Strengthening the Reporting of Observational
Studies in Epidemiology (STROBE): Explanation
Jan P. Vandenbroucke1, Erik von Elm2,3, Douglas G. Altman4, Peter C. Gøtzsche5, Cynthia D. Mulrow6, Stuart J. Pocock7,
Charles Poole8, James J. Schlesselman9, Matthias Egger2,10*for the STROBE Initiative
1 Department of Clinical Epidemiology, Leiden University Medical Center, Leiden, The Netherlands, 2 Institute of Social & Preventive Medicine (ISPM), University of Bern, Bern,
Switzerland, 3 Department of Medical Biometry and Medical Informatics, University Medical Centre, Freiburg, Germany, 4 Cancer Research UK/NHS Centre for Statistics in
Medicine, Oxford, United Kingdom, 5 Nordic Cochrane Centre, Rigshospitalet, Copenhagen, Denmark, 6 University of Texas Health Science Center, San Antonio, United
States of America, 7 Medical Statistics Unit, London School of Hygiene and Tropical Medicine, London, United Kingdom, 8 Department of Epidemiology, University of North
Carolina School of Public Health, Chapel Hill, United States of America, 9 Department of Biostatistics, University of Pittsburgh Graduate School of Public Health, and
University of Pittsburgh Cancer Institute, Pittsburgh, United States of America, 10 Department of Social Medicine, University of Bristol, Bristol, United Kingdom
Funding: The initial STROBE
workshop was funded by the
European Science Foundation (ESF).
Additional funding was received
from the Medical Research Council
Health Services Research
Collaboration and the National
Health Services Research &
Programme. The funders had no role
in study design, data collection and
analysis, decision to publish, or
preparation of the manuscript.
Competing Interests: The authors
have declared that no competing
Citation: VandenbrouckeJP, vonElm
E, Altman DG, Gøtzsche PC, Mulrow
CD, et al. (2007) Strengthening the
Reporting ofObservational Studies in
Epidemiology (STROBE): Explanation
and Elaboration. PLoS Med 4(10):
Received: July 20, 2007
Accepted: August 30, 2007
Published: October 16, 2007
Copyright: ? 2007 Vandenbroucke
et al. This is an open-access article
distributed under the terms of the
Creative Commons Attribution
License, which permits unrestricted
use, distribution, and reproduction in
any medium, provided the original
author and source are credited. In
order to encourage dissemination of
the STROBE Statement, this article is
freely available on the Web site of
PLoS Medicine, and will also be
published and made freely available
by Epidemiology and Annals of
Internal Medicine. The authors jointly
hold the copyright of this article. For
details on further use, see STROBE
Web site (http://www.
Abbreviations: CI, confidence
interval; RERI, Relative Excess Risk
from Interaction; RR, relative risk;
STROBE, Strengthening the
Reporting of Observational Studies
* To whom correspondence should
be addressed. E-mail: strobe@ispm.
A B S T R A C T
Much medical research is observational. The reporting of observational studies is often of
insufficient quality. Poor reporting hampers the assessment of the strengths and weaknesses of
a study and the generalisability of its results. Taking into account empirical evidence and
theoretical considerations, a group of methodologists, researchers, and editors developed the
Strengthening the Reporting of Observational Studies in Epidemiology (STROBE) recommen-
dations to improve the quality of reporting of observational studies. The STROBE Statement
consists of a checklist of 22 items, which relate to the title, abstract, introduction, methods,
results and discussion sections of articles. Eighteen items are common to cohort studies, case-
control studies and cross-sectional studies and four are specific to each of the three study
designs. The STROBE Statement provides guidance to authors about how to improve the
reporting of observational studies and facilitates critical appraisal and interpretation of studies
by reviewers, journal editors and readers. This explanatory and elaboration document is
intended to enhance the use, understanding, and dissemination of the STROBE Statement. The
meaning and rationale for each checklist item are presented. For each item, one or several
published examples and, where possible, references to relevant empirical studies and
methodological literature are provided. Examples of useful flow diagrams are also included.
The STROBE Statement, this document, and the associated Web site (http://www.
strobe-statement.org/) should be helpful resources to improve reporting of observational
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P PL Lo oS S MEDICINE
Rational health care practices require knowledge about the
aetiology and pathogenesis, diagnosis, prognosis and treat-
ment of diseases. Randomised trials provide valuable evi-
dence about treatments and other interventions. However,
much of clinical or public health knowledge comes from
observational research . About nine of ten research papers
published in clinical speciality journals describe observatio-
nal research [2,3].
The STROBE Statement
Reporting of observational research is often not detailed
and clear enough to assess the strengths and weaknesses of
the investigation [4,5]. To improve the reporting of obser-
vational research, we developed a checklist of items that
should be addressed: the Strengthening the Reporting of
Observational Studies in Epidemiology (STROBE) Statement
(Table 1). Items relate to title, abstract, introduction,
methods, results and discussion sections of articles. The
STROBE Statement has recently been published in several
journals . Our aim is to ensure clear presentation of what
was planned, done, and found in an observational study. We
stress that the recommendations are not prescriptions for
setting up or conducting studies, nor do they dictate
methodology or mandate a uniform presentation.
STROBE provides general reporting recommendations for
descriptive observational studies and studies that investigate
associations between exposures and health outcomes.
STROBE addresses the three main types of observational
studies: cohort, case-control and cross-sectional studies.
Authors use diverse terminology to describe these study
designs. For instance, ‘follow-up study’ and ‘longitudinal
study’ are used as synonyms for ‘cohort study’, and
‘prevalence study’ as synonymous with ‘cross-sectional study’.
We chose the present terminology because it is in common
use. Unfortunately, terminology is often used incorrectly 
or imprecisely . In Box 1 we describe the hallmarks of the
three study designs.
The Scope of Observational Research
Observational studies serve a wide range of purposes: from
reporting a first hint of a potential cause of a disease, to
verifying the magnitude of previously reported associations.
Ideas for studies may arise from clinical observations or from
biologic insight. Ideas may also arise from informal looks at
data that lead to further explorations. Like a clinician who
has seen thousands of patients, and notes one that strikes her
attention, the researcher may note something special in the
data. Adjusting for multiple looks at the data may not be
possible or desirable , but further studies to confirm or
refute initial observations are often needed . Existing data
may be used to examine new ideas about potential causal
factors, and may be sufficient for rejection or confirmation.
In other instances, studies follow that are specifically
designed to overcome potential problems with previous
reports. The latter studies will gather new data and will be
planned for that purpose, in contrast to analyses of existing
data. This leads to diverse viewpoints, e.g., on the merits of
looking at subgroups or the importance of a predetermined
sample size. STROBE tries to accommodate these diverse uses
of observational research - from discovery to refutation or
confirmation. Where necessary we will indicate in what
circumstances specific recommendations apply.
How to Use This Paper
This paper is linked to the shorter STROBE paper that
introduced the items of the checklist in several journals ,
and forms an integral part of the STROBE Statement. Our
intention is to explain how to report research well, not how
research should be done. We offer a detailed explanation for
each checklist item. Each explanation is preceded by an
example of what we consider transparent reporting. This
does not mean that the study from which the example was
taken was uniformly well reported or well done; nor does it
mean that its findings were reliable, in the sense that they
were later confirmed by others: it only means that this
particular item was well reported in that study. In addition to
explanations and examples we included Boxes 1–8 with
supplementary information. These are intended for readers
who want to refresh their memories about some theoretical
points, or be quickly informed about technical background
details. A full understanding of these points may require
studying the textbooks or methodological papers that are
STROBE recommendations do not specifically address
topics such as genetic linkage studies, infectious disease
modelling or case reports and case series [11,12]. As many of
the key elements in STROBE apply to these designs, authors
who report such studies may nevertheless find our recom-
mendations useful. For authors of observational studies that
specifically address diagnostic tests, tumour markers and
genetic associations, STARD , REMARK , and STRE-
GA  recommendations may be particularly useful.
The Items in the STROBE Checklist
We now discuss and explain the 22 items in the STROBE
checklist (Table 1), and give published examples for each
item. Some examples have been edited by removing citations
or spelling out abbreviations. Eighteen items apply to all
three study designs whereas four are design-specific. Starred
items (for example item 8*) indicate that the information
should be given separately for cases and controls in case-
control studies, or exposed and unexposed groups in cohort
and cross-sectional studies. We advise authors to address all
items somewhere in their paper, but we do not prescribe a
precise location or order. For instance, we discuss the
reporting of results under a number of separate items, while
recognizing that authors might address several items within a
single section of text or in a table.
TITLE AND ABSTRACT
1 (a). Indicate the study’s design with a commonly used
term in the title or the abstract.
‘‘Leukaemia incidence among workers in the shoe and boot
manufacturing industry: a case-control study’’ .
Readers should be able to easily identify the design that was
used from the title or abstract. An explicit, commonly used
term for the study design also helps ensure correct indexing
of articles in electronic databases [19,20].
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STROBE Explanation and Elaboration
Table 1. The STROBE Statement—Checklist of Items That Should Be Addressed in Reports of Observational Studies
TITLE and ABSTRACT1 (a) Indicate the study’s design with a commonly used term in the title or the abstract
(b) Provide in the abstract an informative and balanced summary of what was done and what was found
2 Explain the scientific background and rationale for the investigation being reported
3State specific objectives, including any prespecified hypotheses
Present key elements of study design early in the paper
Describe the setting, locations, and relevant dates, including periods of recruitment, exposure, follow-up, and data collection
(a) Cohort study—Give the eligibility criteria, and the sources and methods of selection of participants. Describe methods of
Case-control study—Give the eligibility criteria, and the sources and methods of case ascertainment and control selection. Give
the rationale for the choice of cases and controls
Cross-sectional study—Give the eligibility criteria, and the sources and methods of selection of participants
(b) Cohort study—For matched studies, give matching criteria and number of exposed and unexposed
Case-control study—For matched studies, give matching criteria and the number of controls per case
Clearly define all outcomes, exposures, predictors, potential confounders, and effect modifiers. Give diagnostic criteria, if applicable
For each variable of interest, give sources of data and details of methods of assessment (measurement).
Describe comparability of assessment methods if there is more than one group
Describe any efforts to address potential sources of bias
Explain how the study size was arrived at
Explain how quantitative variables were handled in the analyses. If applicable, describe which groupings were chosen, and why
12 (a) Describe all statistical methods, including those used to control for confounding
(b) Describe any methods used to examine subgroups and interactions
(c) Explain how missing data were addressed
(d) Cohort study—If applicable, explain how loss to follow-up was addressed
Case-control study—If applicable, explain how matching of cases and controls was addressed
Cross-sectional study—If applicable, describe analytical methods taking account of sampling strategy
(e) Describe any sensitivity analyses
Participants13*(a) Report the numbers of individuals at each stage of the study—e.g., numbers potentially eligible, examined for eligibility, confirmed
eligible, included in the study, completing follow-up, and analysed
(b) Give reasons for non-participation at each stage
(c) Consider use of a flow diagram
(a) Give characteristics of study participants (e.g., demographic, clinical, social) and information on exposures and potential
(b) Indicate the number of participants with missing data for each variable of interest
(c) Cohort study—Summarise follow-up time (e.g., average and total amount)
Cohort study—Report numbers of outcome events or summary measures over time
Case-control study—Report numbers in each exposure category, or summary measures of exposure
Cross-sectional study—Report numbers of outcome events or summary measures
(a) Give unadjusted estimates and, if applicable, confounder-adjusted estimates and their precision (e.g., 95% confidence interval).
Make clear which confounders were adjusted for and why they were included
(b) Report category boundaries when continuous variables were categorized
(c) If relevant, consider translating estimates of relative risk into absolute risk for a meaningful time period
Report other analyses done—e.g., analyses of subgroups and interactions, and sensitivity analyses
Summarise key results with reference to study objectives
Discuss limitations of the study, taking into account sources of potential bias or imprecision. Discuss both direction and magnitude
of any potential bias
Give a cautious overall interpretation of results considering objectives, limitations, multiplicity of analyses, results from similar stu-
dies, and other relevant evidence
Discuss the generalisability (external validity) of the study results
Funding22 Give the source of funding and the role of the funders for the present study and, if applicable, for the original study on which the
present article is based
*Give such information separately for cases and controls in case-control studies, and, if applicable, for exposed and unexposed groups in cohort and cross-sectional studies.
Note: An Explanation and Elaboration article discusses each checklist item and gives methodological background and published examples of transparent reporting. The STROBE checklist
is best used in conjunction with this article (freely available on the Web sites of PLoS Medicine at http://www.plosmedicine.org/, Annals of Internal Medicine at http://www.annals.org/, and
Epidemiology at http://www.epidem.com/). Separate versions of the checklist for cohort, case-control, and cross-sectional studies are available on the STROBE Web site at http://www.
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STROBE Explanation and Elaboration
1 (b). Provide in the abstract an informative and balanced
summary of what was done and what was found.
‘‘Background: The expected survival of HIV-infected patients
is of major public health interest.
Objective: To estimate survival time and age-specific mortal-
ity rates of an HIV-infected population compared with that
of the general population.
Design: Population-based cohort study.
Setting: All HIV-infected persons receiving care in Denmark
from 1995 to 2005.
Patients: Each member of the nationwide Danish HIV Cohort
Study was matched with as many as 99 persons from the
general population according to sex, date of birth, and
municipality of residence.
Measurements: The authors computed Kaplan–Meier life
tables with age as the time scale to estimate survival from age
25 years. Patients with HIV infection and corresponding
persons from the general population were observed from the
date of the patient’s HIV diagnosis until death, emigration, or
1 May 2005.
Results: 3990 HIV-infected patients and 379 872 persons
from the general population were included in the study,
yielding 22 744 (median, 5.8 y/person) and 2 689 287 (median,
8.4 years/person) person-years of observation. Three percent
of participants were lost to follow-up. From age 25 years, the
median survival was 19.9 years (95% CI, 18.5 to 21.3) among
patients with HIV infection and 51.1 years (CI, 50.9 to 51.5)
among the general population. For HIV-infected patients,
survival increased to 32.5 years (CI, 29.4 to 34.7) during the
2000 to 2005 period. In the subgroup that excluded persons
with known hepatitis C coinfection (16%), median survival
was 38.9 years (CI, 35.4 to 40.1) during this same period. The
relative mortality rates for patients with HIV infection
compared with those for the general population decreased
with increasing age, whereas the excess mortality rate
increased with increasing age.
Limitations: The observed mortality rates are assumed to
apply beyond the current maximum observation time of 10
Conclusions: The estimated median survival is more than 35
years for a young person diagnosed with HIV infection in the
late highly active antiretroviral therapy era. However, an
ongoing effort is still needed to further reduce mortality rates
for these persons compared with the general population’’
The abstract provides key information that enables
readers to understand a study and decide whether to read
the article. Typical components include a statement of the
research question, a short description of methods and
results, and a conclusion . Abstracts should summarize
key details of studies and should only present information
that is provided in the article. We advise presenting key
results in a numerical form that includes numbers of
participants, estimates of associations and appropriate
measures of variability and uncertainty (e.g., odds ratios
with confidence intervals). We regard it insufficient to state
only that an exposure is or is not significantly associated
with an outcome.
A series of headings pertaining to the background, design,
conduct, and analysis of a study may help readers acquire the
essential information rapidly . Many journals require such
structured abstracts, which tend to be of higher quality and
more readily informative than unstructured summaries
The Introduction section should describe why the study
was done and what questions and hypotheses it addresses. It
should allow others to understand the study’s context and
judge its potential contribution to current knowledge.
Box 1. Main study designs covered by STROBE
Cohort, case-control, and cross-sectional designs represent different
approaches of investigating the occurrence of health-related events in a
given population and time period. These studies may address many
types of health-related events, including disease or disease remission,
disability or complications, death or survival, and the occurrence of risk
In cohort studies, the investigators follow people over time. They obtain
information about people and their exposures at baseline, let time pass,
and then assess the occurrence of outcomes. Investigators commonly
make contrasts between individuals who are exposed and not exposed
or among groups of individuals with different categories of exposure.
Investigators may assess several different outcomes, and examine
exposure and outcome variables at multiple points during follow-up.
Closed cohorts (for example birth cohorts) enrol a defined number of
participants at study onset and follow them from that time forward,
often at set intervals up to a fixed end date. In open cohorts the study
population is dynamic: people enter and leave the population at
different points in time (for example inhabitants of a town). Open
cohorts change due to deaths, births, and migration, but the
composition of the population with regard to variables such as age
and gender may remain approximately constant, especially over a short
period of time. In a closed cohort cumulative incidences (risks) and
incidence rates can be estimated; when exposed and unexposed groups
are compared, this leads to risk ratio or rate ratio estimates. Open
cohorts estimate incidence rates and rate ratios.
In case-control studies, investigators compare exposures between
people with a particular disease outcome (cases) and people without
that outcome (controls). Investigators aim to collect cases and controls
that are representative of an underlying cohort or a cross-section of a
population. That population can be defined geographically, but also
more loosely as the catchment area of health care facilities. The case
sample may be 100% or a large fraction of available cases, while the
control sample usually is only a small fraction of the people who do not
have the pertinent outcome. Controls represent the cohort or population
of people from which the cases arose. Investigators calculate the ratio of
the odds of exposures to putative causes of the disease among cases
and controls (see Box 7). Depending on the sampling strategy for cases
and controls and the nature of the population studied, the odds ratio
obtained in a case-control study is interpreted as the risk ratio, rate ratio
or (prevalence) odds ratio [16,17]. The majority of published case-control
studies sample open cohorts and so allow direct estimations of rate
In cross-sectional studies, investigators assess all individuals in a sample
at the same point in time, often to examine the prevalence of exposures,
risk factors or disease. Some cross-sectional studies are analytical and aim
to quantify potential causal associations between exposures and disease.
Such studies may be analysed like a cohort study by comparing disease
prevalence between exposure groups. They may also be analysed like a
case-control study by comparing the odds of exposure between groups
with and without disease. A difficulty that can occur in any design but is
particularly clear in cross-sectional studies is to establish that an
exposure preceded the disease, although the time order of exposure
and outcome may sometimes be clear. In a study in which the exposure
variable is congenital or genetic, for example, we can be confident that
the exposure preceded the disease, even if we are measuring both at the
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STROBE Explanation and Elaboration
2. Background/rationale: Explain the scientific background
and rationale for the investigation being reported.
‘‘Concerns about the rising prevalence of obesity in
children and adolescents have focused on the well docu-
mented associations between childhood obesity and in-
creased cardiovascular risk and mortality in adulthood.
Childhood obesity has considerable social and psychological
consequences within childhood and adolescence, yet little is
known about social, socioeconomic, and psychological con-
sequences in adult life. A recent systematic review found no
longitudinal studies on the outcomes of childhood obesity
other than physical health outcomes and only two longitu-
dinal studies of the socioeconomic effects of obesity in
adolescence. Gortmaker et al. found that US women who had
been obese in late adolescence in 1981 were less likely to be
married and had lower incomes seven years later than women
who had not been overweight, while men who had been
overweight were less likely to be married. Sargent et al. found
that UK women, but not men, who had been obese at 16 years
in 1974 earned 7.4% less than their non-obese peers at age 23.
(...) We used longitudinal data from the 1970 British birth
cohort to examine the adult socioeconomic, educational,
social, and psychological outcomes of childhood obesity’’ .
The scientific background of the study provides important
context for readers. It sets the stage for the study and
describes its focus. It gives an overview of what is known on a
topic and what gaps in current knowledge are addressed by
the study. Background material should note recent pertinent
studies and any systematic reviews of pertinent studies.
3. Objectives: State specific objectives, including any
‘‘Our primary objectives were to 1) determine the
prevalence of domestic violence among female patients
presenting to four community-based, primary care, adult
medicine practices that serve patients of diverse socio-
economic background and 2) identify demographic and
clinical differences between currently abused patients and
patients not currently being abused ’’ .
Objectives are the detailed aims of the study. Well crafted
objectives specify populations, exposures and outcomes, and
parameters that will be estimated. They may be formulated as
specific hypotheses or as questions that the study was
designed to address. In some situations objectives may be
less specific, for example, in early discovery phases. Regard-
less, the report should clearly reflect the investigators’
intentions. For example, if important subgroups or addi-
tional analyses were not the original aim of the study but
arose during data analysis, they should be described accord-
ingly (see also items 4, 17 and 20).
The Methods section should describe what was planned and
what was done in sufficient detail to allow others to
understand the essential aspects of the study, to judge
whether the methods were adequate to provide reliable and
valid answers, and to assess whether any deviations from the
original plan were reasonable.
4. Study design: Present key elements of study design
early in the paper.
‘‘We used a case-crossover design, a variation of a case-
control design that is appropriate when a brief exposure
(driver’s phone use) causes a transient rise in the risk of a rare
outcome (a crash). We compared a driver’s use of a mobile
phone at the estimated time of a crash with the same driver’s
use during another suitable time period. Because drivers are
their own controls, the design controls for characteristics of
the driver that may affect the risk of a crash but do not
change over a short period of time. As it is important that
risks during control periods and crash trips are similar, we
compared phone activity during the hazard interval (time
immediately before the crash) with phone activity during
control intervals (equivalent times during which participants
were driving but did not crash) in the previous week’’ .
We advise presenting key elements of study design early in
the methods section (or at the end of the introduction) so
that readers can understand the basics of the study. For
example, authors should indicate that the study was a cohort
study, which followed people over a particular time period,
and describe the group of persons that comprised the cohort
and their exposure status. Similarly, if the investigation used
a case-control design, the cases and controls and their source
population should be described. If the study was a cross-
sectional survey, the population and the point in time at
which the cross-section was taken should be mentioned.
When a study is a variant of the three main study types, there
is an additional need for clarity. For instance, for a case-
crossover study, one of the variants of the case-control design,
a succinct description of the principles was given in the
example above .
We recommend that authors refrain from simply calling a
study ‘prospective’ or ‘retrospective’ because these terms are
ill defined . One usage sees cohort and prospective as
synonymous and reserves the word retrospective for case-
control studies . A second usage distinguishes prospective
and retrospective cohort studies according to the timing of
data collection relative to when the idea for the study was
developed . A third usage distinguishes prospective and
retrospective case-control studies depending on whether the
data about the exposure of interest existed when cases were
selected . Some advise against using these terms , or
adopting the alternatives ‘concurrent’ and ‘historical’ for
describing cohort studies . In STROBE, we do not use the
words prospective and retrospective, nor alternatives such as
concurrent and historical. We recommend that, whenever
authors use these words, they define what they mean. Most
importantly, we recommend that authors describe exactly
how and when data collection took place.
The first part of the methods section might also be the
place to mention whether the report is one of several from a
study. If a new report is in line with the original aims of the
study, this is usually indicated by referring to an earlier
publication and by briefly restating the salient features of the
study. However, the aims of a study may also evolve over time.
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STROBE Explanation and Elaboration
Researchers often use data for purposes for which they were
not originally intended, including, for example, official vital
statistics that were collected primarily for administrative
purposes, items in questionnaires that originally were only
included for completeness, or blood samples that were
collected for another purpose. For example, the Physicians’
Health Study, a randomized controlled trial of aspirin and
carotene, was later used to demonstrate that a point mutation
in the factor V gene was associated with an increased risk of
venous thrombosis, but not of myocardial infarction or stroke
. The secondary use of existing data is a creative part of
observational research and does not necessarily make results
less credible or less important. However, briefly restating the
original aims might help readers understand the context of
the research and possible limitations in the data.
5. Setting: Describe the setting, locations, and relevant
dates, including periods of recruitment, exposure, follow-
up, and data collection.
‘‘The Pasitos Cohort Study recruited pregnant women
from Women, Infant and Child clinics in Socorro and San
Elizario, El Paso County, Texas and maternal-child clinics of
the Mexican Social Security Institute in Ciudad Juarez,
Mexico from April 1998 to October 2000. At baseline, prior
to the birth of the enrolled cohort children, staff interviewed
mothers regarding the household environment. In this
ongoing cohort study, we target follow-up exams at 6-month
intervals beginning at age 6 months’’ .
Readers need information on setting and locations to assess
the context and generalisability of a study’s results. Exposures
such as environmental factors and therapies can change over
time. Also, study methods may evolve over time. Knowing
when a study took place and over what period participants
were recruited and followed up places the study in historical
context and is important for the interpretation of results.
Information about setting includes recruitment sites or
sources (e.g., electoral roll, outpatient clinic, cancer registry,
or tertiary care centre). Information about location may refer
to the countries, towns, hospitals or practices where the
investigation took place. We advise stating dates rather than
only describing the length of time periods. There may be
different sets of dates for exposure, disease occurrence,
recruitment, beginning and end of follow-up, and data
collection. Of note, nearly 80% of 132 reports in oncology
journals that used survival analysis included the starting and
ending dates for accrual of patients, but only 24% also
reported the date on which follow-up ended .
6 (a). Cohort study: Give the eligibility criteria, and the
sources and methods of selection of participants. Describe
methods of follow-up.
‘‘Participants in the Iowa Women’s Health Study were a
random sample of all women ages 55 to 69 years derived from
the state of Iowa automobile driver’s license list in 1985,
which represented approximately 94% of Iowa women in that
age group. (...) Follow-up questionnaires were mailed in
October 1987 and August 1989 to assess vital status and
address changes. (...) Incident cancers, except for non-
melanoma skin cancers, were ascertained by the State Health
Registry of Iowa (...). The Iowa Women’s Health Study cohort
was matched to the registry with combinations of first, last,
and maiden names, zip code, birthdate, and social security
6 (a). Case-control study: Give the eligibility criteria, and
the sources and methods of case ascertainment and
control selection. Give the rationale for the choice of cases
‘‘Cutaneous melanoma cases diagnosed in 1999 and 2000
were ascertained through the Iowa Cancer Registry (...).
Controls, also identified through the Iowa Cancer Registry,
were colorectal cancer patients diagnosed during the same
time. Colorectal cancer controls were selected because they
are common and have a relatively long survival, and because
arsenic exposure has not been conclusively linked to the
incidence of colorectal cancer’’ .
6 (a). Cross-sectional study: Give the eligibility criteria, and
the sources and methods of selection of participants.
‘‘We retrospectively identified patients with a principal
diagnosis of myocardial infarction (code 410) according to
the International Classification of Diseases, 9th Revision,
Clinical Modification, from codes designating discharge
diagnoses, excluding the codes with a fifth digit of 2, which
designates a subsequent episode of care (...) A random
sample of the entire Medicare cohort with myocardial
infarction from February 1994 to July 1995 was selected
(...) To be eligible, patients had to present to the hospital
after at least 30 minutes but less than 12 hours of chest pain
and had to have ST-segment elevation of at least 1 mm on two
contiguous leads on the initial electrocardiogram’’ .
Detailed descriptions of the study participants help readers
understand the applicability of the results. Investigators
usually restrict a study population by defining clinical,
demographic and other characteristics of eligible partic-
ipants. Typical eligibility criteria relate to age, gender,
diagnosis and comorbid conditions. Despite their impor-
tance, eligibility criteria often are not reported adequately. In
a survey of observational stroke research, 17 of 49 reports
(35%) did not specify eligibility criteria .
Eligibility criteria may be presented as inclusion and
exclusion criteria, although this distinction is not always
necessary or useful. Regardless, we advise authors to report all
eligibility criteria and also to describe the group from which
the study population was selected (e.g., the general popula-
tion of a region or country), and the method of recruitment
(e.g., referral or self-selection through advertisements).
Knowing details about follow-up procedures, including
whether procedures minimized non-response and loss to
follow-up and whether the procedures were similar for all
participants, informs judgments about the validity of results.
For example, in a study that used IgM antibodies to detect
acute infections, readers needed to know the interval between
blood tests for IgM antibodies so that they could judge
whether some infections likely were missed because the
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interval between blood tests was too long . In other
studies where follow-up procedures differed between ex-
posed and unexposed groups, readers might recognize
substantial bias due to unequal ascertainment of events or
differences in non-response or loss to follow-up .
Accordingly, we advise that researchers describe the methods
used for following participants and whether those methods
were the same for all participants, and that they describe the
completeness of ascertainment of variables (see also item 14).
In case-control studies, the choice of cases and controls is
crucial to interpreting the results, and the method of their
selection has major implications for study validity. In general,
controls should reflect the population from which the cases
arose. Various methods are used to sample controls, all with
advantages and disadvantages: for cases that arise from a
general population, population roster sampling, random digit
dialling, neighbourhood or friend controls are used. Neigh-
bourhood or friend controls may present intrinsic matching
on exposure . Controls with other diseases may have
advantages over population-based controls, in particular for
hospital-based cases, because they better reflect the catch-
ment population of a hospital, have greater comparability of
recall and ease of recruitment. However, they can present
problems if the exposure of interest affects the risk of
developing or being hospitalized for the control condition(s)
[43,44]. To remedy this problem often a mixture of the best
defensible control diseases is used .
6 (b). Cohort study: For matched studies, give matching
criteria and number of exposed and unexposed.
‘‘For each patient who initially received a statin, we used
propensity-based matching to identify one control who did
not receive a statin according to the following protocol. First,
propensity scores were calculated for each patient in the
entire cohort on the basis of an extensive list of factors
potentially related to the use of statins or the risk of sepsis.
Second, each statin user was matched to a smaller pool of
non-statin-users by sex, age (plus or minus 1 year), and index
date (plus or minus 3 months). Third, we selected the control
with the closest propensity score (within 0.2 SD) to each statin
user in a 1:1 fashion and discarded the remaining controls.’’
6 (b). Case-control study: For matched studies, give
matching criteria and the number of controls per case.
‘‘We aimed to select five controls for every case from
among individuals in the study population who had no
diagnosis of autism or other pervasive developmental
disorders (PDD) recorded in their general practice record
and who were alive and registered with a participating
practice on the date of the PDD diagnosis in the case.
Controls were individually matched to cases by year of birth
(up to 1 year older or younger), sex, and general practice. For
each of 300 cases, five controls could be identified who met all
the matching criteria. For the remaining 994, one or more
controls was excluded...’’ .
Matching is much more common in case-control studies,
but occasionally, investigators use matching in cohort studies
to make groups comparable at the start of follow-up.
Matching in cohort studies makes groups directly comparable
for potential confounders and presents fewer intricacies than
with case-control studies. For example, it is not necessary to
take the matching into account for the estimation of the
relative risk . Because matching in cohort studies may
increase statistical precision investigators might allow for the
matching in their analyses and thus obtain narrower
In case-control studies matching is done to increase a
study’s efficiency by ensuring similarity in the distribution of
variables between cases and controls, in particular the
distribution of potential confounding variables [48,49].
Because matching can be done in various ways, with one or
more controls per case, the rationale for the choice of
matching variables and the details of the method used should
be described. Commonly used forms of matching are
frequency matching (also called group matching) and
individual matching. In frequency matching, investigators
choose controls so that the distribution of matching variables
becomes identical or similar to that of cases. Individual
matching involves matching one or several controls to each
case. Although intuitively appealing and sometimes useful,
matching in case-control studies has a number of disadvan-
tages, is not always appropriate, and needs to be taken into
account in the analysis (see Box 2).
Even apparently simple matching procedures may be
poorly reported. For example, authors may state that controls
were matched to cases ‘within five years’, or using ‘five year
age bands’. Does this mean that, if a case was 54 years old, the
respective control needed to be in the five-year age band 50
to 54, or aged 49 to 59, which is within five years of age 54? If a
wide (e.g., 10-year) age band is chosen, there is a danger of
residual confounding by age (see also Box 4), for example
because controls may then be younger than cases on average.
7. Variables: Clearly define all outcomes, exposures,
predictors, potential confounders, and effect modifiers.
Give diagnostic criteria, if applicable.
‘‘Only major congenital malformations were included in
the analyses. Minor anomalies were excluded according to the
exclusion list of European Registration of Congenital
Anomalies (EUROCAT). If a child had more than one major
congenital malformation of one organ system, those malfor-
mations were treated as one outcome in the analyses by organ
system (...) In the statistical analyses, factors considered
potential confounders were maternal age at delivery and
number of previous parities. Factors considered potential
effect modifiers were maternal age at reimbursement for
antiepileptic medication and maternal age at delivery’’ .
Authors should define all variables considered for and
included in the analysis, including outcomes, exposures,
predictors, potential confounders and potential effect modi-
fiers. Disease outcomes require adequately detailed descrip-
tion of the diagnostic criteria. This applies to criteria for
cases in a case-control study, disease events during follow-up
in a cohort study and prevalent disease in a cross-sectional
study. Clear definitions and steps taken to adhere to them are
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particularly important for any disease condition of primary
interest in the study.
For some studies, ‘determinant’ or ‘predictor’ may be
appropriate terms for exposure variables and outcomes may
be called ‘endpoints’. In multivariable models, authors some-
times use ‘dependent variable’ for an outcome and ‘inde-
pendent variable’ or ‘explanatory variable’ for exposure and
confounding variables. The latter is not precise as it does not
distinguish exposures from confounders.
If many variables have been measured and included in
exploratory analyses in an early discovery phase, consider
providing a list with details on each variable in an appendix,
additional table or separate publication. Of note, the
International Journal of Epidemiology recently launched a new
section with ‘cohort profiles’, that includes detailed informa-
tion on what was measured at different points in time in
particular studies [56,57]. Finally, we advise that authors
declare all ‘candidate variables’ considered for statistical
analysis, rather than selectively reporting only those included
in the final models (see also item 16a) [58,59].
8. Data sources/measurement: For each variable of
interest give sources of data and details of methods of
assessment (measurement). Describe comparability of
assessment methods if there is more than one group.
‘‘Total caffeine intake was calculated primarily using US
Department of Agriculture food composition sources. In
these calculations, it was assumed that the content of caffeine
was 137 mg per cup of coffee, 47 mg per cup of tea, 46 mg per
can or bottle of cola beverage, and 7 mg per serving of
chocolate candy. This method of measuring (caffeine) intake
was shown to be valid in both the NHS I cohort and a similar
cohort study of male health professionals (...) Self-reported
diagnosis of hypertension was found to be reliable in the NHS
I cohort’’ .
‘‘Samples pertaining to matched cases and controls were
always analyzed together in the same batch and laboratory
personnel were unable to distinguish among cases and
The way in which exposures, confounders and outcomes
were measured affects the reliability and validity of a study.
Measurement error and misclassification of exposures or
outcomes can make it more difficult to detect cause-effect
relationships, or may produce spurious relationships. Error
in measurement of potential confounders can increase the
risk of residual confounding [62,63]. It is helpful, therefore, if
authors report the findings of any studies of the validity or
reliability of assessments or measurements, including details
of the reference standard that was used. Rather than simply
citing validation studies (as in the first example), we advise
that authors give the estimated validity or reliability, which
can then be used for measurement error adjustment or
sensitivity analyses (see items 12e and 17).
In addition, it is important to know if groups being
compared differed with respect to the way in which the data
were collected. This may be important for laboratory
examinations (as in the second example) and other situations.
For instance, if an interviewer first questions all the cases and
then the controls, or vice versa, bias is possible because of the
learning curve; solutions such as randomising the order of
interviewing may avoid this problem. Information bias may
also arise if the compared groups are not given the same
diagnostic tests or if one group receives more tests of the
same kind than another (see also item 9).
9. Bias: Describe any efforts to address potential sources
‘‘In most case-control studies of suicide, the control group
comprises living individuals but we decided to have a control
group of people who had died of other causes (...). With a
Box 2. Matching in case-control studies
In any case-control study, sensible choices need to be made on whether
to use matching of controls to cases, and if so, what variables to match
on, the precise method of matching to use, and the appropriate method
of statistical analysis. Not to match at all may mean that the distribution
of some key potential confounders (e.g., age, sex) is radically different
between cases and controls. Although this could be adjusted for in the
analysis there could be a major loss in statistical efficiency.
The use of matching in case-control studies and its interpretation are
fraught with difficulties, especially if matching is attempted on several
risk factors, some of which may be linked to the exposure of prime
interest [50,51]. For example, in a case-control study of myocardial
infarction and oral contraceptives nested in a large pharmaco-
epidemiologic data base, with information about thousands of women
who are available as potential controls, investigators may be tempted to
choose matched controls who had similar levels of risk factors to each
case of myocardial infarction. One objective is to adjust for factors that
might influence the prescription of oral contraceptives and thus to
control for confounding by indication. However, the result will be a
control group that is no longer representative of the oral contraceptive
use in the source population: controls will be older than the source
population because patients with myocardial infarction tend to be older.
This has several implications. A crude analysis of the data will produce
odds ratios that are usually biased towards unity if the matching factor is
associated with the exposure. The solution is to perform a matched or
stratified analysis (see item 12d). In addition, because the matched
control group ceases to be representative for the population at large, the
exposure distribution among the controls can no longer be used to
estimate the population attributable fraction (see Box 7) . Also, the
effect of the matching factor can no longer be studied, and the search
for well-matched controls can be cumbersome – making a design with a
non-matched control group preferable because the non-matched
controls will be easier to obtain and the control group can be larger.
Overmatching is another problem, which may reduce the efficiency of
matched case-control studies, and, in some situations, introduce bias.
Information is lost and the power of the study is reduced if the matching
variable is closely associated with the exposure. Then many individuals in
the same matched sets will tend to have identical or similar levels of
exposures and therefore not contribute relevant information. Matching
will introduce irremediable bias if the matching variable is not a
confounder but in the causal pathway between exposure and disease.
For example, in vitro fertilization is associated with an increased risk of
perinatal death, due to an increase in multiple births and low birth
weight infants . Matching on plurality or birth weight will bias results
towards the null, and this cannot be remedied in the analysis.
Matching is intuitively appealing, but the complexities involved have led
methodologists to advise against routine matching in case-control
studies. They recommend instead a careful and judicious consideration
of each potential matching factor, recognizing that it could instead be
measured and used as an adjustment variable without matching on it. In
response, there has been a reduction in the number of matching factors
employed, an increasing use of frequency matching, which avoids some
of the problems discussed above, and more case-control studies with no
matching at all . Matching remains most desirable, or even necessary,
when the distributions of the confounder (e.g., age) might differ radically
between the unmatched comparison groups [48,49].
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STROBE Explanation and Elaboration
control group of deceased individuals, the sources of
information used to assess risk factors are informants who
have recently experienced the death of a family member or
close associate - and are therefore more comparable to the
sources of information in the suicide group than if living
controls were used’’ .
‘‘Detection bias could influence the association between
Type 2 diabetes mellitus (T2DM) and primary open-angle
glaucoma (POAG) if women with T2DM were under closer
ophthalmic surveillance than women without this condition.
We compared the mean number of eye examinations
reported by women with and without diabetes. We also
recalculated the relative risk for POAG with additional
control for covariates associated with more careful ocular
surveillance (a self-report of cataract, macular degeneration,
number of eye examinations, and number of physical
Biased studies produce results that differ systematically
from the truth (see also Box 3). It is important for a reader to
know what measures were taken during the conduct of a
study to reduce the potential of bias. Ideally, investigators
carefully consider potential sources of bias when they plan
their study. At the stage of reporting, we recommend that
authors always assess the likelihood of relevant biases.
Specifically, the direction and magnitude of bias should be
discussed and, if possible, estimated. For instance, in case-
control studies information bias can occur, but may be
reduced by selecting an appropriate control group, as in the
first example . Differences in the medical surveillance of
participants were a problem in the second example .
Consequently, the authors provide more detail about the
additional data they collected to tackle this problem. When
investigators have set up quality control programs for data
collection to counter a possible ‘‘drift’’ in measurements of
variables in longitudinal studies, or to keep variability at a
minimum when multiple observers are used, these should be
Unfortunately, authors often do not address important
biases when reporting their results. Among 43 case-control
and cohort studies published from 1990 to 1994 that
investigated the risk of second cancers in patients with a
history of cancer, medical surveillance bias was mentioned in
only 5 articles . A survey of reports of mental health
research published during 1998 in three psychiatric journals
found that only 13% of 392 articles mentioned response bias
. A survey of cohort studies in stroke research found that
14 of 49 (28%) articles published from 1999 to 2003 addressed
potential selection bias in the recruitment of study partic-
ipants and 35 (71%) mentioned the possibility that any type
of bias may have affected results .
10. Study size: Explain how the study size was arrived at.
‘‘The number of cases in the area during the study period
determined the sample size’’ .
‘‘A survey of postnatal depression in the region had
documented a prevalence of 19.8%. Assuming depression in
mothers with normal weight children to be 20% and an odds
ratio of 3 for depression in mothers with a malnourished
child we needed 72 case-control sets (one case to one control)
with an 80% power and 5% significance’’ .
A study should be large enough to obtain a point estimate
with a sufficiently narrow confidence interval to meaningfully
answer a research question. Large samples are needed to
distinguish a small association from no association. Small
studies often provide valuable information, but wide con-
fidence intervals may indicate that they contribute less to
current knowledge in comparison with studies providing
estimates with narrower confidence intervals. Also, small
studies that show ‘interesting’ or ‘statistically significant’
associations are published more frequently than small studies
Box 3. Bias
Bias is a systematic deviation of a study’s result from a true value.
Typically, it is introduced during the design or implementation of a study
and cannot be remedied later. Bias and confounding are not
synonymous. Bias arises from flawed information or subject selection
so that a wrong association is found. Confounding produces relations
that are factually right, but that cannot be interpreted causally because
some underlying, unaccounted for factor is associated with both
exposure and outcome (see Box 5). Also, bias needs to be distinguished
from random error, a deviation from a true value caused by statistical
fluctuations (in either direction) in the measured data. Many possible
sources of bias have been described and a variety of terms are used
[68,69]. We find two simple categories helpful: information bias and
Information bias occurs when systematic differences in the complete-
ness or the accuracy of data lead to differential misclassification of
individuals regarding exposures or outcomes. For instance, if diabetic
women receive more regular and thorough eye examinations, the
ascertainment of glaucoma will be more complete than in women
without diabetes (see item 9) . Patients receiving a drug that causes
non-specific stomach discomfort may undergo gastroscopy more often
and have more ulcers detected than patients not receiving the drug –
even if the drug does not cause more ulcers. This type of information
bias is also called ‘detection bias’ or ‘medical surveillance bias’. One way
to assess its influence is to measure the intensity of medical surveillance
in the different study groups, and to adjust for it in statistical analyses. In
case-control studies information bias occurs if cases recall past
exposures more or less accurately than controls without that disease,
or if they are more or less willing to report them (also called ‘recall bias’).
‘Interviewer bias’ can occur if interviewers are aware of the study
hypothesis and subconsciously or consciously gather data selectively
. Some form of blinding of study participants and researchers is
therefore often valuable.
Selection bias may be introduced in case-control studies if the
probability of including cases or controls is associated with exposure.
For instance, a doctor recruiting participants for a study on deep-vein
thrombosis might diagnose this disease in a woman who has leg
complaints and takes oral contraceptives. But she might not diagnose
deep-vein thrombosis in a woman with similar complaints who is not
taking such medication. Such bias may be countered by using cases and
controls that were referred in the same way to the diagnostic service
. Similarly, the use of disease registers may introduce selection bias: if
a possible relationship between an exposure and a disease is known,
cases may be more likely to be submitted to a register if they have been
exposed to the suspected causative agent . ‘Response bias’ is another
type of selection bias that occurs if differences in characteristics between
those who respond and those who decline participation in a study affect
estimates of prevalence, incidence and, in some circumstances,
associations. In general, selection bias affects the internal validity of a
study. This is different from problems that may arise with the selection of
participants for a study in general, which affects the external rather than
the internal validity of a study (also see item 21).
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STROBE Explanation and Elaboration
that do not have ‘significant’ findings. While these studies may
provide an early signal in the context of discovery, readers
should be informed of their potential weaknesses.
The importance of sample size determination in observa-
tional studies depends on the context. If an analysis is
performed on data that were already available for other
purposes, the main question is whether the analysis of the
data will produce results with sufficient statistical precision to
contribute substantially to the literature, and sample size
considerations will be informal. Formal, a priori calculation of
sample size may be useful when planning a new study [75,76].
Such calculations are associated with more uncertainty than
implied by the single number that is generally produced. For
example, estimates of the rate of the event of interest or other
assumptions central to calculations are commonly imprecise,
if not guesswork . The precision obtained in the final
analysis can often not be determined beforehand because it
will be reduced by inclusion of confounding variables in
multivariable analyses , the degree of precision with which
key variables can be measured , and the exclusion of some
Few epidemiological studies explain or report delibera-
tions about sample size [4,5]. We encourage investigators to
report pertinent formal sample size calculations if they
were done. In other situations they should indicate the
considerations that determined the study size (e.g., a fixed
available sample, as in the first example above). If the
observational study was stopped early when statistical
significance was achieved, readers should be told. Do not
bother readers with post hoc justifications for study size or
retrospective power calculations . From the point of view
of the reader, confidence intervals indicate the statistical
precision that was ultimately obtained. It should be realized
that confidence intervals reflect statistical uncertainty only,
and not all uncertainty that may be present in a study (see
11. Quantitative variables: Explain how quantitative
variables were handled in the analyses. If applicable,
describe which groupings were chosen, and why.
‘‘Patients with a Glasgow Coma Scale less than 8 are
considered to be seriously injured. A GCS of 9 or more
indicates less serious brain injury. We examined the
association of GCS in these two categories with the
occurrence of death within 12 months from injury’’ .
Investigators make choices regarding how to collect and
analyse quantitative data about exposures, effect modifiers
and confounders. For example, they may group a continuous
exposure variable to create a new categorical variable (see
Box 4). Grouping choices may have important consequences
for later analyses [81,82]. We advise that authors explain why
and how they grouped quantitative data, including the
number of categories, the cut-points, and category mean or
median values. Whenever data are reported in tabular form,
the counts of cases, controls, persons at risk, person-time at
risk, etc. should be given for each category. Tables should not
consist solely of effect-measure estimates or results of model
Investigators might model an exposure as continuous in
order to retain all the information. In making this choice, one
needs to consider the nature of the relationship of the
exposure to the outcome. As it may be wrong to assume a
linear relation automatically, possible departures from
linearity should be investigated. Authors could mention
alternative models they explored during analyses (e.g., using
log transformation, quadratic terms or spline functions).
Several methods exist for fitting a non-linear relation
between the exposure and outcome [82–84]. Also, it may be
informative to present both continuous and grouped analyses
for a quantitative exposure of prime interest.
In a recent survey, two thirds of epidemiological publica-
tions studied quantitative exposure variables . In 42 of 50
articles (84%) exposures were grouped into several ordered
categories, but often without any stated rationale for the
choices made. Fifteen articles used linear associations to
model continuous exposure but only two reported checking
for linearity. In another survey, of the psychological
literature, dichotomization was justified in only 22 of 110
articles (20%) .
Box 4. Grouping
There are several reasons why continuous data may be grouped .
When collecting data it may be better to use an ordinal variable than to
seek an artificially precise continuous measure for an exposure based on
recall over several years. Categories may also be helpful for presentation,
for example to present all variables in a similar style, or to show a dose-
Grouping may also be done to simplify the analysis, for example to avoid
an assumption of linearity. However, grouping loses information and
may reduce statistical power  especially when dichotomization is
used [82,85,88]. If a continuous confounder is grouped, residual
confounding may occur, whereby some of the variable’s confounding
effect remains unadjusted for (see Box 5) [62,89]. Increasing the number
of categories can diminish power loss and residual confounding, and is
especially appropriate in large studies. Small studies may use few groups
because of limited numbers.
Investigators may choose cut-points for groupings based on commonly
used values that are relevant for diagnosis or prognosis, for practicality,
or on statistical grounds. They may choose equal numbers of individuals
in each group using quantiles . On the other hand, one may gain
more insight into the association with the outcome by choosing more
extreme outer groups and having the middle group(s) larger than the
outer groups . In case-control studies, deriving a distribution from
the control group is preferred since it is intended to reflect the source
population. Readers should be informed if cut-points are selected post
hoc from several alternatives. In particular, if the cut-points were chosen
to minimise a P value the true strength of an association will be
When analysing grouped variables, it is important to recognise their
underlying continuous nature. For instance, a possible trend in risk
across ordered groups can be investigated. A common approach is to
model the rank of the groups as a continuous variable. Such linearity
across group scores will approximate an actual linear relation if groups
are equally spaced (e.g., 10 year age groups) but not otherwise. Il’yasova
et al . recommend publication of both the categorical and the
continuous estimates of effect, with their standard errors, in order to
facilitate meta-analysis, as well as providing intrinsically valuable
information on dose-response. One analysis may inform the other and
neither is assumption-free. Authors often ignore the ordering and
consider the estimates (and P values) separately for each category
compared to the reference category. This may be useful for description,
but may fail to detect a real trend in risk across groups. If a trend is
observed, a confidence interval for a slope might indicate the strength of
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STROBE Explanation and Elaboration
12. Statistical methods:
12 (a). Describe all statistical methods, including those
used to control for confounding.
‘‘The adjusted relative risk was calculated using the Mantel-
Haenszel technique, when evaluating if confounding by age
or gender was present in the groups compared. The 95%
confidence interval (CI) was computed around the adjusted
relative risk, using the variance according to Greenland and
Robins and Robins et al.’’ .
In general, there is no one correct statistical analysis but,
rather, several possibilities that may address the same
question, but make different assumptions. Regardless, inves-
tigators should pre-determine analyses at least for the
primary study objectives in a study protocol. Often addi-
tional analyses are needed, either instead of, or as well as,
those originally envisaged, and these may sometimes be
motivated by the data. When a study is reported, authors
should tell readers whether particular analyses were sug-
gested by data inspection. Even though the distinction
between pre-specified and exploratory analyses may some-
times be blurred, authors should clarify reasons for partic-
If groups being compared are not similar with regard to
some characteristics, adjustment should be made for possible
confounding variables by stratification or by multivariable
regression (see Box 5) . Often, the study design determines
which type of regression analysis is chosen. For instance, Cox
proportional hazard regression is commonly used in cohort
studies . whereas logistic regression is often the method of
choice in case-control studies [96,97]. Analysts should fully
describe specific procedures for variable selection and not
only present results from the final model [98,99]. If model
comparisons are made to narrow down a list of potential
confounders for inclusion in a final model, this process
should be described. It is helpful to tell readers if one or two
covariates are responsible for a great deal of the apparent
confounding in a data analysis. Other statistical analyses such
as imputation procedures, data transformation, and calcu-
lations of attributable risks should also be described. Non-
standard or novel approaches should be referenced and the
statistical software used reported. As a guiding principle, we
advise statistical methods be described ‘‘with enough detail to
enable a knowledgeable reader with access to the original
data to verify the reported results’’ .
In an empirical study, only 93 of 169 articles (55%)
reporting adjustment for confounding clearly stated how
continuous and multi-category variables were entered into
the statistical model . Another study found that among
67 articles in which statistical analyses were adjusted for
confounders, it was mostly unclear how confounders were
12 (b). Describe any methods used to examine subgroups
‘‘Sex differences in susceptibility to the 3 lifestyle-related
risk factors studied were explored by testing for biological
interaction according to Rothman: a new composite variable
with 4 categories (a?b?, a?bþ, aþb?, and aþbþ) was redefined for
sex and a dichotomous exposure of interest where a?and b?
denote absence of exposure. RR was calculated for each
category after adjustment for age. An interaction effect is
defined as departure from additivity of absolute effects, and
excess RR caused by interaction (RERI) was calculated:
RERI ¼ RRðaþbþÞ ? RRða?bþÞ ? RRðaþb?Þ ? 1
where RR(aþbþ) denotes RR among those exposed to both
factors where RR(a?b?) is used as reference category (RR ¼
1.0). Ninety-five percent CIs were calculated as proposed by
Hosmer and Lemeshow. RERI of 0 means no interaction’’
As discussed in detail under item 17, many debate the use
and value of analyses restricted to subgroups of the study
population [4,104]. Subgroup analyses are nevertheless often
done . Readers need to know which subgroup analyses were
planned in advance, and which arose while analysing the data.
Also, it is important to explain what methods were used to
examine whether effects or associations differed across
groups (see item 17).
Interaction relates to the situation when one factor
modifies the effect of another (therefore also called ‘effect
modification’). The joint action of two factors can be
characterized in two ways: on an additive scale, in terms of
risk differences; or on a multiplicative scale, in terms of
Box 5. Confounding
Confounding literally means confusion of effects. A study might seem to
show either an association or no association between an exposure and
the risk of a disease. In reality, the seeming association or lack of
association is due to another factor that determines the occurrence of
the disease but that is also associated with the exposure. The other
factor is called the confounding factor or confounder. Confounding thus
gives a wrong assessment of the potential ‘causal’ association of an
exposure. For example, if women who approach middle age and develop
elevated blood pressure are less often prescribed oral contraceptives, a
simple comparison of the frequency of cardiovascular disease between
those who use contraceptives and those who do not, might give the
wrong impression that contraceptives protect against heart disease.
Investigators should think beforehand about potential confounding
factors. This will inform the study design and allow proper data
collection by identifying the confounders for which detailed information
should be sought. Restriction or matching may be used. In the example
above, the study might be restricted to women who do not have the
confounder, elevated blood pressure. Matching on blood pressure might
also be possible, though not necessarily desirable (see Box 2). In the
analysis phase, investigators may use stratification or multivariable
analysis to reduce the effect of confounders. Stratification consists of
dividing the data in strata for the confounder (e.g., strata of blood
pressure), assessing estimates of association within each stratum, and
calculating the combined estimate of association as a weighted average
over all strata. Multivariable analysis achieves the same result but permits
one to take more variables into account simultaneously. It is more
flexible but may involve additional assumptions about the mathematical
form of the relationship between exposure and disease.
Taking confounders into account is crucial in observational studies, but
readers should not assume that analyses adjusted for confounders
establish the ‘causal part’ of an association. Results may still be distorted
by residual confounding (the confounding that remains after unsuccess-
ful attempts to control for it ), random sampling error, selection bias
and information bias (see Box 3).
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STROBE Explanation and Elaboration
relative risk (see Box 8). Many authors and readers may have
their own preference about the way interactions should be
analysed. Still, they may be interested to know to what extent
the joint effect of exposures differs from the separate effects.
There is consensus that the additive scale, which uses absolute
risks, is more appropriate for public health and clinical
decision making . Whatever view is taken, this should be
clearly presented to the reader, as is done in the example
above . A lay-out presenting separate effects of both
exposures as well as their joint effect, each relative to no
exposure, might be most informative. It is presented in the
example for interaction under item 17, and the calculations
on the different scales are explained in Box 8.
12 (c). Explain how missing data were addressed.
‘‘Our missing data analysis procedures used missing at
random (MAR) assumptions. We used the MICE (multivariate
imputation by chained equations) method of multiple
multivariate imputation in STATA. We independently
analysed 10 copies of the data, each with missing values
suitably imputed, in the multivariate logistic regression
analyses. We averaged estimates of the variables to give a
single mean estimate and adjusted standard errors according
to Rubin’s rules’’ .
Missing data are common in observational research.
Questionnaires posted to study participants are not always
filled in completely, participants may not attend all follow-up
visits and routine data sources and clinical databases are
often incomplete. Despite its ubiquity and importance, few
papers report in detail on the problem of missing data
[5,107]. Investigators may use any of several approaches to
address missing data. We describe some strengths and
limitations of various approaches in Box 6. We advise that
authors report the number of missing values for each
variable of interest (exposures, outcomes, confounders) and
for each step in the analysis. Authors should give reasons for
missing values if possible, and indicate how many individuals
were excluded because of missing data when describing the
flow of participants through the study (see also item 13). For
analyses that account for missing data, authors should
describe the nature of the analysis (e.g., multiple imputation)
and the assumptions that were made (e.g., missing at random,
see Box 6).
12 (d). Cohort study: If applicable, describe how loss to
follow-up was addressed.
‘‘In treatment programmes with active follow-up, those lost
to follow-up and those followed-up at 1 year had similar
baseline CD4 cell counts (median 115 cells per lL and 123
cells per lL), whereas patients lost to follow-up in pro-
grammes with no active follow-up procedures had consid-
erably lower CD4 cell counts than those followed-up (median
64 cells per lL and 123 cells per lL). (...) Treatment
programmes with passive follow-up were excluded from
subsequent analyses’’ .
Cohort studies are analysed using life table methods or
other approaches that are based on the person-time of
follow-up and time to developing the disease of interest.
Among individuals who remain free of the disease at the end
of their observation period, the amount of follow-up time is
assumed to be unrelated to the probability of developing the
outcome. This will be the case if follow-up ends on a fixed
date or at a particular age. Loss to follow-up occurs when
participants withdraw from a study before that date. This may
hamper the validity of a study if loss to follow-up occurs
selectively in exposed individuals, or in persons at high risk of
developing the disease (‘informative censoring’). In the
example above, patients lost to follow-up in treatment
programmes with no active follow-up had fewer CD4 helper
cells than those remaining under observation and were
therefore at higher risk of dying .
It is important to distinguish persons who reach the end of
the study from those lost to follow-up. Unfortunately,
statistical software usually does not distinguish between the
two situations: in both cases follow-up time is automatically
truncated (‘censored’) at the end of the observation period.
Investigators therefore need to decide, ideally at the stage of
planning the study, how they will deal with loss to follow-up.
Box 6. Missing data: problems and possible solutions
A common approach to dealing with missing data is to restrict analyses
to individuals with complete data on all variables required for a particular
analysis. Although such ‘complete-case’ analyses are unbiased in many
circumstances, they can be biased and are always inefficient . Bias
arises if individuals with missing data are not typical of the whole
sample. Inefficiency arises because of the reduced sample size for
Using the last observation carried forward for repeated measures can
distort trends over time if persons who experience a foreshadowing of
the outcome selectively drop out . Inserting a missing category
indicator for a confounder may increase residual confounding .
Imputation, in which each missing value is replaced with an assumed or
estimated value, may lead to attenuation or exaggeration of the
association of interest, and without the use of sophisticated methods
described below may produce standard errors that are too small.
Rubin developed a typology of missing data problems, based on a model
for the probability of an observation being missing [108,110]. Data are
described as missing completely at random (MCAR) if the probability that
a particular observation is missing does not depend on the value of any
observable variable(s). Data are missing at random (MAR) if, given the
observed data, the probability that observations are missing is
independent of the actual values of the missing data. For example,
suppose younger children are more prone to missing spirometry
measurements, but that the probability of missing is unrelated to the
true unobserved lung function, after accounting for age. Then the
missing lung function measurement would be MAR in models including
age. Data are missing not at random (MNAR) if the probability of missing
still depends on the missing value even after taking the available data
into account. When data are MNAR valid inferences require explicit
assumptions about the mechanisms that led to missing data.
Methods to deal with data missing at random (MAR) fall into three broad
classes [108,111]: likelihood-based approaches , weighted estima-
tion  and multiple imputation [111,114]. Of these three approaches,
multiple imputation is the most commonly used and flexible, particularly
when multiple variables have missing values . Results using any of
these approaches should be compared with those from complete case
analyses, and important differences discussed. The plausibility of
assumptions made in missing data analyses is generally unverifiable. In
particular it is impossible to prove that data are MAR, rather than MNAR.
Such analyses are therefore best viewed in the spirit of sensitivity analysis
(see items 12e and 17).
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When few patients are lost, investigators may either exclude
individuals with incomplete follow-up, or treat them as if they
withdrew alive at either the date of loss to follow-up or the
end of the study. We advise authors to report how many
patients were lost to follow-up and what censoring strategies
12 (d). Case-control study: If applicable, explain how
matching of cases and controls was addressed.
‘‘We used McNemar’s test, paired t test, and conditional
logistic regression analysis to compare dementia patients
with their matched controls for cardiovascular risk factors,
the occurrence of spontaneous cerebral emboli, carotid
disease, and venous to arterial circulation shunt’’ .
In individually matched case-control studies a crude
analysis of the odds ratio, ignoring the matching, usually
leads to an estimation that is biased towards unity (see Box 2).
A matched analysis is therefore often necessary. This can
intuitively be understood as a stratified analysis: each case is
seen as one stratum with his or her set of matched controls.
The analysis rests on considering whether the case is more
often exposed than the controls, despite having made them
alike regarding the matching variables. Investigators can do
such a stratified analysis using the Mantel-Haenszel method
on a ‘matched’ 2 by 2 table. In its simplest form the odds ratio
becomes the ratio of pairs that are discordant for the
exposure variable. If matching was done for variables like
age and sex that are universal attributes, the analysis needs
not retain the individual, person-to-person matching: a
simple analysis in categories of age and sex is sufficient .
For other matching variables, such as neighbourhood, sibship,
or friendship, however, each matched set should be consid-
ered its own stratum.
In individually matched studies, the most widely used
method of analysis is conditional logistic regression, in which
each case and their controls are considered together. The
conditional method is necessary when the number of controls
varies among cases, and when, in addition to the matching
variables, other variables need to be adjusted for. To allow
readers to judge whether the matched design was appropri-
ately taken into account in the analysis, we recommend that
authors describe in detail what statistical methods were used
to analyse the data. If taking the matching into account does
have little effect on the estimates, authors may choose to
present an unmatched analysis.
12 (d). Cross-sectional study: If applicable, describe
analytical methods taking account of sampling strategy.
‘‘The standard errors (SE) were calculated using the Taylor
expansion method to estimate the sampling errors of
estimators based on the complex sample design. (...) The
overall design effect for diastolic blood pressure was found to
be 1.9 for men and 1.8 for women and, for systolic blood
pressure, it was 1.9 for men and 2.0 for women’’ .
Most cross-sectional studies use a pre-specified sampling
strategy to select participants from a source population.
Sampling may be more complex than taking a simple random
sample, however. It may include several stages and clustering
of participants (e.g., in districts or villages). Proportionate
stratification may ensure that subgroups with a specific
characteristic are correctly represented. Disproportionate
stratification may be useful to over-sample a subgroup of
An estimate of association derived from a complex sample
may be more or less precise than that derived from a simple
random sample. Measures of precision such as standard
error or confidence interval should be corrected using the
design effect, a ratio measure that describes how much
precision is gained or lost if a more complex sampling
strategy is used instead of simple random sampling .
Most complex sampling techniques lead to a decrease of
precision, resulting in a design effect greater than 1.
We advise that authors clearly state the method used to
adjust for complex sampling strategies so that readers may
understand how the chosen sampling method influenced the
precision of the obtained estimates. For instance, with
clustered sampling, the implicit trade-off between easier
data collection and loss of precision is transparent if the
design effect is reported. In the example, the calculated
design effects of 1.9 for men indicates that the actual sample
size would need to be 1.9 times greater than with simple
random sampling for the resulting estimates to have equal
12 (e). Describe any sensitivity analyses.
‘‘Because we had a relatively higher proportion of ‘missing’
dead patients with insufficient data (38/148¼25.7%) as
compared to live patients (15/437¼3.4%) (...), it is possible
that this might have biased the results. We have, therefore,
carried out a sensitivity analysis. We have assumed that the
proportion of women using oral contraceptives in the study
group applies to the whole (19.1% for dead, and 11.4% for
live patients), and then applied two extreme scenarios:
either all the exposed missing patients used second
generation pills or they all used third-generation pills’’
Sensitivity analyses are useful to investigate whether or
not the main results are consistent with those obtained with
alternative analysis strategies or assumptions . Issues
that may be examined include the criteria for inclusion in
analyses, the definitions of exposures or outcomes ,
which confounding variables merit adjustment, the handling
of missing data [120,123], possible selection bias or bias from
inaccurate or inconsistent measurement of exposure, disease
and other variables, and specific analysis choices, such as the
treatment of quantitative variables (see item 11). Sophisti-
cated methods are increasingly used to simultaneously
model the influence of several biases or assumptions [124–
In 1959 Cornfield et al. famously showed that a relative
risk of 9 for cigarette smoking and lung cancer was
extremely unlikely to be due to any conceivable confounder,
since the confounder would need to be at least nine times as
prevalent in smokers as in non-smokers . This analysis
did not rule out the possibility that such a factor was
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STROBE Explanation and Elaboration
present, but it did identify the prevalence such a factor
would need to have. The same approach was recently used
to identify plausible confounding factors that could explain
the association between childhood leukaemia and living
near electric power lines . More generally, sensitivity
analyses can be used to identify the degree of confounding,
selection bias, or information bias required to distort an
association. One important, perhaps under recognised, use
of sensitivity analysis is when a study shows little or no
association between an exposure and an outcome and it is
plausible that confounding or other biases toward the null
The Results section should give a factual account of what
was found, from the recruitment of study participants, the
description of the study population to the main results and
ancillary analyses. It should be free of interpretations and
discursive text reflecting the authors’ views and opinions.
13 (a). Report the numbers of individuals at each stage of
the study—e.g., numbers potentially eligible, examined
for eligibility, confirmed eligible, included in the study,
completing follow-up, and analysed.
‘‘Of the 105 freestanding bars and taverns sampled, 13
establishments were no longer in business and 9 were located
in restaurants, leaving 83 eligible businesses. In 22 cases, the
owner could not be reached by telephone despite 6 or more
attempts. The owners of 36 bars declined study participation.
(...) The 25 participating bars and taverns employed 124
bartenders, with 67 bartenders working at least 1 weekly
daytime shift. Fifty-four of the daytime bartenders (81%)
completed baseline interviews and spirometry; 53 of these
subjects (98%) completed follow-up‘‘ .
Detailed information on the process of recruiting study
participants is important for several reasons. Those included
in a study often differ in relevant ways from the target
population to which results are applied. This may result in
estimates of prevalence or incidence that do not reflect the
experience of the target population. For example, people
who agreed to participate in a postal survey of sexual
behaviour attended church less often, had less conservative
sexual attitudes and earlier age at first sexual intercourse,
and were more likely to smoke cigarettes and drink alcohol
than people who refused . These differences suggest that
postal surveys may overestimate sexual liberalism and
activity in the population. Such response bias (see Box 3)
can distort exposure-disease associations if associations
differ between those eligible for the study and those included
in the study. As another example, the association between
young maternal age and leukaemia in offspring, which has
been observed in some case-control studies [131,132], was
explained by differential participation of young women in
case and control groups. Young women with healthy children
were less likely to participate than those with unhealthy
children . Although low participation does not neces-
sarily compromise the validity of a study, transparent
information on participation and reasons for non-partic-
ipation is essential. Also, as there are no universally agreed
definitions for participation, response or follow-up rates,
readers need to understand how authors calculated such
Ideally, investigators should give an account of the
numbers of individuals considered at each stage of recruiting
study participants, from the choice of a target population to
the inclusion of participants’ data in the analysis. Depending
on the type of study, this may include the number of
individuals considered to be potentially eligible, the number
assessed for eligibility, the number found to be eligible, the
number included in the study, the number examined, the
number followed up and the number included in the analysis.
Information on different sampling units may be required, if
sampling of study participants is carried out in two or more
stages as in the example above (multistage sampling). In case-
control studies, we advise that authors describe the flow of
participants separately for case and control groups .
Controls can sometimes be selected from several sources,
including, for example, hospitalised patients and community
dwellers. In this case, we recommend a separate account of
the numbers of participants for each type of control group.
Olson and colleagues proposed useful reporting guidelines
for controls recruited through random-digit dialling and
other methods .
A recent survey of epidemiological studies published in 10
general epidemiology, public health and medical journals
found that some information regarding participation was
provided in 47 of 107 case-control studies (59%), 49 of 154
cohort studies (32%), and 51 of 86 cross-sectional studies
(59%) . Incomplete or absent reporting of participa-
tion and non-participation in epidemiological studies was
also documented in two other surveys of the literature [4,5].
Finally, there is evidence that participation in epidemio-
logical studies may have declined in recent decades
[137,138], which underscores the need for transparent
13 (b). Give reasons for non-participation at each stage.
‘‘The main reasons for non-participation were the partic-
ipant was too ill or had died before interview (cases 30%,
controls , 1%), nonresponse (cases 2%, controls 21%),
refusal (cases 10%, controls 29%), and other reasons (refusal
by consultant or general practitioner, non-English speaking,
mental impairment) (cases 7%, controls 5%)’’ .
Explaining the reasons why people no longer participated
in a study or why they were excluded from statistical analyses
helps readers judge whether the study population was
representative of the target population and whether bias
was possibly introduced. For example, in a cross-sectional
health survey, non-participation due to reasons unlikely to be
related to health status (for example, the letter of invitation
was not delivered because of an incorrect address) will affect
the precision of estimates but will probably not introduce
bias. Conversely, if many individuals opt out of the survey
because of illness, or perceived good health, results may
underestimate or overestimate the prevalence of ill health in
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STROBE Explanation and Elaboration
13 (c). Consider use of a flow diagram.
An informative and well-structured flow diagram can
readily and transparently convey information that might
otherwise require a lengthy description , as in the
example above. The diagram may usefully include the main
results, such as the number of events for the primary
outcome. While we recommend the use of a flow diagram,
particularly for complex observational studies, we do not
propose a specific format for the diagram.
14. Descriptive data:
14 (a). Give characteristics of study participants (e.g.,
demographic, clinical, social) and information on
exposures and potential confounders.
Table. Characteristics of the Study Base at Enrolment,
Castellana G (Italy), 1985–1986
n ¼ 1458
n ¼ 511
n ¼ 513
Mean age at enrolment (SD)
Daily alcohol intake (%)
HCV, Hepatitis C virus.
aMales ,60 g ethanol/day, females ,30 g ethanol/day.
bMales .60 g ethanol/day, females .30 g ethanol/day.
Table adapted from Osella et al. .
Flow diagram from Hay et al. .
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STROBE Explanation and Elaboration
Readers need descriptions of study participants and their
exposures to judge the generalisability of the findings.
Information about potential confounders, including whether
and how they were measured, influences judgments about
study validity. We advise authors to summarize continuous
variables for each study group by giving the mean and
standard deviation, or when the data have an asymmetrical
distribution, as is often the case, the median and percentile
range (e.g., 25th and 75th percentiles). Variables that make up
a small number of ordered categories (such as stages of
disease I to IV) should not be presented as continuous
variables; it is preferable to give numbers and proportions for
each category (see also Box 4). In studies that compare
groups, the descriptive characteristics and numbers should be
given by group, as in the example above.
Inferential measures such as standard errors and con-
fidence intervals should not be used to describe the variability
of characteristics, and significance tests should be avoided in
descriptive tables. Also, P values are not an appropriate
criterion for selecting which confounders to adjust for in
analysis; even small differences in a confounder that has a
strong effect on the outcome can be important [144,145].
In cohort studies, it may be useful to document how an
exposure relates to other characteristics and potential
confounders. Authors could present this information in a
table with columns for participants in two or more exposure
categories, which permits to judge the differences in
confounders between these categories.
In case-control studies potential confounders cannot be
judged by comparing cases and controls. Control persons
represent the source population and will usually be different
from the cases in many respects. For example, in a study of
oral contraceptives and myocardial infarction, a sample of
young women with infarction more often had risk factors for
that disease, such as high serum cholesterol, smoking and a
positive family history, than the control group . This
does not influence the assessment of the effect of oral
contraceptives, as long as the prescription of oral contra-
ceptives was not guided by the presence of these risk
factors—e.g., because the risk factors were only established
after the event (see also Box 5). In case-control studies the
equivalent of comparing exposed and non-exposed for the
presence of potential confounders (as is done in cohorts) can
be achieved by exploring the source population of the cases:
if the control group is large enough and represents the source
population, exposed and unexposed controls can be com-
pared for potential confounders [121,147].
14 (b). Indicate the number of participants with missing
data for each variable of interest.
Table. Symptom End Points Used in Survival Analysis
CoughShort of BreathSleeplessness
Table adapted from Hay et al. .
As missing data may bias or affect generalisability of
results, authors should tell readers amounts of missing data
for exposures, potential confounders, and other important
characteristics of patients (see also item 12c and Box 6). In a
cohort study, authors should report the extent of loss to
follow-up (with reasons), since incomplete follow-up may bias
findings (see also items 12d and 13) . We advise authors
to use their tables and figures to enumerate amounts of
14 (c). Cohort study: Summarise follow-up time—e.g.,
average and total amount.
‘‘During the 4366 person-years of follow-up (median 5.4,
maximum 8.3 years), 265 subjects were diagnosed as having
dementia, including 202 with Alzheimer’s disease’’ .
Readers need to know the duration and extent of follow-up
for the available outcome data. Authors can present a
summary of the average follow-up with either the mean or
median follow-up time or both. The mean allows a reader to
calculate the total number of person-years by multiplying it
with the number of study participants. Authors also may
present minimum and maximum times or percentiles of the
distribution to show readers the spread of follow-up times.
They may report total person-years of follow-up or some
indication of the proportion of potential data that was
captured . All such information may be presented
separately for participants in two or more exposure
categories. Almost half of 132 articles in cancer journals
(mostly cohort studies) did not give any summary of length of
15. Outcome data:
Cohort study: Report numbers of outcome events or
summary measures over time.
Table. Rates of HIV-1 Seroconversion by Selected Sociodemo-
graphic Variables: 1990–1993
48 5.7 (4.1–7.3)
CI, confidence interval.
Table adapted from Kengeya-Kayondo et al. .
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STROBE Explanation and Elaboration
Case-control study: Report numbers in each exposure
category, or summary measures of exposure.
Table. Exposure among Liver Cirrhosis Cases and Controls
(n ¼ 40)
(n ¼ 139)
Vinyl chloride monomer
(cumulative exposure: ppm 3 years)
Alcohol consumption (g/day)
HBsAG, hepatitis B surface antigen; HCV, hepatitis C virus.
Table adapted from Mastrangelo et al. .
Cross-sectional study: Report numbers of outcome events
or summary measures.
Table. Prevalence of Current Asthma and Diagnosed Hay Fever
by Average Alternaria alternata Antigen Level in the Household
Diagnosed Hay Fever
93 16.4 (13.0–20.5)
*1st tertile , 3.90 lg/g; 2nd tertile 3.90–6.27 lg/g; 3rd tertile ? 6.28 lg/g.
?Percentage (95% CI) weighted for the multistage sampling design of the National Survey
of Lead and Allergens in Housing.
Table adapted from Salo et al. .
Before addressing the possible association between ex-
posures (risk factors) and outcomes, authors should report
relevant descriptive data. It may be possible and meaningful
to present measures of association in the same table that
presents the descriptive data (see item 14a). In a cohort
study with events as outcomes, report the numbers of events
for each outcome of interest. Consider reporting the event
rate per person-year of follow-up. If the risk of an event
changes over follow-up time, present the numbers and rates
of events in appropriate intervals of follow-up or as a
Kaplan-Meier life table or plot. It might be preferable to
show plots as cumulative incidence that go up from 0%
rather than down from 100%, especially if the event rate is
lower than, say, 30% . Consider presenting such
information separately for participants in different exposure
categories of interest. If a cohort study is investigating other
time-related outcomes (e.g., quantitative disease markers
such as blood pressure), present appropriate summary
measures (e.g., means and standard deviations) over time,
perhaps in a table or figure.
For cross-sectional studies, we recommend presenting the
same type of information on prevalent outcome events or
summary measures. For case-control studies, the focus will be
on reporting exposures separately for cases and controls as
frequencies or quantitative summaries . For all designs,
it may be helpful also to tabulate continuous outcomes or
exposures in categories, even if the data are not analysed as
16. Main results:
16 (a). Give unadjusted estimates and, if applicable,
confounder-adjusted estimates and their precision (e.g.,
95% confidence intervals). Make clear which confounders
were adjusted for and why they were included.
‘‘We initially considered the following variables as potential
confounders by Mantel-Haenszel stratified analysis: (...) The
variables we included in the final logistic regression models
were those (...) that produced a 10% change in the odds ratio
after the Mantel-Haenszel adjustment’’ .
Table. Relative Rates of Rehospitalisation by Treatment in
Patients in Community Care after First Hospitalisation due to
Schizophrenia and Schizoaffective Disorder
(0.29 to 0.59)
(0.45 to 0.75)
(0.47 to 0.79)
(0.58 to 1.09)
(0.63 to 1.12)
(0.58 to 0.82)
(0.60 to 0.99)
(0.69 to 1.29)
(0.84 to 1.73)
(0.77 to 1.23)
(0.32 to 0.65)
(0.43 to 0.72)
(0.41 to 0.69)
(0.61 to 1.15)
(0.61 to 1.10)
(0.59 to 1.03)
(0.62 to 1.03)
(0.71 to 1.33)
(0.58 to 1.18)
(0.80 to 1.27)
(0.22 to 0.49)
(0.41 to 0.71)
(0.48 to 0.85)
(0.45 to 0.91)
(0.51 to 0.96)
(0.63 to 1.13)
(0.69 to 1.16)
(0.76 to 1.47)
(0.76 to 1.57)
(0.91 to 1.47)
Adjusted for sex, calendar year, age at onset of follow-up, number of previous relapses,
duration of first hospitalisation, and length of follow-up (adjusted column) and
additionally for a score of the propensity to start a treatment other than haloperidol
(fully adjusted column).
Table adapted from Tiihonen et al. .
In many situations, authors may present the results of
unadjusted or minimally adjusted analyses and those from
fully adjusted analyses. We advise giving the unadjusted
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STROBE Explanation and Elaboration
analyses together with the main data, for example the
number of cases and controls that were exposed or not. This
allows the reader to understand the data behind the
measures of association (see also item 15). For adjusted
analyses, report the number of persons in the analysis, as this
number may differ because of missing values in covariates
(see also item 12c). Estimates should be given with
Readers can compare unadjusted measures of association
with those adjusted for potential confounders and judge by
how much, and in what direction, they changed. Readers may
think that ‘adjusted’ results equal the causal part of the
measure of association, but adjusted results are not necessa-
rily free of random sampling error, selection bias, informa-
tion bias, or residual confounding (see Box 5). Thus, great
care should be exercised when interpreting adjusted results,
as the validity of results often depends crucially on complete
knowledge of important confounders, their precise measure-
ment, and appropriate specification in the statistical model
(see also item 20) [157,158].
Authors should explain all potential confounders consid-
ered, and the criteria for excluding or including variables in
statistical models. Decisions about excluding or including
variables should be guided by knowledge, or explicit
assumptions, on causal relations. Inappropriate decisions
may introduce bias, for example by including variables that
are in the causal pathway between exposure and disease
(unless the aim is to asses how much of the effect is carried
by the intermediary variable). If the decision to include a
variable in the model was based on the change in the
estimate, it is important to report what change was
considered sufficiently important to justify its inclusion. If
a ‘backward deletion’ or ‘forward inclusion’ strategy was used
to select confounders, explain that process and give the
significance level for rejecting the null hypothesis of no
confounding. Of note, we and others do not advise selecting
confounders based solely on statistical significance testing
Recent studies of the quality of reporting of epidemio-
logical studies found that confidence intervals were reported
in most articles . However, few authors explained their
choice of confounding variables [4,5].
16 (b). Report category boundaries when continuous
variables were categorised.
Table. Polychlorinated Biphenyls in Cord Serum
Quartile Range (ng/g)Number
Table adapted from Sagiv et al. .
Categorizing continuous data has several important im-
plications for analysis (see Box 4) and also affects the
presentation of results. In tables, outcomes should be given
for each exposure category, for example as counts of persons
at risk, person-time at risk, if relevant separately for each
group (e.g., cases and controls). Details of the categories used
may aid comparison of studies and meta-analysis. If data were
grouped using conventional cut-points, such as body mass
index thresholds , group boundaries (i.e., range of values)
can be derived easily, except for the highest and lowest
categories. If quantile-derived categories are used, the
category boundaries cannot be inferred from the data. As a
minimum, authors should report the category boundaries; it
is helpful also to report the range of the data and the mean or
median values within categories.
16 (c). If relevant, consider translating estimates of
relative risk into absolute risk for a meaningful time
‘‘10 years’ use of HRT [hormone replacement therapy] is
estimated to result in five (95% CI 3–7) additional breast
cancers per 1000 users of oestrogen-only preparations and 19
(15–23) additional cancers per 1000 users of oestrogen-
progestagen combinations’’ .
The results from studies examining the association between
an exposure and a disease are commonly reported in relative
terms, as ratios of risks, rates or odds (see Box 8). Relative
measures capture the strength of the association between an
exposure and disease. If the relative risk is a long way from 1
it is less likely that the association is due to confounding
[164,165]. Relative effects or associations tend to be more
consistent across studies and populations than absolute
measures, but what often tends to be the case may be
irrelevant in a particular instance. For example, similar
relative risks were obtained for the classic cardiovascular risk
factors for men living in Northern Ireland, France, the USA
and Germany, despite the fact that the underlying risk of
coronary heart disease varies substantially between these
countries [166,167]. In contrast, in a study of hypertension as
a risk factor for cardiovascular disease mortality, the data
were more compatible with a constant rate difference than
with a constant rate ratio .
Widely used statistical models, including logistic  and
proportional hazards (Cox) regression  are based on
ratio measures. In these models, only departures from
constancy of ratio effect measures are easily discerned.
Nevertheless, measures which assess departures from addi-
tivity of risk differences, such as the Relative Excess Risk from
Interaction (RERI, see item 12b and Box 8), can be estimated
in models based on ratio measures.
In many circumstances, the absolute risk associated with an
exposure is of greater interest than the relative risk. For
example, if the focus is on adverse effects of a drug, one will
want to know the number of additional cases per unit time of
use (e.g., days, weeks, or years). The example gives the
additional number of breast cancer cases per 1000 women
who used hormone-replacement therapy for 10 years .
Measures such as the attributable risk or population
attributable fraction may be useful to gauge how much
disease can be prevented if the exposure is eliminated. They
should preferably be presented together with a measure of
statistical uncertainty (e.g., confidence intervals as in the
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STROBE Explanation and Elaboration
example). Authors should be aware of the strong assumptions
made in this context, including a causal relationship between
a risk factor and disease (also see Box 7) . Because of the
semantic ambiguity and complexities involved, authors
should report in detail what methods were used to calculate
attributable risks, ideally giving the formulae used .
A recent survey of abstracts of 222 articles published in
leading medical journals found that in 62% of abstracts of
randomised trials including a ratio measure absolute risks
were given, but only in 21% of abstracts of cohort studies
. A free text search of Medline 1966 to 1997 showed that
619 items mentioned attributable risks in the title or abstract,
compared to 18,955 using relative risk or odds ratio, for a
ratio of 1 to 31 .
17. Other analyses: Report other analyses done—e.g.,
analyses of subgroups and interactions, and sensitivity
Table. Analysis of Oral Contraceptive Use, Presence of Factor V
Leiden Allele, and Risk for Venous Thromboembolism
Table modified from Vandenbroucke et al.  by Botto et al. .
Table. Sensitivity of the Rate Ratio for Cardiovascular Outcome
to an Unmeasured Confounder
in the Exposed
in the Comparator
CI, confidence interval.
*Adjusted for age, sex, cardiovascular drug use, and unmeasured binary confounder.
Table adapted from Wei et al. .
In addition to the main analysis other analyses are often
done in observational studies. They may address specific
subgroups, the potential interaction between risk factors, the
calculation of attributable risks, or use alternative definitions
of study variables in sensitivity analyses.
There is debate about the dangers associated with
subgroup analyses, and multiplicity of analyses in general
[4,104]. In our opinion, there is too great a tendency to look
for evidence of subgroup-specific associations, or effect-
measure modification, when overall results appear to suggest
little or no effect. On the other hand, there is value in
exploring whether an overall association appears consistent
across several, preferably pre-specified subgroups especially
when a study is large enough to have sufficient data in each
subgroup. A second area of debate is about interesting
subgroups that arose during the data analysis. They might be
important findings, but might also arise by chance. Some
argue that it is neither possible nor necessary to inform the
reader about all subgroup analyses done as future analyses of
other data will tell to what extent the early exciting findings
stand the test of time . We advise authors to report which
Box 7. Measures of association, effect and impact
Observational studies may be solely done to describe the magnitude and
distribution of a health problem in the population. They may examine
the number of people who have a disease at a particular time
(prevalence), or that develop a disease over a defined period (incidence).
The incidence may be expressed as the proportion of people developing
the disease (cumulative incidence) or as a rate per person-time of follow-
up (incidence rate). Specific terms are used to describe different
incidences; amongst others, mortality rate, birth rate, attack rate, or
case fatality rate. Similarly, terms like point prevalence and period,
annual or lifetime prevalence are used to describe different types of
Other observational studies address cause-effect relationships. Their
focus is the comparison of the risk, rate or prevalence of the event of
interest between those exposed and those not exposed to the risk factor
under investigation. These studies often estimate a ‘relative risk’, which
may stand for risk ratios (ratios of cumulative incidences) as well as rate
ratios (ratios of incidence rates). In case-control studies only a fraction of
the source population (the controls) are included. Results are expressed
as the ratio of the odds of exposure among cases and controls. This odds
ratio provides an estimate of the risk or rate ratio depending on the
sampling of cases and controls (see also Box 1) [175,176]. The prevalence
ratio or prevalence odds ratio from cross-sectional studies may be useful
in some situations .
Expressing results both in relative and absolute terms may often be
helpful. For example, in a study of male British doctors the incidence rate
of death from lung cancer over 50 years of follow-up was 249 per
100,000 per year among smokers, compared to 17 per 100,000 per year
among non-smokers: a rate ratio of 14.6 (249/17) . For coronary
heart disease (CHD), the corresponding rates were 1001 and 619 per
100,000 per year, for a rate ratio of 1.61 (1001/619). The effect of smoking
on death appears much stronger for lung cancer than for CHD. The
picture changes when we consider the absolute effects of smoking. The
difference in incidence rates was 232 per 100,000 per year (249?17) for
lung cancer and 382 for CHD (1001 ? 619). Therefore, among doctors
who smoked, smoking was more likely to cause death from CHD than
from lung cancer.
How much of the disease burden in a population could be prevented by
eliminating an exposure? Global estimates have been published for
smoking: according to one study 91% of all lung cancers, 40% of CHD
and 33% of all deaths among men in 2000 were attributed to smoking
. The population attributable fraction is generally defined as the
proportion of cases caused by a particular exposure, but several
concepts (and no unified terminology) exist, and incorrect approaches
to adjust for other factors are sometimes used [172,180]. What are the
implications for reporting? The relative measures emphasise the strength
of an association, and are most useful in etiologic research. If a causal
relationship with an exposure is documented and associations are
interpreted as effects, estimates of relative risk may be translated into
suitable measures of absolute risk in order to gauge the possible impact
of public health policies (see item 16c) . However, authors should be
aware of the strong assumptions made in this context . Care is
needed in deciding which concept and method is appropriate for a
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STROBE Explanation and Elaboration
analyses were planned, and which were not (see also items 4,
12b and 20). This will allow readers to judge the implications
of multiplicity, taking into account the study’s position on the
continuum from discovery to verification or refutation.
A third area of debate is how joint effects and interactions
between risk factors should be evaluated: on additive or
multiplicative scales, or should the scale be determined by the
statistical model that fits best (see also item 12b and Box 8)? A
sensible approach is to report the separate effect of each
exposure as well as the joint effect—if possible in a table, as in
the first example above , or in the study by Martinelli et
al. . Such a table gives the reader sufficient information
to evaluate additive as well as multiplicative interaction (how
these calculations are done is shown in Box 8). Confidence
intervals for separate and joint effects may help the reader to
judge the strength of the data. In addition, confidence
intervals around measures of interaction, such as the Relative
Excess Risk from Interaction (RERI) relate to tests of
interaction or homogeneity tests. One recurrent problem is
that authors use comparisons of P-values across subgroups,
which lead to erroneous claims about an effect modifier. For
instance, a statistically significant association in one category
(e.g., men), but not in the other (e.g., women) does not in itself
provide evidence of effect modification. Similarly, the
confidence intervals for each point estimate are sometimes
inappropriately used to infer that there is no interaction
when intervals overlap. A more valid inference is achieved by
directly evaluating whether the magnitude of an association
differs across subgroups.
Sensitivity analyses are helpful to investigate the influence
of choices made in the statistical analysis, or to investigate the
robustness of the findings to missing data or possible biases
(see also item 12b). Judgement is needed regarding the level
of reporting of such analyses. If many sensitivity analyses were
performed, it may be impractical to present detailed findings
for them all. It may sometimes be sufficient to report that
sensitivity analyses were carried out and that they were
consistent with the main results presented. Detailed presen-
tation is more appropriate if the issue investigated is of major
concern, or if effect estimates vary considerably [59,186].
Pocock and colleagues found that 43 out of 73 articles
reporting observational studies contained subgroup analyses.
The majority claimed differences across groups but only eight
articles reported a formal evaluation of interaction (see item
The discussion section addresses the central issues of
validity and meaning of the study . Surveys have found
that discussion sections are often dominated by incomplete or
and rhetoric supporting the authors’ findings [192,193].
Structuring the discussion may help authors avoid unwar-
ranted speculation and over-interpretation of results while
guiding readers through the text [194,195]. For example,
Annals of Internal Medicine  recommends that authors
structure the discussion section by presenting the following:
(1) a brief synopsis of the key findings; (2) consideration of
possible mechanisms and explanations; (3) comparison with
relevant findings from other published studies; (4) limitations
of the study; and (5) a brief section that summarizes the
implications of the work for practice and research. Others
have made similar suggestions [191,194]. The section on
research recommendations and the section on limitations of
the study should be closely linked to each other. Investigators
on their studies rather than blandly stating ‘more research is
needed’ [197,198]. We recommend that authors structure their
discussion sections, perhaps also using suitable subheadings.
18. Key results: Summarise key results with reference to
‘‘We hypothesized that ethnic minority status would be
associated with higher levels of cardiovascular disease (CVD)
risk factors, but that the associations would be explained
substantially by socioeconomic status (SES). Our hypothesis
was not confirmed. After adjustment for age and SES, highly
significant differences in body mass index, blood pressure,
diabetes, and physical inactivity remained between white
women and both black and Mexican American women. In
a finding that illustrates the high-risk status of both ethnic
minority women as well as white women with low SES‘‘ .
Box 8. Interaction (effect modification): the analysis of joint
Interaction exists when the association of an exposure with the risk of
disease differs in the presence of another exposure. One problem in
evaluating and reporting interactions is that the effect of an exposure
can be measured in two ways: as a relative risk (or rate ratio) or as a risk
difference (or rate difference). The use of the relative risk leads to a
multiplicative model, while the use of the risk difference corresponds to
an additive model [187,188]. A distinction is sometimes made between
‘statistical interaction’ which can be a departure from either a
multiplicative or additive model, and ‘biologic interaction’ which is
measured by departure from an additive model . However, neither
additive nor multiplicative models point to a particular biologic
Regardless of the model choice, the main objective is to understand how
the joint effect of two exposures differs from their separate effects (in the
absence of the other exposure). The Human Genomic Epidemiology
Network (HuGENet) proposed a lay-out for transparent presentation of
separate and joint effects that permits evaluation of different types of
interaction . Data from the study on oral contraceptives and factor V
Leiden mutation  were used to explain the proposal, and this
example is also used in item 17. Oral contraceptives and factor V Leiden
mutation each increase the risk of venous thrombosis; their separate and
joint effects can be calculated from the 2 by 4 table (see example 1 for
item 17) where the odds ratio of 1 denotes the baseline of women
without Factor V Leiden who do not use oral contraceptives.
A difficulty is that some study designs, such as case-control studies, and
several statistical models, such as logistic or Cox regression models,
estimate relative risks (or rate ratios) and intrinsically lead to multi-
plicative modelling. In these instances, relative risks can be translated to
an additive scale. In example 1 of item 17, the separate odds ratios are
3.7 and 6.9; the joint odds ratio is 34.7. When these data are analysed
under a multiplicative model, a joint odds ratio of 25.7 is expected (3.73
6.9). The observed joint effect of 34.7 is 1.4 times greater than expected
on a multiplicative scale (34.7/25.7). This quantity (1.4) is the odds ratio of
the multiplicative interaction. It would be equal to the antilog of the
estimated interaction coefficient from a logistic regression model. Under
an additive model the joint odds ratio is expected to be 9.6 (3.7 þ 6.9 –
1). The observed joint effect departs strongly from additivity: the
difference is 25.1 (34.7 – 9.6). When odds ratios are interpreted as relative
risks (or rate ratios), the latter quantity (25.1) is the Relative Excess Risk
from Interaction (RERI) . This can be understood more easily when
imagining that the reference value (equivalent to OR¼1) represents a
baseline incidence of venous thrombosis of, say, 1/10 000 women-years,
which then increases in the presence of separate and joint exposures.
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STROBE Explanation and Elaboration
It is good practice to begin the discussion with a short
summary of the main findings of the study.The short summary
reminds readers of the main findings and may help them
assesswhether the subsequent interpretation and implications
offered by the authors are supported by the findings.
19. Limitations: Discuss limitations of the study, taking
into account sources of potential bias or imprecision.
Discuss both direction and magnitude of any potential
‘‘Since the prevalence of counseling increases with
increasing levels of obesity, our estimates may overestimate
the true prevalence. Telephone surveys also may over-
estimate the true prevalence of counseling. Although persons
without telephones have similar levels of overweight as
persons with telephones, persons without telephones tend
to be less educated, a factor associated with lower levels of
counseling in our study. Also, of concern is the potential bias
caused by those who refused to participate as well as those
who refused to respond to questions about weight. Further-
more, because data were collected cross-sectionally, we
cannot infer that counseling preceded a patient’s attempt
to lose weight’’ .
The identification and discussion of the limitations of a
study are an essential part of scientific reporting. It is
important not only to identify the sources of bias and
confounding that could have affected results, but also to
discuss the relative importance of different biases, including
the likely direction and magnitude of any potential bias (see
also item 9 and Box 3).
Authors should also discuss any imprecision of the results.
Imprecision may arise in connection with several aspects of a
study, including the study size (item 10) and the measurement
of exposures, confounders and outcomes (item 8). The
inability to precisely measure true values of an exposure
tends to result in bias towards unity: the less precisely a risk
factor is measured, the greater the bias. This effect has been
described as ‘attenuation’ [201,202], or more recently as
‘regression dilution bias’ . However, when correlated risk
factors are measured with different degrees of imprecision,
the adjusted relative risk associated with them can be biased
towards or away from unity [204–206].
When discussing limitations, authors may compare the
study being presented with other studies in the literature in
terms of validity, generalisability and precision. In this
approach, each study can be viewed as contribution to the
literature, not as a stand-alone basis for inference and
action . Surprisingly, the discussion of important
limitations of a study is sometimes omitted from published
reports. A survey of authors who had published original
research articles in The Lancet found that important
weaknesses of the study were reported by the investigators
in the survey questionnaires, but not in the published article
20. Interpretation: Give a cautious overall interpretation
considering objectives, limitations, multiplicity of
analyses, results from similar studies, and other relevant
‘‘Any explanation for an association between death from
myocardial infarction and use of second generation oral
contraceptives must be conjectural. There is no published
evidence to suggest a direct biologic mechanism, and there
are no other epidemiologic studies with relevant results. (...)
The increase in absolute risk is very small and probably
applies predominantly to smokers. Due to the lack of
corroborative evidence, and because the analysis is based on
relatively small numbers, more evidence on the subject is
needed. We would not recommend any change in prescribing
practice on the strength of these results’’ .
The heart of the discussion section is the interpretation of
a study’s results. Over-interpretation is common and human:
even when we try hard to give an objective assessment,
reviewers often rightly point out that we went too far in some
respects. When interpreting results, authors should consider
the nature of the study on the discovery to verification
continuum and potential sources of bias, including loss to
follow-up and non-participation (see also items 9, 12 and 19).
Due consideration should be given to confounding (item 16a),
the results of relevant sensitivity analyses, and to the issue of
multiplicity and subgroup analyses (item 17). Authors should
also consider residual confounding due to unmeasured
variables or imprecise measurement of confounders. For
example, socioeconomic status (SES) is associated with many
health outcomes and often differs between groups being
compared. Variables used to measure SES (income, educa-
tion, or occupation) are surrogates for other undefined and
unmeasured exposures, and the true confounder will by
definition be measured with error . Authors should
address the real range of uncertainty in estimates, which is
larger than the statistical uncertainty reflected in confidence
intervals. The latter do not take into account other
uncertainties that arise from a study’s design, implementa-
tion, and methods of measurement .
To guide thinking and conclusions about causality, some
may find criteria proposed by Bradford Hill in 1965 helpful
. How strong is the association with the exposure? Did it
precede the onset of disease? Is the association consistently
observed in different studies and settings? Is there supporting
evidence from experimental studies, including laboratory and
animal studies? How specific is the exposure’s putative effect,
and is there a dose-response relationship? Is the association
biologically plausible? These criteria should not, however, be
applied mechanically. For example, some have argued that
relative risks below 2 or 3 should be ignored [210,211]. This is
a reversal of the point by Cornfield et al. about the strength of
large relative risks (see item 12b) . Although a causal
effect is more likely with a relative risk of 9, it does not follow
that one below 3 is necessarily spurious. For instance, the
small increase in the risk of childhood leukaemia after
intrauterine irradiation is credible because it concerns an
adverse effect of a medical procedure for which no
alternative explanations are obvious . Moreover, the
carcinogenic effects of radiation are well established. The
doubling in the risk of ovarian cancer associated with eating 2
to 4 eggs per week is not immediately credible, since dietary
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STROBE Explanation and Elaboration
habits are associated with a large number of lifestyle factors
as well as SES . In contrast, the credibility of much
debated epidemiologic findings of a difference in thrombosis
risk between different types of oral contraceptives was greatly
enhanced by the differences in coagulation found in a
randomised cross-over trial . A discussion of the existing
external evidence, from different types of studies, should
always be included, but may be particularly important for
studies reporting small increases in risk. Further, authors
should put their results in context with similar studies and
explain how the new study affects the existing body of
evidence, ideally by referring to a systematic review.
21. Generalisability: Discuss the generalisability (external
validity) of the study results.
’’How applicable are our estimates to other HIV-1-infected
patients? This is an important question because the accuracy
of prognostic models tends to be lower when applied to data
other than those used to develop them. We addressed this
issue by penalising model complexity, and by choosing
models that generalised best to cohorts omitted from the
estimation procedure. Our database included patients from
many countries from Europe and North America, who were
treated in different settings. The range of patients was broad:
men and women, from teenagers to elderly people were
included, and the major exposure categories were well
represented. The severity of immunodeficiency at baseline
ranged from not measureable to very severe, and viral load
from undetectable to extremely high’’ .
Generalisability, also called external validity or applicabil-
ity, is the extent to which the results of a study can be applied
to other circumstances . There is no external validity per
se; the term is meaningful only with regard to clearly specified
conditions . Can results be applied to an individual,
groups or populations that differ from those enrolled in the
study with regard to age, sex, ethnicity, severity of disease,
and co-morbid conditions? Are the nature and level of
exposures comparable, and the definitions of outcomes
relevant to another setting or population? Are data that
were collected in longitudinal studies many years ago still
relevant today? Are results from health services research in
one country applicable to health systems in other countries?
The question of whether the results of a study have external
validity is often a matter of judgment that depends on the
study setting, the characteristics of the participants, the
exposures examined, and the outcomes assessed. Thus, it is
crucial that authors provide readers with adequate informa-
tion about the setting and locations, eligibility criteria, the
exposures and how they were measured, the definition of
outcomes, and the period of recruitment and follow-up. The
degree of non-participation and the proportion of unex-
posed participants in whom the outcome develops are also
relevant. Knowledge of the absolute risk and prevalence of
the exposure, which will often vary across populations, are
helpful when applying results to other settings and popula-
tions (see Box 7).
22. Funding: Give the source of funding and the role of
the funders for the present study and, if applicable, for the
original study on which the present article is based.
Some journals require authors to disclose the presence or
absence of financial and other conflicts of interest [100,218].
Several investigations show strong associations between the
source of funding and the conclusions of research articles
[219–222]. The conclusions in randomised trials recommen-
ded the experimental drug as the drug of choice much more
often (odds ratio 5.3) if the trial was funded by for-profit
organisations, even after adjustment for the effect size .
Other studies document the influence of the tobacco and
telecommunication industries on the research they funded
[224–227]. There are also examples of undue influence when
the sponsor is governmental or a non-profit organisation.
Authors or funders may have conflicts of interest that
influence any of the following: the design of the study ;
choice of exposures [228,229], outcomes , statistical
methods , and selective publication of outcomes 
and studies . Consequently, the role of the funders
should be described in detail: in what part of the study they
took direct responsibility (e.g., design, data collection,
analysis, drafting of manuscript, decision to publish) .
Other sources of undue influence include employers (e.g.,
university administrators for academic researchers and
government supervisors, especially political appointees, for
government researchers), advisory committees, litigants, and
special interest groups.
The STROBE Statement aims to provide helpful recom-
mendations for reporting observational studies in epidemi-
ology. Good reporting reveals the strengths and weaknesses of
a study and facilitates sound interpretation and application
of study results. The STROBE Statement may also aid in
planning observational studies, and guide peer reviewers and
editors in their evaluation of manuscripts.
We wrote this explanatory article to discuss the importance
of transparent and complete reporting of observational
studies, to explain the rationale behind the different items
included in the checklist, and to give examples from
published articles of what we consider good reporting. We
hope that the material presented here will assist authors and
editors in using STROBE.
We stress that STROBE and other recommendations on the
reporting of research [13,233,234] should be seen as evolving
documents that require continual assessment, refinement,
and, if necessary, change [235,236]. For example, the CON-
SORT Statement for the reporting of parallel-group random-
ized trials was first developed in the mid 1990s . Since
then members of the group have met regularly to review the
need to revise the recommendations; a revised version
appeared in 2001  and a further version is in develop-
ment. Similarly, the principles presented in this article and
the STROBE checklist are open to change as new evidence
and critical comments accumulate. The STROBE Web site
(http://www.strobe-statement.org/) provides a forum for dis-
cussion and suggestions for improvements of the checklist,
this explanatory document and information about the good
reporting of epidemiological studies.
PLoS Medicine | www.plosmedicine.org October 2007 | Volume 4 | Issue 10 | e2971649
STROBE Explanation and Elaboration
Several journals ask authors to follow the STROBE State-
ment in their instructions to authors (see http://www.
strobe-statement.org/ for current list). We invite other
journals to adopt the STROBE Statement and contact us
through our Web site to let us know. The journals publishing
the STROBE recommendations provide open access. The
STROBE Statement is therefore widely accessible to the
We are grateful to Gerd Antes, Kay Dickersin, Shah Ebrahim and
Richard Lilford for supporting the STROBE Initiative. We are
grateful to the following institutions that have hosted working
meetings: Institute of Social and Preventive Medicine (ISPM),
University of Bern, Switzerland; Department of Social Medicine,
University of Bristol, UK; London School of Hygiene & Tropical
Medicine, London, UK; Nordic Cochrane Centre, Copenhagen,
Denmark; and Centre for Statistics in Medicine, Oxford, UK. We
are grateful to four anonymous reviewers who provided helpful
comments on a previous draft of this paper.
Contributors to the STROBE Initiative. The following persons have
contributed to the content and elaboration of the STROBE State-
ment: Douglas G. Altman, Maria Blettner, Paolo Boffetta, Hermann
Brenner, Genevie `ve Che ˆne, Cyrus Cooper, George Davey-Smith, Erik
von Elm, Matthias Egger, France Gagnon, Peter C. Gøtzsche, Philip
Greenland, Sander Greenland, Claire Infante-Rivard, John Ioannidis,
Astrid James, Giselle Jones, Bruno Ledergerber, Julian Little,
Margaret May, David Moher, Hooman Momen, Alfredo Morabia,
Hal Morgenstern, Cynthia D. Mulrow, Fred Paccaud, Stuart J. Pocock,
Charles Poole, Martin Ro ¨o ¨sli, Dietrich Rothenbacher, Kenneth
Rothman, Caroline Sabin, Willi Sauerbrei, Lale Say, James J.
Schlesselman, Jonathan Sterne, Holly Syddall, Jan P. Vandenbroucke,
Ian White, Susan Wieland, Hywel Williams, Guang Yong Zou.
Author contributions. All authors contributed to the writing of the
paper. JPV, EvE, DGA, PCG, SJP, and ME wrote the first draft of
different sections of the paper. EvE takes care of most of the practical
coordination of STROBE. ME initiated STROBE and, together with
EvE, organised the first workshop.
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