case among 10,001 unexposed, then we
calculate:
• prevalence ratio = (5 ÷ 5,005)/(1 ÷ 10,001) = 0.000999 ÷ 0.00009999 = 9.99
• risk ratio = (5 ÷ 5,005)/(1 ÷ 10,001) = 0.000999 ÷ 0.00009999 = 9.99
• odds ratio of outcome = (5 ÷ 5,000)/(1 ÷ 10,000) = 0.001 ÷ 0.0001 = 10.00
• odds ratio of exposure = (5 ÷ 1)/(5,000 ÷ 10,000) = 5 ÷ 0.5 = 10.00
• incidence rate ratio = (5 ÷ 5,005)/(1 ÷ 10,001) = 0.000999 ÷ 0.00009999 = 9.99
The rarer the outcome,the more the denominator for the odds resembles the denom-
inator for the risk,and the more similar are the measures of association.If the exposure
were more common, then this would be even more so. For example, if there were five
cases among 10,005 exposed and 1 case among 10,001 unexposed, we can calculate:
• risk ratio = (5/10,005)/(1/10,001) = 0.00049975 ÷ 0.00009999 = 4.998
• odds ratio of outcome = (5/10,000)/(1/10,000) = 0.0005 ÷ 0.0001 = 5.00
You will often see the odds ratio (of outcome) presented in a study that has measured
prevalence or risk. It is used to approximate the prevalence ratio or risk ratio because
of its role in complex statistical models for analysis (see Chapter 5). However, it is
worth remembering that this approximation is only valid for a very rare outcome, and
the odds ratio will tend to overestimate the prevalence ratio or risk ratio if the out-
come is not sufficiently rare.
Activity 3.1
Investigators followed a population of 2,000 women aged over 65 years who did
not have osteoporosis, over a 10-year period and measured the number of cases of
osteoporosis diagnosed during that time-period.The investigators were interested in
the effect of regular exercise on the development of osteoporosis.They divided the
23346.indb 3123346.indb 31 22/08/2011 15:1222/08/2011 15:12

women into two groups: 1,000 women who exercised regularly (exposed) and 1,000
women who did not exercise regularly (unexposed).
During the 10-year study period,investigators recorded 800 new cases of osteoporosis,
300 in those women who exercised regularly and 500 in those who did not.The number
of person-years at risk was 8,350 in the exposed group and 6,950 in the unexposed group.
1 Calculate the risk ratio, odds ratio and incidence rate ratio for the effect of regular
exercise on osteoporosis in these women and provide a one-sentence interpreta-
tion for each result.
2 Contrast the ﬁndings of these measures of association, and discuss which measure
is most appropriate.
Investigators then conducted another study of osteoporosis in women aged under
55 years old.They followed 1,000 women who exercised regularly and 1,000 women
who did not for 10 years.They recorded 3 cases of osteoporosis in those who exer-
cised regularly and 5 cases in those who did not.The number of person-years at risk
was 9,500 in the exposed group and 9,000 in the unexposed group.
3 Again, calculate the risk ratio, odds ratio and incidence rate ratio for the effect of
regular exercise on osteoporosis in these 2,000 younger women, and provide a one-
sentence interpretation for each of these results.
4 Describe differences you see in the results from the two studies.
You have been introduced to several important new concepts that form the basis
of epidemiology.You may ﬁnd it useful to take time to digest this information before
continuing with the rest of this chapter.
23346.indb 3223346.indb 32 22/08/2011 15:1222/08/2011 15:12

Measures of attributable risk
Relative measures are useful when we want to know how strongly an exposure is
associated with a particular outcome, but they do not give any indication of the real
impact of exposure on the incidence of outcome in a specific population. Imagine that
the risk of mortality due to outcome A is six times greater in those exposed to factor
A, and similarly the mortality due to outcome B is six times greater in those exposed
to factor B.The incidence rate ratio is equal for both outcomes (see Table 3.2).
Table 3.2 Comparison of mortality rates for two outcomes
Epidemiological measure Outcome A Outcome B
Incidence rate in exposed 6 per 1,000 person-years 30 per 1,000 person-years
Incidence rate in unexposed 1 per 1,000 person-years 5 per 1,000 person-years
Incidence rate ratio 6 ÷ 1 = 6.0 30 ÷ 5 = 6.0
Source: Ilona Carneiro, modified from Bailey et al. (2005).
However, it is clear from Table 3.2 that the health impact of the exposure to factor
B is greater than exposure to factor A because the underlying mortality rate is greater
for outcome B than outcome A.The measure of relative risk is unable to capture this
important difference,and we need to use different measures that take into account the
incidence of the outcome.
Attributable risk is the excess incidence of the outcome that we can‘attribute’ to
the exposure, if we assume a causal association between the exposure and outcome. It
is calculated by subtracting the underlying incidence (as a risk or a rate) of outcome in
unexposed individuals from that in exposed individuals in the same population:
Attributable risk = Incidence in exposed – Incidence in unexposed
In the example above (Table 3.2), the incidence rate of outcome A that is attributable
to the exposure is calculated as 6 – 1 = 5 deaths per 1,000 person-years at risk,
while the incidence of outcome B that is attributable to the exposure is calculated as
30 – 5 = 25 deaths per 1,000 person-years at risk. This measure of attributable risk
reveals the relative importance of the two exposures, based on the underlying
incidence of the outcomes and is useful for comparing individual-level risks.How much
worse is it for an individual in this population to be exposed to factor B than factor
A? Although the relative risk of death is six times greater for exposure to either risk
factor, the actual risk of death is five times greater (25 ÷ 5 = 5) if an individual is
exposed to factor B than if they are exposed to factor A.
The attributable fraction is the proportion (fraction) of the outcome in exposed
individuals that can be attributed to the exposure, and is calculated as:
Attributable fraction =
Incidence in exposed – Incidence in unexposed
Incidence in exposed
or
Attributable risk
Incidence in exposed
23346.indb 3323346.indb 33 22/08/2011 15:1222/08/2011 15:12

In the example fromTable 3.2,the attributable fraction for outcomeA is (6 – 1) ÷ 6 = 0.83,
i.e.83% of deaths from outcomeA can be attributed to exposure to factorA.This means
that 83% of deaths from outcomeA could be prevented if we were able to remove expo-
sure to factor A completely. For outcome B, the attributable fraction is (30 – 5) ÷ 30 =
0.83, so 83% of deaths from outcome B can be attributed to exposure to factor B.
The attributable fraction is the same for both outcomes because it is related to the
relative risk (risk ratio or incidence rate ratio) in the following way:
Relative risk – 1
Relative risk
In the example from Table 3.2 this can be calculated as (6 – 1) ÷ 6 = 0.83, i.e. 83% for
both outcomeA and B.This is a useful approach if we do not know the actual incidence
of the outcome.
For a protective factor where the incidence among the unexposed is greater than the
incidence in the exposed, we calculate the preventable fraction as:
Preventable fraction =
Incidence in unexposed – Incidence in exposed
Incidence in unexposed
This refers to the proportion of outcome incidence that can be prevented by a protec-
tive factor (e.g. genetic attribute) and can also be calculated from the relative risk:
Preventable fraction = 1 – Relative risk
When used to describe an intervention (e.g. a vaccine against an infectious disease),
this may be referred to as the protective efﬁcacy (see Chapter 10).
Population attributable risk and fraction
We may want to apply the measures of relative risk or attributable risk from an epide-
miological study to a real population to enable appropriate public health planning.The
population attributable risk (PAR) is the incidence of outcome in the population
(i.e. exposed and unexposed to the risk factor) that can be attributed to the exposure
of interest if we assume causality. It is calculated as the difference (excess risk) in inci-
dence between the population and those individuals unexposed to the risk factor:
Population attributable risk = Incidence in population – Incidence in
unexposed
For example, a study of the effect of chronic hepatitis B infection on liver cancer found
the following results:the incidence rate of liver cancer was 4 per 100,000 person-years
in those without chronic hepatitis B infection and 94 per 100,000 person-years in the
entire population.The population attributable risk of exposure to chronic hepatitis B
was calculated as 94 – 4 = 90 per 100,000 person-years.This can be interpreted as 90
per 100,000 liver cancer cases in this study population can be attributed to chronic
hepatitis B infection,and could be avoided if hepatitis B infection were to be eliminated
from the population.
The population attributable fraction (PAF) is therefore the proportion (fraction)
of the outcome in the population that is attributable to the exposure,and is calculated as:
Population attributable fraction =
Incidence in population – Incidence in unexposed
Incidence in population
23346.indb 3423346.indb 34 22/08/2011 15:1222/08/2011 15:12

or
Population attributable risk
Incidence in population
For the study of liver cancer described above, we can calculate the PAF as (94 – 4) ÷
94 = 0.96, so 96% of liver cancer cases in the population are attributable to chronic
hepatitis B infection.
The PAF can also be expressed in terms of the relative risk, as long as the propor-
tion of the total population exposed to the risk factor (‘p’) is known:
p × (Relative risk – 1)
p × (Relative risk – 1) + 1
In the example above,the researchers found the rate of liver cancer in the study sample
to be 602 per 100,000 person-years in those with chronic hepatitis B infection and
4 per 100,000 person-years in those without hepatitis B. The prevalence of chronic
hepatitis B infection in the general population was 15%. If the incidence rate of liver
cancer in the general population had not been known, they could have calculated the
incidence rate ratio as 602 ÷ 4 = 150.5.An incidence rate ratio of 150.5 is huge, but it
is difficult to translate such a figure into real public health impact.The PAF calculated
from the relative risk is (0.15 × (150.5 – 1)) ÷ (0.15 × (150.5 – 1) + 1) = 22.425 ÷
23.425 = 0.96. This suggests that 96% of liver cancer cases could be eliminated
if chronic hepatitis B infection could be eliminated, assuming that the association is
causal. Note that there are often several risk factors for an outcome that may overlap
or interact (component causes – see Chapter 1), such that reducing exposure to
one risk factor may result in an increase in the proportion of cases due to another risk
factor.
The comparative value of the attributable fraction and the population attributable
fraction can be illustrated by the following hypothetical example.A study determined
the risk of repetitive strain injury (RSI) to the hand in office workers to be 4 per 100
over a one-year period.Among those who used a computer keyboard for more than
5 hours a day, this risk was 10 per 100 person-years, while for those who used a com-
puter keyboard for less than 5 hours the risk was 3 per 100 person-years.The attribut-
able fraction identifies the proportion of RSI due to using a computer keyboard among
those who use keyboards, and is calculated as (10 – 3) ÷ 10 = 0.70 or 70%. The
population attributable fraction identifies the proportion of RSI due to using a
computer keyboard for more than 5 hours a day among all the office workers,
calculated as (4 – 3) ÷ 4 = 0.25 or 25%. In considering whether to invest in ergonomic
keyboards, the employer may not consider a 25% increased risk in RSI overall to be of
sufficient importance, whereas the individual would consider a 70% increase in their
own risk of RSI to be considerable.This would advocate for a workstation assessment
followed by a needs-based provision of ergonomic keyboards.
Activity 3.2
Between 1951 and 1971, a total of 10,000 deaths were recorded among 34,440 male
British doctors (Doll and Peto 1976). Of these deaths, 441 were from lung cancer and
3,191 were from ischaemic heart disease (IHD). Doctors who smoked at least one
cigarette per day during this follow-up period were classified as smokers and the rest
23346.indb 3523346.indb 35 22/08/2011 15:1222/08/2011 15:12

as non-smokers. The age-adjusted annual death rates per 100,000 male doctors for
lung cancer and IHD among smokers and non-smokers are given in Table 3.3. (Note
that this is a comparative table, not a 2×2 table of outcome by exposure.)
Table 3.3 Cause of death and speciﬁc death rates by smoking habits of British male doctors, 1951–71
Annual death rate per 100,000 doctors
Cause of death Non-smokers Smokers
Lung cancer 10 140
Ischaemic heart disease 413 669
Source: Doll and Peto (1976).
1 Calculate an appropriate epidemiological measure to assess the strength of associa-
tion between smoking and lung cancer, and smoking and IHD.
2 Based on your calculation, which of the two diseases is most strongly associated
with smoking?
3 Reduction in mortality from which of the two diseases would have greater public
health impact if there were a reduction in smoking? Calculate and interpret an
appropriate epidemiological measure and list the assumptions you would make
when estimating the impact of a reduction in smoking.
4 Assuming that the data shown in Table 3.3 are valid and that smoking causes lung
cancer, how much of the mortality from lung cancer could be attributable to smok-
ing? Assuming that smoking is one of the causes of IHD, how much of the mortality
from IHD could be attributable to smoking?
Activity 3.3
A separate case-control study was conducted to investigate the risk factors for myo-
cardial infarction. Information on smoking was collected from cases and controls. Sixty
of the 400 myocardial infarction cases reported current cigarette smoking, deﬁned as
smoking within the past 3 months, compared with 40 of the 400 healthy controls.
1 Set up a 2×2 table showing the information above.
2 Calculate and interpret an appropriate measure to estimate the strength of the
association between current cigarette smoking and myocardial infarction.
Activity 3.4
The incidence of tuberculosis and the mid-year population of different ethnic groups in
a European country, country Z, in 2011 are given in Table 3.4.
1 Calculate the incidence rate and rate ratio for each ‘exposure’ group, using the
European group as the reference (‘unexposed’) group.
2 Based on your calculations, which group is most strongly associated with tuberculo-
sis in this study?
23346.indb 3623346.indb 36 22/08/2011 15:1222/08/2011 15:12

3 Explain why the number of tuberculosis cases is greater in the European group even
though the incidence rate is lower than in the other two groups.
4 The incidence rate for the entire population is 7.08 per 100,000 person-years. If you
assume that a targeted intervention could reduce the incidence rate in all groups to
the level of that in the European group (4.13 per 100,000 person-years), what
percentage of tuberculosis cases in each group would be prevented?
5 If a targeted intervention reduced the incidence rate in all groups to that of the
European group, what percentage of tuberculosis cases in the whole population
would be prevented?
Conclusion
You have been introduced to the relative measures (prevalence ratio, risk ratio, odds
ratio and incidence rate ratio) that are used to quantify the association between an
exposure and an outcome.These measures are the foundation of analytical epidemiol-
ogy, and you will have the opportunity to consider them in context in subsequent
chapters relating to specific study designs.You have also been introduced to measures
of impact (attributable risk, attributable fraction) and population measures of impact
(population attributable risk and population attributable fraction) that are needed to
translate research findings into information of public health value.
References
Bailey L,Vardulaki K,Langham J and Chandramon D (2005) Introduction to Epidemiology 1st edn.Maidenhead:
Open University Press.
Doll R and Peto R (1976) Mortality in relation to smoking: 20 years’ observations on male British doctors.
British Medical Journal 2: 1525–36.
Feedback to activities
Activity 3.1
1 To calculate the risk ratio, first calculate the incidence risk of osteoporosis in both
exposed and unexposed women:
Risk in women who exercised regularly = 300 ÷ 1,000 = 0.3 per 10 years.
Risk in women who did not exercise regularly = 500 ÷ 1,000 = 0.5 per 10 years.
Table 3.4 Incidence of tuberculosis and mid-year population by ethnic group in country Z, 2011
Ethnic group New tuberculosis cases, 2011 Mid-year population, 2011
European 2,890 69,900,000
Indian 1,900 1,790,000
Sri Lankan 400 1,650,000
Total 5,190 73,340,000
Source: Adapted from Bailey et al. (2005).
23346.indb 3723346.indb 37 22/08/2011 15:1222/08/2011 15:12

Then divide the incidence risk in the exposed group by the incidence risk in
the unexposed group:
Risk ratio =
0.3
= 0.6
0.5
A risk ratio of 0.60 indicates that women over age 65 who exercise regularly have a
40% lower risk of developing osteoporosis than women over age 65 who do not
exercise regularly, in this study population.
To calculate the odds ratio,ﬁrst calculate the odds of osteoporosis in women who
exercised regularly and in those who did not:
Odds in women who exercised regularly = 300 ÷ (1,000 – 300) = 300 ÷ 700 = 0.43.
Odds in women who did not exercise regularly = 500 ÷ (1,000 – 500) = 500 ÷ 500 = 1.
Then divide the odds in the exposed group by the odds in the unexposed
group:
Odds ratio =
0.43
= 0.43
1.00
An odds ratio of 0.43 indicates that women over age 65 who exercise regularly have
a 57% lower odds of developing osteoporosis than women who do not exercise
regularly, in this study population.
To calculate the rate ratio, ﬁrst calculate the incidence rate of osteoporosis in
women who exercised regularly and in those who did not:
Incidence rate in women who exercised regularly = 300 ÷ 8,350 person-years =
0.03593 per person-year = 35.93 per 1,000 person-years. (You may have multiplied
by 100 to get a rate of 3.59 per 100 person-years, which is also correct as
long as the units are clearly stated, and the same units are used throughout the
calculation.)
Incidence rate in women who did not exercise regularly = 500 ÷ 6,950 person-years
= 0.07194 per person-year = 71.94 per 1,000 person-years (make sure you remain
consistent with the previous rate in the unit of person-years used for the denominator).
Then divide the incidence rate in the exposed group by the incidence rate in the
unexposed group:
Rate ratio =
35.93
= 0.50
71.94
A rate ratio of 0.50 indicates that women over age 65 who exercise regularly have a
50% lower rate of osteoporosis than women who do not exercise regularly, in this
study population.
2 As this is a long cohort study, the rate ratio is probably the most appropriate meas-
ure as it takes into account the actual person-years at risk in the exposed and unex-
posed groups.
3 For the study on younger women, start by calculating the risk ratio:
Risk in younger women who exercised regularly = 3 ÷ 1,000 = 0.003 per 10 years.
Risk in women who did not exercise regularly = 5 ÷ 1,000 = 0.005 per 10 years.
Then divide the risk in the exposed group by the risk in the unexposed group:
Risk ratio =
0.003
= 0.60
0.005
23346.indb 3823346.indb 38 22/08/2011 15:1222/08/2011 15:12

A risk ratio of 0.60 indicates that women under age 55 who exercise regularly have
a 40% lower risk of developing osteoporosis than women under age 55 who do not,
in this study population.
For the odds ratio, ﬁrst calculate the odds of osteoporosis in younger women
who exercised regularly and in those who did not:
Odds in women who exercised regularly = 3 ÷ (1,000 – 3) = 3 ÷ 997 = 0.003.
Odds in women who did no regular exercise = 5 ÷ (1,000 – 5) = 5 ÷ 995 = 0.005.
Then divide the odds in the exposed group by the odds in the unexposed group:
Odds ratio =
0.003
= 0.60
0.005
An odds ratio of 0.60 indicates that women under age 55 who exercise regularly
have a 40% lower odds of developing osteoporosis than women under age 55 who
do not, in this study population.
Calculate the rate ratio, by ﬁrst calculating the incidence rate of osteoporosis in
younger women who exercised regularly and in those who did not:
Rate in women who exercised regularly = 3 ÷ 9,500 person-years = 0.00032 per
person-year = 0.32 per 1,000 person-years (or, perhaps more intuitively, 3.16 per
10,000 person-years).
Rate in women who did not exercise regularly = 5 ÷ 9,000 person-years =
0.00056 per person-year = 0.56 per 1,000 person-years.
Then divide the incidence rate in the exposed group by the incidence rate in
the unexposed group:
Rate ratio =
0.32
= 0.57
0.56
A rate ratio of 0.57 indicates that women aged under age 55 who exercise regularly
have a 43% lower rate of developing osteoporosis than women under age 55 who
do not, in this study population.
4 You probably noticed that in the study of women aged over 65 years, the measures
of association gave somewhat different estimates for risk ratio, odds ratio, and rate
ratio.This is because the outcome of interest was common. By contrast, in the study
of women under 55 years, the measures of effect gave very similar estimates for risk
ratio, odds ratio, and rate ratio.This is because the outcome of interest was rare.
Activity 3.2
1 An appropriate measure to assess the strength of an association in this example
would be the incidence rate ratio because we know the incidence rate in each group.
Rate ratio of lung cancer in smokers compared to non-smokers:
Rate ratio =
140 per 100,000
= 14.00
10 per 100,000
Rate ratio of ischaemic heart disease (IHD) in smokers compared to non-smokers:
Rate ratio =
669 per 100,000
= 1.62
413 per 100,000
2 A rate ratio of 14.00 for the association of smoking with lung cancer compared to a
rate ratio of 1.62 for the association of smoking with IHD indicates that smoking is
much more strongly associated with lung cancer than it is with IHD.
23346.indb 3923346.indb 39 22/08/2011 15:1222/08/2011 15:12

3 To assess the impact of smoking, the excess mortality attributable to smoking must
be estimated.An appropriate measure to assess this is the attributable risk:
Attributable risk of smoking for lung cancer = (140 per 100,000) – (10 per 100,000)
= 130 per 100,000.
Attributable risk of smoking for IHD = (669 per 100,000) – (413 per 100,000) = 256
per 100,000.
An attributable risk of smoking for lung cancer of 130 per 100,000 compared to an
attributable risk of smoking for IHD of 256 per 100,000 indicates that,among smokers,
a reduction in smoking would prevent far more deaths from IHD than from lung cancer.
Among non-smokers, the death rate from lung cancer is fairly low (10 per 100,000),
while the death rate from IHD is 413 per 100,000. The 1.62 times increase in IHD
mortality associated with smoking affects a much larger number of people than the
14-fold increase in the risk of death from lung cancer. Thus, the potential public health
impact of a reduction in smoking on mortality is far greater for IHD than for lung cancer.
To arrive at the conclusions above, you would need to assume that smoking is
causally related to lung cancer and to IHD, and that smoking is responsible for an
equal proportion of the mortality from both of these diseases.
4 To assess what percentage of the risk of death from lung cancer could be attributed
to smoking, you would calculate the attributable fraction.There are two ways you
could calculate this:
Attributable fraction = attributable risk in smokers divided by risk in smokers:
(130 per 100,000)
= 0.93
(140 per 100,000)
Alternatively,the attributable fraction can be calculated from the relative risk of lung
cancer in smokers compared to non-smokers as follows:
14 – 1
= 0.93
14
This can be interpreted as 93% of deaths from lung cancer among smokers being
attributable to smoking.
Similarly, the attributable-fraction of IHD deaths among smokers is calculated
as:
256 per 100,000
= 0.38
669 per 10,000
or
1.62 – 1
= 0.381.62
This can be interpreted as 38% of deaths from IHD among smokers being due to
smoking.
Activity 3.3
1 Your table should look like Table 3.5.
23346.indb 4023346.indb 40 22/08/2011 15:1222/08/2011 15:12

Table 3.5 Odds of smoking in cases of myocardial infarction (MI) and controls
Exposure MI (Cases) No MI (Controls) Total
Current smokers 60 40 100
Non-smokers 340 360 700
Total 400 400 800
Source: Natasha Howard.
Table 3.6 Incidence of tuberculosis, mid-year population, incidence rate and rate ratio by ethnic group in
country Z, 2011
Ethnic group New tuberculosis cases,
2011
Mid-year population,
2011
Incidence rate per
100,000
Rate ratio
European 2,890 69,900,000 4.13 1
Indian 1,900 1,790,000 106.15 25.70
Sri Lankan 400 1,650,000 24.24 5.87
Total 5,190 73,340,000 7.08 –
2 As this is a case-control study, an appropriate measure to assess the strength of
association between smoking and myocardial infarction (MI) is the odds ratio of
exposure.
60 ÷ 340
=
60 × 360
= 1.59
40 ÷ 360 40 × 340
An odds ratio of 1.59 indicates that the odds of cigarette smoking are 1.59
times (or 59% if we calculate the difference from 1) higher in cases of MI compared
to healthy controls, in this study population. Note it is incorrect to say that the
odds of MI are 1.59 times greater in smokers than in non-smokers as we do not
know the incidence, and therefore cannot calculate the odds, of MI in the study
population.
Activity 3.4
1 The incidence rate and rate ratio for tuberculosis in each group is given inTable 3.6.
2 The rate ratio is 25.70 times as high in the Indian group as in the European group and
5.87 times as high in the Sri Lankan group as in the European group. Thus, Indian
ethnicity is more strongly associated with tuberculosis than are either European or
Sri Lankan ethnicity.
We can also change the reference (‘unexposed’) to the Sri Lankan group to show
that the rate ratio between Indian and Sri Lankan ethnicity is 106.15 ÷ 24.24 = 4.38.
3 The total number of tuberculosis cases is greater in the European group because the
mid-year population in this group is much higher. Even though the incidence rate is
23346.indb 4123346.indb 41 22/08/2011 15:1222/08/2011 15:12

lower than in the other two groups,the European group constitutes 95% (69,900,000
÷ 73,340,000 = 0.95) of the population.
4 Assuming that a targeted intervention has reduced the incidence rate in the Indian
and Sri Lankan groups to 4.13 per 100,000, an appropriate measure to calculate the
proportion of tuberculosis cases in the Indian group prevented by the intervention
would be the preventable fraction. The current rate is taken as the rate in those
unexposed to the intervention and the reduced rate is taken as the rate in those
exposed to the intervention:
Rate in unexposed – Rate in exposed
=
106.15 – 4.13
= 0.96
Rate in unexposed 106.15
A preventable fraction of 0.96 or 96% means that if the incidence rate in the Indian
group were reduced to the level of the European group, then 96% of tuberculosis
cases in the Indian population must have been prevented by the intervention.
Similarly for the Sri Lankan group, the preventable fraction is calculated as:
Rate in unexposed – Rate in exposed
=
24.24 – 4.13
= 0.83
Rate in unexposed 24.24
This means that the intervention would prevent 0.83 or 83% of tuberculosis
cases in the Sri Lankan population.
5 Assuming the incidence rate in Indian and Sri Lankan groups is reduced to 4.13 per
100,000, an appropriate measure of the percentage reduction of tuberculosis cases
in the whole population attributable to the intervention, is the population attribut-
able fraction:
Population rate – Reduced rate
=
7.08 – 4.13
= 0.42
Population rate 7.08
A population attributable fraction of 0.42 or 42% means that if the incidence rate in
all groups were reduced to the level of the European group, then 42% of tuberculo-
sis cases would be prevented by the intervention in the whole population.
23346.indb 4223346.indb 42 22/08/2011 15:1222/08/2011 15:12

Overview
Epidemiological measures of association between an exposure and outcome cannot be
used to infer causality unless alternative explanations have been excluded. In this chap-
ter you will learn about alternative explanations for an apparent association: chance,
bias and confounding.The role of these effects needs to be considered when designing
a study, and assessed whenever an association is found.To ﬁnally infer causality, it is
necessary to build up supportive evidence, for example by using the Bradford-Hill list
of considerations for causality.
Learning objectives
• distinguish between chance, bias and confounding as alternative explanations for
an apparent association between an exposure and an outcome
• explain the concept of chance in relation to measures of frequency and measures
of association
• describe how different types of selection bias and information bias may distort
measures of association
• identify confounding factors and be aware of how to control for their effects in
the analysis
• specify methods for avoiding chance, bias and confounding in study design
• distinguish between statistical association and causality
• list the nine considerations for supporting causality.
Critical appraisal
The ultimate aim of analytical epidemiology is to show whether a measured associa-
tion between an exposure and outcome is causal, providing a target for subsequent
public health interventions. In the previous chapter, you learned about relative meas-
ures of association, and the need to assume causality in order to estimate the impact
of an exposure. However, before we can infer causality, it is necessary to critically
appraise the evidence and exclude other possible reasons for a measured association.
The three main alternative explanations for an observed epidemiological association
are chance, bias and confounding. Once these have been excluded, it is then
necessary to consider whether there is sufﬁcient evidence that an association is
likely to be causal.
Interpreting associations
4
23346.indb 4323346.indb 43 22/08/2011 15:1222/08/2011 15:12

Chance and statistical probability
In both descriptive and analytical studies, we make inferences about a population from
a sample of individuals. It is usually not feasible to measure the outcome and/or expo-
sure in every member of a given population or subgroup.There is, therefore, a chance
that if the sample were repeated with different individuals,the result would be different.
For example,consider that we want to know the number of children who have received
three doses of diptheria-tetanus-pertussis (DTP3) vaccine, as a marker of access to
routine child health interventions for a region of country X.If we question the mothers
of 10 infants at random, and then repeat this several times for different infants, we
would most likely get a different prevalence of DTP3 coverage each time. One way to
reduce the variability in our results would be to increase the number of infants we
sampled.As this sample size increases, the sample becomes more representative of
the population of interest, and this is therefore the main way to reduce the role of
chance in an epidemiological study.
Statistical analysis of results can then be used to assess how representative a sample
was of the population of interest, and this is described by two measures: the P-value
and the conﬁdence interval. Both of these are based on sampling variation and the fact
that many variables show a normal distribution, also known as a bell-shaped curve (as
shown in Figure 4.1).Consider a DTP3 survey of 100 infants in a population where the
‘true’ coverage is 75%. Figure 4.1 shows the distribution of prevalence that we might
see if we repeated the sample 100 times.We would most frequently measure values
close to the true population prevalence and less frequently measure values higher or
lower than this.The height and width of the curve will vary according to the amount of
variation in the prevalence of DTP3 in the population.
Figure 4.1 A normal distribution or ‘bell-shaped’ curve, illustrating the 95% conﬁdence interval as a
dashed line
The P-value is the probability that an observed value or association from a sample
occurred by chance alone, and that it does not exist in the population from which the
sample was selected.A P-value of less than or equal to 0.05 means that there is a 5%
or 1 in 20 chance that the sample result does not represent the reality.This is generally
23346.indb 4423346.indb 44 22/08/2011 15:1222/08/2011 15:12

Interpreting associations 45
considered low enough to imply that the result is not due to chance. However, this
should be used as a guide and not as fixed threshold for reporting the statistical
significance. For example, in a study of diarrhoea in children given iron supplementa-
tion compared with a placebo, if the incidence rate ratio = 1.20, P = 0.04, we would
interpret this as borderline statistically significant evidence of an increased risk,requiring
further investigation.
The confidence interval is the range of values, estimated from a sample, within
which the ‘true’ population value is likely to be found. In Figure 4.1, if the area under
the curve represents the results of 100 samples of DTP3 coverage, then the unshaded
area represents the results of 95 of these samples. The values at either end of this
unshaded area are known as the limits of the confidence interval. In this example, we
can say that we have 95% confidence that the DTP3 coverage in the population is
between 61–89%.This means that if we were to repeat the random sample 100 times,
95 times out of 100 we would obtain a result that lies within this interval.The wider
the confidence interval is,the less precision we have about the true value (i.e.the more
possible numbers that could be the true value).
For a measure of association (prevalence ratio, odds ratio, risk ratio, rate ratio)
where the value 1.0 represents no association, if the 95% confidence interval (CI)
includes 1.0, we can say that the association is not significant at the 5% level (i.e. the
P-value will be greater than 0.05). For example, if the risk ratio = 1.10 (95% CI: 0.90,
1.20), this suggests that it is not significantly different from 1.0 and there is no signifi-
cant association between the exposure and outcome. If the entire range of the 95% CI
had been greater than 1.0, we could be more confident that there was truly an
increased risk of the outcome among exposed individuals.
Bias
Bias is a systematic (i.e. non-random) error that leads to an incorrect measure of
association. Sample size does not affect bias, and statistical methods cannot be used to
adjust for bias; it must, therefore, be avoided through appropriate study design.
The random selection of study participants or random allocation of individuals to
comparison groups aims to reduce systematic bias, but does not completely prevent it.
Bias can be categorized as either selection bias or information bias.
Selection bias
Selection bias occurs when there is a systematic difference between the character-
istics of individuals sampled and the population from which the sample is taken, or a
systematic difference between the comparison groups within the study population.For
example,people who volunteer to participate in a study are‘self-selected’ and are likely
to differ from the general population in terms of health awareness,education and other
factors that may also affect the outcome of interest. Selection bias is most important
in case-control studies where cases and controls should only differ on the outcome
and exposure of interest. Several factors may affect whether selection bias occurs:
1 The definition of the study population or comparison group. For example, in an
occupational cohort study where comparison is made with the general population,
the overall health of the occupational cohort will usually be better than the general
23346.indb 4523346.indb 45 22/08/2011 15:1222/08/2011 15:12

population, which includes individuals who are not well enough to work. This is
known as the‘healthy worker effect’,and can be reduced by selecting for comparison
other workers without the exposure of interest.
2 The inclusion and exclusion criteria. For example, in a study of access to routine
healthcare using household lists drawn up by village elders, recent migrants or
marginalized groups may be excluded from the study.
3 The rate of loss to follow-up. For example, if individuals in an intervention study
receiving an active intervention are more likely to continue attending follow-up
clinics than those receiving a placebo, our detection of cases will be different
between the two groups. If more cases are detected in intervention than control
individuals we may wrongly conclude that the intervention has failed.
Information bias
Information bias occurs when there is a systematic difference between comparison
groups in the way that data are collected, and can be introduced by those measuring
the outcome (observer bias), the study participants (responder bias), or measurement
tools, such as weighing scales or questionnaires (measurement bias). Information bias
may result in the misclassification of exposure or disease status in a non-differential
(random) or differential (non-random) way.
Non-differential misclassification occurs when both comparison groups
(exposed and unexposed; cases and controls) are equally likely to be misclassified. It is
therefore independent of exposure or outcome status, and will not bias the direction
of any observed association between exposure and outcome. However, it causes the
comparison groups to appear more similar than they actually are, and may lead to an
underestimation of the strength of the association.Always consider the potential role of
non-differential misclassification when interpreting a study that appears to show no
statistically significant association between the exposure and outcome.
Consider a case-control study of the association of oral contraceptive use with
ovarian cancer,using 20 years of clinic records to determine exposure.It is unlikely that
all records of oral contraceptive use over the previous 20 years from a family planning
clinic will be traceable. The loss of records would probably be distributed equally
among the cases and the controls, since record keeping in family planning clinics is
independent of the risk of developing cancer. However, if the investigators decided to
classify all women without a record as unexposed to contraceptives, then the odds of
exposure would be underestimated in both cases and controls. This would lead to
underestimation of the effect of contraceptives on ovarian cancer.
Differential misclassification occurs when classification of the exposure is
dependent on the outcome or vice versa,and is generally due to observer or responder
bias. It can lead to the over- or underestimation of a measure of association, and may
also lead to false associations.
For example, in an intervention study of the effect of promoting regular exercise
among the elderly on blood pressure, a visiting health worker may under-estimate the
blood pressure of those known to be receiving the intervention, or over-estimate
the blood pressure of those known to not be receiving the intervention.
Observer bias refers to misclassification caused by the observer’s knowledge of the
comparison group.This may not be deliberate, or very large, but if it is systematically
high or low, it can affect the study outcome. It may take the form of tending to ‘round
23346.indb 4623346.indb 46 22/08/2011 15:1222/08/2011 15:12

up’ measures for one group and‘round down’ measures for the other group.To reduce
the effect of observer bias, the exposure status (or outcome status in a case-control
study) should be concealed from the person measuring the outcome or exposure –
this is known as blinding.
Responder bias refers to systematic differences in the information provided by a
study participant, and may take the form of recall or reporting bias. For example, in a
case-control study of lung cancer and exposure to secondary smoke, cases may be
more likely to remember their historical experience of secondary smoke (recall bias) if
they are aware of the association between smoking and cancer, overestimating the
association.Similarly,in a study of sexual behaviour and prevalence of sexually transmit-
ted infections (STIs), individuals with a higher number of sexual partners and therefore
at higher risk of STIs,may also be more likely to under-report their number of partners
due to social stigma (reporting bias), resulting in an under-estimate of the association.
Responder bias is reduced by ‘blinding’ the participants, i.e. concealing the exposure
from them.This may be done by using a placebo in intervention trials or concealing
the hypothesis under investigation in other studies. For example, investigators may ask
about a wide variety of exposures rather than focusing only on the exposure of inter-
est.They may also ask a question in several different ways to ensure consistency of
responses.Recall bias can be reduced by using objective records (e.g.vaccination cards)
or shortening the recall period (e.g. asking ‘did you eat dairy products yesterday?’
rather than within the last week).
Confounding
Confounding occurs when an apparent association between an exposure and an out-
come is actually the result of another factor (confounder).A confounding factor must
be independently associated with both the exposure and the outcome, and must not be
on the causal pathway between the two (i.e. where the exposure causes an inter-
mediary factor, which then causes the outcome). Figure 4.2 illustrates the relationship
between an exposure, outcome and confounder. For example, an apparent association
between occupation and lung cancer could be the result of the occupational cohort
being more likely to smoke (or smokers being more likely to choose a particular
occupation) and therefore at increased risk of lung cancer.A confounder does not need
to cause the outcome or wholly explain the relationship between the exposure and
outcome.Age and socio-economic status are two common confounders.
Figure 4.2 The relationship between an exposure, outcome and confounder
Source: Ilona Carneiro, modiﬁed from LSHTM lecture notes.
23346.indb 4723346.indb 47 22/08/2011 15:1222/08/2011 15:12

If the third factor is on the causal pathway between the exposure and outcome, it is
not a confounder. For example, coronary heart disease is associated with high blood
cholesterol, and blood cholesterol is a direct result of diet. Blood cholesterol does not
provide an alternative explanation for the relationship between diet and coronary heart
disease, but is an intermediary between them, and is therefore not a confounder.
There are three ways to avoid confounding effects when designing a study:
1 Randomization involves the random allocation of individuals to the exposure
and control groups, such that each study participant has an equal chance of being
exposed or unexposed. If the sample size is sufficiently large, this method ensures
the equal distribution between exposure groups of known and unknown
confounders.This is the best method to avoid confounding, but can only be used in
intervention studies.
2 Restriction limits the study to people who are similar in relation to the con-
founder.For example,if sex is known to be a confounder,the study may only include
men. However, this means that the results of the study cannot then be extrapolated
to women.
3 Matching selects the two comparison groups to have the same distribution of
potential confounders, and is generally only used in case-control studies. At an
individual level it is known as ‘pair matching’. For example, when looking at the
effect of hygiene practices on the risk of diarrhoea,a community control of the same
age is identified for each diarrhoea case. At a group level it is called ‘frequency
matching’. For example, when looking at exposure to smoking, female cases of
lung cancer may be matched to female hospital controls and male cases matched to
male controls.
There are two ways to control for confounding in the analysis, if data on confounders
have been measured:
1 Stratification is an extension of frequency matching as it measures the association
between exposure and outcome separately for each category (stratum) of a
confounder. For example, in a study of the association between long-term cannabis
use and cognitive function, the measure of association should be calculated
separately for each age group, as age is likely to be associated with amount of
cannabis exposure and independently with cognitive function. The results can
then be combined to obtain a measure of association that has been adjusted for
the effects of the confounder. Always try to limit the number of strata in the
analysis, as the sample size of each stratum will be reduced, increasing the role of
chance.
2 Statistical modelling allows us to adjust simultaneously for several confounders
using methods such as multivariable regression analyses (see Chapter 5).
Our ability to control for confounding will depend on the accuracy with which the
confounders have been measured.Non-differential (random) misclassification of a con-
founder would underestimate the effect of that confounder, reducing our ability to
control for it.This is known as residual confounding and it biases the association
between the exposure and outcome in the same direction as the confounding.
For example, a case-control study (Becher 1992) found that laryngeal cancer was
associated with a four times greater odds of regular alcohol consumption (Odds Ratio
= 4.22).After adjusting for the confounding effect of smoking (i.e. comparing smokers
23346.indb 4823346.indb 48 22/08/2011 15:1222/08/2011 15:12

to non-smokers),this was reduced slightly to give an OR of 4.02.However,after adjust-
ing for the average number of cigarettes smoked per day, which is more precise, the
OR was 3.07. This shows that using two categories of smoking resulted in residual
confounding, because it was not a sufficiently accurate measure of exposure to smok-
ing to adjust for the confounding effect.
Activity 4.1
In each of the following examples,there is an alternative explanation for the association
between the exposure and the outcome. For each example, identify the alternative
explanation (bias, confounding, or chance) and why you think it occurred (imagine you
are explaining your reasons to a colleague).
1 In a study of risk factors for infant mortality,the investigators find that infant mortality
is significantly lower in households where the father wears a watch.The investigators
therefore conclude that if watches were given to fathers, infant mortality would fall.
2 Four people want to give up smoking.At random, two of them are given garlic pills
to help them stop, and two are not.The two who take garlic pills succeed in giving
up smoking.The other two do not.The investigators conclude that garlic pills help
people give up smoking. However, a significance test shows that P = 0.3.
3 In a case-control study to examine risk factors for lung cancer, cases are people
admitted to hospital with lung cancer, and controls are people admitted to the same
hospital with emphysema (a chronic lung disease for which smoking is a risk factor).
The study finds no association between smoking and lung cancer.
4 A case-control study of Down’s syndrome found that fewer mothers of cases
smoked during pregnancy than didn’t. After adjusting for maternal age (<35 years,
≥35 years) the effect was still negative, but not statistically significant.After adjusting
for exact year of maternal age there was no association (odds ratio = 1.00).
Inferring causality
A statistically significant association between an exposure and an outcome is not
sufficient to imply causality. Once alternative explanations for an observed association
have been discounted or adjusted for, we must then consider whether the association
is likely to be causal.
For example,in a baseline survey of 10,000 children,of whom half were subsequently
randomized to receive an intervention, the mean haemoglobin concentration was
significantly different at 11.7 compared with 11.9 g/dl.The groups are very large, have
been randomized, and no interventions have yet been applied.There is therefore no
explanation for any association between the randomization group and the mean
haemoglobin. In addition, the magnitude of difference is very small, and it is only
statistically significant as a result of the fine grading of the measurement, low variability
in between children and the large sample size. We therefore have to apply our
judgement as to whether a statistically significant result has epidemiological
importance, or whether there is a logical basis for an observed association.
SirAustin Bradford Hill (1965) listed nine considerations,none of which are essential,
that are used in epidemiology to build-up evidence for a causal relationship:
23346.indb 4923346.indb 49 22/08/2011 15:1222/08/2011 15:12

1 Strength: the stronger the association between the exposure and outcome, the less
likely that the relationship is due to some other factor. For example, a ten times
greater odds of laryngeal cancer among heavy alcohol drinkers decreases the likeli-
hood that the relationship is wholly confounded by some other factor.A confounder
would have to be much more frequent among heavy drinkers than non-drinkers.
This criterion does not imply that an association of small magnitude cannot be
causal, but in such cases it is more difficult to exclude alternative explanations.
2 Consistency: is the repeatability of the result. If the same association has been
observed from various studies and in different geographic settings, it suggests that
the association is real. For example, the assessment of a cause–effect relationship
between cigarette smoking and coronary heart disease has been enhanced by the
fact that similar results have been obtained by a number of cohort and case-control
studies conducted over 30 years in different populations.
3 Temporality: while it may seem obvious that the exposure must be present or have
occurred prior to the outcome, this can be more complex to ascertain for out-
comes of slow development. For example, does a particular diet lead to a digestive
disorder, or do the symptoms of the disorder affect the sufferer’s diet? Temporality
is also not easy to establish in cross-sectional or case-control studies, where the
exposure and outcome are measured simultaneously. In such cases an apparent risk
factor may actually be a consequence of the outcome, this is known as reverse
causality.
4 Dose–response: where there is an increased risk of outcome with increased expo-
sure. For example, increased risk of lung cancer among heavy smokers compared
with moderate smokers, and increased risk among moderate smokers compared
with light smokers. However, a dose–response relationship alone does not confirm
causality and the absence of a dose–response relationship does not rule out
causality.
5 Plausibility: the existence of a reasonable biological mechanism for the cause and
effect lends weight to the association, but depends on the existing knowledge. For
example, a causal relationship between the moderate consumption of alcohol and
decreased risk of coronary heart disease is enhanced by the fact that alcohol is
known to increase the level of high-density lipoprotein, which is associated with a
decreased risk of coronary heart disease. However, the lack of a known or
postulated mechanism does not necessarily rule out a cause–effect relationship. For
example, John Snow hypothesized that water was the source of cholera epidemics
in London long before the identification of Vibrio cholera (see Chapter 1).
6 Reversibility: relates to whether an intervention to remove or reduce the exposure
results in the elimination or reduction of the outcome. For example, vitamin D
deficiency is associated with muscle weakness, and older people are prone to
develop vitamin D deficiency. However, it is difficult to infer a causal association
between vitamin D deficiency and muscle weakness in the elderly. Other conditions
may also cause weakness or tiredness, preventing elderly people from going outside
and being exposed to sunlight (a source of vitamin D), and thus confounding the
association. Randomized intervention trials of vitamin D supplementation in the
elderly have been shown to improve muscle strength and function, indicating
causality (Janssen et al. 2002).
7 Coherence: refers to a logical consistency with other information. For example, the
simultaneous increase in smoking habits and incidence of lung cancer over a period
of time would support a causal link, as would isolation from cigarette smoke of
factors that caused cancer in laboratory animals (Hill 1965).
23346.indb 5023346.indb 50 22/08/2011 15:1222/08/2011 15:12

8 Analogy: similarity with other established cause–effect relationships helps to
support the argument for causality. For example, previous experience with the
effects of thalidomide or rubella infection in pregnancy would lend support for a
causal effect of another drug or viral infection in pregnancy with similar, but weaker,
evidence.
9 Specificity: this relates to the relationship being specific to the outcome of interest.
For example, in a study of the effect of bicycle helmets, if we saw a reduction only in
head injuries and not to other parts of the body, it would strengthen the inference
of a protective effect of the helmet, and reduce the likelihood that the association
was confounded by factors such as helmet-wearers being more careful riders (Weiss
2002). However, many outcomes are the result of more than one exposure (see
Chapter 1 on component causes). For example, smoking is a cause of coronary
heart disease, however, high cholesterol is also a cause of coronary heart disease,
and smoking is also a cause of lung cancer and other illnesses.
Activity 4.2
A randomized, clinical intervention trial compared the effect of miltefosine, the first
oral drug for the treatment of zoonotic cutaneous leishmaniasis caused by Leishmania
major, with standard meglumine antimoniate treatment in northeastern Iran.The out-
come of interest was clinical recovery (cure) measured three months post treatment.
At this time point, 26 of 32 patients receiving oral miltefosine were cured and 20 of 31
patients receiving intramuscular meglumine antimoniate were cured.No relapses were
observed at six-month follow-up and both regimens were well tolerated. Investigators
compared treatment results in intervention (miltefosine) and control (meglumine)
groups.
1 Identify, calculate and interpret a ratio to compare treatment results after three
months, using the control group as baseline.What does this tell you?
The investigators calculated a 95% confidence interval (95%CI) of 0.62 – 1.33 and
P-value of 0.09 for this association measure.
2 Interpret the 95% CI and P-value shown for this study.What do these tell you?
3 How might you reduce the role of chance in this study?
Activity 4.3
A case-control study was conducted to assess the association between maternal
depression and infant nutritional status in a peri-urban district of Liberia. Cases were
82 undernourished infants (low weight-for-age) recruited at the local clinic while
attending for measles immunization. Controls were 82 infants (normal weight-for-age)
recruited during a measles campaign in the local community and matched with cases
by age and gender. Some 122 of the mothers provided informed consent and were
screened for depression using a standard assessment tool.
1 Might selection of controls introduce bias into this study, and if so how?
2 Might lack of consent by some mothers introduce bias into this study,and if so how?
3 How might potential bias be reduced in this study?
23346.indb 5123346.indb 51 22/08/2011 15:1222/08/2011 15:12

Activity 4.4
A cross-sectional study was carried out to assess the association between a school-
based health promotion package with adolescent use of health services in DistrictY of
northern Ghana.The investigators were interested in exposure to school-based health
promotion activities. Participants were selected randomly from ‘exposed’ students
attending the ten schools in which the health promotion package had been
implemented for the previous two years, and ‘unexposed’ students attending ten
schools that had not implemented the package. The outcome of interest was the
prevalence of self-reported attendance at health services in the previous year
measured through a survey undertaken at the schools.
1 Could measurement of exposure introduce bias into this study? Give reasons for
your answer.
2 Could measurement of the study outcome introduce bias into this study? Give
reasons for your answer.
3 How might you reduce potential information bias in this study?
Activity 4.5
An intervention study in women of different ages showed a strong association between
intense exercise and reduced risk of osteoporosis.
1 Define the concept of confounding in the context of this study.
2 Describe how this study finding could be the result of confounding.
3 How could you address potential confounding in this study?
Conclusion
You should now appreciate that epidemiological associations need to be interpreted
with caution.An apparent association could be the result of chance,bias or confounding,
which may be avoided by appropriate study design or adjusted for in analysis.You have
been introduced to several criteria that may support causal inference in an epidemio-
logical association. Alternative explanations and evidence for causality need to be
considered when designing and undertaking an epidemiological investigation, and when
interpreting the results of epidemiological studies.
References
Becher H (1992)The concept of residual confounding in regression models and some applications.Statistics
in Medicine 11: 1747–58.
Hill A B (1965) The environment and disease: association or causation? Proceedings of the Royal Society of
Medicine 58: 295–300.
Janssen HC, Samson MM and Verhaar HJ (2002) Vitamin D deficiency, muscle function, and falls in elderly
people. American Journal of Clinical Nutrition 75: 611–5.
Weiss NS (2002) Can the ‘specificity’ of an association be rehabilitated as a basis for supporting a causal
hypothesis? Epidemiology 13: 6–8.
23346.indb 5223346.indb 52 22/08/2011 15:1222/08/2011 15:12

Feedback to activities
Activity 4.1
1 This is an example of confounding.The exposure of interest is wearing a watch, which
is associated with socio-economic group. Low socio-economic group is a risk factor
for infant mortality. Therefore, the apparent association between wearing a watch
and lower infant mortality is probably due to confounding by socio-economic group.
Socio-economic group (the confounder) is an alternative explanation for the
apparent association between wearing a watch (the exposure of interest) and infant
mortality (the outcome).
2 In this example the result was due to chance or random error.This study shows an
apparent association between taking garlic pills and giving up smoking, but the
number of subjects is very small, and the P-value is 0.30, meaning that there is a 30%
chance that this association might be seen with this sample size even if it was not
real.A much larger sample size would be needed to determine if there was a real
association between taking garlic pills and giving up smoking.
3 The study has been poorly designed and has resulted in selection bias.The controls
have emphysema, which has an increased risk with smoking tobacco, suggesting that
this group is more likely to smoke tobacco than the overall population that the cases
came from.A more appropriate control group would be hospital admissions for an
outcome that is unrelated to exposure to tobacco smoke, such that the prevalence
of smoking among the controls would be the same as among the population that
produced the cases.
4 This is an example of confounding – more precisely residual confounding.The apparent
protective effect of smoking in pregnancy on Down’s syndrome was confounded by
maternal age.When the investigators adjusted for crude categories of maternal age,
it had some effect on the odds ratio of exposure, but after they adjusted for actual
maternal age there was a greater effect. Adjustment by age categories did not
completely remove the effect of confounding because it was not an adequate
measure of how the confounder was working.
(It has been shown that the risk of Down’s syndrome increases with maternal age.
The proportion of smoking during pregnancy must have been associated with
maternal age, for age to confound the association between smoking and Down’s
syndrome. In fact, the proportion of smoking must have shown a constant (linear)
decrease with age for the continuous maternal age variable to have a greater effect
on the association than the binomial categories of maternal age.)
Activity 4.2
1 The outcome is‘risk of recovery’,i.e.how many people changed their infection status
during a ﬁxed time-period, therefore, an appropriate measure of association would
be the risk ratio.
The ‘risk of recovery’ among the intervention group was 26 ÷ 32 = 0.81 or 81%.
The risk of recovery among the control group was 20 ÷ 31 = 0.65 or 65%.Therefore
the risk ratio = 0.81 ÷ 0.65 = 1.25.
A risk ratio of 1.25 indicates that those receiving miltefosine have a 25% higher
likelihood of having achieved a cure at three months than do those receiving stand-
ard meglumine treatment in this study. However, this does not tell you whether this
difference is real or due to chance.
23346.indb 5323346.indb 53 22/08/2011 15:1222/08/2011 15:12

2 Evaluating the role of chance in study findings requires two related statistical
assessments: (a) calculating a P-value to test the study hypothesis and determine the
likelihood that sampling variability could explain study results; and (b) estimating the
95% confidence interval (CI) to indicate the range within which the true result is
likely to be.
A P-value of 0.09 is relatively high,indicating a 9% probability that the study result
of 1.25 may be due to chance.A 95% CI of (0.62 – 1.33) indicates that you can be
95% confident that the true risk ratio in this study population is between 0.62 and
1.33. Because this CI includes ‘1.00’, you know that the P-value is greater than 0.05
and that the measure of association is not significant at the 5% level.The confidence
interval is relatively wide, so you would not be confident of extrapolating the
observed RR estimate of 1.26 to the whole population.
3 Statistical significance and confidence intervals help to evaluate the role of chance as
an alternative explanation of an observed association. The most common way of
reducing the role of chance is to increase sample size,which increases the magnitude
of the P-value.This study sample is only 63 participants so a larger sample size might
provide a more robust estimate.
Activity 4.3
1 Yes, selection of controls might introduce selection bias in this study. Controls were
selected from the community while cases were selected from the clinic.Thus,controls
may in some way be different from cases,for example in access to healthcare.This type
of bias cannot be corrected through statistical techniques at the analysis stage.
2 Yes,lack of consent may cause selection bias (more specifically non-responder bias) in
this study.There were 164 infants (82 cases and 82 controls), but only 122 mothers
(122 ÷ 164 = 0.74 or 74%) agreed to be assessed for depression.A non-participant
rate of 26% (100 – 74 = 26) is high, and these mothers may have been different from
those participating in many ways.Additionally,we have no information about how the
percentage of non-participating mothers was distributed among cases and controls
and so do not know if this differed systematically between the cases and controls.
3 To reduce potential selection bias, controls could have been selected from non-
malnourished infants attending for measles vaccination in the clinic.
Reducing the number of non-responders would be more challenging, but might
be done through community information meetings and discussion of the aims and
benefits of the research.
Activity 4.4
1 Yes, measurement of exposure to the health promotion package could cause bias in
this study.We do not know what the promotion activities consisted of or whether
there could be overlap (‘contamination’) between schools attended by partici-
pants categorized as ‘exposed’ and schools attended by participants categorized as
‘unexposed’.For example,we do not know how far apart health promotion and non-
promotion schools were from each other.We also do not know if there were other
activities to promote health service attendance in the communities from which the
‘non-exposed’ students were selected.The effect of such a bias would most likely
reduce the association between outcome and exposure.
2 Yes. Outcomes were measured through self-reporting, so information bias may have
been introduced in the form of observer or reporting bias. If ‘exposed’ students had
23346.indb 5423346.indb 54 22/08/2011 15:1222/08/2011 15:12

been sensitized to the importance of attending health services, they might be more
likely to report having attended in the past year.Additionally, one year is a long recall
period and both ‘exposed’ and ‘non-exposed’ participants might not remember cor-
rectly whether they had attended services. Interviewers would be aware of partici-
pants’ status as ‘exposed’ and ‘non-exposed’ as this varied by school. There is
therefore a possibility that, if the interviewers were aware of the study outcome of
interest, they might be more likely to record an ‘exposed’ participant as having
attended health services.
3 Potential recall or observer bias could both be reduced through objective outcome
measurement (e.g. checking health centre records). Self-reporting is subjective by
nature and is therefore more prone to bias.
Activity 4.5
1 The presence of confounding would mean that the observed association between
exposure (intense exercise) and outcome (reduced osteoporosis risk) is due totally
or in part to the effects of another variable or variables. Such a variable must be
associated with intense exercise and independently of this also be associated with
osteoporosis.
2 In this study, age could act as a confounder, providing an alternative explanation for
the observed association between heavy exercise and osteoporosis risk. Young
women, as a group, tend to exercise more heavily. Additionally, and independently,
younger women have a lower risk of osteoporosis. Note that this alternative
association does not need to be causal – increased age does not necessarily cause
osteoporosis.
3 The three common ways of controlling for confounding at the design stage are ran-
domization, restriction and matching. Confounding can be addressed at the analysis
stage by statistical techniques such as stratiﬁed and multivariate analyses if data on
potential confounders have been collected.
23346.indb 5523346.indb 55 22/08/2011 15:1222/08/2011 15:12

23346.indb 5623346.indb 56 22/08/2011 15:1222/08/2011 15:12

SECTION 2
Epidemiological
research studies
23346.indb 5723346.indb 57 22/08/2011 15:1222/08/2011 15:12

23346.indb 5823346.indb 58 22/08/2011 15:1222/08/2011 15:12

Overview
An epidemiological investigation starts with identifying the association of interest and
choosing an appropriate study design.Then investigators employ methods to reduce
the role of chance, bias and confounding, and collect data in a way that will maximize
its utility. In this chapter you will learn about choosing an appropriate study design and
issues of developing a protocol and data management that are common to the different
epidemiological study designs. Design-specific topics will be covered in subsequent
chapters.
Learning objectives
• recognize the principal study designs and select an appropriate design for a
specific situation
• outline the steps for developing a study protocol, e.g. sample size calculation,
sampling of subjects, design of data collection tools
• explain the need for unique identifiers and relational databases
• define both quantitative (binomial, categorical, continuous) and qualitative data
types
• describe the basic approaches to analysing epidemiological data.
Choice of study design
In Chapter 1 you were introduced to descriptive and analytical sources of epidemio-
logical data. Descriptive data provide information on the frequency of an outcome or
level of exposure, but do not analyse an association between the outcome and expo-
sure. Analytical studies measure the association between an exposure and outcome,
with the aim of inferring causality.
Descriptive data may come from routinely collected data sources or epidemiological
studies, and are used to identify health issues for further study. For example, a fifteen-
fold increase was seen in the number of lung-cancer deaths in England and Wales
between 1922 and 1947, prompting investigation of the cause of this change (Doll and
Hill 1950). Routinely collected data include population censuses and population health
surveys (described further in Chapter 6), vital registration systems, outcome registries
and health facility data (described further in Chapter 12). Descriptive epidemiological
studies may be undertaken to assess whether the burden of an outcome is of public
health importance, or as part of a situational analysis for subsequent epidemiological
5Study design and
handling data
23346.indb 5923346.indb 59 22/08/2011 15:1222/08/2011 15:12

60 Epidemiological research studies
investigation. Descriptive studies may use cross-sectional surveys or longitudinal
follow-up of a cohort, and the methodological issues are the same as for analytical
forms of these study designs.
There are five main types of analytical study:
1 Ecological studies compare the frequency of outcome and exposure at a population-
level.They may use cross-sectional or cohort methods to identify epidemiological
associations that then require further investigation to infer causality. Using the lung-
cancer example above, mortality rates differed between urban and rural popula-
tions, lending support to the hypothesis that the risk factor may be atmospheric
pollution.
2 Cross-sectional studies compare the prevalence of outcome with exposure status
at one time-point, from a random sample of individuals. These are rapid and less
costly than other studies, and may be best for common or chronic outcomes.The
simultaneous collection of outcome and exposure data makes it difficult to infer
causality, and these studies are often used to provide preliminary evidence of an
individual-level association, e.g. population surveys of obesity and reported dietary
habits.
3 Cohort studies compare the incidence of outcome in individuals with recorded dif-
ferences in exposure.These require a well-defined population and are usually time-
consuming, costly and logistically more difficult than other study designs. However,
they are ideal for inferring causality, as the exposure is recorded prior to the out-
come. For example, a large cohort of men working at several oil refineries, could be
followed up over several years to assess whether this occupation was associated
with the incidence of various causes of death.
4 Case-control studies select individuals on the basis of their outcome status
and analyse whether they differ in relation to previous exposure, making them
prone to selection and information bias.These are best for studying rare outcomes,
or for outbreak investigations, where it would not be practical to follow-up indi-
viduals over a long period of time. Early case-control studies of AIDS (acquired
immunodeficiency syndrome) identified risk groups and risk factors, resulting in the
restriction of high-risk blood donors and promotion of safer behaviours even before
identification of the HIV (human immunodeficiency) virus (Schulz and Grimes
2002).
5 Intervention studies allocate a protective exposure, and compare outcomes
between those exposed and unexposed.These are the gold standard for inferring
causality but can only be used for protective exposures, which include the removal
of exposure to a risk factor.Intervention studies may combine several study designs.
For example, study of a malaria control intervention may start with a baseline
descriptive study, followed by a cohort study to analyse the effect on malaria inci-
dence, and end with a cross-sectional study to analyse the effect on malaria and
anaemia prevalence.
The choice of analytical design will depend on existing information about the associa-
tion of interest, expected frequency of the outcome, and logistical constraints such as
time, budget and personnel. Each analytical design also has different strengths and
weaknesses in relation to bias and confounding (see Table 5.1).
23346.indb 6023346.indb 60 22/08/2011 15:1222/08/2011 15:12

Table5.1Keyfeatures,advantagesanddisadvantagesofmainepidemiologicalstudydesigns
StudydesignKeyfeaturesAdvantagesDisadvantages
Ecological•Population-based
•Prevalentorincidentcases
+Relativelyeasytocollectdata(routine)
+Rapid
+Relativelyinexpensive
–Cannotshowcausality
–Highprobabilityofconfounding
Cross-sectional•Outcomeandexposuremeasured
simultaneously
•Prevalentcases
•Measuresassociationasprevalence
ratio(oroddsratioifoutcomeis
rare)
+Relativelyeasytocollectdata
+Rapid
–Difﬁculttoknowifexposure
precededoutcome(problemsof
informationbias)
–Mediumprobabilityofselectionbias
–Mediumprobabilityofconfounding
Cohort•Exposuredeterminedbeforecases
detected
•Incidentcases
•Measureassociationasriskratio,
oddsratioorrateratio
+Lowprobabilityofselectionbias
+Lowprobabilityofrecallbias
+Lowprobabilityofconfounding
–Mediumtohighprobabilityof
loss-to-follow-up(dependenton
lengthofstudy)
–Logisticallymoredifﬁcult
–Moreexpensive
Casecontrol•Participantsselectedbyoutcome
withexposuredetermined
subsequently
•Nomeasureofoutcomefrequency
•Measuresassociationasoddsratioof
exposure
+Lowprobabilityofloss-to-follow-up
+Canberapid
–Highprobabilityofselectionbias
–Highprobabilityofinformationbias
–Mediumprobabilityofconfounding
Intervention
(Randomized)
•Protectivemeasureappliedorrisk
factorremovedfromonegroup
•Prevalentorincidentcases
•Measuresassociationaspreventable
fraction
+Lowprobabilityofselectionbias
+Lowprobabilityofinformationbias
+Verylowprobabilityofconfounding
–Mediumprobabilityofloss-to-
follow-up
–Morecomplex
–Moreexpensive
Source:IlonaCarneiro.
23346.indb 6123346.indb 61 22/08/2011 15:1222/08/2011 15:12

Activity 5.1
For each of the following examples identify the study design used and list the possible
measures of association that could be calculated:
1 Comparison of 50 people with brain cancer and 100 people without brain cancer to
identify the relative risk of brain cancer in those regularly using a mobile phone.
2 A study of 10,000 people followed up during a ten-year period to identify the risk
factors for heart disease.
3 A comparison of the prevalence of anaemia (haemoglobin < 8 g/dl) at eight months
gestation among women using an insecticide-treated mosquito net in pregnancy,
compared with women using an untreated mosquito net in pregnancy.
4 Comparison of national infant mortality rates by gross domestic product.
5 A study of the number of children with existing Ascaris lumbricoides (an intestinal
worm) infection and household access to running water.
Study design
There are several methodological components that need to be considered when plan-
ning a study.A study protocol is prepared in advance to define the methods to be used
in implementing the study, and in collecting and analysing the data. In this chapter we
consider the key components of any study protocol.
Sampling
Epidemiological investigations are undertaken using a sample population (of indi-
viduals, villages, schools, hospitals, etc.) and findings are then extrapolated to the tar-
get population (e.g. infants, students, women over 55 years, etc.). In Chapter 4 you
learned about the roles of chance and selection bias,and the need for the study sample
population to be representative of the target general population.We can reduce the role
of chance by having a sufficiently large sample size.We can reduce selection bias by
selecting a random sample from the study population, taking care to ensure that hard-
to-reach or minority groups are proportionately sampled.
Sample size
To calculate a sample size, it is necessary to define a specific, testable hypothesis. It is
not sufficient to state the association of interest,for example,‘To measure the effect of
gender on depression’. Instead we must specify the comparison groups, expected size
of the effect, and measure of frequency or association to be detected.This is known as
the study objective and would explicitly mention subjects, study population and effect.
For example‘To detect a 30% difference in the prevalence of unipolar depression between
men and women in British cities.’
There are two important concepts in sample size calculation: statistical power and
precision.Statistical power is the probability of detecting an effect if it is real.Statistical
precision is the probability of detecting an effect if it is not real, i.e. by chance (see
Chapter 4 on P-values). It is typical to aim for a sample size with 80–90% power and
23346.indb 6223346.indb 62 22/08/2011 15:1222/08/2011 15:12

Study design and handling data 63
5% precision (significance) to detect a valid estimate of effect. Increased power and
precision require increasingly larger sample sizes, and this will have implications for
how much a study costs and how long it takes.
The size of effect to be detected will also determine the sample size.The larger the
effect, the easier it is to detect and the fewer study subjects are required to obtain
statistical significance. However, it is rare to find very large effects, so we need to
decide what magnitude of effect would be of public health importance.If we found that
people drinking one glass of orange juice a day had a 10% reduced risk of catching a
cold, we would not recommend that everybody drank orange juice. However, if we
found that one glass of orange juice per day reduced the risk of colds by 50%,we might
promote it or at least undertake more research into the nature of the relationship.
When calculating a sample size we need to identify the unit of observation: individ-
ual, household, school, community, hospital, district, etc. Note, a comparison of
improved cognitive function in 500 students taking omega-3 supplementation and
500 students taking a placebo,is not the same as comparing it in 5 exposed schools and
5 unexposed schools each with 100 students. This is because there are likely to
be unmeasured similarities between students in the same school that we would not
be able to adjust for in the analysis.
Sample size formulae vary according to the outcome of interest (prevalence, inci-
dence, mean) and the level of observation (individual, group). Formulae are available in
several statics textbooks (e.g. Kirkwood and Sterne 2003) and computer statistical
software packages (e.g. Stata, SPSS) are generally used for sample size calculation.
Sampling methods
Once the sample size has been determined, it is necessary to sample (i.e. select study
participants from) the population, with an equal probability of sampling any subject (e.g.
individual,household,clinic).Random sampling requires a sampling frame (i.e.a list detail-
ing all eligible subjects in the study population) from which to sample the following:
1 Simple random sampling is random selection from the sampling frame,for example,
by labelling a card for each district,shuffling them and choosing the required number
for the study. Random number tables can also reduce selection bias, either by
manual or computer-assisted selection depending on sample size.
2 Systematic sampling is the selection of sampling units at regular intervals, rather than
at random.This may be used when a fixed proportion, e.g. 20%, of the village house-
holds, are to be sampled. For example, the starting house may be selected at ran-
dom, and then a bottle is spun and the fifth house in that direction is also sampled,
and the procedure is repeated until sufficient households are recruited.
If a sampling frame is difficult to obtain,if the population is spread out over a large area
or if there are subgroups, the following more complex methods may be used:
1 Stratified sampling is used when there are distinct groups or strata with different
expected frequencies of the outcome or exposure of interest (e.g. age, gender, or
other potential confounders).To ensure that the sample represents the population,
an equal proportion is sampled from each strata using simple random sampling.
2 Multi-stage sampling uses the organizational structure of the study population,
with a sampling frame required only for the higher-level unit, and for the primary
23346.indb 6323346.indb 63 22/08/2011 15:1222/08/2011 15:12

sampling units within those higher levels sampled. For example, in a study of
school children (i.e. primary sampling units), first x number of schools will be
randomly sampled from a regional list, and then y number of children will be
randomly sampled from within each selected school. If the schools are of different
sizes, then sampling is carried out using ‘probability proportional to size’, such that a
school with three times as many pupils will be sampled three times more than
another school.
3 Cluster sampling also uses the organizational structure,but samples all or most of the
primary sampling units.An equal probability of sampling the higher-level units is used,
regardless of differences in size.For example,in an intervention study of the protec-
tive effect of insecticide-treated mosquito nets, where the intervention is known to
protect other household members, x number of households (i.e. higher-level unit)
would be sampled, and all eligible household members (i.e. primary sampling units)
within sampled houses would be included in the sample.
Selection criteria
The sample population should represent the general population to whom the results
will be applied. However, in some cases it is necessary to exclude certain individuals
(e.g. those who may be at greater risk of loss-to-follow-up). It is therefore important
to develop clear inclusion and exclusion criteria. Inclusion criteria specify the
sample population of interest. For example, a study of diabetes in pregnancy may
specify ‘women enrolled in their first trimester of pregnancy’ to obtain sufficient
baseline data. Exclusion criteria specify those individuals who are not eligible for
inclusion in the study, perhaps because they have underlying conditions that may
interfere with assessment of the outcome. For example, in a study of the incidence of
clinical malaria fevers, children with severe anaemia (haemoglobin < 5g/dl) at baseline
may be excluded because they require medical treatment and may be more prone to a
severe outcome.
Informed consent
Ethical permission will need to be obtained from institutional and national ethical bod-
ies before starting any epidemiological studies (and often prior to obtaining funding).
For large-scale field trials it is appropriate to inform local government and civil society,
and community sensitization meetings may improve local understanding of the study
aims and thus cooperation with investigators and recruitment to the study.
Before participants are recruited into an epidemiological study, they must be made
fully aware of what the study is about and what the potential risks are.Participants then
need to give their consent to participate. This is known as informed consent.
Sometimes it is not possible for the participant to provide their consent, for example,
in the case of a child or an unconscious patient,in which case consent must be obtained
from a parent, caregiver or close relative. The information must be provided in the
language of the consent giver and, if they are illiterate, the information must be clearly
read to them.Consent usually takes the form of a signature,or a fingerprint in the case
of illiterate consent givers. Details of the format of information and consent should be
clearly stated when the results of the trial are reported.
23346.indb 6423346.indb 64 22/08/2011 15:1222/08/2011 15:12

It is also important that individuals are allowed to refuse to participate and that
participants have the option to drop out of the study at any time, without any adverse
consequences for their access to preventive or treatment services.
Activity 5.2
1 In a region of country X, all single births occurring in four randomly selected dis-
tricts during a one-week period were identified from a birth register to assess the
gender ratio.What was the outcome measure, what type of sampling was used and
what were the inclusion criteria?
2 In a large secondary school with 9 classes of children aged 9–12 years old, 100 girls
were randomly selected from the class-registers to be tested for rubella antibodies.
What was the outcome measure,what type of sampling was used and what were the
inclusion criteria?
3 In countryY, six of 15 regions were randomly selected. Five per cent of households
were subsequently selected from each of these six regions and a survey on access
to healthcare among children under 5 years of age administered. What was the
outcome measure, what type of sampling was used and what were the inclusion
criteria?
Data collection
The key to conducting a good epidemiological investigation is to plan the data collec-
tion and the analytical approach beforehand. Even studies with large sample sizes and
unbiased subject selection can be seriously flawed if key data (e.g.confounders) are not
collected. The methods used to collect the data will depend on the exposures and
outcomes being studied and how practical and costly it is to collect them. Data may be
quantitative (i.e. measurable and relating to ‘what?’,‘where?’ and ‘when?’) or qualitative
(i.e. descriptive and relating to ‘why?’ and ‘how?’).
Data may be obtained from sources of routinely collected information on outcomes
or exposures (e.g. medical records, census data, health surveys, cancer registries,
records kept by schools or employers).These indirect data collection methods have
the advantage that the data are already available and can provide information relatively
quickly and cheaply. However, data quality may be poor due to missing or inaccurate
data. Routine data systems are designed to serve other objectives, such as surveillance,
and not a research study, so may not be able to provide all the information required.
Therefore, a combination of data collection methods may be used.
Most epidemiological studies obtain data directly from the study participants
(or their caregivers). Direct data collection methods include questionnaires (e.g. self-
administered,filled in by an investigator),structured interviews (e.g.conducted face-to-
face, by telephone) and clinical examination (e.g. having a blood sample taken for a
diagnostic test).The advantage of direct data collection is that it is collected prospec-
tively (even though questions may relate to historical events) and questionnaires
are designed for the specific study. However, in addition to being costly and time-
consuming, there may be recall bias or a poor response rate.
Environmental data can also be collected, and the recent advancements in global
positioning system (GPS) technology enable us to identify the precise geographic loca-
tion of a household,village or health centre,for example.Specific data may be collected
23346.indb 6523346.indb 65 22/08/2011 15:1222/08/2011 15:12

during an epidemiological study, or from routine sources of climate data (e.g. rainfall,
cloud cover), satellite images (e.g. land-use, road access), etc.Whereas John Snow used
a simple spot map to identify the cause of the cholera outbreak in 1854 (see Chapter
1),such data can now be analysed using more sophisticated digital technology.Different
layers of data (e.g. geographical, epidemiological) can be linked using geographic infor-
mation systems (GIS), using the location of the data in space and time.This allows a
more complex analysis of the data, enabling us to measure the incidence of childhood
cancer in relation to distance to the nearest electricity pylon, or the prevalence of
malaria infection in relation to altitude and rainfall, for example.
Qualitative methods of direct data collection in epidemiological research may take
different forms. Structured interviews can include quantitative or qualitative data.They
provide a framework for the interviewer, defining the wording and question sequence
to improve the validity of responses. Other qualitative methods such as semi-
structured interviews, participant observation or focus group discussions, rarely
include quantitative data, and usually deal with limited numbers or non-randomly
selected participants, making them inappropriate for the measurement of epidemio-
logical associations. The utility of such methods will depend on the culture and
sensitivity of the topic.
Unique identifiers
Investigators must be able to link all necessary data to the appropriate study partici-
pant,using a relational database,which is a method of relating different layers of data.A
study using multi-stage or cluster sampling will need to collect and link data on the
different sampling levels.A cohort study will repeatedly measure individuals,such as the
baseline measurement and final contact recording the outcome. In addition to names
being common or misspelled, they should not be used, as the identity of participants
should be kept confidential and results must always be reported anonymously.
Unique identifiers should be created for each sampling unit (e.g. individual, household,
hospital) and used whenever data are collected.For example,a cohort study of malaria
in children will include a unique identifier per child (e.g. number 00142) and then
collect data on the child (e.g. name, date of birth, gender), the child’s household
(e.g.household size,distance to nearest health facility),and health facility visits (e.g.data
of outpatient attendance, body temperature, haemoglobin level, presence of malaria
parasites). Different data collection tools may be used for each layer of data, but all
(e.g. household questionnaire, clinic record, blood slide) must record the same unique
identifier that will enable, for example, a laboratory test result to be linked to the
correct patient.
Data management
It is important that data collection is standardized and investigators ensure the validity
of the methods used (i.e. that they really are measuring what they aim to measure).
Data collection tools need to be carefully designed and pre-tested (‘piloted’) to reduce
data errors. Data format and the legitimate values or ranges for quantitative data need
to be defined when developing data collection tools and training those collecting data.
Data collection tools include questionnaires, specimen labels for clinical samples and
audio/video recordings for qualitative data.
23346.indb 6623346.indb 66 22/08/2011 15:1222/08/2011 15:12

Data may be recorded on paper and entered into a computer, or may be directly
entered into a computer or hand-held digital device.When data are being transferred
from paper to a computer,it is advisable to double-enter the data to reduce data-entry
inputting errors.The computer programme should also be designed to restrict entry
only to feasible response values,e.g.prevent the entry of gender as anything other than
‘male’,‘female’ or ‘unknown’.
The data should be ‘cleaned’ periodically.This refers to checking the data to ensure
that there are no impossible values (e.g. 50-year-old infants), to check for missing
values, and to ensure that data can be linked (e.g. every participant enrolled has an
outcome measure).
Data variables
The term ‘variable’ refers to quantitative data that can have more than one value, and
is usually applied to each distinct unit of data that is collected.There are three types of
quantitative variable:
1 Binomial variables only have two values (e.g.Yes/No, Male/Female).
2 Categorical variables have several values (e.g. age groups: 0–4 years, 5–9 years,
10–14 years; religion: Christian, Muslim, Jewish, etc.).
3 Continuous variables can have any value within a given range (e.g. blood pressure;
age in years, months, or days).
Continuous variables can be grouped into categories, and categorical variables can be
further grouped into binary variables.This increases the sample size in each category,
providing greater statistical power to detect any effect. For example, haemoglobin
concentration is a continuous variable, which can be grouped categorically as mild
(8–11 g/dl), moderate (5–8 g/dl) or severe (<5 g/dl) anaemia. It can also be grouped
binomially as moderately anaemic (<8 g/dl): Yes/No, for example. If qualitative data
are used to deﬁne outcomes or exposures (e.g. a case-control study of post-natal
depression and a history of depression), these will need to be coded as binomial or
categorical variables to measure the epidemiological association.
Data analysis
Data may be summarized according to the variable type. Binary and categorical
variables may be summarized as proportions of the total (e.g. 49% male and 51%
female).Continuous variables are usually presented as the average value of the variable
and the amount of variation around this average.This may be summarized as a mean
(sum of values divided by the number of values) and standard deviation, or median
(midpoint of ordered values) and interquartile range (25–75%, i.e. middle 50% of
ordered values). Such summary values are used to present the baseline characteristics
of the study sample,to compare exposed with unexposed groups,or to compare cases
with controls.
Descriptive data may be presented graphically. In epidemiology, histograms (see
Figure 5.1a) are most commonly used to describe the distribution of a continuous
outcome, while bar charts (see Figure 5.1b) are used to compare the mean or propor-
tional distribution of a variable by categories. Analytical data may also be presented
23346.indb 6723346.indb 67 22/08/2011 15:1222/08/2011 15:12

graphically, most commonly as a scatter plot (see Figure 5.2) when investigating the
relationship between two continuous variables.
In Chapters 2 and 3 you saw how to present measures of frequency for the outcome
of interest and measures of association for the effect of interest. Statistical tests (e.g.
chi-squared test or t-test) that will not be described here are used to test the null
hypothesis.This is the opposite of the hypothesis being tested, i.e. that there is no
association between the exposure and outcome.The P-value represents the probability
that an association at least as big as the one observed could have occurred by chance
alone, if there truly was no association.
Figure 5.1 (a) Histogram of the frequency distribution of haemoglobin concentration (g/dl) values from
a cross-sectional survey of children. (b) Bar chart of the proportion of children in a refugee camp under-
weight by ethnic group
23346.indb 6823346.indb 68 22/08/2011 15:1222/08/2011 15:12

Regression models
These analyses can also be undertaken using more complex statistical methods
known as regression models, which cannot be described in detail here. Brieﬂy,
regression is a way of describing the relationship between a variable and potential
explanatory factors; in epidemiology this is usually the relationship between an out-
come and an exposure or confounding factors. Regression models use data on the
explanatory factors to predict the outcome (for further information see Kirkwood and
Sterne 2003).
Continuous variables, such as blood pressure or haemoglobin concentration, may
be analysed using linear regression, with the results presented as a mean and
standard deviation. Binary variables (e.g. prevalence, risk) can be analysed using
logistic regression with results presented as an odds ratio. While this is frequently
used, it must be remembered that this is only valid for rare outcomes, where the
prevalence or risk are approximately equal to the odds (see Chapter 3: Comparability
of measures of association on p. 31). Incidence rates may be analysed using
other regression models (i.e. Poisson, negative binomial) with results presented
as an incidence rate ratio. Categorical variables can be included as explanatory
variables in a model but not as outcome variables, so an outcome such as the
Glasgow coma score (a neurological scale of consciousness ranging from 3–15)
would need to be reclassiﬁed as a binary variable and analysed using logistic
regression.
If an exposure variable has more than two categories (e.g. ethnicity), we would need
to decide which to use as the reference category to compare the other categories
against. For example, for a quantitative variable such as exposure to smoking, non-
smokers may be used as the reference or unexposed group, and other categories (e.g.
ex-smokers,infrequent smokers,frequent smokers) can each be treated as the exposed
group in turn. For a qualitative variable, such as religion, the choice of reference cate-
gory is arbitrary.A categorical exposure will result in several relative risks, and you will
Figure 5.2 Scatter plot of national incidence of breast cancer per 100,000 person-years,by estimated per
capita alcohol consumption for selected countries
Source: Drawn by Ilona Carneiro using selected data from Schatzkin et al. (1989).
23346.indb 6923346.indb 69 22/08/2011 15:1222/08/2011 15:12

see the relative risk for the reference category presented as 1.00 (i.e. frequency in
unexposed divided by frequency in unexposed). Differences between non-reference
categories can be assessed by comparing their 95% confidence intervals:if they overlap,
then there is no significant difference at the P = 0.05 level.If the exposure can be quan-
tified (e.g. low, medium or high alcohol consumption), the relative risks are examined
for a dose–response effect.
Univariate regression analyses the effect of just one explanatory variable and the
measures of frequency or association from univariate regression analysis are called
‘unadjusted’.The real benefit of regression models is in multivariate regression, which
enables us to look at the effect of several variables at the same time and therefore
control for other risk factors and confounders.The measures of frequency or associa-
tion from multivariate regression are ‘adjusted’ for all the variables included in the
model.
If the measure of association varies across categories of a third variable, this is
known as interaction or effect modification because it modifies the effect of the
exposure of interest. For example, if the relative risk of ischaemic heart disease in
heavy smokers compared to non-smokers is greater at younger ages than at older ages,
we would say that age-group was an effect modifier, or that there was an interaction
between age and smoking exposure.
Meta-analysis
When several studies of the same exposure–outcome association are available,
it may be possible to obtain a combined estimate effect.A meta-analysis uses complex
statistical techniques to estimate a combined effect from several studies on the
assumption that, despite study differences, the increased statistical power will
provide an estimate closer to the true value. A systematic literature review is
conducted to identify all published and unpublished records of relevant studies.
Predefined inclusion and exclusion criteria are used to select studies of sufficiently
good quality and where the methodological differences are not too extreme.
In its most simple form, a meta-analysis weights the individual estimates in relation
to the sample size of each study.The results of a meta-analysis are usually presented
graphically in a forest plot (see Figure 5.3) showing the spread of estimates of
effect from individual studies together with the combined estimate of effect. A
meta-analysis may be especially useful when faced with conflicting evidence from
different studies.
Dissemination of results
As epidemiological studies involve the participation of human subjects, there is a duty
to disseminate the results of these studies not only to the scientific and public health
communities,but also to those individuals and communities participating in the studies.
This may be done through leaflets for participants, community meetings, health educa-
tion campaigns or providing information to support groups (e.g. Parkinson’s Disease
Society). It may also be appropriate to present the results to ministries of health or
local policy-makers and implementers.The dissemination of study findings should be
planned from the beginning, as this helps to focus the study on obtaining information
that will be relevant to the end-user.
23346.indb 7023346.indb 70 22/08/2011 15:1222/08/2011 15:12

Activity 5.3
For each of the following studies identify the study design, the outcome and
exposure of interest, and state whether the variables are binary, categorical,
continuous or qualitative. List potential confounders for which you might also want to
collect data.
1 The caregivers of 500 children were invited to participate in an epidemiological study
by bringing the children for testing for malaria parasites at a central point during a
5-day period. Caregivers were asked about the number of mosquito nets in the
household and other information.
2 17,530 men working in the British civil service were surveyed about their grade of
employment (e.g. administrative, executive, clerical) and then followed-up for seven
and a half years, during which there were 1,086 deaths.
3 Investigators observed and recorded whether the prescribing practice of ten
doctors to each of ten patients with respiratory tract infections was consistent
with national guidelines on antibiotic prescription. They then assessed whether
symptoms had resolved in these 100 patients at a home follow-up visit after
15 days.
Figure 5.3 Forest plot of estimates from 15 studies of the relative risk of heterosexual HIV infection
among circumcised males compared with uncircumcised males. The shaded square and horizontal line
correspond to the relative risk and 95% confidence interval for each study.The area of the shaded square
reflects the weight of each study.The diamond represents the estimate of combined relative risk and 95%
confidence interval
Source: Weiss et al. (2000).
23346.indb 7123346.indb 71 22/08/2011 15:1222/08/2011 15:12

4 80 women with breast cancer and their twin sisters without breast cancer were
questioned about their previous history and length of oral contraception use.
Conclusion
In this chapter you have reviewed the characteristics of each of the main epidemio-
logical study designs. You have been introduced to the basics of sample selection,
sample size calculation, data collection and analysis. These issues will be discussed
further in subsequent chapters on specific study designs, and should be considered
when critically reviewing any epidemiological data.
References
Doll R and Hill AB (1950) Smoking and carcinoma of the lung; preliminary report. British Medical Journal 2:
739–48.
Kirkwood BR and Sterne JAC (2003) Essential Medical Statistics. Oxford: Blackwell Science.
SchatzkinA,Piantadosi S,Miccozzi M and Bartee D (1989)Alcohol consumption and breast cancer:a cross-
national correlation study. International Journal of Epidemiology 18: 28–31.
Schulz KF and Grimes DA (2002) Case-control studies: research in reverse. Lancet 359: 431–4.
Weiss HA, Quigley MA and Hayes RJ (2000) Male circumcision and risk of HIV infection in sub-Saharan
Africa: a systematic review and meta-analysis. AIDS 14: 2361–70.
Feedback on activities
Activity 5.1
1 This is case-control study, with twice as many controls as cases. Study participants
are identified in relation to their outcome status, although we are not told how
controls were selected.The odds ratio of exposure is the only measure of associa-
tion that can be calculated for a case-control study.
2 This is a cohort study, which would prospectively measure the incidence of
heart disease in relation to various exposures recorded at the start of the study.
As this is a follow-up study, the incidence will be measured, so that either the
risk ratio, odds ratio or incidence rate ratio could be calculated. Given the high
likelihood of loss-to-follow-up for a ten-year study, the most appropriate measure
would be the incidence rate ratio, if person-time at risk has been sufficiently
recorded.
3 This is an intervention study, using untreated mosquito nets as the control for the
intervention of treated mosquito nets.We are not told whether it is a randomized
trial, or whether observers or participants are blinded to the outcome. The fre-
quency measure is prevalence of anaemia, therefore the appropriate measure of
association would be the prevalence ratio.
4 This is an ecological study,comparing the incidence of infant mortality with exposure
to gross domestic product,an indicator of standard of living at a population (national)
level.The measure of frequency is incidence,however,there is no measure of person-
time at risk.The preferred measure of association would be the risk ratio, although
the odds ratio could also be calculated.
23346.indb 7223346.indb 72 22/08/2011 15:1222/08/2011 15:12

5 This is a cross-sectional study measuring existing (prevalent) infections, and there-
fore prevalence ratio will be the appropriate measure of association between house-
hold access to running water and ascaris infection.
Activity 5.2
1 The outcome measure of interest would be prevalence of males (or females).This is
a cluster sample, with all births in a deﬁned period being sampled for each selected
district. The inclusion criteria would be all single births, i.e. multiple births (twins,
triplets, etc.) would be excluded.
2 The outcome measure of interest would be the prevalence of rubella seropositivity
(proportion with rubella antibodies). Simple random sampling was used, as the girls
could have been from any of the nine eligible classes.The inclusion criteria would be
girls, aged 9–12 years old, providing informed (parental) consent (as blood samples
would need to be taken).
3 The outcome measure of interest would be access to healthcare (e.g. percentage
of children taken to a health clinic with 48 hours of fever onset).This is a multi-stage
sample. First, the regions were selected by simple random sampling, and then
5% of households in each region were selected, such that larger regions would
contribute more households to the study sample. Inclusion criteria would be
households with at least one child under 5 years old and consenting to participate in
the survey.
Activity 5.3
1 This is a cross-sectional study of the relationship between malaria prevalence and
household mosquito net ownership. Prevalence is a binary outcome, while number
of mosquito nets is a continuous exposure (depending on household size), which
could be regrouped as categorical (e.g. 0, 1–2, 3+) or binary (i.e. 0, 1+).The measure
of association would be the prevalence ratio.
Potential confounders should include socio-economic indicators that are likely to
affect mosquito net ownership and prevalence of malaria.
2 This is an occupational cohort study measuring the relationship between employ-
ment grade and incidence of all-cause death. The exposure is categorical, and the
outcome could be binary (risk of death) or continuous (mortality rate,if the person-
time at risk is known for each individual).The measure of association would be a risk
ratio or incidence rate ratio.
Likely measurable confounders are smoking history, medical conditions, blood
pressure, body-mass-index (weight divided by height-squared), etc.
3 This is a cohort study following-up participants to measure the ‘risk’ of cure, which
is a binary outcome.The explanatory variable is qualitative and was measured using
participant observation.It would need to be coded as binary (e.g.according to guide-
lines, not according to guidelines) or categorical (e.g. number of guideline points
met). Presumably many more than ten patient consultations would be observed in
order to avoid observer inﬂuence and to recruit ten patients with respiratory tract
infections). The measure of association would be a risk ratio.
Confounders would relate to differences between the prescribing doctors and
their practices that might also affect patients’ risk of cure. For example, a more
onscientious doctor who might prescribe correctly, might also be more likely to
explain medication instructions, antibiotic compliance and second-line measures
23346.indb 7323346.indb 73 22/08/2011 15:1222/08/2011 15:12

to the patient. Likewise, a busy doctor in an under-resourced neighbourhood may
make more prescribing mistakes and the patients may have poorer general health.
4 This is a matched case-control study, where each breast cancer case is individually
matched with a control on the basis of genetics, age and some socio-behavioural
factors.The outcome is binomial (cancer or no cancer), and the explanatory variable
may be continuous (number of years of contraceptive use) or categorical (e.g. none,
<2 years, 2–5 years, 5–10 years, 10+ years of contraceptive use). The measure of
association will be the odds ratio of exposure, as this is a case-control study.
Age,family history of breast cancer,and ethnicity have already been controlled for.
Potential confounders that may be associated with length of contraceptive use and
risk of breast cancer include parity (i.e. number of live births), breast-feeding
practices, onset of menopause, alcohol use and physical activity.
23346.indb 7423346.indb 74 22/08/2011 15:1222/08/2011 15:12

Overview
Ecological studies analyse epidemiological associations at a population or group level,
usually using data collected for other purposes.While the ecological design is relatively
convenient and inexpensive, it is subject to many biases. In this chapter you will review
the characteristics, advantages and limitations of the ecological study design for
analytical epidemiology. You will be introduced to different sources of routine data,
and methods of standardization to compare data from populations with different
demographic structures.
Learning objectives
• describe the features and uses of ecological studies
• identify different sources of routine data that may be used
• define and calculate standardized rates, using direct or indirect methods, to
compare populations
• discuss the potential sources of bias and confounding in ecological studies.
What defines an ecological study?
Ecological studies analyse the relationship between outcome and exposure at a population
level, where ‘population’ represents a group of individuals with a shared characteristic
such as geography, ethnicity, socio-economic status or employment.The defining factor
of an ecological study is that data on both outcome and exposure are not linked to,and
usually not available for, individual study participants.The unit of analysis is the group,
and outcome and exposure are summarized at the group level. For example, the inci-
dence rates of an outcome in two groups are compared with the proportion of each
group exposed to a potential risk factor.
Advantages and disadvantages
The main reasons for undertaking an ecological study are as follows:
1 When data are only available at a group level,or differences may vary more between
groups/areas than within groups/areas (e.g. air pollution, healthcare services, and
climate variation between regions).
6Ecological studies
23346.indb 7523346.indb 75 22/08/2011 15:1222/08/2011 15:12

2 If data are difﬁcult to measure at an individual level, for example, because of consid-
erable variation in individual dietary habits, group averages may be easier to distin-
guish (e.g. ethnic or social differences in alcohol consumption may be more
consistent than individual measures).
3 To study group-speciﬁc effects where interventions may be aimed at the group level
through control programmes,health policies or legislation,such as injury prevention
through national road safety laws.
4 When data are readily available (faster and less expensive to collect) at a group level,
as with indirect data sources from routine monitoring, population registries, demo-
graphic surveys or censuses.
However, because the data on exposure and outcome are not linked at the individual
level, it is not possible to infer causality.This design suffers from many potential biases
(see Interpretation section on p. 85). It may also be necessary to standardize data (see
Analysis section on p. 80) if the groups being compared have different demographic
characteristics (e.g. age distribution).
Study design
An ecological study may compare populations or groups using a multi-group design,
periods of time using a time-trend design, or groups and time using a mixed design. In a
multi-group study, data on the frequency of an outcome may be measured individually
and aggregated (combined), or estimated for particular groups (e.g. country, district,
hospital). Similarly, individual-level data on exposures are aggregated for the same
groups.The relationship between outcome and various exposures are then compared
at this group level to see if an association can be found. Figure 6.1 shows that the
Figure 6.1 Incidence of neonatal and maternal mortality by percentage of births without a skilled birth
attendant for different regions
Source: WHO (2005).
23346.indb 7623346.indb 76 22/08/2011 15:1222/08/2011 15:12

Ecological studies 77
incidence of neonatal and maternal mortality for each WHO region increases with
the percentage of births without a skilled birth attendant.This design is often used to
compare spatial (geographical) patterns in the frequency of an outcome. For example,
by comparing the geographical distribution of populations with high frequency genetic
blood disorders (e.g. thalassaemia) with that of malaria, it was suggested that such
genes might provide some protection against malaria infection. The use of geographical
information systems (see Chapter 5) has enabled more sophisticated analyses of envi-
ronmental risks for health outcomes.
In a time-trend study, data on outcome and exposure for a given population are
compared over a period of time. Comparisons can investigate whether changes in
incidence of an outcome over time correlate with changes in risk factors or coverage
of an intervention over the same period (e.g. changes in air quality and incidence
of asthma in children). However, if the outcome has a long or unknown latent period
(i.e. where it is present but not yet detected), time-trend analysis may be difﬁcult to
interpret.In addition,it is possible that the association between exposure and outcome
may vary over time, making interpretation of a time-trend analysis more complicated.
Mixed-studies compare different groups over time, and if consistent differences are
seen this may lend weight to a causal association, as in Bradford-Hill’s considerations
for causality (see Chapter 4).
Sampling
The choice of study sample in ecological studies is often deﬁned by availability and
quality of routinely collected data.For example,hospital records may vary according to
institution, and using these to compare outcome frequencies for different hospital
catchment areas will subject the analysis to inherent selection and information bias of
each hospital’s record-keeping systems.
Data collection
Data may be measured:
1 at an individual level and aggregated at a group level, such as data on cancer inci-
dence from a cancer registry,or all-cause mortality rates from consecutive censuses.
2 at a group level but vary by individual, such as estimated neonatal and maternal
mortality rates, and percentage of births without a skilled birth attendant byWHO
region (see Figure 6.1).
3 at a group level as they are attributes of the group and do not vary by individual,such
as national estimates of life expectancy and gross domestic product (see Figure 6.2).
Routine data sources
Many ecological studies utilize data collected routinely for other purposes,as these are
readily available at little or no cost. Routine data often provide baseline information to
describe a population, and variations in health outcome (e.g. by age, sex, ethnicity,
geography). If routine data are collected systematically over time, we can study the
23346.indb 7723346.indb 77 22/08/2011 15:1222/08/2011 15:12

progression of an outcome in a population or the impact of a health intervention such
as screening or vaccination.
However,the accuracy of such data depends on the infrastructure available to collect
them and how they are used.The more often a data source is used, the greater the
incentive to ensure that data are complete, valid and accurate. Routine data sources
include:
1 demographic data through population censuses and household surveys;
2 births and deaths through vital registration systems or demographic surveillance
systems;
3 information on chronic conditions through outcome-speciﬁc registries.
Demographic data
Demographic data describe the basic characteristics of a population, such as age,
gender, ethnic group, religion and socio-economic indicators. Many countries collect
demographic data through regular population censuses. A census is the systematic
collection of data about all members of a population, as opposed to a sample, at one
time-point using a cross-sectional design. While in high-income countries censuses
may take the form of postal questionnaires, countries without sufﬁcient infrastructure
require census staff to undertake door-to-door visits.A full population census is ideally
Figure 6.2 Gross Domestic Product (GDP) per capita and life expectancy at birth in 169 countries (1975
and 2005)
Source: WHO (2008).
23346.indb 7823346.indb 78 22/08/2011 15:1222/08/2011 15:12

carried out at regular intervals (e.g. every ten years), however, given its complexity and
cost,this is not always possible.Census data may also be used to provide data on fertil-
ity, mortality and key health indices in countries with poor vital registration (see below).
Censuses provide data on the demographic structure of a population that are
needed for data standardization (see Analysis section on p. 80). The World Health
Organization (WHO) publishes estimates of population size and key health indicators
for its 193 member states on the Internet (World Health Organization 2011).While
these may not be as detailed as some locally collected data, it does enable us to make
national comparisons.
Population health surveys are also conducted by some countries to provide informa-
tion on specific demographic groups or health outcomes.UNICEF undertakes Multiple
Indicator Cluster Surveys to provide information on health indicators. Demographic
and Health Surveys (DHS) collect nationally representative data from household sur-
veys in developing countries using standardized methodologies and data collection
methods.These data are also publicly available (Measure DHS 2011) and can be used
to form the basis for ecological studies comparing national or sub-national populations,
or to show changes in health outcomes over time in response to changing exposures
and public health interventions.
Vital registration data
Many countries collect data on births and deaths by age, sex and cause through an
official birth and death certification, known as civil registration. Birth data may be used
as a health outcome or to provide a denominator for mortality. Death data may be
used as an outcome, or as an indicator of population health and the provision of
medical care to large populations, i.e. as an exposure. The main indicators used
for national and sub-national analyses are neonatal (first 28 days of life), infant
(1–11 months of age) and under-five (<5 years of age) and maternal mortality per
1,000 (or 100,000) live births. Note that while these are often called rates, they are
actually risks (see Chapter 2). For example, infant mortality in Mozambique fell from
155 per 1,000 live births in 1990 to 96 per 1,000 in 2009.This decline may be inter-
preted as evidence of improvements in medical care, sanitation and housing in
Mozambique between 1990 and 2009.
Cause-specific mortality statistics are usually based on identifying a single underlying
(primary) cause of death, defined as the ‘disease or injury that initiated the series of
events leading directly to death, or the circumstances of the accident or violence that
produced the fatal injury’. In addition to the underlying cause of death, data is also
recorded on significant conditions or diseases, for example, diabetes, which may have
contributed to death.
These data allow comparison of mortality within countries, over time, and with
other countries if the same definitions are used.To enable comparisons to be made, a
single standardized coding system is used when death certificates are collated.Trained
personnel use the International Classification of Disease (ICD), the tenth version of
which came into use in 1994,to code cause of death.However,there may be information
bias related to the accuracy of clinical diagnoses, completion of the registration of
death, or the subsequent coding. For example, outcomes that are stigmatized
(e.g. maternal death due to illegal abortion, suicide, HIV/AIDS) may not be accurately
reported. All these factors need to be considered when using and interpreting
these data.
23346.indb 7923346.indb 79 22/08/2011 15:1222/08/2011 15:12

The WHO collates data on registered deaths by age group, sex, year and cause of
death for individual member states as part of its mandate to provide health information
worldwide (World Health Organization 2011).However,the proportion of deaths that
are registered in a population will be lower in settings with weaker infrastructure for
certification and collation of data on numbers and causes of death.The ‘completeness’
of mortality data will depend on access to formal health services,and is likely to be less
in low-income countries and rural areas. Some countries use sample vital registration
to collate data on births, all-cause deaths and cause-specific deaths in a nationally rep-
resentative sample of population clusters, to obtain data that can then be extrapolated
to national level. In some countries, demographic surveillance sites collect vital regis-
tration data on a defined population.While these may not be nationally representative,
they may provide useful indications of trends over time,and may be used for ecological
analyses of risk factors.
Disease registries
Data from disease registries are frequently used in ecological studies for comparison
of trends over time, and comparison between populations within a country and
between countries with similar registration systems.These will be discussed in more
detail in Chapter 12, as they are also used for surveillance.
Analysis
In ecological studies, measures of exposure and outcome are often continuous (e.g.
disease prevalence, mortality rate, proportion of population exposed to a particular
factor, mean temperature in a geographical region). Such data need to be displayed as a
scatter plot (see Figure 6.2) in which the outcome variable is plotted against the expo-
sure variable. From this we can determine whether there seem to be any trends in the
data, which can then be confirmed using statistical methods (correlation or regression
models). Correlation measures how closely two variables are associated, while regres-
sion describes the relationship mathematically, enabling the prediction of one variable
from another (for further information, see Kirkwood and Sterne 2003).Alternatively, if
the outcome can be grouped as two comparison groups, we can estimate the relative
risk of outcome for a given exposure. Regression models can then be used to estimate
the relative risk for continuous exposures and adjust for potential confounders.
Standardization
In an ecological study, the data may come from different places (e.g. countries, regions
within a country) or from the same population during different time-periods.
Comparing the crude incidence rate of an outcome may result in significant confound-
ing if there are differences in the age-structure or other demographic characteristics
(e.g. gender, ethnic group) between these different data sources. For example, Figure
6.3 shows that the male population of South Africa has many more children and young
people than elderly, whilst Switzerland has a more middle-aged and older population.
Age standardization will be described here to overcome such differences, although the
same methods can be applied to standardization for other demographic characteristics.
23346.indb 8023346.indb 80 22/08/2011 15:1222/08/2011 15:12

To reduce confounding, we standardize the data by comparing them to a population
for which the demographic structure is known (‘standard population’) using direct or
indirect methods. There are available ‘standards’ based on averages from world or
European populations, however, the actual population structure used as the standard
does not matter, so long as the same structure is used for all populations being com-
pared.This is because the standardized rate that results cannot be used as a real value
(i.e. it does not relate to a population, time and place), but only allows us to compare
populations and to calculate incidence rate ratios adjusting for differences in their
underlying structures.
Direct standardization is used when we know the group-specific outcome rates
in the study population.The age-specific rate is the incidence rate (number of cases
divided by the person-time at risk) calculated separately for each age group.The per-
centage of the standard population in each age group is multiplied by the age-specific
Figure 6.3 Population age-distribution of males in Switzerland and South Africa in 2005
Source: Drawn by Ilona Carneiro using data from United Nations Population Division (2008).
23346.indb 8123346.indb 81 22/08/2011 15:1222/08/2011 15:12

rate for that age group in the study population to obtain a weighted average.The sum
of these across all age groups divided by 100 gives a standardized rate for the whole
population.The directly standardized rate is therefore the expected rate in the stand-
ard population if the age-specific rates of the study population had applied.
We will illustrate this with an example.The mortality rate for all cancers in men in
2007 was 246 per 100,000 in Switzerland and 58 per 100,000 in South Africa (World
Health Organization 2010).We might calculate the incidence rate ratio as 246 ÷ 58 =
4.24 and conclude that men living in Switzerland have a four times greater risk of dying
from cancer than those living in South Africa. Since we know from Figure 6.3 that the
age-distribution of these two populations is different, we might want to look more
closely at the age-specific rates to see at which ages this huge difference occurs.
However, Figure 6.4 suggests that the age-specific rates are actually very similar until
old age, at which point men aged over 85 years old have almost twice as much risk of
dying of cancer in South Africa than in Switzerland. How can we make sense of these
contradictory results?
Figure 6.4 Age-specific male cancer mortality rates for 2007 in Switzerland and South Africa
Source: Drawn by Ilona Carneiro using data from WHO cancer mortality database (2010).
To compare these data properly we must standardize the crude rates to see how
many cancer deaths we might expect if the two populations had the same age-
structures.Table 6.1 shows the World Standard Population developed by the WHO
and based on the predicted average age structure of the world’s population from 2000
to 2025 (Ahmad et al.2001).Using this,we can calculate the expected cancer mortality
rate in each population of interest if they had the same population age-structure.
First, multiply the study population age-specific mortality rate by the percentage of
the standard population for each age group,then sum all of these and divide by 100.The
23346.indb 8223346.indb 82 22/08/2011 15:1222/08/2011 15:12

male cancer mortality rate for Switzerland standardized for age is 145 per 100,000 and
for South Africa is 154 per 100,000.These are similar, indicating that after adjusting for
differences in age-structure there is no difference in the overall incidence rate of can-
cer mortality between these two countries, although the age-specific rates will differ.
Indirect standardization calculates the expected number of cases in the study
population if the age-specific rates of a‘standard’ population had applied.It can be used
if we do not have age-specific rates for the study population of interest, but we know
the population structure and the total number of cases.The expected number of cases
is then used to calculate a standardized mortality (or morbidity) ratio (SMR),
which compares the observed number of deaths (or poor health outcome) to that
expected in the same population.The SMR is interpreted in the same way as a relative
risk and is calculated as:
Table 6.1 Direct standardization of Swiss and South African (SA) 2007 male cancer mortality rates
per 100,000
Age group (years) World standard
population (%)
Swiss 2007
age-specific
mortality rate*
Expected rate*
in Switzerland
SA 2007
age-specific
mortality rate*
Expected rate*
in SA
0–4 8.86 1.60 14.18 2.70 23.92
5–9 8.69 3.00 26.07 1.80 15.64
10–14 8.60 1.80 15.48 1.80 15.48
15–19 8.47 2.60 22.02 3.40 28.80
20–24 8.22 6.10 50.14 5.50 45.21
25–29 7.93 8.60 68.20 9.10 72.16
30–34 7.61 9.20 70.01 20.10 152.96
35–39 7.15 11.70 83.66 32.70 233.81
40–44 6.59 28.40 187.16 53.50 352.57
45–49 6.04 58.60 353.94 102.70 620.31
50–54 5.37 147.10 789.93 167.70 900.55
55–59 4.55 255.70 1,163.44 279.00 1,269.45
60–64 3.72 452.50 1,683.30 370.10 1,376.77
65–69 2.96 671.40 1,987.34 596.60 1,765.94
70–74 2.21 969.80 2,143.26 860.50 1,901.71
75–79 1.52 1,464.00 2,225.28 1,321.30 2,008.38
80–84 0.91 2,015.30 1,833.92 2,115.30 1,924.92
85+ 0.63 2,838.30 1,788.13 4,330.70 2,728.34
Total 100.00 14,505.45 15,436.91
Note: * per 100,000 population
Source: Ilona Carneiro, using data from Ahmad et al. (2001) and WHO cancer mortality database (World Health
Organization 2010).
23346.indb 8323346.indb 83 22/08/2011 15:1222/08/2011 15:12

Standardized Mortality/Morbidity Ratio =
Observed cases in population of interest
Expected cases in population of interest
Using the example above,suppose that we did not have the age-specific mortality rates
for Switzerland, but we had this for South Africa.Assuming that the male population
age-structure for Switzerland in 2005 (from Figure 6.3) was still valid in 2007, and we
knew that there were 8,596 deaths from cancer among men in Switzerland in 2007.We
could calculate the expected deaths for each age group by multiplying the population
in each age group in Switzerland with the age-specific incidence rate for South Africa
(see Table 6.2).
Table 6.2 Indirect age standardization of Swiss and South African (SA) 2007 male cancer mortality
Age group (years) SA 2007 mortality rate
(per 100,000)
Switzerland 2005
population (1,000s)
Expected deaths in
Switzerland 2007
0–4 2.70 187 5
5–9 1.80 205 4
10–14 1.80 225 4
15–19 3.40 223 8
20–24 5.50 226 12
25–29 9.10 228 21
30–34 20.10 261 52
35–39 32.70 303 99
40–44 53.50 317 170
45–49 102.70 283 291
50–54 167.70 247 414
55–59 279.00 239 667
60–64 370.10 204 755
65–69 596.60 154 919
70–74 860.50 128 1,101
75–79 1,321.30 97 1,282
80–84 2,115.30 66 1,396
85+ 4,330.70 46 1,992
Total 3,639 9,191
Source: Ilona Carneiro, using data from Ahmad et al. (2001) and WHO cancer mortality database (World Health
Organization 2010).
If Switzerland had the same age-specific mortality rates as South Africa 2007, we
would expect 9,191 cancer deaths among men in 2007.The SMR can then be calcu-
lated as 8,596 ÷ 9,191 = 0.94, i.e. nearly one, indicating little difference in male cancer
mortality between Switzerland and South Africa in 2007.
SMRs should only be compared with the standard population, unless the underlying
population structures are shown to be comparable. As the indirect standardization
23346.indb 8423346.indb 84 22/08/2011 15:1222/08/2011 15:12

method does not use a common standard age-structure, if SMRs are calculated for
several populations with very different age-structures,they must not be compared with
each other.This is because any differences may be due to the population structures
rather than differences in age-speciﬁc rates (i.e. confounding by age).
Interpretation
The results of ecological studies need to be interpreted with caution for the following
reasons:
1 Ecological fallacy:This is the mismatch that arises from trying to draw conclusions
about individual-level epidemiological associations from a group-level study. For
example, an ecological analysis of anaemia prevalence and malaria prevalence in
children for several districts of country X may reveal that the two are closely
related. However, we cannot determine from these data that this relationship exists
at an individual level and that children with malaria are the same as those that have
anaemia; they may be completely different. Note that the same mismatch can occur
when trying to draw conclusions about group-level effects from individual-level data.
Therefore, it is not possible to make any causal inference from an ecological study.
2 Bias: Data may be collected in different ways for different groups, and diagnostic
criteria and technologies can change over time, leading to differential misclassiﬁca-
tion (see Chapter 4).
3 Mixing: Geographical comparisons may suffer from migration of populations
between groups over the period of the study, which may dilute differences between
groups.
4 Confounding: Data are often collected for purposes other than epidemiological
research and at a group level data on potential confounding factors are often
missing.
Activity 6.1
Table 6.3 shows HIV-related deaths and mid-year population by age group.The mid-
year population of countryY in 2010 was estimated at 198,812,000.
Table 6.3 HIV-related deaths and estimated population by age group in countryY, 2010
Age group (years) HIV-related deaths Mid-year population
0–4 110 11,217,000
5–14 30 28,146,000
15–24 423 31,698,000
25–34 4,328 37,315,000
35–44 4,096 29,305,000
45–54 1,522 19,276,000
55+ 897 41,855,000
Total 11,406 198,812,000
23346.indb 8523346.indb 85 22/08/2011 15:1222/08/2011 15:12

1 Calculate the crude HIV-related mortality rate and the age-specific HIV-related
mortality rate for countryY in 2010.
2 Compare the HIV-related mortality rate for country Y with an estimated rate of
4 per 100,000 for country Z in 2010 using an appropriate crude (unstandardized)
measure of association and interpret your result.
3 Table 6.4 shows the age-specific HIV-related mortality rate for country Z in 2010.
Comparing this with the age-specific HIV-related mortality that you calculated for
countryY, what do you observe and what might explain this?
Table 6.4 Age-specific HIV-related mortality for country Z in 2010
Age group (years) Age-specific HIV-related mortality per 100,000
0–4 1.00
5–14 0.14
15–24 1.30
25–34 11.60
35–44 14.00
45–54 7.90
55+ 2.10
4 The mid-year population for country Z in 2010 was estimated as 240,000,000. Using
the information provided, name and calculate a standardized HIV-related mortality
measure to compare these two populations, and interpret your result.
Activity 6.2
Table 6.5 compares age-specific mortality in two populations.
Table 6.5 Age-specific mortality rates in City A and City B
City A City B
Age Deaths Population
(1,000s)
Mortality rate
(per 1,000)
Deaths Population
(1,000s)
Mortality rate
(per 1,000)
0–17 2,343 2,101 1.10 2,076 440 4.70
18–44 6,104 2,365 2.60 766 256 3.00
45–60 23,845 857 27.80 3,210 96 33.40
60+ 38,102 656 58.10 2,311 38 60.80
All 70,394 5,979 11.80 8,363 830 10.10
1 Describe the data in Table 6.5. Can you determine whether mortality rates are
higher in City A or City B?
23346.indb 8623346.indb 86 22/08/2011 15:1222/08/2011 15:12

2 Use indirect standardization to calculate the number of deaths you would have
expected to see in City B if it had the same age-speciﬁc mortality rates as City A.
3 Calculate and interpret the standardized mortality ratio (SMR) for CityA compared
with City B.
Activity 6.3
An ecological study was conducted to investigate the effect of air pollutants on preg-
nancy outcomes estimated from routinely collected data (Bobak and Leon 1999).
Figure 6.5 shows data on the annual prevalence of low birthweight (<2500g) and
Figure 6.5 (a) Annual geometric mean sulphur dioxide concentrations in 1987 (no data available for
unshaded areas).(b) Prevalence of low birthweight (<2500g) in districts for which data were available in (a)
Source: Bobak and Leon (1999).
(a)
(b)
23346.indb 8723346.indb 87 22/08/2011 15:1222/08/2011 15:12

geometric mean concentration of sulphur dioxide plotted for the 85 administrative
districts of the Czech Republic.
1 Looking at Figure 6.5, was there an association between sulphur dioxide concentra-
tion and prevalence of low birthweight for the 39 shaded districts?
A logistic regression model was used to estimate associations, adjusting for socio-
economic factors at the district level.An odds ratio for low birthweight of 1.10 (95%
CI: 1.02, 1.17) and an odds ratio for stillbirths of 0.98 (95% CI: 0.80, 1.20) was
estimated for each 50 μg/m2
increase in sulphur dioxide pollution.
2 Interpret these results in relation to whether there is an epidemiological association
between the exposure and each outcome.
Activity 6.4
Data from a 1976 aerial survey were used to determine the measure of outdoor
gamma radiation at the mid-point of each of 69 census areas within a ten-mile radius
of a nuclear power station in the USA (Hatch and Susser 1990). Incident cases of can-
cer between 1 January 1975 and 31 December 1985 were identiﬁed from hospital
records within a 30-mile radius of the nuclear power station and referral hospitals in
nearby cities.The population at risk for each census area was estimated from census
data.The incidence rate of cancer in children aged 0–14 years was calculated for each
of the 69 census areas.
1 Identify the study hypothesis, exposure and outcome of interest.
The census areas were divided into quartiles (four groups with equal numbers,each
representing a quarter of the total sample) based on the level of outdoor gamma
radiation.Table 6.6 shows the incidence rate of childhood leukaemia and childhood
cancer for each quartile.
Table 6.6 Outdoor gamma radiation and cancer incidence among children from 69 census areas within
10 miles of a US nuclear plant
Incidence per
100,000
Gamma radiation at mid-point of census area
Quartile 1 Quartile 2 Quartile 3 Quartile 4
Childhood leukaemia 1.9 1.5 2.0 4.9
Childhood cancer 8.2 15.4 13.9 22.6
Source: Hatch and Susser (1990).
2 Identify and calculate an appropriate measure of relative risk for both childhood
leukaemia and all childhood cancers, comparing incidence in those with the highest
exposure to gamma radiation (Quartile 4) with incidence in those with the lowest
exposure (Quartile 1). Interpret your result.
3 From your calculation and the data presented, can you say that higher exposure
to outdoor gamma radiation causes an increased risk of childhood cancers? Give
reasons for your answer.
23346.indb 8823346.indb 88 22/08/2011 15:1222/08/2011 15:12

Conclusion
In this chapter you have reviewed key features, advantages and limitations of the eco-
logical study design.There are various sources of routinely collected data that may be
used in ecological studies, such as vital registrations, population censuses and outcome
registries. While this design is generally cost-effective, and is necessary for some
population-level risk factors, it is not possible to infer causality at an individual level
from the results of ecological studies.
References
Ahmad OB, Boschi-Pinto C, Lopez AD, et al. (2001) Age standardization of rates: a new WHO standard.
GPE Discussion Paper Series. Geneva:World Health Organization.
Bailey L, Vardulaki K, Langham J and Chandramohan D (2005) Introduction to Epidemiology. 1st edn.
Maidenhead: Open University Press.
Bobak M and Leon DA (1999) Pregnancy outcomes and outdoor air pollution: an ecological study in
districts of the Czech Republic 1986–8. Occupational and Environmental Medicine 56: 539–43.
Measure DHS (2011) Demographic and Health Surveys [Online]. Available: http://www.measuredhs.com/
start.cfm (accessed 02/05/2011).
Hatch M and Susser M (1990) Background gamma radiation and childhood cancers within ten miles of a US
nuclear plant. International Journal of Epidemiology 19: 546–52.
Kirkwood BR and Sterne JAC (2003) Essential Medical Statistics. Oxford: Blackwell Science.
United Nations World Population Prospects, the 2008 revision [Online]. Available: http://www.un.org/esa/
population/unpop.htm (accessed 01/05/2011).
World Health Organization (2005) World Health Report 2005: Make Every Mother and Child Count. Geneva:
World Health Organization.
World Health Organization (2008) TheWorld Health Report 2008:Primary Health Care – Now MoreThan Ever.
Geneva:World Health Organization.
World Health Organization (2010) Cancer Mortality Database [Online]. Available: http://www-dep.iarc.fr/
WHOdb/WHOdb.htm (accessed 01/05/2011).
World Health Organization (2011) Global Health Observatory (GHO) [Online]. Available: http://www.who.
/gho/en/ (accessed 02/05/2001).
Activity 6.1
1 Mortality rate is simply the incidence rate for deaths,and is calculated as the number
of deaths divided by the mid-year population for the time at risk (i.e. the year 2010).
For example, for the whole population the number of HIV-related deaths was
11,406 and the mid-year population was 198,812,000. Therefore the crude HIV-
related mortality rate was 11,406 ÷ 198,812,000 = 0.000057 or 5.74 per 100,000.
The results for age-speciﬁc mortality rates are shown in the last column ofTable 6.7.
2 The appropriate crude measure of association is the incidence rate ratio (IRR)
calculated as the incidence in the exposed divided by the incidence in the unexposed
(see Chapter 3).
For HIV-related mortality the IRR for country Y compared with country Z is
5.74 ÷ 4 = 1.44.This might suggest that the all-cause mortality rate in country Y is
23346.indb 8923346.indb 89 22/08/2011 15:1222/08/2011 15:12

approximately 44% higher than that in country Z. However, there is no information
on how these measures were obtained and therefore we cannot account for the
role of chance (no 95% Confidence Intervals are given), bias or confounding.
3 The age-specific HIV-related mortality rates appear to be almost identical in both
populations.Given that the crude population rates were different,this would suggest
that the population age-structures are different, probably mostly in those age groups
at highest risk of HIV.
4 As the age-specific rates are similar, it means that if direct standardization methods
were used, the age-standardized rate of HIV-specific mortality would be similar in
the two countries. If indirect methods were used, the SMR would equal 1. (You can
check this by using theWorld standard population structure inTable 6.1 or by apply-
ing the age-specific rates of country Z to the age-specific population for countryY.)
Activity 6.2
1 Age-specific mortality increases with age in both populations. The crude (whole
population) mortality rate is slightly higher in City A than in City B. However, if we
look at the age-specific mortality rates, we see that they are higher in all age groups
in City B compared with City A.
The higher crude mortality is likely to be due to the population age-structure
being older in City A than in City B (10.97% versus 4.58% aged 60+) as the elderly
are generally at greater risk of dying. Therefore age acts as a confounder since it
is independently associated both with the exposure (living in City A or B) and the
outcome (mortality).
2 You should have constructed a table to calculate the number of expected deaths in
city B if it had the same age-specific mortality rates as the ‘standard’ population of
City A.Your table should look likeTable 6.8 and the total number of expected deaths
in City B would be 6,027.
3 Using the expected deaths from Table 6.8, you can calculate the SMR as:
SMR =
Observed deaths
=
8,363
= 1.39
Expected deaths 6,027
Table 6.7 HIV-related deaths and estimated population by age group in countryY, 2010
Age group (years) HIV-related deaths Mid-year population Age-specific HIV-related mortality
rate per 100,000
0–4 110 11,217,000 0.98
5–14 30 28,146,000 0.11
15–24 423 31,698,000 1.33
25–34 4,328 37,315,000 11.60
35–44 4,096 29,305,000 13.98
45–54 1,522 19,276,000 7.90
55+ 897 41,855,000 2.14
Total 11,406 198,812,000 5.74
23346.indb 9023346.indb 90 22/08/2011 15:1222/08/2011 15:12

An SMR of 1.39 tells us that people living in City B are 1.39 times (or 39%) more likely
to die than people living in City A.
Activity 6.3
1 The presentation of a map for each variable is descriptive rather than analytical, but
we can see that both sulphur dioxide pollution and the prevalence of low birth-
weight were higher in the north-western and south-eastern districts, although the
overlap is not perfect.This suggests that a relationship might exist, but requires an
epidemiological analysis of the data.
2 The odds ratio for low birthweight is 1.10, indicating a 10% increase in the annual
prevalence of low birthweight for every 50 μg/m2
increase in population exposure to
sulphur dioxide pollution.The 95% confidence interval was 1.02–1.17, meaning we
can be 95% certain that the true estimate of the odds ratio lies within this range.The
95% confidence interval does not include 1.00, meaning that the P-value will be less
than 5 (i.e. less than 5% chance that this association is not true). However, this does
not mean that individual exposure to sulphur dioxide will increase the risk of low
birthweight in a pregnant mother.
The odds ratio for stillbirths is 0.98,and the 95% confidence interval includes 1.00,
meaning there is no evidence that population exposure to sulphur dioxide pollution
affects the risk of stillbirths.
Activity 6.4
1 This is an ecological study as exposure (outdoor gamma radiation) and outcome
(incidence rate of childhood cancer) are measured and calculated at the level of the
census area.The hypothesis being tested was, therefore, that populations (not indi-
viduals) exposed to higher levels of outdoor gamma radiation in 1976 would have a
higher incidence of childhood cancer between 1975–1985.
2 The appropriate measure of relative risk is the incidence rate ratio (see Chapter 3).
Using Quartile 4 as the exposed group and Quartile 1 as the unexposed group,
we calculate the incidence rate ratio (IRR) for childhood leukaemia as:
IRR for childhood leukaemia =
4.9
= 2.58
1.9
and the incidence rate ratio for childhood cancer as:
Table 6.8 Expected mortality for City B using rates from City A
City A City B
Age Mortality rate (per 1,000) Population (1,000s) Deaths expected
0–17 1.10 440 (440,000 × 1.1)/1,000 = 484
18–44 2.60 256 (256,000 × 2.6)/1,000 = 666
45–60 27.80 96 (96,000 × 27.8)/1,000 = 2,669
60 58.10 38 (38,000 × 58.1)/1,000 = 2,208
All 11.80 830 6,027
Source: Natasha Howard.
23346.indb 9123346.indb 91 22/08/2011 15:1222/08/2011 15:12

IRR for childhood cancer =
22.6
= 2.76
8.2
An incidence rate ratio of 2.58 for childhood leukaemia and an incidence rate ratio
of 2.76 for all childhood cancers indicates these are more than twice as high among
populations exposed to the highest quartile of outdoor gamma radiation, as among
populations exposed to the lowest quartile of outdoor gamma radiation, between
1975–1985 in this study population.
3 We can say that the study results show that populations exposed to higher levels of
outdoor gamma radiation have higher incidences of childhood cancer.
However, we cannot conclude that outdoor gamma radiation is a causal factor for
the increased risk of childhood cancer for several reasons:
(a) This is an ecological study,and we do not know that the incident cancer cases were
themselves exposed to higher levels of radiation (refer to ecological fallacy).
(b) We have not calculated any statistical measures (e.g. 95% conﬁdence intervals or
P-values) to exclude the role of chance.
(c) We have not adjusted for information bias: outdoor gamma radiation may not be a
good measure of actual exposure given that many children will spend much of their
time indoors.
(d) We have not adjusted for potential confounders (e.g. age, gender, population
density).
(e) There is no clear dose–response relationship. However, categorizing the gamma
radiation by quartile is likely to make this more difﬁcult to detect. In reality, the
lower three quartiles had smaller ranges of exposure than the fourth quartile,
which may partially explain some of the similarities in risk between the lower
quartiles.
23346.indb 9223346.indb 92 22/08/2011 15:1222/08/2011 15:12

7Cross-sectional studies
Overview
Cross-sectional studies measure the frequency of outcomes and/or exposures at one
point in time.The cross-sectional design can investigate large numbers of study subjects
relatively rapidly. However, because the outcome and exposure are measured simulta-
neously, it is often difficult to know whether the exposure preceded the outcome,
making it difficult to infer causality.This chapter reviews the characteristics, advantages
and limitations of the cross-sectional study design for analytical epidemiology.
Learning objectives
• describe the basic uses, strengths and limitations of cross-sectional studies
• discuss potential sources of bias in cross-sectional studies
• recognize the basic analytical approaches used in cross-sectional studies.
What defines a cross-sectional study?
In a cross-sectional study, data on outcomes and/or exposures are collected on each
study participant at one point in time. Cross-sectional studies have the main advantage
of being relatively quick and easy to perform.They are better for measuring the fre-
quency of chronic outcomes as they include prevalent rather than incident cases.Those
with acute outcomes may die or resolve their symptoms before detection by cross-
sectional survey.
Cross-sectional surveys provide a snapshot of a population’s current health status,
which can be used in the planning of health services or the determination of health
practices. Repeated studies can be used to determine changes in exposure and out-
come frequency over time.They therefore form a core part of routine monitoring (see
Chapter 12).
Study design
The cross-sectional survey design is often used in descriptive epidemiological studies to
estimate the frequency of outcomes or exposures without the intention of investigating
causal associations.They may be referred to as‘prevalence surveys’,as they collect data
on existing (prevalent) cases of an outcome, and may be used to provide baseline
descriptive data for other types of analytical studies.
23346.indb 9323346.indb 93 22/08/2011 15:1222/08/2011 15:12

An analytical cross-sectional study collects data on both outcome and exposure at the
same time-point for a given study subject. Cross-sectional studies can be used to test
hypotheses of association where the exposure status does not change over time (e.g.
blood group antigens).However,it is often not possible to know whether the exposure
preceded the outcome,and some outcomes have long latent periods,making it difficult
to infer causality. For example, the time between exposure to HIV and onset of AIDS
can be more than 10 years.Therefore, a cross-sectional study would not have been
appropriate to investigate an association between HIV infection and AIDS prevalence
in the early days of the AIDS epidemic. For this reason, cross-sectional studies are
generally used for generating research hypotheses and for health service planning and
monitoring, rather than for establishing causal links.
Sampling
A representative sample of the population must be selected using the methods of
random selection and sample size calculation discussed in Chapter 5. In a cross-
sectional study, there is no loss to follow-up, though there may be some non-response.
Interviewers may include errors when filling-in questionnaires, although these can be
considerably reduced by appropriate questionnaire design and training. Respondents
may refuse to answer particular questions, for example, on income-level or sexual
behaviours. Even clinical measures may suffer losses, for example, when taking finger-
prick samples from infants to measure haemoglobin, some infants may not release
sufficient blood.Many of these issues can be highlighted with a pilot-study,pre-testing
data collection and data entry methods. However, if there is still potential for non-
reponse in either the outcome or exposure of interest, the sample size should be
increased to allow for this.A larger sample size will increase the statistical power and
precision of the estimated frequency or association, though this may also increase the
time and cost of the study.
Data collection
Cross-sectional studies may collect information using a combination of questionnaires
and diagnostic tests.They allow for collection of data on many variables, and are ideal
for collecting data on potential confounders for use at the analytical stage. Although
data in a cross-sectional study are collected at one time-point, the measures collected
may be current (e.g. blood pressure, current symptoms) or past (e.g. vaccination his-
tory, previous smoking practices).
To measure prevalence, it is important that survey questions are sufficiently specific.
Asking ‘Did your child have fever in the last 24 hours?’ will provide an estimate of the
point prevalence of (current) fever.Asking ‘Has your child had fever during the last two
weeks?’ will record fever episodes that started prior to two weeks and continued into
it,as well as episodes that started during the two-week period of interest.Surveys that
relate to the prevalence of an outcome during a period of time in the past will estimate
period prevalence.While period prevalence may increase case detection and there-
fore reduce the necessary sample size, questions about past experience may also
increase the possibility of recall bias.
Measurement of current exposure in a cross-sectional survey is appropriate when
the exposure is constant (e.g. genetic markers), and will be unaffected by the outcome
or potential confounders.However,some exposures may change over time,particularly
23346.indb 9423346.indb 94 22/08/2011 15:1222/08/2011 15:12

Cross-sectional studies 95
in response to the outcome. For example, people with colon cancer may adapt the
foods they eat to reduce discomfort, so current diet would not be a reasonable proxy
for previous diet as a risk factor. Self-reported history may suffer from recall bias.
Therefore, measures of past exposure from routine data (e.g. health records), or more
memorable exposures (e.g.occupation,previous smoking habits),are more appropriate.
Questions need to be appropriately designed and tested to improve response rates.
A question that is unclear, or that the respondent may be embarrassed to answer, can
result in non-responder bias (a form of information bias). Choosing appropriate meth-
ods for the topic of investigation (interview vs. self-completed questionnaire), ensuring
anonymity, and careful wording and pre-testing of questions should reduce such error.
Analysis
In an analytical cross-sectional study, the appropriate measure of association is the
prevalence ratio.This is the ratio of the prevalence of the outcome in those exposed
divided by the prevalence in those unexposed. However, when the outcome is rare (i.e.
the prevalence is low),the prevalence ratio is approximately the same as the odds ratio
(see Chapter 3 – Comparability of measures of association on p. 31). This is useful,
because it means that we can use logistic regression models to analyse cross-sectional
studies,adjusting for several potential confounders,and report results using odds ratios.
Interpretation
The results of analytical cross-sectional studies need to be interpreted with caution,
because both outcome and exposure are measured simultaneously and it may not be
possible to know which preceded the other. In the example of colon cancer and diet,
investigating current diet as a risk factor would lead to reverse causality, where the
exposure is actually a consequence of the outcome.
Activity 7.1
Many intervention studies have shown that mosquito nets treated with insecticide can
reduce illness and mortality from malaria in young children in Africa. Investigators car-
ried out a cross-sectional study of randomly selected children under two years of age
in 18 villages in Tanzania at the beginning of a marketing campaign to promote the use
of insecticide-treated nets (ITNs) (Abdulla et al. 2001). They collected data on net
ownership and other factors by interviewing the mothers of young children using a
questionnaire.They took blood samples from the children to test whether they were
infected with malaria parasites and if they were anaemic (haemoglobin < 8g/dl) as a
result. Two further cross-sectional surveys, each with a different random sample of
children, were conducted over the next 2 years.Table 7.1 combines selected results
from the three surveys combined.
1 What type of cross-sectional study is this?
2 Describe the results of the study shown inTable 7.1 and determine whether you can
calculate the effect of net ownership on the proportion of children with malaria
parasites from this table.
23346.indb 9523346.indb 95 22/08/2011 15:1222/08/2011 15:12

Table 7.2 shows numbers of children with anaemia and malaria parasites according to
net ownership for all three surveys combined.
Table 7.1 Numbers (%) of children from three cross-sectional surveys, 1997–1999
Year of survey
1997 1998 1999
Number of children eligible 325 330 330
Number of children analysed 240 269 239
Reported net ownership (%)
no net 100 (42) 49 (18) 40 (17)
untreated net 116 (48) 64 (24) 53 (22)
ITN 24 (10) 156 (58) 146 (61)
Number (%) of children
with anaemia (haemoglobin <8 g/dl) 118 (49) 83 (31) 62 (26)
with malaria parasites 151 (63) 126 (47) 90 (38)
Source: Abdullah et al. (2001).
Table 7.2 Effect of net ownership on the prevalence of anaemia and malaria parasites
Number (%) of children
with anaemia with malaria parasites Total
Net ownership
no net 103 (54%) 132 (70%) 189
untreated net 90 (39%) 115 (49%) 233
ITN 70 (21%) 120 (37%) 326
Total 263 367
Source: Abdullah et al. (2001).
3 What is the prevalence ratio for anaemia of the effect of owning an ITN compared
with no net?
4 What is the prevalence ratio for malaria parasites of the effect of not owning a net,
whether ITN or untreated? Hint: Construct a 2×2 table of each outcome and expo-
sure variable, and convert the exposure into two categories (i.e. net versus no net;
ITN versus no ITN), as indicated for each question.
Activity 7.2
A survey of adolescents aged 12–16 years was undertaken in Goa, India, using a devel-
opment and well-being assessment to diagnose the presence of mental disorders (Pillai
23346.indb 9623346.indb 96 22/08/2011 15:1222/08/2011 15:12

et al. 2008). Structured interviews were also conducted to assess risk factors, including
family relations in the previous 12 months. Eligible individuals were identiﬁed through
health centre family registers and a door-to-door survey. Of 2,648 eligible adolescents,
358 were absent from home on three visits by the researcher,85 had migrated,187 did
not consent to participate and 6 did not complete the assessment. Of the 2,048 ana-
lysed, 37 were diagnosed as having a mental disorder. Selected results of multiple logis-
tic regression analyses are shown in Table 7.3.
Table 7.3 Selected factors associated with the presence of a mental disorder in adolescents (n= 2048)
Risk factor Odds ratio (95% CI) P-value
Physical/verbal abuse from parents: 0.02
Never/rarely 1.00
Occasionally 1.50 (0.6, 3.7)
Often 2.90 (1.3, 6.8)
Perceived family support: 0.01
Rarely 1.00
Sometimes 0.18 (0.1, 0.7)
Often 0.15 (0.04, 0.5)
Always 0.16 (0.1, 0.5)
Source: Pillai (2008).
1 What are the two hypotheses being tested inTable 7.3? (Note,the reference or unex-
posed group is that with an odds ratio of 1.00.)
2 Interpret the results in Table 7.3, with reference to the trends in odds ratios, 95%
conﬁdence intervals and P-values.
3 What potential sources of bias can you identify from the information given, and how
might these affect interpretation of the results?
Conclusion
In this chapter you have reviewed the key features, advantages and disadvantages of
cross-sectional studies.This study design is a relatively cheap and cost-effective way to
collect descriptive epidemiological data. In analytical epidemiology, cross-sectional
studies may suffer from bias, confounding, and issues of reverse causality if the expo-
sure is not constant.This is therefore not the design of choice for inferring causality.
References
Abdulla S, Schellenberg JA, Nathan R, et al. (2001) Impact on malaria morbidity of a programme supplying
insecticide treated nets in children aged under 2 years inTanzania: community cross-sectional study.
Pillai A, Patel V, Cardozo P, et al. (2008) Non-traditional lifestyles and prevalence of mental disorders in
adolescents in Goa, India. British Journal of Psychiatry 192: 45–51.
23346.indb 9723346.indb 97 22/08/2011 15:1222/08/2011 15:12

Activity 7.1
1 This is an analytical cross-sectional study, because the investigators are interested in
the effect that the preventive measure of using insecticide-treated nets (ITNs) will
have on the prevalence of malaria in children.
2 The results inTable 7.1 suggest that ownership of ITNs increases over the period of
the study, while the number of households with no nets or untreated nets, and the
proportion of children with anaemia or malaria parasites, decreases over the course
of the study. However, from Table 7.1 it is not possible to calculate the effect of net
ownership on the proportion of children with malaria, because we have not been
given the numbers of children with either anaemia or malaria parasites in each of the
net ownership categories.
3 To calculate the prevalence ratio for anaemia of the effect of ITNs compared with no
net ownership, your 2×2 table should look likeTable 7.4, with appropriate labelling.
Table 7.4 ITN ownership among children with and without anaemia
Number of children
Anaemia No anaemia Total
ITN 70 256 326
No net 103 86 189
Total 173 342 515
To compare the prevalence of anaemia in the two exposure groups:
Prevalence of anaemia in those with ITNs = 70 ÷ 326 = 0.215 or 21.5%.
Prevalence of anaemia in those without nets = 103 ÷ 189 = 0.545 or 54.5%.
Therefore the prevalence ratio is 0.215 ÷ 0.545 = 0.394 or 39.4%.
A prevalence ratio of 0.39 indicates that children in households with ITNs have 39%
the risk of anaemia as those in households without nets.This is the same as saying
that children with ITNs have 61% (1 – 0.394 = 0.606) lower prevalence of anaemia
than those without nets.
4 To calculate the prevalence ratio for malaria parasites of the effect of no net owner-
ship compared with any net ownership, your 2×2 table should look like Table 7.5.
Table 7.5 Net ownership among children with and without malaria parasites
Number of children
with parasites without parasites Total
No net 132 57 189
Net 235 324 559
Total 367 381 748
23346.indb 9823346.indb 98 22/08/2011 15:1222/08/2011 15:12

To compare the prevalence of malaria parasites in the two exposure groups:
Prevalence of parasites in those without nets = 132 ÷ 189 = 0.698 or 69.8%.
Prevalence of parasites in those with nets = 235 ÷ 559 = 0.420 or 42.0%.
Therefore the prevalence ratio is 0.698 ÷ 0.420 = 1.66, indicating that children in
households without nets have a 66% higher prevalence of parasites than those with
nets.
Activity 7.2
1 Hypothesis 1:‘The prevalence of mental disorder in adolescents in this population
increases with more frequent physical or verbal abuse from parents.’ OR ‘Prevalence
is greater among adolescents exposed to occasional or frequent physical/verbal abuse
from parents than those exposed to no or rare physical/verbal abuse from parents.’
Hypothesis 2:‘The prevalence of mental disorder in adolescents in this population
decreases with more frequent family support.’ OR ‘Prevalence is lower in adolescents
who receive support from their family (sometimes/often/always) than in those rarely
supported by their family.’
2 In Table 7.3, the odds ratio of mental disorders appears to increase with increasing
frequency of physical/verbal abuse from parents.The overall P-value of 0.02, means
that there is less than a 2% chance that this association would be observed if it did
not truly exist. The 95% confidence interval for occasional abuse from parents is
0.6 – 3.7 which includes the value 1.00, therefore individuals in this category are not
at a significantly increased risk of mental disorder than those in the never/rarely
category. However, the 95% confidence interval for the ‘often’ category is 1.3 – 6.8,
which does not include 1.00, indicating that adolescents ‘often’ exposed to abuse
from parents have almost three times (odds ratio = 2.90), greater odds of mental
disorder than those ‘never/rarely’ exposed to abuse from parents.
The odds ratio of mental disorders is much lower in adolescents who reported
family support ‘sometimes’, ‘often’ or ‘always’, compared to those who reported
family support ‘rarely’. The overall P-value of 0.01 means there is less than a 1%
chance that this association would be observed if it did not truly exist. However,
there does not appear to be much of a trend as all categories had similar odds ratios
(0.18, 0.15, 0.16), and their 95% confidence intervals overlapped with each other.
This suggests that the measure of level of family support did not discriminate well
between the different categories.All three categories of adolescents who reported
some family support had 95% confidence intervals that did not include 1.0,indicating
that they were all significantly different from those who reported ‘rarely’ receiving
family support.In summary,adolescents reporting some family support had between
82–85% lower odds of suffering from a mental disorder.
3 There is likely to be selection bias.The 358 absent adolescents, 187 who refused to
consent, and 6 who did not complete assessment, may have been different from the
individuals analysed in relation to outcome or exposures.As this totals 20% of those
eligible,such potential bias in the estimate of effect makes it difficult to generalize the
results to the target population.
There is likely to be information bias, as exposures were all self-reported.The investi-
gators developed structured interviews that had previously been tested elsewhere,and
also interviewed a sibling for 36% of participants.Given the high levels of stigma associ-
ated with the topic, there may have been under-reporting of abuse by parents, which
may be non-differential and lead to an underestimate of the strength of the association.
There may also be reverse causality, if individuals with mental disorders have
different perceptions of their interactions and are, for example, more prone to
perceiving abuse by parents or lack of family support.
23346.indb 9923346.indb 99 22/08/2011 15:1222/08/2011 15:12

Overview
Cohort studies measure the exposures of interest and then follow up study partici-
pants over time to measure the incidence of the outcome of interest. Cohort studies
are a type of natural experiment because defined groups are followed, as they would
be in an intervention trial, although the investigator’s job is purely to observe and not
to intervene.This is one of the best analytical designs as the definition of exposure
prior to outcome may reduce problems of selection and participant bias. In this
chapter you will review the characteristics, advantages and limitations of the cohort
study design for analytical epidemiology.
Learning objectives
• describe the uses, strengths and limitations of cohort studies
• discuss the potential sources of bias in cohort studies
• recognize the basic analytical approaches commonly used.
What defines a cohort study?
Epidemiologists use the term cohort to describe a group of individuals who share a
common characteristic, and are followed up to measure the incidence of an outcome.
A cohort may be a group of workers from a factory,a group of children who were born
in the same year, or a group of individuals at risk of a particular outcome. The
exposures of interest are recorded at the start of the study,and may be updated during
the study. Cohort studies are therefore more likely than other observational study
designs to meet the temporality criterion for causality (see Chapter 4).
Cohort studies are most often used when the outcome of interest is common, as a
rare outcome would require too large a sample size.They may also be used to study
relatively rare exposures by careful selection of participants on the basis of their exposure.
The incidence of an outcome in an exposed cohort is compared with that in an
unexposed cohort to see whether the exposure results in any observable difference.
Cohort studies enable us to study a wide range of outcomes that may be associated
with a single exposure of interest. Even an outcome that was not anticipated at the
start of the study may be included in data collection during the course of the study.
This is especially useful when dealing with the introduction of new exposures whose
health risks are undefined (e.g. mobile phone use, wireless technologies).
The main disadvantages of cohort studies are: (a) the large number of participants
required; (b) the cost of data collection for active follow-up (e.g. health evaluations,
Cohort studies
8
23346.indb 10023346.indb 100 22/08/2011 15:1222/08/2011 15:12

Cohort studies 101
quality-of-life questionnaires) versus passive follow-up (e.g. death or cancer notifica-
tions); and (c) the length of the study, as some prospective cohort studies may take
decades to complete.
Study design
The cohort design can be used in descriptive studies to provide baseline data, and for
routine monitoring (see Chapter 12). The observational nature of the design may
sometimes raise ethical conflicts when dealing with severe and potentially fatal out-
comes, as any interference by the investigator can have an impact on the outcomes
being measured.
Analytical cohort studies (also known as incidence studies, longitudinal studies, or follow-
up studies) can be prospective or retrospective. However, both types define the cohort
on the basis of exposure and not outcome status. It can be helpful to present the flow
of numbers of study participants when describing a cohort study (see Figure 8.1).
Figure 8.1 Flow-chart of numbers of participants recruited, numbers categorized as exposed or unex-
posed, numbers lost-to-follow-up in each category, and numbers with and without the outcome in each
exposure category at the end of the study
Prospective cohorts identify participants and then follow them over time until
they either acquire the outcome of interest or the time limit for the study has been
reached.The main feature of prospective cohort studies is that data on exposures are
collected before data on the outcome. Study participants must be free of the outcome
of interest at the start of the study. For example, if the outcome is having cancer, it is
important to ensure that all participants are cancer-free at the start of the study.
Prospective cohorts have a major advantage over other study types in determining
23346.indb 10123346.indb 101 22/08/2011 15:1222/08/2011 15:12

whether an exposure might be causally associated with the outcome, since we can be
fairly sure in which order the exposure and outcome occurred and outcome status
cannot affect the classiﬁcation of exposure status.
Retrospective cohorts use pre-existing data on exposures and outcomes – for
example, from medical or occupational records – and therefore do not need to follow
individuals over time since all the information is already available. These are usually
quicker and cheaper to carry out than prospective studies, particularly for diseases or
events that may take decades to develop (e.g. cancer). However, routine data may be
poorly collected (e.g. inaccurate, missing data), may not provide necessary information
on other important risk factors or confounders, and may be liable to changes in deﬁni-
tions and coding systems over time.
A cohort study may combine both retrospective and prospective data. For example,
a study may identify a cohort of children aged 2 years old and follow them for a year
to measure the incidence of vaccine preventable diseases, while using vaccination
records that pre-date the start of the study to provide information on prior exposures.
Sampling
Selection of the study population usually depends on whether the exposure of interest
is common or rare. If the exposure is common, we can select the study population
before classifying each individual as exposed or unexposed, for example, a random
sample of the general population.Information on exposure can then be collected as the
individuals are followed up, and the original selection of the cohort purely depends on
the group being disease-free at the start of the study.
Alternatively, the study population could be selected from a particular occupation
group (e.g. nurses, government workers, or mine workers) or by place of work (e.g.
factory, other large institution).This is known as a workforce or occupational cohort and
has the advantage of higher participation and higher level of follow-up than general
population cohorts. It usually does not matter that the workforce cohort is not
representative of the general population,as long as the exposed and unexposed groups
are comparable within the cohort.
If the exposure is rare, the study sample can be selected on the basis of exposure to
make sure that enough exposed people are included to make the study viable. For
example, if the exposure of interest is contact with industrial chemicals, then workers
at a particular factory, known to handle chemicals as part of their job, can be chosen as
the exposure group.The comparison group would then be selected from workers at
the same factory who did not work with those chemicals.This is known as an internal
comparison group. However, if all workers at the factory had some degree of exposure,
we would need to select a comparison group from another population,possibly another
type of factory, to ensure that the comparison group only differed in terms of their
exposure and not in terms of other factors.This would be an external comparison group,
and would be chosen from another workforce to avoid the healthy worker effect (a form
of selection bias that tends to underestimate excess risk associated with an occupation
by comparing with the general population, which includes people too sick to work).
The sample size is related to the amount of time that participants are followed up.For
example,if the sample size for a study is calculated as 1,000 person years at risk,the study
could follow-up 1,000 people for one year, or 500 people for two years, or 250 people
for four years. However, a longer follow-up time implies a greater likelihood of loss of
contact with participants.This‘loss to follow-up’ needs to be accounted for by increasing
23346.indb 10223346.indb 102 22/08/2011 15:1222/08/2011 15:12

Cohort studies 103
the initial sample size to cover expected losses. For example, if we expect we may lose
contact with 10% of participants over the course of a two-year study, the number of
participants recruited to the study should be 10% greater than the calculated sample size.
Data collection
For a retrospective study, data are usually collected from routine sources, such as
patient hospital records, workplace personnel records or death notifications. For a
prospective cohort study, data on exposures can be collected similarly to a cross-
sectional study. This includes interviewing participants, consulting medical records,
taking biological samples, or using other forms of routine data. Exposures that are not
going to change during the study, such as date of birth, sex, birthweight, adult height,
blood type and genetic factors, are collected when participants enter the study.
Exposures that may change, such as blood pressure, physical activity, smoking, or dis-
ease status, are collected by re-assessing individuals in the cohort at predefined time-
points during the study, or sometimes from medical records as and when they occur. If
data on the exposure are detailed,there may be an opportunity to study dose–response
relationships between exposure and outcome. Detailed information on confounding
factors can also be collected, allowing investigators to control for them in the analysis.
Outcomes may be collected through periodic health examinations or health outcome
questionnaires to members of the cohort.
The length of follow-up needed for a sufficient proportion of the participants to have
acquired an outcome may be many years (even decades for more rare outcomes).This
can make cohort studies expensive and time-consuming to conduct, although occupa-
tional cohorts are easier and cheaper to follow up where record-keeping systems on
employees already exist.
Analysis
If the cohort study is descriptive, we can measure the frequency of outcome as a risk
or a rate. If the follow-up times for all participants are similar, then we can use the risk.
If the follow-up times differ between participants, and person-time at risk is known,
then a rate would be more appropriate.
In an analytical cohort study the appropriate measure of epidemiological association
is the risk ratio or rate ratio, depending on the frequency measure used. Measures of
impact such as attributable risk,attributable fraction,population attributable risk and popula-
tion attributable fraction can also be calculated (see Chapter 3).Using regression models
allows us to adjust for the effect of potential confounders (see Chapter 5).
If data are being compared between two cohorts that do not have the same demo-
graphic structure (e.g. age, sex), the result may be confounded by these other factors.
This may occur when comparing males and females,two cohorts selected from different
populations, or the study cohort with the general population. In these cases it is neces-
sary to standardize the incidence using a standard population structure (see Chapter 6).
Time-series analysis
As some exposures may vary over time, it is important that any changes in exposure
status are recorded and updated.A more complex statistical technique called time-series
23346.indb 10323346.indb 103 22/08/2011 15:1222/08/2011 15:12

analysis can be used to take account of changes in exposure, timing of outcome and for
more detailed changes in person-time at risk (e.g. temporary movement out of the
study area).Results of such analyses may be presented graphically as a survival curve or
a failure curve. Such graphs can be used for any outcome, where failure represents
acquisition of the outcome (e.g.incidence of cancer) and survival represents the lack of
outcome (e.g. those not rejecting an organ after a transplant operation).
Figure 8.2 shows a child survival curve from a cohort study in rural Bangladesh,
comparing those whose mother had died before the child’s tenth birthday to those
whose mother had not. The distance between the two lines provides a graphical
representation of the relative effect of maternal mortality and enables us to see how
the effect changes over time (in this case, by age of the child).
Figure 8.2 Kaplan-Meier survival curve from birth according to survival status of mother
Source: Ronsmans et al. (2010).
Interpretation
As with other analytical studies, any observed association between exposure and out-
come may be affected by chance, bias and confounding and consideration needs to be
given to how these may have affected the results.
Selection bias may occur if the selected cohort participants are not representative of
the target population. High rates of loss to follow-up or differences in the loss to follow-
up between exposure groups can also lead to selection bias. For example, if long-term
follow-up is conducted by a self-completed questionnaire, participants may be less
likely to respond due to death, disability, moving into a nursing home, etc. Similarly, if
cohorts have been selected according to their exposure status, it is important that the
exposed and unexposed cohorts are not different with respect to other factors that
have not been measured. For example, if an occupational cohort of asbestos removal
workers were compared with the general population,a ﬁnding of increased risk of lung
cancer would not provide useful information,as we could not eliminate the occupation.
However, by comparing within the cohort, we can investigate the risks associated
with type of respirator used and number of exposure hours, for example, to provide
recommendations for appropriate occupation regulations.
23346.indb 10423346.indb 104 22/08/2011 15:1222/08/2011 15:12

Cohort studies 105
Observer bias may occur if knowledge of exposure status affects classification of
outcome status,or in retrospective cohorts if knowledge of the outcome status affects
classification of exposure status. This may lead to systematic misclassification bias
(see Chapter 4).
Activity 8.1
In 1951, a prospective cohort study was initiated to investigate the relationship
between smoking and mortality among British doctors, particularly mortality due to
lung cancer (Doll and Peto 1976; Doll et al. 1980).This is an important study, which
ultimately followed up participants for 50 years (Doll et al. 2004).
In 1951,a questionnaire on smoking habits was sent to 49,913 male and 10,323 female
doctors registered with the British General Medical Council; 34,440 male doctors and
6,194 female doctors gave sufficient information to classify their smoking status.The vital
status of these doctors was followed up from the records of the Registrar General’s
Office, the British Medical Council and the British Medical Association.The causes of
death of 10,072 male and 1,094 female doctors who had died during the first 20 and 22
years of follow-up respectively were ascertained from death certificates. The rate of
death from lung cancer among smokers was compared to that among non-smokers.
1 Discuss the potential sources of bias in this study.
2 Identify what information on smoking you would collect to classify smoking
exposure status.
3 Age-adjusted lung cancer death rates per 100,000 persons per year among smokers
and non-smokers in male and female doctors are given inTable 8.1. Calculate appro-
priate epidemiological measures of association between smoking and lung cancer
and discuss the result, especially the differences between males and females.
Table 8.1 Lung cancer death rates per 100,000 person-years by gender and smoking status
Gender Lung cancer death rates per 100,000 persons per year
Non-smokers Smoking 1–14
cigarettes/day
Smoking 15–24
cigarettes/day
Smoking 25+
cigarettes/day
Male 10 78 127 251
Female 7 9 45 208
Source: Bailey et al. (2005), using data from Doll and Peto (1976) and Doll et al. (1980).
Activity 8.2
A study of the effect of HIV infection on the incidence of pulmonary tuberculosis (TB)
was undertaken in the year 2000. Investigators analysed data from personnel and
medical records between 1991–1997 on miners working at four gold mines in South
Africa (Sonnenberg et al. 2005). Using unique employee numbers, a confidential data-
base of HIV results from tests performed with consent was linked to data on the
incidence of first episode of pulmonary TB from annual chest-radiograph screening.
23346.indb 10523346.indb 105 22/08/2011 15:1222/08/2011 15:12

1 What type of study design is this? Be as speciﬁc as you can.
2 Calculate the missing values in Table 8.2 for:
(a) the incidence of pulmonary TB according to HIV infection status.
(b) the incidence rate ratio for pulmonary TB by age group.
3 The 95% conﬁdence interval (CI) for the rate ratio of pulmonary TB with HIV
infection is 3.12–4.19. How would you interpret this result?
4 The rate ratio of pulmonaryTB by HIV infection status after adjusting for the effect
of age and calendar period of the study was 2.90 (95% CI: 2.48–3.38). From this
information and the results inTable 8.2, do you think that age is a confounder in the
association between HIV and pulmonary TB?
Conclusion
In this chapter, you have reviewed the key features, advantages and disadvantages of
cohort studies.As exposure to a risk factor is usually determined before outcome in
cohort studies, this design enables us to assess temporality when inferring causality.
Biases can be minimized through appropriate study design and data on confounding
factors can be collected for adjustment during analysis,making this the most appropriate
observational study design for investigating epidemiological associations.
References
Doll R, Gray R, Hafner B and Peto R (1980) Mortality in relation to smoking: 22 years’ observations on
female British doctors. British Medical Journal 280: 967–71.
Doll R and Peto R (1976) Mortality in relation to smoking: 20 years’ observations on male British doctors.
Doll R,Peto R,Boreham J and Sutherland I (2004) Mortality in relation to smoking:50 years’ observations on
male British doctors. British Medical Journal 328: 1519.
Ronsmans C, Chowdhury ME, Dasgupta SK,Ahmed A and Koblinsky M (2010) Effect of parent’s death on
child survival in rural Bangladesh: a cohort study. Lancet 375: 2024–31.
Table 8.2 Incidence of pulmonary tuberculosis (TB) by HIV status and age
Category Person-years at
risk
PulmonaryTB
cases
Incidence per 100
person-years at risk
Rate
ratio
HIV negative miners 36,020 289 1.00
HIV positive miners 15,561 451 3.61
Age:
<30 years 15,483 103 0.67
30–39 years 24,645 387 1.57
40–49 years 8,670 176 2.03
≥ 50 years 2,783 74 2.66
Source: Sonnenberg et al. (2005).
23346.indb 10623346.indb 106 22/08/2011 15:1222/08/2011 15:12

Cohort studies 107
Sonnenberg P, Glynn JR, Fielding K, et al. (2005) How soon after infection with HIV does the risk of tuber-
culosis start to increase? A retrospective cohort study in South African gold miners. Journal of
Infectious Disease 191: 150–8.
Activity 8.1
1 This is effectively an occupational cohort.Therefore, actual estimates from the study
may not be directly extrapolated to the general population, because of the healthy
worker effect. Doctors are also likely to have had better access to good medical care
than the general population.
There may be some selection bias. First, only 69% (34,400/49,913) of eligible male
doctors and 60% (6,194/10,323) eligible female doctors gave sufficient information
to be included in the cohort.Those who did not respond, or gave incomplete infor-
mation may have been different from those who did respond in a way that may also
have affected their exposure or risk of outcome.
Second, it is unlikely that investigators were able to follow up all subjects for the
full period, due to migration or loss of records (i.e. loss to follow-up). However, in this
study, where the sample size is large and the routine reporting systems are robust,
this is unlikely to have greatly affected the result.
There may have been some information bias. First, if some doctors gave inaccurate
information regarding their smoking habits, this could have resulted in misclassifica-
tion of exposure to smoking.At the time of classification of exposure to smoking in
1951, the association with lung cancer was not commonly known. Some case-con-
trol studies had indicated an association, and some doctors may have been aware of
this, but they would not have known their own future risk of lung cancer.Therefore,
any such responder bias would likely result in non-differential misclassification and
underestimate the strength of the association.
Second, there could have been observer bias if lung cancer was more frequently
diagnosed or certified as the cause of death among smokers than among non-
smokers. However, this is unlikely since doctors would be likely to have access to
good medical care and lung cancer can be diagnosed accurately using various radio-
graphic and histological investigations. In addition, the cause of death was obtained
from death certificates and not diagnosed by study investigators.
2 A simple categorization could be to classify individuals as current smokers,
former smokers or lifelong non-smokers. However, the effect of smoking may vary
by the age doctors started to smoke, age of stopping smoking for former
smokers, type of smoke (i.e. cigarette, cigar, pipe), and a dose effect may be
investigated by quantifying the amount smoked (i.e. number of cigarettes per day,
inhalation of smoke, second-hand smoke). Information on all these variables should
be collected.
3 As rates are given inTable 8.1,the appropriate measure of association is the incidence
rate ratio of lung cancer deaths among different categories of smokers for males and
females. It would be most appropriate to use the death rate in non-smokers as the
reference ‘unexposed’ category.
The rate ratio for lung cancer among males smoking 1–14 cigarettes per day
compared with male non-smokers is calculated as follows (you may wish to refer to
Chapter 3):
23346.indb 10723346.indb 107 22/08/2011 15:1222/08/2011 15:12

78
= 7.8
10
Similarly, the rate ratio for lung cancer among females smoking 25+ cigarettes per day
compared with female non-smokers is calculated as follows:
208
= 29.7
7
You should have calculated the remaining incidence rate ratios from Table 8.1 as
shown inTable 8.3. Note, the rate ratio for the reference category is always 1.00.
Table 8.3 Incidence rate ratios for lung cancer death by gender and smoking status
Gender Lung cancer death rates per 100,000 persons per year
Non-smokers Smoking 1–14
cigarettes/day
Smoking 15–24
cigarettes/day
Smoking 25+
cigarettes/day
Male 1 7.8 12.7 25.1
Female 1 1.3 6.4 29.7
The rate ratio for lung cancer death increased with the quantity smoked among both
male and female doctors.This dose–response effect lends support to a causal associa-
tion between smoking and lung cancer.
The rate ratio in men smoking 1–14 and 15–24 cigarettes per day is much higher than
in women.In those smoking 25 or more cigarettes per day,the rate ratio in men is mar-
ginally less than that in women. Does this mean that the effect of low levels of smoking
is higher among men than among women?Without carrying out statistical tests,we can-
not know whether these rate ratios are signiﬁcantly different, but the study had a large
sample size and the magnitude of difference is high, so it is unlikely to be due to chance.
However, number of cigarettes smoked is unlikely to be a sufﬁciently good
estimate of overall exposure to tobacco, which will also be affected by other factors
such as the age of starting smoking (which was later among women than men in this
cohort), and inhalation (more men than women in this cohort reported inhaling).These
other factors modify the effect of number of cigarettes smoked on lung cancer death.
Activity 8.2
1 This is a retrospective occupational cohort study. Retrospective, because data on both
exposure and outcome are taken from routine data collected prior to the analysis.
Occupational,because all study participants share the same occupation,and employee
records were used to obtain data. Cohort, because the outcome frequency measure
is incidence.
2 The completed table should look like Table 8.4.
(a) The incidence rate is calculated as the number of new (incident)TB cases divided
by the person-time at risk for each category. For example, for HIV negative min-
ers, the incidence is 289 ÷ 36,020 = 0.0080 cases per person-year at risk, or 0.8
cases per 100 person-years at risk.
23346.indb 10823346.indb 108 22/08/2011 15:1222/08/2011 15:12

Cohort studies 109
(b) The incidence rate ratio is calculated as the rate in the exposed group divided by
the rate in the unexposed group. For example, the rate ratio ofTB for age 30–39
years compared with <30 years is 1.57 ÷ 0.67 = 2.34. You may have used a
different reference category,which would also be correct as long as the rate ratio
for the reference category is listed as 1.00.
3 A rate ratio of 3.61 indicates that the risk of pulmonary TB in this cohort is more
than three times greater in miners with HIV infection than in those without HIV.
This is a statistically significant result with less than 5% probability that it is due to
chance, as the 95% confidence interval does not include the value 1.00.We can be
95% certain that the true estimate of association between HIV and pulmonaryTB in
this mining population is between 3.12 and 4.19.
4 There is a clear association between age and the incidence of pulmonary TB, as the
rate ratio increases with age, and all estimates are statistically significant. It is also
possible that age is associated with HIV infection status, although we do not have
that information.The change in rate ratio after adjusting for age and study period
suggests that the initial estimate of association between pulmonaryTB and HIV may
be partly explained by the effects of age and study period. This suggests that age
may be a confounder in the association between pulmonary TB and HIV infection.
However,we would need to know the association between age and HIV,and the rate
ratio of pulmonary TB by HIV infection adjusted only for age group, to be sure.
Table 8.4 Incidence of tuberculosis (TB) by HIV status and age
Category Person-years at risk TB cases Incidence per 100
person-years at risk
Rate ratio
HIV negative miners 36,020 289 0.80 1.00
HIV positive miners 15,561 451 2.90 3.61
Age:
<30 years 15,483 103 0.67 1.00
30–39 years 24,645 387 1.57 2.34
40–49 years 8,670 176 2.03 3.03
≥ 50 years 2,783 74 2.66 3.97
Source: Ilona Carneiro, using data from Sonnenberg et al. (2005).
23346.indb 10923346.indb 109 22/08/2011 15:1222/08/2011 15:12

Overview
Case-control studies take the opposite approach to cohort studies,by identifying those
with and without the outcome, and then determining their previous exposure to
potential risk factors.This approach is especially useful for rare outcomes, as well as
being cheaper and faster than cohort studies, as the sample size can be smaller and
there is no need for lengthy follow-up. However, with this design it is impossible to
estimate the frequency of an outcome and it is more difficult to avoid bias.In this chap-
ter you will review the characteristics, advantages and limitations of the case-control
study design for analytical epidemiology.
Learning objectives
• describe the uses, strengths and limitations of case-control studies
• discuss potential sources of bias in case-control studies
• recognize the basic analytical approaches used in case-control studies.
What defines a case-control study?
In case-control studies, the study groups are defined by outcome and not by exposure.
Groups are selected on the basis of whether they do (cases) or do not (controls)
have the outcome under study at the beginning of the study.The cases are then com-
pared with controls to assess whether they are different in terms of their previous
exposure to particular risk factors.It is therefore impossible to estimate the frequency
(i.e. prevalence, risk, odds or incidence rate) of the outcome in the target population.
Case-control studies were first developed in the early 1950s to avoid some of the dis-
advantages of cohort studies. One of the advantages of case-control studies is that they
can be used to study rare outcomes. As participants are selected according to their
outcome status, it is possible to recruit the minimum number of cases and controls
required before the study begins. A cohort study requires follow-up of prohibitively
large numbers of individuals to ensure that enough participants develop a rare outcome.
The case-control design is also useful when a rapid result is required,as with outbreak
investigations, or with the appearance of a new syndrome (e.g. AIDS). Case-control
studies can also be more efficient than cohort studies when there is a long period of
Case-control studies
9
23346.indb 11023346.indb 110 22/08/2011 15:1222/08/2011 15:12

Case-control studies 111
time between the exposure and outcome (latency period), as for chronic diseases such
as cancer or AIDS.As the exposure is classified after the outcome, it is also possible to
investigate the association with multiple exposures.
One of the problems with case-control studies is that both exposure and outcome
have occurred by the time the patient is recruited into the study, making the design
susceptible to selection and information bias.
Genetic epidemiology
Case-control studies are especially useful in genetic epidemiology (Khoury and Beaty
1994), where the interaction between genetic and environmental factors is investi-
gated, because genes do not change with time.The sequencing of the human genome
has led to the search for disease susceptibility genes, and the case-control design
enables investigation of several genetic markers (and potentially the whole genome) in
the same study.In addition,genetic mutations are rare,requiring clinical and laboratory
tests that would be prohibitively expensive in a cohort study. However, when studying
associations within families, this may not be an appropriate design because of the risk
of overmatching (see below). Note that gender, ethnicity and other forms of population
structuring are likely to be confounders in studies of genetic traits and outcomes.
Study design
One way to reduce confounding in the study design is to identify controls with the
same characteristics as the cases – this is known as matching.However,matching can
be more complicated and costly, and is not necessary as long as sufficient data on
potential confounders are collected to enable adjustment in the analysis.
A special type of case-control design is the nested case-control study. In this
design, cases are members of a cohort that have developed the outcome, and controls
are those without the outcome.This allows us to automatically match on factors com-
mon to all cohort members. For instance, in an occupational cohort study, cases and
controls will be matched on employment status simply by virtue of being in that cohort.
This form of study design also means that new hypotheses can be tested more easily,
since data on exposures are likely to have already been collected as part of the cohort
study, which will save time and money.As data on exposures will have been collected
prior to the outcome, there is less chance of recall and observer bias, and it is easier
to establish the temporal condition for causality.
Sampling
As participants are selected on the basis of their outcome and will be compared by
their exposure, it is important that the participants are representative of the target
population in relation to the frequency of the exposure,and that the selection of cases
and controls is not influenced by their exposure (selection bias).
The case definition must be very precise and inclusion and exclusion criteria must
be clearly stated before the study is conducted to ensure that the practice of identify-
ing cases is kept uniform throughout the study. It is necessary to consider whether
both incident and prevalent cases should be included. Inclusion of prevalent cases may
23346.indb 11123346.indb 111 22/08/2011 15:1222/08/2011 15:12

make it easier to generalize the study to the target population. However, prevalent
cases may differ from incident cases in ways that may reduce the validity of the study.
Inclusion of prevalent cases, especially for chronic outcomes, can create problems for
determining exposure to certain risk factors that may change over time.This may lead
to reverse causality where the exposure changes as a result of the outcome (e.g.diet
or exercise regime).
Inclusion of prevalent cases may also lead to under-representation of more severe
cases of a rapidly progressive outcome, who will die sooner after diagnosis and be less
likely to be selected for the study. This in turn may affect the associations being
investigated, as exposures associated with increased survival may be associated with
the outcome, even though they might be protective against the development of severe
disease.If the outcome is fatal,it is important to ensure that patients who have died are
included to avoid selection bias.
An important consideration is the source of cases and controls. For example, if an
outcome is particularly severe,it may mean that cases are only found in hospitals.If the
outcome is rare or unusual, it is important to make sure that all locations of patients
are identified, as patients may travel out of their local hospital catchment area to get
specialist treatment, for example, at a referral hospital.
Although the recruitment process can be easier if cases are hospital-based, this
makes it more difficult to identify appropriate controls. If there is some selection of
who reaches hospital,then it may be appropriate to recruit controls from among other
hospital patients, as long as their selection is not then biased in terms of the exposure
of interest. For example, we may want to investigate risk factors for liver cirrhosis.
If we suspect heavy alcohol use to be a major risk factor and select cases from hospital
records, we may have problems if our hospital-based controls include a large propor-
tion of people admitted to hospital for trauma, since people admitted for this reason
are known to be more likely to be heavy users of alcohol than the general population.
If all people with the outcome go to hospital, and there is no other selection process
involved in the cases reaching hospital other than the outcome and the exposures
under consideration, then controls can be selected from the general population.
If cases can be selected from the general population, then controls can be randomly
selected from the same population with less likelihood of selection bias. Controls
should meet all the criteria for cases (i.e. be as similar as possible), except for the out-
come itself. For example, if the cases are men aged 40–65 years with lung cancer, the
controls should be selected from men of that age group who do not have lung cancer.
Matching
Matching may be used to reduce confounding of the association between exposure and
outcome, where confounders are known or highly probable. Individual matching identi-
fies between one and four controls for each case, with the same age or gender. Other
potential confounders, such as place of residence or ethnic group may also be used,
depending on the aim of the study.Be careful not to select too many characteristics on
which to match, or to select factors that might be very closely associated with
exposure status.This can lead to overmatching, such that cases and controls do not
differ sufficiently in relation to the main exposure of interest and we are unable to
measure the association.
An example of overmatching comes from an early case-control study of AIDS
(Moss et al. 1987), where investigators compared AIDS cases with two age-matched
23346.indb 11223346.indb 112 22/08/2011 15:1222/08/2011 15:12

homosexual male control groups.The first control was selected from the same neigh-
bourhood as each case, while the second control was selected from those attending a
clinic for sexually transmitted infections (STIs). The study found that cases were
52 times more likely to have >100 versus 0–5 sexual partners in the previous year
compared with HIV-negative neighbourhood controls, but only 2.9 times more likely
when compared with HIV-negative clinic controls.This is because STIs are associated
with number of sexual partners, so clinic controls were biased towards having more
partners.
An alternative to individual matching is frequency matching,in which the control group
is selected to be similar to the case group regarding the matched variable.To frequency-
match by gender, for example, if our cases were 60% female, we would need to select
controls that were also 60% female.
Data collection
Case-control studies start with assessment of the outcome,so collection of information
on exposures is almost always retrospective. Exposure data can be gathered in many
different ways, including by interview (e.g. face-to-face, self-completed questionnaire),
from records (e.g. medical, employer), or from biological samples. Ideally, the researcher
collecting exposure information should not know whether the study participant is a
case or control to avoid observer bias.
Reporting bias is more likely in case-control studies, as knowledge of being a case (or
control) may affect what individuals remember, or how they report events or expo-
sures. Cases may be more likely to remember events that occurred at around the time
they were diagnosed with disease or underwent a traumatic event. For example, par-
ents of children who develop autism may be more likely than other parents to remem-
ber the date of a vaccination, if it occurred in the days preceding a change in their
child’s behaviour. For this reason, it is important to use routinely collected data, or
memory guides and prompts, when collecting data on exposure.
Analysis
Case-control studies do not randomly sample the population, instead selecting indi-
viduals on the basis of their outcome status.Therefore, they cannot directly estimate
prevalence or incidence of the outcome or frequency of the exposure in the general
population.The outcome measure for a case-control study is therefore the odds ratio
of exposure (see Chapter 3),which is the odds of exposure in cases divided by the odds
of exposure in controls.This has the same numerical value as the odds ratio of out-
come, although the interpretation is different. For example, in a case-control study
measuring the association between stress and traffic accidents, an exposure odds ratio
of 1.82 indicates that cases (individuals in a traffic accident) have 82% greater odds of
exposure to stress than controls.If the outcome is rare and the exposure is reasonably
common, this measure approximates the risk ratio.
If the study is matched, then a more complicated analysis needs to be performed to
account for matching. In this type of analysis, only the matched groups that are discord-
ant (i.e. where either the case is exposed and the control unexposed, or the case is
unexposed and the control exposed) are compared to give the odds ratio of exposure.
This is because pairs where both case and control are exposed,or both case and control
23346.indb 11323346.indb 113 22/08/2011 15:1222/08/2011 15:12

are unexposed, provide no information on differences in exposure.This can be done
using conditional logistic regression.
Interpretation
Even if an association between exposure and outcome is found, the investigator still
must consider whether the result could have arisen through chance, bias or confound-
ing. As noted previously, the case-control design is especially prone to selection bias
and reporting bias,because exposure is determined after outcome.Precautions should
be taken to avoid observer bias when collecting data on exposures (e.g. blinding data
collectors to the outcome status). For chronic outcomes or those with a long latent
period (e.g. AIDS), there may be a possibility of reverse causality, when the outcome
causes the exposure (e.g. change in diet) to occur before symptoms of the outcome
were identified.
Activity 9.1
A review of epidemiological studies of the association between alcohol consumption
and breast cancer identified 27 case-control studies, 8 cohort studies and 5 ecological
studies carried out between 1977 and 1992 (Rosenberg et al. 1993).
1 Why do you think more investigators preferred the case-control study design over
the other designs?
Activity 9.2
It is now well accepted that early age at menarche (first menstrual cycle), late age at
menopause (end of fertility), nulliparity (never having given birth), and late age at first
birth are risk factors for breast cancer in women.
A case-control study investigated the relation between alcohol and breast cancer in
women. Some 160 women aged under 75 years were treated for newly diagnosed
breast cancer at four hospitals. Of these women, 30 could not be interviewed because
the patient refused, their consultant refused or the patient was too ill to be inter-
viewed.The remaining 130 women were interviewed at hospital within 6 months of
diagnosis by one of six interviewers. The investigators recruited 520 controls who
were attending the same hospital for other conditions.The interviewers were aware of
the hypothesis, and which women were cases and which were controls.
1 Why do you think that cases in the study were restricted to:
(a) women who had been diagnosed with breast cancer in the 6 months before the
interview?
(b) women who were attending hospital?
2 If you were designing a questionnaire for this study, what information on alcohol
consumption would you ask for? What other questions would you consider
necessary?
3 If you were one of the study investigators,from where would you have selected your
controls, and what would your inclusion and exclusion criteria have been?
23346.indb 11423346.indb 114 22/08/2011 15:1222/08/2011 15:12

4 If the investigators had matched the controls to cases, what matching variables
should they have used?
5 Describe potential sources of bias in the study design.
Activity 9.3
In May 1997, a 3-year-old boy died of a respiratory illness labelled as ‘avian’ influenza A
(H5N1).A case-control study was carried out in Hong Kong in January 1998 to identify
risk factors for an outbreak of influenza A (H5N1) after 15 patients were hospitalized
with the disease (Mounts et al. 1999). Two age- and gender-matched controls were
identified for each case by randomly selecting a neighbouring apartment building to
each case’s residence and asking for volunteers.
1 Discuss the benefits and limitations of using a case-control design in this situation.
2 Interpret the investigators’ main finding of an odds ratio of 4.50 (95% confidence
interval: 1.20, 21.70) for exposure to live poultry in the market the week before
illness, and consider the implications.
Conclusion
case-control studies. This design takes the opposite approach to cohort studies, by
determining outcome before exposure status,and therefore has a greater likelihood of
bias.The population is not sampled randomly, so case-control studies cannot be used
to estimate the incidence or prevalence of outcome or frequency of exposure. Case-
control studies are generally cheaper and shorter than cohort studies, as they do not
require any follow-up of participants.This design is especially useful for studying rare
outcomes, or those with long latency periods.
References
Khoury MJ and Beaty TH (1994) Applications of the case-control method in genetic epidemiology.
Epidemiologic Reviews 16: 134–50.
Moss AR, Osmond D, Bacchetti P, et al. (1987) Risk factors for AIDS and HIV seropositivity in homosexual
men. American Journal of Epidemiology 125: 1035–47.
Mounts AW, Kwong H, Izurieta HS, et al. (1999) Case-control study of risk factors for avian influenza A
(H5N1) disease, Hong Kong, 1997. Journal of Infectious Diseases 180: 505–8.
Rosenberg L, Metzger LS and Palmer JR (1993) Alcohol consumption and risk of breast cancer: a review of
the epidemiologic evidence. Epidemiologic Reviews 15: 133–44.
Activity 9.1
1 A case-control design is superior in this example for several reasons. First, breast
cancer is known to be associated with several risk factors and the case-control design
23346.indb 11523346.indb 115 22/08/2011 15:1222/08/2011 15:12

allows investigation of multiple exposures. Second, breast cancer has a long latent
period and is relatively uncommon, so a cohort design would need more resources
and time to follow up sufficient participants.Third, an ecological study would not be
able to establish a causal link,though it could be used initially to generate the research
question by indicating a possible link between breast cancer and alcohol.
Activity 9.2
1 (a) Women were interviewed within 6 months of diagnosis, so that only incident
cases of breast cancer were included in the study.Inclusion of prevalent cases may
lead to bias if as prevalent cases may have changed their behaviour and therefore
their exposure to risk factors as a result of their disease. Restricting the study to
incident cases also ensures that severe cases are not under-represented.
(b) Although selection of population-based cases may result in a study that is less prone
to bias, the logistics and costs involved may make it easier to identify cases in a
hospital setting,particularly cases of a rare disease such as cancer. There is then the
consideration of whether those with the disease under investigation are likely to be
admitted to hospital.Women with breast cancer are almost certain to be referred
or admitted to hospital once diagnosed, so selection of hospital-based cases is
appropriate in this study.
2 In designing a questionnaire,you would consider what information is needed,and how
you would ask questions to reduce potential measurement and recall bias. For exam-
ple, it is well known that people tend to under-report their alcohol consumption.
You might collect the following information related to alcohol consumption:
• Whether the participant is a current, past, or non-drinker.
• What type of alcohol they consume (e.g. beer, wine, spirits).
• How much alcohol they consume (e.g. number of drinks per day).
• How often they drink (e.g. number of days per week).
• The age at which they started drinking (and age at which they stopped drinking, if
they stopped).
Other questions you would ask would elicit basic demographic information about the
participants (e.g. date of birth, education, occupation).You would ask about potential
confounders such as smoking and known risk factors for breast cancer (e.g. age at
menarche, age at menopause, number of pregnancies, age at first birth).
3 In general, investigators find it convenient to select controls from the same setting
in which they selected the cases. However, it is important that the study is not then
biased by selecting controls that are more similar to cases in terms of exposure than
they would have been if selected from the general population.
Some hospital-based studies use two control groups, one from a hospital setting
and the other from the population. If the selection of controls from within the hospi-
tal setting has not led to any bias, the results should not differ between the two
control groups. However, if the results differ between the control groups, interpreta-
tion may be a problem.
Any exclusion criteria that apply to cases should also apply to controls (e.g.women
aged over 74 years, women with previous breast cancer). You may also consider
excluding patients who are admitted to hospital with alcohol-related diseases, and
diseases related to known risk factors for breast cancer (e.g.gynaecological diseases).
Many case-control studies of a specific cancer also exclude controls with any sort of
23346.indb 11623346.indb 116 22/08/2011 15:1222/08/2011 15:12

cancer. In hospital-based studies, it is important to include controls with a range of
different diseases so that no one disease is unduly represented.
4 The investigators could have matched on age.They could also have matched on a
known risk factor for breast cancer such as parity (the number of times a woman has
given birth). However, this would be more complicated and it is important not to
overmatch (i.e. match on alcohol status by mistake).
5 The 30 women with breast cancer who were not included in the study may have
differed from other cases in some way.This would lead to selection bias as the cases
might not be representative of all women with breast cancer, especially if those not
participating differed in relation to their alcohol consumption.
The investigators’ knowledge of the hypothesis might have led to observer bias.The
investigators may have asked more probing questions about alcohol use if the par-
ticipant was a case.
The six interviewers may also have varied in the way they conducted the interview,
or the way they recorded information, leading to information bias.
Biases could have been minimized by:
• blinding the interviewers to the study hypothesis;
• blinding the interviewers to the identity of the cases and controls;
• using a small number of interviewers to reduce inter-observer variation;
• using a structured questionnaire to avoid subjectivity on the part of the interviewer;
• training the interviewers and supervising some interviews to ensure consistency.
Activity 9.3
1 The case-control design is ideal for an outbreak situation as rapid results are needed.
There are unlikely to be many prevalent cases, so a cross-sectional study would be
inappropriate. It is not possible to predict the frequency of the outcome, and when
first identified the outcome is likely to be rare, making it impractical to implement a
cohort study.
However, there may be selection bias due to difficulties in identifying appropriate
controls,especially if the risk factors have not yet been identified.The choice of neigh-
bourhood controls could lead to overmatching if the risk factor is an environmental
exposure, and several types of controls should be used in this situation to avoid this
bias.There may be information bias, as the outcome status is already known. In this
situation, where media coverage of the death had occurred and the source of the
virus had been identified as birds, cases may have remembered their recent
contact with live poultry differently to controls, thus biasing results.
2 As this is a case-control study, the measure of association is the odds ratio of expo-
sure.This means that cases were four times more likely than controls to have had
contact with live poultry in the week before the illness. It does not tell us that those
who had contact with live poultry were four times more likely to suffer from H5N1
disease. However, while it is a useful indicator of the factors that may be associated
with an outcome, this study does not provide sufficient evidence of causality for
reasons mentioned in the previous answer.
Given the potential implications of identifying live poultry markets as the cause of
the outbreak (e.g. slaughter of all poultry, closure of poultry markets), further sup-
portive evidence would be needed (e.g. isolation of H5N1 virus from poultry in the
markets) before inferring causality.
23346.indb 11723346.indb 117 22/08/2011 15:1222/08/2011 15:12

Intervention studies
10
Overview
The analytical study designs described in Chapters 6–9 are all observational, i.e. investi-
gators observe the natural development of the outcome without interfering.Intervention
studies are epidemiological experiments during which the investigators aim to change
the natural occurrence of an outcome by manipulating the exposure. Both cross-
sectional and cohort methods may be used to measure the relative frequency between
exposure and outcome and consequently the effect of the introduced intervention.The
randomized controlled trial (RCT) is the ideal intervention study design as it reduces
error due to bias and confounding. Given ethical constraints, other intervention study
designs may be used when a RCT is not acceptable. Intervention studies may measure
intervention efficacy under ideal conditions or effectiveness under routine conditions.
Learning objectives
• describe the use, strengths and limitations of intervention studies
• distinguish between the different types of intervention study design
• recognize the basic analytical approaches used
• discuss ethical issues related to the design and conduct of intervention studies.
What defines an intervention study?
An intervention study measures the association between an outcome and exposure to
a specific intervention. Interventions may focus on prevention of exposure in those at
risk of the outcome (e.g. insecticide-treated mosquito nets against malaria) or treat-
ment to reduce mortality or severity in those who already have the outcome (e.g.
interferon treatment of people with chronic Hepatitis B to reduce progression to liver
cancer). An intervention may remove or reduce an assumed risk factor (e.g. health
education to reduce smoking), or it may introduce or increase an assumed protective
factor (e.g. vaccination against poliovirus).
Either cohort or cross-sectional methods may be used to measure the relative fre-
quency of the outcome in those exposed and unexposed to the intervention under
study. However, unlike the observational study designs described previously, interven-
tion studies are experimental because the investigators are able to intervene. In this
design,the investigators define which study subjects are‘exposed’ and which are‘unex-
posed’.For ethical reasons experimental studies are restricted to evaluating exposures
that reduce the frequency of a negative outcome.
23346.indb 11823346.indb 118 22/08/2011 15:1222/08/2011 15:12

Intervention studies 119
The intervention study design is ideal for inferring causality (see Chapter 4) for the
following reasons:
1 The exposure is defined prior to development of the outcome, so the temporal
sequence is established, satisfying the temporality consideration for causality.
2 If the intervention is the removal or reduction of an exposure of interest that
results in a reduction in the frequency of an outcome, it satisfies the reversibility
consideration for causality.
3 Investigators are able to randomize study subjects to be exposed and unexposed to
the intervention. If the number of subjects is large enough to reduce the effects of
chance, this ensures that all known and unknown confounders are equally distributed
between comparison groups (i.e. comparison groups are identical in all ways except
for the intervention and there is no selection bias).
4 Investigators may be able to conceal the allocation of the intervention from study
subjects and from those measuring the outcome, reducing information bias.
Intervention studies are not appropriate for very rare outcomes, as they generally use
cohort methods that would require a long follow-up time. However, if the outcome is
chronic (e.g. Hepatitis C infection) it may be possible to measure the intervention
effect using cross-sectional surveys with very large sample sizes.
Intervention studies are often long and expensive to carry out.They may require a
large study team and lengthy follow-up time to identify sufficient subjects with the
outcome.There may also be additional costs of the intervention itself, as well as costs
related to concealing the allocation and monitoring the safety of the intervention.
If an intervention is already in routine use, it may not be feasible to withdraw it from
participants in the control group without providing an alternative, even if the safety or
efficacy of the intervention is unknown or in doubt. For example, there is no evidence
that prenatal ultrasound screening improves birth outcome and concerns have been
raised about its potential long-term effects. However, routine ultrasound scans are an
accepted part of obstetric care in developed countries and it would be difficult to
recruit sufficient subjects to a randomized trial where routine ultrasound was withheld
from the comparison group.
Ethical objections may be raised about withholding an intervention from the com-
parison group if the intervention has already been shown to be safe and effective in a
previous study. However, it is not unusual for an initial study to show evidence of an
effect, while subsequent studies in different settings give conflicting results. Ethical
responsibility must be balanced against the need for sufficient and consistent epide-
miological evidence,and a systematic review of existing evidence should be undertaken
before developing any intervention study proposal.
Study design
Ethical approval
It is necessary to obtain ‘ethical approval’ (i.e. permission) from national and
institutional ethical bodies prior to conducting any epidemiological investigation, but
this is even more relevant to intervention studies as investigators determine which
23346.indb 11923346.indb 119 22/08/2011 15:1222/08/2011 15:12

intervention the participants receive.TheWorld Health Organization and other national
and international bodies have developed guidelines for intervention studies based on
the Declaration of Helsinki. However, whether a study is judged to be ethical can vary
greatly between countries and over time, as scientific knowledge and cultural norms
develop.
Intervention studies need to address questions of sufficient public health importance
to justify their use. Ethical considerations will often drive the choice of specific study
design (see below) as most designs involve the ‘denial’ of a potentially efficacious inter-
vention to subjects allocated to the control arm during the study period. However, the
general population will eventually benefit if the study provides sufficient evidence of a
protective intervention effect, and those who participated in the trial should be the
first to benefit from such an intervention once the trial is over.
Efficacy and effectiveness
There are two stages in evaluating an intervention that can be addressed using the
intervention study design.Efficacy studies aim to measure the effect of the intervention
under ‘experimental’ conditions, where maximum effort is put into intervention deliv-
ery. For example, participants in an infant vaccine trial may be reminded to attend for
vaccination or even visited at home if they do not attend the vaccination clinic.
Once an intervention has been proven to be efficacious,it may be appropriate to under-
take an effectiveness study to measure the effect of the intervention under routine condi-
tions.This is especially important for interventions that rely on fragile delivery systems such
as a weak health infrastructure, or where long-term patient compliance is required.The
effectiveness of an intervention may be very different to its efficacy, and provides a better
estimate of its likely impact when administered to the general population.In the infant vac-
cine example, effectiveness will depend on factors such as whether the vaccine is in stock
and viable, whether infants attend for vaccination, their age when they attend, and the
number of doses they receive.While the vaccine may have a 90% efficacy against the out-
come,if only 50% of those at risk of the outcome actually receive sufficient doses of viable
vaccine at the correct time,the effectiveness could be closer to 45% (0.9 × 0.5 = 0.45).
Plausibility studies
Plausibility studies evaluate the effectiveness of interventions by comparison with a
historical, geographical or opportunistic control group, but without randomization.
They are appropriate in the following situations (Victora et al. 2004):
1 When an intervention is so complex that RCT results will be unacceptably artificial.
2 When an intervention is known to be efficacious or effective in small-scale studies,
but its effectiveness on a large scale must be demonstrated.
3 When ethical concerns prevent the use of an RCT.
Historical controls
If it is not possible to have a contemporary comparison arm for ethical or logistical
reasons, an intervention study may compare outcome frequency before and after the
intervention is introduced.This design is most commonly used in evaluations of health
23346.indb 12023346.indb 120 22/08/2011 15:1222/08/2011 15:12

services. However, the use of such ‘historical’ controls makes it difficult to distinguish
the effect of the intervention from other changes that may have affected the outcome
over the study period. If this design is used, it is necessary to carefully monitor other
changes that may occur in the study population (e.g. migrations, introduction of other
interventions, changes in climate variables), other outcomes that should not have been
affected by the intervention, and the outcome of interest in the general population to
which the intervention has not been applied.
Geographical controls
The use of communities or individuals as contemporary control from outside the trial
area may adjust for the effects of temporal changes during the course of the evaluation.
However,there are likely to be inherent differences between the control and interven-
tion communities that need to be considered when interpreting the results.
A variant of this,which enables some randomization,is called the stepped-wedge design.
It is not frequently used,because of the complexity of the design and logistics.The inter-
ventions may be phased in to a population over time,usually in line with practical delays
in introducing a new intervention (e.g. training of health staff, community health educa-
tion).In the first such trial,Hepatitis B vaccine was gradually introduced intoThe Gambia
by adding a new immunization team responsible for a different part of the country every
three months (The Gambia Hepatitis Study Group 1987). The order in which the
Figure 10.1 Schematic of stepped-wedge intervention trial design. Shaded squares represent clusters
receiving the intervention.Unshaded squares represent clusters that have not yet received the intervention
(controls).Over the course of the trial the total number of intervention and control clusters are equal,but
the distribution varies with time
Source: Drawn by Ilona Carneiro, modified fromThe Gambia Hepatitis Study Group (1987) and Brown and Lilford (2006).
23346.indb 12123346.indb 121 22/08/2011 15:1222/08/2011 15:12

intervention was introduced was randomly allocated, and those areas that had not yet
received the intervention acted as the control arm of the study (see Figure 10.1).
As the intervention and control arms are not equally distributed over time, any
change in other risk factors for the outcome over the course of the study may con-
found the findings.This can be reduced by having large numbers of clusters and small
interval periods for introduction of the intervention to each additional cluster.
Opportunistic controls
This involves the use of individuals or communities that should have received the inter-
vention but did not because the programme was unable to reach them. If the controls
have varying degrees of exposure to the intervention, it may be possible to measure a
dose–response effect.
Randomized-controlled trials
While effectiveness studies may be subject to ethical and practical design limitations,an
efficacy study is ideally conducted as a randomized-controlled trial (RCT). Trials in
which the intervention is not randomly allocated are likely to suffer from selection bias
and confounding, but may be used to provide preliminary evidence prior to a more
rigorous study. RCTs are defined by: (a) the existence of a contemporary comparison
group of study subjects who do not receive the intervention,known as the‘control’ arm;
and (b) the random allocation of study subjects to the intervention and control arms.
You may see the terms ‘phase 2’ or ‘phase 3’ applied to RCTs, especially where a
clinical outcome is being measured. For example, a phase 3 RCT to evaluate the effi-
cacy of insecticide-treated mosquito nets against malaria incidence.This classification
comes from clinical trials of new medical interventions (e.g.drugs,vaccines,diagnostics,
surgical procedures), which are conducted in several consecutive phases. Phase 1 trials
apply the intervention to small numbers of healthy volunteers to assess issues such as
safety and tolerability. Phase 2 trials evaluate efficacy and safety in larger groups of
about 100–300 people, and may use the RCT design. Phase 3 clinical trials aim to pro-
vide definitive evidence of efficacy in individuals at risk of the outcome and usually use
the RCT design. Phase 4 trials monitor the routine use of an intervention without a
comparison group,mainly to collect data on safety (pharmacovigilance),and are akin to
effectiveness studies and monitoring of routine health programmes (see Chapter 12).
Cluster-randomized trials
In cluster-randomized RCTs,groups of individuals known as‘clusters’ are randomly
allocated to the intervention and control arms, and all individuals within the same
cluster receive the same intervention or control.This design may be used if the inter-
vention acts at the cluster level (e.g. an intervention that reduces air pollution would
need to be introduced at the community level since it would be impossible to intro-
duce pollution controls at an individual level). Cluster randomization may be appropri-
ate when there is a risk of contamination between the intervention and control groups,
such that controls may be exposed to the intervention or vice versa. For example, in a
trial of health education leaflets to promote healthy diet in school children, investiga-
tors would randomize at the school level.If they had randomized at the individual level,
23346.indb 12223346.indb 122 22/08/2011 15:1222/08/2011 15:12

children within a particular school might show the leaflets to friends in the control
group. Cluster-randomized trials require larger sample sizes as individuals within a
cluster will share several characteristics and cannot be treated as independent obser-
vations, leading to reduced statistical power.Therefore, special methods are required
to estimate sample sizes for cluster-randomized trials and to analyse the results (for
more information see Hayes and Moulton 2009).
Factorial design
In a factorial trial, two or more interventions are compared individually and in com-
bination against a control comparison group.This has the advantage of enabling us to
assess interactions between interventions, and may save time and money by evaluating
several intervention combinations simultaneously.For example we might want to com-
pare the relative and additive efficacy of an insecticide-treated net (ITN) and intermit-
tent preventive treatment for malaria in infants (ITPi) with sulphadoxine-pyrimethamine
(SP) (see Figure 10.2).A factorial design would result in a four-arm trial: (i) infants in
group 1 would receive an untreated mosquito net and an IPTi placebo-drug and would
be the reference group;(ii) infants in group 2 would receive an untreated mosquito net
and IPTi with SP,(iii) infants in group 3 would receive an ITN and an IPTi placebo-drug,
and (iv) infants in group 4 would receive both an ITN and IPTi with SP.
Figure 10.2 Flow-chart of a factorial design randomized controlled trial of an insecticide treated net
(ITN) and/or intermittent preventive treatment in infants (IPTi) with sulphadoxine pyrimethamine (SP) or
a placebo
Source: Ilona Carneiro, modified from LSHTM lecture notes.
Crossover design
In a crossover design RCT, each trial subject (e.g. individual, village) acts as its own
control by receiving either the intervention or control at different points in the study,
with a washout period (i.e. the time needed for the intervention to stop having an
effect) to avoid contamination between the study periods. The order in which the
23346.indb 12323346.indb 123 22/08/2011 15:1222/08/2011 15:12

subject receives the intervention or control (e.g.intervention then placebo,or placebo
then intervention) is determined by random allocation. This design is only suitable
when the intervention does not have long-term effects. However, it enables us to
control for all confounders and effect modifiers.
The following specific study design issues refer to RCTs.
Sampling
As with all epidemiological studies, study participants should be representative of the
population to which the intervention will ultimately be applied. Eligible subjects are
identified using clearly defined inclusion and exclusion criteria and informed consent
must be obtained (see Chapter 5).
There may be some selection bias at enrolment, especially if there is a risk of serious
side-effects or a chance of not receiving active treatment for a medical condition. For
example,an individual with asymptomatic chronic Hepatitis B infection might be less willing
to join a trial of treatment to suppress viral replication than might an individual with abnor-
mal liver function.Equally,individuals with advanced cancer that have already tried existing
treatments may be more willing to try a new experimental treatment.Such selection may
affect the estimate of efficacy if the intervention acts differently at different stages of dis-
ease,and it may not be appropriate to generalize the result to the wider target population.
Selection bias may also be introduced during the course of the study if there is a differ-
ence in the follow-up between the intervention arms. For example, participants may be
more likely to withdraw from a study if there are side effects or if they feel the interven-
tion is not working.There may also be differences in compliance due to clinical deteriora-
tion or because a participant forgets to administer a placebo because they do not notice
any benefit (e.g. a placebo mosquito repellent). Participants who are lost to follow-up or
do not comply may be different from those who complete the study,and baseline data on
important risk factors should be compared to assess the potential for selection bias.The
proportions of subjects lost to follow-up and those not included in the final analysis must
also be compared between the different intervention arms to identify any selection bias.
Choice of control
Participants receiving the intervention of interest are compared to those not receiving
the intervention of interest,called the control arm.Comparison will vary according to
the intervention being evaluated, and subjects in the control arm may receive nothing,
a placebo intervention, or an existing intervention. Typically, we want to know the
effect of an intervention compared with current practice.If no intervention is currently
in use, the control arm may receive no intervention, but should otherwise have identi-
cal access to all the treatment and preventive services as those in the intervention arm.
Investigators may use a placebo, a simulated intervention with no active properties,
as a negative control in intervention studies, because the act of receiving an interven-
tion may itself affect a subject’s perceived or actual outcome.An individual who thinks
they are receiving a treatment may actually experience a reduction in symptoms.This
positive outcome without any active intervention is known as the placebo effect. A
study subject may also experience more negative effects (i.e. increased symptoms or
side-effects) after receiving a placebo, which is known as the nocebo effect.
23346.indb 12423346.indb 124 22/08/2011 15:1222/08/2011 15:12

These responses have been shown to have a neurobiological basis in brain imaging
studies, but they are not yet fully understood. For some outcomes (e.g. Parkinson’s
disease, irritable bowel syndrome), self-healing processes were identified as playing a
role after a placebo intervention was shown to have an effect. In epidemiology, the use
of a placebo enables us to adjust for the‘background’ effects of participating in the trial,
such as participant expectation, interaction with study investigators and tests for
monitoring and measuring the outcome.
Where an intervention already exists,it would be unethical to withdraw the existing
intervention in exchange for a placebo.The control arm participants must receive the
best current drug or practice available to them, although this may not always be the
best available worldwide. For example, studies in country X find drug A to be a better
treatment for tuberculosis than the existing drug B, and drug A is implemented as the
new first-line therapy in countries X and Y. However, no studies have yet been under-
taken in country Z where drug B is still the first-line therapy.Investigators may success-
fully argue for a RCT of drug A compared with drug B in country Z, as control
participants will be receiving the best available current practice. However, it would no
longer be possible to carry out the same trial in countryY, even if there were no prior
local evidence,because drugA is already the best treatment currently available to study
participants.
Allocation
Allocation of participants is usually done randomly so that any study participant has an
equal chance of being allocated to the intervention or control arms,therefore avoiding
selection bias (see Chapter 4). If the sample size is sufficiently large, this randomization
ensures that any known or unknown confounding factors are equally distributed
between study arms and will not interfere with an estimate of intervention effect.
Random allocation can be undertaken using similar methods to those described for
random sampling in Chapter 5:
• Simple randomization uses random number tables or a computer-generated random
number list. However, this could result in different numbers of subjects in each
study arm.
• Systematic randomization allocates participants to each group alternately (e.g.on spe-
cific days), but this may be subject to selection bias. For example, there may be sys-
tematic differences in the severity of patients presenting to a clinic on a Monday
(after the weekend) and those presenting on a Tuesday.
• Blocked randomization restricts the allocation list to ensure equal numbers in all
study arms. For example, a trial comparing interventions A and B may use blocks of
four to generate six possible randomization sequences with equal allocation:AABB,
ABAB, BABA, ABBA, BAAB, BBAA. Blocks can then be chosen at random to
define the allocation sequence but the investigator should not know the block size,
as they might be able to predict the allocation for the last few participants in each
block. Block size must be a multiple of the number of intervention arms, but large
blocks should be avoided.
• Stratified randomization divides participants into subgroups or strata based on key
risk factors (e.g. age, gender), and equal numbers of subjects from each stratum are
randomly allocated to each study arm.This ensures that suspected confounders or
effect modifiers of the association between intervention and outcome are equally
23346.indb 12523346.indb 125 22/08/2011 15:1222/08/2011 15:12

distributed between comparison groups. For example, malaria incidence varies con-
siderably between communities due to socio-economic and geographic differences.
In a RCT of an infant malaria vaccine, infants should be stratified according to their
village of residence and allocation of the intervention based on block-randomization
within village.This allows the investigators to control for village-level differences in
malaria risk and other factors, which could otherwise vary by chance between the
study arms.
• Matched-pair randomization is a form of stratified random allocation that matches
individuals or communities into pairs with similar baseline risks of the outcome.
In small trials when several variables need to be balanced between study arms, strati-
fied randomization is not sufficient to ensure comparability.Differences between study
arms may still occur by chance,making it difficult to interpret results,even after adjust-
ing for these differences in the analysis.In this situation,rather than randomly allocating
subjects we purposefully allocate subjects based on a pre-specified list of criteria.This
is known as minimization, as the intention is to minimize differences between study
arms. As each subject is enrolled, their allocation depends on the characteristics of
those subjects already enrolled (for further details see Altman and Bland 2005).
For all the methods described above there is a chance of conscious or unconscious
selection bias if a study investigator undertakes the allocation. For example, they may
tend to allocate more seriously affected patients to the intervention and less seriously
affected patients to the control arm.To avoid such bias, the allocation sequence should
be concealed from those enrolling study subjects.
Allocation concealment may use sealed envelopes determining the allocation,
which are only opened after an eligible subject has consented to enter the trial. For
multi-centre trials,there may be a centralized system where subject details are entered
into the trial computer, which then randomly allocates the subject to one of the treat-
ment groups.Another method is for allocation to be done by the manufacturer of the
intervention (e.g. drug, vaccine, mosquito net), with the intervention and control pack-
aged identically with serial numbers whose coding is known only to the manufacturer.
Allocation concealment is not the same as blinding (see below).It is possible to conceal
the allocation sequence prior to allocation in all RCTs,even though it may not then be
possible to conceal it from subjects or observers after the allocation has been made.
Blinding
An ‘open-label’ trial is one in which participants and investigators are aware of which
intervention is allocated to which study subjects. However, if a participant knows
whether they are receiving a new intervention, existing intervention or placebo, it may
affect their behaviour during the trial or their response to questions that aim to deter-
mine outcome. For example, a mother who knows her child was vaccinated against
measles may be less likely to seek treatment for a fever than one whose child was not.
If one of the study outcomes is clinic attendance with fever, this could result in ascer-
tainment bias between the study arms.This is of greater concern if the outcome may
be subjective, such as reported improvement in symptoms of multiple sclerosis.
Observer bias can also occur if the person assessing the outcome is aware of the
allocation. For example, a microscopist reading blood slides to detect malaria parasites
may be less thorough if they read the slides while sitting in a village with insecticide-
treated curtains in every doorway than in one without curtains. For most outcomes it
23346.indb 12623346.indb 126 22/08/2011 15:1222/08/2011 15:12

is usually possible to‘blind’ the observer,i.e.to conceal the intervention allocation from
the person diagnosing the outcome.
Use of a placebo intervention can help to conceal the allocation.While a placebo is
easier to develop for drugs and vaccines it is not impossible to develop placebos for
non-chemical interventions such as counselling or acupuncture. For example, ‘sham’
surgery maintains the illusion of an operation by using real anaesthesia,surgical incision
and pre- and postoperative care, but leaving-out the actual intervention of interest.
While this raises many ethical concerns,the increasing use of minimally invasive proce-
dures (e.g.keyhole surgery) reduces negative effects for the participants while enabling
a more rigorous testing of such interventions.
If either participant or observer is blinded, the study is single-blind, whereas if both
are blinded, the study is double-blind.The ‘gold standard’ for RCTs is the double-blind,
randomized placebo-controlled trial.
Data collection
Data collection methods in an intervention trial will be the same as for cohort or
cross-sectional studies, depending on the design used. However, if the study has been
blinded to those observing the outcome, it is important that intervention allocation is
also blinded to those entering and analysing the data, to prevent any intentional or
unintentional bias from being introduced.
Analysis
It is good practice for a statistician independent of the study team to hold the codes
to the intervention allocation. Codes should not be revealed to study investigators
until after data have been entered and cleaned. In large clinical trials, the data are
‘frozen’, i.e. a copy of the data prior to ‘breaking-the-code’ is sent to an independent
statistician for safekeeping, to ensure that data are not changed after the allocation is
revealed.
A detailed analytical plan should be developed prior to breaking the allocation codes.
This will state the primary outcome of interest, any secondary outcomes of interest,
the methods of analysis to be used (e.g.logistic regression models) and any variables to
be adjusted for in the analysis.This prevents investigators from searching through the
data and only presenting positive results.
Interim analysis
In intervention studies with a long follow-up period, where there may be a possibility
of severe adverse events, it is usual to have an independent trial safety monitoring
board.This board is responsible for periodically reviewing all reports of severe adverse
events. If there is a concern about greater than expected numbers of adverse events in
one study arm,the board will analyse the data and if necessary the trial will be stopped.
It is also common for the monitoring board to undertake an independent interim
analysis of the data halfway through a long study. If there is sufﬁcient epidemiological
evidence that the intervention is working, or that the trial will have insufﬁcient power
to detect an effect, the trial may also be interrupted.
23346.indb 12723346.indb 127 22/08/2011 15:1222/08/2011 15:12

Intention-to-treat vs. per-protocol
The primary analysis of an intervention study should be by intention-to-treat (ITT).This
means that the outcome is compared between study participants according to the groups
to which they were allocated at the start of the study, even if they changed groups, with-
drew from the study or were lost to follow-up. ITT maintains the original allocation to
ensure comparability between intervention arms,and avoids potential selection biases that
can arise from different levels of participation during the study. For example, assume that
the side-effects of cancer treatment X caused more advanced-stage patients to deteriorate
more rapidly and be withdrawn from the study prior to completing treatment. Excluding
them from the analysis might result in more severe cases in the comparison arm at the end
of the study,mistakenly implying that treatment X was more effective than the control.
The ITT estimate of intervention effect will be closer to what may result in the ‘real
world’, where individuals may not all receive the intervention at the prescribed time
points or may not use the interventions as intended. However, we might also want to
know what the ‘true potential’ of the intervention might be in an ideal world (e.g. if we
were able to improve delivery or compliance). For this reason, a secondary analysis
may be carried out per-protocol. In per-protocol analysis, only those study partici-
pants who receive the intervention according to the pre-defined protocol are included
in the analysis. For example, a vaccine trial may specify vaccination of infants between
6–10 weeks,10–14 weeks and 14–18 weeks of age.Including infants in the analysis who
missed doses or who received doses very late will lead to non-differential misclassifica-
tion bias and may underestimate the potential of the vaccine.
Intervention efficacy
Once the intervention allocation has been revealed, the baseline data (e.g. age, sex,
ethnic group, disease grade) are compared between intervention arms to show how
successful the allocation process was in producing comparable participants.Differences
in baseline characteristics may be due to chance or to biases in the allocation method.
If differences are considered to be due to chance,they may be adjusted for by including
these factors in a multivariable regression model,for example.If the differences may be
due to biased allocation, then it will not be possible to interpret whether any differ-
ences are due to the intervention or to selection bias.
As intervention studies generally use cohort methods, the measures of association
are risk and rate ratios (see Chapter 3). Some intervention studies may also measure
prevalence as a secondary outcome using cross-sectional surveys, and the odds ratio
may be calculated as an estimate of the prevalence ratio (see Chapter 7).
The efficacy of an intervention is calculated as the proportion of cases that can be
prevented by the intervention.This is also known as the protective efficacy or preventable
fraction and is the inverse of the attributable fraction (see Chapter 3). Intervention
efficacy is calculated as:
Intervention efficacy = 1 – Relative risk
Interpretation
As with all epidemiological studies, the results need to be interpreted with caution,
considering the roles of chance, bias and confounding. However, if the trial has been
23346.indb 12823346.indb 128 22/08/2011 15:1222/08/2011 15:12

conducted correctly with effective allocation and blinding procedures, and it has suffi-
cient statistical power, these alternative explanations are unlikely to unduly influence
the estimated measure of intervention effect. Even if we can infer a causal relationship
between exposure to the intervention and frequency of outcome, additional factors
such as adverse effects, delivery, cost and acceptability of the intervention all need to
be evaluated before an intervention is considered for implementation.
Activity 10.1
In The Gambia, infants aged 6–51 weeks who presented to a government vaccination
post were screened for eligibility and written parental consent obtained for inclusion
in an intervention study. Some 17,437 children were randomly allocated to receive
three doses of either pneumococcal vaccine or a placebo with intervals of at least
25 days between doses (Cutts et al. 2005). They were subsequently monitored for
pneumonia over 24 months through attendance at the local health facilities and
hospital.An independent contractor had labelled vaccine and placebo vials with code
numbers using a blocked design and unique study identity numbers. These numbers
were subsequently used on health cards, and after the third vaccination had been
received, there was no record of the randomization code on the health card.
1 What type of study is this? Be as specific as you can.
2 The results presented included only those children who received the first dose when
aged 40–364 days with at least 25 days’ interval between doses.What type of analysis
is this and which children might have been excluded from the analysis?
3 The incidence rate for first episode of radiological pneumonia was 26.0 per 1,000
child years in infants who received the vaccine and 40.9 in infants who received the
placebo. Calculate and name an appropriate measure of effect, showing details of
your calculations, and interpret your result.
4 The investigators state:‘Efficacy did not vary by age ...’.Given the information presented
inTable 10.1, do you agree with their interpretation? Give reasons for your answer.
Table 10.1 Vaccine efficacy against first episode of
invasive pneumococcal disease
Age (months) %Vaccine efficacy (95% CI)
3–11 93 (54, 100)
12–23 75 (32, 93)
24–29 26 (–339, 89)
Source: Cutts et al. (2005).
Activity 10.2
A (fictitious) study was carried out on the maternity ward of ten hospitals to test the
effect of oral versus intramuscular vitamin K to reduce clinical bleeding in newborns.
After obtaining informed parental consent, children born on odd-numbered days
received doses of 2.0 mg oral vitamin K on days 1 and 3 after birth. Children born on
23346.indb 12923346.indb 129 22/08/2011 15:1222/08/2011 15:12

even-numbered days constituted the control group and received 1.0 mg of intramuscu-
lar vitamin K the day after birth according to existing practice.All infants were followed
up to assess spontaneous bleeding on days 1–7 after birth.
1 What type of study is this? Be as specific as you can.
2 Discuss the potential limitations of this design and ways in which it might be
improved.
Activity 10.3
A multi-centre double-blind randomized placebo-controlled trial in 274 hospitals
across 40 countries was undertaken to assess whether early administration of tran-
examic acid to 20,211 adult trauma patients with haemorrhage could reduce the risk
of death in hospital within 4 weeks of injury.Data were analysed by time from injury to
treatment, and found that the relative risk of death due to bleeding was 0.68 (95%
confidence interval (CI): 0.57, 0.82) if treatment occurred within 1 hour, 0.79 (95% CI:
0.64, 0.97) if treatment occurred within 1–3 hours, and 1.44 (95% CI: 1.12, 1.84) if
treatment occurred three or more hours after trauma (Roberts et al. 2011).
1 Interpret these results referring to the study design used, and give your recommen-
dations for the use of tranexamic acid based on these data.
2 In some cases,the injury was not witnessed and the time interval between injury and
treatment was estimated. How might this have affected the results?
Activity 10.4
Intermittent preventive treatment for malaria in infants (IPTi) is a single curative dose
of an anti-malarial drug given to infants at routine vaccination clinic contacts regardless
of symptoms or malaria infection.A study randomly selected 12 out of 24 sub-districts
in ruralTanzania to introduce IPTi through the existing health infrastructure (Armstrong
Schellenberg et al. 2010).
A representative sample of 600 infants surveyed a year later using rapid diagnostic
tests (dipsticks) found 31% infected with malaria in the intervention sub-districts and
38% in the comparison sub-districts (P = 0.06).A comparison of only those infants who
had received IPTi and/or routine vaccination 2–6 weeks prior to the survey found 22%
malaria infection in the intervention sub-districts compared with 41% in the compari-
son sub-districts (P = 0.01).
1 What type of study design is this? Be as specific as you can.
2 Identify the two approaches to analysis that were undertaken and describe their
results.What does a comparison of these results imply about implementation of IPTi?
Conclusion
intervention studies.The experimental nature of this type of study raises many ethical
concerns that subsequently drive the specific choice of study design. Intervention
23346.indb 13023346.indb 130 22/08/2011 15:1222/08/2011 15:12

studies are generally more complex and costly than other study designs. However,
intervention studies are less likely to suffer from bias and confounding, and are usually
the design of choice for producing relevant public health evidence.
References
Altman DG and Bland JM (2005) Treatment allocation by minimisation. British Medical Journal 330: 843.
Armstrong Schellenberg JR, Shirima K, Maokola W, et al. (2010) Community effectiveness of intermittent
preventive treatment for infants (IPTi) in rural southernTanzania.American Journal ofTropical Medicine
and Hygiene 82: 772–81.
Brown CA and Lilford RJ (2006)The stepped wedge trial design:a systematic review.BMC Medical Research
Methodology 6: 54.
Cutts FT, Zaman SM, Enwere G, et al. (2005) Efficacy of nine-valent pneumococcal conjugate vaccine
against pneumonia and invasive pneumococcal disease in The Gambia: randomised, double-blind,
placebo-controlled trial. Lancet 365: 1139–46.
Hayes RJ and Moulton LH (2009) Cluster RandomisedTrials. Boca Raton, FL: Chapman and Hall/CRC Press.
Roberts I, Shakur H, Afolabi A, et al. (2011) The importance of early treatment with tranexamic acid in
bleeding trauma patients: an exploratory analysis of the CRASH-2 randomised controlled trial.
Lancet 377: 1096–101, 1101–12.
The Gambia Hepatitis Study Group (1987) The Gambia Hepatitis Intervention Study. Cancer Research 47:
5782–7.
Victora CG,Habicht JP and Bryce J (2004) Evidence-based public health:moving beyond randomized trials.
American Journal of Public Health 94: 400–5.
Activity 10.1
1 This is a double-blind, randomized placebo-controlled trial of pneumococcal vaccine
in infants in The Gambia.‘Double-blind’ because allocation codes and unique identi-
fiers were used so that neither the parents of the infants nor the health personnel
assessing the outcomes were aware of the allocation. ‘Randomized’ because there
was an equal chance of any infant being in either study arm. ‘Placebo-controlled’
because the infants in the comparison group received an identical vaccine that had
no active properties against any outcome.
2 This is a per-protocol analysis as it includes only those who received the intervention
as it was originally intended.This analysis would exclude children who were less than
6 weeks or greater than 52 weeks (1 year) old when they received the first dose,
those who had less than 25 days between either the first and second or second and
third doses, those who did not receive all three doses, and those who may have
received the vaccine instead of the placebo or the placebo instead of the vaccine at
any of the three doses.Those who withdrew or died during the study after receiving
all doses would still be able to contribute person-time at risk for the period that they
were in the study, and would not be excluded from a per-protocol analysis.
3 As this is an intervention study, the appropriate measure of effect would be the
vaccine efficacy, which is calculated as 1 – relative risk.As the reported frequency of
the outcome is an incidence rate, the appropriate measure of relative risk is the
incidence rate ratio (IRR):
23346.indb 13123346.indb 131 22/08/2011 15:1222/08/2011 15:12

IRR =
Incidence rate in infants receiving vaccine
=
26.0
= 0.6357
Incidence rate in infants receiving placebo 40.9
The vaccine efficacy is calculated as 1 – 0.6357 = 0.3643 or 36%.A vaccine efficacy
of 36% means that 36% of episodes of radiological pneumonia in young children in
The Gambia can be prevented by vaccination with three doses of the pneumococcal
vaccine.
4 You may have stated that you disagree with the authors’ interpretation because the
estimates of vaccine efficacy are clearly different for each age group. The efficacy
appears to decrease substantially with age, and vaccine efficacy is no longer signifi-
cant in 24–29-month-old children as the 95% confidence interval includes zero.
However, this is an incomplete interpretation of the results.
The authors’ statement is in fact correct.The 95% confidence intervals are rela-
tively wide and overlap between all age groups. This tells us that the estimates of
vaccine efficacy are not significantly different between the age groups using a 5%
probability cut-off.The difference in the point estimates of vaccine efficacy are likely
to be due to a reduced statistical power to detect an effect in older age groups
where the sample size may have been too small or the underlying incidence of inva-
sive pneumococcal disease may have been lower.
Activity 10.2
1 This is a multi-centre, open-label (non-blinded), systematically randomized-controlled
trial.‘Multi-centre’ because subjects were recruited and followed up in several study
sites (hospitals).‘Open-label’ because the parents of the infants and those administer-
ing the intervention will be aware of whether the infant receives an injection or an
oral supplement. It is also likely a clinician recording the outcome would be aware of
the child’s date of birth and could therefore determine the allocation group.
‘Systematically randomized’ because the intervention allocation depends on the day a
child was born and is not totally random, neither is it non-random, because there is
usually no choice (either from the parents or the investigators) about the day a child
is born unless it is a scheduled caesarean delivery. ‘Controlled’ because there is a
comparison group that receives the existing intervention (not a placebo intervention).
2 You may have identified the following potential limitations:
(a) ‘Open-label’:The study is not blinded,so that parents of infants and those admin-
istering the intervention are aware of which intervention is received by a par-
ticular infant. Even the person recording bleeding events may be aware of the
allocation as they will observe the child’s date of birth on the medical charts.
Knowledge of the intervention allocation may affect a parent’s report of adverse
events, or a clinician’s diagnosis of outcome. It would not be justifiable to use a
placebo injectable on a newborn, and even if a placebo oral supplement were
used, it would not be ethical to withdraw the existing injectable intervention
from the control arm participants.Therefore,the study outcomes would need to
be very clearly defined (e.g. amount of bleeding) to reduce subjectivity and
potential information bias.
(b) ‘Systematic allocation’:The allocation is systematic so that, even if a placebo had
been used, investigators could determine the intervention allocation from the
child’s date of birth. However, children born on odd- or even-numbered days are
unlikely to differ in any way and the two groups should still be sufficiently similar
to control for any confounding factors. Given that the study is open-label,
systematic allocation of the intervention is unlikely to result in any further bias.
23346.indb 13223346.indb 132 22/08/2011 15:1222/08/2011 15:12

(c) As this is an intervention in newborn children,there may be a high proportion of
parents refusing to participate in the study.Alternatively, if injectable vitamin K is
routinely given without the need for parental consent, parents may prefer to
participate in the study to have a 50% chance of the less invasive oral interven-
tion instead.If parents providing informed consent to participate in the trial differ
from those who do not,this may affect our ability to extrapolate these results to
the general population.
Activity 10.3
1 The protective efficacy of tranexamic acid given within one hour of injury is 1 – 0.68 =
0.32,between 1–3 hours is 1 – 0.79 = 0.21 and after three hours or more is 1 – 1.44 =
–0.44.This means treatment with tranexamic can reduce the risk of deaths due to bleed-
ing by 32% if given within one hour of injury, by 21% if given within 1–3 hours of injury
and will increase the risk of death by 44% if given more than three hours after injury.
The 95% confidence intervals for all three relative risks do not include one, mean-
ing that these estimates are significant at the 5% level. Given the size of the study, it
is unlikely that these results could be due to chance.The trial was randomized, so it
is unlikely that these results could be explained by confounding factors that varied
between the study arms.As this was a double-blind trial, there is unlikely to be any
information bias that would affect these estimates.
Given the strength of evidence, the recommendation would be that tranexamic
acid should be given as early as possible to bleeding trauma patients. However, tran-
examic acid may be harmful for those admitted late after injury (Roberts et al. 2011).
2 If there were inaccuracies in estimating the time between injury and treatment, this
would have led to misclassification of some individuals into the incorrect category of
time to treatment. However, this should not have varied between study arms as the
intervention allocation was randomized and blind.Any inaccuracies would therefore
have led to non-differential misclassification of time-to-treatment, which may have
diluted the association between intervention and outcome, underestimating the
relative risks for each category.
Activity 10.4
1 This is an open-label, cluster-randomized, controlled effectiveness study of intermit-
tent preventive treatment for malaria in infants.‘Open-label (non-blinded)’ because
there was no placebo intervention and both the communities involved and the study
investigators determining the prevalence would have been aware of the intervention
allocation (Note,if malaria infection had been determined by microscopy,it may have
been possible to ‘blind’ the microscopist to the intervention allocation, however, the
use of rapid diagnostic tests meant that infection status was determined in situ and
investigators would have been aware of the sub-district allocation.)‘Cluster’ because
the units of randomization are sub-districts.‘Randomized’ because the sub-districts
were randomly selected to receive IPTi or not. ‘Controlled’ because there was a
contemporary comparison arm of sub-districts that did not receive the intervention
of interest.‘Effectiveness’ because the intervention was delivered through the rou-
tine health system and not as part of a rigorous trial.
2 The first result of prevalence among infants in intervention compared with non-
intervention sub-districts is an intention-to-treat analysis, where all infants were
included according to whether the intervention was available in their sub-district,
23346.indb 13323346.indb 133 22/08/2011 15:1222/08/2011 15:12

and regardless of whether they had received it.The prevalence ratio of malaria infec-
tion for those receiving IPTi was 0.31 ÷ 0.38 = 0.815 meaning that those in the IPTi
communities had a 19% (1 – 0.815 = 0.185) lower likelihood of being infected than
those in the control communities.A P-value of 0.06 means that,given the sample size
and underlying prevalence, there is a 6% probability that this difference in prevalence
might have been detected by chance if it was not real.
The second result was a per-protocol analysis, including only those infants who had
actually received the intervention (or attended for routine vaccination in the control
arm).The prevalence ratio was 0.22 ÷ 0.41 = 0.537 meaning that those in the IPTi
communities had a 46% (1 – 0.537 = 0.463) lower likelihood of being infected than
those in the control communities.This result showed a statistically signiﬁcant reduc-
tion (P = 0.01) in malaria prevalence in those infants who had recently received the
intervention compared to those who had not.
The difference between the intention-to-treat and per-protocol results suggests
that while the efﬁcacy of IPTi was good in this setting, its effectiveness was not.These
results suggest that, in this setting, the delivery of the intervention would need to be
improved for it to have an important effect.
23346.indb 13423346.indb 134 22/08/2011 15:1222/08/2011 15:12

SECTION 3
Epidemiology in
public health
23346.indb 13523346.indb 135 22/08/2011 15:1222/08/2011 15:12

23346.indb 13623346.indb 136 22/08/2011 15:1222/08/2011 15:12

Overview
In the previous chapters you learned how to measure epidemiological associations
between an exposure and outcome, and to estimate the impact of a risk factor. In this
chapter we consider how to apply such evidence to different approaches to preventive
intervention.You will be introduced to the concepts of primary,secondary and tertiary
prevention, and how the shape of the relationship between exposure and outcome
influences whether to use a population or high-risk approach to targeting prevention.
Screening is a key tool for prevention programmes and you will learn about the meas-
ures of sensitivity and specificity used to assess validity of a screening method and
predictive values used to assess its utility at an individual level. We assess the main
criteria necessary to evaluate whether a screening programme should be implemented.
Learning objectives
• define strategies in terms of primary, secondary and tertiary prevention
• recognize the importance of different dose–response relationships for prevention
• calculate measures of sensitivity, specificity and predictive values of a screening
method
• explain the relationship between prevalence and predictive values
• list criteria for assessing the appropriateness of a screening programme
• distinguish between population and high-risk targeting, and identify the most
appropriate prevention strategy for a given situation.
Prevention strategies
In previous chapters you learned about conducting rigorous epidemiological research
studies, and how to evaluate epidemiological results.When there is satisfactory evi-
dence that modification of an exposure can affect the frequency of an outcome, such
data can be used to promote good health and prevent or reduce adverse outcomes.
There are three main opportunities for preventive intervention relating to the natural
development stages of an outcome (see Figure 11.1).
Primary prevention aims to stop an outcome developing, either by preventing or
reducing exposure to a risk factor (e.g.vaccination against an infectious disease).When
provided with information on risks,individuals can choose to modify behaviour,such as
decreasing their weekly alcohol intake.At a population level, this may require societal
changes in attitude or even legislation. For example, in Europe, health education
11Prevention strategies
23346.indb 13723346.indb 137 22/08/2011 15:1222/08/2011 15:12

138 Epidemiology in public health
campaigns were used to discourage the uptake and continued use of tobacco, then
regulation of advertising and increased taxation of tobacco products was introduced,
and ﬁnally laws prohibiting smoking in public places to reduce passive smoking (expo-
sure to second-hand tobacco smoke).
Secondary prevention aims to interrupt progression from early to mid-stage of
the outcome, mainly by early detection and prompt treatment. An individual may be
unaware of having acquired an outcome because they have no symptoms or have not
noticed the effects. Knowledge of the natural history of an outcome can help develop-
ment of screening methods to detect the outcome early – this is a major component
of secondary prevention. For example, childhood lead poisoning from house paint or
industrial sites can cause seizures, coma and death. In the USA, blood lead screening
identiﬁes children at risk while they still have low blood lead levels.
Once the outcome is established and symptomatic, tertiary prevention aims to
reduce complications or severity by offering appropriate treatments and interventions.
For example, renal disease and glaucoma, both complications of uncontrolled diabetes,
may be prevented in the diabetic patient if blood glucose levels are successfully regu-
lated through the use of insulin and/or dietary restrictions.
For an outcome such as skin cancer, primary prevention might consist of health
promotion campaigns to encourage people to reduce their exposure to the sun
(e.g.using sun protection creams and protective clothing).Secondary prevention would
focus on detecting and removing skin cancer lesions as soon as they occur to prevent
development of invasive melanoma, sentinel lymph node biopsy to assess whether
the cancer has spread, and regular check-ups to monitor recurrence.Tertiary preven-
tion would include removal of any affected lymph nodes to prevent further cancer
spread, and chemotherapy or radiotherapy to improve prognosis if the cancer has
already spread.
Figure 11.1 General outcome process illustrating the three levels at which intervention for prevention
can act
23346.indb 13823346.indb 138 22/08/2011 15:1222/08/2011 15:12

Prevention strategies 139
Dose–response proﬁles
Prevention strategies may focus on those considered to be at highest risk of an outcome,
or they may apply the intervention to the whole population. It does not make sense to
target interventions at those who are not ‘at risk’. In this chapter, the term ‘population’
refers to those generally at risk, as distinct from those at highest risk of an outcome.
To decide which approach is most appropriate we need to understand how the
exposure relates to the outcome. Doctors typically classify people as being ‘well’ or
‘unwell’, as this helps decision-making about whether or not to admit a patient, pre-
scribe a drug, or perform an operation. However, this approach provides little recogni-
tion of the disease process and how it manifests in populations. For many outcomes
there is a range of poor health that may be related to a range of exposures to a risk
factor.This is known as the ‘dose–response’ relationship, i.e. how the risk of outcome
varies with changes in the measure of exposure (see Figure 11.2). For example, body
mass index (or BMI, i.e. weight in kilogrammes divided by the square of height in
metres) may result in poor health outcomes for those at very low levels or very high
levels. Promoting an intervention to reduce BMI in the whole population could there-
fore negatively affect individuals with an already low BMI.
Figure 11.2 Schematic models of four different relationships between exposure to a risk factor and risk
of outcome
Source: adapted from Rose (1992).
Alcohol and heart disease is another example. High alcohol intake may increase the
risk of heart disease and other health problems (e.g. violence, road trafﬁc accidents,
etc.). However, there is some evidence to suggest that modest alcohol intake may have
a protective effect on the risk of heart disease. It is therefore desirable to encourage
23346.indb 13923346.indb 139 22/08/2011 15:1222/08/2011 15:12

people to reduce their alcohol intakes, but perhaps undesirable to encourage them to
take no alcohol. In such cases, health promotion messages to the whole population
need to be more sophisticated and complex, which may make it more difficult to
appropriately inform people and encourage healthy behaviour.
The shape of the dose–response profile therefore has an important influence on
our choice of prevention strategy. In Activity 11.1, you will look more closely at
different dose–response profiles and consider their implications for prevention
strategies.
Activity 11.1
1 Figure 11.2 provides four simplified ‘dose–response’ graphs. For each graph, briefly
describe the relationship between exposure and outcome and the implications for
the prevention strategy.
Screening
As you saw from Activity 11.1, it may be appropriate to target those at highest risk of
an adverse outcome when the dose–response curve is not constant. Methods to
identify individuals at greater risk of an outcome include physical examination, blood
test, X-ray, and biopsy. Screening aims to identify small numbers of individuals at
high risk of an outcome, whereas diagnosis is used to confirm outcome.The use of
screening assumes that effective interventions are available to reduce risk, or to
effectively treat an outcome that is detected sufficiently early. For example, screening
individuals for high blood cholesterol levels aims to identify those at higher risk of
coronary heart disease for targeted health promotion or cholesterol-lowering drug
treatment. Screening may also be used for other purposes, including selection of
people fit enough for a job, or containment of infection (e.g. screening new nurses or
teachers for tuberculosis or food handlers for salmonella).
Screening can either include the whole population (mass screening) or selected
groups who are expected to have a higher risk of exposure or outcome (targeted
screening). A survey to measure the blood cholesterol of all adults in a population
would be an example of mass screening. Targeted screening might only measure
blood cholesterol in the relatives of people with familial hypercholesterolaemia (a high
cholesterol genetic disorder).
Opportunistic screening may occur when a patient visits a healthcare provider and is
offered screening unrelated to the reason for their visit.For example,a general medical
practitioner may habitually take and record patients’ blood pressure at the start of
every consultation, or may offer all sexually active patients under 25 years of age a test
for Chlamydia infection.
Systematic screening refers to an organized health programme (e.g. all women in the
UK aged 25–64 are reminded to attend for a Papanicolaou cervical smear test every
three years).
A screening method should ideally be inexpensive, easy to administer, and impose
minimal discomfort on those to whom it is administered, given that a large proportion
of those screened may not be at risk of adverse outcome. More importantly, the
screening method (e.g. ultrasound scan, laboratory test, clinical definition) must cor-
rectly identify those at risk.
23346.indb 14023346.indb 140 22/08/2011 15:1222/08/2011 15:12

Sensitivity and specificity
The validity of a screening method is its ability to correctly distinguish between indi-
viduals with and without the condition of interest (i.e. risk factor, precursor, outcome).
The validity of a screening method (or diagnostic test) is evaluated by calculating its
sensitivity and specificity.An ideal screening method would have a high sensitivity
and high specificity.
Table 11.1 Standard cross-tabulation (2 × 2 table) of true
condition by screening/diagnostic result
True condition
Present Absent Total
Positive a b a + b
Negative c d c + d
Total a + c b + d a + b + c + d
Screening
Result
InTable 11.1 we compare the distribution of screening method results in relation to
the true condition of an individual:
• a represents the ‘true positives’ (i.e. the number who have the condition and have a
positive result using the screening method);
• b represents the ‘false positives’ (i.e. the number of individuals who do not have the
condition but have a positive result using the screening method);
• c represents the ‘false negatives’ (i.e. the number of individuals who have the condi-
tion but have a negative result using the screening method);
• d represents the ‘true negatives’ (i.e. the number of individuals who do not have the
condition and have a negative result using the screening method).
The true condition of an individual may be determined either by a ‘gold standard’
diagnostic test (i.e. providing a definitive diagnosis), using the best existing alternative
screening method,or by follow-up to assess final outcome.Where the screening method
provides a continuous variable (e.g. blood glucose levels for diabetes), this must be cat-
egorized into a binomial variable using a defined cut-off based on previous evidence.
Sensitivity is the proportion of those who truly have the condition who are cor-
rectly identified (‘true positives’). Referring to the notation in Table 11.1, sensitivity is
calculated as:
Sensitivity =
Number of true positives
=
a
Total number with the condition a + c
Specificity is defined as the proportion of those who truly do not have the condition
who are correctly identified (‘true negatives’). Using the notation inTable 11.1, specifi-
city is calculated as:
Specificity =
Number of true negatives
=
d
Total number without the condition b + d
23346.indb 14123346.indb 141 22/08/2011 15:1222/08/2011 15:12

The sensitivity and specificity values for a given method are usually not equal, and the
relative importance of each depends on the outcome of interest. A low sensitivity
means that the screening method results in many ‘false negatives’ (i.e. it would identify
many people with the condition, as not having the condition).A low specificity means
that the screening method results in many ‘false positives’ (i.e. it would identify many
people without the condition as having the condition).
Higher sensitivity may be preferred for infectious disease control, to reduce the
number of false negatives that could result in continued transmission of the disease.
Higher specificity may be preferred for a screening programme where the subsequent
diagnostic test for an outcome is very expensive or carries health risks, to avoid per-
forming unnecessary procedures on many false positives.
Predictive values
From the individual’s perspective, it is more useful to know the ‘predictive value’ of a
screening method.The positive predictive value (PPV) is the likelihood of outcome
based on the result, while the negative predictive value (NPV) is the likelihood of
no outcome based on the result. For example, the PPV of mammography will tell a
woman how likely it is that she truly has breast cancer if she has a positive mammo-
gram, while the NPV will tell her how likely it is that she truly does not have breast
cancer if she has a negative mammogram. Using the notation in Table 11.1, these are
calculated as:
Positive predictive value =
Number of true positives
=
a
Number tested positive a + b
Negative predictive value =
Number of true negatives
=
d
Number tested negative c + d
Predictive values are determined by the sensitivity and specificity of the
screening method. The higher the sensitivity, the less likely it is that an individual
with a negative result will have the condition, so the greater the NPV of the
method. The higher the specificity, the less likely it is that an individual with a
positive result will actually not have the outcome, so the greater the PPV of the
method.
Predictive values are also determined by the prevalence of the condition
being screened for. Why? Remember that prevalence is calculated as the number
of individuals who have the outcome, divided by the total number of individuals
sampled. Consider that Table 11.1 has the same format as Table 3.1 (see Chapter 3),
and think of the ‘true condition’ as the ‘outcome’ and the ‘screening method result’
as the ‘exposure’. If you compare the formula for prevalence (Chapter 3) with
those for PPV and NPV, you will see it effectively calculates the prevalence of
the true condition among those ‘exposed’ and ‘unexposed’ to a positive result
respectively.
Note, that the sensitivity and specificity of a screening method are independent
of the prevalence of the condition in the population being screened.This is because
sensitivity only relates to those who truly have the condition, while specificity
only relates to those who truly do not have the condition.Therefore, in contrast to
predictive values, neither measure considers the frequency (prevalence) of the true
condition.
23346.indb 14223346.indb 142 22/08/2011 15:1222/08/2011 15:12

Ethical issues
In addition to assessing the validity of a screening method, the ethical consequences of
screening must be evaluated.The risks of screening can be considered at both individ-
ual and population levels.An unwell person seeking medical help is willing to undergo
a medical examination and associated tests in the hope of receiving a definitive diagno-
sis and appropriate treatment. However, a screening test is a preventive intervention
applied to outwardly healthy individuals with no symptoms of the outcome.
It is therefore essential that the benefits of participating in screening outweigh the
risks.It is an ethical responsibility to provide enough information for individuals to make
an informed decision about whether or not to participate.While many screening meth-
ods present no risk, others have the potential to harm the participant (e.g. repeated
exposure to X-ray radiation in mammography for breast cancer, or increased risk of
miscarriage following an amniocentesis test to identify Down’s syndrome pregnancies).
All screening methods will result in false negatives and false positives, either through
low sensitivity or specificity, or because of human error. A false positive result can
cause unnecessary anxiety while a false negative result can lead to a loss of confidence
in medical intervention or a potential loss of life. An individual with a false negative
result is provided with a false sense of security and may fail to recognize subsequent
symptoms, resulting in poorer outcomes. Even a true positive result may increase anx-
iety, posing a risk to mental health or quality of life, while health and life insurance
premiums may also increase.
Before introducing a national screening policy, any additional resource requirements
must be planned for. Good quality control is essential to ensure correct functioning of
a screening programme.Any variation in standards and criteria used to indicate further
intervention may result in poor compliance,reducing the proportion of the population
likely to benefit. Specialist equipment may be required. Staff may require additional
training. Pre- and post-test counselling may be necessary.The incidence of the condi-
tion must be estimated to plan for the numbers requiring screening and the subse-
quent proportion needing further diagnostic tests or expensive treatments. It is
unethical to screen if there will be insufficient facilities or effective treatments for
those who need them.
Criteria for screening
The World Health Organization developed criteria for assessing the appropriateness
of screening in 1968 (Wilson and Jungner 1968) that continue to be used today
(see Table 11.2). Some of these criteria are context-specific and may differ from the
point of view of the individual or community.
Using these criteria, we can evaluate whether or not to implement a screening pro-
gramme.The three main themes to consider are: (1) relative burden of the condition;
(2) feasibility of organizing a screening programme; and (3) potential effectiveness of a
programme.An outcome that is rare but very serious and easily preventable may be
worth screening for. For example, Phenylketonuria, a congenitally acquired inability to
metabolize the amino acid phenylalanine, is a rare disease. If undetected, it leads to
serious mental retardation.A highly sensitive and specific screening test, performed on
a blood sample taken from a prick in the heel of a newborn, can identify babies who
have this condition.A diet low in phenylalanine can then effectively prevent develop-
ment of mental retardation in these children.
23346.indb 14323346.indb 143 22/08/2011 15:1222/08/2011 15:12

The relative burden of the condition compared with other health problems should
justify the expense of a screening programme in relation to the resources available.
However wealthy a society is, there will always be finite resources available for health-
care.The resource costs of a screening programme need to be balanced with the cost-
savings of treating fewer patients identified at a later stage with an advanced outcome.
The feasibility of organizing a screening programme will depend on:
1 systems for identifying and contacting individuals (e.g. general practioner’s lists,
mother and child health clinics, schools);
2 compliance levels (e.g. colonoscopy to detect colon cancer is invasive, uncomfort-
able and may not be acceptable to sufficient individuals);
3 whether facilities are in place for more extensive diagnostic tests if needed (e.g. a
mammography campaign will result in a greater than usual referral for breast biopsies);
4 availability of resources for increased treatment (e.g. screening for cholesterol will
result in increased demand for cholesterol-lowering drugs).
Measuring effectiveness
The potential effectiveness of a programme to reduce the frequency of a condition is
hard to measure and often subject to various biases. Selection bias occurs because
those who participate in screening programmes often differ from those who do not.
Women who are at high risk of breast cancer because of family history may be more
likely to attend for mammography. By contrast, women at low risk of cervical cancer
appear to be more likely to accept an invitation for a cervical smear test.
Lead-time bias can occur when screening identifies an outcome earlier than it
would otherwise have been identified, but has no effect on the outcome. For example,
a disease that would otherwise be diagnosed at 60 years when symptoms arise might
be detected by screeningTest A at 55 years and byTest B at 50 years (see Figure 11.3).
Even without medical intervention, it may appear that Test A prolongs survival for five
years and Test B for ten years, whereas this is a consequence of earlier detection.This
effect must be considered when evaluating the results of a screening method, by using
outcome measures other than survival time.
Table 11.2 List of ten WHO criteria for assessing the appropriateness of screening
Focus Criterion
Condition: The condition being screened for should be an important health problem
The natural history of the condition should be well understood
There should be a recognizable latent or early stage
Method: There should be a suitable method for detection
The screening method should be acceptable to the population
Treatment: There should be an accepted treatment for those with the condition
Programme: There should be an agreed policy on who to treat
Facilities for diagnosis and treatment should be available
The costs of detection should be balanced in relation to overall healthcare spending
Screening should be ongoing and not one-off
Source: Ilona Carneiro, using data from Wilson and Jungner (1968).
23346.indb 14423346.indb 144 22/08/2011 15:1222/08/2011 15:12

Length-time bias can occur for outcomes that take longer to develop to a stage
where they threaten health (i.e. longer asymptomatic period). For example, slower-
growing breast cancer tumours are more likely to be detected by screening prior to
the development of symptoms than faster-growing tumours. However, slower-growing
tumours may also be less aggressive and associated with a better prognosis,leading to
an over-estimate of the screening success. Consider a population of 100 people with
cancer: 20 have slower-growing tumours and all are detected by screening, 80 have
faster-growing tumours only half (40) of which are detected by screening before they
develop symptoms.If all of the slower-growing tumours and none of the faster-growing
tumours respond to subsequent treatment, we would calculate the success of screen-
ing as 20 ÷ (20 + 40) = 33%. However, the true success should be measured over all
those detected and un-detected by the screening, as 20 ÷ 100 = 20%.
It is difficult to identify appropriate study designs to evaluate screening programmes
because of these biases. Table 11.3 summarizes potential study designs and the key
biases that may arise.
Figure 11.3 Lead-time bias effect for a disease with onset at 50 years and death at 65 years
Source: Ilona Carneiro, modified from Bailey et al. (2005).
Table 11.3 Comparison of methods and biases of study designs for evaluating screening methods
Study type Method Potential biases
Cohort Compares time to adverse outcome in screen-
detected and non-screen-detected cases
Lead-time bias
Length-time bias
Case control Compares screening history of cases with age-
matched controls
Selection bias
Information bias
Non-randomized
trial
Compares outcome using a historical or
neighbourhood comparison group
Selection bias
Randomized-controlled
trial
Compares outcome between individuals randomly
allocated to screening or control groups
Information bias
Misclassification bias
Source: Ilona Carneiro, adapted from Bailey et al. (2005).
A randomized-controlled trial (RCT) is the best method for evaluation (see Chapter
10), as the effects of lead-time, length-time and selection biases are balanced by random
allocation. However, it may not be appropriate to use an RCT for screening if the
screening method has already been introduced into a population or if the population
23346.indb 14523346.indb 145 22/08/2011 15:1222/08/2011 15:12

perceives the screening as beneficial (even if unproven). It is unethical to undertake a
‘blind’ trial where participants receive placebo screening, as those given a false-negative
result from placebo-screening may be less likely to notice symptom development and
delay treatment-seeking. If those responsible for subsequent patient care are aware of
the trial and subject allocation, this may affect their knowledge, recognition of subse-
quent symptoms, and attribution of cause in the case of death (observer bias).There may
be a risk of ‘contamination’ if awareness of a screening programme leads subjects in the
control (non-screened) group to seek-out screening, which may lead to differential mis-
classification of exposure to screening.As many of the conditions that would be screened
for are relatively rare,large sample sizes would be necessary to detect a significant effect.
Activity 11.2
In a hypothetical study, 1,000 patients attending a hospital general outpatient depart-
ment were tested for diabetes using the following two tests:
• fasting blood sugar (FBS)
• glucose tolerance test (GTT).
The 100 patients with a positive GTT were classified as true cases of diabetes. Of 140
patients with an FBS of at least 6 mmol/l (the cut-off point to distinguish people who
have diabetes from those who do not),only 98 were true cases of diabetes (i.e.only 98
also had a positive GTT).
1 What are the sensitivity, specificity, and positive and negative predictive values of the
FBS test in this study population?You may find it useful to create a 2×2 table of the
information given.
2 When the cut-off point for the FBS was raised to 7 mmol/l,the sensitivity of the test
decreased to 95% while specificity increased to 98%. Create a new 2×2 table using
this new cut-off and calculate:
(a) the positive predictive value of FBS in the study population;
(b) the proportion of diabetics given a false negative FBS result.
3 In a subsequent community survey to screen for diabetes, of 1,000 people
surveyed, 40 had a positive GTT and were classified as true cases of diabetes. Using
a cut-off value of 6 mmol/l the FBS had a sensitivity of 97.5% and specificity of 95%.
What is the positive predictive value of FBS in this survey and why is it different from
that observed in the hospital-based study?
4 If the FBS cut-off point is increased to 7.5 mmol/l, the sensitivity is 90% and the
specificity is 99% for diagnosing diabetes in the community.
If you were to fix the cut-off point of FBS for a survey in your community would you
select 6 mmol/l or 7.5 mmol/l? Give reasons for your answer.
Targeting high-risk individuals
When there are appropriate methods to identify individuals at high risk of an outcome
(e.g. screening), it may be tempting to target interventions at ‘high-risk’ individuals
rather than a whole community.This is a more of clinically oriented approach to pre-
vention.The focus on the individual is sometimes perceived as easier to promote since
23346.indb 14623346.indb 146 22/08/2011 15:1222/08/2011 15:12

the impact of high-risk exposure is more apparent to those at greatest risk, so they
may be more likely to comply and therefore benefit from an intervention. Another
benefit of the high-risk approach is that it fits with society’s perception of the role of
medical intervention (i.e. focusing on needy individuals, rather than aiming to change
the behaviour of the whole population to achieve general health gains).
The general population would be unlikely to consent to testing for sexually transmit-
ted infections (STIs) to stop an increasing incidence of STIs, expecting such screening
to be targeted at those who practice ‘risky’ sexual behaviours (e.g. multiple sexual
partners, unprotected sex). Similarly, it would not be cost-effective to provide routine
mammograms to women under 30 years of age, given that the main burden of breast
cancer is in women over 50 years of age and mammograms are costly.
However, when assessing whether an individual is in a high-risk group, definitions or
screening methods should be accurate. Labelling individuals as ‘high-risk’ can cause
unnecessary anxiety in healthy individuals and may even be stigmatizing.Criteria should
be standardized to prevent a blurring of categories (e.g. being slightly overweight can
merge with being more overweight which can merge with being labelled ‘obese’).
Another limitation of this approach is that it does not always seek to change the
circumstances that encourage exposure to a known risk factor (i.e.it does not address
the root-causes of risky exposures). For example, vaccination of people at risk of a
water-borne disease without efforts to improve the quality of the local water supply,
or the use of cholesterol-lowering drugs rather than improving diet, are temporary
solutions.This may also shift the burden of responsibility (and ‘guilt’) to high-risk indi-
viduals or groups, while failing to recognize the role of external influences such as
economics and advertising, which ultimately affect the wider population.
The high-risk approach may not be able to predict the individual impact of an inter-
vention as levels of risk and outcome will vary within risk groups.Therefore,individuals
are unable to make an informed decision about whether to comply. It may also be
argued that the targeted approach is exclusive, and that all individuals should have
access to interventions that improve general health. Finally, targeting high-risk groups
may be more expensive, often requiring mass screening to identify at-risk individuals.
The prevention paradox and the population approach
Another problem with targeting those at highest risk occurs when those individuals
are only a small proportion of the total population at risk.In such circumstances,a large
risk reduction among a few high-risk individuals may not have any population-level
impact on an outcome, while a slight risk reduction among many people may have a
large impact at the population level.This is known as the prevention paradox.
For example, a number of risk factors have been identified for heart attack (myocar-
dial infarction or MI), including smoking, raised blood pressure, high cholesterol and
psychosocial stress.The risk of MI increases with the number of risk factors to which
an individual is exposed. However, a prevention strategy that focused on those indi-
viduals with elevated risk factors (see Table 11.4), would reach just 15% of men of
whom only 9% would subsequently develop a MI (i.e.91% of those targeted would not
experience MI).Targeting individuals with elevated risk factors and signs of early heart
disease whose risk of MI is much greater (22%), would prevent just 11% of all MIs.
As 61% of MIs occur in men who are not at high-risk, primary prevention of MI
should be directed at the whole population. If a population-wide strategy was put into
place and all men over a certain age modified their behaviour slightly, the public health
23346.indb 14723346.indb 147 22/08/2011 15:1222/08/2011 15:12

benefit could be considerable.This illustrates the fact that targeting high-risk groups
may not be appropriate in a situation where a small risk affects a large proportion of
the population and will therefore generate a large number of cases.
The prevention paradox can be applied to individuals who modify their behaviour to
reduce exposure to known risk factors in the hope of avoiding an outcome.As most
outcomes are rare,many individuals who adopt a certain lifestyle or behaviour designed
to reduce their risk of adverse outcome will not benefit directly (because they would
never have developed the outcome),while a few individuals will benefit greatly (because
they would otherwise have developed the outcome).The greatest public benefit will
therefore often come from applying a preventive intervention to the whole population.
Rose (1992) argued that it is not only the extreme cases that require attention, but
also the much larger proportion of people with milder features of an outcome.In addi-
tion, individuals are not always simply exposed or not exposed to a risk factor, but may
be exposed to varying degrees.For a risk factor with a‘normal’ population distribution
(i.e. very few people are highly exposed, very few people are not exposed, and the
majority are somewhat exposed to the risk factor), it makes more sense to reduce
everyone’s exposure rather than targeting the very few at highest risk.
Choosing the appropriate approach
To decide whether to take an individual or population approach to preventive inter-
vention, we must consider the characteristics of the intervention. Some preventive
measures can only be implemented on a mass scale (e.g. fluoridation of water to pre-
vent tooth decay, environmental legislation to control air pollution). However, for out-
comes where the greatest burden is known to be concentrated among high-risk
individuals, it may be more appropriate to target high-risk groups rather than the
whole population, if we can adequately identify those at high risk.Alternatively, there
may be benefits to using both approaches together. For example, in HIV prevention,
health education messages on safer sex practices are aimed at the whole population,
while sex-workers and drug-users may be targeted for HIV-screening, and given
improved access to condoms and disposable needles respectively.
If we have sufficient information on the prevalence of risk factors and incidence of
outcome, we can calculate the population-attributable fraction for a risk factor (see
Chapter 3) and compare the proportion of cases that could be prevented by using
either the population or high-risk approach.The appropriate approach also depends on
whether the intervention will be implemented in the community, within hospitals or in
a primary healthcare setting.
Table 11.4 Distribution of myocardial infarction (MI) by high-risk group
Risk group Total
(% under study)
Developed MI
(% of sub-group)
Percentage of MI
cases (n = 403)
All men under study 8,147 (100) 245 (4) 61
Elevated risk factors 1,222 (15) 115 (9) 29
Elevated risk factors and evidence of early disease 199 (2) 43 (22) 11
Source: Ilona Carneiro, adapted from Heller et al. (1984) and Rose (1992).
23346.indb 14823346.indb 148 22/08/2011 15:1222/08/2011 15:12

Activity 11.3
Figure 11.4 contrasts population distributions of serum cholesterol in Japan and
Finland. Elevated serum cholesterol is a risk factor for coronary heart disease.
Figure 11.4 Population distribution of serum cholesterol levels in Japan and Finland
Source: Rose (1992).
1 Describe what Figure 11.4 shows.
2 List some potential explanations for the difference in serum cholesterol distribution
between these populations.
3 Would you choose a population or high-risk prevention strategy to reduce the
risk of coronary heart disease in the Finnish population? Give reasons for your
answer.
Activity 11.4
1 You are responsible for developing a public health strategy to reduce fatal injuries as
the result of road trafﬁc crashes. Describe at which level of prevention each of the
following interventions could be involved.
(a) Car seat-belt restraints.
(b) Driving speed limits.
(c) Paramedic pre-hospital care at the crash site.
23346.indb 14923346.indb 149 22/08/2011 15:1222/08/2011 15:12

Activity 11.5
1 Human papilloma virus (HPV) has been identified as a necessary cause of cervical
cancer, although it is not a sufficient cause and the majority of those infected do not
develop cervical cancer. A programme of routine vaccination of adolescent girls
against HPV is to be conducted in country X, where the prevalence of HPV among
women is 10% and the incidence of cervical cancer is 10 per 100,000 women per
year. Is this an example of the ‘prevention paradox’? Explain your answer.
Conclusion
In this chapter you have learned about different prevention strategies (primary,second-
ary, tertiary) relating to intervention stage and dose–response relationship.As screen-
ing is key in secondary prevention, you learned statistical methods for evaluating
screening methods (i.e. sensitivity, specificity, and predictive values) and evaluation of a
screening programme using WHO criteria. Public health approaches may be targeted
or general, depending on risk distribution, relative outcome burden in the population,
and intervention delivery method.While a population approach can be more effective
given the ‘prevention paradox’, a combination of both approaches is often most
powerful.
References
Bailey L, Vardulaki K, Langham J and Chandramohan D (2005) Introduction to Epidemiology. Maidenhead:
Open University Press.
Heller RF, Chinn S, Pedoe HD and Rose G (1984) How well can we predict coronary heart disease?
Findings in the United Kingdom Heart Disease Prevention Project.British Medical Journal (Clin Res Ed)
288: 1409–11.
Rose G (1992) The Strategy of Preventive Medicine. Oxford: Oxford University Press.
Wilson JM and JungnerYG (1968) Principles and Practice of Screening for Disease.Public Health Papers.Geneva:
World Health Organization.
Activity 11.1
1 Your answers should be similar to the following:
(a) Exposure increases without adverse outcome until a particular level is reached,
after which the risk of outcome increases rapidly. It would be most appropriate
to target preventive interventions to those at high risk of exposure.
For example, an increase in intra-ocular (inside the eye) pressure is not dan-
gerous until it exceeds certain levels.Above these levels the incidence of glau-
coma (damage to the optic nerve affecting vision and eventually leading to
blindness) rises rapidly. It is therefore desirable to keep intra-ocular pressure
under the threshold, but there is no benefit to be gained in further reducing it.
Note, however, that the definition of a threshold level beyond which adverse
effects appear is derived from population data.At an individual level, there may
23346.indb 15023346.indb 150 22/08/2011 15:1222/08/2011 15:12

be some people with adverse outcomes below the threshold, while others con-
tinue to be healthy despite being above the threshold.
(b) There is a linear relationship between the exposure and outcome.The greater
the exposure, the greater the risk, even at very low exposure levels. Shifting the
whole population exposure towards lower levels will bring beneficial effects and
is the most appropriate public health objective.
For example, there is an increased risk of lung cancer even with the small
amounts of tobacco smoke associated with passive smoking.There is no safe level
of exposure to tobacco smoke,but removing all exposure would be very difficult.
Health promotion activities and legislation at the population level are the best
way to achieve the large change in behaviour necessary to reduce population
exposure.
(c) The risk of outcome increases with exposure, but the slope is shallow at lower
exposure and increases more rapidly at higher exposures.If a large proportion of
the outcome is due to those at higher exposure, then it would be appropriate to
target preventive interventions to those at high risk. However, if the majority of
outcome is due to those at lower exposure (because few individuals have a high
exposure), then it would be more appropriate to shift the whole population
towards a reduced exposure.
This curved exposure to outcome relationship is usually a more accurate
description than the oversimplified linear relationship above. For example, in
osteoporosis, the bone mineral density (BMD) is reduced, resulting in fractures,
which can be prevented with appropriate medication. The risk of hip fracture
increases gradually with declining BMD until about 700–800 mg/cm2
below
which the risk increases more rapidly.The relative benefit of bone-density X-ray
scans depends on the distribution of BMD in the population, and this distribu-
tion shifts with age.The benefit of bone-density scans is greater in post-meno-
pausal women in whom the likelihood of low BMD is greater.
(d) This relationship is more complex, showing a wide range of exposure during
which there is no increased risk of outcome, with increased risk of outcome
at very low and very high exposure.This fits the common belief that ‘moderation
is good and extremes are bad’. For this dose–response pattern, there are
inherent problems in shifting the entire population too far in either direction,
and either a targeted approach or a complex intervention for the whole
population is required.
For example, for a given body size, there is a wide range of weight that carries
no increased risk of adverse outcome.At the extremes of low weight and high
weight, however, there may be associated health hazards.A policy that aims to
decrease body-weight for the entire population might inadvertently shift some
low weight people into the extremely underweight category associated with
increased mortality.The health promotion messages therefore need to be more
sophisticated and complex.
Activity 11.2
1 Your 2×2 table of FBS test by true diabetes (GTT test) should look like Table 11.5.
Explanation of rationale:
Of the total 1,000 patients tested,100 had a positive GTT (i.e.diabetic),therefore 1,000
– 100 = 900 had a negative GTT (i.e.not diabetic).Of the 1,000,140 had a positive FBS,
therefore 1,000 – 140 = 860 had a negative FBS.Of the 140 positive FBS,98 were also
23346.indb 15123346.indb 151 22/08/2011 15:1222/08/2011 15:12

positive for GTT (diabetic), therefore 140 – 98 = 42 were negative for GTT (not
diabetic).
The sensitivity of FBS is the number of true positives detected by the test, divided
by the total of number of diabetics (GTT positive): 98 ÷ 100 = 0.98 or 98%
The speciﬁcity of FBS is the number of true negatives detected by the test, divided
by the total number not diabetic (GTT negative): 858 ÷ 900 = 0.95 or 95%
The positive predictive value of FBS is the number of true positives divided by
the total detected positive by the test: 98 ÷ 140 = 0.70 or 70%
The negative predictive value of FBS is the number of true negatives divided by
the total detected negative by the test: 858 ÷ 860 = 0.998 or 99.8%
2 The new 2×2 table using the 7 mmol/l cut-off should look like Table 11.6.
Table 11.5 FBS test results (cut-off 6 mmol/l) by true diabetes
(GTT test) status
True diabetes (GTT)
Test results (FBS) Diabetic Not diabetic Total
Positive 98 42 140
Negative 2 858 860
Total 100 900 1,000
Table 11.6 FBS test results (cut-off 7 mmol/l) by true
diabetes (GTT test) status
True diabetes (GTT)
Positive 95 18 113
Negative 5 882 887
Total 100 900 1,000
We know that the number of diabetics was 100, and the number not diabetic was
900. If the sensitivity of the test decreased to 95%, this means that 0.95 × 100 = 95
of the diabetics (GTT positive) were diagnosed positive using the new FBS cut-off,
and the remaining 5 diabetics were diagnosed as negative by FBS. If the speciﬁcity
increased to 98%, it means that 0.98 × 900 = 882 of those not diabetic were diag-
nosed as negative using the new FBS cut-off, and 900 – 882 = 18 of those not dia-
betic were diagnosed as positive by FBS.
(a) The positive predictive value of FBS using the new cut-off is 95 ÷ 113 = 0.84
or 84%
(b) The proportion of false negatives with FBS is 5 ÷ 100 = 0.05 or 5%.
Alternatively, it can be calculated directly from knowledge of the sensitivity only
as: 1 – sensitivity = 1 – 0.95 = 0.05 or 5%.
23346.indb 15223346.indb 152 22/08/2011 15:1222/08/2011 15:12

If 40 were truly diabetic,then 1,000 – 40 = 960 were not diabetic using GTT.If FBS had
97.5% sensitivity, then 0.975 × 40 = 39 diabetics were detected as positive by the FBS
test,and 40 – 39 = 1 diabetic was detected as negative by FBS.If FBS had 95% specifi-
city,then 0.95 × 960 = 912 of those not diabetic were detected as negative by the FBS
test, and 960 – 912 = 48 of those not diabetic were detected as positive by FBS.
The positive predictive value of FBS is the number of true positives divided by the
total detected positive by the test: 39 ÷ 87 = 0.45 or 45%.
Although the sensitivity and specificity of the FBS using a cut-off 6 mmol/l were
almost the same in the hospital-based and community surveys, there is marked
reduction in the positive predictive value of FBS in the community survey.This is
because the prevalence of diabetes in the hospital population was higher (100 ÷
1,000 = 10%) than in the community (40 ÷ 1,000 = 4%).
4 You should have chosen 6 mmol/l as an appropriate cut-off point for FBS in the com-
munity,because the sensitivity is higher at 6 mmol/l (97.5%) than at 7.5 mmol/l (90%),
so that we detect a greater proportion of diabetics. It is better to have fewer false
negative results (2% vs. 10%), as there are effective treatments for diabetes that can
effectively prevent later complications so that timely intervention matters.
This is preferable to a higher specificity with fewer false positives, as the implica-
tions of false positives for an outcome such as diabetes are not very severe. The
physical and psychological stress following a false positive test for diabetes is minimal
since further diagnostic tests (e.g. GTT) are available to refute the diagnosis.
Activity 11.3
1 The Japanese distribution curve is taller with a narrow spread, and the majority of
samples around 150mg/100cc. This suggests that most of the Japanese population
presents with a lower level of cholesterol and that there is little variation.The Finnish
distribution curve is shorter with a wider spread,and the majority of samples around
250mg/100cc.This suggests that the Finnish population has a higher average serum
cholesterol level with more variation. While the two distributions do overlap, the
majority of the Finnish population have higher levels of cholesterol than the Japanese
population.
2 When there are major differences between populations, as shown in Figure 11.4, it
suggests that some community-level factor is determining the difference.There may
Table 11.7 FBS test results (cut-off 6 mmol/l) by true diabetes
(GTT test) status
True diabetes (GTT)
Positive 39 48 87
Negative 1 912 913
Total 40 960 1,000
3 As before, you should have started by setting up a 2×2 table as shown in Table 11.7.
23346.indb 15323346.indb 153 22/08/2011 15:1222/08/2011 15:12

be genetic, behavioural (e.g. diet), or environmental differences between the popula-
tions that may be addressed as part of any prevention strategy.
3 A population approach would be appropriate if the aim is to shift the whole Finnish
distribution curve towards lower cholesterol levels, making it more similar to the
Japanese distribution. A high-risk approach would be appropriate if the aim is to
reduce cholesterol levels only in those with extremely high values.
In deciding which approach would have a greater public health impact, you would
need to know the shape of the relationship between cholesterol level and risk of
coronary heart disease.
If there are behavioural or environmental differences, it may be possible to shift
the entire distribution in a healthier direction with a population-level prevention
strategy if appropriate policies are adopted. A moderate change by the whole
population might greatly reduce the number of people with the most extreme
cholesterol levels.Thus,while many individuals might each receive a small benefit,the
total benefit to the whole population may still be larger than with a targeted
approach.
Activity 11.4
The process of outcome development can be simply outlined as: (i) road traffic crash,
(ii) serious injury, (iii) death. The level of prevention for each intervention can be
explained as:
(a) Secondary prevention because car seat-belt restraints act to reduce injury in case
of a crash
(b) Primary prevention because driving speed limits aim to reduce road traffic crashes
from occurring
(c) Tertiary prevention because on-site medical care may reduce the risk of death from
serious injuries.
Activity 11.5
Yes, this is an example of the prevention paradox, as many women will receive the
intervention, but only a small proportion of these will benefit.We can estimate that
90% of those to be vaccinated would not have contracted HPV anyway, and the major-
ity of those who might have contracted HPV would not have then developed cervical
cancer.Therefore, at an individual level, the risk reduction is small. However, at a popu-
lation level, the risk reduction is great, as HPV is one of the leading causes of cancer
mortality.
23346.indb 15423346.indb 154 22/08/2011 15:1222/08/2011 15:12

Overview
In earlier chapters, you learned how to conduct epidemiological research studies and
how to interpret their results. In the previous chapter, you considered different
approaches to preventive interventions.In this chapter,you will be introduced to public
health surveillance systems and methods for monitoring and evaluating public health
programmes. Many of the research methods you have learned can be adapted for use
under routine conditions, so that public health may continue to be evidence-based
even after research has been completed.
Learning objectives
• describe the purpose and types of public health surveillance, and the importance
of registries and notifiable diseases in surveillance
• identify indicators that may be used for evaluating public health programmes
• discuss the role of epidemiological data in informing public health policy and practice.
Health information systems
The health information system (HIS) of a country aims to integrate the collection,
analysis and reporting of data on health outcomes, to provide evidence for improving
health services and ultimately the population’s health. This may include population-
based data, i.e. censuses and vital registration systems (discussed in Chapter 6),
routinely collected health facility data and surveillance of notifiable diseases and regis-
tries. Repeated cross-sectional surveys for specific diseases may also be carried out as
part of monitoring a population’s health.
Use of routinely collected data
Regular, systematic and accurate reporting of health outcomes allows us to determine
the usual ‘baseline’ outcome frequency in a population, and to look at variations
between populations and over time.The prevalence of known risk factors for adverse
health outcomes, such as smoking and alcohol consumption, may also be monitored
using household health surveys to review population behaviours over time. For
example, the Behavioral Risk Factor Surveillance System in the USA uses telephone
surveys of randomly sampled adults to obtain such data, while information on occupa-
tional risks may come from employer records.
12Surveillance, monitoring
and evaluation
23346.indb 15523346.indb 155 22/08/2011 15:1222/08/2011 15:12

Changes in frequency over time may be described as secular or seasonal.A secular
trend refers to a change that is expected to be sustained over a long period of time.For
example, Figure 12.1 shows a decline in syphilis among men and women in the USA
between 1993 and 1998, but a subsequent increase among men since 2000. Changes in
time can indicate that public health efforts are working, or alert the health system to a
growing health danger.
Figure 12.1 Incidence of notified syphilis cases in the USA per 100,000 population by gender and year
Source: Centers for Disease Control and Prevention (2010).
Other explanations for observed changes over time may be related to a change in
the way data are collected or in the case definition. Such changes need to be docu-
mented and considered when interpreting a change in the expected incidence of an
outcome. Figure 12.2 shows how an expansion of the case definition for AIDS in the
USA in 1993 led to an artificial increase in the numbers of cases reported. Changes
may also be due to awareness. For example, an examining doctor may be more likely
to diagnose a particular outcome after a real or suspected outbreak, leading to case-
ascertainment bias and an apparent increase in incidence.
Seasonal trends in frequency refer to changes that occur periodically, usually with a
defined time cycle. Many childhood infections to which immunity is acquired show
cycles of two to three years length. Many outcomes show a seasonal (i.e. intra-annual)
variation that is related to changes in weather (e.g. vector-borne disease, meningitis).
For example,cardiac mortality rates tend to increase during colder months in both the
northern and southern hemispheres. Expected seasonal variation must be incorpo-
rated into any estimates of baseline incidence, for example to distinguish seasonal
peaks from the start of an epidemic (e.g. influenza).
23346.indb 15623346.indb 156 22/08/2011 15:1222/08/2011 15:12

Surveillance, monitoring and evaluation 157
Once baseline and normal variations are known, unusual changes can be more easily
detected, highlighting an outbreak or the emergence of a new health problem. A
sudden increase in the incidence of measles in a population, for example, can be
investigated together with possible explanations (e.g.a decline in vaccination coverage).
Routine data can be compared between different populations, if they share the same
demographic structure, or if this has been adjusted for using standardization methods
(see Chapter 6). Data on different geographic areas within a country, urban or rural
residence, socio-economic status, ethnicity and religion may be collected to enable
inequalities in health outcomes and the use of healthcare to be investigated.The use of
geographical information systems enables data to be mapped, highlighting focus areas
for attention. For example, Figure 12.3 shows the prevalence of obesity by county in
the USA in 2007, enabling further epidemiological research and preventive health
promotion to be more accurately targeted.
Population-based data
In Chapter 6, you learned about censuses and vital registration to collect demographic
data.We will review the uses of these routine data sources for monitoring a popula-
tion’s health.
Vital registration collects data on all registered births and deaths, providing data on
population denominators, demographic structure, birth and mortality rates, and key
health indicators. Registration of births may include information on health-related
conditions, such as length of gestation, birthweight and congenital malformations.
Mortality data can be used as an indicator of the incidence of speciﬁc outcomes,and of
the population’s health overall.These data can be used for planning health services, and
may be compared between populations and monitored over time to identify issues of
Figure 12.2 Total number of AIDS cases reported to the Centers for Disease Control in the USA
between 1982 and 2002
23346.indb 15723346.indb 157 22/08/2011 15:1222/08/2011 15:12

concern. In countries with poor vital registration systems this information is obtained
from sample vital registration or population censuses (see Chapter 6).
Population censuses aim to collect data on the age,gender,ethnicity,religion,occupa-
tion, etc. of all residents.These data are useful to assist the planning and allocation of
health service resources and policy-making. Rigorous methods and quality control
must be used to avoid information bias (e.g. exaggeration of sub-national population if
it is perceived that government services are linked population size).There will be some
selection bias as population subgroups, such as the homeless and migrant workers, will
be under-represented.Statistical methods are used to estimate the data for intervening
years between census surveys, and to make projections about future trends.
Public health surveillance
Public health surveillance is the monitoring of health in a given population over time.In
Chapter 1, you saw an early example of this through John Snow’s monitoring of the
distribution of cholera-related deaths temporally (i.e. over time) and spatially (i.e. by
geographic area). It enabled him to identify a pattern, and to generate and test his
hypotheses on drinking water as the source of the epidemic. Modern surveillance sys-
tems also aim to provide timely information on which to base public health decisions,and
for the planning, implementation, and evaluation of public health policies and practices.
Surveillance can detect and verify the emergence of health hazards such as infectious
disease outbreaks,or more gradual increases in cause-speciﬁc deaths over time that may
indicate changes in exposure to a risk factor.This enables initiation of an appropriate
public health response to minimize any adverse impact on the health of a population.
Figure 12.3 Age-adjusted percentage of adults ≥ 20 years old who were obese in the USA in 2007
23346.indb 15823346.indb 158 22/08/2011 15:1222/08/2011 15:12

A reporting framework is necessary for the systematic collection, analysis, interpreta-
tion and dissemination of health data. While these exist for specified infectious and
chronic diseases, for many outcomes there is no specific surveillance system in place.
The development of a surveillance system requires clear objectives and the use of
strict criteria with which to identify and classify disease.A clear case definition is vital
to ensure accurate data are collected and detection is usually based on clinical findings,
laboratory results to confirm a diagnosis, and epidemiological data describing the time,
place and type of individuals affected. Standardized reporting methods are essential if
authorities are to have confidence in the data collected.
However, many factors can affect data quality. Large numbers of people are usually
responsible for surveillance data collection across many sites.Without the opportunity
for specific training, the validity of data may suffer. Feeding-back data to the individuals
collecting it can motivate them to ensure data are of a high standard. Motivation to
record data systematically may also be influenced by perception of whether the
capacity and infrastructure exist to elicit an appropriate public health response.
Types of surveillance
Surveillance systems may be passive or active. Passive surveillance is the detection
of cases when they seek healthcare.Responsibility for reporting is placed on the health
service provider (e.g. doctor, laboratory, health centre, hospital), which will routinely
collect data on the numbers, basic demographics and diagnoses of patients seen.
Practitioners may also report to registries that centralize data on specific chronic
conditions (e.g. cancers). Passive surveillance also includes the use of certified death
data to monitor cause-specific mortality (see Chapter 6).
Active surveillance involves case-finding using methods such as reviews of clinical
records or community health surveys.Active surveillance is costly and labour-intensive,
and is not usually used for routine surveillance unless (a) there is a need to monitor
the emergence or elimination of a new disease,or (b) when cases may not be accessing
the formal healthcare infrastructure.
Health facility data
Public hospitals and clinics generally collect data on outpatient and inpatient attendance,
together with basic patient demographics and diagnoses,which is collated and reported
to a central body. Health facility data cannot be used to estimate the true incidence of
an outcome in the population, because many factors will influence whether or not an
individual attends a health facility.For example,some individuals may seek care from the
private, voluntary, or informal sectors (e.g. traditional healers, medication sellers), and
they would not be included in estimates of incidence calculated from public hospital
data.Access to healthcare also varies geographically and with socio-economics.
These data may still be used to monitor the healthcare needs of a population, and as
an indicator of what may be occurring in the population, as long as we are aware of
their biases. For example, an unexpected increase in patients attending with influenza
may suggest the start of an epidemic that requires more comprehensive population-
based surveillance and health advice. In low-income settings, where the health services
are already overloaded, there may be minimal record keeping and the data may not be
an accurate reflection of the situation.
23346.indb 15923346.indb 159 22/08/2011 15:1222/08/2011 15:12

While many effective surveillance systems function around the world, the propor-
tion of outcomes recorded and reported will vary and surveillance is unlikely to
capture all cases.Population incidence calculated from routine surveillance is therefore
likely to underestimate the true incidence in the community.
Registry data
A registry is a systematic collection of data about every patient with a particular
diagnosis, condition or procedure (e.g. cancer, artificial joints). Registries allow the
monitoring of individual patients over time and may be used to coordinate recall of
patients to attend for regular check-ups and reviews of medication. Information is
collected on various factors including basic demographics, patient history, diagnosis,
treatment and health status. Data may come from general practitioners, treatment
facilities, hospitals or death certificates.
Registers are also used for surveillance.In the UK,the National CongenitalAnomaly
System (NCAS) was established in 1964 in response to the thalidomide tragedy.
Thalidomide was licensed for use by pregnant women as a medication to reduce
nausea but was subsequently found to cause limb malformations in the unborn child.
The NCAS was set up to detect new hazards and help prevent a similar tragedy.
Although the main purpose of the NCAS is surveillance, it also provides valuable birth
prevalence data.
Another example comes from Australia’s Northern Territory, which reports the
highest published incidence of acute rheumatic fever (ARF) in the world among its
Aboriginal population. Since recurrent cases of ARF lead to cumulative heart valve
damage,ARF is a significant cause of cardiovascular morbidity and mortality for these
communities.Since 1997,a rheumatic heart disease control programme has established
a computerized registry of all known or suspected cases of ARF or rheumatic heart
disease within the region. The registry is used to improve patient care, particularly
secondary prevention, by establishing a reminder system for monthly penicillin
injections and other clinical follow-up by the primary care system, and to organize and
conduct education programmes.
Registries can be used to monitor outcome incidence, prevalence and patient
survival over time.Analysis of registry data can be used to evaluate the effectiveness of
screening programmes, other preventive interventions, treatments or surgical proce-
dures using cohort study designs.Healthcare providers may also collect information to
monitor the quality of care (e.g. treatment waiting times, average length of stay in
hospital). By analysing registry data on previous patients, healthcare providers can
inform patients,and plan,monitor and improve their services.Registry data can also be
analysed in ecological studies to compare populations using standardized rates (see
Chapter 6) and to develop hypotheses on possible disease causation by considering
patient characteristics and environmental exposures.
Infectious disease surveillance
Many countries have systems in place for monitoring certain notifiable diseases (e.g.
cholera,tuberculosis,yellow fever) through compulsory (i.e.legally enforced) reporting.
The health service provider must keep detailed records and notify a central public
health agency of each notifiable case diagnosed. Data on notifiable diseases are then
23346.indb 16023346.indb 160 22/08/2011 15:1222/08/2011 15:12

collated and analysed by public health agencies (e.g. Health Protection Agency in the
UK, Centers for Disease Control and Prevention in the USA).
Notification rates will depend primarily on whether an affected individual seeks
medical advice.In some communities,healthcare providers may be difficult to access or
patients may be unaware of their condition and not seek help.The infrastructure may
not exist to record data of sufficient quality and to communicate that data.
The list of notifiable diseases varies between countries, but the majority are infec-
tious. If the infection is not endemic to a country, notification aims to identify impor-
tations and stop local transmission. If the infection is endemic, notification enables
monitoring for early detection of, and rapid response to, an outbreak (see Figure 12.4).
However,public health agencies need resources and infrastructure to act rapidly on the
information they receive,if they are to successfully stop or slow the spread of a disease.
Figure 12.4 Number of cases of anthrax notified by year in the USA (1953–2008)
An example of the utility of surveillance for disease control is the use of epidemic-
warning systems in the malaria epidemic-prone highlands of Africa (Jones et al. 2008). If
routine data on the incidence of clinical malaria cases attending a health facility are
collected and analysed in a timely manner, abnormal patterns can be identified early in
the epidemic.This allows for implementation of appropriate preventive measures, such
as indoor-residual spraying of houses with insecticide, which may avert a major epi-
demic. Previously, the delays inherent in collating paper-based clinic records and sum-
marizing data for each area resulted in data reaching the malaria control programme
too late to be of use.Knowing this,clinic staff had no incentive to ensure that data were
rigorously recorded.The introduction of computer databases to enter and summarize
data, and appropriate training, has improved the accuracy and utility of the surveillance
23346.indb 16123346.indb 161 22/08/2011 15:1222/08/2011 15:12

system. Data can be rapidly fed back to clinic staff, and the malaria control programme,
which can take action as necessary.
Sentinel surveillance is the collection and analysis of data by designated institu-
tions selected for their geographic location, disease specialization, and ability to accu-
rately diagnose and report high quality data. It involves the identification of health
providers and diagnostic facilities with sufficient capacity to participate in a reporting
network. Sentinel surveillance may be appropriate when costly diagnostic tests are
involved. For example, taking throat-swabs from patients with flu-like symptoms to
obtain a laboratory diagnosis of influenza in the UK, or monitoring the spread of anti-
malarial drug resistance across Africa. In low-income countries, this may require an ini-
tial investment of appropriate training and resources to develop a functioning network.
Outbreak response
The Global Polio Eradication Initiative has worked to strengthen surveillance of polio
and reporting systems in low-income countries.As the programme nears its target, the
numbers of cases of paralytic poliomyelitis decline, and detection of circulating wild
poliovirus becomes harder. In countries that have already locally eliminated the dis-
ease,there is a risk that an importation of polio virus could lead to the re-establishment
of local transmission. Consequently, surveillance is the key to successful eradication.
While acute poliomyelitis is a notifiable disease, those countries without sufficient
infrastructure may rely on reporting of all acute flaccid paralysis cases followed by a
laboratory diagnosis.The global programme assesses how effectively a country’s surveil-
lance systems are functioning though a network of sentinel sites. Information on cases
detected, importations and local outbreaks is analysed and shared to enable a rapid
response using targeted vaccination.
TheWorld Health Organization (WHO) coordinates a number of surveillance strat-
egies around the world and aims to strengthen the capacity of countries to conduct
effective surveillance.The International Health Regulations (2005), implemented since
2007, outline ‘global rules to enhance national, regional and global public health
security’ that are legally binding for all member states (World Health Organization
2011b).These regulations require countries to strengthen their capacities for public
health surveillance and response. The regulations were updated in response to the
crisis resulting from the SevereAcute Respiratory Syndrome (SARS) epidemic in 2003
inAsia and concerns about circulating InfluenzaA (H5N1) (sometimes called‘avian flu’).
The regulations require countries to strengthen their capacities for public health
surveillance and response. The Global Outbreak Alert and Response Network
(GOARN) was initiated in 2000 as a technical collaboration to pool human and
technical resources for rapid identification, confirmation and response to outbreaks of
international importance (World Health Organization 2011a).
The new regulations and network were first tested when an outbreak of Influenza A
(H1N1) (sometimes called‘swine flu’) was reported to theWHO from Mexico and the
USA in April 2009. It was categorized as a ‘public health emergency of international
concern’ and scientific and epidemiological investigations followed,with unprecedented
sharing of information between collaborating institutions (Schuchat et al. 2011), mem-
ber states and the WHO.The WHO coordinated surveillance of cases and eventually
classified it as a pandemic on the basis of outbreaks in countries from differentWHO
regions.While the extent of the 2009 pandemic was not as great as originally feared, it
is difficult to evaluate to what extent this was the result of the early detection,response
23346.indb 16223346.indb 162 22/08/2011 15:1222/08/2011 15:12

and control efforts undertaken in several countries and the efforts coordinated by the
WHO.This highlights the important role of surveillance both at the national and inter-
national level.
Activity 12.1
Acute lower respiratory infections (ALRI – pneumonia and bronchitis) are a leading
cause of illness and mortality in children under 5 years of age in low-income countries.
Country X set up a hospital-based surveillance of clinically diagnosedALRIs in 2004,using
five sentinel hospitals. Figure 12.5 shows data from the first five years of surveillance.
Figure 12.5 Incidence of acute lower respiratory tract infections per 100,000 cases by 3-month reporting
period
1 Describe the data shown in Figure 12.5.
2 What are the potential biases of these data for:
(a) planning hospital-based ALRI healthcare for Country X?
(b) estimating the true burden of ALRI disease in Country X?
Activity 12.2
1 Nosocomial (i.e. hospital-acquired) infections are an increasing problem in high-
income countries. Hospitals with low rates of nosocomial infection tend to have
strong infection-control programmes.Two methods of hospital surveillance of post-
surgery nosocomial infections were compared in several hospitals in a high-income
country. Passive surveillance (clinically diagnosed infections by the surgeon) was
23346.indb 16323346.indb 163 22/08/2011 15:1222/08/2011 15:12

found to have 65% sensitivity and 98% specificity when compared with active
surveillance (retrospective review of hospital records and discharge notes by trained
medical personnel).What are the benefits and disadvantages of setting up an active
surveillance system for nosocomial infections in this setting?
2 RiftValley Fever (RVF) is a mosquito-borne viral zoonosis (i.e. it can be transmitted
from animals to humans). RVF outbreaks have been reported regularly in
Sub-Saharan and North Africa since 2006, and are usually preceded by high rates of
abortion among sheep and goats. Most human infections have mild influenza-like
symptoms, but RVF can cause more severe symptoms including haemorrhagic fever
and death. In 2011, after several cases were confirmed by laboratory testing, an
epidemiological surveillance network for RVF was set up in a low-income African
country.What are the benefits and limitations of using a passive surveillance system
that provides reporting forms to village health workers with monthly collection
of data?
Monitoring and evaluation
Epidemiology has an important role in health programme monitoring and evaluation.
Monitoring is the term applied to the systematic routine collection of evidence
about the effectiveness of a specific health programme over a period of time. It
involves the collection of descriptive data to ensure that programmes will meet
their goals. Epidemiological data used for monitoring include measures of outcome
frequency (i.e. prevalence, risk, incidence rate), indicators related to the outcome of
interest (e.g. anaemia prevalence as an indicator of impact on malaria), and data on
adverse events.
Data on adverse events are a type of outcome measure that must be collected when
a clinical intervention (e.g. medication, vaccine, X-ray) is being applied to a population.
While an intervention must have been demonstrated as safe before it can be imple-
mented, few intervention studies would have sufficient statistical power to detect rare
events. Adverse events that may not have been detected during a Phase 3 trial may
become apparent once an intervention is applied to larger populations, under routine
conditions (i.e. poorer compliance or clinical follow-up), and over longer periods of
time.These are sometimes referred to as Phase 4 studies.
Monitoring often involves measuring process indicators in relation to pre-specified
targets.This may be numbers of cases detected by a screening programme, numbers of
hospital admissions or waiting times for surgical interventions. Coverage is a measure
of what proportion of the eligible population is reached by the intervention
(e.g. proportion of children under 12 months old receiving three doses of diphtheria-
tetanus-pertussis vaccine, proportion of births attended by a skilled-birth attendant).
For a complex intervention, each step necessary for effective delivery should be
monitored. For example, the success of a vaccination programme will depend on:
(a) the acquisition of a quality-controlled vaccine;(b) delivery of viable vaccine to health
centres; (c) sufficient training of health workers on vaccination; (d) availability of viable
vaccine, disposable needles and syringes at the time of attendance; (e) attendance of
infants for vaccination; and finally (f) the protection of the infant by the vaccine.
Monitoring may therefore measure several essential and desirable indicators along a
programme’s process pathway.
Monitoring may make use of indicators that are collected routinely as part of a
country’s health information system or indicators introduced as part of a specific
23346.indb 16423346.indb 164 22/08/2011 15:1222/08/2011 15:12

health programme. The equity of a programme can also be measured by comparing
process indicators across groups, for example, using household income quintiles (i.e.
dividing the population at risk into five equal-sized groups based on their income).
Outcome indicators can be collected using cross-sectional or cohort methods, or
more often may be collected routinely through passive surveillance or health-facility
data.Process indicators can be collected routinely,through the development or adapta-
tion of existing data collection tools.For example,a child health card may be revised to
include an additional space for a new vaccination that has been introduced, and the
vaccination clinic records will be similarly adapted.
To measure coverage or differential access to a health programme, surveys of a
representative sample of those at risk can be conducted. For example, routine data
from a mother and child clinic may indicate that all infants attending received their
measles vaccinations. If we have a good estimate of the number of infants in the com-
munity, we can calculate coverage. Otherwise a household survey may provide more
accurate data on which households are not sending their children for vaccination, and
why.This information can be used to improve coverage or equity.
Evaluation is taken here to mean the measurement of a programme’s effects and
effectiveness after a specified time-period. Note that healthcare evaluation is a broad
field, and evaluation can involve needs assessment and cost-effectiveness, for example,
which will not be covered here. The effect of a programme refers to whether it
has achieved delivery of the public health intervention or service and is usually
measured by coverage e.g. proportion of women over 50 attending for a regular
mammogram.
The effectiveness of a programme refers to whether it has had a measurable public
health impact in terms of improving health outcomes (e.g. decline in chicken pox
(Varicella zoster) incidence after the introduction of the varicella vaccine). Process and
outcome data can be compared to assess whether the health programme has had any
result.A vaccination programme could not claim responsibility for substantial declines
in disease-specific child mortality if insufficient stocks of vaccine had been delivered to
vaccination clinics,and the number of children receiving the vaccine had been very low.
If there are sufficient data points (e.g. from several time-points or sub-populations), a
simple analysis might compare process indicators with outcome measures, using a
scatter plot (Chapter 5).
Plausibility studies (see Chapter 10) may be used to estimate effectiveness by
comparing outcome frequency in the population before and after introduction of the
programme; comparing a population covered by the programme with a population
without access to the programme; or comparing individuals who did and did not
receive a particular type of public health intervention or healthcare. For example,
this could include mortality rates among those with short versus long diagnosis-to-
treatment intervals, using a pre-defined cut-off. Case-control studies may provide a
more rapid means of assessing effectiveness, although they will be subject to different
biases (see Chapter 8). For example, cases of Haemophilous influenzae type b (Hib)
identified from notifiable disease surveillance systems could be compared with
community age-matched controls to compare the odds of having received routine
infant Hib vaccination (from health records).
The documentation of time-trends following introduction of a health programme
may provide supportive evidence of its effectiveness. However, for these ‘adequacy
evaluations’ to be convincing, the programme’s process pathway needs be relatively
short and simple,the impact should be large,and confounding must be unlikely (Victora
et al. 2004).
23346.indb 16523346.indb 165 22/08/2011 15:1222/08/2011 15:12

Activity 12.3
This activity is based on the monitoring and evaluation of a malaria intervention pro-
gramme by Hanson et al. (2008). Pregnant women and children under 5 years of age
are a high-risk group for severe malaria outcomes. Insecticide-treated nets (ITNs)
provide protection from night-biting mosquitoes to those sleeping under them, and
have been proven safe and effective in reducing maternal anaemia and child mortality,
particularly in Africa.A programme was established inTanzania to increase ITN cover-
age of pregnant women and young children through the delivery of vouchers during
the first antenatal care (ANC) visit.Vouchers provided a subsidy (i.e. price reduction)
for purchasing an ITN in local shops.
Suppose you are part of a team involved in designing a monitoring and evaluation
strategy for this complex intervention.
1 Identify the intermediary processes involved in achieving the programme’s aims.
2 Which process indicators and methods would you use to monitor how well the
programme was functioning and whether it was on track to deliver its outputs?
3 Describe how you would evaluate the effectiveness of the programme after a
five-year period. Identify the primary outcome measure and methods for collecting
relevant data.
Informing policy and practice
While epidemiology aims to influence public health policy and practice, decision-
makers often need to act rapidly and, if evidence is incomplete or contradictory, may
do so in the absence of good evidence. The results of epidemiological studies, and
routine data on the burden of an outcome or risk of an exposure, need to be
communicated appropriately and rapidly to policy-makers.
An example of poor medical research data having a detrimental impact on public
health is the controversy over claims that measles–mumps–rubella (MMR) vaccine
caused autism. In 1998, a study of 12 children with developmental disorders reported
that parents of eight of these children linked the start of behavioural symptoms to recent
MMR vaccination (Wakefield et al. 1998). No further epidemiological evidence was pre-
sented, but high profile media coverage led to a significant decline in MMR coverage in
the UK. Concerned parents refused to vaccinate their children, and increases in the
numbers of confirmed measles cases followed. Subsequent epidemiological research,
including a large case-control study using routine data from general practitioners (Smeeth
et al.2004),found no association between MMR vaccination and autism.However,these
took time to conduct, analyse and disseminate. MMR coverage in the UK started to
increase after 2003, but by 2011 had still not regained its pre-vaccination-scare level.
Routine monitoring data can inform public health practice through the detection of
and rapid response to outbreaks, and through the detection of more gradual changes
in population health over time. Routine data can also be used to identify risk factors
for subsequent epidemiological investigation. An example of this is the initiation of a
surveillance system for AIDS soon after it was first described, which subsequently
provided data that helped to identify high-risk groups and risk factors for the disease,
long before its cause was discovered.
Epidemiological research data have often been used successfully to inform public
health policy and practice. Examples include national policies on routine childhood
23346.indb 16623346.indb 166 22/08/2011 15:1222/08/2011 15:12

vaccination to prevent specific childhood infectious diseases, and public policies and
legislation to reduce exposure to tobacco smoke.Epidemiological evidence that obesity
is caused by complex interactions between diet and physical activity is currently inform-
ing the development of policies to slow the obesity epidemic in high-income countries.
In the UK,for example,the government is attempting a controversial health promotion
approach to encourage individual behaviour change.
The importance of collecting high quality data increases as data access and usage
grow. As more agencies and individuals, including policy-makers and the media, have
access to descriptive information on the health of populations its use (and misuse) will
increase.We hope that reading this book has given you the incentive and basic tools to
collect, analyse, or interpret public health data using effective epidemiological tools.
Conclusion
In this chapter you have learned about surveillance, monitoring and evaluation for
public health. Epidemiological methods, rigour and analysis can be applied to routinely
collected data to continually inform public health policy and practice. Surveillance
systems allow us to identify disease outbreaks and epidemics, monitor time trends and
identify population-level risk factors for an outcome. Demographic systems (i.e. vital
registration, population census) provide contextual baseline and denominator data
within which monitoring can be interpreted. Routine monitoring of process and
outcome indicators can be used to evaluate the impact of public health programmes.
Epidemiological data from research and routine monitoring can be used to provide an
evidence-base for making informed public health decisions.
References
Centers for Disease Control and Prevention (2004) Summary of notifiable diseases—United States, 2002.
Morbidity MortalityWeekly Report 51: 1–84.
Centers for Disease Control and Prevention (2009) Estimated county-level prevalence of diabetes and
obesity—United States, 2007. Morbidity MortalityWeekly Report 58: 1259–63.
Centers for Disease Control and Prevention (2010) Summary of Notifiable Diseases—United States,2008.
Morbidity MortalityWeekly Report 57: 1–94.
Hanson K,Nathan R,MarchantT,et al.(2008)Vouchers for scaling up insecticide-treated nets inTanzania:meth-
ods for monitoring and evaluation of a national health system intervention.BMC Public Health 8:205.
Jones C, Abeku TA, Rapuoda B, Okia M and Cox J (2008) District-based malaria epidemic early warning
systems in East Africa: perceptions of acceptability and usefulness among key staff at health facility,
district and central levels. Social Science and Medicine 67(2): 292–300.
Schuchat A, Bell BP and Redd SC (2011) The science behind preparing and responding to pandemic
influenza: the lessons and limits of science. Clinical Infectious Diseases 52 Suppl. 1: S8–12.
Smeeth L, Cook C, Fombonne E, et al. (2004) MMR vaccination and pervasive developmental disorders: a
case-control study. Lancet 364: 963–9.
Victora CG,Habicht JP and Bryce J (2004) Evidence-based public health:moving beyond randomized trials.
American Journal of Public Health 94: 400–5.
WakefieldAJ,Murch SH,AnthonyA,et al.(1998) Ileal-lymphoid-nodular hyperplasia,non-specific colitis,and
pervasive developmental disorder in children. Lancet 351: 637–41.
World Health Organization (2011a) Global Outbreak Alert and Response [Online].Available:http://www.who.
int/csr/en/ (accessed 02/05/2011).
23346.indb 16723346.indb 167 22/08/2011 15:1222/08/2011 15:12

World Health Organization (2011b) International Health Regulations (IHR) [Online].Available: http://www.
who.int/ihr/global_alert/en/ (accessed 02/05/2011).
Activity 12.1
Your answers should be similar to the following.
1 The data show an annual seasonal variation in the incidence of ALRI, with peaks in
July–September, and lows in January–March. There appears to be a halving of the
incidence between 2006 and 2007, which is then sustained for the subsequent three
years.The peak incidence declines from approximately 1,200 cases per 10,000 (2005
and 2006) to approximately 600 cases per 100,000 (2007–2010), while the low
incidence declines from approximately 400 per 100,000 (2005 and 2006) to 200 per
100,000 (2007–2010).
Without more historical data, we cannot tell whether the 2005–2006 data repre-
sent unusual or epidemic incidence, or whether these data represent a stable
incidence with a subsequent decline, for example, after the introduction of a public
health intervention.
2 These data present biases at two levels:
(a) The data may not be representative of other hospitals in country X because they
come from five sentinel hospitals. This can result in selection bias if the geo-
graphical location of the sentinel hospitals is not nationally representative. For
example, they may be more likely to be in urban rather than rural settings, in
additional to potential regional and ethnic differences. Sentinel hospitals also
tend to be chosen because they have sufficient capacity for diagnosis and report-
ing, which is likely to vary from the infrastructure in most other hospitals.
(b) In addition to the reasons given above relating to geographical and social
representativeness of the sentinel hospitals, hospital or health-facility-based data
generally underestimate the community burden of most diseases. Many
people may not access government healthcare services because of distance,
poor quality of care (perceived or real), economics (e.g. in settings with cost-
sharing, travel costs), or social exclusion. There are also likely to be several
alternative sources of healthcare (e.g. mission hospitals, private and traditional
practitioners).
As these are designated sentinel hospitals, the quality of data are likely to be
monitored and of a reasonable standard. However, a large number of staff will be
involved,and there may be differences in diagnosis and reporting within and between
sites,and over time.
Activity 12.2
1 Active surveillance is very costly, taking time and requiring additional staff.
However,a sensitivity of 65% means that 100 – 65 = 35% of patients with nosoco-
mial infections were not being identified by the surgeon, i.e. the rate of nosocomial
infections was being underestimated. If the surgeons and the hospital are unaware of
the magnitude of the problem, it is unlikely to be resolved.
An active surveillance system would therefore most probably result in better
recognition of the burden of nosocomial infections, and subsequent improvements
23346.indb 16823346.indb 168 22/08/2011 15:1222/08/2011 15:12

in infection control.As retrospective review does not impact patient care it may be
preferable to set up a sample active surveillance, with retrospective review of a
randomly selected proportion of patients as an indicator of the problem.
2 Routine monitoring by personnel with limited training is unlikely to provide accurate
or comparable data. However, this surveillance aims to detect outbreaks, rather than
routinely ‘monitor’ for secular trends or to compare populations, therefore data
consistency is not the top priority. The most important issue here will be high
coverage, which would not be possible with an active surveillance system.
As RVF outbreaks are generally preceded by high rates of abortion among live-
stock, resident village health workers will be best placed to detect these warning
signs. Since the majority of cases have non-specific symptoms, active surveillance
would be unable to rely on clinical diagnosis anyway, and laboratory facilities are
unlikely to be routinely available.
Collation of monthly reports can be used to ‘screen’ for areas with increasing
numbers of reported influenza-like cases for further investigation. Any reports of
cases with more severe symptoms that had not already been notified through the
formal healthcare system, would identify the local population as high-risk. (A cross-
sectional serological survey (i.e. testing antibody levels) could then be conducted.)
Activity 12.3
1 The intermediary processes can be identified as:
• Vouchers available in health facilities.
• Pregnant women attending for routine antenatal care (ANC) visits.
• Pregnant women receiving a subsidy voucher.
• Pregnant women seeking to purchase an ITN.
• ITNs available for purchase with the voucher in the local shops.
• Pregnant women sleeping under an ITN.
• Babies or young children co-sleeping under an ITN.
2 Appropriate process indicators for monitoring should correspond to each of the
intermediary processes.You may have identified some or all of the following.
• Health facility stock records could be used to document receipt and availability of
subsidy vouchers.
• Health facility records could provide information on the number of women
attending forANC,and demographic data can be used to estimate the number of
pregnant women in the population.
• Pregnant women could be interviewed as they leave the health facilityANC clinic
to evaluate what proportion were given a voucher by the health facility staff.This
is known as an ‘exit interview’.These data could also be obtained from a cross-
sectional household survey.
• A household survey might ask about the willingness to purchase a net given that
there is some cost to the household.This is a complex issue involving household
economics and decision-making powers, and would probably require additional
qualitative methods.
• A structured interview administered to a random sample of shopkeepers could
collect data on ITN availability in the local shops,and participation of shops in the
voucher programme.This is known as a ‘retail audit’ and could be undertaken at
regular intervals. Additional qualitative data on shopkeeper perceptions of the
voucher scheme, collected through in-depth interviews, could identify potential
difficulties.
23346.indb 16923346.indb 169 22/08/2011 15:1222/08/2011 15:12

• Routine programme records on the exchange of vouchers for ﬁnancial subsidy by
shopkeepers could be used to monitor how the process was functioning.
• A cross-sectional household survey could be used to measure the effects of the
programme.The main effects of interest would be the proportion of households
with a pregnant woman that own an ITN, the proportion of pregnant women
reporting that they regularly sleep under an ITN,and the proportion of infants or
young children reported to regularly sleep under an ITN.
3 While the aim of the programme is ‘to increase ITN coverage of pregnant women
and young children’, its ultimate goal is to reduce adverse malaria outcomes in this
high-risk target group:
• Child mortality would be hard to measure, and would have to rely on demo-
graphic data such as population censuses or representative population surveys,
which may not take place within the ﬁve-year time-period.
• Maternal anaemia would be the preferred outcome measure as it could be meas-
ured at routine ANC visits.This would not require many additional resources, as
training and strengthening of data recording systems would already be implemented
in the health facilities and ANC clinics as part of the programme.
• Maternal anaemia is related to low birthweight, but this is harder to measure in a
developing country setting as a low proportion of births are attended by skilled
birth attendants.
• More direct measures of malaria outcome include outpatient attendance for
clinical malaria, or hospital admissions for severe malaria. However, these data
would be dependent on the quality of data collection at the hospitals or health
facilities.
23346.indb 17023346.indb 170 22/08/2011 15:1222/08/2011 15:12

This is a reference guide to the epidemiological terms used in this book. For further
explanation of these terms,use the index to refer to them in the main text.Cross-references
to other glossary terms are shown in italics.
Absolute risk See attributable risk.
Active surveillance The surveillance of an outcome by searching for cases in the community.
Allocation The distribution of study subjects to intervention and control arms in an interven-
tion study.
Allocation concealment In a randomized-controlled trial:when the randomization schedule for
intervention allocation is not revealed to the person enrolling subjects, to reduce selection bias.
Alternative hypothesis Usually the opposite of the null hypothesis, but may indicate the
direction of an association.
Analytical study Designed to test a hypothesis. Generally, to examine whether a certain
exposure is a risk factor for a particular outcome. (Contrast: descriptive.)
Ascertainment bias A type of information bias, where detection of outcome may vary
between exposure groups.May be especially a problem for intervention studies without blinding.
Assessment bias See information bias.
Asymptomatic The state of having an outcome with no outward symptoms.
Attributable fraction (Synonym:Attributable risk percentage.) A measure that calculates
the attributable risk as a proportion of the incidence of outcome in those exposed, i.e. the pro-
portion of cases among those exposed that may be due to the exposure, and that could be
prevented if the exposure were eliminated completely.
Attributable risk (Synonym: absolute risk, excess risk.) A measure that calculates the
additional incidence of outcome in those exposed after subtracting the incidence that would
have occurred in the absence of exposure (i.e. in those unexposed). It assumes that the
relationship between exposure and outcome is causal, and can be calculated using either
risks or incidence rates. It is used to indicate the number of cases that could be prevented if
the exposure were eliminated completely, i.e. the public health impact.
Attributable risk percentage See attributable fraction.
Bias A systematic difference from the truth. In epidemiology, this represents a source
of error in estimating the association between exposure and outcome. (See selection bias,
information bias.)
Blinding (Synonym: masking.) Where information about exposure or outcome is concealed
from the participants and/or observers to reduce information bias.
Case An individual that meets the case deﬁnition for having the outcome of interest.
Case-control study An observational study in which two groups are deﬁned on the basis
of their outcome status. Those with the outcome are called cases and those without the
outcome are called controls.The level of exposure to a risk factor is then measured in the two
Glossary
23346.indb 17123346.indb 171 22/08/2011 15:1222/08/2011 15:12

172 Glossary
groups and compared.The odds ratio of exposure is the only measure of relative risk that can be
obtained from case-control studies, as there is no measure of the frequency of the outcome.
Case definition Criteria for identifying an individual as having the health outcome of inter-
est,which may specify clinical signs and symptoms,diagnostic test results and time-period (e.g.
a malaria case as malaria bloodslide positive with reported fever within 48 hours).
Case-fatality rateThe proportion of cases with an outcome,which are fatal within a specified
period of time. (Note, this is a proportion not a rate.)
Causal pathway The sequence of events leading from an exposure to an outcome.
Causality The relationship between an exposure and a health outcome, where the outcome
is considered to be a consequence of the exposure.
Chance The possibility of observing a value or event without reason or predictability. In
epidemiology this is often taken to mean that something is not representative of the reality.
Cluster-randomized trial A randomized-controlled trial in which groups of individuals
(clusters) rather than single individuals are randomized, and all individuals within a cluster
receive the same intervention.
Cohort study (Synonym: follow-up study.) An observational study in which two groups are
defined on the basis of their exposure to a potential risk factor,and are followed up over time
to measure the incidence of the outcome, which is then compared between the groups to
give an estimate of relative risk.
Compliance rate In an intervention study: the proportion of individuals who cooperate fully
with all the study procedures. (Note, this is a proportion not a rate.)
Component cause A factor that contributes to producing an outcome.
Confidence interval The range of values,estimated from a sample,within which the‘true’
population value is likely to be found.A 95 per cent confidence interval is usually presented,
meaning that there is a 5 per cent probability that the ‘true’ population value lies outside of
this range. It is used to indicate the reliability of the estimated result.
Confounder (Synonym: confounding variable.) A variable that is associated with both the
exposure and the outcome under study, but is not on the causal pathway between the two. It
may provide an alternative explanation for any association observed.
Confounding A situation in which the estimate of association between an exposure and an
outcome is distorted because of the association of the exposure with another factor (see
confounder) that is also associated with the outcome.
Consent See informed consent.
Contamination In an intervention study: exposure of the control group to the intervention,
or vice versa.
Control (Case-control) An individual that does not fulfil the case definition for the out-
come of interest. (Contrast: case.) Note, this is different to the meaning of control in an
intervention study.
Control (Intervention) A study subject (individual, household, village, etc.) in an interven-
tion study who does not receive, and is therefore unexposed to, the intervention of interest.
Note, this is different to the meaning in a case-control study.
Cross-sectional study An observational study in which information on the outcome and
exposure is measured simultaneously (at one point in time).
Crossover trial A randomized-controlled trial in which each subject acts as its own control
by receiving both the intervention and control at different time-points, with a washout period
in-between.
23346.indb 17223346.indb 172 22/08/2011 15:1222/08/2011 15:12

Glossary 173
Crude rate The incidence rate in the total population, without any adjustment for potential
confounders. (Contrast: standardized rate.)
Cumulative incidence See risk.
Descriptive Designed to describe the existing distribution of variables in a population
without regard to causal or other associations.An example would be a cross-sectional study
to assess the prevalence of anaemia in a population. (Contrast: analytical study.)
Diagnosis Identification of an outcome using rigorous tests or methods.
Differential misclassification Incorrect classification of exposure or outcome of study sub-
jects as a result of information bias,where this differs between comparison groups.This can lead
to over- or under-estimation of a measure of association and may lead to false associations.
Direct standardization See standardization.
Ecological bias (Synonym: ecological fallacy.)
Ecological fallacy (Synonym: ecological bias.) The misleading idea that a group-level
association from an ecological study can be applied at the individual level. For example, a
positive correlation between national average dietary fat intake and national mortality rates
from female breast cancer does not necessarily mean that the women who died of breast
cancer were the ones who had a diet rich in fat.
Ecological study An observational study in which the units of analysis are populations or
groups of people rather than individuals. (See ecological fallacy.)
Effect modification (Synonym: interaction.) Variation in effect of the exposure on an out-
come across values of another factor (effect modifier). It can be detected by stratification
during analysis and may be adjusted for with statistical modelling.
Effect modifier Factor across whose categories the effect of an exposure on particular
outcome may vary. See effect modification.
Effectiveness The extent to which an intervention produces an improvement in a health
outcome when it is applied through a routine delivery system. (Contrast: efficacy.)
Efficacy The extent to which an intervention produces an improvement in a health outcome
under ideal trial conditions. (Contrast: effectiveness.)
Elimination The total removal of an outcome (usually by removal of the exposure) from a
country or region. (Contrast: eradication.)
Endemic The maintenance of an infection in a defined population without external
introduction.
EpidemicThe increase in the frequency of an outcome that is significantly in excess of what
would normally be expected.
EradicationThe total removal of an outcome (usually by removal of the exposure) from the
entire world. (Contrast: elimination.)
Excess risk See attributable risk.
Exclusion criteria Characteristics defining which individuals may not be included in a
study. (Contrast: inclusion criteria.)
Exposed Those subjects who have experienced or possess (e.g.genetic or physical charac-
teristics) the risk factor of interest.
Exposure Synonymous with risk factor, or the act of being exposed to a potential risk or
protective factor.
Factorial trial A randomized-controlled trial in which two or more interventions are com-
pared individually and in combination against a control comparison group.
23346.indb 17323346.indb 173 22/08/2011 15:1222/08/2011 15:12

174 Glossary
Follow-up Observation over a period of time of an individual, group, or initially defined
population whose relevant characteristics have been assessed, in order to observe changes
in exposures or outcomes.
Frequency A measure of the number of occurrences of an outcome per population (see
prevalence) or per unit time (see incidence).
General population The wider population to whom the results of analytical epidemio-
logical studies are to be applied. For example, the ‘general population of India’ refers to all
individuals living in India. (Contrast: sample population, target population.)
Hypothesis A supposition phrased in such a way as to allow it to be tested and confirmed
or refuted.
Incidence The number of new cases of an outcome that develop in a defined population
of individuals at risk during a specified period of time. It can be measured as risk, odds or
incidence rate. See null hypothesis.
Incidence rate The number of new cases of an outcome that develop in a defined population
of individuals at risk during a specified period of time,divided by the total person-time at risk.
Incidence rate ratio (Synonym: rate ratio.) A measure of relative risk. Calculated as the
incidence rate of outcome in those exposed, divided by the incidence rate of outcome in
those unexposed.
Inclusion criteria Characteristics defining which individuals may be included in a study.
(Contrast: exclusion criteria.)
Indirect standardization See standardization.
Information bias (Synonym: measurement bias, assessment bias.) Error due to systematic
differences in the measurement or classification of study participants. See observer bias,
responder bias, misclassification.
Informed consent Voluntary agreement to participate in an epidemiological study after
receiving sufficient details of the aims,methods,and potential risks and benefits of the study.
Intention-to-treat analysis In intervention studies: subjects are analysed on the basis of
initial intervention allocation irrespective of whether they complied with this allocation.
Interaction See effect modification.
Interim analysis Independent analysis of a randomized-controlled trial before the planned
finish in the case of safety concerns or lack of study power to detect an effect.
Intervention The preventive or therapeutic measure under study in an intervention study.
Also refers to medical or public health involvement to change the developmental process
of an outcome.
Intervention efficacy A measure of the proportion of incidence of an outcome that can
be prevented by an intervention. See also protective efficacy.
Intervention study Analytical study designed to test whether there is a causal relation-
ship by reducing/removing exposure to a risk factor, or increasing/introducing exposure to
a protective factor, and observing the effect on the outcome. Randomized-controlled trial is an
example of an intervention study design. (Contrast: observational study.)
Latent Time between acquiring an outcome and appearance of symptoms.
Lead-time bias A type of bias resulting from the time difference between detection of
an outcome or risk factor, and the appearance of symptoms, that may lead to an apparent
increase in survival time even if there is no effect on the outcome.
Length-time bias A type of bias resulting from differences in the length of time taken for an
outcome to progress to severe effects,that may affect the apparent efficacy of a screening method.
23346.indb 17423346.indb 174 22/08/2011 15:1222/08/2011 15:12

Glossary 175
Masking See blinding.
MatchingA technique used to control for confounding during study design.The comparison
groups are selected to have the same distribution of potential confounders by matching
individually (pair matching) or at a group-level (frequency matching).
Measurement bias See information bias.
Minimization Method of allocation that aims to minimize differences between the inter-
vention and control arms in a small randomized-controlled trial where there may be several
confounders or effect modifiers.
Necessary cause A component cause that is essential for an outcome to occur.
Negative predictive value The proportion of individuals identified as not having an out-
come by a screening or diagnostic method that truly do not have the outcome. See positive
predictive value, screening, sensitivity, specificity.
Nested case-control study Case-control study where cases and controls are identified from
a prospective cohort study, reducing problems of information bias.
Non-differential misclassification Incorrect classification of exposure or outcome of
study subjects as a result of information bias, where this does not vary between comparison
groups.This can lead to an underestimation of the strength (statistical significance) of an
association.
Notifiable disease A disease that is required by law to be reported to government
authorities to enable national surveillance.
Null hypothesis A falsifiable hypothesis against which to statistically test data. Usually,
that there is no association between an exposure and outcome. (Contrast: alternative
hypothesis.)
Observational study Analytical study in which the role of the investigator is to observe
the relationship between an exposure and outcome. Ecological, cross-sectional, cohort and case-
control are examples of observational study designs. (Contrast: intervention study.)
Observer bias Information bias introduced by those measuring or assessing the outcome.
Occupational cohort A group of individuals selected for prospective study on the basis of
a shared occupation.
Odds (of exposure) The number of individuals in a defined population exposed to a
particular risk factor, divided by the number of individuals not exposed to that risk factor in
the same population.
Odds (of outcome) The number of new cases of an outcome that develop in a defined
population of individuals at risk during a specified period of time, divided by the number
of individuals who do not develop the outcome during the same time-period. It can be
interpreted as the ratio of the risk that the outcome will occur to the risk that it will not
occur during a specified period of time.
Odds ratio (of exposure) Calculated as the odds of exposure in those with the outcome,
divided by the odds of exposure in those without the outcome. Used in case-control studies
as an estimate of the relative risk, because incidence cannot be measured.
Odds ratio (of outcome) A measure of relative risk. Calculated as the odds of outcome
in those exposed, divided by the odds of outcome in those unexposed.
Outbreak A sudden epidemic, usually of short duration. See epidemic.
Outcome A health state or event of interest such as infection, illness, disability, or death,
or a health indicator such as high blood pressure or presence of antibodies. Can also be
specified as the opposite of any of these.
23346.indb 17523346.indb 175 22/08/2011 15:1222/08/2011 15:12

176 Glossary
Overmatching In a case-control study: where matching results in cases and controls that are
too similar with respect to the exposure of interest to enable detection of an association
with outcome.
P-value The numerical probability that an observed value or estimated association from a
sample occurred by chance alone, and that it does not exist in the population from which
the sample was selected.
Pandemic An epidemic that is occurring in populations over a large number of countries
or worldwide.
Passive surveillance The surveillance of an outcome by detection of cases when they seek
healthcare.
Per-protocol analysis In intervention studies: subjects are analysed on the basis of actual
compliance with initial intervention allocation.
Period prevalence The number of existing cases of an outcome in a defined population dur-
ing a specified (short) period of time divided by the total number of people in that population
during the same time-period. It is a proportion.
Person-time at risk The sum of the time each individual in a defined population is at risk
of an outcome. It is used as a denominator in the calculation of incidence rates.
Pilot study A small-scale study conducted prior to the main study to test methods, data
collection, data entry, etc.
Placebo An inert medication or procedure that may be given to the control group in an
intervention trial, specified as a placebo-controlled trial.
Plausibility studies A type of intervention study designed to examine whether an interven-
tion might reasonably be considered to reduce a particular outcome.Due to practical or ethical
limitations, the methods for reducing the effects of chance, bias and confounding are not as
rigorous as with a randomized-controlled trial. Mostly used to evaluate the effectiveness of an
intervention or healthcare programme.
Point prevalence (Synonym: prevalence.) The number of existing cases of an outcome in a
defined population at a particular point in time divided by the total number of people in that
population at the same time. It is a proportion.
Population Individuals with a shared characteristic (usually geographic area). See general
population, sample population, target population.
Population attributable fraction (Synonym: population attributable risk percentage.) A
measure that calculates the population attributable risk as a proportion of the incidence of
outcome in the population, i.e. the proportion of cases in the population that may be due
to the exposure, and that could be prevented if the exposure were eliminated completely.
Population attributable risk A measure that calculates the additional incidence of out-
come in the population after subtracting the incidence that would have occurred in the
absence of exposure (i.e. in those unexposed). (See also attributable risk.)
Population attributable risk percentage See population attributable fraction.
Positive predictive valueThe proportion of individuals identified as having an outcome by
a screening or diagnostic method that truly have the outcome. See negative predictive value,
screening, sensitivity, specificity.
Power The statistical probability of detecting an association if it is real.
Precision The statistical probability of detecting an association by chance (i.e. if it is
not real).
23346.indb 17623346.indb 176 22/08/2011 15:1222/08/2011 15:12

Glossary 177
Prevalence See point prevalence and period prevalence.
Prevalence ratio An estimate of the magnitude of association between exposure and preva-
lence of an outcome.Calculated as the prevalence of outcome in those exposed to a particular
risk factor, divided by the prevalence of outcome in those unexposed.
Preventable fraction A measure that calculates the additional incidence of outcome
in those unexposed to a protective factor after subtracting the incidence that would have
occurred in the presence of exposure (i.e.in those exposed).It is calculated by subtracting the
relative risk from 1. (Contrast: attributable fraction.) See also protective efficacy.
Prevention paradox The concept that a large reduction in exposure among a few individu-
als at high risk of an outcome may not have as great an impact at the population-level as a slight
reduction in exposure by many individuals.
Primary prevention Intervention to prevent the onset of an outcome by removing or
reducing exposure. (Contrast: secondary prevention, tertiary prevention.)
Prognosis A medical term used to describe the likely end result (e.g. survival, recovery)
of an outcome.
Proportion The relationship between two numbers of the same type where one is a part
and the other the whole. By definition, it can only take values between 0 and 1 (or between
0 per cent and 100 per cent if expressed as a percentage). See prevalence, risk.
Prospective cohort Cohort study in which on-going data collection enables measurement
of incidence after exposure has been recorded. (Contrast: retrospective cohort.)
Protective efficacy A measure of the proportion of incidence of an outcome that can be
prevented by a protective factor. See also preventable fraction.
Protective factor (Synonym: protective risk factor.) A risk factor that is associated with a
decreased probability of a negative health outcome. (Contrast: risk factor.)
Random allocation See randomization.
Random error The variation of an observed sample value from the true population value
due to chance alone.
Random selection Selection in a random (unpredictable) manner where each study unit
(person, village, school) has an equal (or known) probability of being selected.
Randomization Where allocation to intervention groups is determined by chance, i.e. each
study unit has the same probability of being allocated to each of the intervention groups,
and the probability that a given unit will receive a particular intervention is independent
of the probability that any other unit will receive the same intervention. (See randomized
controlled trial.)
Randomized-controlled trial An intervention study in which the intervention is compared
to a control, and allocation of intervention is by randomization.
RateThe relationship between two numbers of different types. In epidemiology it refers to
the occurrence of events per unit time. See incidence rate.
Rate difference See attributable risk.
Rate ratio See incidence rate ratio.
Ratio The relationship between two numbers of the same type, either expressed as
a:b or a/b.See prevalence ratio,risk ratio,odds ratio,incidence rate ratio,standardized mortality ratio.
Reference category The group against which all others are compared.This is usually the
unexposed group.
23346.indb 17723346.indb 177 22/08/2011 15:1222/08/2011 15:12

178 Glossary
Regression Statistical modelling to explain how much variation in one variable may be the
result of other variables. It enables us to estimate the association between exposure and
outcome, adjusting for the effects of confounding and effect modification.
Relative risk An estimate of the magnitude of association between exposure and incidence
of an outcome. It can be interpreted as the likelihood of developing an outcome in those
exposed compared to those unexposed. It can be calculated as risk ratio, odds ratio and
incidence rate ratio.
Representative sample A sample that has the same characteristics as the population from
which it was selected.
Residual confounding The effects of confounding that remain even after adjustment
because data on the confounder are not sufficiently accurate.
Responder bias Information bias introduced by study participants, or those providing
relevant information on study participants.
Restriction A technique used to control for confounding during study design. It limits the
study to people who are similar in relation to the confounder.
Retrospective cohort Cohort study in which historical data are collected and there is no
follow-up of study participants. (Contrast: prospective cohort.)
Reverse causality A situation in which an apparent risk factor may be a consequence of
the outcome.
Risk (Synonym: cumulative incidence.) The number of new cases of an outcome that develop
in a defined population of individuals at risk during a specified period of time, divided by the
total number of individuals at risk during the same period of time. It is a proportion and can
be interpreted as the probability that the outcome will occur within a specified time.
Risk factor (Synonym: exposure.) An environmental (e.g. radiation), socio-economic
(e.g. occupation), behavioural (e.g. alcohol consumption), physical (e.g. height) or inherited
(e.g. blood group) factor that is associated with an increased probability of a negative health
outcome. (Contrast: protective risk factor.)
Risk ratio A measure of relative risk. Calculated as the risk of outcome in those exposed,
divided by the risk of outcome in those unexposed.
Sample A subset of a population selected for study.
Sample population Subjects selected for epidemiological study from a wider population.
See general population.
Sample size The number of study units (individuals, groups) under study.
Screening The systematic detection of an outcome or indicators of increased risk for an
outcome among apparently healthy people.
Secondary attack rate A specific type of risk:the number of new cases of an outcome that
develop among contacts of an initial case during a specified period of time, divided by the
total number of contacts at risk during the same period of time.
Secondary prevention Intervention to prevent the development of adverse health conse-
quences of an established outcome. (Contrast: primary prevention, tertiary prevention.)
Secular trends Changes in the frequency of an outcome or exposure in a population over
time that are expected to be long-term.
Selection bias Error due to systematic differences in characteristics between the study
participants and the population from which they are selected, or between the groups being
compared within the study.
23346.indb 17823346.indb 178 22/08/2011 15:1222/08/2011 15:12

Glossary 179
Sensitivity (Synonym: true positive ‘rate’.) The proportion of individuals who truly have
an outcome that are correctly identified by a screening or diagnostic method. (Contrast:
specificity.)
Sentinel surveillance The surveillance of an outcome by detecting cases through desig-
nated institutions with quality control of diagnosis and reporting.
Specificity (Synonym: true negative ‘rate’.) The proportion of individuals who truly do not
have an outcome that are correctly identified by a screening or diagnostic method. (Contrast:
sensitivity.)
Standard population A population with a defined demographic structure.
Standardization (direct) A technique to remove demographic differences between pop-
ulations so that they may be compared. The direct method applies the category-specific
incidence rates of the study population to a standard population structure.
Standardization (indirect) A technique to remove demographic differences between
populations so that they may be compared. The indirect method applies the category-
specific incidence rates of a standard population to the study population structure.This is used
to calculate the standardized mortality (or morbidity) ratio.
Standardized mortality/morbidity ratio A comparative measure of the difference in
outcome incidence between two populations if they had had the same population demo-
graphic structure.
Standardized rate The expected incidence rate in a population if it had the same demo-
graphic structure as another population (or standard population) enabling comparison of
different populations.This is obtained by standardization. (Contrast: crude rate.)
Statistical modelling Definition of the relationship between two variables using
mathematical descriptions. See regression.
Statistical significance The probability that a result did not occur by chance. See P-value.
Stratification The process of separating a sample into several sub-samples according to
specified criteria.It can be used to control for confounding during analysis,or to detect effect
modification.
Subject An individual or group participating in a study.
Subjects Units of an epidemiological study.These may be, for example, individuals, house-
holds, communities, geographical areas, countries.
Sufficient cause A factor or set of factors that inevitably produces the outcome.
Surveillance The monitoring of outcomes in a given population over time.
Susceptible An individual that is at risk of acquiring the outcome of interest. For example,
for many infectious diseases to which immunity is acquired,an immune individual is no longer
susceptible to infection.This may also apply to individuals with certain genetic characteristics.
Symptoms Changes noticed by a patient that indicate the presence of an adverse health
outcome.
Systematic Method that is non-random, ordered or organized.
Target population The population to which the results of an epidemiological study are
to be extrapolated, or to which a public health intervention is to be applied.This may be a
subset or the whole of the general population.
Tertiary prevention Intervention to reduce progression of an established outcome and
prevent complications or more severe consequences. (Contrast: primary prevention, second-
ary prevention.)
23346.indb 17923346.indb 179 22/08/2011 15:1222/08/2011 15:12

180 Glossary
True negative rate See specificity. Note this is an incorrect usage of the term rate.
True positive rate See sensitivity. Note this is an incorrect usage of the term rate.
Unexposed Those subjects who have not experienced or do not possess (e.g. genetic or
physical characteristics) the risk factor of interest.
Vaccine efficacy A measure of the proportion of incidence of an outcome that can be
prevented by administration of a vaccine. See also protective efficacy.
Washout period Period after an intervention has been removed during which its effect
declines.
23346.indb 18023346.indb 180 22/08/2011 15:1222/08/2011 15:12

Page numbers in italics refer to figures and tables.
Index
Abdulla S, et al. 95, 96
active surveillance 159
acute lower respiratory infections
(ALRI) 163, 168
age standardization 80–5
age-specific mortality 82–5
activities and feedback 85–7,
89–91
Ahmad OB, et al. 82, 83, 84
air pollution and pregnancy outcomes
87–8, 91
alcohol consumption and breast cancer
114–17
alternative explanations 8, 49, 53
confounding 8, 47–9, 85
see also bias
analogy argument for causality 51
analytical studies
and descriptive studies 6–7
design 8–9
types 60
ascertainment bias 126, 156
association
activities and feedback 31–2, 35–42,
51–2, 53–5
comparability of measures 31
see also causality; risk
attributable risk, measures of 33–5
Bailey L, et al 20, 23, 33, 37, 85, 86,
105, 145
bar charts 67, 68
bias 8, 45–7, 85
ascertainment 126, 156
information 46–7
lead-time 144
length-time 145
observer 46–7, 105, 126–7
selection 45–6, 104, 144
birth and death registries 79–80,
157–8
blinding 126–7
observer bias and 46–7, 126–7
Bobak M and Leon DA 87–8
cancer
breast, alcohol consumption and
114–17
cervical, human papilloma virus
(HPV) and 150, 154
childhood, radiation and 88, 91–2
lung, smoking and 35–6, 39–40, 105,
107–8
Carneiro I 6, 7, 28, 33, 44, 61, 68, 82,
83, 84, 101, 109, 121, 123, 141,
145, 148
case definition 17
case-control studies 9
activities and feedback 114–17
advantages and disadvantages 61,
110–11
analysis 113–14
data collection 113
defining features 110
genetic epidemiology 111
interpretation 114
matching 111, 112–13
sampling 111–13
study design 111
causality 7–8
inferring 8, 49–52
reverse 95, 112
Centers for Disease Control and
Prevention, USA 156, 157, 158,
161
chance 44
cholera 10–14, 15–16
cholesterol levels, population
distribution 149, 153–4
cluster sampling 64
cluster-randomized trials 122–3
coherence of association 50
cohort studies 9, 61
107–9
analysis 103–4
data collection 103
defining features 100–1
interpretation 104–5
sampling 102–3
types 101–2
component causes 8
confidence interval 44, 45
confounding 8, 47–9, 85
consistency of association 50
critical appraisal 43
cross-sectional studies 9, 61
activities and feedback 95–7, 98–9
analysis 95
data collection 94–5
interpretation 95
sampling 94
study design 93–4
crossover design 123–4
cumulative incidence see risk
Cutts FT, et al. 129
data analysis 67–8, 69, 80–5, 95, 103–4,
113–14, 127–8
data collection 65–6, 77, 94–5, 103,
113, 127
data management 66–7
data sources 6, 77–80, 155–8, 159–60
data variables 67
demographics see population
descriptive studies 9, 59–60
and analytical studies 6–7
diabetes screening 146, 151–3
differential miscalculation 46
direct data collection methods 65, 66
direct standardization 81–2
disease frequency measurement 18–21
activities and feedback 21–6
disease registries 80, 160
dissemination of results 70
Doll R
et al. 105
and Hill AB 59
and Peto R 35–6, 105
dose–response association 50
dose–response profiles 139–40, 140,
150–1
double-blind studies 127
23346.indb 18123346.indb 181 22/08/2011 15:1222/08/2011 15:12

182 Index
ecological fallacy 85
ecological studies 9
75–6
analysis (standardization) 80–5
data collection 77
data sources 77–80
interpretation 85
sampling 77
study design 76–7
effect modification 70
effectiveness
efficacy and 5, 120, 128
measuring 144–6, 165
environmental data collection 65–6
epidemic-warning systems 161–2
epidemiology
application 9–10
definition 5–6
study 6–9
ethical issues 119–20, 143
evaluation, monitoring and 164–6
exclusion and inclusion criteria 46, 64
exposure 8
and outcome 8, 9, 28, 33
factorial design 123
follow-up 100–1
loss to 20, 46, 102–3, 104
forest plots 70, 71
frequency
and pattern of outcomes 5
see also disease frequency
measurement
Gambia Hepatitis Study Group 121–2
genetic epidemiology 111
geographic controls 121–2
geographical information systems
(GIS) 66
global positioning system (GPS) 65–6
Hanson K, et al. 166
Hatch M and Susser M 88
health facilities data 159–60
health information systems (HIS) 155
see also data sources
heart disease see smoking
Heller RF, et al. 148
high-risk individuals 146–7
Hill AB 49–51
histograms 67, 68
historical controls 120–1
HIV 22–3, 25–6, 85–6, 89–90
and TB 105–6, 108–9
human papilloma virus (HPV) and
cancer 150, 154
hypotheses 8, 68
incidence/incidence rate 18–21
person-time at risk and 20–1
ratio 30–1, 33, 41–2
inclusion and exclusion criteria 46, 64
indirect standardization 83–5
infectious disease surveillance 160–2
influenza A (H5N1) 115, 117
information bias 46–7
informed consent 64–5
insecticide-treated nets (ITNs) 95–6,
98–9, 166, 169–70
intention-to-treat (ITT) vs. per-
protocol 128
interim analysis 127
interpretation 95, 104–5, 114, 128–9
intervention studies 9
119
efficacy and effectiveness 120
ethical approval 119–20
plausibility studies 120–2, 165
study design 119–20
see also randomized-controlled trials
(RCTs)
intestinal worm infection in adoles-
cents 22, 24–5
lead-time bias 144
leishmaniasis treatment comparison 51,
53–4
length-time bias 145
loss to follow-up 20, 46, 102–3, 104
malaria
insecticide-treated nets (ITNs) 95–6,
98–9, 166, 169–70
monitoring and evaluation of
intervention 166, 169–70
prevalence 21, 24
matching 48, 111, 112–13
maternal depression and infant
nutritional status 51, 54
measles risk and secondary attack rate
22, 24
mental disorder in adolescents 96–7, 99
meta-analysis 70, 71
minimization 126
mixed study design 76, 77
mixing: interpretation of ecological
studies 85
monitoring and evaluation 164–6
monkeypox risk and secondary attack
rate 21, 24
mortality
data 79–80, 157–8
see also age-specific mortality
multi-group study design 76–7
multi-stage sampling 63–4
necessary causes 7
nested case-control studies 111
non-differential miscalculation 46
nosocomial infections 163–4, 168–9
notifiable diseases 160–2
observational studies 9
observer bias 105
and blinding 46–7, 126–7
occupational cohort studies 45–6, 102
odds 19–20
odds ratio 29–30, 38, 39, 95
of exposure 29–30, 41
opportunistic controls 122
osteoporosis and exercise association
31–2, 37–9, 52, 55
outbreak 157
response 162–4
outcomes
and exposure 8, 9, 28, 33
frequency and pattern of 5
overmatching 112–13
P-value 44–5, 68
passive surveillance 159
period prevalence 94
person-time at risk, incidence rate and
20–1
Pillai A, et al. 96–7
placebo effect 47, 124–5, 127
plausibility of association 50
plausibility studies 120–2, 165
population
approach and prevention paradox
147–8
attributable risk and fraction 34–5
-based data 78–9, 157–8
predictive values 142
prevalence 18
prevalence ratio 28, 95
prevention strategies
activities and feedback 140, 149–54
choice of approach 148
23346.indb 18223346.indb 182 22/08/2011 15:1222/08/2011 15:12

Index 183
dose–response profiles 139–40
high-risk individuals, targeting 146–7
prevention paradox and population
approach 147–8
primary 137–8
secondary 138
tertiary 138
see also screening
prospective cohorts 101–2
protective factors 5–6
public health policy and practice
166–7
public health surveillance 158–63
health facilities data 159–60
infectious disease 160–2
outbreak response 162–4
registry data 160
types 159
radiation and childhood cancer 88,
91–2
random allocation 125–6
random selection 63, 65, 73
randomization 8, 48
randomized-controlled trials (RCTs)
122
131–4
allocation 125–6
analysis 127–8
blinding 126–7
choice of control 124–5
cluster-randomized 122–3
crossover design 123–4
data collection 127
factorial design 123
interpretation 128–9
sampling 124
screening 145–6
reference category 69–70
registry data
disease 80, 160
vital 79–80, 157–8
regression models 69–70
relative measures of association/
relative risk 27–32, 33, 34
residual confounding 48–9
restriction 48
retrospective cohorts 102
reverse causality 95, 112
reversibility of association 50
rheumatic fever 14, 15
RiftValley Fever (RVF) 164, 169
risk 19
measures of attributable 33–5
person-time at 20–1
relative 27–32, 33, 34
targeting high-risk individuals
146–7
risk factors 5–6, 7, 8, 9
risk ratio 28–9, 38–9
road traffic crashes, injuries prevention
149, 154
Ronsmans C, et al. 104
routine data sources 77–80, 155–8
sample size 8, 44, 62–3
sampling methods 63–4, 77, 94, 102–3,
111–13, 124
scatter plots 67–8, 69
school-based health promotion
package and use of health
services 52, 54–5
screening 140–6
criteria 143–4
ethical issues 143
measuring effectiveness 144–6
predictive values 142
sensitivity and specificity 141–2
seasonal trends 156
secondary attack rate 19, 21, 22, 24
secondary prevention strategies
138
secular trends 156
selection bias 45–6, 104, 144
selection criteria 64
sensitivity and specificity 141–2
sentinel surveillance 162
smoking
lung cancer and ischaemic heart
disease (IDH) 35–6, 39–40, 105,
107–8
myocardial infarction (MI) 36, 41
Snow J 10, 11–14, 16
Sonnenberg P, et al. 105–6, 109
specificity of association 51
standardization 80–5
standardized mortality ratio (SMR)
83–5
statistical modelling 48
regression analysis 69–70
statistical power and precision 62–3
statistical probability (P-value) 44–5, 68
stratification 48
stratified sampling 63
strength of association 50
study design
choice of 59–62
components 62–70
key features, advantages and
disadvantages 61
see also specific study designs
sufficient causes 7
surveillance see data sources; public
health surveillance
Taranta A and Markowitz M 7
TB and ethnicity 36–7, 41–2
temporality of association 50
time-series analysis 103–4
time-trend study design 76, 77
tuberculosis (TB) and HIV 105–6, 108–9
unique identifiers 66
washout period 123–4
Weiss HA 51
et al. 71
Wilson JM and JungnerYG 143, 144
World Health Organization (WHO)
10, 76–7, 78, 79, 80, 82, 84, 143,
144, 162–3
23346.indb 18323346.indb 183 22/08/2011 15:1222/08/2011 15:12

23346.indb 18423346.indb 184 22/08/2011 15:1222/08/2011 15:12

introduction to epidemiology (2011, mc-graw-hill_open university press)

More Related Content

What's hot (20)

Similar to introduction to epidemiology (2011, mc-graw-hill_open university press) (20)

More from Abdiwali Abdullahi Abdiwali (20)

Recently uploaded (20)

introduction to epidemiology (2011, mc-graw-hill_open university press)