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

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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.
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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
1
Universita
`di Modena e Reggio Emilia, Modena, Italy
2
Centro Cochrane Italiano, Istituto Ricerche Farmacologiche Mario Negri, Milan, Italy
3
Centre for Statistics in Medicine, University of Oxford, Oxford, United Kingdom
4
Ottawa Methods Centre, Ottawa Hospital Research Institute, Ottawa, Ontario, Canada
5
Annals of Internal Medicine, Philadelphia, Pennsylvania, United States of America
6
The Nordic Cochrane Centre, Copenhagen, Denmark
7
Department of Hygiene and Epidemiology, University of Ioannina School of Medicine, Ioannina, Greece
8
UK Cochrane Centre, Oxford, United Kingdom
9
School 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
Accepted 22 June 2009
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 dimin-
ishes their value to clinicians, policy makers, and other users.
Since the development of the QUOROM (QUality OfReporting OfMeta-analysis) Statementda reporting guideline published in
1999dthere 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. Ó2009 The Authors. Published by Elsevier
Inc. All rights reserved.
Abbreviations: PICOS, participants, interventions, comparators,outcomes,
and study design; PRISMA, Preferred Reporting Items for Systematic reviews
and Meta-Analyses; QUOROM, QUality OfReporting OfMeta-analyses.
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,and
BMJ Websites. The authors jointlyhold the copyright of this article. For details
on further use see the PRISMA Web site (http://www.prisma-statement.org/).
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 2006prot. 2006062298).DGA is funded by CancerResearch 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 doc-
uments. Additionally, no funder played a role in drafting the manuscript.
* Corresponding author.
E-mail address:alesslib@mailbase.it (A. Liberati).
0895-4356/09/$ esee front matter Ó2009 The Authors. Published by Elsevier Inc. All rights reserved.
doi: 10.1016/j.jclinepi.2009.06.006
Journal of Clinical Epidemiology 62 (2009) e1ee34
1. 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 start-
ing point for clinical practice guideline developers; provide
summaries of previous research for funders wishing to sup-
port 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
information is often poorly reported in systematic reviews,
thus diminishing their potential usefulness [3e6]. 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 OfRe-
porting OfMeta-analysis) Statement; those detailed report-
ing recommendations were published in 1999 [8]. In this
paper we describe the updating 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 differ-
ent groups of researchers and authors (see Box 1). In this doc-
ument 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, system-
atic methods that are selected to minimize bias, thus providing
reliable findingsfrom which conclusions can be drawn and de-
cisions 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.
2. The QUOROM statement and its evolution
into PRISMA
The QUOROM Statement, developed in 1996 and pub-
lished 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 ex-
panded considerably. For example, The Cochrane Library’s
Methodology Register (which includes reports of studies
relevant to the methods for systematic reviews) now con-
tains 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 [3e6]. 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).
3. Development of PRISMA
The PRISMA Statement was developed by a group of 29
review authors, methodologists, clinicians, medical editors,
and consumers [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 tem-
plate 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 PRIS-
MA 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 docu-
ment, which was circulated and ultimately approved by the
larger PRISMA Group.
4. 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 [13e16].
We developed the PRISMA Statement and this explana-
tory document to help authors report a wide array of system-
atic reviews to assess the benefits and harms of a health care
intervention. We consider most of the checklist items rele-
vant 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
e2 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
studies may need to modify or incorporate additional items
for their systematic reviews.
5. How to use this paper
We modeled this Explanation and Elaboration docu-
ment after those prepared for other reporting guidelines
[17e19]. 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 pub-
lished 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 perti-
nent issue, the rationale for including the item, and relevant
evidence from the literature, whenever possible. No sys-
tematic 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 trans-
parency of the review process. We present the items numer-
ically 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.
6. The PRISMA checklist
Item 1: Title
Identify the report as a systematic review, meta-analysis,
or both.
Examples. ‘Recurrence rates of video-assisted thor-
acoscopic versus open surgery in the prevention of
recurrent pneumothoraces: a systematic review of
randomised and non-randomised trials’’ [20]
‘Mortality in randomized trials of antioxidant sup-
plements for primary and secondary prevention:
systematic review and meta-analysis’’ [21]
Explanation. Authors should identify their report as a sys-
tematic 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
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 reproducible 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 differ-
ences across the included 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 editionof 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) system-
atic presentation, and synthesis, of the characteristics and findings of the included studies.
e3A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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 ofidentified 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.
e4 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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, outcomes, and study design) (see Item 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 indi-
cate 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 oversim-
plify or exaggerate findings. Thus, many journals and
methodologists prefer indicative titles as used in the exam-
ples above.
Item 2: Structured summary
Provide a structured summary including, as applicable:
background; objectives; data sources; study eligibility crite-
ria, participants, and interventions; study appraisal and
synthesis methods; results; limitations; conclusions and im-
plications of key findings; funding for the systematic review;
and systematic review registration number.
Example. ‘‘Context: The role and dose of oral vita-
min 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
fractures in older persons.
Data Sources: A systematic review of English and
non-English articles using MEDLINE and the Co-
chrane Controlled Trials Register (1960-2005), and
EMBASE (1991-2005). Additional studies were iden-
tified by contacting clinical experts and searching
bibliographies and abstracts presented at the Ameri-
can Society for Bone and Mineral Research (1995-
2004). Search terms included randomized controlled
trial (RCT), controlled clinical trial, random alloca-
tion, double-blind method, cholecalciferol, ergocalci-
ferol, 25-hydroxyvitamin D, fractures, humans,
elderly, falls, and bone density.
Study Selection: Only double-blind RCTs of oral vi-
tamin D supplementation (cholecalciferol, ergocalci-
ferol) with or without calcium supplementation vs
calcium supplementation or placebo in older persons
(O60 years) that examined hip or nonvertebral frac-
tures were included.
Data Extraction: Independent extraction of articles
by 2 authors using predefined data fields, including
study quality indicators.
# of records identified through
database searching
# of additional records
identified through other sources
# of records after duplicates removed
# of records screened # of records excluded
# of full-text articles
assessed for eligibility
# of studies included in
qualitative synthesis
# of full-text articles
excluded, with reasons
# of studies included in
quantitative synthesis
(meta-analysis)
IdentificationScreeningEligibility
Included
Fig. 1. Flow of information through the different phases of a systematic review.
e5A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
Data Synthesis: All pooled analyses were based on
random-effects models. Five RCTs for hip fracture
(n 59294) and 7 RCTs for nonvertebral fracture risk
(n 59820) met our inclusion criteria. All trials used
cholecalciferol. Heterogeneity 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 pre-
vention.’[23]
Explanation. Abstracts provide key information that en-
ables readers to understand the scope, processes, and find-
ings of a review and to decide whether to read the full
report. The abstract may be all that is readily available to
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 consum-
ing. 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 interven-
tions (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 report-
ing what the intervention is compared with is very important and may sometimes have implications for the inclusion of
studies in a reviewdmany reviews compare with ‘‘standard care,’’ which is otherwise undefined; this should be prop-
erly addressed by authors.
The outcomes of the intervention 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].
e6 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
a reader, for example, in a bibliographic database. The ab-
stract 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 publica-
tions needs improvement [24,25]. While we do not uni-
formly favor a specific format over another, we generally
recommend structured abstracts. Structured abstracts pro-
vide readers with a series of headings pertaining to the pur-
pose, 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 [28e32].
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). Alterna-
tively, 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
aData 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 inclu-
sion 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 im-
portant outcomes. Ideally, they should specify the amount
of evidence in these analyses (numbers of studies and num-
bers 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 au-
thors 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. Therefore, 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 sup-
ported 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 interventions can be improved. Con-
sequently, many local governments have enacted or
are considering policies that mandate increased phys-
ical activity in schools, although the effect of such
interventions on body composition has not been
assessed.’[33]
Explanation. Readers need to understand the rationale be-
hind 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 inter-
ventions 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).
Example. ‘‘To examine whether topical or intralumi-
nal antibiotics reduce catheter-related bloodstream
infection, we reviewed randomized, controlled trials
e7A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
that assessed the efficacy of these antibiotics for pri-
mary prophylaxis against catheter-related bloodstream
infection and mortality compared with no antibiotic
therapy in adults undergoing hemodialysis.’[34]
Explanation. The questions being addressed, and the ratio-
nale 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 re-
view 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 end-
point 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 nar-
rowly 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-spec-
ifies the objectives and methods of the systematic review.
For instance, a protocol specifies outcomes of primary inter-
est, how reviewers will extract information about those out-
comes, 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 out-
come reporting. Several sources provide guidance about ele-
ments 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 participat-
ing collaborators endorsed it [40,41].
Authors may modify protocols during the research, and
readers should not automatically consider such modifications
inappropriate. 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 com-
mon, one must consider the effects that protocol modifica-
tions 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 (n543)
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 [45e48], reduce publication bias, and
provide greater transparency when updating systematic re-
views. Of note, a survey of systematic reviews indexed in
MEDLINE in November 2004 found that reports of pro-
tocol 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 characteristics (e.g., PICOS, length of
follow-up) and report characteristics (e.g., years consid-
ered, language, publication status) used as criteria for eligi-
bility, giving rationale.
Examples. Types of studies: ‘‘Randomised clinical
trials studying the administration of hepatitis B vac-
cine 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 perito-
neal 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 pre-
vent rejection of their transplanted organs, and they
have essentially normal renal function.’’
e8 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
Types of intervention: ‘‘Trials comparing the beneficial
and harmful effects of hepatitis B vaccines with adju-
vant or cytokine co-interventions [and] trials comparing
the beneficial 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 reg-
imens versus placebo, control vaccine, or no vaccine.’’
Types of outcome measures: ‘‘Primary outcome mea-
sures: Seroconversion, ie, proportion of patients with
adequate anti-HBs response (O10 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 in-
fections 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].mortal-
ity.[50]
Explanation. Knowledge of the eligibility criteria is es-
sential in appraising the validity, applicability, and compre-
hensiveness of 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 devel-
opment of the search strategy and serve to ensure that stud-
ies 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 sepa-
rate 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 mini-
mum 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 [51e55],unpublished
data, or older data can influence the effect estimates in meta-
analyses [56e59]. Cautionmay need to be exercised in includ-
ing all identified studies due to potential differences in the risk
of bias such as, for example, selective reporting in abstracts
[60e62].
Item 7: Information Sources
Describe all information sources in the search (e.g., data-
bases with dates of coverage, contact with study authors to
identify additional studies) and date last searched.
Example. ‘‘Studies were identified by searching elec-
tronic databases, scanning reference lists of articles
and consultation 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 MED-
LINE database is one of the most comprehensive sources of
health care information in the world. Like any database, how-
ever, its coverage is not complete and varies according to the
field. Retrieval from any single database, even by an experi-
enced searcher, may be imperfect, which is why detailed re-
porting 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, search-
ing trials registries or regulatory agency Web sites [67],con-
tacting manufacturers, or contacting authors. Authors should
also report if they attempted to acquire any missing informa-
tion (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:
e9A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
immunoglobulin*; IVIG; sepsis; septic shock; septi-
caemia; 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 comprehensiveness and completeness of the search, and to
replicate it. Thus, we advise authors to report their full elec-
tronic search strategy for at least one major database. As an al-
ternative 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 ques-
tion (e.g., questions relating to benefits and questions relating
to harms), we recommend authors provide at least one exam-
ple of a strategy for each part of the objective [69].Wealsoen-
courage 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., repli-
cate 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 data-
base searching skills, or review questions for which perti-
nent 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
independently 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
e10 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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 peo-
ple, who these people were, and, whenever multiple inde-
pendent investigators performed 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 pro-
cesses 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 accordingly. One review author extracted the follow-
ing 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 onlybeen presented graphically
in the published paper.’[77]
Explanation. Reviewers extract information from each in-
cluded study so that they can critique, present, and summa-
rize 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. Regard-
less, 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 indepen-
dently and how disagreements were resolved.
Published reports of the included studies may not pro-
vide all the information required for the review. Reviewers
should describe any actions they took to seek additional in-
formation 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 to-
gether data from multiple reports of the same study (e.g., jux-
taposing 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 multi-
ple 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]. Authors ide-
ally 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 in-
cluded trial on: (1) characteristics of trial participants
(including age, stage and severity of disease, and
method of diagnosis), and the trial’s inclusion and exclu-
sion criteria; (2) type of intervention (including type,
dose, duration and frequency of the NSAID [non-steroi-
dal 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 (in-
cluding 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]
e11A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
Explanation. It is important for readers to know what in-
formation review authors sought, even if some of this infor-
mation 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 ob-
tained, 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 descrip-
tion 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 identi-
fied (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 ex-
ample, 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 indi-
vidual 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.
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 systematic
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’’ phenomenon, 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 independently, whether ‘‘consensus’’data were used in the analyses, and if the
review team completed an informal training exercise or a more formal reliability exercise.
e12 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
Example. ‘‘To ascertain the validity of eligible ran-
domized trials, pairs of reviewers working indepen-
dently and with adequate reliability determined the
adequacy of randomization and concealment of alloca-
tion, 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 in-
vestigators were not able to ascertain outcomes).’[85]
‘‘To explore variability in study results (heterogeneity)
we specified the following hypotheses before conduct-
ing 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 re-
ported in a systematic review approximates the truth de-
pends on the validity of the included studies, as certain
methodological characteristics may be associated with ef-
fect sizes [87,88]. For example, trials without reported ad-
equate 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 popu-
lar term to describe the issues relevant to this item is ‘‘qual-
ity,’ 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 individ-
ual 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 methodological components that
they assessed. Common markers of validity for randomized
trials include the following: appropriate generation of
random allocation sequence [94]; concealment of the allo-
cation sequence [93]; blinding of participants, health care
providers, data collectors, and outcome adjudicators
[95e98]; 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 princi-
ple [100,102]. The ultimate decision regarding which meth-
odological 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 ex-
clude 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 inten-
tion-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 differ-
ence in log
10
HIV-1 viral load comparing zinc supple-
mentation to placebo.’’ [107]
Explanation. When planning a systematic review, it is gen-
erally desirable that authors pre-specify the outcomes of pri-
mary 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 mea-
sures 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
e13A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
[111]. Risk ratio and odds ratio (in relation to events occur-
ring 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 consis-
tency (e.g., I
2
) for each meta-analysis.
Examples. ‘‘We tested for heterogeneity with the Bre-
slow-Day test, and usedthe method proposedby 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 re-
view may need some transformation (processing) before they
are suitable for analysis or for presentation in an evidence ta-
ble. Although such data handling may facilitate meta-analy-
ses, 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 interven-
tions), 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 re-
constructed from other statistics such as p-values and tstatis-
tics [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
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 evidence [194]. Checklists are less fre-
quently 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 effectiveness in randomized trials (sequence generation, allocation concealment, blind-
ing, 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.
e14 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
a consistent format [111]. Authors should report details of
any such data processing.
Statistical combination of data from two or more sepa-
rate 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 variabil-
ity (heterogeneity or inconsistency) (Box 6). The consis-
tency 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 publica-
tion of small trials with negative results.Because
graphical evaluation can be subjective, we also con-
ducted an adjusted rank correlation test and a regression
asymmetry test as formal statistical tests for publication
bias.We acknowledge that other factors, such as dif-
ferences in trial quality or true study heterogeneity,
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 re-
porting is present in a systematic review. If a protocol of an in-
dividual study is available, the outcomes in the protocol and the
published report canbe compared. Evenin the absence of a pro-
tocol, outcomes listed in the methods section of the published
report can be compared with those for which results are pre-
sented [120]. In only half of 196 trial reports describing com-
parisons oftwo 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 outcomewas measured even if it was not reported. For ex-
ample, in a particular disease, if one oftwo 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
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 as-
sessments were reported, most were based on fewer than ten
studies; most displayed statistically significant heterogene-
ity; 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 es-
timates 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 ro-
bust, 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 individ-
ual 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 clini-
cal) characteristics of the included studies or their partici-
pants. 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 un-
dertaken. The choice of which analysis to undertake will de-
pend on the aims of the review. None of these analyses,
however, are exempt from producing potentially misleading re-
sults. It is important to inform readers whether these analyses
were performed, their rationale, and which were pre-specified.
e15A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
Results
Item 17: Study selection
Give numbers of studies screened, assessed for eligibil-
ity, 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 identi-
fied for inclusion in the review. The search of Med-
line, PsycInfo and Cinahl databases provided a total
of 584 citations. After adjusting for duplicates 509
remained. Of these, 479 studies were discarded be-
cause 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 in-
clusion criteria as described. Five studies.met the
inclusion criteria and were included in the systematic
review. An additional five studies.that met the crite-
ria for inclusion were identified by checking the
references of located, relevant papers and searching
for studies that have cited these papers. No unpub-
lished 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 da-
tabase or registry searches), hand searches of various sour-
ces, reference lists, citation indices, and experts. It is useful
if authors delineate for readers the number of selected arti-
cles that were identified from the different sources so that
they can see, for example, whether most articles were iden-
tified through electronic bibliographic sources or from ref-
erences or experts. Literature identified primarily from
references or experts may be prone to citation or publica-
tion bias [131,132].
The flow diagram and text should describe clearly the pro-
cess of report selection throughout the review. Authors should
report: unique records identifiedin searches; records excluded
after preliminary screening (e.g., screening of titles and ab-
stracts); 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 ex-
clusion; and the studies included in the review. Indeed, the
most appropriate layout may vary for different reviews.
Authors should also note the presence of duplicate or sup-
plementary 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 be-
lieve 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 sta-
tistical analysis. A recent review of 87 systematic re-
views found that about half included a QUOROM flow
diagram [133]. The authors of this research recommen-
ded some important ways that reviewers can improve
Box 5. Whether or Not To Combine Data
Deciding whether or not to combine data involves statistical, clinical, and methodological considerations. The sta-
tistical 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 comor-
bid 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.
e16 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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 re-
ported [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
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 out-
comes (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 DerSimonian
and Laird approach, although other methods exist, including Bayesian meta-analysis [201].
In the presence of demonstrable between-study heterogeneity (see below), some consider that the use of a fixed-ef-
fect analysis is counterintuitive because their main assumption is violated. Others argue that it is inappropriate to con-
duct 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 somevariation (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 sta-
tistical 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 var-
iation in results across studies beyond that expected by chance and so is preferable to Q [202,203].I
2
represents the per-
centage 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].
e17A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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
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 sum-
marized as ‘‘publication bias’’ although in fact the bias arises from non-publication of full studies and selective pub-
lication 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
pO0.05 [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 ad-
dition, 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. Sta-
tistically significant outcomes had a higher odds of being fully reported in publications when compared with non-sig-
nificant 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 fun-
nel plot [212], and analytic methods (e.g., Egger’s test) are often used [213e215], although their interpretation can
be problematic [216,217]. Strictly speaking, such analyses investigate ‘‘small study bias’’; there may be many rea-
sons 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 es-
timated effects than large ones may suggest the possibility that the available evidence is biased, misinterpretation
of such data is common [123].
e18 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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 Eu-
rope and the USA, RIO-Diabetes in the USA and 10 other
different countries not specified, and RIO-Lipids in eight
unspecified different countries.
The intervention received was placebo, 5 mg of rimo-
nabant 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
Fig. 2. Example Figure: Example flow diagram of study selection. DDW, Digestive Disease Week; UEGW, United European Gastroenterology Week.
Reproduced with permission from [130].
e19A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
prevention of weight regain between the first and sec-
ond year. All studies evaluated adverse effects, includ-
ing 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 appli-
cability of a systematic review’s results, they need to
know something about the included studies. Such informa-
tion includes PICOS (Box 2) and specific information rel-
evant 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 in-
cluded 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 re-
view. Authors should present enough detail to allow readers
to make their own judgments about the relevance of in-
cluded 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 in-
formation 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 system-
atic review. If this information is not obtained, this should
be noted in the report. If information is imputed, the
reader 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 pub-
lic 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 miss-
ing 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 omis-
sion of important aspects of the methods or results of in-
cluded studies, since these can, if necessary, be shown on
a Web site.
Following the presentation and description of each in-
cluded study, as discussed above, reviewers usually provide
a narrative summary of the studies. Such a summary pro-
vides readers with an 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-pharmacological interventions, it may be
helpful to specify for each study the key elements of the
intervention received by each group. Full details of the in-
terventions 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 meth-
odological shortcoming. A more informative approach is to
explicitly report the methodological features evaluated for
each study. The Cochrane Collaboration’s new tool for as-
sessing 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 tabu-
lar 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), pres-
ent, for each study: (a) simple summary data for each inter-
vention 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 individ-
ual studies allows the analyses to be reproduced and other
e20 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
analyses and graphical displays to be investigated. Others
may wish to assess the impact of excluding particular stud-
ies or consider subgroup analyses not reported by the re-
view authors. Displaying the results of each treatment
group in included studies also enables inspection of indi-
vidual 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 er-
rors 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 examine the consistency of standard
deviations across studies, for example, to be reassured that
standard deviation and standard error have not been con-
fused [138].
For each study, the summary data for each intervention
group are generally given for binary outcomes as frequen-
cies with and without the event (or as proportions such as
12/45). It is not sufficient to report event rates per interven-
tion 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 informa-
tion may be incorporated in a table showing study charac-
teristics 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 pro-
vided for every outcome considered in the review, includ-
ing 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 pro-
tocol. Authors should explicitly mention if the planned
main outcomes cannot be presented due to lack of
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 e10 years GE with mild to moderate dehydration and
vomiting in the preceding 4 hours
Ondansetron PO 1e2 weeks
Reeves et al., 2002 ED 107 1 month e22 years GE and vomiting requiring IV rehydration Ondansetron IV 5e7 days
Roslund et al., 2007 ED 106 1e10 years GE with failed oral rehydration attempt in ED Ondansetron PO 1 week
Stork et al., 2006 ED 137 6 months e12 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].
e21A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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 mea-
sures of consistency.
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 ran-
domizing 232 patients, 64 of whom died. In the
pooled analysis, surfactant was associated with sig-
nificantly lower mortality (relative risk 50.7,
95% confidence interval 50.4e0.97, P 50.04).
There was no evidence of heterogeneity (I
2
50%)’’.
[142]
‘‘Because the study designs, participants, interven-
tions, 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 com-
parison (I
2
546.6%; c
2
513.11, df 57; P 50.07).
Retrospective exploration of the heterogeneity identi-
fied one trial that seemed to differ from the others. It in-
cluded only small ulcers (wound area less than 5 cm
2
).
Exclusion of this trial removed the statistical heteroge-
neity and did not affect the finding of no evidence of
a difference in healing rate between hydrocolloids and
simple low adherent dressings (relative risk50.98,
[95% confidence interval] 0.85 to 1.12; I
2
50%).[144]
Explanation. Results of systematic reviews should be pre-
sented 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 facili-
tate the examination of patterns across studies. They may also
provide important information about applicability of evi-
dence, suggest the likely effects of any major biases, and allow
consideration, in a systematic manner, of multiple explana-
tions 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 con-
tributed 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
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].
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].
e22 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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 out-
comes. 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 incon-
sistency 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
579%, 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 report-
ing mean HRSD [Hamilton Rating Scale for Depres-
sion] 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. Anal-
yses 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
Fig. 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].
Fig. 4. Example Figure: Example of a funnel plot showing evidence of con-
siderable asymmetry. SE,standard error. Adaptedfrom [146], with permission.
e23A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
sertraline and citalopram trials for which means were
reported to the FDA would constitute a form of re-
porting bias similar to publication bias and would
lead to overestimation of drugeplacebo 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 as-
sessments 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 pos-
sible asymmetry (see Item 15). Results of any investiga-
tions of selective reporting of outcomes within studies (as
discussed in Item 15) should also be reported. Also, we ad-
vise 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., sensi-
tivity or subgroup analyses, meta-regression [see Item 16]).
Examples. ‘‘.benefits of chondroitin were smaller in
trials with adequate concealment of allocation com-
pared with trials with unclear concealment (P for inter-
action 50.050), in trials with an intention-to-treat
analysis compared with those that had excluded
patients from the analysis (P for interaction 50.017),
and in large compared with small trials (P for interac-
tion 50.022).’[148]
‘‘Subgroup analyses according to antibody status,
antiviral medications, organ transplanted, treatment
duration, use of antilymphocyte therapy, time to out-
come assessment, study quality and other aspects of
study design did not demonstrate any differences in
treatment effects. Multivariate meta-regression
showed no significant difference in CMV [cytomega-
lovirus] disease after allowing for potential confound-
ing 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 sen-
sitivity 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 aspi-
rin), the authors should report any tests for interactions, as
well as estimates and confidence intervals from meta-anal-
yses within each subgroup. Similarly, meta-regression re-
sults (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 sensi-
tivity 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 report-
ing bias within the review as has been demonstrated in re-
ports of randomized controlled trials [42,44,121,151,152].
Results from exploratory subgroup or sensitivity analyses
should be interpreted cautiously, bearing in mind the poten-
tial 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 suffi-
cient duration to allow definitive conclusions to be
made about clinical outcomes, such as mortality and
cardiovascular or kidney failure events.
Some acceptable evidence from comparison of med-
ical treatment and angioplasty suggested no differ-
ence 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 re-
viewed studies did not explicitly address patients with
rapid clinical deterioration who may need acute inter-
vention, our conclusions do not apply to this impor-
tant subset of patients.’[143]
Explanation. Authors should give a brief and balanced
summary of the nature and findings of the review. Some-
times, outcomes for which little or no data were found
should be noted due to potential relevance for policy deci-
sions 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
e24 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
standard way to assess applicability simultaneously to dif-
ferent 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].
Authors need to keep in mind that statistical significance
of the effects does not always suggest clinical or policy rel-
evance. Likewise, a non-significant result does not demon-
strate 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 set-
tings 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 organiza-
tional 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 asymmetrical funnel plot suggests that selec-
tive 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 limita-
tions 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 popula-
tions, and interventions may hamper interpretation and
synthesis of the included studies [84]. Applicability 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 com-
parator 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 con-
text 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 effec-
tiveness of the treatment. Only one among the five
available reviews, however, suggested that a weak as-
sociation between respiratory tract infections and mor-
tality 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 sys-
temic 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 en-
rolled (n 51056) 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 rel-
evant issue of treatment induced resistance. To produce
a satisfactory answer to this, studies with a different de-
sign would be necessary. Though a detailed discussion
e25A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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 occur-
rence of antibiotic resistance is monitored over a long
period of time should be undertaken.’[156]
Explanation. Systematic reviewers sometimes draw con-
clusions 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 find-
ing 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 re-
sults. 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 recommenda-
tions for future research. In a sample of 2,535 Cochrane re-
views, 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 assess-
ment about systematic reviews published in medical jour-
nals, 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 that this still does not occur as it should and that au-
thors of primary studies do not consider a systematic review
when they design their studies [163]. We believe systematic re-
views have great potential for guiding future clinical research.
Funding
Item 27: Funding
Describe sources of funding or other support (e.g., sup-
ply 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 fund-
ing issues, authors should report any real or perceived con-
flicts 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 stud-
ies, 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 liter-
ature 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 use-
ful principle is for systematic review authors to ensure that
their methods are reported with adequate clarity and trans-
parency 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 sum-
mary statistics. These systematic reviews are called individ-
ual patient (or participant) data reviews [40,41]. Individual
e26 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
patient data meta-analyses may also be conducted with pro-
spective 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].Net-
work meta-analyses, also known as multiple treatments
meta-analyses, can be used to analyze data from compar-
isons of many different treatments [176,177].Theyuse
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 understand-
ing 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 epidemiologi-
cal studies.
8. Discussion
We developed the PRISMA Statement using an
approach for developing reporting guidelines that has
evolved over several years [178]. The overall aim of PRIS-
MA is to help ensure the clarity and transparency of report-
ing 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 dissemination of the PRISMA Statement and hope-
fully provide a pedagogical framework for those interested
in conducting and reporting systematic reviews. It follows
a format similar to that used in other explanatory docu-
ments [17,18,19]. Following the recommendations in the
PRISMA checklist may increase the word count of a sys-
tematic review report. We believe, however, that the ben-
efit 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 com-
pleted [178]. Publication of the QUOROM Statement was
delayed for two years while a research team attempted to
evaluate its effectiveness by conducting a randomized con-
trolled trial with the participation of eight major medical
journals. Unfortunately that trial was not completed due
to accrual problems (David Moher, personal communica-
tion). Other evaluation 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.
If the PRISMA Statement is endorsed by and adhered to
in journals, as other reporting guidelines have been
[17e19,180], 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 system-
atic 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 limita-
tion 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 neces-
sary to appraise the reliability of a review. To keep PRIS-
MA up-to-date and as evidence-based as possible requires
regular vigilance of the literature, which is growing rapidly.
Currently the Cochrane Methodology 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 else-
where 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 develop-
ment 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 re-
views are increasingly used by health care providers to in-
form ‘‘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 consider-
able effort, experience, and expertise. While reporting
e27A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
guidelines have been successful for some individual efforts
[17e19], 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 main-
taining a resource center of reporting tools, and other
infor-mation 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 en-
dorsed 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 aware-
ness through specific editorial actions.
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 (Cam-
bridge, 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’Ami-
co, 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 Biostatis-
tics 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, Nether-
lands); 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 Magri-
ni, MD, NHS Centre for the Evaluation of the Effectiveness
of Health Care eCeVEAS (Modena, Italy); David McNa-
mee, PhD, The Lancet (London, UK); Lorenzo Moja, MD,
MSc, Centro Cochrane Italiano, Istituto Ricerche Farmaco-
logiche Mario Negri (Milan, Italy); David Moher, PhD,
Ottawa Methods Centre, Ottawa Hospital Research Insti-
tute (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, GlaxoSmithKline Canada,
Mississauga, Canada); Drummond Rennie, MD, FRCP,
FACP, University of California San Francisco (San Francis-
co, 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, Cana-
da); David Tovey, FRCGP, The Cochrane Library,
Cochrane Collaboration (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.
Supporting data
Supporting data associated with this article can be
found, in the online version, at doi:10.1016/j.jclinepi.
2009.06.006.
e28 A. Liberati et al. / Journal of Clinical Epidemiology 62 (2009) e1ee34
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