ArticlePDF AvailableLiterature Review

The PRISMA Statement for Reporting Systematic Reviews and Meta-Analyses of Studies That Evaluate Health Care Interventions: Explanation and Elaboration

Authors:

Abstract and Figures

Systematic reviews and meta-analyses are essential to summarize evidence relating to efficacy and safety of health care interventions accurately and reliably. The clarity and transparency of these reports, however, is not optimal. Poor reporting of systematic reviews diminishes their value to clinicians, policy makers, and other users.Since the development of the QUOROM (QUality Of Reporting Of Meta-analysis) Statement--a reporting guideline published in 1999--there have been several conceptual, methodological, and practical advances regarding the conduct and reporting of systematic reviews and meta-analyses. Also, reviews of published systematic reviews have found that key information about these studies is often poorly reported. Realizing these issues, an international group that included experienced authors and methodologists developed PRISMA (Preferred Reporting Items for Systematic reviews and Meta-Analyses) as an evolution of the original QUOROM guideline for systematic reviews and meta-analyses of evaluations of health care interventions.The PRISMA Statement consists of a 27-item checklist and a four-phase flow diagram. The checklist includes items deemed essential for transparent reporting of a systematic review. In this Explanation and Elaboration document, we explain the meaning and rationale for each checklist item. For each item, we include an example of good reporting and, where possible, references to relevant empirical studies and methodological literature. The PRISMA Statement, this document, and the associated Web site (http://www.prisma-statement.org/) should be helpful resources to improve reporting of systematic reviews and meta-analyses.
Content may be subject to copyright.
1
Guidelines and Guidance
The PRISMA Statement for Reporting Systematic Reviews
and Meta-Analyses of Studies That Evaluate Health Care
Interventions: Explanation and Elaboration
Alessandro Liberati
1,2
*, Douglas G. Altman
3
, Jennifer Tetzlaff
4
, Cynthia Mulrow
5
, Peter C. Gøtzsche
6
,
John P. A. Ioannidis
7
, Mike Clarke
8,9
, P. J. Devereaux
10
, Jos Kleijnen
11,12
, David Moher
4,13
1Universita
`di Modena e Reggio Emilia, Modena, Italy, 2Centro Cochrane Italiano, Istituto Ricerche Farmacologiche Mario Negri, Milan, Italy, 3Centre for Statistics in
Medicine, University of Oxford, Oxford, United Kingdom, 4Ottawa Methods Centre, Ottawa Hospital Research Institute, Ottawa, Ontario, Canada, 5Annals of Internal
Medicine, Philadelphia, Pennsylvania, United States of America, 6The Nordic Cochrane Centre, Copenhagen, Denmark, 7Department of Hygiene and Epidemiology,
University of Ioannina School of Medicine, Ioannina, Greece, 8UK Cochrane Centre, Oxford, United Kingdom, 9School of Nursing and Midwifery, Trinity College, Dublin,
Ireland, 10 Departments of Medicine, Clinical Epidemiology and Biostatistics, McMaster University, Hamilton, Ontario, Canada, 11 Kleijnen Systematic Reviews Ltd, York,
United Kingdom, 12 School for Public Health and Primary Care (CAPHRI), University of Maastricht, Maastricht, The Netherlands, 13 Department of Epidemiology and
Community Medicine, Faculty of Medicine, Ottawa, Ontario, Canada
Abstract: Systematic reviews and meta-analyses are
essential to summarize evidence relating to efficacy and
safety of health care interventions accurately and reliably.
The clarity and transparency of these reports, however, is
not optimal. Poor reporting of systematic reviews
diminishes their value to clinicians, policy makers, and
other users. Since the development of the QUOROM
(QUality OfReporting OfMeta-analysis) Statement—a
reporting guideline published in 1999—there have been
several conceptual, methodological, and practical advanc-
es regarding the conduct and reporting of systematic
reviews and meta-analyses. Also, reviews of published
systematic reviews have found that key information about
these studies is often poorly reported. Realizing these
issues, an international group that included experienced
authors and methodologists developed PRISMA (Preferred
Reporting Items for Systematic reviews and Meta-Analy-
ses) as an evolution of the original QUOROM guideline for
systematic reviews and meta-analyses of evaluations of
health care interventions. The PRISMA Statement con-
sists of a 27-item checklist and a four-phase flow diagram.
The checklist includes items deemed essential for
transparent reporting of a systematic review. In this
Explanation and Elaboration document, we explain the
meaning and rationale for each checklist item. For each
item, we include an example of good reporting and,
where possible, references to relevant empirical studies
and methodological literature. The PRISMA Statement,
this document, and the associated Web site (http://www.
prisma-statement.org/) should be helpful resources to
improve reporting of systematic reviews and meta-
analyses.
Introduction
Systematic reviews and meta-analyses are essential tools for
summarizing evidence accurately and reliably. They help
clinicians keep up-to-date; provide evidence for policy makers to
judge risks, benefits, and harms of health care behaviors and
interventions; gather together and summarize related research for
patients and their carers; provide a starting point for clinical
practice guideline developers; provide summaries of previous
research for funders wishing to support new research [1]; and help
editors judge the merits of publishing reports of new studies [2].
Recent data suggest that at least 2,500 new systematic reviews
reported in English are indexed in MEDLINE annually [3].
Unfortunately, there is considerable evidence that key informa-
tion is often poorly reported in systematic reviews, thus
diminishing their potential usefulness [3,4,5,6]. As is true for all
research, systematic reviews should be reported fully and
transparently to allow readers to assess the strengths and
weaknesses of the investigation [7]. That rationale led to the
development of the QUOROM (QUality OfReporting OfMeta-
analyses) Statement; those detailed reporting recommendations
were published in 1999 [8]. In this paper we describe the updating
Citation: Liberati A, Altman DG, Tetzlaff J, Mulrow C, Gøtzsche PC, et al. (2009) The
PRISMA Statement for Reporting Systematic Reviews and Meta-Analyses of
Studies That Evaluate Health Care Interventions: Explanation and
Elaboration. PLoS Med 6(7): e1000100. doi:10.1371/journal.pmed.1000100
Published July 21, 2009
Copyright: ß2009 Liberati 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.
Funding: PRISMA was funded by the Canadian Institutes of Health Research;
Universita
`di Modena e Reggio Emilia, Italy; Cancer Research UK; Clinical Evidence
BMJ Knowledge; The Cochrane Collaboration; and GlaxoSmithKline, Canada. AL is
funded, in part, through grants of the Italian Ministry of University (COFIN - PRIN
2002 prot. 2002061749 and COFIN - PRIN 2006 prot. 2006062298). DGA is funded
by Cancer Research UK. DM is funded by a University of Ottawa Research Chair.
None of the sponsors had any involvement in the planning, execution, or write-up
of the PRISMA documents. Additionally, no funder played a role in drafting the
manuscript.
Competing Interests: MC’s employment is as Director of the UK Cochrane
Centre. He is employed by the Oxford Radcliffe Hospitals Trust on behalf of the
Department of Health and the National Institute for Health Research in England.
This is a fixed term contract, the renewal of which is dependent upon the value
placed upon his work, that of the UK Cochrane Centre, and of The Cochrane
Collaboration more widely by the Department of Health. His work involves the
conduct of systematic reviews and the support of the conduct and use of
systematic reviews. Therefore, work–such as this manuscript–relating to
systematic reviews might have an impact on his employment.
Abbreviations: PICOS, participants, interventions, comparators, outcomes, and
study design; PRISMA, Preferred Reporting Items for Systematic reviews and
Meta-Analyses; QUOROM, QUality OfReporting OfMeta-analyses.
* E-mail: alesslib@mailbase.it
Provenance: Not commissioned; externally peer reviewed. In order to
encourage dissemination of the PRISMA explanatory paper, this article is freely
accessible on the PLoS Medicine,Annals of Internal Medicine,andBMJ Web sites.
The authors jointly hold the copyright of this article. For details on further use see
the PRISMA Web site (http://www.prisma-statement.org/).
PLoS Medicine | www.plosmedicine.org 1 July 2009 | Volume 6 | Issue 7 | e1000100
of that guidance. Our aim is to ensure clear presentation of what
was planned, done, and found in a systematic review.
Terminology used to describe systematic reviews and meta-
analyses has evolved over time and varies across different groups of
researchers and authors (see Box 1). In this document we adopt the
definitions used by the Cochrane Collaboration [9]. A systematic
review attempts to collate all empirical evidence that fits pre-
specified eligibility criteria to answer a specific research question.
It uses explicit, systematic methods that are selected to minimize
bias, thus providing reliable findings from which conclusions can
be drawn and decisions made. Meta-analysis is the use of statistical
methods to summarize and combine the results of independent
studies. Many systematic reviews contain meta-analyses, but not
all.
The QUOROM Statement and Its Evolution into
PRISMA
The QUOROM Statement, developed in 1996 and published
in 1999 [8], was conceived as a reporting guidance for authors
reporting a meta-analysis of randomized trials. Since then, much
has happened. First, knowledge about the conduct and reporting
of systematic reviews has expanded considerably. For example,
The Cochrane Library’s Methodology Register (which includes
reports of studies relevant to the methods for systematic reviews)
now contains more than 11,000 entries (March 2009). Second,
there have been many conceptual advances, such as ‘‘outcome-
level’’ assessments of the risk of bias [10,11], that apply to
systematic reviews. Third, authors have increasingly used
systematic reviews to summarize evidence other than that
provided by randomized trials.
However, despite advances, the quality of the conduct and
reporting of systematic reviews remains well short of ideal
[3,4,5,6]. All of these issues prompted the need for an update
and expansion of the QUOROM Statement. Of note, recognizing
that the updated statement now addresses the above conceptual
and methodological issues and may also have broader applicability
than the original QUOROM Statement, we changed the name of
the reporting guidance to PRISMA (Preferred Reporting Items for
Systematic reviews and Meta-Analyses).
Development of PRISMA
The PRISMA Statement was developed by a group of 29 review
authors, methodologists, clinicians, medical editors, and consum-
ers [12]. They attended a three-day meeting in 2005 and
participated in extensive post-meeting electronic correspondence.
A consensus process that was informed by evidence, whenever
possible, was used to develop a 27-item checklist (Table 1; see also
Text S1 for a downloadable template checklist for researchers to
re-use) and a four-phase flow diagram (Figure 1; see Figure S1 for
a downloadable template document for researchers to re-use).
Items deemed essential for transparent reporting of a systematic
review were included in the checklist. The flow diagram originally
proposed by QUOROM was also modified to show numbers of
identified records, excluded articles, and included studies. After 11
revisions the group approved the checklist, flow diagram, and this
explanatory paper.
The PRISMA Statement itself provides further details
regarding its background and development [12]. This accom-
panying Explanation and Elaboration document explains the
meaning and rationale for each checklist item. A few PRISMA
Group participants volunteered to help draft specific items for
this document, and four of these (DGA, AL, DM, and JT) met
on several occasions to further refine the document, which was
circulated and ultimately approved by the larger PRISMA
Group.
Box 1. Terminology
The terminology used to describe systematic reviews and
meta-analyses has evolved over time and varies between
fields. Different terms have been used by different groups,
such as educators and psychologists. The conduct of a
systematic review comprises several explicit and repro-
ducible steps, such as identifying all likely relevant records,
selecting eligible studies, assessing the risk of bias,
extracting data, qualitative synthesis of the included
studies, and possibly meta-analyses.
Initially this entire process was termed a meta-analysis
and was so defined in the QUOROM Statement [8]. More
recently, especially in health care research, there has been a
trend towards preferring the term systematic review. If
quantitative synthesis is performed, this last stage alone is
referred to as a meta-analysis. The Cochrane Collaboration
uses this terminology [9], under which a meta-analysis, if
performed, is a component of a systematic review.
Regardless of the question addressed and the complexities
involved, it is always possible to complete a systematic
review of existing data, but not always possible, or
desirable, to quantitatively synthesize results, due to clinical,
methodological, or statistical differences across the includ-
ed studies. Conversely, with prospective accumulation of
studies and datasets where the plan is eventually to
combine them, the term ‘‘(prospective) meta-analysis’’
may make more sense than ‘‘systematic review.’’
For retrospective efforts, one possibility is to use the
term systematic review for the whole process up to the
point when one decides whether to perform a quantitative
synthesis. If a quantitative synthesis is performed, some
researchers refer to this as a meta-analysis. This definition
is similar to that found in the current edition of the
Dictionary of Epidemiology [183].
While we recognize that the use of these terms is
inconsistent and there is residual disagreement among the
members of the panel working on PRISMA, we have adopted
the definitions used by the Cochrane Collaboration [9].
Systematic review: A systematic review attempts to
collate all empirical evidence that fits pre-specified
eligibility criteria to answer a specific research question.
It uses explicit, systematic methods that are selected with
a view to minimizing bias, thus providing reliable findings
from which conclusions can be drawn and decisions made
[184,185]. The key characteristics of a systematic review
are: (a) a clearly stated set of objectives with an explicit,
reproducible methodology; (b) a systematic search that
attempts to identify all studies that would meet the
eligibility criteria; (c) an assessment of the validity of the
findings of the included studies, for example through the
assessment of risk of bias; and (d) systematic presentation,
and synthesis, of the characteristics and findings of the
included studies.
Meta-analysis: Meta-analysis is the use of statistical
techniques to integrate and summarize the results of
included studies. Many systematic reviews contain meta-
analyses, but not all. By combining information from all
relevant studies, meta-analyses can provide more precise
estimates of the effects of health care than those derived
from the individual studies included within a review.
PLoS Medicine | www.plosmedicine.org 2 July 2009 | Volume 6 | Issue 7 | e1000100
Table 1. Checklist of items to include when reporting a systematic review (with or without meta-analysis).
Section/Topic #Checklist Item Reported on Page #
TITLE
Title 1 Identify the report as a systematic review, meta-analysis, or both.
ABSTRACT
Structured summary 2 Provide a structured summary including, as applicable: background; objectives; data sources; study eligibility
criteria, participants, and interventions; study appraisal and synthesis methods; results; limitations; conclusions
and implications of key findings; systematic review registration number.
INTRODUCTION
Rationale 3 Describe the rationale for the review in the context of what is already known.
Objectives 4 Provide an explicit statement of questions being addressed with reference to participants, interventions,
comparisons, outcomes, and study design (PICOS).
METHODS
Protocol and registration 5 Indicate if a review protocol exists, if and where it can be accessed (e.g., Web address), and, if available, provide
registration information including registration number.
Eligibility criteria 6 Specify study characteristics (e.g., PICOS, length of follow-up) and report characteristics (e.g., years considered,
language, publication status) used as criteria for eligibility, giving rationale.
Information sources 7 Describe all information sources (e.g., databases with dates of coverage, contact with study authors to identify
additional studies) in the search and date last searched.
Search 8 Present full electronic search strategy for at least one database, including any limits used, such that it could be
repeated.
Study selection 9 State the process for selecting studies (i.e., screening, eligibility, included in systematic review, and, if applicable,
included in the meta-analysis).
Data collection process 10 Describe method of data extraction from reports (e.g., piloted forms, independently, in duplicate) and any
processes for obtaining and confirming data from investigators.
Data items 11 List and define all variables for which data were sought (e.g., PICOS, funding sources) and any assumptions and
simplifications made.
Risk of bias in individual
studies
12 Describe methods used for assessing risk of bias of individual studies (including specification of whether this was
done at the study or outcome level), and how this information is to be used in any data synthesis.
Summary measures 13 State the principal summary measures (e.g., risk ratio, difference in means).
Synthesis of results 14 Describe the methods of handling data and combining results of studies, if done, including measures of
consistency (e.g., I
2
) for each meta-analysis.
Risk of bias across studies 15 Specify any assessment of risk of bias that may affect the cumulative evidence (e.g., publication bias, selective
reporting within studies).
Additional analyses 16 Describe methods of additional analyses (e.g., sensitivity or subgroup analyses, meta-regression), if done,
indicating which were pre-specified.
RESULTS
Study selection 17 Give numbers of studies screened, assessed for eligibility, and included in the review, with reasons for exclusions
at each stage, ideally with a flow diagram.
Study characteristics 18 For each study, present characteristics for which data were extracted (e.g., study size, PICOS, follow-up period)
and provide the citations.
Risk of bias within studies 19 Present data on risk of bias of each study and, if available, any outcome-level assessment (see Item 12).
Results of individual
studies
20 For all outcomes considered (benefits or harms), present, for each study: (a) simple summary data for each
intervention group and (b) effect estimates and confidence intervals, ideally with a forest plot.
Synthesis of results 21 Present results of each meta-analysis done, including confidence intervals and measures of consistency.
Risk of bias across studies 22 Present results of any assessment of risk of bias across studies (see Item 15).
Additional analysis 23 Give results of additional analyses, if done (e.g., sensitivity or subgroup analyses, meta-regression [see Item 16]).
DISCUSSION
Summary of evidence 24 Summarize the main findings including the strength of evidence for each main outcome; consider their
relevance to key groups (e.g., health care providers, users, and policy makers).
Limitations 25 Discuss limitations at study and outcome level (e.g., risk of bias), and at review level (e.g., incomplete retrieval of
identified research, reporting bias).
Conclusions 26 Provide a general interpretation of the results in the context of other evidence, and implications for future
research.
FUNDING
Funding 27 Describe sources of funding for the systematic review and other support (e.g., supply of data); role of funders for
the systematic review.
doi:10.1371/journal.pmed.1000100.t001
PLoS Medicine | www.plosmedicine.org 3 July 2009 | Volume 6 | Issue 7 | e1000100
Scope of PRISMA
PRISMA focuses on ways in which authors can ensure the
transparent and complete reporting of systematic reviews and
meta-analyses. It does not address directly or in a detailed manner
the conduct of systematic reviews, for which other guides are
available [13,14,15,16].
We developed the PRISMA Statement and this explanatory
document to help authors report a wide array of systematic
reviews to assess the benefits and harms of a health care
intervention. We consider most of the checklist items relevant
when reporting systematic reviews of non-randomized studies
assessing the benefits and harms of interventions. However, we
recognize that authors who address questions relating to
etiology, diagnosis, or prognosis, for example, and who review
epidemiological or diagnostic accuracy studies may need to
modify or incorporate additional items for their systematic
reviews.
How To Use This Paper
We modeled this Explanation and Elaboration document after
those prepared for other reporting guidelines [17,18,19]. To
maximize the benefit of this document, we encourage people to
read it in conjunction with the PRISMA Statement [11].
We present each checklist item and follow it with a published
exemplar of good reporting for that item. (We edited some
examples by removing citations or Web addresses, or by spelling
out abbreviations.) We then explain the pertinent issue, the
rationale for including the item, and relevant evidence from the
literature, whenever possible. No systematic search was carried out
to identify exemplars and evidence. We also include seven Boxes
that provide a more comprehensive explanation of certain
thematic aspects of the methodology and conduct of systematic
reviews.
Although we focus on a minimal list of items to consider when
reporting a systematic review, we indicate places where additional
information is desirable to improve transparency of the review
process. We present the items numerically from 1 to 27; however,
authors need not address items in this particular order in their
reports. Rather, what is important is that the information for each
item is given somewhere within the report.
The PRISMA Checklist
TITLE and ABSTRACT
Item 1: TITLE. Identify the report as a systematic review,
meta-analysis, or both.
Examples. ‘‘Recurrence rates of video-assisted thoraco-
scopic versus open surgery in the prevention of recurrent
pneumothoraces: a systematic review of randomised and
non-randomised trials’’ [20]
Figure 1. Flow of information through the different phases of a systematic review.
doi:10.1371/journal.pmed.1000100.g001
PLoS Medicine | www.plosmedicine.org 4 July 2009 | Volume 6 | Issue 7 | e1000100
‘‘Mortality in randomized trials of antioxidant supplements
for primary and secondary prevention: systematic review
and meta-analysis’’ [21]
Explanation. Authors should identify their report as a
systematic review or meta-analysis. Terms such as ‘‘review’’ or
‘‘overview’’ do not describe for readers whether the review was
systematic or whether a meta-analysis was performed. A recent
survey found that 50% of 300 authors did not mention the terms
‘‘systematic review’’ or ‘‘meta-analysis’’ in the title or abstract of
their systematic review [3]. Although sensitive search strategies
have been developed to identify systematic reviews [22], inclusion
of the terms systematic review or meta-analysis in the title may
improve indexing and identification.
We advise authors to use informative titles that make key
information easily accessible to readers. Ideally, a title reflecting the
PICOS approach (participants, interventions, comparators, out-
comes, and study design) (seeItem 11 and Box 2) may help readers as
it provides key information about the scope of the review. Specifying
the design(s) of the studies included, as shown in the examples, may
also help some readers and those searching databases.
Some journals recommend ‘‘indicative titles’’ that indicate the
topic matter of the review, while others require declarative titles
that give the review’s main conclusion. Busy practitioners may
prefer to see the conclusion of the review in the title, but
declarative titles can oversimplify or exaggerate findings. Thus,
many journals and methodologists prefer indicative titles as used in
the examples above.
Item 2: STRUCTURED SUMMARY. Provide a structured
summary including, as applicable: background; objectives; data
sources; study eligibility criteria, participants, and interventions;
study appraisal and synthesis methods; results; limitations;
conclusions and implications of key findings; funding for the
systematic review; and systematic review registration number.
Example. ‘‘Context: The role and dose of oral vitamin D
supplementation in nonvertebral fracture prevention have
not been well established.
Objective: To estimate the effectiveness of vitamin D
supplementation in preventing hip and nonvertebral frac-
tures in older persons.
Data Sources: A systematic review of English and non-English
articles using MEDLINE and the Cochrane Controlled
Trials Register (1960–2005), and EMBASE (1991–2005).
Additional studies were identified by contacting clinical
experts and searching bibliographies and abstracts presented
at the American Society for Bone and Mineral Research
(1995–2004). Search terms included randomized controlled
trial (RCT), controlled clinical trial, random allocation,
double-blind method, cholecalciferol, ergocalciferol, 25-
hydroxyvitamin D, fractures, humans, elderly, falls, and
bone density.
Study Selection: Only double-blind RCTs of oral vitamin D
supplementation (cholecalciferol, ergocalciferol) with or
without calcium supplementation vs calcium supplementa-
tion or placebo in older persons (.60 years) that examined
hip or nonvertebral fractures were included.
Data Extraction: Independent extraction of articles by 2
authors using predefined data fields, including study quality
indicators.
Data Synthesis: All pooled analyses were based on random-
effects models. Five RCTs for hip fracture (n = 9294) and 7
Box 2. Helping To Develop the Research
Question(s): The PICOS Approach
Formulating relevant and precise questions that can be
answered in a systematic review can be complex and time
consuming. A structured approach for framing questions
that uses five components may help facilitate the process.
This approach is commonly known by the acronym ‘‘PICOS’’
where each letter refers to a component: the patient
population or the disease being addressed (P), the
interventions or exposure (I), the comparator group (C),
the outcome or endpoint (O), and the study design chosen
(S) [186]. Issues relating to PICOS impact several PRISMA
items (i.e., Items 6, 8, 9, 10, 11, and 18).
Providing information about the population requires a
precise definition of a group of participants (often patients),
such as men over the age of 65 years, their defining
characteristics of interest (often disease), and possibly the
setting of care considered, such as an acute care hospital.
The interventions (exposures) under consideration in
the systematic review need to be transparently reported.
For example, if the reviewers answer a question regarding
the association between a woman’s prenatal exposure to
folic acid and subsequent offspring’s neural tube defects,
reporting the dose, frequency, and duration of folic acid
used in different studies is likely to be important for
readers to interpret the review’s results and conclusions.
Other interventions (exposures) might include diagnostic,
preventative, or therapeutic treatments, arrangements of
specific processes of care, lifestyle changes, psychosocial
or educational interventions, or risk factors.
Clearly reporting the comparator (control) group
intervention(s), such as usual care, drug, or placebo, is
essential for readers to fully understand the selection criteria
of primary studies included in systematic reviews, and
might be a source of heterogeneity investigators have to
deal with. Comparators are often very poorly described.
Clearly reporting what the intervention is compared with is
very important and may sometimes have implications for
the inclusion of studies in a review—many reviews compare
with ‘‘standard care,’’ which is otherwise undefined; this
should be properly addressed by authors.
The outcomes of theintervention being assessed, such as
mortality, morbidity, symptoms, or quality of life improve-
ments, should be clearly specified as they are required to
interpret the validity and generalizability of the systematic
review’s results.
Finally, the type of study design(s) included in the
review should be reported. Some reviews only include
reports of randomized trials whereas others have broader
design criteria and include randomized trials and certain
types of observational studies. Still other reviews, such as
those specifically answering questions related to harms,
may include a wide variety of designs ranging from cohort
studies to case reports. Whatever study designs are
included in the review, these should be reported.
Independently from how difficult it is to identify the
components of the research question, the important point is
that a structured approach is preferable, and this extends
beyond systematic reviews of effectiveness. Ideally the
PICOS criteria should be formulated a priori, in the
systematic review’s protocol, although some revisions might
be required due to the iterative nature of the review process.
Authors are encouraged to report their PICOS criteria and
whether any modifications were made during the review
process. A useful example in this realm is the Appendix of
the ‘‘Systematic Reviews of Water Fluoridation’’ undertaken
by the Centre for Reviews and Dissemination [187].
PLoS Medicine | www.plosmedicine.org 5 July 2009 | Volume 6 | Issue 7 | e1000100
RCTs for nonvertebral fracture risk (n = 9820) met our
inclusion criteria. All trials used cholecalciferol. Heteroge-
neity among studies for both hip and nonvertebral fracture
prevention was observed, which disappeared after pooling
RCTs with low-dose (400 IU/d) and higher-dose vitamin D
(700–800 IU/d), separately. A vitamin D dose of 700 to
800 IU/d reduced the relative risk (RR) of hip fracture by
26% (3 RCTs with 5572 persons; pooled RR, 0.74; 95%
confidence interval [CI], 0.61–0.88) and any nonvertebral
fracture by 23% (5 RCTs with 6098 persons; pooled RR,
0.77; 95% CI, 0.68–0.87) vs calcium or placebo. No
significant benefit was observed for RCTs with 400 IU/d
vitamin D (2 RCTs with 3722 persons; pooled RR for hip
fracture, 1.15; 95% CI, 0.88–1.50; and pooled RR for any
nonvertebral fracture, 1.03; 95% CI, 0.86–1.24).
Conclusions: Oral vitamin D supplementation between 700 to
800 IU/d appears to reduce the risk of hip and any
nonvertebral fractures in ambulatory or institutionalized
elderly persons. An oral vitamin D dose of 400 IU/d is not
sufficient for fracture prevention.’’ [23]
Explanation. Abstracts provide key information that enables
readers to understand the scope, processes, and findings of a
review and to decide whether to read the full report. The abstract
may be all that is readily available to a reader, for example, in a
bibliographic database. The abstract should present a balanced
and realistic assessment of the review’s findings that mirrors, albeit
briefly, the main text of the report.
We agree with others that the quality of reporting in abstracts
presented at conferences and in journal publications needs
improvement [24,25]. While we do not uniformly favor a specific
format over another, we generally recommend structured abstracts.
Structured abstracts provide readers with a series of headings
pertaining to the purpose, conduct, findings, and conclusions of the
systematic review being reported [26,27]. They give readers more
complete information and facilitate finding information more easily
than unstructured abstracts [28,29,30,31,32].
A highly structured abstract of a systematic review could include
the following headings: Context (or Background); Objective (or
Purpose); Data Sources; Study Selection (or Eligibility Criteria);
Study Appraisal and Synthesis Methods (or Data Extraction and
Data Synthesis); Results; Limitations; and Conclusions (or
Implications). Alternatively, a simpler structure could cover but
collapse some of the above headings (e.g., label Study Selection
and Study Appraisal as Review Methods) or omit some headings
such as Background and Limitations.
In the highly structured abstract mentioned above, authors use
the Background heading to set the context for readers and explain
the importance of the review question. Under the Objectives
heading, they ideally use elements of PICOS (see Box 2) to state
the primary objective of the review. Under a Data Sources
heading, they summarize sources that were searched, any
language or publication type restrictions, and the start and end
dates of searches. Study Selection statements then ideally describe
who selected studies using what inclusion criteria. Data Extraction
Methods statements describe appraisal methods during data
abstraction and the methods used to integrate or summarize
the data. The Data Synthesis section is where the main results of
the review are reported. If the review includes meta-analyses,
authors should provide numerical results with confidence
intervals for the most important outcomes. Ideally, they should
specify the amount of evidence in these analyses (numbers of
studies and numbers of participants). Under a Limitations
heading, authors might describe the most important weaknesses
of included studies as well as limitations of the review process.
Then authors should provide clear and balanced Conclusions that
are closely linked to the objective and findings of the review.
Additionally, it would be helpful if authors included some
information about funding for the review. Finally, although
protocol registration for systematic reviews is still not common
practice, if authors have registered their review or received a
registration number, we recommend providing the registration
information at the end of the abstract.
Taking all the above considerations into account, the intrinsic
tension between the goal of completeness of the abstract and its
keeping into the space limit often set by journal editors is
recognized as a major challenge.
INTRODUCTION
Item 3: RATIONALE. Describe the rationale for the review
in the context of what is already known.
Example. ‘‘Reversing the trend of increasing weight for
height in children has proven difficult. It is widely accepted
that increasing energy expenditure and reducing energy
intake form the theoretical basis for management. There-
fore, interventions aiming to increase physical activity and
improve diet are the foundation of efforts to prevent and
treat childhood obesity. Such lifestyle interventions have
been supported by recent systematic reviews, as well as by
the Canadian Paediatric Society, the Royal College of
Paediatrics and Child Health, and the American Academy
of Pediatrics. However, these interventions are fraught with
poor adherence. Thus, school-based interventions are
theoretically appealing because adherence with interven-
tions can be improved. Consequently, many local govern-
ments have enacted or are considering policies that mandate
increased physical activity in schools, although the effect of
such interventions on body composition has not been
assessed.’’ [33]
Explanation. Readers need to understand the rationale
behind the study and what the systematic review may add to
what is already known. Authors should tell readers whether their
report is a new systematic review or an update of an existing one.
If the review is an update, authors should state reasons for the
update, including what has been added to the evidence base since
the previous version of the review.
An ideal background or introduction that sets context for
readers might include the following. First, authors might define the
importance of the review question from different perspectives (e.g.,
public health, individual patient, or health policy). Second, authors
might briefly mention the current state of knowledge and its
limitations. As in the above example, information about the effects
of several different interventions may be available that helps
readers understand why potential relative benefits or harms of
particular interventions need review. Third, authors might whet
readers’ appetites by clearly stating what the review aims to add.
They also could discuss the extent to which the limitations of the
existing evidence base may be overcome by the review.
Item 4: OBJECTIVES. Provide an explicit statement of
questions being addressed with reference to participants,
interventions, comparisons, outcomes, and study design
(PICOS).
PLoS Medicine | www.plosmedicine.org 6 July 2009 | Volume 6 | Issue 7 | e1000100
Example. ‘‘To examine whether topical or intraluminal
antibiotics reduce catheter-related bloodstream infection, we
reviewed randomized, controlled trials that assessed the
efficacy of these antibiotics for primary prophylaxis against
catheter-related bloodstream infection and mortality com-
pared with no antibiotic therapy in adults undergoing
hemodialysis.’’ [34]
Explanation. The questions being addressed, and the
rationale for them, are one of the most critical parts of a
systematic review. They should be stated precisely and explicitly
so that readers can understand quickly the review’s scope and the
potential applicability of the review to their interests [35].
Framing questions so that they include the following five
‘‘PICOS’’ components may improve the explicitness of review
questions: (1) the patient population or disease being addressed
(P), (2) the interventions or exposure of interest (I), (3) the
comparators (C), (4) the main outcome or endpoint of interest
(O), and (5) the study designs chosen (S). For more detail
regarding PICOS, see Box 2.
Good review questions may be narrowly focused or broad,
depending on the overall objectives of the review. Sometimes
broad questions might increase the applicability of the results and
facilitate detection of bias, exploratory analyses, and sensitivity
analyses [35,36]. Whether narrowly focused or broad, precisely
stated review objectives are critical as they help define other
components of the review process such as the eligibility criteria
(Item 6) and the search for relevant literature (Items 7 and 8).
METHODS
Item 5: PROTOCOL AND REGISTRATION. Indicate if a
review protocol exists, if and where it can be accessed (e.g., Web
address) and, if available, provide registration information
including the registration number.
Example. ‘‘Methods of the analysis and inclusion criteria
were specified in advance and documented in a protocol.’’ [37]
Explanation. A protocol is important because it pre-specifies
the objectives and methods of the systematic review. For instance,
a protocol specifies outcomes of primary interest, how reviewers
will extract information about those outcomes, and methods that
reviewers might use to quantitatively summarize the outcome data
(see Item 13). Having a protocol can help restrict the likelihood of
biased post hoc decisions in review methods, such as selective
outcome reporting. Several sources provide guidance about
elements to include in the protocol for a systematic review
[16,38,39]. For meta-analyses of individual patient-level data, we
advise authors to describe whether a protocol was explicitly
designed and whether, when, and how participating collaborators
endorsed it [40,41].
Authors may modify protocols during the research, and readers
should not automatically consider such modifications inappropri-
ate. For example, legitimate modifications may extend the period
of searches to include older or newer studies, broaden eligibility
criteria that proved too narrow, or add analyses if the primary
analyses suggest that additional ones are warranted. Authors
should, however, describe the modifications and explain their
rationale.
Although worthwhile protocol amendments are common, one
must consider the effects that protocol modifications may have on
the results of a systematic review, especially if the primary outcome
is changed. Bias from selective outcome reporting in randomized
trials has been well documented [42,43]. An examination of 47
Cochrane reviews revealed indirect evidence for possible selective
reporting bias for systematic reviews. Almost all (n= 43) contained
a major change, such as the addition or deletion of outcomes,
between the protocol and the full publication [44]. Whether (or to
what extent) the changes reflected bias, however, was not clear.
For example, it has been rather common not to describe outcomes
that were not presented in any of the included studies.
Registration of a systematic review, typically with a protocol and
registration number, is not yet common, but some opportunities
exist [45,46]. Registration may possibly reduce the risk of multiple
reviews addressing the same question [45,46,47,48], reduce
publication bias, and provide greater transparency when updating
systematic reviews. Of note, a survey of systematic reviews indexed
in MEDLINE in November 2004 found that reports of protocol
use had increased to about 46% [3] from 8% noted in previous
surveys [49]. The improvement was due mostly to Cochrane
reviews, which, by requirement, have a published protocol [3].
Item 6: ELIGIBILITY CRITERIA. Specify study charac-
teristics (e.g., PICOS, length of follow-up) and report
characteristics (e.g., years considered, language, publication
status) used as criteria for eligibility, giving rationale.
Examples. Types of studies: ‘‘Randomised clinical trials
studying the administration of hepatitis B vaccine to CRF
[chronic renal failure] patients, with or without dialysis. No
language, publication date, or publication status restrictions
were imposed…’’
Types of participants: ‘‘Participants of any age with CRF or
receiving dialysis (haemodialysis or peritoneal dialysis) were
considered. CRF was defined as serum creatinine greater
than 200 mmol/L for a period of more than six months or
individuals receiving dialysis (haemodialysis or peritoneal
dialysis)…Renal transplant patients were excluded from this
review as these individuals are immunosuppressed and are
receiving immunosuppressant agents to prevent rejection of
their transplanted organs, and they have essentially normal
renal function…’’
Types of intervention: ‘‘Trials comparing the beneficial and
harmful effects of hepatitis B vaccines with adjuvant or
cytokine co-interventions [and] trials comparing the bene-
ficial and harmful effects of immunoglobulin prophylaxis.
This review was limited to studies looking at active
immunization. Hepatitis B vaccines (plasma or recombinant
(yeast) derived) of all types, dose, and regimens versus
placebo, control vaccine, or no vaccine…’’
Types of outcome measures: ‘‘Primary outcome measures:
Seroconversion, ie, proportion of patients with adequate
anti-HBs response (.10 IU/L or Sample Ratio Units).
Hepatitis B infections (as measured by hepatitis B core
antigen (HBcAg) positivity or persistent HBsAg positivity),
both acute and chronic. Acute (primary) HBV [hepatitis B
virus] infections were defined as seroconversion to HBsAg
positivity or development of IgM anti-HBc. Chronic HBV
infections were defined as the persistence of HBsAg for more
than six months or HBsAg positivity and liver biopsy
compatible with a diagnosis or chronic hepatitis B.
Secondary outcome measures: Adverse events of hepatitis
B vaccinations…[and]…mortality.’’ [50]
Explanation. Knowledge of the eligibility criteria is essential
in appraising the validity, applicability, and comprehensiveness of
PLoS Medicine | www.plosmedicine.org 7 July 2009 | Volume 6 | Issue 7 | e1000100
a review. Thus, authors should unambiguously specify eligibility
criteria used in the review. Carefully defined eligibility criteria
inform various steps of the review methodology. They influence
the development of the search strategy and serve to ensure that
studies are selected in a systematic and unbiased manner.
A study may be described in multiple reports, and one report may
describe multiple studies. Therefore, we separate eligibility criteria
into the following two components: study characteristics and report
characteristics. Both need to be reported. Study eligibility criteria
are likely to include the populations, interventions, comparators,
outcomes, and study designs of interest (PICOS; see Box 2), as well
as other study-specific elements, such as specifying a minimum
length of follow-up. Authors should state whether studies will be
excluded because they do not include (or report) specific outcomes
to help readers ascertain whether the systematic review may be
biased as a consequence of selective reporting [42,43].
Report eligibility criteria are likely to include language of
publication, publication status (e.g., inclusion of unpublished
material and abstracts), and year of publication. Inclusion or not of
non-English language literature [51,52,53,54,55], unpublished
data, or older data can influence the effect estimates in meta-
analyses [56,57,58,59]. Caution may need to be exercised in
including all identified studies due to potential differences in the
risk of bias such as, for example, selective reporting in abstracts
[60,61,62].
Item 7: INFORMATION SOURCES. Describe all
information sources in the search (e.g., databases with dates of
coverage, contact with study authors to identify additional studies)
and date last searched.
Example. ‘‘Studies were identified by searching electronic
databases, scanning reference lists of articles and consulta-
tion with experts in the field and drug companies…No limits
were applied for language and foreign papers were
translated. This search was applied to Medline (1966–
Present), CancerLit (1975–Present), and adapted for Embase
(1980–Present), Science Citation Index Expanded (1981–
Present) and Pre-Medline electronic databases. Cochrane
and DARE (Database of Abstracts of Reviews of Effective-
ness) databases were reviewed…The last search was run on
19 June 2001. In addition, we handsearched contents pages
of Journal of Clinical Oncology 2001, European Journal of
Cancer 2001 and Bone 2001, together with abstracts printed
in these journals 1999–2001. A limited update literature
search was performed from 19 June 2001 to 31 December
2003.’’ [63]
Explanation. The National Library of Medicine’s
MEDLINE database is one of the most comprehensive sources
of health care information in the world. Like any database,
however, its coverage is not complete and varies according to the
field. Retrieval from any single database, even by an experienced
searcher, may be imperfect, which is why detailed reporting is
important within the systematic review.
At a minimum, for each database searched, authors should
report the database, platform, or provider (e.g., Ovid, Dialog,
PubMed) and the start and end dates for the search of each
database. This information lets readers assess the currency of the
review, which is important because the publication time-lag
outdates the results of some reviews [64]. This information should
also make updating more efficient [65]. Authors should also report
who developed and conducted the search [66].
In addition to searching databases, authors should report the
use of supplementary approaches to identify studies, such as hand
searching of journals, checking reference lists, searching trials
registries or regulatory agency Web sites [67], contacting
manufacturers, or contacting authors. Authors should also report
if they attempted to acquire any missing information (e.g., on study
methods or results) from investigators or sponsors; it is useful to
describe briefly who was contacted and what unpublished
information was obtained.
Item 8: SEARCH. Present the full electronic search strategy
for at least one major database, including any limits used, such that
it could be repeated.
Examples. In text: ‘‘We used the following search terms to
search all trials registers and databases: immunoglobulin*;
IVIG; sepsis; septic shock; septicaemia; and septicemia…’’
[68]
In appendix: ‘‘Search strategy: MEDLINE (OVID)
01. immunoglobulins/
02. immunoglobulin$.tw.
03. ivig.tw.
04. 1 or 2 or 3
05. sepsis/
06. sepsis.tw.
07. septic shock/
08. septic shock.tw.
09. septicemia/
10. septicaemia.tw.
11. septicemia.tw.
12. 5 or 6 or 7 or 8 or 9 or 10 or 11
13. 4 and 12
14. randomized controlled trials/
15. randomized-controlled-trial.pt.
16. controlled-clinical-trial.pt.
17. random allocation/
18. double-blind method/
19. single-blind method/
20. 14 or 15 or 16 or 17 or 18 or 19
21. exp clinical trials/
22. clinical-trial.pt.
23. (clin$ adj trial$).ti,ab.
24. ((singl$ or doubl$ or trebl$ or tripl$) adj (blind$)).ti,ab.
25. placebos/
26. placebo$.ti,ab.
27. random$.ti,ab.
28. 21 or 22 or 23 or 24 or 25 or 26 or 27
29. research design/
30. comparative study/
31. exp evaluation studies/
32. follow-up studies/
33. prospective studies/
34. (control$ or prospective$ or volunteer$).ti,ab.
35. 30 or 31 or 32 or 33 or 34
36. 20 or 28 or 29 or 35
37. 13 and 36’’ [68]
Explanation. The search strategy is an essential part of the
report of any systematic review. Searches may be complicated and
iterative, particularly when reviewers search unfamiliar databases
or their review is addressing a broad or new topic. Perusing the
search strategy allows interested readers to assess the
PLoS Medicine | www.plosmedicine.org 8 July 2009 | Volume 6 | Issue 7 | e1000100
comprehensiveness and completeness of the search, and to
replicate it. Thus, we advise authors to report their full
electronic search strategy for at least one major database. As an
alternative to presenting search strategies for all databases, authors
could indicate how the search took into account other databases
searched, as index terms vary across databases. If different
searches are used for different parts of a wider question (e.g.,
questions relating to benefits and questions relating to harms), we
recommend authors provide at least one example of a strategy for
each part of the objective [69]. We also encourage authors to state
whether search strategies were peer reviewed as part of the
systematic review process [70].
We realize that journal restrictions vary and that having the
search strategy in the text of the report is not always feasible. We
strongly encourage all journals, however, to find ways, such as a
‘‘Web extra,’’ appendix, or electronic link to an archive, to make
search strategies accessible to readers. We also advise all authors to
archive their searches so that (1) others may access and review
them (e.g., replicate them or understand why their review of a
similar topic did not identify the same reports), and (2) future
updates of their review are facilitated.
Several sources provide guidance on developing search
strategies [71,72,73]. Most searches have constraints, for example
relating to limited time or financial resources, inaccessible or
inadequately indexed reports and databases, unavailability of
experts with particular language or database searching skills, or
review questions for which pertinent evidence is not easy to find.
Authors should be straightforward in describing their search
constraints. Apart from the keywords used to identify or exclude
records, they should report any additional limitations relevant to
the search, such as language and date restrictions (see also
eligibility criteria, Item 6) [51].
Item 9: STUDY SELECTION. State the process for selecting
studies (i.e., for screening, for determining eligibility, for inclusion
in the systematic review, and, if applicable, for inclusion in the
meta-analysis).
Example. ‘‘Eligibility assessment…[was] performed inde-
pendently in an unblinded standardized manner by 2
reviewers…Disagreements between reviewers were resolved
by consensus.’’ [74]
Explanation. There is no standard process for selecting
studies to include in a systematic review. Authors usually start with
a large number of identified records from their search and
sequentially exclude records according to eligibility criteria. We
advise authors to report how they screened the retrieved records
(typically a title and abstract), how often it was necessary to review
the full text publication, and if any types of record (e.g., letters to
the editor) were excluded. We also advise using the PRISMA flow
diagram to summarize study selection processes (see Item 17; Box
3).
Efforts to enhance objectivity and avoid mistakes in study
selection are important. Thus authors should report whether each
stage was carried out by one or several people, who these people
were, and, whenever multiple independent investigators per-
formed the selection, what the process was for resolving
disagreements. The use of at least two investigators may reduce
the possibility of rejecting relevant reports [75]. The benefit may
be greatest for topics where selection or rejection of an article
requires difficult judgments [76]. For these topics, authors should
ideally tell readers the level of inter-rater agreement, how
commonly arbitration about selection was required, and what
efforts were made to resolve disagreements (e.g., by contact with
the authors of the original studies).
Item 10: DATA COLLECTION PROCESS. Describe the
method of data extraction from reports (e.g., piloted forms,
independently by two reviewers) and any processes for obtaining
and confirming data from investigators.
Example. ‘‘We developed a data extraction sheet (based on
the Cochrane Consumers and Communication Review
Group’s data extraction template), pilot-tested it on ten
randomly-selected included studies, and refined it accord-
ingly. One review author extracted the following data from
included studies and the second author checked the
extracted data…Disagreements were resolved by discussion
between the two review authors; if no agreement could be
reached, it was planned a third author would decide. We
contacted five authors for further information. All responded
and one provided numerical data that had only been
presented graphically in the published paper.’’ [77]
Explanation. Reviewers extract information from each
included study so that they can critique, present, and summarize
evidence in a systematic review. They might also contact authors
of included studies for information that has not been, or is
unclearly, reported. In meta-analysis of individual patient data,
this phase involves collection and scrutiny of detailed raw
databases. The authors should describe these methods, including
any steps taken to reduce bias and mistakes during data collection
and data extraction [78] (Box 3).
Some systematic reviewers use a data extraction form that could
be reported as an appendix or ‘‘Web extra’’ to their report. These
forms could show the reader what information reviewers sought
(see Item 11) and how they extracted it. Authors could tell readers
if the form was piloted. Regardless, we advise authors to tell
readers who extracted what data, whether any extractions were
completed in duplicate, and, if so, whether duplicate abstraction
was done independently and how disagreements were resolved.
Published reports of the included studies may not provide all the
information required for the review. Reviewers should describe
any actions they took to seek additional information from the
original researchers (see Item 7). The description might include
how they attempted to contact researchers, what they asked for,
and their success in obtaining the necessary information. Authors
should also tell readers when individual patient data were sought
from the original researchers [41] (see Item 11) and indicate the
studies for which such data were used in the analyses. The
reviewers ideally should also state whether they confirmed the
accuracy of the information included in their review with the
original researchers, for example, by sending them a copy of the
draft review [79].
Some studies are published more than once. Duplicate
publications may be difficult to ascertain, and their inclusion
may introduce bias [80,81]. We advise authors to describe any
steps they used to avoid double counting and piece together data
from multiple reports of the same study (e.g., juxtaposing author
names, treatment comparisons, sample sizes, or outcomes). We
also advise authors to indicate whether all reports on a study were
considered, as inconsistencies may reveal important limitations.
For example, a review of multiple publications of drug trials
showed that reported study characteristics may differ from report
to report, including the description of the design, number of
patients analyzed, chosen significance level, and outcomes [82].
PLoS Medicine | www.plosmedicine.org 9 July 2009 | Volume 6 | Issue 7 | e1000100
Authors ideally should present any algorithm that they used to
select data from overlapping reports and any efforts they used to
solve logical inconsistencies across reports.
Item 11: DATA ITEMS. List and define all variables for
which data were sought (e.g., PICOS, funding sources), and any
assumptions and simplifications made.
Examples. ‘‘Information was extracted from each included
trial on: (1) characteristics of trial participants (including age,
stage and severity of disease, and method of diagnosis), and
Box 3. Identification of Study Reports and
Data Extraction
Comprehensive searches usually result in a large number
of identified records, a much smaller number of studies
included in the systematic review, and even fewer of these
studies included in any meta-analyses. Reports of system-
atic reviews often provide little detail as to the methods
used by the review team in this process. Readers are often
left with what can be described as the ‘‘X-files’’ phenom-
enon, as it is unclear what occurs between the initial set of
identified records and those finally included in the review.
Sometimes, review authors simply report the number of
included studies; more often they report the initial number
of identified records and the number of included studies.
Rarely, although this is optimal for readers, do review
authors report the number of identified records, the
smaller number of potentially relevant studies, and the
even smaller number of included studies, by outcome.
Review authors also need to differentiate between the
number of reports and studies. Often there will not be a
1:1 ratio of reports to studies and this information needs to
be described in the systematic review report.
Ideally, the identification of study reports should be
reported as text in combination with use of the PRISMA
flow diagram. While we recommend use of the flow
diagram, a small number of reviews might be particularly
simple and can be sufficiently described with a few brief
sentences of text. More generally, review authors will need
to report the process used for each step: screening the
identified records; examining the full text of potentially
relevant studies (and reporting the number that could not
be obtained); and applying eligibility criteria to select the
included studies.
Such descriptions should also detail how potentially
eligible records were promoted to the next stage of the
review (e.g., full text screening) and to the final stage of
this process, the included studies. Often review teams have
three response options for excluding records or promoting
them to the next stage of the winnowing process: ‘‘yes,’’
‘‘no,’’ and ‘‘maybe.’’
Similarly, some detail should be reported on who
participated and how such processes were completed. For
example, a single person may screen the identified records
while a second person independently examines a small
sample of them. The entire winnowing process is one of
‘‘good book keeping’’ whereby interested readers should
be able to work backwards from the included studies to
come up with the same numbers of identified records.
There is often a paucity of information describing the
data extraction processes in reports of systematic reviews.
Authors may simply report that ‘‘relevant’’ data were
extracted from each included study with little information
about the processes used for data extraction. It may be
useful for readers to know whether a systematic review’s
authors developed, a priori or not, a data extraction form,
whether multiple forms were used, the number of
questions, whether the form was pilot tested, and who
completed the extraction. For example, it is important for
readers to know whether one or more people extracted
data, and if so, whether this was completed independent-
ly, whether ‘‘consensus’’ data were used in the analyses,
and if the review team completed an informal training
exercise or a more formal reliability exercise.
Box 4. Study Quality and Risk of Bias
In this paper, and elsewhere [11], we sought to use a new
term for many readers, namely, risk of bias, for evaluating
each included study in a systematic review. Previous
papers [89,188] tended to use the term ‘‘quality’’. When
carrying out a systematic review we believe it is important
to distinguish between quality and risk of bias and to focus
on evaluating and reporting the latter. Quality is often the
best the authors have been able to do. For example,
authors may report the results of surgical trials in which
blinding of the outcome assessors was not part of the
trial’s conduct. Even though this may have been the best
methodology the researchers were able to do, there are
still theoretical grounds for believing that the study was
susceptible to (risk of) bias.
Assessing the risk of bias should be part of the conduct
and reporting of any systematic review. In all situations, we
encourage systematic reviewers to think ahead carefully
about what risks of bias (methodological and clinical) may
have a bearing on the results of their systematic reviews.
For systematic reviewers, understanding the risk of bias
on the results of studies is often difficult, because the
report is only a surrogate of the actual conduct of the
study. There is some suggestion [189,190] that the report
may not be a reasonable facsimile of the study, although
this view is not shared by all [88,191]. There are three main
ways to assess risk of bias: individual components,
checklists, and scales. There are a great many scales
available [192], although we caution their use based on
theoretical grounds [193] and emerging empirical evi-
dence [194]. Checklists are less frequently used and
potentially run the same problems as scales. We advocate
using a component approach and one that is based on
domains for which there is good empirical evidence and
perhaps strong clinical grounds. The new Cochrane risk of
bias tool [11] is one such component approach.
The Cochrane risk of bias tool consists of five items for
which there is empirical evidence for their biasing
influence on the estimates of an intervention’s effective-
ness in randomized trials (sequence generation, allocation
concealment, blinding, incomplete outcome data, and
selective outcome reporting) and a catch-all item called
‘‘other sources of bias’’ [11]. There is also some consensus
that these items can be applied for evaluation of studies
across very diverse clinical areas [93]. Other risk of bias
items may be topic or even study specific, i.e., they may
stem from some peculiarity of the research topic or some
special feature of the design of a specific study. These
peculiarities need to be investigated on a case-by-case
basis, based on clinical and methodological acumen, and
there can be no general recipe. In all situations, systematic
reviewers need to think ahead carefully about what
aspects of study quality may have a bearing on the results.
PLoS Medicine | www.plosmedicine.org 10 July 2009 | Volume 6 | Issue 7 | e1000100
the trial’s inclusion and exclusion criteria; (2) type of
intervention (including type, dose, duration and frequency
of the NSAID [non-steroidal anti-inflammatory drug];
versus placebo or versus the type, dose, duration and
frequency of another NSAID; or versus another pain
management drug; or versus no treatment); (3) type of
outcome measure (including the level of pain reduction,
improvement in quality of life score (using a validated scale),
effect on daily activities, absence from work or school, length
of follow up, unintended effects of treatment, number of
women requiring more invasive treatment).’’ [83]
Explanation. It is important for readers to know what
information review authors sought, even if some of this
information was not available [84]. If the review is limited to
reporting only those variables that were obtained, rather than
those that were deemed important but could not be obtained, bias
might be introduced and the reader might be misled. It is therefore
helpful if authors can refer readers to the protocol (see Item 5), and
archive their extraction forms (see Item 10), including definitions
of variables. The published systematic review should include a
description of the processes used with, if relevant, specification of
how readers can get access to additional materials.
We encourage authors to report whether some variables were
added after the review started. Such variables might include those
found in the studies that the reviewers identified (e.g., important
outcome measures that the reviewers initially overlooked). Authors
should describe the reasons for adding any variables to those
already pre-specified in the protocol so that readers can
understand the review process.
We advise authors to report any assumptions they made about
missing or unclear information and to explain those processes. For
example, in studies of women aged 50 or older it is reasonable to
assume that none were pregnant, even if this is not reported.
Likewise, review authors might make assumptions about the route
of administration of drugs assessed. However, special care should
be taken in making assumptions about qualitative information. For
example, the upper age limit for ‘‘children’’ can vary from 15 years
to 21 years, ‘‘intense’’ physiotherapy might mean very different
things to different researchers at different times and for different
patients, and the volume of blood associated with ‘‘heavy’’ blood
loss might vary widely depending on the setting.
Item 12: RISK OF BIAS IN INDIVIDUAL STUDIES.
Describe methods used for assessing risk of bias in individual
studies (including specification of whether this was done at the
study or outcome level, or both), and how this information is to be
used in any data synthesis.
Example. ‘‘To ascertain the validity of eligible randomized
trials, pairs of reviewers working independently and with
adequate reliability determined the adequacy of randomi-
zation and concealment of allocation, blinding of patients,
health care providers, data collectors, and outcome
assessors; and extent of loss to follow-up (i.e. proportion of
patients in whom the investigators were not able to ascertain
outcomes).’’ [85]
‘‘To explore variability in study results (heterogeneity) we
specified the following hypotheses before conducting the
analysis. We hypothesised that effect size may differ
according to the methodological quality of the studies.’’
[86]
Explanation. The likelihood that the treatment effect reported
in a systematic review approximates the truth depends on the validity
of the included studies, as certain methodological characteristics may
be associated with effect sizes [87,88]. For example, trials without
reported adequate allocation concealment exaggerate treatment
effects on average compared to those with adequate concealment
[88]. Therefore, it is important for authors to describe any methods
that they used to gauge the risk of bias in the included studies and how
that information was used [89]. Additionally, authors should provide
a rationale if no assessment of risk of bias was undertaken. The most
popular term to describe the issues relevant to this item is ‘‘quality,’’
but for the reasons that are elaborated in Box 4 we prefer to name this
item as ‘‘assessment of risk of bias.’
Many methods exist to assess the overall risk of bias in included
studies, including scales, checklists, and individual components
[90,91]. As discussed in Box 4, scales that numerically summarize
multiple components into a single number are misleading and
unhelpful [92,93]. Rather, authors should specify the methodolog-
ical components that they assessed. Common markers of validity for
randomized trials include the following: appropriate generation of
random allocation sequence [94]; concealment of the allocation
sequence [93]; blinding of participants, health care providers, data
collectors, and outcome adjudicators [95,96,97,98]; proportion of
patients lost to follow-up [99,100]; stopping of trials early for benefit
[101]; and whether the analysis followed the intention-to-treat
principle [100,102]. The ultimate decision regarding which
methodological features to evaluate requires consideration of the
strength of the empiric data, theoretical rationale, and the unique
circumstances of the included studies.
Authors should report how they assessed risk of bias; whether
it was in a blind manner; and if assessments were completed by
more than one person, and if so, whether they were completed
independently [103,104]. Similarly, we encourage authors to
report any calibration exercises among review team members
that were done. Finally, authors need to report how their
assessments of risk of bias are used subsequently in the data
synthesis (see Item 16). Despite the often difficult task of
assessing the risk of bias in included studies, authors are
sometimes silent on what they did with the resultant assessments
[89]. If authors exclude studies from the review or any
subsequent analyses on the basis of the risk of bias, they should
tell readers which studies they excluded and explain the reasons
for those exclusions (see Item 6). Authors should also describe
any planned sensitivity or subgroup analyses related to bias
assessments (see Item 16).
Item 13: SUMMARY MEASURES. State the principal
summary measures (e.g., risk ratio, difference in means).
Examples. ‘‘Relative risk of mortality reduction was the
primary measure of treatment effect.’’ [105]
‘‘The meta-analyses were performed by computing relative
risks (RRs) using random-effects model. Quantitative
analyses were performed on an intention-to-treat basis and
were confined to data derived from the period of follow-up.
RR and 95% confidence intervals for each side effect (and
all side effects) were calculated.’’ [106]
‘‘The primary outcome measure was the mean difference in
log
10
HIV-1 viral load comparing zinc supplementation to
placebo…’’ [107]
Explanation. When planning a systematic review, it is
generally desirable that authors pre-specify the outcomes of
PLoS Medicine | www.plosmedicine.org 11 July 2009 | Volume 6 | Issue 7 | e1000100
primary interest (see Item 5) as well as the intended summary effect
measure for each outcome. The chosen summary effect measure
may differ from that used in some of the included studies. If
possible the choice of effect measures should be explained, though
it is not always easy to judge in advance which measure is the most
appropriate.
For binary outcomes, the most common summary measures are
the risk ratio, odds ratio, and risk difference [108]. Relative effects
are more consistent across studies than absolute effects [109,110],
although absolute differences are important when interpreting
findings (see Item 24).
For continuous outcomes, the natural effect measure is the
difference in means [108]. Its use is appropriate when outcome
measurements in all studies are made on the same scale. The
standardized difference in means is used when the studies do not
yield directly comparable data. Usually this occurs when all studies
assess the same outcome but measure it in a variety of ways (e.g.,
different scales to measure depression).
For time-to-event outcomes, the hazard ratio is the most
common summary measure. Reviewers need the log hazard ratio
and its standard error for a study to be included in a meta-analysis
[111]. This information may not be given for all studies, but
methods are available for estimating the desired quantities from
other reported information [111]. Risk ratio and odds ratio (in
relation to events occurring by a fixed time) are not equivalent to
the hazard ratio, and median survival times are not a reliable basis
for meta-analysis [112]. If authors have used these measures they
should describe their methods in the report.
Item 14: PLANNED METHODS OF ANALYSIS. Describe
the methods of handling data and combining results of studies, if
done, including measures of consistency (e.g., I
2
) for each meta-
analysis.
Examples. ‘‘We tested for heterogeneity with the Breslow-
Day test, and used the method proposed by Higgins et al. to
measure inconsistency (the percentage of total variation
across studies due to heterogeneity) of effects across lipid-
lowering interventions. The advantages of this measure of
inconsistency (termed I
2
) are that it does not inherently
depend on the number of studies and is accompanied by an
uncertainty interval.’’ [113]
‘‘In very few instances, estimates of baseline mean or mean
QOL [Quality of life] responses were obtained without
corresponding estimates of variance (standard deviation
[SD] or standard error). In these instances, an SD was
imputed from the mean of the known SDs. In a number of
cases, the response data available were the mean and
variance in a pre study condition and after therapy. The
within-patient variance in these cases could not be
calculated directly and was approximated by assuming
independence.’’ [114]
Explanation. The data extracted from the studies in the
review may need some transformation (processing) before they are
suitable for analysis or for presentation in an evidence table.
Although such data handling may facilitate meta-analyses, it is
sometimes needed even when meta-analyses are not done. For
example, in trials with more than two intervention groups it may
be necessary to combine results for two or more groups (e.g.,
receiving similar but non-identical interventions), or it may be
desirable to include only a subset of the data to match the review’s
inclusion criteria. When several different scales (e.g., for
depression) are used across studies, the sign of some scores may
need to be reversed to ensure that all scales are aligned (e.g., so low
values represent good health on all scales). Standard deviations
may have to be reconstructed from other statistics such as p-values
and tstatistics [115,116], or occasionally they may be imputed
from the standard deviations observed in other studies [117].
Time-to-event data also usually need careful conversions to a
consistent format [111]. Authors should report details of any such
data processing.
Statistical combination of data from two or more separate
studies in a meta-analysis may be neither necessary nor desirable
(see Box 5 and Item 21). Regardless of the decision to combine
individual study results, authors should report how they planned to
evaluate between-study variability (heterogeneity or inconsistency)
(Box 6). The consistency of results across trials may influence the
decision of whether to combine trial results in a meta-analysis.
When meta-analysis is done, authors should specify the effect
measure (e.g., relative risk or mean difference) (see Item 13), the
statistical method (e.g., inverse variance), and whether a fixed- or
random-effects approach, or some other method (e.g., Bayesian)
was used (see Box 6). If possible, authors should explain the
reasons for those choices.
Item 15: RISK OF BIAS ACROSS STUDIES. Specify any
assessment of risk of bias that may affect the cumulative evidence
(e.g., publication bias, selective reporting within studies).
Examples. ‘‘For each trial we plotted the effect by the
inverse of its standard error. The symmetry of such ‘funnel
plots’ was assessed both visually, and formally with Egger’s
test, to see if the effect decreased with increasing sample
size.’’ [118]
‘‘We assessed the possibility of publication bias by evaluating
a funnel plot of the trial mean differences for asymmetry,
which can result from the non publication of small trials with
negative results…Because graphical evaluation can be
subjective, we also conducted an adjusted rank correlation
test and a regression asymmetry test as formal statistical tests
for publication bias…We acknowledge that other factors,
such as differences in trial quality or true study heteroge-
neity, could produce asymmetry in funnel plots.’’ [119]
Explanation. Reviewers should explore the possibility that
the available data are biased. They may examine results from the
available studies for clues that suggest there may be missing studies
(publication bias) or missing data from the included studies
(selective reporting bias) (see Box 7). Authors should report in
detail any methods used to investigate possible bias across studies.
It is difficult to assess whether within-study selective reporting is
present in a systematic review. If a protocol of an individual study is
available, the outcomes in the protocol and the published report can
be compared. Even in the absence of a protocol, outcomes listed in
the methods section of the published report can be compared with
those for which results are presented [120]. In only half of 196 trial
reports describing comparisons of two drugs in arthritis were all the
effect variables in the methods and results sections the same [82]. In
other cases, knowledge of the clinical area may suggest that it is
likely that the outcome was measured even if it was not reported.
For example, in a particular disease, if one of two linked outcomes is
reported but the other is not, then one should question whether the
latter has been selectively omitted [121,122].
Only 36% (76 of 212) of therapeutic systematic reviews
published in November 2004 reported that study publication
PLoS Medicine | www.plosmedicine.org 12 July 2009 | Volume 6 | Issue 7 | e1000100
bias was considered, and only a quarter of those intended to
carry out a formal assessment for that bias [3]. Of 60 meta-
analyses in 24 articles published in 2005 in which formal
assessments were reported, most were based on fewer than ten
studies; most displayed statistically significant heterogeneity; and
many reviewers misinterpreted the results of the tests employed
[123]. A review of trials of antidepressants found that meta-
analysis of only the published trials gave effect estimates 32%
larger on average than when all trials sent to the drug agency
were analyzed [67].
Item 16: ADDITIONAL ANALYSES. Describe methods of
additional analyses (e.g., sensitivity or subgroup analyses, meta-
regression), if done, indicating which were pre-specified.
Example. ‘‘Sensitivity analyses were pre-specified. The
treatment effects were examined according to quality
components (concealed treatment allocation, blinding of
patients and caregivers, blinded outcome assessment), time
to initiation of statins, and the type of statin. One post-hoc
sensitivity analysis was conducted including unpublished
data from a trial using cerivastatin.’’ [124]
Explanation. Authors may perform additional analyses to
help understand whether the results of their review are robust, all
of which should be reported. Such analyses include sensitivity
analysis, subgroup analysis, and meta-regression [125].
Sensitivity analyses are used to explore the degree to which the
main findings of a systematic review are affected by changes in
its methods or in the data used from individual studies (e.g.,
study inclusion criteria, results of risk of bias assessment).
Subgroup analyses address whether the summary effects vary
in relation to specific (usually clinical) characteristics of the
included studies or their participants. Meta-regression extends
the idea of subgroup analysis to the examination of the
quantitative influence of study characteristics on the effect size
[126]. Meta-regression also allows authors to examine the
contribution of different variables to the heterogeneity in study
findings. Readers of systematic reviews should be aware that
meta-regression has many limitations, including a danger of
over-interpretation of findings [127,128].
Even with limited data, many additional analyses can be
undertaken. The choice of which analysis to undertake will depend
on the aims of the review. None of these analyses, however, are
exempt from producing potentially misleading results. It is
important to inform readers whether these analyses were
performed, their rationale, and which were pre-specified.
RESULTS
Item 17: STUDY SELECTION. Give numbers of studies
screened, assessed for eligibility, and included in the review, with
reasons for exclusions at each stage, ideally with a flow diagram.
Examples. In text:
‘‘A total of 10 studies involving 13 trials were identified for
inclusion in the review. The search of Medline, PsycInfo and
Cinahl databases provided a total of 584 citations. After
adjusting for duplicates 509 remained. Of these, 479 studies
were discarded because after reviewing the abstracts it
appeared that these papers clearly did not meet the criteria.
Three additional studies…were discarded because full text
of the study was not available or the paper could not be
feasibly translated into English. The full text of the
remaining 27 citations was examined in more detail. It
appeared that 22 studies did not meet the inclusion criteria
as described. Five studies…met the inclusion criteria and
were included in the systematic review. An additional five
studies…that met the criteria for inclusion were identified by
checking the references of located, relevant papers and
searching for studies that have cited these papers. No
unpublished relevant studies were obtained.’’ [129]
See flow diagram Figure 2.
Explanation. Authors should report, ideally with a flow
diagram, the total number of records identified from electronic
bibliographic sources (including specialized database or registry
searches), hand searches of various sources, reference lists, citation
indices, and experts. It is useful if authors delineate for readers the
number of selected articles that were identified from the different
sources so that they can see, for example, whether most articles were
identified through electronic bibliographic sources or from references
or experts. Literature identified primarily from references or experts
may be prone to citation or publication bias [131,132].
The flow diagram and text should describe clearly the process of
report selection throughout the review. Authors should report:
unique records identified in searches; records excluded after
preliminary screening (e.g., screening of titles and abstracts);
reports retrieved for detailed evaluation; potentially eligible reports
that were not retrievable; retrieved reports that did not meet
inclusion criteria and the primary reasons for exclusion; and the
Box 5. Whether or Not To Combine Data
Deciding whether or not to combine data involves
statistical, clinical, and methodological considerations.
The statistical decisions are perhaps the most technical
and evidence-based. These are more thoroughly discussed
in Box 6. The clinical and methodological decisions are
generally based on discussions within the review team and
may be more subjective.
Clinical considerations will be influenced by the
question the review is attempting to address. Broad
questions might provide more ‘‘license’’ to combine more
disparate studies, such as whether ‘‘Ritalin is effective in
increasing focused attention in people diagnosed with
attention deficit hyperactivity disorder (ADHD).’’ Here
authors might elect to combine reports of studies
involving children and adults. If the clinical question is
more focused, such as whether ‘‘Ritalin is effective in
increasing classroom attention in previously undiagnosed
ADHD children who have no comorbid conditions,’’ it is
likely that different decisions regarding synthesis of studies
are taken by authors. In any case authors should describe
their clinical decisions in the systematic review report.
Deciding whether or not to combine data also has a
methodological component. Reviewers may decide not to
combine studies of low risk of bias with those of high risk
of bias (see Items 12 and 19). For example, for subjective
outcomes, systematic review authors may not wish to
combine assessments that were completed under blind
conditions with those that were not.
For any particular question there may not be a ‘‘right’’
or ‘‘wrong’’ choice concerning synthesis, as such decisions
are likely complex. However, as the choice may be
subjective, authors should be transparent as to their key
decisions and describe them for readers.
PLoS Medicine | www.plosmedicine.org 13 July 2009 | Volume 6 | Issue 7 | e1000100
studies included in the review. Indeed, the most appropriate layout
may vary for different reviews.
Authors should also note the presence of duplicate or
supplementary reports so that readers understand the number of
individual studies compared to the number of reports that were
included in the review. Authors should be consistent in their use of
terms, such as whether they are reporting on counts of citations,
records, publications, or studies. We believe that reporting the
number of studies is the most important.
A flow diagram can be very useful; it should depict all the
studies included based upon fulfilling the eligibility criteria,
whether or not data have been combined for statistical analysis.
A recent review of 87 systematic reviews found that about half
included a QUOROM flow diagram [133]. The authors of this
research recommended some important ways that reviewers can
improve the use of a flow diagram when describing the flow of
information throughout the review process, including a separate
flow diagram for each important outcome reported [133].
Item 18: STUDY CHARACTERISTICS. For each study,
present characteristics for which data were extracted (e.g., study
size, PICOS, follow-up period) and provide the citation.
Examples. In text:
‘‘Characteristics of included studies
Methods
All four studies finally selected for the review were randomised
controlled trials published in English. The duration of the
intervention was 24 months for the RIO-North America and
12 months for the RIO-Diabetes, RIO-Lipids and RIO-
Europe study. Although the last two described a period of 24
months during which they were conducted, only the first 12-
months results are provided. All trials had a run-in, as a single
blind period before the randomisation.
Participants
The included studies involved 6625 participants. The main
inclusion criteria entailed adults (18 years or older), with a
body mass index greater than 27 kg/m
2
and less than 5 kg
variation in body weight within the three months before
study entry.
Intervention
All trials were multicentric. The RIO-North America was
conducted in the USA and Canada, RIO-Europe in Europe
and the USA, RIO-Diabetes in the USA and 10 other
Box 6. Meta-Analysis and Assessment of Consistency (Heterogeneity)
Meta-Analysis: Statistical Combination of the Results
of Multiple Studies If it is felt that studies should have
their results combined statistically, other issues must be
considered because there are many ways to conduct a meta-
analysis. Different effect measures can be used for both
binary and continuous outcomes (see Item 13). Also, there
are two commonly used statistical models for combining
data in a meta-analysis [195]. The fixed-effect model assumes
that there is a common treatment effect for all included
studies [196]; it is assumed that the observed differences in
results across studies reflect random variation [196]. The
random-effects model assumes that there is no common
treatment effect for all included studies but rather that the
variation of the effects across studies follows a particular
distribution [197]. In a random-effects model it is believed
that the included studies represent a random sample from a
larger population of studies addressing the question of
interest [198].
There is no consensus about whether to use fixed- or
random-effects models, and both are in wide use. The
following differences have influenced some researchers
regarding their choice between them. The random-effects
model gives more weight to the results of smaller trials than
does the fixed-effect analysis, which may be undesirable as
small trials may be inferior and most prone to publication
bias. The fixed-effect model considers only within-study
variability whereas the random-effects model considers both
within- and between-study variability. This is why a fixed-
effect analysis tends to give narrower confidence intervals
(i.e., provide greater precision) than a random-effects
analysis [110,196,199]. In the absence of any between-study
heterogeneity, the fixed- and random-effects estimates will
coincide.
In addition, there are different methods for performing
both types of meta-analysis [200]. Common fixed-effect
approaches are Mantel-Haenszel and inverse variance,
whereas random-effects analyses usually use the DerSimo-
nian and Laird approach, although other methods exist,
including Bayesian meta-analysis [201].
In the presence of demonstrable between-study hetero-
geneity (see below), some consider that the use of a fixed-
effect analysis is counterintuitive because their main
assumption is violated. Others argue that it is inappropriate
to conduct any meta-analysis when there is unexplained
variability across trial results. If the reviewers decide not to
combine the data quantitatively, a danger is that eventually
they may end up using quasi-quantitative rules of poor
validity (e.g., vote counting of how many studies have
nominally significant results) for interpreting the evidence.
Statistical methods to combine data exist for almost any
complex situation that may arise in a systematic review, but
one has to be aware of their assumptions and limitations to
avoid misapplying or misinterpreting these methods.
Assessment of Consistency (Heterogeneity) We expect
some variation (inconsistency) in the results of different
studies due to chance alone. Variability in excess of that due
to chance reflects true differences in the results of the trials,
and is called ‘‘heterogeneity.’’ The conventional statistical
approach to evaluating heterogeneity is a chi-squared test
(Cochran’s Q), but it has low power when there are few
studies and excessive power when there are many studies
[202]. By contrast, the I
2
statistic quantifies the amount of
variation in results across studies beyond that expected by
chance and so is preferable to Q [202,203]. I
2
represents the
percentage of the total variation in estimated effects across
studies that is due to heterogeneity rather than to chance;
some authors consider an I
2
value less than 25% as low [202].
However, I
2
also suffers from large uncertainty in the
common situation where only a few studies are available
[204], and reporting the uncertainty in I
2
(e.g., as the 95%
confidence interval) may be helpful [145]. When there are
few studies, inferences about heterogeneity should be
cautious.
When considerable heterogeneity is observed, it is
advisable to consider possible reasons [205]. In particular,
the heterogeneity may be due to differences between
subgroups of studies (see Item 16). Also, data extraction
errors are a common cause of substantial heterogeneity in
results with continuous outcomes [139].
PLoS Medicine | www.plosmedicine.org 14 July 2009 | Volume 6 | Issue 7 | e1000100
different countries not specified, and RIO-Lipids in eight
unspecified different countries.
The intervention received was placebo, 5 mg of rimonabant
or 20 mg of rimonabant once daily in addition to a mild
hypocaloric diet (600 kcal/day deficit).
Outcomes
Primary
In all studies the primary outcome assessed was weight
change from baseline after one year of treatment and the
RIO-North America study also evaluated the prevention of
weight regain between the first and second year. All studies
evaluated adverse effects, including those of any kind and
serious events. Quality of life was measured in only one
study, but the results were not described (RIO-Europe).
Secondary and additional outcomes
These included prevalence of metabolic syndrome after one
year and change in cardiometabolic risk factors such as
blood pressure, lipid profile, etc.
No study included mortality and costs as outcome.
The timing of outcome measures was variable and could
include monthly investigations, evaluations every three
months or a single final evaluation after one year.’’ [134]
In table: See Table 2.
Explanation. For readers to gauge the validity and
applicability of a systematic review’s results, they need to know
something about the included studies. Such information includes
PICOS (Box 2) and specific information relevant to the review
question. For example, if the review is examining the long-term
effects of antidepressants for moderate depressive disorder, authors
should report the follow-up periods of the included studies. For
each included study, authors should provide a citation for the
source of their information regardless of whether or not the study
is published. This information makes it easier for interested
readers to retrieve the relevant publications or documents.
Reporting study-level data also allows the comparison of the
main characteristics of the studies included in the review. Authors
should present enough detail to allow readers to make their own
judgments about the relevance of included studies. Such
information also makes it possible for readers to conduct their
own subgroup analyses and interpret subgroups, based on study
characteristics.
Authors should avoid, whenever possible, assuming information
when it is missing from a study report (e.g., sample size, method of
randomization). Reviewers may contact the original investigators
to try to obtain missing information or confirm the data extracted
for the systematic review. If this information is not obtained, this
should be noted in the report. If information is imputed, the reader
Box 7. Bias Caused by Selective Publication of Studies or Results within Studies
Systematic reviews aim to incorporate information from all
relevant studies. The absence of information from some
studies may pose a serious threat to the validity of a review.
Data may be incomplete because some studies were not
published, or because of incomplete or inadequate reporting
within a published article. These problems are often summa-
rized as ‘‘publication bias’’ although in fact the bias arises from
non-publication of full studies and selective publication of
results in relation to their findings. Non-publication of research
findings dependent on the actual results is an important risk of
bias to a systematic review and meta-analysis.
Missing Studies Several empirical investigations have
shown that the findings from clinical trials are more likely
to be published if the results are statistically significant
(p,0.05) than if they are not [125,206,207]. For example, of
500 oncology trials with more than 200 participants for
which preliminary results were presented at a conference of
the American Society of Clinical Oncology, 81% with p,0.05
were published in full within five years compared to only
68% of those with p.0.05 [208].
Also, among published studies, those with statistically
significant results are published sooner than those with non-
significant findings [209]. When some studies are missing for
these reasons, the available results will be biased towards
exaggerating the effect of an intervention.
Missing Outcomes In many systematic reviews only some
of the eligible studies (often a minority) can be included in a
meta-analysis for a specific outcome. For some studies, the
outcome may not be measured or may be measured but not
reported. The former will not lead to bias, but the latter
could.
Evidence is accumulating that selective reporting bias is
widespread and of considerable importance [42,43]. In
addition, data for a given outcome may be analyzed in
multiple ways and the choice of presentation influenced by
the results obtained. In a study of 102 randomized trials,
comparison of published reports with trial protocols showed
that a median of 38% efficacy and 50% safety outcomes per
trial, respectively, were not available for meta-analysis.
Statistically significant outcomes had a higher odds of being
fully reported in publications when compared with non-
significant outcomes for both efficacy (pooled odds ratio 2.4;
95% confidence interval 1.4 to 4.0) and safety (4.7, 1.8 to 12)
data. Several other studies have had similar findings [210,211].
Detection of Missing Information Missing studies may
increasingly be identified from trials registries. Evidence of
missing outcomes may come from comparison with the
study protocol, if available, or by careful examination of
published articles [11]. Study publication bias and selective
outcome reporting are difficult to exclude or verify from the
available results, especially when few studies are available.
If the available data are affected by either (or both) of the
above biases, smaller studies would tend to show larger
estimates of the effects of the intervention. Thus one
possibility is to investigate the relation between effect size
and sample size (or more specifically, precision of the effect
estimate). Graphical methods, especially the funnel plot
[212], and analytic methods (e.g., Egger’s test) are often used
[213,214,215], although their interpretation can be problem-
atic [216,217]. Strictly speaking, such analyses investigate
‘‘small study bias’’; there may be many reasons why smaller
studies have systematically different effect sizes than larger
studies, of which reporting bias is just one [218]. Several
alternative tests for bias have also been proposed, beyond
the ones testing small study bias [215,219,220], but none can
be considered a gold standard. Although evidence that
smaller studies had larger estimated effects than large ones
may suggest the possibility that the available evidence is
biased, misinterpretation of such data is common [123].
PLoS Medicine | www.plosmedicine.org 15 July 2009 | Volume 6 | Issue 7 | e1000100
should be told how this was done and for which items. Presenting
study-level data makes it possible to clearly identify unpublished
information obtained from the original researchers and make it
available for the public record.
Typically, study-level characteristics are presented as a table as
in the example in Table 2. Such presentation ensures that all
pertinent items are addressed and that missing or unclear
information is clearly indicated. Although paper-based journals
do not generally allow for the quantity of information available in
electronic journals or Cochrane reviews, this should not be
accepted as an excuse for omission of important aspects of the
methods or results of included studies, since these can, if necessary,
be shown on a Web site.
Following the presentation and description of each included
study, as discussed above, reviewers usually provide a narrative
summary of the studies. Such a summary provides readers with an
Figure 2. Example Figure: Example flow diagram of study selection. DDW, Digestive Disease Week; UEGW, United European
Gastroenterology Week. Reproduced with permission from [130].
doi:10.1371/journal.pmed.1000100.g002
PLoS Medicine | www.plosmedicine.org 16 July 2009 | Volume 6 | Issue 7 | e1000100
overview of the included studies. It may for example address the
languages of the published papers, years of publication, and
geographic origins of the included studies.
The PICOS framework is often helpful in reporting the narrative
summary indicating, for example, the clinical characteristics and
disease severity of the participants and the main features of the
intervention and of the comparison group. For non-pharmacolog-
ical interventions, it may be helpful to specify for each study the key
elements of the intervention received by each group. Full details of
the interventions in included studies were reported in only three of
25 systematic reviews relevant to general practice [84].
Item 19: RISK OF BIAS WITHIN STUDIES. Present data
on risk of bias of each study and, if available, any outcome-level
assessment (see Item 12).
Example. See Table 3.
Explanation. We recommend that reviewers assess the risk of
bias in the included studies using a standard approach with
defined criteria (see Item 12). They should report the results of any
such assessments [89].
Reporting only summary data (e.g., ‘‘two of eight trials
adequately concealed allocation’’) is inadequate because it fails
to inform readers which studies had the particular methodological
shortcoming. A more informative approach is to explicitly report
the methodological features evaluated for each study. The
Cochrane Collaboration’s new tool for assessing the risk of bias
also requests that authors substantiate these assessments with any
relevant text from the original studies [11]. It is often easiest to
provide these data in a tabular format, as in the example.
However, a narrative summary describing the tabular data can
also be helpful for readers.
Item 20: RESULTS OF INDIVIDUAL STUDIES. For all
outcomes considered (benefits and harms), present, for each study:
(a) simple summary data for each intervention group and (b) effect
estimates and confidence intervals, ideally with a forest plot.
Examples. See Table 4 and Figure 3.
Explanation. Publication of summary data from individual
studies allows the analyses to be reproduced and other analyses
and graphical displays to be investigated. Others may wish to
assess the impact of excluding particular studies or consider
subgroup analyses not reported by the review authors. Displaying
the results of each treatment group in included studies also enables
inspection of individual study features. For example, if only odds
ratios are provided, readers cannot assess the variation in event
rates across the studies, making the odds ratio impossible to
interpret [138]. Additionally, because data extraction errors in
meta-analyses are common and can be large [139], the
presentation of the results from individual studies makes it easier
to identify errors. For continuous outcomes, readers may wish to
Table 2. Example Table: Summary of included studies evaluating the efficacy of antiemetic agents in acute gastroenteritis.
Source Setting
No. of
Patients Age Range Inclusion Criteria Antiemetic Agent Route Follow-Up
Freedman et al., 2006 ED 214 6 months–10 years GE with mild to moderate
dehydration and vomiting
in the preceding 4 hours
Ondansetron PO 1–2 weeks
Reeves et al., 2002 ED 107 1 month–22 years GE and vomiting requiring IV
rehydration
Ondansetron IV 5–7 days
Roslund et al., 2007 ED 106 1–10 years GE with failed oral rehydration
attempt in ED
Ondansetron PO 1 week
Stork et al., 2006 ED 137 6 months–12 years GE, recurrent emesis, mild
to moderate dehydration,
and failed oral hydration
Ondansetron and
dexamethasone
IV 1 and 2 days
ED, emergency department; GE, gastroenteritis; IV, intravenous; PO, by mouth.
Adapted from [135].
doi:10.1371/journal.pmed.1000100.t002
Table 3. Example Table: Quality measures of the randomized controlled trials that failed to fulfill any one of six markers of validity.
Trials
Concealment of
Randomisation
RCT Stopped
Early
Patients
Blinded
Health Care
Providers Blinded
Data Collectors
Blinded
Outcome
Assessors Blinded
Liu No No Yes Yes Yes Yes
Stone Yes No No Yes Yes Yes
Polderman Yes Yes No No No Yes
Zaugg Yes No No No Yes Yes
Urban Yes Yes No No, except
anesthesiologists
Yes Yes
RCT, randomized controlled trial.
Adapted from [96].
doi:10.1371/journal.pmed.1000100.t003
PLoS Medicine | www.plosmedicine.org 17 July 2009 | Volume 6 | Issue 7 | e1000100
examine the consistency of standard deviations across studies, for
example, to be reassured that standard deviation and standard
error have not been confused [138].
For each study, the summary data for each intervention group
are generally given for binary outcomes as frequencies with and
without the event (or as proportions such as 12/45). It is not
sufficient to report event rates per intervention group as
percentages. The required summary data for continuous outcomes
are the mean, standard deviation, and sample size for each group.
In reviews that examine time-to-event data, the authors should
report the log hazard ratio and its standard error (or confidence
interval) for each included study. Sometimes, essential data are
missing from the reports of the included studies and cannot be
calculated from other data but may need to be imputed by the
reviewers. For example, the standard deviation may be imputed
using the typical standard deviations in the other trials [116,117]
(see Item 14). Whenever relevant, authors should indicate which
results were not reported directly and had to be estimated from
other information (see Item 13). In addition, the inclusion of
unpublished data should be noted.
For all included studies it is important to present the estimated
effect with a confidence interval. This information may be
incorporated in a table showing study characteristics or may be
shown in a forest plot [140]. The key elements of the forest plot are
the effect estimates and confidence intervals for each study shown
graphically, but it is preferable also to include, for each study, the
numerical group-specific summary data, the effect size and
confidence interval, and the percentage weight (see second example
[Figure 3]). For discussion of the results of meta-analysis, see Item 21.
In principle, all the above information should be provided for
every outcome considered in the review, including both benefits
and harms. When there are too many outcomes for full
information to be included, results for the most important
outcomes should be included in the main report with other
information provided as a Web appendix. The choice of the
information to present should be justified in light of what was
originally stated in the protocol. Authors should explicitly mention
if the planned main outcomes cannot be presented due to lack of
information. There is some evidence that information on harms is
only rarely reported in systematic reviews, even when it is available
in the original studies [141]. Selective omission of harms results
biases a systematic review and decreases its ability to contribute to
informed decision making.
Item 21: SYNTHESES OF RESULTS. Present the main
results of the review. If meta-analyses are done, include for each,
confidence intervals and measures of consistency.
Table 4. Example Table: Heterotopic ossification in trials
comparing radiotherapy to non-steroidal anti-inflammatory
drugs after major hip procedures and fractures.
Author (Year) Radiotherapy NSAID
Kienapfel (1999) 12/49 24.5% 20/55 36.4%
Sell (1998) 2/77 2.6% 18/77 23.4%
Kolbl (1997) 39/188 20.7% 18/113 15.9%
Kolbl (1998) 22/46 47.8% 6/54 11.1%
Moore (1998) 9/33 27.3% 18/39 46.2%
Bremen-Kuhne (1997) 9/19 47.4% 11/31 35.5%
Knelles (1997) 5/101 5.0% 46/183 25.4%
NSAID, non-steroidal anti-inflammatory drug.
Adapted from [136].
doi:10.1371/journal.pmed.1000100.t004
Figure 3. Example Figure: Overall failure (defined as failure of assigned regimen or relapse) with tetracycline-rifampicin versus
tetracycline-streptomycin. CI, confidence interval. Reproduced with permission from [137].
doi:10.1371/journal.pmed.1000100.g003
PLoS Medicine | www.plosmedicine.org 18 July 2009 | Volume 6 | Issue 7 | e1000100
Examples. ‘‘Mortality data were available for all six trials,
randomizing 311 patients and reporting data for 305
patients. There were no deaths reported in the three
respiratory syncytial virus/severe bronchiolitis trials; thus
our estimate is based on three trials randomizing 232
patients, 64 of whom died. In the pooled analysis, surfactant
was associated with significantly lower mortality (relative
risk = 0.7, 95% confidence interval = 0.4–0.97, P = 0.04).
There was no evidence of heterogeneity (I
2
= 0%)’’. [142]
‘‘Because the study designs, participants, interventions, and
reported outcome measures varied markedly, we focused on
describing the studies, their results, their applicability, and
their limitations and on qualitative synthesis rather than
meta-analysis.’’ [143]
‘‘We detected significant heterogeneity within this compar-
ison (I
2
= 46.6%; x
2
= 13.11, df = 7; P = 0.07). Retrospective
exploration of the heterogeneity identified one trial that
seemed to differ from the others. It included only small
ulcers (wound area less than 5 cm
2
). Exclusion of this trial
removed the statistical heterogeneity and did not affect the
finding of no evidence of a difference in healing rate
between hydrocolloids and simple low adherent dressings
(relative risk = 0.98, [95% confidence interval] 0.85 to 1.12;
I
2
= 0%).’’ [144]
Explanation. Results of systematic reviews should be
presented in an orderly manner. Initial narrative descriptions of
the evidence covered in the review (see Item 18) may tell readers
important things about the study populations and the design and
conduct of studies. These descriptions can facilitate the
examination of patterns across studies. They may also provide
important information about applicability of evidence, suggest the
likely effects of any major biases, and allow consideration, in a
systematic manner, of multiple explanations for possible
differences of findings across studies.
If authors have conducted one or more meta-analyses, they
should present the results as an estimated effect across studies
with a confidence interval. It is often simplest to show each
meta-analysis summary with the actual results of included studies
in a forest plot (see Item 20) [140]. It should always be clear
which of the included studies contributed to each meta-analysis.
Authors should also provide, for each meta-analysis, a measure
of the consistency of the results from the included studies such
as I
2
(heterogeneity; see Box 6); a confidence interval may also
be given for this measure [145]. If no meta-analysis was
performed, the qualitative inferences should be presented as
systematically as possible with an explanation of why meta-
analysis was not done, as in the second example above [143].
Readers may find a forest plot, without a summary estimate,
helpful in such cases.
Authors should in general report syntheses for all the outcome
measures they set out to investigate (i.e., those described in the
protocol; see Item 4) to allow readers to draw their own
conclusions about the implications of the results. Readers should
be made aware of any deviations from the planned analysis.
Authors should tell readers if the planned meta-analysis was not
thought appropriate or possible for some of the outcomes and the
reasons for that decision.
It may not always be sensible to give meta-analysis results and
forest plots for each outcome. If the review addresses a broad
question, there may be a very large number of outcomes. Also,
some outcomes may have been reported in only one or two
studies, in which case forest plots are of little value and may be
seriously biased.
Of 300 systematic reviews indexed in MEDLINE in 2004, a
little more than half (54%) included meta-analyses, of which the
majority (91%) reported assessing for inconsistency in results.
Item 22: RISK OF BIAS ACROSS STUDIES. Present
results of any assessment of risk of bias across studies (see Item 15).
Examples. ‘‘Strong evidence of heterogeneity (I
2
= 79%,
P,0.001) was observed. To explore this heterogeneity, a
funnel plot was drawn. The funnel plot in Figure 4 shows
evidence of considerable asymmetry.’’ [146]
‘‘Specifically, four sertraline trials involving 486 participants
and one citalopram trial involving 274 participants were
reported as having failed to achieve a statistically significant
drug effect, without reporting mean HRSD [Hamilton Rating
Scale for Depression] scores. We were unable to find data from
these trials on pharmaceutical company Web sites or through
our search of the published literature. These omissions
represent 38% of patients in sertraline trials and 23% of
patients in citalopram trials. Analyses with and without
inclusion of these trials found no differences in the patterns
of results; similarly, the revealed patterns do not interact with
drug type. The purpose of using the data obtained from the
FDA was to avoid publication bias, by including unpublished
as well as published trials. Inclusion of only those sertraline and
citalopram trials for which means were reported to the FDA
would constitute a form of reporting bias similar to publication
bias and would lead to overestimation of drug–placebo
differences for these drug types. Therefore, we present analyses
only on data for medications for which complete clinical trials
change was reported.’’ [147]
Explanation. Authors should present the results of any
assessments of risk of bias across studies. If a funnel plot is
reported, authors should specify the effect estimate and measure of
precision used, presented typically on the x-axis and y-axis,
respectively. Authors should describe if and how they have tested
the statistical significance of any possible asymmetry (see Item 15).
Results of any investigations of selective reporting of outcomes
within studies (as discussed in Item 15) should also be reported.
Also, we advise authors to tell readers if any pre-specified analyses
for assessing risk of bias across studies were not completed and the
reasons (e.g., too few included studies).
Item 23: ADDITIONAL ANALYSES. Give results of
additional analyses, if done (e.g., sensitivity or subgroup analyses,
meta-regression [see Item 16]).
Examples. ‘‘…benefits of chondroitin were smaller in trials
with adequate concealment of allocation compared with
trials with unclear concealment (P for interaction = 0.050), in
trials with an intention-to-treat analysis compared with those
that had excluded patients from the analysis (P for
interaction = 0.017), and in large compared with small trials
(P for interaction = 0.022).’’ [148]
‘‘Subgroup analyses according to antibody status, antiviral
medications, organ transplanted, treatment duration, use of
antilymphocyte therapy, time to outcome assessment, study
quality and other aspects of study design did not
demonstrate any differences in treatment effects. Multivar-
PLoS Medicine | www.plosmedicine.org 19 July 2009 | Volume 6 | Issue 7 | e1000100
iate meta-regression showed no significant difference in
CMV [cytomegalovirus] disease after allowing for potential
confounding or effect-modification by prophylactic drug
used, organ transplanted or recipient serostatus in CMV
positive recipients and CMV negative recipients of CMV
positive donors.’’ [149]
Explanation. Authors should report any subgroup or
sensitivity analyses and whether or not they were pre-specified
(see Items 5 and 16). For analyses comparing subgroups of
studies (e.g., separating studies of low- and high-dose aspirin), the
authors should report any tests for interactions, as well as
estimates and confidence intervals from meta-analyses within
each subgroup. Similarly, meta-regression results (see Item 16)
should not be limited to p-values, but should include effect sizes
and confidence intervals [150], as the first example reported
above does in a table. The amount of data included in each
additional analysis should be specified if different from that
considered in the main analyses. This information is especially
relevant for sensitivity analyses that exclude some studies; for
example, those with high risk of bias.
Importantly, all additional analyses conducted should be
reported, not just those that were statistically significant. This
information will help avoid selective outcome reporting bias
within the review as has been demonstrated in reports of
randomized controlled trials [42,44,121,151,152]. Results from
exploratory subgroup or sensitivity analyses should be interpret-
ed cautiously, bearing in mind the potential for multiple analyses
to mislead.
DISCUSSION
Item 24: SUMMARY OF EVIDENCE. Summarize the main
findings, including the strength of evidence for each main
outcome; consider their relevance to key groups (e.g., health
care providers, users, and policy makers).
Example. ‘‘Overall, the evidence is not sufficiently robust
to determine the comparative effectiveness of angioplasty
(with or without stenting) and medical treatment alone. Only
2 randomized trials with long-term outcomes and a third
randomized trial that allowed substantial crossover of
treatment after 3 months directly compared angioplasty
and medical treatment…the randomized trials did not
evaluate enough patients or did not follow patients for a
sufficient duration to allow definitive conclusions to be made
about clinical outcomes, such as mortality and cardiovascu-
lar or kidney failure events.
Some acceptable evidence from comparison of medical
treatment and angioplasty suggested no difference in long-
term kidney function but possibly better blood pressure
control after angioplasty, an effect that may be limited to
patients with bilateral atherosclerotic renal artery stenosis.
The evidence regarding other outcomes is weak. Because the
reviewed studies did not explicitly address patients with
rapid clinical deterioration who may need acute interven-
tion, our conclusions do not apply to this important subset of
patients.’’ [143]
Explanation. Authors should give a brief and balanced
summary of the nature and findings of the review. Sometimes,
outcomes for which little or no data were found should be noted
due to potential relevance for policy decisions and future research.
Applicability of the review’s findings, to different patients, settings,
or target audiences, for example, should be mentioned. Although
there is no standard way to assess applicability simultaneously to
different audiences, some systems do exist [153]. Sometimes,
authors formally rate or assess the overall body of evidence
addressed in the review and can present the strength of their
summary recommendations tied to their assessments of the quality
of evidence (e.g., the GRADE system) [10].
Figure 4. Example Figure: Example of a funnel plot showing evidence of considerable asymmetry. SE, standard error. Adapted from
[146], with permission.
doi:10.1371/journal.pmed.1000100.g004
PLoS Medicine | www.plosmedicine.org 20 July 2009 | Volume 6 | Issue 7 | e1000100
Authors need to keep in mind that statistical significance of the
effects does not always suggest clinical or policy relevance.
Likewise, a non-significant result does not demonstrate that a
treatment is ineffective. Authors should ideally clarify trade-offs
and how the values attached to the main outcomes would lead
different people to make different decisions. In addition, adroit
authors consider factors that are important in translating the
evidence to different settings and that may modify the estimates of
effects reported in the review [153]. Patients and health care
providers may be primarily interested in which intervention is
most likely to provide a benefit with acceptable harms, while policy
makers and administrators may value data on organizational
impact and resource utilization.
Item 25: LIMITATIONS. Discuss limitations at study and
outcome level (e.g., risk of bias), and at review level (e.g.,
incomplete retrieval of identified research, reporting bias).
Examples. Outcome level:
‘‘The meta-analysis reported here combines data across
studies in order to estimate treatment effects with more
precision than is possible in a single study. The main
limitation of this meta-analysis, as with any overview, is that
the patient population, the antibiotic regimen and the
outcome definitions are not the same across studies.’’ [154]
Study and review level:
‘‘Our study has several limitations. The quality of the studies
varied. Randomization was adequate in all trials; however, 7
of the articles did not explicitly state that analysis of data
adhered to the intention-to-treat principle, which could lead
to overestimation of treatment effect in these trials, and we
could not assess the quality of 4 of the 5 trials reported as
abstracts. Analyses did not identify an association between
components of quality and re-bleeding risk, and the effect
size in favour of combination therapy remained statistically
significant when we excluded trials that were reported as
abstracts.
Publication bias might account for some of the effect we
observed. Smaller trials are, in general, analyzed with less
methodological rigor than larger studies, and an asymmet-
rical funnel plot suggests that selective reporting may have
led to an overestimation of effect sizes in small trials.’’ [155]
Explanation. A discussion of limitations should address the
validity (i.e., risk of bias) and reporting (informativeness) of the
included studies, limitations of the review process, and
generalizability (applicability) of the review. Readers may find it
helpful if authors discuss whether studies were threatened by
serious risks of bias, whether the estimates of the effect of the
intervention are too imprecise, or if there were missing data for
many participants or important outcomes.
Limitations of the review process might include limitations of the
search (e.g., restricting to English-language publications), and any
difficulties in the study selection, appraisal, and meta-analysis
processes. For example, poor or incomplete reporting of study
designs, patient populations, and interventions may hamper
interpretation and synthesis of the included studies [84]. Applica-
bility of the review may be affected if there are limited data for
certain populations or subgroups where the intervention might
perform differently or few studies assessing the most important
outcomes of interest; or if there is a substantial amount of data
relating to an outdated intervention or comparator or heavy reliance
on imputation of missing values for summary estimates (Item 14).
Item 26: CONCLUSIONS. Provide a general interpretation
of the results in the context of other evidence, and implications for
future research.
Example. Implications for practice:
‘‘Between 1995 and 1997 five different meta-analyses of the
effect of antibiotic prophylaxis on infection and mortality
were published. All confirmed a significant reduction in
infections, though the magnitude of the effect varied from
one review to another. The estimated impact on overall
mortality was less evident and has generated considerable
controversy on the cost effectiveness of the treatment. Only
one among the five available reviews, however, suggested
that a weak association between respiratory tract infections
and mortality exists and lack of sufficient statistical power
may have accounted for the limited effect on mortality.’’
Implications for research:
‘‘A logical next step for future trials would thus be the
comparison of this protocol against a regimen of a systemic
antibiotic agent only to see whether the topical component
can be dropped. We have already identified six such trials
but the total number of patients so far enrolled (n = 1056) is
too small for us to be confident that the two treatments are
really equally effective. If the hypothesis is therefore
considered worth testing more and larger randomised
controlled trials are warranted. Trials of this kind, however,
would not resolve the relevant issue of treatment induced
resistance. To produce a satisfactory answer to this, studies
with a different design would be necessary. Though a
detailed discussion goes beyond the scope of this paper,
studies in which the intensive care unit rather than the
individual patient is the unit of randomisation and in which
the occurrence of antibiotic resistance is monitored over a
long period of time should be undertaken.’’ [156]
Explanation. Systematic reviewers sometimes draw
conclusions that are too optimistic [157] or do not consider
the harms equally as carefully as the benefits, although some
evidence suggests these problems are decreasing [158]. If
conclusions cannot be drawn because there are too few reliable
studies, or too much uncertainty, this should be stated. Such a
finding can be as important as finding consistent effects from
several large studies.
Authors should try to relate the results of the review to other
evidence, as this helps readers to better interpret the results. For
example, there may be other systematic reviews about the same
general topic that have used different methods or have addressed
related but slightly different questions [159,160]. Similarly, there
may be additional information relevant to decision makers, such as
the cost-effectiveness of the intervention (e.g., health technology
assessment). Authors may discuss the results of their review in the
context of existing evidence regarding other interventions.
We advise authors also to make explicit recommendations for
future research. In a sample of 2,535 Cochrane reviews, 82%
included recommendations for research with specific interventions,
30% suggested the appropriate type of participants, and 52%
suggested outcome measures for future research [161]. There is no
corresponding assessment about systematic reviews published in
medical journals, but we believe that such recommendations are
much less common in those reviews.
Clinical research should not be planned without a thorough
knowledge of similar, existing research [162]. There is evidence
PLoS Medicine | www.plosmedicine.org 21 July 2009 | Volume 6 | Issue 7 | e1000100
that this still does not occur as it should and that authors of
primary studies do not consider a systematic review when they
design their studies [163]. We believe systematic reviews have
great potential for guiding future clinical research.
FUNDING
Item 27: FUNDING. Describe sources of funding or other
support (e.g., supply of data) for the systematic review; role of
funders for the systematic review.
Examples: ‘‘The evidence synthesis upon which this article
was based was funded by the Centers for Disease Control
and Prevention for the Agency for Healthcare Research and
Quality and the U.S. Prevention Services Task Force.’’
[164]
‘‘Role of funding source: the funders played no role in study
design, collection, analysis, interpretation of data, writing of
the report, or in the decision to submit the paper for
publication. They accept no responsibility for the contents.’’
[165]
Explanation. Authors of systematic reviews, like those of any
other research study, should disclose any funding they received to
carry out the review, or state if the review was not funded. Lexchin
and colleagues [166] observed that outcomes of reports of
randomized trials and meta-analyses of clinical trials funded by
the pharmaceutical industry are more likely to favor the sponsor’s
product compared to studies with other sources of funding. Similar
results have been reported elsewhere [167,168]. Analogous data
suggest that similar biases may affect the conclusions of systematic
reviews [169].
Given the potential role of systematic reviews in decision
making, we believe authors should be transparent about the
funding and the role of funders, if any. Sometimes the funders will
provide services, such as those of a librarian to complete the
searches for relevant literature or access to commercial databases
not available to the reviewers. Any level of funding or services
provided to the systematic review team should be reported.
Authors should also report whether the funder had any role in the
conduct or report of the review. Beyond funding issues, authors
should report any real or perceived conflicts of interest related to
their role or the role of the funder in the reporting of the
systematic review [170].
In a survey of 300 systematic reviews published in November
2004, funding sources were not reported in 41% of the
reviews [3]. Only a minority of reviews (2%) reported being
funded by for-profit sources, but the true proportion may be
higher [171].
Additional Considerations for Systematic Reviews
of Non-Randomized Intervention Studies or for
Other Types of Systematic Reviews
The PRISMA Statement and this document have focused on
systematic reviews of reports of randomized trials. Other study
designs, including non-randomized studies, quasi-experimental
studies, and interrupted time series, are included in some
systematic reviews that evaluate the effects of health care
interventions [172,173]. The methods of these reviews may differ
to varying degrees from the typical intervention review, for
example regarding the literature search, data abstraction,
assessment of risk of bias, and analysis methods. As such, their
reporting demands might also differ from what we have described
here. A useful principle is for systematic review authors to ensure
that their methods are reported with adequate clarity and
transparency to enable readers to critically judge the available
evidence and replicate or update the research.
In some systematic reviews, the authors will seek the raw data
from the original researchers to calculate the summary statistics.
These systematic reviews are called individual patient (or
participant) data reviews [40,41]. Individual patient data meta-
analyses may also be conducted with prospective accumulation of
data rather than retrospective accumulation of existing data. Here
too, extra information about the methods will need to be reported.
Other types of systematic reviews exist. Realist reviews aim to
determine how complex programs work in specific contexts and
settings [174]. Meta-narrative reviews aim to explain complex
bodies of evidence through mapping and comparing different
over-arching storylines [175]. Network meta-analyses, also known
as multiple treatments meta-analyses, can be used to analyze data
from comparisons of many different treatments [176,177]. They
use both direct and indirect comparisons, and can be used to
compare interventions that have not been directly compared.
We believe that the issues we have highlighted in this paper are
relevant to ensure transparency and understanding of the
processes adopted and the limitations of the information presented
in systematic reviews of different types. We hope that PRISMA
can be the basis for more detailed guidance on systematic reviews
of other types of research, including diagnostic accuracy and
epidemiological studies.
Discussion
We developed the PRISMA Statement using an approach for
developing reporting guidelines that has evolved over several years
[178]. The overall aim of PRISMA is to help ensure the clarity
and transparency of reporting of systematic reviews, and recent
data indicate that this reporting guidance is much needed [3].
PRISMA is not intended to be a quality assessment tool and it
should not be used as such.
This PRISMA Explanation and Elaboration document was
developed to facilitate the understanding, uptake, and dissemina-
tion of the PRISMA Statement and hopefully provide a
pedagogical framework for those interested in conducting and
reporting systematic reviews. It follows a format similar to that
used in other explanatory documents [17,18,19]. Following the
recommendations in the PRISMA checklist may increase the word
count of a systematic review report. We believe, however, that the
benefit of readers being able to critically appraise a clear,
complete, and transparent systematic review report outweighs
the possible slight increase in the length of the report.
While the aims of PRISMA are to reduce the risk of flawed
reporting of systematic reviews and improve the clarity and
transparency in how reviews are conducted, we have little data to
state more definitively whether this ‘‘intervention’’ will achieve its
intended goal. A previous effort to evaluate QUOROM was not
successfully completed [178]. Publication of the QUOROM
Statement was delayed for two years while a research team
attempted to evaluate its effectiveness by conducting a randomized
controlled trial with the participation of eight major medical
journals. Unfortunately that trial was not completed due to accrual
problems (David Moher, personal communication). Other evalu-
ation methods might be easier to conduct. At least one survey of
139 published systematic reviews in the critical care literature
[179] suggests that their quality improved after the publication of
QUOROM.
PLoS Medicine | www.plosmedicine.org 22 July 2009 | Volume 6 | Issue 7 | e1000100
If the PRISMA Statement is endorsed by and adhered to in
journals, as other reporting guidelines have been
[17,18,19,180], there should be evidence of improved reporting
of systematic reviews. For example, there have been several
evaluations of whether the use of CONSORT improves reports
of randomized controlled trials. A systematic review of these
studies [181] indicates that use of CONSORT is associated
with improved reporting of certain items, such as allocation
concealment. We aim to evaluate the benefits (i.e., improved
reporting) and possible adverse effects (e.g., increased word
length) of PRISMA and we encourage others to consider doing
likewise.
Even though we did not carry out a systematic literature
search to produce our checklist, and this is indeed a limitation
of our effort, PRISMA was nevertheless developed using an
evidence-based approach, whenever possible. Checklist items
were included if there was evidence that not reporting the item
was associated with increased risk of bias, or where it was
clear that information was necessary to appraise the reliability
of a review. To keep PRISMA up-to-date and as evidence-
based as possible requires regular vigilance of the literature,
which is growing rapidly. Currently the Cochrane Methodol-
ogy Register has more than 11,000 records pertaining to the
conduct and reporting of systematic reviews and other
evaluations of health and social care. For some checklist items,
such as reporting the abstract (Item 2), we have used evidence
from elsewhere in the belief that the issue applies equally well
to reporting of systematic reviews. Yet for other items,
evidence does not exist; for example, whether a training
exercise improves the accuracy and reliability of data
extraction. We hope PRISMA will act as a catalyst to help
generate further evidence that can be considered when further
revising the checklist in the future.
More than ten years have passed between the development of
the QUOROM Statement and its update, the PRISMA
Statement. We aim to update PRISMA more frequently. We
hope that the implementation of PRISMA will be better than it
has been for QUOROM. There are at least two reasons to be
optimistic. First, systematic reviews are increasingly used by health
care providers to inform ‘‘best practice’’ patient care. Policy
analysts and managers are using systematic reviews to inform
health care decision making, and to better target future research.
Second, we anticipate benefits from the development of the
EQUATOR Network, described below.
Developing any reporting guideline requires considerable effort,
experience, and expertise. While reporting guidelines have been
successful for some individual efforts [17,18,19], there are likely
others who want to develop reporting guidelines who possess little
time, experience, or knowledge as to how to do so appropriately.
The EQUATOR Network (Enhancing the QUAlity and Trans-
parency Of health Research) aims to help such individuals and
groups by serving as a global resource for anybody interested in
developing reporting guidelines, regardless of the focus
[7,180,182]. The overall goal of EQUATOR is to improve the
quality of reporting of all health science research through the
development and translation of reporting guidelines. Beyond this
aim, the network plans to develop a large Web presence by
developing and maintaining a resource center of reporting tools,
and other information for reporting research (http://www.
equator-network.org/).
We encourage health care journals and editorial groups, such as
the World Association of Medical Editors and the International
Committee of Medical Journal Editors, to endorse PRISMA in
much the same way as they have endorsed other reporting
guidelines, such as CONSORT. We also encourage editors of
health care journals to support PRISMA by updating their
‘‘Instructions to Authors’’ and including the PRISMA Web
address, and by raising awareness through specific editorial
actions.
Supporting Information
Figure S1 Flow of information through the different phases of a
systematic review (downloadable template document for research-
ers to re-use).
Found at: doi:10.1371/journal.pmed.1000100.s001 (0.08 MB
DOC)
Text S1 Checklist of items to include when reporting a
systematic review or meta-analysis (downloadable template
document for researchers to re-use).
Found at: doi:10.1371/journal.pmed.1000100.s002 (0.04 MB
DOC)
Acknowledgments
The following people contributed to this paper:
Doug Altman, DSc, Centre for Statistics in Medicine (Oxford, UK);
Gerd Antes, PhD, University Hospital Freiburg (Freiburg, Germany);
David Atkins, MD, MPH, Health Services Research and Development
Service, Veterans Health Administration (Washington, D. C., US);
Virginia Barbour, MRCP, DPhil, PLoS Medicine (Cambridge, UK); Nick
Barrowman, PhD, Children’s Hospital of Eastern Ontario (Ottawa,
Canada); Jesse A. Berlin, ScD, Johnson & Johnson Pharmaceutical
Research and Development (Titusville, New Jersey, US); Jocalyn Clark,
PhD, PLoS Medicine (at the time of writing, BMJ, London, UK); Mike
Clarke, PhD, UK Cochrane Centre (Oxford, UK) and School of
Nursing and Midwifery, Trinity College (Dublin, Ireland); Deborah
Cook, MD, Departments of Medicine, Clinical Epidemiology and
Biostatistics, McMaster University (Hamilton, Canada); Roberto
D’Amico, PhD, Universita` di Modena e Reggio Emilia (Modena,
Italy) and Centro Cochrane Italiano, Istituto Ricerche Farmacologiche
Mario Negri (Milan, Italy); Jonathan J. Deeks, PhD, University of
Birmingham (Birmingham, UK); P. J. Devereaux, MD, PhD,
Departments of Medicine, Clinical Epidemiology and Biostatistics,
McMaster University (Hamilton, Canada); Kay Dickersin, PhD, Johns
Hopkins Bloomberg School of Public Health (Baltimore, Maryland,
US); Matthias Egger, MD, Department of Social and Preventive
Medicine, University of Bern (Bern, Switzerland); Edzard Ernst, MD,
PhD, FRCP, FRCP(Edin), Peninsula Medical School (Exeter, UK);
Peter C. Gøtzsche, MD, MSc, The Nordic Cochrane Centre
(Copenhagen, Denmark); Jeremy Grimshaw, MBChB, PhD, FRCFP,
Ottawa Hospital Research Institute (Ottawa, Canada); Gordon Guyatt,
MD, Departments of Medicine, Clinical Epidemiology and Biostatistics,
McMaster University (Hamilton, Canada); Julian Higgins, PhD, MRC
Biostatistics Unit (Cambridge, UK); John P. A. Ioannidis, MD,
University of Ioannina Campus (Ioannina, Greece); Jos Kleijnen,
MD, PhD, Kleijnen Systematic Reviews Ltd (York, UK) and School
for Public Health and Primary Care (CAPHRI), University of
Maastricht (Maastricht, Netherlands); Tom Lang, MA, Tom Lang
Communications and Training (Davis, California, US); Alessandro
Liberati, MD, Universita` di Modena e Reggio Emilia (Modena, Italy)
and Centro Cochrane Italiano, Istituto Ricerche Farmacologiche Mario
Negri (Milan, Italy); Nicola Magrini, MD, NHS Centre for the
Evaluation of the Effectiveness of Health Care – CeVEAS (Modena,
Italy); David McNamee, PhD, The Lancet (London, UK); Lorenzo
Moja, MD, MSc, Centro Cochrane Italiano, Istituto Ricerche Farm-
acologiche Mario Negri (Milan, Italy); David Moher, PhD, Ottawa
Methods Centre, Ottawa Hospital Research Institute (Ottawa, Canada);
Cynthia Mulrow, MD, MSc, Annals of Internal Medicine (Philadelphia,
Pennsylvania, US); Maryann Napoli, Center for Medical Consumers
(New York, New York, US); Andy Oxman, MD, Norwegian Health
Services Research Centre (Oslo, Norway); Ba’ Pham, MMath, Toronto
Health Economics and Technology Assessment Collaborative (Toronto,
Canada) (at the time of the first meeting of the group, GlaxoSmithK-
PLoS Medicine | www.plosmedicine.org 23 July 2009 | Volume 6 | Issue 7 | e1000100
line Canada, Mississauga, Canada); Drummond Rennie, MD, FRCP,
FACP, University of California San Francisco (San Francisco,
California, US); Margaret Sampson, MLIS, Children’s Hospital of
Eastern Ontario (Ottawa, Canada); Kenneth F. Schulz, PhD, MBA,
Family Health International (Durham, North Carolina, US); Paul G.
Shekelle, MD, PhD, Southern California Evidence Based Practice
Center (Santa Monica, California, US); Jennifer Tetzlaff, BSc, Ottawa
Methods Centre, Ottawa Hospital Research Institute (Ottawa, Canada);
David Tovey, FRCGP, The Cochrane Library, Cochrane Collabora-
tion (Oxford, UK) (at the time of the first meeting of the group, BMJ,
London, UK); Peter Tugwell, MD, MSc, FRCPC, Institute of
Population Health, University of Ottawa (Ottawa, Canada).
Dr. Lorenzo Moja helped with the preparation and the several updates
of the manuscript and assisted with the preparation of the reference list.
Alessandro Liberati is the guarantor of the manuscript.
Author Contributions
ICMJE criteria for authorship read and met: AL DGA JT CM PCG JPAI
MC PJD JK DM. Wrote the first draft of the paper: AL DGA JT JPAI
DM. Contributed to the writing of the paper: AL DGA JT CM PCG JPAI
MC PJD JK DM. Concept and design of the Explanation and Elaboration
statement: AL DGA JT DM. Agree with the recommendations: AL DGA
JT CM PCG JPAI MC PJD JK DM.
References
1. Canadian Institutes of Health Research (2006) Randomized controlled trials
registration/application checklist (12/2006). Available: http://www.cihr-irsc.
gc.ca/e/documents/rct_reg_e.pdf. Accessed 26 May 2009.
2. Young C, Horton R (2005) Putting clinical trials into context. Lancet 366:
107–108.
3.MoherD,TetzlaffJ,TriccoAC,SampsonM,AltmanDG(2007)
Epidemiology and reporting characteristics of systematic reviews. PLoS Med
4: e78. doi:10.1371/journal.pmed.0040078.
4. Dixon E, Hameed M, Sutherland F, Cook DJ, Doig C (2005) Evaluating meta-
analyses in the general surgical literature: A critical appraisal. Ann Surg 241:
450–459.
5. Hemels ME, Vicente C, Sadri H, Masson MJ, Einarson TR (2004) Quality
assessment of meta-analyses of RCTs of pharmacotherapy in major depressive
disorder. Curr Med Res Opin 20: 477–484.
6. Jin W, Yu R, Li W, Youping L, Ya L, et al. (2008) The reporting quality of
meta-analyses improves: A random sampling study. J Clin Epidemiol 61:
770–775.
7. Moher D, Simera I, Schulz KF, Hoey J, Altman DG (2008) Helping editors,
peer reviewers and authors improve the clarity, completeness and transparency
of reporting health research. BMC Med 6: 13.
8. Moher D, Cook DJ, Eastwood S, Olkin I, Rennie D, et al. (1999) Improvi ng
the quality of reports of meta-analyses of randomised controlled trials: The
QUOROM statement. Quality of Reporting of Meta-analyses. Lancet 354:
1896–1900.
9. Green S, Higgins JPT, Alderson P, Clarke M, Mulrow CD, et al. (2008)
Chapter 1: What is a systematic review? In: Higgins JPT, Green S, editors.
Cochrane handbook for systematic reviews of interventions version 5.0.0
[updated February 2008]. The Cochrane Collaboration. Available: http://
www.cochrane-handbook.org/. Accessed 26 May 2009.
10. Guyatt GH, Oxman AD, Vist GE, Kunz R, Falck-Ytter Y, et al. (2008)
GRADE: An emerging consensus on rating quality of evidence and strength of
recommendations. BMJ 336: 924–926.
11. Higgins JPT, Altman DG (2008) Chapter 8: Assessing risk of bias in included
studies. In: Higgins JPT, Green S, eds. Cochrane handbook for systematic
reviews of interventions version 5.0.0 [updated February 2008]. The Cochrane
Collaboration, Available: http://www.cochrane-handbook.org/. Accessed 26
May 2009.
12. Moher D, Liberati A, Tetzlaff J, Altman DG, The PRISMA Group (2008)
Preferred reporting items for systematic reviews and meta-analyses: The
PRISMA Statement. PLoS Med 6: e1000097. 10.1371/journal.pmed.1000097.
13. Atkins D, Fink K, Slutsky J (2005) Better informat ion for better health care:
The Evidence-based Practice Center program and the Agency for Healthcare
Research and Quality. Ann Intern Med 142: 1035–1041.
14. Helfand M, Balshem H (2009) Principles for developing guidance: AHRQ and
the effective health-care program. J Clin Epidemiol, In press.
15. Higgins JPT, Green S (200 8) Cochrane handbook for systematic reviews of
interventions version 5.0.0 [updated February 2008]. The Cochrane
Collaboration. Available: http://www.cochrane-handbook.org/. Accessed 26
May 2009.
16. Centre for Reviews and Dissemination (2009) Syst ematic reviews: CRD’s
guidance for undertaking reviews in health care. York: University of York,
Available: http://www.york.ac.uk/inst/crd/systematic_reviews_book.htm. Ac-
cessed 26 May 2009.
17. Altman DG, Schulz KF, Moher D, Egger M, Davidoff F, et al. (2001) The
revised CONSORT statement for reporting randomized trials: Explanation
and elaboration. Ann Intern Med 134: 663–694.
18. Bossuyt PM, Reitsma JB, Bruns DE, Gatsonis CA, Glasziou PP, et al. (2003)
The STARD statement for reporting studies of diagnostic accuracy:
Explanation and elaboration. Clin Chem 49: 7–18.
19. Vandenbroucke JP, von Elm E, Altman DG, Gøtzsche PC, Mulrow CD, et al.
(2007) Strengthening the Reporting of Observational Studies in Epidemiology
(STROBE): Explanation and elaboration. PLoS Med 4: e297. doi:10.1371/
journal.pmed.0040297.
20. Barker A, Maratos EC, Edmonds L, Lim E (2007) Recurrence rates of video-
assisted thoracoscopic versus open surgery in the prevention of recurrent
pneumothoraces: A systematic review of randomised and non-randomised
trials. Lancet 370: 329–335.
21. Bjelakovic G, Nikolova D, Gluud LL, Simonetti RG, Gluud C (2007)
Mortality in randomized trials of antioxidant supplements for primary and
secondary prevention: Systematic review and meta-analysis. JAMA 297:
842–857.
22. Montori VM, Wilczynski NL, Morgan D, Haynes RB (2005) Optimal search
strategies for retrieving systematic reviews from Medline: Analytical survey.
BMJ 330: 68.
23. Bischoff-Ferrari HA, Willett WC, Wong JB, Giovannucci E, Dietrich T, et al.
(2005) Fracture prevention with vitamin D supplementation: A meta-analysis of
randomized controlled trials. JAMA 293: 2257–2264.
24. Hopewell S, Clarke M, Moher D, Wager E, Middleton P, et al. (2008)
CONSORT for reporting randomis ed trials in journal and conference
abstracts. Lancet 371: 281–283.
25. Hopewell S, Clarke M, Moher D, Wager E, Middleton P, et al. (2008)
CONSORT for reporting randomized controlled trials in journal and
conference abst racts: Explanation and elaboration. PLoS Med 5: e20.
doi:10.1371/journal.pmed.0050020.
26. Haynes RB, Mulrow CD, Huth EJ, Altman DG, Gardner MJ (1990) More
informative abstracts revisited. Ann Intern Med 113: 69–76.
27. Mulrow CD, Thacker SB, Pugh JA (1988) A proposal for more informative
abstracts of review articles. Ann Intern Med 108: 613–615.
28. Froom P, Froom J (1993) Deficiencies in structured medical abstracts. J Clin
Epidemiol 46: 591–594.
29. Hartley J (2000) Clarifying the abstracts of systematic literature reviews. Bull
Med Libr Assoc 88: 332–337.
30. Hartley J, Sydes M, Blurton A (1996) Obtaining information accurately and
quickly: Are structured abstract more efficient? J Infor Sci 22: 349–356.
31. Pocock SJ, Hughes MD, Lee RJ (1987) Statistical problems in the reporting of
clinical trials. A survey of three medical journals. N Engl J Med 317: 426–432.
32. Taddio A, Pain T, Fassos FF, Boon H, Ilersich AL, et al. (1994) Qua lity of
nonstructured and structured abstracts of original research articles in the British
Medical Journal, the Canadian Medical Association Journal and the Journal of
the American Medical Association. CMAJ 150: 1611–1615.
33. Harris KC, Kuramoto LK, Schulzer M, Retallack JE (2009) Effect of school-
based physical activity interventions on body mass index in children: A meta-
analysis. CMAJ 180: 719–726.
34. James MT, Conley J, Tonelli M, Manns BJ, MacRae J, et al. (2008) Meta-
analysis: Antibiotics for prophylaxis against hemodialysis catheter-related
infections. Ann Intern Med 148: 596–605.
35. Counsell C (1997) Formulating questions and locating primary studies for
inclusion in systematic reviews. Ann Intern Med 127: 380–387.
36. Gotzsche PC (2000) Why we need a broad perspective on meta-analysis. It may
be crucially important for patients. BMJ 321: 585–586.
37. Grossman P, Niemann L, Schmi dt S, Walach H (2004) Mindfulness-based
stress reduction and health benefits. A meta-analysis. J Psychosom Res 57:
35–43.
38. Brunton G, Green S, Higgins JPT, Kjeldstrøm M, Jackson N, et al. (2008)
Chapter 2: Preparing a Cochrane review. In: Higgins JPT, Green S, eds.
Cochrane handbook for systematic reviews of interventions version 5.0.0
[updated February 2008]. The Cochrane Collaboration, Available: http://
www.cochrane-handbook.org/. Accessed 26 May 2009.
39. Sutton AJ, Abrams KR, Jones DR, Sheldon TA, Song F (1998) Systematic
reviews of trials and other studies. Health Technol Assess 2: 1–276.
40. Ioannidis JP, Rosenberg PS, Goedert JJ, O’Brien TR (2002) Commentary:
Meta-analysis of individual participants’ data in genetic epidemiology.
Am J Epidemiol 156: 204–210.
41. Stewart LA, Clarke MJ (1995) Practical methodology of meta-analyses
(overviews) using updated individual patient data. Cochrane Working Group.
Stat Med 14: 2057–2079.
42. Chan AW, Hrobjartsson A, Haahr MT, Gøtzsche PC, Altman DG (2004)
Empirical evidence for selective reporting of outcomes in randomized trials:
Comparison of protocols to published articles. JAMA 291: 2457–2465.
43. Dwan K, Altman DG, Arnaiz JA, Bloom J, Chan AW, et al. (2008) Systematic
review of the empirical evidence of study publication bias and outcome
reporting bias. PLoS ONE 3: e3081. doi:10.1371/journal.pone.0003081.
PLoS Medicine | www.plosmedicine.org 24 July 2009 | Volume 6 | Issue 7 | e1000100
44. Silagy CA, Middleton P, Hopewel l S (2002) Publishing protocols of systematic
reviews: Comparing what was done to what was planned. JAMA 287:
2831–2834.
45. Centre for Reviews and Dissemination (2009) Research projects. York:
University of York, Available: http://www.crd.york.ac.uk/crdweb. Accessed
26 May 2009.
46. The Joanna Briggs Institute (2009) Protocols & work in progress. Available:
http://www.joannabriggs.edu.au/pubs/systematic_reviews_prot.php. Ac-
cessed 26 May 2009.
47. Bagshaw SM, McAlister FA, Manns BJ, Ghali WA (2006) Acetylcysteine in the
prevention of contrast-induced nephropathy: A case study of the pitfalls in the
evolution of evidence. Arch Intern Med 166: 161–166.
48. Biondi-Zoccai GG, Lotrionte M, Abbate A, Testa L, Remigi E, et al. (2006)
Compliance with QUOROM and quality of reporting of overlapping meta-
analyses on the role of acetylcysteine in the prevention of contrast associated
nephropathy: Case study. BMJ 332: 202–209.
49. Sacks HS, Berrier J, Reitman D, Ancona-B erk VA, Chalmers TC (1987) Meta-
analyses of randomized controlled trials. N Engl J Med 316: 450–455.
50. Schroth RJ, Hitchon CA, Uhanova J, Noreddin A, Taback SP, et al. (2004)
Hepatitis B vaccination for patients with chronic renal failure. Cochrane
Database Syst Rev Issue 3: CD003775. doi:10.1002/14651858.CD003775.
pub2.
51. Egger M, Zellweger-Zahner T, Schneider M, Junker C, Lengeler C, et al.
(1997) Language bias in randomised controlled trials published in English and
German. Lancet 350: 326–329.
52. Gregoire G, Derderian F, Le Lorier J (1995) Selecting the language of the
publications included in a meta-analysis: Is there a Tower of Babel bias? J Clin
Epidemiol 48: 159–163.
53. Ju¨ni P, Holenstein F, Sterne J, Bartlett C, Egger M (2002) Direction and impact
of language bias in meta-analyses of controlled trials: Empirical study.
Int J Epidemiol 31: 115–123.
54. Moher D, Pham B, Klassen TP, Schulz KF, Berlin JA, et al. (2000) What
contributions do languages other than English make on the results of meta-
analyses? J Clin Epidemiol 53: 964–972.
55. Pan Z, Trikalinos TA, Kavvoura FK, Lau J, Ioannidis JP (2 005) Local
literature bias in genetic epidemiology: An empirical evaluation of the Chinese
literature. PLoS Med 2: e334. doi:10.1371/journal.pmed.0020334.
56. Hopewell S, McDonald S, Clarke M, Egger M (2007) Grey literature in meta-
analyses of randomized trials of health care interventions. Cochrane Database
Syst Rev Issue 2: MR000010. doi:10.1002/14651858.MR000010.pub3.
57. Melander H, Ahlqvist-Rastad J, Meijer G, Beermann B (2003) Evidence
b(i)ased medicine—Selective reporting from studies sponsored by pharmaceu-
tical industry: Rev iew of studies in new dr ug applications. BMJ 326:
1171–1173.
58. Sutton AJ, Duval SJ, Tweedie RL, Abrams KR, Jones DR (2000) Empirical
assessment of effect of publication bias on meta-analyses. BMJ 320: 1574–1577.
59. Gotzsche PC (2006) Believability of relative risks and odds ratios in abstracts:
Cross sectional study. BMJ 333: 231–234.
60. Bhandari M, Devereaux PJ, Guyatt GH, Cook DJ, Swiontkowski MF, et al.
(2002) An observational study of orthopaedic abstracts and subsequent full-text
publications. J Bone Joint Surg Am 84-A: 615–621.
61. Rosmarakis ES, Soteriades ES, Vergidis PI, Kasiakou SK, Falagas ME (2005)
From conference abstract to full paper: Differences between data presented in
conferences and journals. Faseb J 19: 673–680.
62. Toma M, McAlister FA, Bialy L, Adams D, Vanderme er B, et al. (2006)
Transition from meeting abstract to full-length journal article for randomized
controlled trials. JAMA 295: 1281–1287.
63. Saunders Y, Ross JR, Broadley KE, Edmonds PM, Patel S (2004) Systematic
review of bisphosphonates for hypercalcaemia of malignancy. Palliat Med 18:
418–431.
64. Shojania KG, Sampson M, Ansari MT, Ji J, Doucette S, et al. (2007) How
quickly do systematic reviews go out of date? A survival analysis. Ann Intern
Med 147: 224–233.
65. Bergerhoff K, Ebrahim S, Paletta G (2004) Do we need to consider ‘in process
citations’ for search strategies? 12th Cochrane Colloquium; 2–6 October 2004;
Ottawa, Ontario, Canada. Available: http://www.cochrane.org/colloquia/
abstracts/ottawa/P-039.htm. Accessed 26 May 2009.
66. Zhang L, Sampson M, McGowan J (2006) Repor ting of the role of expert
searcher in Cochrane reviews. Evid Based Libr Info Pract 1: 3–16.
67. Turner EH, Matthews AM, Linardatos E, Tell RA, Rosenthal R (2008)
Selective publication of antidepressant trials and its influence on apparent
efficacy. N Engl J Med 358: 252–260.
68. Alejandria MM, Lansang MA, Dans LF, Mantaring JB (2002) Intravenous
immunoglobulin for treating sepsis and septic shock. Cochrane Database Syst
Rev Issue 1: CD001090. doi:10.1002/14651858.CD001090.
69. Golder S, McIntosh HM, Duf fy S, Glanville J (2006) Developing efficient
search strategies to identify reports of adverse effects in MEDLINE and
EMBASE. Health Info Libr J 23: 3–12.
70. Sampson M, McGowan J, Cogo E, Grimshaw J, Moher D, et al. (2009) An
evidence-based practice guideline for the peer review of electronic search
strategies. J Clin Epidemiol, E-pub 2009 February 18.
71. Flores-Mir C, Major MP, Major PW (2006) Search and selection methodology
of systematic reviews in orthodontics (2000–2004). Am J Orthod Dentofacial
Orthop 130: 214–217.
72. Major MP, Major PW, Flores-Mir C (2006) An evaluat ion of search and
selection methods used in dental systematic reviews published in English. J Am
Dent Assoc 137: 1252–1257.
73. Major MP, Major PW, Flores-Mir C (2007) Benchmarking of reported search
and selection methods of systematic reviews by dental speciality. Evid Based
Dent 8: 66–70.
74. Shah MR, Hasselblad V, Stevenson LW, Binanay C, O’Connor CM, et al.
(2005) Impact of the pulmonary artery catheter in critically ill patients: Meta-
analysis of randomized clinical trials. JAMA 294: 1664–1670.
75. Edwards P, Clarke M, DiGuiseppi C, Pratap S, Rober ts I, et al. (2002)
Identification of randomized controlled trials in systematic reviews: Accuracy
and reliability of screening records. Stat Med 21: 1635–1640.
76. Cooper HM, Ribble RG (1989) Influences on the outcome of literature
searches for integrative research reviews. Knowledge 10: 179–201.
77. Mistiaen P, Poot E (2006) Telephone follow-up, initiated by a hospital-based
health professional, for postdischarge problems in patients discharged from
hospital to home. Cochrane Database Syst Rev Issue 4: CD004510.
doi:10.1002/14651858.CD004510.pub3.
78. Jones AP, Remmington T, Williamson PR, Ashby D, Smyth RL (2005) High
prevalence but low impact of data extraction and reporting errors were found
in Cochrane systematic reviews. J Clin Epidemiol 58: 741–742.
79. Clarke M, Hopewell S, Juszczak E, Eisinga A, Kjeldstr om M (2006)
Compression stockings for preventing deep vein thrombosis in airline
passengers. Cochrane Database Syst Rev Issue 2: CD004002. doi:10.1002/
14651858.CD004002.pub2.
80. Tramer MR, Reynolds DJ, Moore RA, McQuay HJ (1997) Impact of covert
duplicate publication on meta-analysis: A case study. BMJ 315: 635–640.
81. von Elm E, Poglia G, Walder B, Tramer MR (2004) Different patterns of
duplicate publication: An analysis of articles used in systematic reviews. JAMA
291: 974–980.
82. Gotzsche PC (1989) Multiple publication of reports of drug trials. Eur J Clin
Pharmacol 36: 429–432.
83. Allen C, Hopewell S, Prentice A (2005) Non-steroidal anti-inflammatory drugs
for pain in women with endometriosis. Cochrane Database Syst Rev Issue 4:
CD004753. doi:10.1002/14651858.CD004753.pub2.
84. Glasziou P, Meats E, Heneghan C, Shepperd S (2008) What is missing from
descriptions of treatment in trials and reviews? BMJ 336: 1472–1474.
85. Tracz MJ, Sideras K, Bolona ER, Haddad RM, Kennedy CC, et al. (2006)
Testosterone use in men and its effects on bone health. A systematic revi ew and
meta-analysis of randomized placebo-controlled trials. J Clin Endocrinol Metab
91: 2011–2016.
86. Bucher HC, Hengstler P, Schindler C, Guyatt GH (2000) Percutaneou s
transluminal coronary angioplasty versus medical treatment for non-acute
coronary heart disease: Meta-analysis of randomised controlled trials. BMJ 321:
73–77.
87. Gluud LL (2006) Bias in clinical intervention research. Am J Epidemiol 163:
493–501.
88. Pildal J, Hro´bjartsson A, Jorgensen KJ, Hilden J, Altman DG, et al. (2007)
Impact of allocation concealment on conclusions drawn from meta-analyses of
randomized trials. Int J Epidemiol 36: 847–857.
89. Moja LP, Telaro E, D’Amico R, Moschetti I, Coe L, et al. (2005) Assessment of
methodological quality of primary studies by systematic reviews: Results of the
metaquality cross sectional study. BMJ 330: 1053.
90. Moher D, Jadad AR, Tugwell P (1996) Assessing the quality of randomized
controlled trials. Current issues and future directions. Int J Technol Assess
Health Care 12: 195–208.
91. Sanderson S, Tatt ID, Higgins JP (2007) Tools for assessing quality and
susceptibility to bias in observational studies in epidemiology: A systematic
review and annotated bibliography. Int J Epidemiol 36: 666–676.
92. Greenland S (1994) Invited commentary: A critical look at some popular meta-
analytic methods. Am J Epidemiol 140: 290–296.
93. Ju¨ni P, Altman DG, Egger M (2001) Systematic reviews in health care:
Assessing the quality of controlled clinical trials. BMJ 323: 42–46.
94. Kunz R, Oxman AD (1998) The unpredictabi lity paradox: Review of empirical
comparisons of randomised and non-randomised clinical trials. BMJ 317:
1185–1190.
95. Balk EM, Bonis PA, Moskowitz H, Schmid CH, Ioannidis JP, et al. (2002)
Correlation of quality measures with estimates of treatment effect in meta-
analyses of randomized controlled trials. JAMA 287: 2973–2982.
96. Devereaux PJ, Beattie WS, Choi PT, Badner NH, Guyatt GH, et al. (2005)
How strong is the evidence for the use of perioperative beta blockers in non-
cardiac surgery? Systematic review and meta-analysis of randomised controlled
trials. BMJ 331: 313–321.
97. Devereaux PJ, Bhandari M, Montori VM, Manns BJ, Ghali WA, et al. (2002)
Double blind, you are the weakest link—Good-bye! ACP J Club 136: A11.
98. van Nieuw enhoven CA, Buske ns E, van Tiel FH, Bonten MJ (2001)
Relationship between methodological trial quality and the effects of selective
digestive decontamination on pneumonia and mortality in critically ill patients.
JAMA 286: 335–340.
99. Guyatt GH, Cook D, Devereaux PJ, Meade M, Straus S (2002) Therapy.
Users’ guides to the medical literature. AMA Press. pp 55–79.
100. Sackett DL, Gent M (1979) Controversy in counting and attributing events in
clinical trials. N Engl J Med 301: 1410–1412.
PLoS Medicine | www.plosmedicine.org 25 July 2009 | Volume 6 | Issue 7 | e1000100
101. Montori VM, Devereaux PJ, Adhikari NK, Burns KE, Eggert CH, et al. (2005)
Randomized trials stopped early for benefit: A systematic review. JAMA 294:
2203–2209.
102. Guyatt GH, Devereaux PJ (2002) Therapy and validity: The principle of
intention-to-treat. In: Guyatt GH, Rennie DR, eds. Users’ guides to the
medical literature AMA Press. pp 267–273.
103. Berlin JA (1997) Does blinding of readers affect the results of meta-analyses?
University of Pennsylvania Meta-analysis Blinding Study Group. Lancet 350:
185–186.
104. Jadad AR, Moore RA, Carroll D, Jenkinson C, Reynolds DJ, et al. (1996)
Assessing the quality of reports of randomized clinical trials: Is blinding
necessary? Control Clin Trials 17: 1–12.
105. Pittas AG, Siegel RD, Lau J (2004) Insulin therapy for critically ill hospitalized
patients: A meta-analysis of randomized controlled trials. Arch Intern Med 164:
2005–2011.
106. Lakhdar R, Al-Mallah MH, Lanfear DE (2008) Safety and tolerability of
angiotensin-converting enzyme inhibitor versus the combination of angioten-
sin-converting enzyme inhibitor and angiotensin receptor blocker in patients
with left ventricular dysfunction: A systematic review and meta-analysis of
randomized controlled trials. J Card Fail 14: 181–188.
107. Bobat R, Coovadia H, Stephen C, Naidoo KL, McKerrow N, et al. (2005)
Safety and efficacy of zinc supplementation for children with HIV-1 infection
in South Africa: A randomised double-blind placebo-controlled trial. Lancet
366: 1862–1867.
108. Deeks JJ, Altman DG (2001) Effect measures for meta-analysis of trials with
binary outcomes. In: Egger M, Smith GD, Altman DG, eds. Systematic reviews
in healthcare: Meta-analysis in context. 2nd edition. London: BMJ Publishing
Group.
109. Deeks JJ (2002) Issues in the selection of a summary statistic for meta-analysis of
clinical trials with binary outcomes. Stat Med 21: 1575–1600.
110. Engels EA, Schmid CH, Terrin N, Olkin I, Lau J (2000) Heterogeneity and
statistical significance in meta-analysis: An empirical study of 125 meta-
analyses. Stat Med 19: 1707–1728.
111. Tierney JF, Stewart LA, Ghersi D, Burdett S, Sydes MR (2007) Practical
methods for incorporating summary time-to-event data into meta-analysis.
Trials 8: 16.
112. Michiels S, Piedbois P, Burdett S, Syz N, Stewart L, et al. (2005) Meta-analysis
when only the median survival times are known: A comparison with individual
patient data results. Int J Technol Assess Health Care 21: 119–125.
113. Briel M, Studer M, Glass TR, Bucher HC (2004) Effects of statins on stroke
prevention in patients with and without coronary heart disease: A meta-analysis
of randomized controlled trials. Am J Med 117: 596–606.
114. Jones M, Schenkel B, Just J, Fallowfield L (2004) Epoetin alfa improves quality
of life in patients with cancer: Results of metaanalysis. Cancer 101: 1720–1732.
115. Elbourne DR, Altman DG, Higgins JP, Curtin F, Worthington HV, et al.
(2002) Meta-analyses involving cross-over trials: Methodological issues.
Int J Epidemiol 31: 140–149.
116. Follmann D, Elliott P, Suh I, Cutler J (1992) Variance imputation for overviews
of clinical trials with continuous response. J Clin Epidemiol 45: 769–773.
117. Wiebe N, Vandermeer B, Platt RW, Klassen TP, Moher D, et al. (2006) A
systematic review identifies a lack of standardization in methods for handling
missing variance data. J Clin Epidemiol 59: 342–353.
118. Hrobjartsson A, Gotzsche PC (2004) Placebo interventions for all clinical
conditions. Cochrane Database Syst Rev Issue 2: CD003974. doi:10.1002/
14651858.CD003974.pub2.
119. Shekelle PG, Morton SC, Maglione M, Suttorp M, Tu W, et al. (2004)
Pharmacological and surgical treatment of obesity. Evid Rep Technol Assess
(Summ). pp 1–6.
120. Chan AW, Altman DG (2005) Identifying outcome reporting bias in
randomised trials on PubMed: Review of publications and survey of authors.
BMJ 330: 753.
121. Williamson PR, Gamble C (2005) Identification and impact of outcome
selection bias in meta-analysis. Stat Med 24: 1547–1561.
122. Williamson PR, Gamble C, Altman DG, Hutton JL (2005) Outcome selection
bias in meta-analysis. Stat Methods Med Res 14: 515–524.
123. Ioannidis JP, Trikalinos TA (2007) The appropriateness of asymmetry tests for
publication bias in meta-analyses: A large survey. CMAJ 176: 1091–1096.
124. Briel M, Schwartz GG, Thompson PL, de Lemos JA, Blazing MA, et al. (2006)
Effects of early treatment with statins on short-term clinical outcomes in acute
coronary syndromes: A meta-analysis of randomized controlled trials. JAMA
295: 2046–2056.
125. Song F, Eastwood AJ, Gilbody S, Duley L, Sutton AJ (2000) Publication and
related biases. Health Technol Assess 4: 1–115.
126. Schmid CH, Stark PC, Berlin JA, Landais P, Lau J (2004) Meta-regression
detected associations between heterogeneous treatment effects and study-level,
but not patient-level, factors. J Clin Epidemiol 57: 683–697.
127. Higgins JP, Thompson SG (2004) Controlling the risk of spurious findings from
meta-regression. Stat Med 23: 1663–1682.
128. Thompson SG, Higgins JP (2005) Treating individuals 4: Can meta-analysis
help target interventions at individuals most likely to benefit? Lancet 365:
341–346.
129. Uitterhoeve RJ, Vernooy M, Litjens M, Potting K, Bensing J, et al. (2004)
Psychosocial interventions for patients with advanced cancer—A systematic
review of the literature. Br J Cancer 91: 1050–1062.
130. Fuccio L, Minardi ME, Zagar i RM, Grilli D, Magrini N, et al. (2007) Meta-
analysis: Duration of first-line proton-pump inhibitor based triple therapy for
Helicobacter pylori eradication. Ann Intern Med 147: 553–562.
131. Egger M, Smith GD (1998) Bias in location and selection of studies. BMJ 316:
61–66.
132. Ravnskov U (1992) Cholesterol lowering trials in coronary heart disease:
Frequency of citation and outcome. BMJ 305: 15–19.
133. Hind D, Booth A (2007) Do hea lth technology assessments comply with
QUOROM diagram guidance? An empirical study. BMC Med Res Methodol
7: 49.
134. Curioni C, Andre C (2006) Rimonabant for overweight or obesity. Cochrane
Database Syst Rev Issue 4: CD006162. doi:10.1002/14651858.CD006162.
pub2.
135. DeCamp LR, Byerley JS, Doshi N, Steiner MJ (2008) Use of antiemetic agents
in acute gastroenteritis: A systematic review and meta-analysis. Arch Pediatr
Adolesc Med 162: 858–865.
136. Pakos EE, Ioannidis JP (2004) Radiotherapy vs. nonsteroidal anti-infl ammatory
drugs for the prevention of heterotopic ossification after major hip procedures:
A meta-analysis of randomized trials. Int J Radiat Oncol Biol Phys 60:
888–895.
137. Skalsky K, Yahav D, Bishara J, Pitlik S, Leibovici L, et al. (2008) Treatment of
human brucellosis: Systematic review and meta-analysis of rand omised
controlled trials. BMJ 336: 701–704.
138. Altman DG, Cates C (2001) The need for individual trial results in reports of
systematic reviews. BMJ. Rapid response.
139. Gotzsche PC, Hrobjartsson A, Maric K, Tendal B (2007) Data extraction
errors in meta-analyses that use standardized mean differences. JAMA 298:
430–437.
140. Lewis S, Clarke M (2001) Forest plots: Trying to see the wood and the trees.
BMJ 322: 1479–1480.
141. Papanikolaou PN, Ioannidis JP (2004) Availability of large-scale evidence on
specific harms from systematic reviews of randomized trials. Am J Med 117:
582–589.
142. Duffett M, Choong K, Ng V, Randolph A, Cook DJ (2007) Surfactant therapy
for acute respiratory failure in children: A systematic review and meta-analysis.
Crit Care 11: R66.
143. Balk E, Raman G, Chung M, Ip S, Tatsioni A, et al. (2006) Effectiveness of
management strategies for renal artery stenosis: A systematic review. Ann
Intern Med 145: 901–912.
144. Palfreyman S, Nelson EA, Michaels JA (2007) Dressings for venous leg ulcers:
Systematic review and meta-analysis. BMJ 335: 244.
145. Ioannidis JP, Patsopoulos NA, Evangelou E (2007) Uncertainty in heteroge-
neity estimates in meta-analyses. BMJ 335: 914–916.
146. Appleton KM, Hayward RC, Gunnell D, Peters TJ, Rogers PJ, et al. (2006)
Effects of n-3 long-chain polyunsaturated fatty acids on depressed mood:
Systematic review of published trials. Am J Clin Nutr 84: 1308–1316.
147. Kirsch I, Deacon BJ, Huedo-Medina TB, Scoboria A, Moore TJ, et al. (2008)
Initial severity and antidepressant benefits: A meta-analysis of data submitted to
the Food and Drug Administration. PLoS Med 5: e45. doi:10.1371/
journal.pmed.0050045.
148. Reichenbach S, Sterchi R, Scherer M, Trelle S, Burgi E, et al. (2007) Meta-
analysis: Chondroitin for osteoarthritis of the knee or hip. Ann Intern Med 146:
580–590.
149. Hodson EM, Craig JC, Strippo li GF, Webster AC (2008) Antiviral medications
for preventing cytomegalovirus disease in solid organ transplant recipients.
Cochrane Database Syst Rev Issue 2: CD003774. doi:10.1002/
14651858.CD003774.pub3.
150. Thompson SG, Higgins JP (2002) How should meta-regression analyses be
undertaken and interpreted? Stat Med 21: 1559–1573.
151. Chan AW, Krleza-Jeric K, Schmid I, Altman DG (2004) Outcome reporting
bias in randomized trials funded by the Canadian Institutes of Health
Research. CMAJ 171: 735–740.
152. Hahn S, Williamson PR, Hutton JL, Garner P, Flynn EV (2000) Assessing the
potential for bias in meta-analysis due to selective reporting of subgroup
analyses within studies. Stat Med 19: 3325–3336.
153. Green LW, Glasgow RE (2006) Evaluating the relevance, generalization, and
applicability of research: Issues in external validation and translation
methodology. Eval Health Prof 29: 126–153.
154. Liberati A, D’Amico R, Pifferi, Torri V, Brazzi L (2004) Antibiotic prophylaxis
to reduce respiratory tract infections and mortality in adults receiving intensive
care. Cochrane Database Syst Rev Issue 1: CD00 0022. doi:10.1002/
14651858.CD000022.pub2.
155. Gonzalez R, Zamora J, Gomez-Camarero J, Molinero LM, Banares R, et al.
(2008) Meta-analysis: Combination endoscopic and drug therapy to prevent
variceal rebleeding in cirrhosis. Ann Intern Med 149: 109–122.
156. D’Amico R, Pifferi S, Leonetti C, Torri V, Tinazzi A, et al. (1998) Effectiveness
of antibiotic prophylaxis in critically ill adult patients: Systematic review of
randomised controlled trials. BMJ 316: 1275–1285.
157. Olsen O, Middleton P, Ezzo J, Gotzsche PC, Hadhazy V, et al. (2001) Quality
of Cochrane reviews: Assessment of sample from 1998. BMJ 323: 829–832.
158. Hopewell S, Wolfenden L, Clarke M (2008) Reporting of adverse events in
systematic reviews can be improved: Survey results. J Clin Epidemiol 61:
597–602.
PLoS Medicine | www.plosmedicine.org 26 July 2009 | Volume 6 | Issue 7 | e1000100
159. Cook DJ, Reeve BK, Guyatt GH, Heyland DK, Griffith LE, et al. (1996) Stress
ulcer prophylaxis in critically ill patients. Resolving discordant meta-analyses.
JAMA 275: 308–314.
160. Jadad AR, Cook DJ, Browm an GP (1997) A guide to interpreting discordant
systematic reviews. CMAJ 156: 1411–1416.
161. Clarke L, Clarke M, Clarke T (2007) How useful are Cochrane reviews in
identifying research needs? J Health Serv Res Policy 12: 101–103.
162. [No authors listed] (2000) World Medical Association Declaration of Helsinki:
Ethical principles for medical research involving human subjects. JAMA 284:
3043–3045.
163. Clarke M, Hopewell S, Chalmers I (2007) Reports of clinical trials should begin
and end with up-to-date systematic reviews of other relevant evidence: A status
report. J R Soc Med 100: 187–190.
164. Dube C, Rostom A, Lewin G, Tsertsvadze A, Barrowman N, et al. (2007) The
use of aspirin for primary prevention of colorectal cancer: A systematic review
prepared for the U.S. Preventive Services Task Force. Ann Intern Med 146:
365–375.
165. Critchley J, Bates I (2005) Haemoglo bin colour scale for anaemia diagnosis
where there is no laboratory: A systematic review. Int J Epidemiol 34:
1425–1434.
166. Lexchin J, Bero LA, Djulbegovic B, Clark O (2003) Pharmaceutical industry
sponsorship and research outcome and quality: Systematic review. BMJ 326:
1167–1170.
167. Als-Nielsen B, Chen W, Gluud C, Kjaergard LL (2003) Association of funding
and conclusions in randomized drug trials: A reflection of treatment effect or
adverse events? JAMA 290: 921–928.
168. Peppercorn J, Blood E, Winer E, Partridge A (2007) Association between
pharmaceutical involvement and outcomes in breast cancer clinical trials.
Cancer 109: 1239–1246.
169. Yank V, Rennie D, Bero LA (2007) Financial ties and concordance between
results and conclusions in meta-analyses: Retrospective cohort study. BMJ 335:
1202–1205.
170. Jorgensen AW, Hilden J, Gøtzsche PC (2006) Cochrane reviews compared with
industry supported meta-analyses and other meta-analyses of the same drugs:
Systematic review. BMJ 333: 782.
171. Gotzsche PC, Hrobjartsson A, Johansen HK, Haahr MT, Altman DG, et al.
(2007) Ghost authorship in industry-initiated randomised trials. PLoS Med 4:
e19. doi:10.1371/journal.pmed.0040019.
172. Akbari A, Mayhew A, Al-Alawi M, Grimshaw J, Winkens R, et al. (2008)
Interventions to improve outpatient referrals from primary care to secondary
care. Cochrane Database Syst Rev Issue 2: CD 005471. doi:10.1002/
14651858.CD005471.pub2.
173. Davies P, Boruch R (2001) The Campbell Collaboration. BMJ 323: 294–295.
174. Pawson R, Greenhalgh T, Harvey G, Walshe K (2005) Realist review—A new
method of systematic review designed for complex policy interventions. J Health
Serv Res Policy 10(Suppl 1): 21–34.
175. Greenhalgh T, Robert G, Macfarlane F, Bate P, Kyriakidou O, et al. (2005)
Storylines of research in diffusion of innovation: A meta-narrative approach to
systematic review. Soc Sci Med 61: 417–430.
176. Lumley T (2002) Network meta-analysis for indirect treatment comparisons.
Stat Med 21: 2313–2324.
177. Salanti G, Higgins JP, Ades AE, Ioannidis JP (2008) Evaluation of networks of
randomized trials. Stat Methods Med Res 17: 279–301.
178. Altman DG, Moher D (2005) [Developing guidelines for reporting healthcare
research: Scientific rationale and procedures.]. Med Clin (Barc) 125(Suppl 1):
8–13.
179. Delaney A, Bagshaw SM, Ferland A, Manns B, Laupland KB, et al. (2005) A
systematic evaluation of the quality of meta-analyses in the critical care
literature. Crit Care 9: R575–582.
180. Altman DG, Simera I, Hoey J, Moher D, Schulz K (2008) EQUATOR:
Reporting guidelines for health research. Lancet 371: 1149–1150.
181. Plint AC, Moher D, Morrison A, Schulz K, Altman DG, et al. (2006) Does the
CONSORT checklist improve the quality of reports of randomised controlled
trials? A systematic review. Med J Aust 185: 263–267.
182. Simera I, Altman DG, Moher D, Schulz KF, Hoey J (2008) Guidelines for
reporting health research: The EQUATOR network’s survey of guideline
authors. PLoS Med 5: e139. doi:10.1371/journal.pmed.0050139.
183. Last JM (2001) A dictionary of epidemiology. Oxford: Oxford University Press
& International Epidemiological Association.
184. Antman EM, Lau J, Kupelnick B, Mosteller F, Chalmers TC (1992) A
comparison of results of meta-analyses of randomized control trials and
recommendations of clinical experts. Treatments for myocardial infarction.
JAMA 268: 240–248.
185. Oxman AD, Guyatt GH (1993) The science of reviewing research.
Ann N Y Acad Sci 703: 125–133; discussion 133–124.
186. O’Connor D, Green S, Higgins JPT (2008) Chapter 5: Defining the revi ew
question and developing criteria for including studies. In: Higgins JPT, Green S,
eds. Cochrane handbook for systematic reviews of interventions version 5.0.0
[updated February 2008]. The Cochrane Collaboration, Available: http://
www.cochrane-handbook.org/. Accessed 26 May 2009.
187. McDonagh M, Whiting P, Bradley M, Cooper J, Sutton A, et al. (2000) A
systematic review of public water fluoridation. Protocol changes (Appendix M).
NHS Centre for Reviews and Dissemination. York: University of York,
Available: http://www.york.ac.uk/inst/crd/pdf/appm.pdf. Accessed 26 May
2009.
188. Moher D, Cook DJ, Jadad AR, Tugwell P, Moher M, et al. (1999) Assessing the
quality of reports of randomised trials: Implications for the conduct of meta-
analyses. Health Technol Assess 3: i–iv, 1–98.
189. Devereaux PJ, Choi PT, El-Dika S, Bhandari M, Montori VM, et al. (2004) An
observational study found that authors of ra ndomized controlle d trials
frequently use concealment of randomization and blinding, despite the failure
to report these methods. J Clin Epidemiol 57: 1232–1236.
190. Soares HP, Daniels S, Kumar A, Clarke M, Scott C, et al. (2004) Bad reporting
does not mean bad methods for randomised trials: Observational study of
randomised controlled trials performed by the Radiation Therapy Oncology
Group. BMJ 328: 22–24.
191. Liberati A, Himel HN, Chalmers TC (1 986) A quality assessme nt of
randomized control trials of primary treatment of breast cancer. J Clin Oncol
4: 942–951.
192. Moher D, Jadad AR, Nichol G, Penman M, Tugwell P, et al. (1995) Assessing
the quality of randomized controlled trials: An annotated bibliography of scales
and checklists. Control Clin Trials 16: 62–73.
193. Greenland S, O’Rourke K (2001) On the bias produced by quality scores in
meta-analysis, and a hierarchical view of proposed solutions. Biostatistics 2:
463–471.
194. Ju¨ni P, Witschi A, Bloch R, Egger M (1999) The hazards of scoring the quality
of clinical trials for meta-analysis. JAMA 282: 1054–1060.
195. Fleiss JL (1993) The statistical basis of meta-analysis. Stat Methods Med Res 2:
121–145.
196. Villar J, Mackey ME, Carroli G, Donner A (2001) Meta-analyses in systematic
reviews of randomized controlled trials in perinatal medicine: Comparison of
fixed and random effects models. Stat Med 20: 3635–3647.
197. Lau J, Ioannidis JP, Schmid CH (1998) Summing up evidence: One answer is
not always enough. Lancet 351: 123–127.
198. DerSimonian R, Laird N (1986) Meta-analysis in clinical trials. Control Clin
Trials 7: 177–188.
199. Hunter JE, Schmidt FL (2000) Fixed effects vs. random effects meta-analysis
models: Implications for cumulative research knowledge. Int J Sel Assess 8:
275–292.
200. Deeks JJ, Altman DG, Bradburn MJ (2001) Statistical methods for examining
heterogeneity and combining results from several studies in meta-analysis. In:
Egger M, Davey Smith G, Altman DG, eds. Systematic reviews in healthcare:
Meta-analysis in context. London: BMJ Publishing Group. pp 285–312.
201. Warn DE, Thompson SG, Spiegelhalter DJ (2002) Bayesian random effects
meta-analysis of trials with binary outcomes: Methods for the absolute risk
difference and relative risk scales. Stat Med 21: 1601–1623.
202. Higgins JP, Thompson SG, Deeks JJ, Altman DG (2003) Measuring
inconsistency in meta-analyses. BMJ 327: 557–560.
203. Higgins JP, Thompson SG (2002) Qua ntifying heterogeneity in a meta-
analysis. Stat Med 21: 1539–1558.
204. Huedo-Medina TB, Sanchez-Meca J, Marin-Martinez F, Botella J (2006)
Assessing heterogeneity in meta-analysis: Q statistic or I2 index? Psychol
Methods 11: 193–206.
205. Thompson SG, Turner RM, Warn DE (2001) Multilevel models for meta-
analysis, and their application to absolute risk differences. Stat Methods Med
Res 10: 375–392.
206. Dickersin K (2005) Publication bias: Recognising the problem, understanding
its origin and scope, and preventing harm. In: Rothstein HR, Sutton AJ,
Borenstein M, eds. Publication bias in meta-analysis—Prevention, assessment
and adjustments. West Sussex: John Wiley & Sons. 356 p.
207. Scherer RW, Langenberg P, von Elm E (2007) Full publication of results
initially presented in abstracts. Cochrane Database Syst Rev Issue 2:
MR000005. doi:10.1002/14651858.MR000005.pub3.
208. Krzyzanowska MK, Pintilie M, Tannock IF (2003) Factors associated with
failure to publish large randomized trials presented at an oncology meeting.
JAMA 290: 495–501.
209. Hopewell S, Clarke M (2001) Methodologists and their methods. Do
methodologists write up their conference presentations or is it just 15 minutes
of fame? Int J Technol Assess Health Care 17: 601–603.
210. Ghersi D (2006) Issues in the design, conduct and reporting of clinical trials that
impact on the quality of decision making. PhD thesis. Sydney: School of Public
Health, Faculty of Medicine, University of Sydney.
211. von Elm E, Rollin A, Blumle A, Huwiler K, Witsc hi M, et al. (2008) Publication
and non-publication of clinical trials: Longitudinal study of applications
submitted to a research ethics committee. Swiss Med Wkly 138: 197–203.
212. Sterne JA, Egger M (2001) Funnel plots for detecting bias in meta-analysis:
Guidelines on choice of axis. J Clin Epidemiol 54: 1046–1055.
213. Harbord RM, Egger M, Sterne JA (2006) A modified test for small-study effects
in meta-analyses of controlled trials with binary endpoints. Stat Med 25:
3443–3457.
214. Peters JL, Sutton AJ, Jones DR, Abrams KR, Rushton L (2006) Comparison of
two methods to detect publication bias in meta-analysis. JAMA 295: 676–680.
215. Rothstein HR, Sutton AJ, Borenstein M (2005) Publication bias in meta-
analysis: Prevention, assessment and adjustments. West Sussex: John Wiley &
Sons.
216. Lau J, Ioannidis JP, Terrin N, Schmid CH, Olkin I (2006) The case of the
misleading funnel plot. BMJ 333: 597–600.
PLoS Medicine | www.plosmedicine.org 27 July 2009 | Volume 6 | Issue 7 | e1000100
217. Terrin N, Schmid CH, Lau J (2005) In an empirical evaluation of the funnel
plot, researchers could not visually identify publication bias. J Clin Epidemiol
58: 894–901.
218. Egger M, Davey Smith G, Schneider M, Minder C (1997) Bias in meta-analysis
detected by a simple, graphical test. BMJ 315: 629–634.
219. Ioannidis JP, Trikalinos TA (2007) An exploratory test for an excess of
significant findings. Clin Trials 4: 245–253.
220. Sterne JAC, Egger M, Moher D (2008) Chapter 10: Addressing reporting
biases. In: Higgins JPT, Green S, eds. Cochrane handbook for systematic
reviews of interventions version 5.0.0 [updated February 2008]. The Cochrane
Collaboration, Available: http://www.cochrane-handbook.org/. Accessed 26
May 2009.
PLoS Medicine | www.plosmedicine.org 28 July 2009 | Volume 6 | Issue 7 | e1000100
... Bei der Überprüfung der Eignung bzw. Fallauswahl wurde in Anlehnung an das PRISMA-Modell nachLiberati et al. (2009) verfahren. Da bei der Datenbankrecherche eine Volltextsuche vorgenommen wurde, sorgten vor allem Zeitschriftentitel wie das ,Journal of Education for Sustainable Development' (Sage) oder ,The Learning Organization' (Emerald) über etwaige Literaturhinweise für Begriffsnennungen ohne inhaltlichen Bezug. ...
... Bei der Überprüfung der Eignung bzw. Fallauswahl wurde in Anlehnung an das PRISMA-Modell nach Liberati et al. (2009) verfahren. Da bei der Datenbankrecherche eine Volltextsuche vorgenommen wurde, sorgten vor allem Zeitschriftentitel wie das ,Journal of Education for Sustainable Development' (Sage) oder ,The Learning Organization' (Emerald) über etwaige Literaturhinweise für Begriffsnennungen ohne inhaltlichen Bezug. ...
Article
Full-text available
Zusammenfassung Im Rahmen dieses Beitrags der Zeitschrift Gruppe. Interaktion. Organisation. (GIO) wird eine organisationsforscherische Perspektive auf Bildung für Nachhaltige Entwicklung (BNE) – insbesondere unter Rückgriff auf Konzepte organisationalen Lernens – als analytisch potenzialreich vorgeschlagen. Dazu werden zunächst anhand der Ergebnisse eines (quantifizierenden) systematischen Literaturreviews einige Lücken im BNE-Diskurs aufgezeigt: Insbesondere lassen sich für den Begriff des organisationalen Lernens konzeptionelle Schwächen feststellen, die teilweise der politischen Schwerpunktsetzung der BNE-Programme entsprechen. Hieran anschließend werden theoretische Anknüpfungspunkte und Ergänzungspotenziale einer organisationstheoretisch fundierten Rekonstruktion nachhaltigkeitsbezogener Bildungsprozesse aufgezeigt, um schließlich zusammenfassend für die Erweiterung des BNE-Diskurses durch organisationspädagogische Perspektiven zu plädieren.
... We drew upon the PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-analyses) Statement and PRISMA Checklist as outlined by Liberati et al. (2009) in this review. As per their recommendations, we outline below the parameters of our SLR, and the results of our systematic searches including criteria for inclusion or exclusion. ...
Article
Full-text available
There is growing interest in examining the gendered nature of music practices worldwide. Recent investigations of access to and equity in the music industry have included studies of gender discrimination in classical music, popular music, film music, and within the structure of colonization. This article contributes to this work by reporting the findings of a Systematic Literature Review (SLR) of research that addresses the gendered nature of jazz and improvised music practices in education settings, ensembles, and professional performance environments. Our purpose was to generate an understanding of the phenomenon of gendered jazz and improvised music practices through the following research questions: (1) what is the scope and focus of existing empirical research on gender in jazz and improvised music? (2) where has this research been undertaken, by whom, and to what purpose? (3) what methodological approaches have been employed? (4) how has gender been understood in this research? Findings indicate that research on gender in the jazz and improvisation sector is largely undertaken by women researchers working individually within the Euro-Anglosphere (US, UK, Australia). The majority of studies were undertaken in the qualitative paradigm with autoethnographies, case studies, ethnography, and narrative inquiry as the dominant research approaches. A small number of studies used quantitative or mixed methods with gender as the key variable. By contrast, qualitative studies focused on gendered accounts of working in the jazz and improvisation sector providing deeply personal narratives via artistic research, as illustrations of how larger institutional and societal factors shape the experiences of the individual. Given this personal focus, explicit referencing to theoretical frameworks was de-emphasized in the papers reviewed. Our discussion focuses on the individual and institutional factors that might account for these patterns of research and knowledge production as a way of framing past and present understandings of issues relating to gender in jazz and improvised music. We argue that small-scale qualitative research needs to be supported by larger-scale intersectional investigation into systemic or institutionalized phenomena that investigates how gender marginalization is enabled through these structures. Recommendations for further research, policy and practice are provided.
Article
Background: Girls/women with autism spectrum disorder (ASD) are suggested to exhibit different symptom profiles than boys/men with ASD. Accumulating evidence suggests that intellectual disability (ID) may affect sex/gender differences in ASD. However, a systematic review and meta-analysis on this topic is missing. Methods: Two databases (MEDLINE and PsycINFO) were used to search for studies reporting sex/gender differences (girls/women versus boys/men) in social communication and interaction, restrictive and repetitive behaviour and interests (RRBIs), sensory processing, and linguistic and motor abilities in ASD. The final sample consisted of 79 studies. The meta-analysis was performed with Review Manager using a random-effects model. Participants with ASD without and with ID were analysed as separate subgroups, and the effects in these two subgroups were also compared with each other. Results: Girls/women with ASD without ID displayed fewer RRBIs, more sensory symptoms and less problems in linguistic abilities than their boys/men counterparts. In contrast, girls/women with ASD with ID displayed more social difficulties and RRBIs, poorer linguistic abilities and more motor problems than boys/men with ASD with ID. Comparisons of groups of participants with ASD without ID versus participants with ASD with ID confirmed differences in sex/gender effects on social difficulties, sensory processing, linguistic abilities and motor abilities. Conclusions: Our results clearly suggest that the female phenotype of ASD is moderated by ID. Among individuals with ASD with ID, girls/women seem to be more severely affected than boys/men, whereas among individuals with ASD without ID, girls/women with ASD may have less symptoms than boys/men. Such phenotypic differences could be a potential cause of underrecognition of girls/women with ASD, and it is also possible that observed phenotypic differences may reflect underdiagnosing of girls/women with ASD.