Academia and Clinic
`
`The Revised CONSORT Statement for Reporting Randomized Trials:
`Explanation and Elaboration
`
`Douglas G. Altman, DSc; Kenneth F. Schulz, PhD; David Moher, MSc; Matthias Egger, MD; Frank Davidoff, MD; Diana Elbourne, PhD;
`Peter C. Gøtzsche, MD; and Thomas Lang, MA, for the CONSORT Group
`
`Overwhelming evidence now indicates that the quality of report-
`ing of randomized, controlled trials (RCTs) is less than optimal.
`Recent methodologic analyses indicate that inadequate reporting
`and design are associated with biased estimates of treatment
`effects. Such systematic error is seriously damaging to RCTs,
`which boast the elimination of systematic error as their primary
`hallmark. Systematic error in RCTs reflects poor science, and poor
`science threatens proper ethical standards.
`A group of scientists and editors developed the CONSORT
`(Consolidated Standards of Reporting Trials) statement to improve
`the quality of reporting of RCTs. The statement consists of a
`checklist and flow diagram that authors can use for reporting an
`RCT. Many leading medical journals and major international edi-
`torial groups have adopted the CONSORT statement. The CON-
`SORT statement facilitates critical appraisal and interpretation of
`RCTs by providing guidance to authors about how to improve the
`
`reporting of their trials.
`This explanatory and elaboration document is intended to
`enhance the use, understanding, and dissemination of the CON-
`SORT statement. The meaning and rationale for each checklist
`item are presented. For most items, at least one published exam-
`ple of good reporting and, where possible, references to relevant
`empirical studies are provided. Several examples of flow diagrams
`are included.
`The CONSORT statement, this explanatory and elaboration
`document, and the associated Web site (http://www.consort
`-statement.org) should be helpful resources to improve reporting
`of randomized trials.
`
`Ann Intern Med. 2001;134:663-694.
`
`www.annals.org
`
`For author affiliations and current addresses, see end of text.
`
`The RCT is a very beautiful technique, of wide appli-
`cability, but as with everything else there are snags.
`When humans have to make observations there is
`always the possibility of bias (1).
`
`Well-designed and properly executed randomized,
`
`controlled trials (RCTs) provide the best evi-
`dence on the efficacy of health care interventions*, but
`trials with inadequate methodologic approaches are as-
`sociated with exaggerated treatment effects (2–5). Bi-
`ased* results from poorly designed and reported trials
`can mislead decision making in health care at all levels,
`from treatment decisions for the individual patient to
`formulation of national public health policies.
`Critical appraisal of the quality of clinical trials is
`possible only if the design, conduct, and analysis of
`RCTs are thoroughly and accurately described in pub-
`lished articles. Far from being transparent, the reporting
`of RCTs is often incomplete (6 –9), compounding prob-
`lems arising from poor methodology (10 –15).
`
`INCOMPLETE AND INACCURATE REPORTING
`Many reviews have documented deficiencies in re-
`ports of clinical trials. For example,
`information on
`
`Throughout the text, terms marked with an asterisk are defined at end of text.
`
`whether assessment of outcomes* was blinded was re-
`ported in only 30% of 67 trial reports in four leading
`journals in 1979 and 1980 (16). Similarly, only 27% of
`45 reports published in 1985 defined a primary end
`point* (14), and only 43% of 37 trials with negative
`findings published in 1990 reported a sample size* cal-
`culation (17). Reporting is not only frequently incom-
`plete but also sometimes inaccurate. Of 119 reports stat-
`ing that all participants* were included in the analysis in
`the groups to which they were originally assigned (in-
`tention-to-treat* analysis), 15 (13%) excluded patients
`or did not analyze all patients as allocated (18). Many
`other reviews have found that inadequate reporting was
`common in specialty journals (19 –29) and journals
`published in languages other than English (30, 31).
`Proper randomization* eliminates selection bias*
`and is the crucial component of high-quality RCTs (32)
`Successful randomization hinges on two steps: genera-
`tion* of an unpredictable allocation sequence and con-
`cealment* of this sequence from the investigators enroll-
`(Table 1)
`ing participants
`(2, 21). Unfortunately,
`reporting of the methods used for allocation of partici-
`pants to interventions is also generally inadequate. For
`
`www.annals.org
`
`17 April 2001 Annals of Internal Medicine Volume 134 • Number 8 663
`
`Downloaded From: http://annals.org/ by David Rogers on 08/31/2016
`
`JANSSEN EXHIBIT 2048
`Mylan v. Janssen IPR2016-01332
`
`

`

`Academia and Clinic The CONSORT Statement: Explanation and Elaboration
`
`Table 1. Treatment Allocation. What’s So Special about
`Randomization?
`
`The method used to assign treatments or other interventions to trial
`participants is a crucial aspect of clinical trial design. Random assignment*
`is the preferred method; it has been successfully used in trials for more
`than 50 years (33). Randomization has three major advantages (34). First,
`it eliminates bias in the assignment of treatments. Without randomization,
`treatment comparisons may be prejudiced, whether consciously or not, by
`selection of participants of a particular kind to receive a particular
`treatment. Second, random allocation facilitates blinding* the identity of
`treatments to the investigators, participants, and evaluators, possibly by
`use of a placebo, which reduces bias after assignment of treatments (35).
`Third, random assignment permits the use of probability theory to express
`the likelihood that any difference in outcome* between intervention
`groups merely reflects chance (36). Preventing selection and confound-
`ing* biases is the most important advantage of randomization (37).
`
`Successful randomization in practice depends on two interrelated aspects:
`adequate generation of an unpredictable allocation sequence and
`concealment of that sequence until assignment occurs (2, 21). A key issue
`is whether the schedule is known or predictable by the people involved in
`allocating participants to the comparison groups* (38). The treatment
`allocation system should thus be set up so that the person enrolling
`participants does not know in advance which treatment the next person
`will get, a process termed allocation concealment* (2, 21). Proper
`allocation concealment shields knowledge of forthcoming assignments,
`whereas proper random sequences prevent correct anticipation of future
`assignments based on knowledge of past assignments.
`
`Terms marked with an asterisk are defined in the glossary at the end of the text.
`
`example, at least 5% of 206 reports of supposed RCTs
`in obstetrics and gynecology journals described studies
`that were not truly randomized (21). This estimate is
`conservative, as most reports do not at present provide
`adequate information about the method of allocation
`(19, 21, 23, 25, 30, 39).
`
`IMPROVING THE REPORTING OF RCTS:
`THE CONSORT STATEMENT
`DerSimonian and colleagues (16) suggested that
`“editors could greatly improve the reporting of clinical
`trials by providing authors with a list of items that they
`expected to be strictly reported.” Early in the 1990s, two
`groups of journal editors, trialists, and methodologists
`independently published recommendations on the re-
`porting of trials (40, 41). In a subsequent editorial, Ren-
`nie (42) urged the two groups to meet and develop a
`common set of recommendations; the outcome was the
`CONSORT statement (Consolidated Standards of Re-
`porting Trials) (43).
`simply CON-
`(or
`The CONSORT statement
`SORT) comprises a checklist of essential
`items that
`should be included in reports of RCTs and a diagram
`for documenting the flow of participants through a trial.
`It is aimed at first reports of two-group parallel designs.
`
`664 17 April 2001 Annals of Internal Medicine Volume 134 • Number 8
`
`Most of CONSORT is also relevant to a wider class of
`trial designs, such as equivalence, factorial, cluster, and
`crossover
`trials. Modifications
`to the CONSORT
`checklist for reporting trials with these and other designs
`are in preparation.
`The objective of CONSORT is to facilitate critical
`appraisal and interpretation of RCTs by providing guid-
`ance to authors about how to improve the reporting of
`their trials. Peer reviewers and editors can also use
`CONSORT to help them identify reports that are dif-
`ficult to interpret and those with potentially biased re-
`sults. However, CONSORT was not meant to be used
`as a quality assessment instrument. Rather, the content
`of CONSORT focuses on items related to the internal
`and external validity* of trials. Many items not explicitly
`mentioned in CONSORT should also be included in a
`report, such as information about approval by an ethics
`committee, obtaining of informed consent from partic-
`ipants, existence of a data safety and monitoring com-
`mittee, and sources of funding. In addition, other as-
`pects of a trial should be properly reported, such as
`information pertinent to cost-effectiveness analysis (44 –
`46) and quality-of-life assessments (47).
`
`THE REVISED CONSORT STATEMENT:
`EXPLANATION AND ELABORATION
`Since its publication in 1996, CONSORT has been
`supported by an increasing number of journals (48 –51)
`and several editorial groups, including the International
`Committee of Medical Journal Editors (the Vancouver
`Group) (52). Evidence is accumulating that the intro-
`duction of CONSORT has improved the quality of re-
`ports of RCTs (53, 54). However, CONSORT is an
`ongoing initiative, and the statement is revised periodi-
`cally (3). The 1996 version of the statement (43) re-
`ceived much comment and some criticism. For example,
`Meinert (55) pointed out that the terminology used
`lacked clarity and that the information presented in the
`flow diagram was incomplete. Work on a revised state-
`ment started in 1999; the revised checklist is shown
`in Table 2 and the revised flow diagram in Figure 1
`(56 –58).
`During revision, it became clear that explanation
`and elaboration of the principles underlying the CON-
`SORT statement would help investigators and others to
`write or appraise trial reports. In this article, we discuss
`the rationale and scientific background for each item
`
`www.annals.org
`
`Downloaded From: http://annals.org/ by David Rogers on 08/31/2016
`
`

`

`The CONSORT Statement: Explanation and Elaboration
`
`Academia and Clinic
`
`Table 2. Checklist of Items To Include When Reporting a Randomized Trial†
`
`Paper Section and Topic
`
`Item
`Number
`
`Descriptor
`
`Reported on
`Page Number
`
`Title and abstract
`
`Introduction
`Background
`
`Methods
`Participants
`
`Interventions
`
`Objectives
`Outcomes
`
`Sample size
`
`Randomization
`Sequence generation
`
`Allocation concealment
`
`Implementation
`
`Blinding (masking)
`
`Statistical methods
`
`Results
`Participant flow
`
`Recruitment
`Baseline data
`Numbers analyzed
`
`Outcomes and estimation
`
`Ancillary analyses
`
`Adverse events
`
`Discussion
`Interpretation
`
`Generalizability
`Overall evidence
`
`† From references 56 –58.
`
`1
`
`2
`
`3
`
`4
`
`5
`6
`
`7
`
`8
`
`9
`
`10
`
`11
`
`12
`
`13
`
`14
`15
`16
`
`17
`
`18
`
`19
`
`20
`
`21
`22
`
`How participants were allocated to interventions (e.g., “random allocation,” “randomized,”
`or “randomly assigned”).
`
`Scientific background and explanation of rationale.
`
`Eligibility criteria for participants and the settings and locations where the data were
`collected.
`Precise details of the interventions intended for each group and how and when they were
`actually administered.
`Specific objectives and hypotheses.
`Clearly defined primary and secondary outcome measures and, when applicable, any
`methods used to enhance the quality of measurements (e.g., multiple observations,
`training of assessors).
`How sample size was determined and, when applicable, explanation of any interim analyses
`and stopping rules.
`
`Method used to generate the random allocation sequence, including details of any
`restriction (e.g., blocking, stratification).
`Method used to implement the random allocation sequence (e.g., numbered containers or
`central telephone), clarifying whether the sequence was concealed until interventions
`were assigned.
`Who generated the allocation sequence, who enrolled participants, and who assigned
`participants to their groups.
`Whether or not participants, those administering the interventions, and those assessing the
`outcomes were blinded to group assignment. If done, how the success of blinding was
`evaluated.
`Statistical methods used to compare groups for primary outcome(s); methods for additional
`analyses, such as subgroup analyses and adjusted analyses.
`
`Flow of participants through each stage (a diagram is strongly recommended). Specifically,
`for each group report the numbers of participants randomly assigned, receiving intended
`treatment, completing the study protocol, and analyzed for the primary outcome.
`Describe protocol deviations from study as planned, together with reasons.
`Dates defining the periods of recruitment and follow-up.
`Baseline demographic and clinical characteristics of each group.
`Number of participants (denominator) in each group included in each analysis and whether
`the analysis was by “intention to treat.” State the results in absolute numbers when
`feasible (e.g., 10 of 20, not 50%).
`For each primary and secondary outcome, a summary of results for each group and the
`estimated effect size and its precision (e.g., 95% confidence interval).
`Address multiplicity by reporting any other analyses performed, including subgroup analyses
`and adjusted analyses, indicating those prespecified and those exploratory.
`All important adverse events or side effects in each intervention group.
`
`Interpretation of the results, taking into account study hypotheses, sources of potential bias
`or imprecision, and the dangers associated with multiplicity of analyses and outcomes.
`Generalizability (external validity) of the trial findings.
`General interpretation of the results in the context of current evidence.
`
`(Table 2) and provide published examples of good re-
`porting. (For further examples, see www.consort-state-
`ment.org). In these examples, we have removed authors’
`references to other publications to avoid confusion;
`
`however, relevant references should always be cited
`where needed, such as to support unfamiliar method-
`ologic approaches. Where possible, we describe the find-
`ings of relevant empirical studies. Many excellent books
`
`www.annals.org
`
`17 April 2001 Annals of Internal Medicine Volume 134 • Number 8 665
`
`Downloaded From: http://annals.org/ by David Rogers on 08/31/2016
`
`

`

`Academia and Clinic The CONSORT Statement: Explanation and Elaboration
`
`Figure 1. Revised template of the CONSORT
`(Consolidated Standards of Reporting Trials) diagram
`showing the flow of participants through each stage of a
`randomized trial (56 –58).
`
`on clinical trials offer fuller discussion of methodologic
`issues (59 – 61).
`For convenience, we sometimes refer to “treat-
`ments” and “patients,” although we recognize that not
`all interventions evaluated in RCTs are technically treat-
`ments and the participants in trials are not always patients.
`
`CHECKLIST ITEMS
`
`Title and Abstract
`
`Examples
`
`Title: “Smoking reduction with oral nicotine inhal-
`ers: double blind, randomised clinical trial of efficacy
`and safety” (62).
`Abstract: “Design: Randomized, double-blind, pla-
`cebo-controlled trial” (63).
`
`Explanation
`The ability to identify a relevant report in an elec-
`tronic database depends to a large extent on how it was
`indexed. Indexers for the National Library of Medicine’s
`MEDLINE database may not classify a report as an
`RCT if the authors do not explicitly report this infor-
`mation. To help ensure that a study is appropriately
`indexed as an RCT, authors should state explicitly in the
`abstract of their report that the participants were ran-
`domly assigned to the comparison groups. Possible
`wordings include “participants were randomly assigned
`to . . . ,” “treatment was randomized,” or “participants
`were assigned to interventions by using random alloca-
`tion.” We also strongly encourage the use of the word
`“randomized” in the title of the report to permit instant
`identification.
`In the mid-1990s, electronic searching of MED-
`LINE yielded only about half of all RCTs relevant to a
`topic (64). This deficiency has been remedied in part by
`the work of the Cochrane Collaboration, which by 1999
`had identified almost 100 000 RCTs that had not been
`indexed as such in MEDLINE. These reports have been
`reindexed (65). Adherence to this recommendation
`should improve the accuracy of indexing in the future.
`We encourage the use of structured abstracts when a
`summary of the report is required. Structured abstracts
`provide readers with a series of headings pertaining to
`the design, conduct, and analysis of a trial; standardized
`information appears under each heading (66). Some
`studies have found that structured abstracts are of higher
`quality than the more traditional descriptive abstracts
`(67) and that they allow readers to find information
`more easily (68).
`
`Item 1. How participants were allocated to inter-
`ventions (e.g., “random allocation,” “randomized,” or
`“randomly assigned”).
`
`666 17 April 2001 Annals of Internal Medicine Volume 134 • Number 8
`
`Introduction
`
`Item 2. Scientific background and explanation of
`rationale.
`
`www.annals.org
`
`Downloaded From: http://annals.org/ by David Rogers on 08/31/2016
`
`

`

`The CONSORT Statement: Explanation and Elaboration
`
`Academia and Clinic
`
`Example
`
`The carpal tunnel syndrome is caused by compres-
`sion of the median nerve at the wrist and is a common
`cause of pain in the arm, particularly in women. Injec-
`tion with corticosteroids is one of the many recom-
`mended treatments.
`One of the techniques for such injection entails
`injection just proximal to (not into) the carpal tunnel.
`The rationale for this injection site is that there is often
`a swelling at the volar side of the forearm, close to the
`carpal tunnel, which might contribute to compression
`of the median nerve. Moreover, the risk of damaging
`the median nerve by injection at this site is lower than
`by injection into the narrow carpal tunnel. The ratio-
`nale for using lignocaine (lidocaine) together with cor-
`ticosteroids is twofold: the injection is painless, and
`diminished sensation afterwards shows that the injec-
`tion was properly carried out.
`We investigated in a double blind randomised trial,
`firstly, whether symptoms disappeared after injection
`with corticosteroids proximal to the carpal tunnel and,
`secondly, how many patients remained free of symp-
`toms at follow up after this treatment (69).
`
`Explanation
`Typically, the introduction consists of free-flowing
`text, without a structured format, in which authors ex-
`plain the scientific background or context and the sci-
`entific rationale for their trial. The rationale may be
`explanatory (for example, to compare the bioavailability
`of two formulations of a drug or assess the possible in-
`fluence of a drug on renal function) or pragmatic (for
`example, to guide practice by comparing the clinical
`effects of two alternative treatments). Authors should
`report the evidence of the benefits of any active inter-
`vention included in a trial. They should also suggest a
`plausible explanation for how the intervention under
`investigation might work, especially if there is little or
`no previous experience with the intervention (70).
`The Helsinki Declaration states that biomedical re-
`search involving people should be based on a thorough
`knowledge of the scientific literature (71). That is, it is
`unethical to expose human subjects unnecessarily to the
`risks of research. Some clinical trials have been shown to
`have been unnecessary because the question they ad-
`dressed had been or could have been answered by a
`systematic review of the existing literature (72). Thus,
`the need for a new trial should be justified in the intro-
`
`www.annals.org
`
`duction. Ideally, the introduction should include a ref-
`erence to a systematic review of previous similar trials or
`a note of the absence of such trials (73).
`In the first part of the introduction, authors should
`describe the problem that necessitated the work. The
`nature, scope, and severity of the problem should pro-
`vide the background and a compelling rationale for the
`study. This information is often missing from reports.
`Authors should then describe briefly the broad approach
`taken to studying the problem. It may also be appropri-
`ate to include here the objectives* of the trial (item 5).
`
`Methods
`
`Item 3a. Eligibility criteria for participants.
`Example
`
`. . . all women requesting an IUCD [intrauterine
`contraceptive device] at the Family Welfare Centre, Ken-
`yatta National Hospital, who were menstruating regu-
`larly and who were between 20 and 44 years of age,
`were candidates for inclusion in the study. They were
`not admitted to the study if any of the following crite-
`ria were present: (1) a history of ectopic pregnancy, (2)
`pregnancy within the past 42 days, (3) leiomyomata of
`the uterus, (4) active PID [pelvic inflammatory dis-
`ease], (5) a cervical or endometrial malignancy, (6) a
`known hypersensitivity to tetracyclines, (7) use of any
`antibiotics within the past 14 days or long-acting in-
`jectable penicillin, (8) an impaired response to infec-
`tion, or (9) residence outside the city of Nairobi, insuf-
`ficient address for follow-up, or unwillingness to return
`for follow-up (74).
`
`Explanation
`Every RCT addresses an issue relevant to some pop-
`ulation with the condition of interest. Trialists usually
`restrict this population by using eligibility criteria* and
`by performing the trial in one or a few centers. Typical
`selection criteria may relate to age, sex, clinical diagno-
`sis, and comorbid conditions; exclusion criteria are often
`used to ensure patient safety. Eligibility criteria should
`be explicitly defined. If relevant, any known inaccuracy
`in patients’ diagnoses should be discussed because it can
`affect the power* of the trial (75). The common distinc-
`tion between inclusion and exclusion criteria is unnec-
`essary (76).
`Careful descriptions of the trial participants and the
`
`17 April 2001 Annals of Internal Medicine Volume 134 • Number 8 667
`
`Downloaded From: http://annals.org/ by David Rogers on 08/31/2016
`
`

`

`Academia and Clinic The CONSORT Statement: Explanation and Elaboration
`
`setting in which they were studied are needed so that
`readers may assess the external validity (generalizability)
`of the trial results (item 21). Of particular importance is
`the method of recruitment*, such as by referral or self-
`selection (for example, through advertisements). Because
`they are applied before randomization, eligibility criteria
`do not affect the internal validity of a trial, but they do
`affect the external validity.
`Despite their importance, eligibility criteria are of-
`ten not reported adequately. For example, 25% of 364
`reports of RCTs in surgery did not specify the eligibility
`criteria (77). Eight published trials leading to clinical
`alerts by the National Institutes of Health specified an
`average of 31 eligibility criteria. Only 63% of the criteria
`were mentioned in the journal articles, and only 19%
`were mentioned in the clinical alerts (78). The number
`of eligibility criteria in cancer trials increased markedly
`between the 1970s and 1990s (76).
`
`Item 3b. The settings and locations where the data
`were collected.
`
`Example
`
`Volunteers were recruited in London from four
`general practices and the ear, nose, and throat out-
`patient department of Northwick Park Hospital. The
`prescribers were familiar with homoeopathic principles
`but were not experienced in homoeopathic immuno-
`therapy (79).
`
`Explanation
`Settings and locations affect the external validity of
`a trial. Health care institutions vary greatly in their or-
`ganization, experience, and resources and the baseline
`risk for the medical condition under investigation. Cli-
`mate and other physical factors, economics, geography,
`and the social and cultural milieu can all affect a study’s
`external validity.
`Authors should report the number and type of set-
`tings and care providers involved so that readers can
`assess external validity. They should describe the settings
`and locations in which the study was carried out, includ-
`ing the country, city, and immediate environment (for
`example, community, office practice, hospital clinic, or
`inpatient unit). In particular, it should be clear whether
`the trial was carried out in one or several centers (“mul-
`ticenter trials”). This description should provide enough
`information that readers can judge whether the results of
`
`668 17 April 2001 Annals of Internal Medicine Volume 134 • Number 8
`
`the trial are relevant to their own setting. Authors
`should also report any other information about the set-
`tings and locations that could influence the observed
`results, such as problems with transportation that might
`have affected patient participation.
`
`Item 4. Precise details of the interventions intended
`for each group and how and when they were actually
`administered.
`
`Example
`
`Patients with psoriatic arthritis were randomised to
`receive either placebo or etanercept (Enbrel) at a dose
`of 25 mg twice weekly by subcutaneous administration
`for 12 weeks . . . Etanercept was supplied as a sterile,
`lyophilised powder in vials containing 25 mg etaner-
`cept, 40 mg mannitol, 10 mg sucrose, and 1–2 mg
`tromethamine per vial. Placebo was identically supplied
`and formulated except that it contained no etanercept.
`Each vial was reconstituted with 1 mL bacteriostatic
`water for injection (80).
`
`Explanation
`Authors should describe each intervention thor-
`oughly, including control interventions. The character-
`istics of a placebo and the way in which it was disguised
`should also be reported. It is especially important to
`describe thoroughly the “usual care” given to a control
`group or an intervention that is in fact a combination of
`interventions.
`In some cases, description of who administered
`treatments is critical because it may form part of the
`intervention. For example, with surgical interventions, it
`may be necessary to describe the number, training, and
`experience of surgeons in addition to the surgical proce-
`dure itself (81).
`When relevant, authors should report details of
`the timing and duration of interventions, especially if
`multiple-component interventions were given.
`
`Item 5. Specific objectives and hypotheses.
`
`Example
`
`In the current study we tested the hypothesis that a
`policy of active management of nulliparous labour
`would: 1. reduce the rate of caesarean section, 2. reduce
`the rate of prolonged labour; 3. not influence maternal
`satisfaction with the birth experience (82).
`
`www.annals.org
`
`Downloaded From: http://annals.org/ by David Rogers on 08/31/2016
`
`

`

`The CONSORT Statement: Explanation and Elaboration
`
`Academia and Clinic
`
`Explanation
`Objectives are the questions that the trial was de-
`signed to answer. They often relate to the efficacy of a
`particular therapeutic or preventive intervention. Hy-
`potheses* are prespecified questions being tested to help
`meet the objectives.
`Hypotheses are more specific than objectives and are
`amenable to explicit statistical evaluation. In practice,
`objectives and hypotheses are not always easily differen-
`tiated, as in the example above.
`Some evidence suggests that the majority of reports
`of RCTs provide adequate information about trial ob-
`jectives and hypotheses (24).
`
`Item 6a. Clearly defined primary and secondary out-
`come measures.
`
`Example
`
`The primary endpoint with respect to efficacy in
`psoriasis was the proportion of patients achieving a
`75% improvement in psoriasis activity from baseline to
`12 weeks as measured by the PASI [psoriasis area and
`severity index]. Additional analyses were done on the
`percentage change in PASI scores and improvement in
`target psoriasis lesions (80).
`
`Explanation
`All RCTs assess response variables, or outcomes, for
`which the groups are compared. Most trials have several
`outcomes, some of which are of more interest than oth-
`ers. The primary outcome measure is the prespecified out-
`come of greatest importance and is usually the one used
`in the sample size calculation (item 7). Some trials may
`have more than one primary outcome. Having more
`than one or two outcomes, however, incurs the prob-
`lems of interpretation associated with multiplicity* of
`analyses (see items 18 and 20) and is not recommended.
`Primary outcomes should be explicitly indicated as such
`in the report of an RCT. Other outcomes of interest
`are secondary outcomes. There may be several secondary
`outcomes, which often include unanticipated or un-
`intended effects of the intervention (item 19).
`All outcome measures, whether primary or second-
`ary, should be identified and completely defined. When
`outcomes are assessed at several time points after ran-
`domization, authors should indicate the prespecified
`time point of primary interest. It is sometimes helpful to
`specify who assessed outcomes (for example, if special
`
`www.annals.org
`
`skills are required to do so) and how many assessors
`there were.
`Many diseases have a plethora of possible outcomes
`that can be measured by using different scales or instru-
`ments. Where available and appropriate, previously de-
`veloped and validated scales or consensus guidelines
`should be used (83, 84), both to enhance quality of
`measurement and to assist in comparison with similar
`studies. For example, assessment of quality of life is
`likely to be improved by using a validated instrument
`(85). Authors should indicate the provenance and prop-
`erties of scales.
`More than 70 outcomes were used in 196 RCTs of
`nonsteroidal anti-inflammatory drugs for rheumatoid
`arthritis (28), and 640 different instruments had been
`used in 2000 trials in schizophrenia, of which 369 had
`been used only once (33). Investigation of 149 of those
`2000 trials showed that unpublished scales were a source
`of bias. In nonpharmacologic trials, one third of the
`claims of treatment superiority based on unpublished
`scales would not have been made if a published scale had
`been used (86). Similar evidence has been reported else-
`where (87, 88).
`
`Item 6b. When applicable, any methods used to
`enhance the quality of measurements (e.g., multiple
`observations, training of assessors).
`
`Examples
`
`The clinical end point committee . . . evaluated all
`clinical events in a blinded fashion and end points were
`determined by unanimous decision (89).
`Blood pressure (diastolic phase 5) while the patient
`was sitting and had rested for at least five minutes was
`measured by a trained nurse with a Copal UA-251 or a
`Takeda UA-751 electronic auscultatory blood pressure
`reading machine (Andrew Stephens, Brighouse, West
`Yorkshire) or with a Hawksley random zero sphygmo-
`manometer (Hawksley, Lancing, Sussex) in patients
`with atrial fibrillation. The first reading was discarded
`and the mean of the next three consecutive readings
`with a coefficient of variation below 15% was used in
`the study, with additional readings if required (90).
`
`Explanation
`Authors should give full details of how the primary
`and secondary outcomes were measured and whether
`any particular steps were taken to increase the reliability
`of the measurements.
`
`17 April 2001 Annals of Internal Medicine Volume 134 • Number 8 669
`
`Downloaded From: http://annals.org/ by David Rogers on 08/31/2016
`
`

`

`Academia and Clinic The CONSORT Statement: Explanation and Elaboration
`
`Some outcomes are easier to measure than others.
`Death (from any cause) is usually easy to assess, whereas
`blood pressure, depression, or quality of life are more
`difficult. Some strategies can be used to improve the
`quality of measurements. For example, assessment of
`blood pressure is more reliable if more than one reading
`is obtained, and digit preference can be avoided by using
`a random-zero sphygmomanometer. Assessments are
`more likely to be free of bias if the participant and as-
`sessor are blinded to group assignment (item 11a). If a
`trial requires taking unfamiliar measurements, formal,
`standardized training of the people who will be taking
`the measurements can be beneficial.
`
`Item 7a. How sample size was determined.
`
`Examples
`
`We believed that . . . the incidence of symptomatic
`deep venous thrombosis or pulmonary embolism or
`death would be 4% in the placebo group and 1.5% in
`the ardeparin sodium group. Based on 0.9 power to
`detect a significant difference (P 5 0.05, two-sided),
`976 patients were required for each study group. To
`compensate for nonevaluable patients, we planned to
`enroll 1000 patients per group (91).
`To have an 85% chance of detecting as significant
`(at the two sided 5% level) a five point difference be-
`tween the two groups in the mean SF-36 [Short Form-
`36] genera