Guideline
Strengthening the Reporting of Observational Studies in Epidemiology
(STROBE): Explanation and elaboration
Q7
Jan P. Vandenbroucke
a
, Erik von Elm
b
,
c
, Douglas G. Altman
d
, Peter C. Gøtzsche
e
,
Cynthia D. Mulrow
f
, Stuart J. Pocock
g
, Charles Poole
h
, James J. Schlesselman
i
,
Matthias Egger
b
,
j
,
*
, for the STROBE Initiative
a
Department of Clinical Epidemiology, Leiden University Medical Center, Leiden, The Netherlands
Q
1
b
Institute of Social & Preventive Medicine (ISPM), University of Bern, Bern, Switzerland
c
Department of Medical Biometry and Medical Informatics, University Medical Centre, Freiburg, Germany
d
Cancer Research UK/NHS Centre for Statistics in Medicine, Oxford, United Kingdom
e
Nordic Cochrane Centre, Rigshospitalet, Copenhagen, Denmark
f
University of Texas Health Science Center, San Antonio, United States
g
Medical Statistics Unit, London School of Hygiene and Tropical Medicine, London, United Kingdom
h
Department of Epidemiology, University of North Carolina School of Public Health, Chapel Hill, United States
i
Department of Biostatistics, University of Pittsburgh Graduate School of Public Health, and University of Pittsburgh Cancer Institute,
Pittsburgh, United States
j
Department of Social Medicine, University of Bristol, Bristol, United Kingdom
abstract
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) recommendations 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 studie s, caseecontrol 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
research.
© 2014 Published by Elsevier Ltd on behalf of Surgical Associates Ltd. This is an open access article under
the CC BY-NC-ND license (http://creativecommons.org/licenses/by-nc-nd/3.0/).
1. Introduction
Q2
Rational health care practices require knowledge about the
aetiology and pathogenesis, diagnosis, prognosis and treatment of
diseases. Randomised trials provide valuable evidence about
treatments and other interventions. However, much of clinical or
public health knowledge comes from observational research [1].
About nine of ten research papers published in clinical speciality
journals describe observational research [2,3].
Abbreviations: CI, confidence interval; RERI, Relative Excess Risk from Interac-
tion; RR, relative risk; STROBE, Strengthening the Reporting of Observational
Studies in Epidemiology.
* Corresponding author. Institute of Social & Preventive Medicine (ISPM), Uni-
versity of Bern, Bern, Switzerland.
E-mail addresses: strobe@ispm.unibe.ch, egger@ispm.unibe.ch (M. Egger).
Contents lists available at ScienceDirect
International Journal of Surgery
journal homepage: www.journal-surgery.net
http://dx.doi.org/10.1016/j.ijsu.2014.07.014
1743-9191/© 2014 Published by Elsevier Ltd on behalf of Surgical Associates Ltd. This is an open access article under the CC BY-NC-ND license (http://creativecommons.org/
licenses/by-nc-nd/3.0/).
International Journal of Surgery xxx (2014) 1e25
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Please cite this article in press as: J.P. Vandenbroucke, et al., Strengthening the Reporting of Observational Studies in Epidemiology (STROBE):
Explanation and elaboration, International Journal of Surgery (2014), http://dx.doi.org/10.1016/j.ijsu.2014.07.014
source: https://doi.org/10.7892/boris.55060 | downloaded: 29.1.2021
2. The STROBE Statement
Reporting of observational researc h is often not detailed and
clear enough to assess the strengths and weaknesses of the
investigation [4,5]. To improve the reporting of ob servational
research, we developed a checklist of items that should be
addressed: the Strengthening the Reporting of O bservational
Studies in Epide miology (STROBE) Statement ( Table 1). Items
relate to title, abstract, introduction, methods, results and
discussion sections of articles. The STROBE Statement has
recently been pu blished in several jo urnals [6].Ouraimisto
ensure clear presentation of what was planned, done, and
found in an observational study. We stress that the recom-
mendations are not prescriptions for setting up or conducting
studies, nor do they dictate methodology or mandate a uniform
presentation.
Table 1
The STROBE Statementdchecklist of items that should be addressed in reports of observational studies.
Item
number
Recommendation
Title and Abstract 1 (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
Introduction
Background/Rationale 2 Explain the scientific background and rationale for the investigation being reported
Objectives 3 State specific objectives, including any pre-specified hypotheses
Methods
Study design 4 Present key elements of study design early in the paper
Setting 5 Describe the setting, locations, and relevant dates, including periods of recruitment, exposure, follow-up, and data collection
Participants 6 (a) Cohort studydGive the eligibility criteria, and the sources and methods of selection of participants. Describe methods
of follow-up
Caseecontrol studydGive 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 studydGive the eligibility criteria, and the sources and methods of selection of participants
(b) Cohort studydFor matched studies, give matching criteria and number of exposed and unexposed Caseecontrol
studydFor matched studies, give matching criteria and the number of controls per case
Variables 7 Clearly define all outcomes, exposures, predictors, potential confounders, and effect modifi ers. Give diagnostic criteria,
if applicable
Data sources/
measurement
8
a
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
Bias 9 Describe any efforts to address potential sources of bias
Study size 10 Explain how the study size was arrived at
Quantitative variables 11 Explain how quantitative variables were handled in the analyses. If applicable, describe which groupings were chosen,
and why
Statistical methods 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 studydIf applicable, explain how loss to follow-up was addressed Caseecontrol study dIf applicable, explain
how matching of cases and controls was addressed Cross-sectional studydIf applicable, describe analytical methods
taking account of sampling strategy
(e) Describe any sensitivity analyses
Results
Participants 13
a
(a) Report the numbers of individuals at each stage of the studyde.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
Descriptive 14
a
(a) Give characteristics of study participants (e.g., demographic, clinical, social) and information on exposures and
potential data confounders
(b) Indicate the number of participants with missing data for each variable of interest
(c) Cohort studydsummarise follow-up time (e.g., average and total amount)
Outcome data 15
a
Cohort studydReport numbers of outcome events or summary measures over time
Caseecontrol studydReport numbers in each exposure category, or summary measures of exposure Cross-sectional
studydReport numbers of outcome events or summary measures
Main results 16 (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
Other analyses 17 Report other analyses donede.g., analyses of subgroups and interactions, and sensitivity analyses
Discussion
Key results 18 Summarise key results with reference to study objectives
Limitations 19 Discuss limitations of the study, taking into account sources of potential bias or imprecision. Discuss both direction
and magnitude of any potential bias
Interpretation 20 Give a cautious overall interpretation of results considering objectives, limitations, multiplicity of analyses, results
from similar studies, and other relevant evidence
Generalisability 21 Discuss the generalisability (external validity) of the study results.
Other information
Funding 22 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.
a
Give such information separately for cases and controls in caseecontrol 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, caseecontrol, and cross-sectional studies are
available on the STROBE Web site at http://www.strobe-statement.org/.
J.P. Vandenbroucke et al. / International Journal of Surgery xxx (2014) 1e252
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STROBE provides general reporting recommendations for
descriptive observational studies and studies that investigate as-
sociations between exposures and health outcomes. STROBE ad-
dresses the three main types of observational studies: cohort,
caseecontrol and cross-sectional studies. Authors use diverse ter-
minology 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 [7] or
imprecisely [8].InBox 1 we describe the hallmarks of the three
study designs.
3. 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 ex-
plorations. 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 [9], but further studies to
confirm or refute initial observations are often needed [10]. 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 pre-
determined sample size. STROBE tries to accommodate these
diverse uses of observational research - from discovery to refuta-
tion or confirmation. Where necessary we will indicate in what
circumstances specific recommendations apply.
4. How to use this paper
This paper is linked to the shorter STROBE paper that introduced
the items of the checklist in several journals [6], and forms an in-
tegral 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 explana-
tion 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 1e
8 with supplementary infor-
mation. These are intended for readers who want to refresh their
Box 1
Main study designs covered by STROBE.
Cohort, caseecontrol, 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 factors.
In cohort studies, the investigators follow people overtime. 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 unex-
posed groups are compared, this leads to risk ratio or rate ratio estimates. Open cohorts estimate incidence rates and rate ratios.
In caseecontrol 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 caseecontrol study is interpreted as the risk ratio, rate ratio or (prevalence) odds ratio [16,17]. The majority of
published caseecontrol studies sample open cohorts and so allow direct estimations of rate ratios.
In cross-sectional studies, investigators assess all individuals in a sample at the same point in time, often to examine the prev-
alence 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 caseecontrol 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 same time.
J.P. Vandenbroucke et al. / International Journal of Surgery xxx (2014) 1e25 3
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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 pa-
pers that are cited.
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 recommendations useful. For authors of
observational studies that specifically address diagnostic tests,
tumour markers and genetic associations, STARD [13], REMARK
[14], and STREGA [15] recommendations may be particularly useful.
5. 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 caseecontrol studies, or exposed and unex-
posed groups in cohort and cross-sectional studies. We advise au-
thors 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.
6. The items
6.1. Title and Abstract
1(a). Indicate the study's design with a commonly used term in
the title or the abstract.
Example
“Leukaemia incidence among workers in the shoe and boot
manufacturing industry: a caseecontrol study” [18].
Explanation
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].
1(b). Provide in the abstract an informative and balanced sum-
mary of what was done and what was found.
Example
“Background: The expected survival of HIV-infected patients is
of major public health interest.
Box 2
Matching in caseecontrol studies.
In any caseecontrol 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 caseecontrol 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 caseecontrol study
of myocardial infarction and oral contraceptives nested in a large pharmacoepidemiologic database, 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) [52]. Also, the effect of the matching factor can no longer be studied, and the search for
well-matched controls can be cumbersome e 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 caseecontrol 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 [53]. 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
caseecontrol studies. They recommend instead a careful and judicious consideration of each potential matching factor, recog-
nizing 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 caseecontrol studies with no matching at all [54]. 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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Objective: To estimate survival time and age-specific mortality
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 KaplaneMeier 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 2,689,28 7 (median, 8.4 years/person)
person-years of observation. Three percent of participants were
lost to fol low-up. From age 25 years , the median survival was 19.9
years (95% CI, 18.5e21.3) among patients with HIV infection and
51.1 years (CI, 50.9e51.5) amo ng the general population. For HI V-
infected patients, s urv ival increased to 32.5 years (CI, 29.4e34.7)
during the 2000 to 2005 period. In the subgroup that excluded
persons with known hepatitis C coinfection (16%), median sur-
vival was 38.9 years (CI, 35.4e 40.1) during this same period. The
relative mortality rates for pati ents with HIV in fection compared
with th ose for the general popula tion decreased with increasing
age, w hereas the excess mortality rate increased wi th increasing
age.
Limitations: The observed mortality rates are assumed to apply
beyond the current maximum observation time of 10 years.
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” [21].
Explanation
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 [22] . 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 partici-
pants, estimates of associations and appropriate measures of vari-
ability 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 [23]. Many journals require such
structured abstracts, which tend to be of higher quality and more
readily informative than unstructured summaries [24,25].
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 selection bias.
Information bias occurs when systematic differences in the completeness or the accuracy of data lead to differential misclassi-
fication 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) [65]. 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 e 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 sur-
veillance in the different study groups, and to adjust for it in statistical analyses. In caseecontrol 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 caseecontrol 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 [72].
‘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).
J.P. Vandenbroucke et al. / International Journal of Surgery xxx (2014) 1e25 5
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IJSU1454_proof ■ 18 July 2014 ■ 5/25
Please cite this article in press as: J.P. Vandenbroucke, et al., Strengthening the Reporting of Observational Studies in Epidemiology (STROBE):
Explanation and elaboration, International Journal of Surgery (2014), http://dx.doi.org/10.1016/j.ijsu.2014.07.014