CONSORT 2010 Explanation and Elaboration: updated guidelines for reporting parallel group randomised trials

Open AccessPublished:March 26, 2010DOI:https://doi.org/10.1016/j.jclinepi.2010.03.004

      Abstract

      Overwhelming evidence shows the quality of reporting of randomised controlled trials (RCTs) is not optimal. Without transparent reporting, readers cannot judge the reliability and validity of trial findings nor extract information for systematic reviews. Recent methodological analyses indicate that inadequate reporting and design are associated with biased estimates of treatment effects. Such systematic error is seriously damaging to RCTs, which are considered the gold standard for evaluating interventions because of their ability to minimise or avoid bias.
      A group of scientists and editors developed the CONSORT (Consolidated Standards of Reporting Trials) statement to improve the quality of reporting of RCTs. It was first published in 1996 and updated in 2001. The statement consists of a checklist and flow diagram that authors can use for reporting an RCT. Many leading medical journals and major international editorial groups have endorsed the CONSORT statement. The statement facilitates critical appraisal and interpretation of RCTs.
      During the 2001 CONSORT revision, it became clear that explanation and elaboration of the principles underlying the CONSORT statement would help investigators and others to write or appraise trial reports. A CONSORT explanation and elaboration article was published in 2001 alongside the 2001 version of the CONSORT statement.
      After an expert meeting in January 2007, the CONSORT statement has been further revised and is published as the CONSORT 2010 Statement. This update improves the wording and clarity of the previous checklist and incorporates recommendations related to topics that have only recently received recognition, such as selective outcome reporting bias.
      This explanatory and elaboration document—intended to enhance the use, understanding, and dissemination of the CONSORT statement—has also been extensively revised. It presents the meaning and rationale for each new and updated checklist item providing examples of good reporting and, where possible, references to relevant empirical studies. Several examples of flow diagrams are included.
      The CONSORT 2010 Statement, this revised explanatory and elaboration document, and the associated website (www.consort-statement.org) should be helpful resources to improve reporting of randomised trials.
      “The whole of medicine depends on the transparent reporting of clinical trials”[
      • Rennie D.
      CONSORT revised—improving the reporting of randomized trials.
      ].
      Well designed and properly executed randomised controlled trials (RCTs) provide the most reliable evidence on the efficacy of healthcare interventions, but trials with inadequate methods are associated with bias, especially exaggerated treatment effects [
      • Schulz K.F.
      • Chalmers I.
      • Hayes R.J.
      • Altman D.G.
      Empirical evidence of bias. Dimensions of methodological quality associated with estimates of treatment effects in controlled trials.
      ,
      • Moher D.
      CONSORT: an evolving tool to help improve the quality of reports of randomized controlled trials. Consolidated Standards of Reporting Trials.
      ,
      • Kjaergard L.L.
      • Villumsen J.
      • Gluud C.
      Quality of randomised clinical trials affects estimates of intervention efficacy.
      ,
      • Juni P.
      • Altman D.G.
      • Egger M.
      Systematic reviews in health care: Assessing the quality of controlled clinical trials.
      ]. Biased results from poorly designed and reported trials can mislead decision making in health care at all levels, from treatment decisions for a 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 the report. Far from being transparent, the reporting of RCTs is often incomplete [
      • Veldhuyzen van Zanten S.J.
      • Cleary C.
      • Talley N.J.
      • Peterson T.C.
      • Nyren O.
      • Bradley L.A.
      • et al.
      Drug treatment of functional dyspepsia: a systematic analysis of trial methodology with recommendations for design of future trials.
      ,
      • Talley N.J.
      • Owen B.K.
      • Boyce P.
      • Paterson K.
      Psychological treatments for irritable bowel syndrome: a critique of controlled treatment trials.
      ,
      • Adetugbo K.
      • Williams H.
      How well are randomized controlled trials reported in the dermatology literature?.
      ,
      • Kjaergard L.L.
      • Nikolova D.
      • Gluud C.
      Randomized clinical trials in HEPATOLOGY: predictors of quality.
      ], compounding problems arising from poor methodology [
      • Schor S.
      • Karten I.
      Statistical evaluation of medical journal manuscripts.
      ,
      • Gore S.M.
      • Jones I.G.
      • Rytter E.C.
      Misuse of statistical methods: critical assessment of articles in BMJ from January to March 1976.
      ,
      • Hall J.C.
      • Hill D.
      • Watts J.M.
      Misuse of statistical methods in the Australasian surgical literature.
      ,
      • Altman D.G.
      Statistics in medical journals.
      ,
      • Pocock S.J.
      • Hughes M.D.
      • Lee R.J.
      Statistical problems in the reporting of clinical trials. A survey of three medical journals.
      ,
      • Altman D.G.
      The scandal of poor medical research.
      ].

      1. Incomplete and inaccurate reporting

      Many reviews have documented deficiencies in reports of clinical trials. For example, information on the method used in a trial to assign participants to comparison groups was reported in only 21% of 519 trial reports indexed in PubMed in 2000 [
      • Chan A.W.
      • Altman D.G.
      Epidemiology and reporting of randomised trials published in PubMed journals.
      ], and only 34% of 616 reports indexed in 2006 [
      • Hopewell S.
      • Dutton S.
      • Yu L.M.
      • Chan A.W.
      • Altman D.G.
      The quality of reports of randomised trials in 2000 and 2006: comparative study of articles indexed in PubMed.
      ]. Similarly, only 45% of trial reports indexed in PubMed in 2000 [
      • Chan A.W.
      • Altman D.G.
      Epidemiology and reporting of randomised trials published in PubMed journals.
      ] and 53% in 2006 [
      • Hopewell S.
      • Dutton S.
      • Yu L.M.
      • Chan A.W.
      • Altman D.G.
      The quality of reports of randomised trials in 2000 and 2006: comparative study of articles indexed in PubMed.
      ] defined a primary end point, and only 27% in 2000 and 45% in 2006 reported a sample size calculation. Reporting is not only often incomplete but also sometimes inaccurate. Of 119 reports stating that all participants were included in the analysis in the groups to which they were originally assigned (intention-to-treat analysis), 15 (13%) excluded patients or did not analyse all patients as allocated [
      • Hollis S.
      • Campbell F.
      What is meant by intention to treat analysis? Survey of published randomised controlled trials.
      ]. Many other reviews have found that inadequate reporting is common in specialty journals [
      • Chan A.W.
      • Altman D.G.
      Epidemiology and reporting of randomised trials published in PubMed journals.
      ,
      • Lai T.Y.
      • Wong V.W.
      • Lam R.F.
      • Cheng A.C.
      • Lam D.S.
      • Leung G.M.
      Quality of reporting of key methodological items of randomized controlled trials in clinical ophthalmic journals.
      ] and journals published in languages other than English [
      • Moher D.
      • Fortin P.
      • Jadad A.R.
      • Juni P.
      • Klassen T.
      • Le L.J.
      • et al.
      Completeness of reporting of trials published in languages other than English: implications for conduct and reporting of systematic reviews.
      ,
      • Junker C.A.
      Adherence to published standards of reporting: a comparison of placebo-controlled trials published in English or German.
      ].
      Proper randomisation reduces selection bias at trial entry and is the crucial component of high quality RCTs [
      • Altman D.G.
      ]. Successful randomisation hinges on two steps: generation of an unpredictable allocation sequence and concealment of this sequence from the investigators enrolling participants (see Box 1) [
      • Schulz K.F.
      • Chalmers I.
      • Hayes R.J.
      • Altman D.G.
      Empirical evidence of bias. Dimensions of methodological quality associated with estimates of treatment effects in controlled trials.
      ,
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ].
      Treatment allocation. What's so special about randomisation?
      The method used to assign interventions to trial participants is a crucial aspect of clinical trial design. Random assignment is the preferred method; it has been successfully used regularly in trials for more than 50 years [
      Streptomycin treatment of pulmonary tuberculosis: a Medical Research Council investigation.
      ]. Randomisation has three major advantages [
      • Schulz K.F.
      Randomized controlled trials.
      ]. First, when properly implemented, it eliminates selection bias, balancing both known and unknown prognostic factors, in the assignment of treatments. Without randomisation, treatment comparisons may be prejudiced, whether consciously or not, by selection of participants of a particular kind to receive a particular treatment. Second, random assignment permits the use of probability theory to express the likelihood that any difference in outcome between intervention groups merely reflects chance [
      • Greenland S.
      Randomization, statistics, and causal inference.
      ]. Third, random allocation, in some situations, 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 [
      • Armitage P.
      The role of randomization in clinical trials.
      ]. Of these three advantages, reducing selection bias at trial entry is usually the most important [
      • Kleijnen J.
      • Gotzsche P.C.
      • Kunz R.
      • Oxman A.D.
      • Chalmers I.
      So what's so special about randomisation.
      ].
      Successful randomisation in practice depends on two interrelated aspects—adequate generation of an unpredictable allocation sequence and concealment of that sequence until assignment occurs [
      • Schulz K.F.
      • Chalmers I.
      • Hayes R.J.
      • Altman D.G.
      Empirical evidence of bias. Dimensions of methodological quality associated with estimates of treatment effects in controlled trials.
      ,
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ]. A key issue is whether the schedule is known or predictable by the people involved in allocating participants to the comparison groups [
      • Chalmers I.
      Assembling comparison groups to assess the effects of health care.
      ]. 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 [
      • Schulz K.F.
      • Chalmers I.
      • Hayes R.J.
      • Altman D.G.
      Empirical evidence of bias. Dimensions of methodological quality associated with estimates of treatment effects in controlled trials.
      ,
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ]. Proper allocation concealment shields knowledge of forthcoming assignments, whereas proper random sequences prevent correct anticipation of future assignments based on knowledge of past assignments.
      Unfortunately, despite that central role, reporting of the methods used for allocation of participants to interventions is also generally inadequate. For example, 5% of 206 reports of supposed RCTs in obstetrics and gynaecology journals described studies that were not truly randomised [
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ]. This estimate is conservative, as most reports do not at present provide adequate information about the method of allocation [
      • Moher D.
      • Fortin P.
      • Jadad A.R.
      • Juni P.
      • Klassen T.
      • Le L.J.
      • et al.
      Completeness of reporting of trials published in languages other than English: implications for conduct and reporting of systematic reviews.
      ,
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ,
      • Nicolucci A.
      • Grilli R.
      • Alexanian A.A.
      • Apolone G.
      • Torri V.
      • Liberati A.
      Quality, evolution, and clinical implications of randomized, controlled trials on the treatment of lung cancer. A lost opportunity for meta-analysis.
      ,
      • Ah-See K.W.
      • Molony N.C.
      A qualitative assessment of randomized controlled trials in otolaryngology.
      ,
      • Altman D.G.
      • Dore C.J.
      Randomisation and baseline comparisons in clinical trials.
      ,
      • Thornley B.
      • Adams C.
      Content and quality of 2000 controlled trials in schizophrenia over 50 years.
      ].

      2. Improving the reporting of RCTs: the CONSORT statement

      DerSimonian and colleagues 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”[
      • DerSimonian R.
      • Charette L.J.
      • McPeek B.
      • Mosteller F.
      Reporting on methods in clinical trials.
      ]. Early in the 1990s, two groups of journal editors, trialists, and methodologists independently published recommendations on the reporting of trials [
      A proposal for structured reporting of randomized controlled trials. The Standards of Reporting Trials Group.
      ,
      Call for comments on a proposal to improve reporting of clinical trials in the biomedical literature. Working Group on Recommendations for Reporting of Clinical Trials in the Biomedical Literature.
      ]. In a subsequent editorial, Rennie urged the two groups to meet and develop a common set of recommendations [
      • Rennie D.
      Reporting randomized controlled trials. An experiment and a call for responses from readers.
      ]; the outcome was the CONSORT statement (Consolidated Standards of Reporting Trials) [
      • Begg C.
      • Cho M.
      • Eastwood S.
      • Horton R.
      • Moher D.
      • Olkin I.
      • et al.
      Improving the quality of reporting of randomized controlled trials: the CONSORT statement.
      ].
      The CONSORT statement (or simply CONSORT) 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 primary reports of RCTs with two group, parallel designs. Most of CONSORT is also relevant to a wider class of trial designs, such as non-inferiority, equivalence, factorial, cluster, and crossover trials. Extensions to the CONSORT checklist for reporting trials with some of these designs have been published [
      • Piaggio G.
      • Elbourne D.R.
      • Altman D.G.
      • Pocock S.J.
      • Evans S.J.
      Reporting of noninferiority and equivalence randomized trials: an extension of the CONSORT statement.
      ,
      • Campbell M.K.
      • Elbourne D.R.
      • Altman D.G.
      CONSORT statement: extension to cluster randomised trials.
      ,
      • Zwarenstein M.
      • Treweek S.
      • Gagnier J.J.
      • Altman D.G.
      • Tunis S.
      • Haynes B.
      • et al.
      Improving the reporting of pragmatic trials: an extension of the CONSORT statement.
      ], as have those for reporting certain types of data (harms [
      • Ioannidis J.P.
      • Evans S.J.
      • Gotzsche P.C.
      • O'Neill R.T.
      • Altman D.G.
      • Schulz K.
      • et al.
      Better reporting of harms in randomized trials: an extension of the CONSORT statement.
      ]), types of interventions (non-pharmacological treatments [
      • Boutron I.
      • Moher D.
      • Altman D.G.
      • Schulz K.F.
      • Ravaud P.
      Extending the CONSORT statement to randomized trials of nonpharmacologic treatment: explanation and elaboration.
      ], herbal interventions [
      • Gagnier J.J.
      • Boon H.
      • Rochon P.
      • Moher D.
      • Barnes J.
      • Bombardier C.
      Reporting randomized, controlled trials of herbal interventions: an elaborated CONSORT statement.
      ]), and abstracts [
      • Hopewell S.
      • Clarke M.
      • Moher D.
      • Wager E.
      • Middleton P.
      • Altman D.G.
      • et al.
      CONSORT for reporting randomized controlled trials in journal and conference abstracts: explanation and elaboration.
      ].
      The objective of CONSORT is to provide guidance to authors about how to improve the reporting of their trials. Trial reports need be clear, complete, and transparent. Readers, peer reviewers, and editors can also use CONSORT to help them critically appraise and interpret reports of RCTs. 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 informed consent from participants, and, where relevant, existence of a data safety and monitoring committee. In addition, any other aspects of a trial that are mentioned should be properly reported, such as information pertinent to cost effectiveness analysis [
      • Siegel J.E.
      • Weinstein M.C.
      • Russell L.B.
      • Gold M.R.
      Recommendations for reporting cost-effectiveness analyses. Panel on Cost-Effectiveness in Health and Medicine.
      ,
      • Drummond M.F.
      • Jefferson T.O.
      Guidelines for authors and peer reviewers of economic submissions to the BMJ. The BMJ Economic Evaluation Working Party.
      ,
      • Lang T.A.
      • Secic M.
      How to report statistics in medicine. Annotated guidelines for authors, editors, and reviewers.
      ].
      Since its publication in 1996, CONSORT has been supported by more than 400 journals (www.consort-statement.org) and several editorial groups, such as the International Committee of Medical Journal Editors [
      • Davidoff F.
      News from the International Committee of Medical Journal Editors.
      ]. The introduction of CONSORT within journals is associated with improved quality of reports of RCTs [
      • Hopewell S.
      • Dutton S.
      • Yu L.M.
      • Chan A.W.
      • Altman D.G.
      The quality of reports of randomised trials in 2000 and 2006: comparative study of articles indexed in PubMed.
      ,
      • Plint A.C.
      • Moher D.
      • Morrison A.
      • Schulz K.
      • Altman D.G.
      • Hill C.
      • et al.
      Does the CONSORT checklist improve the quality of reports of randomised controlled trials? A systematic review.
      ,
      • Egger M.
      • Juni P.
      • Bartlett C.
      Value of flow diagrams in reports of randomized controlled trials.
      ]. However, CONSORT is an ongoing initiative, and the CONSORT statement is revised periodically [
      • Moher D.
      CONSORT: an evolving tool to help improve the quality of reports of randomized controlled trials. Consolidated Standards of Reporting Trials.
      ]. CONSORT was last revised nine years ago, in 2001 [
      • Moher D.
      • Schulz K.F.
      • Altman D.G.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials.
      ,
      • Moher D.
      • Schulz K.F.
      • Altman D.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials.
      ,
      • Moher D.
      • Schulz K.F.
      • Altman D.G.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomised trials.
      ]. Since then the evidence base to inform CONSORT has grown considerably; empirical data have highlighted new concerns regarding the reporting of RCTs, such as selective outcome reporting [
      • Chan A.W.
      • Hrobjartsson A.
      • Haahr M.T.
      • Gotzsche P.C.
      • Altman D.G.
      Empirical evidence for selective reporting of outcomes in randomized trials: comparison of protocols to published articles.
      ,
      • Al-Marzouki S.
      • Roberts I.
      • Evans S.
      • Marshall T.
      Selective reporting in clinical trials: analysis of trial protocols accepted by the Lancet.
      ,
      • Dwan K.
      • Altman D.G.
      • Arnaiz J.A.
      • Bloom J.
      • Chan A.W.
      • Cronin E.
      • et al.
      Systematic review of the empirical evidence of study publication bias and outcome reporting bias.
      ]. A CONSORT Group meeting was therefore convened in January 2007, in Canada, to revise the 2001 CONSORT statement and its accompanying explanation and elaboration document. The revised checklist is shown in Table 1 and the flow diagram, not revised, in Fig 1 [
      • Moher D.
      • Schulz K.F.
      • Altman D.G.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials.
      ,
      • Moher D.
      • Schulz K.F.
      • Altman D.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials.
      ,
      • Moher D.
      • Schulz K.F.
      • Altman D.G.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomised trials.
      ].
      Table 1CONSORT 2010 checklist of information to include when reporting a randomised trial
      We strongly recommend reading this statement in conjunction with the CONSORT 2010 Explanation and Elaboration for important clarifications on all the items. If relevant, we also recommend reading CONSORT extensions for cluster randomised trials [40], non-inferiority and equivalence trials [39], non-pharmacological treatments [43], herbal interventions [44], and pragmatic trials [41]. Additional extensions are forthcoming: for those and for up to date references relevant to this checklist, see www.consort-statement.org.
      Section/TopicItem NoChecklist itemReported on page No
      Title and abstract
      1aIdentification as a randomised trial in the title
      1bStructured summary of trial design, methods, results, and conclusions (for specific guidance see CONSORT for abstracts
      • Hopewell S.
      • Clarke M.
      • Moher D.
      • Wager E.
      • Middleton P.
      • Altman D.G.
      • et al.
      CONSORT for reporting randomized controlled trials in journal and conference abstracts: explanation and elaboration.
      ,
      • Hopewell S.
      • Clarke M.
      • Moher D.
      • Wager E.
      • Middleton P.
      • Altman D.G.
      • et al.
      CONSORT for reporting randomised trials in journal and conference abstracts.
      )
      Introduction
       Background and objectives2aScientific background and explanation of rationale
      2bSpecific objectives or hypotheses
      Methods
       Trial design3aDescription of trial design (such as parallel, factorial) including allocation ratio
      3bImportant changes to methods after trial commencement (such as eligibility criteria), with reasons
       Participants4aEligibility criteria for participants
      4bSettings and locations where the data were collected
       Interventions5The interventions for each group with sufficient details to allow replication, including how and when they were actually administered
       Outcomes6aCompletely defined pre-specified primary and secondary outcome measures, including how and when they were assessed
      6bAny changes to trial outcomes after the trial commenced, with reasons
       Sample size7aHow sample size was determined
      7bWhen applicable, explanation of any interim analyses and stopping guidelines
       Randomisation:
      Sequence generation8aMethod used to generate the random allocation sequence
      8bType of randomisation; details of any restriction (such as blocking and block size)
      Allocation concealment mechanism9Mechanism used to implement the random allocation sequence (such as sequentially numbered containers), describing any steps taken to conceal the sequence until interventions were assigned
      Implementation10Who generated the random allocation sequence, who enrolled participants, and who assigned participants to interventions
       Blinding11aIf done, who was blinded after assignment to interventions (for example, participants, care providers, those assessing outcomes) and how
      11bIf relevant, description of the similarity of interventions
       Statistical methods12aStatistical methods used to compare groups for primary and secondary outcomes
      12bMethods for additional analyses, such as subgroup analyses and adjusted analyses
      Results
       Participant flow (a diagram is strongly recommended)13aFor each group, the numbers of participants who were randomly assigned, received intended treatment, and were analysed for the primary outcome
      13bFor each group, losses and exclusions after randomisation, together with reasons
       Recruitment14aDates defining the periods of recruitment and follow-up
      14bWhy the trial ended or was stopped
       Baseline data15A table showing baseline demographic and clinical characteristics for each group
       Numbers analysed16For each group, number of participants (denominator) included in each analysis and whether the analysis was by original assigned groups
       Outcomes and estimation17aFor each primary and secondary outcome, results for each group, and the estimated effect size and its precision (such as 95% confidence interval)
      17bFor binary outcomes, presentation of both absolute and relative effect sizes is recommended
       Ancillary analyses18Results of any other analyses performed, including subgroup analyses and adjusted analyses, distinguishing pre-specified from exploratory
       Harms19All important harms or unintended effects in each group (for specific guidance see CONSORT for harms
      • Ioannidis J.P.
      • Evans S.J.
      • Gotzsche P.C.
      • O'Neill R.T.
      • Altman D.G.
      • Schulz K.
      • et al.
      Better reporting of harms in randomized trials: an extension of the CONSORT statement.
      )
      Discussion
       Limitations20Trial limitations, addressing sources of potential bias, imprecision, and, if relevant, multiplicity of analyses
       Generalisability21Generalisability (external validity, applicability) of the trial findings
       Interpretation22Interpretation consistent with results, balancing benefits and harms, and considering other relevant evidence
      Other information
       Registration23Registration number and name of trial registry
       Protocol24Where the full trial protocol can be accessed, if available
       Funding25Sources of funding and other support (such as supply of drugs), role of funders
      We strongly recommend reading this statement in conjunction with the CONSORT 2010 Explanation and Elaboration for important clarifications on all the items. If relevant, we also recommend reading CONSORT extensions for cluster randomised trials
      • Campbell M.K.
      • Elbourne D.R.
      • Altman D.G.
      CONSORT statement: extension to cluster randomised trials.
      , non-inferiority and equivalence trials
      • Piaggio G.
      • Elbourne D.R.
      • Altman D.G.
      • Pocock S.J.
      • Evans S.J.
      Reporting of noninferiority and equivalence randomized trials: an extension of the CONSORT statement.
      , non-pharmacological treatments
      • Boutron I.
      • Moher D.
      • Altman D.G.
      • Schulz K.F.
      • Ravaud P.
      Extending the CONSORT statement to randomized trials of nonpharmacologic treatment: explanation and elaboration.
      , herbal interventions
      • Gagnier J.J.
      • Boon H.
      • Rochon P.
      • Moher D.
      • Barnes J.
      • Bombardier C.
      Reporting randomized, controlled trials of herbal interventions: an elaborated CONSORT statement.
      , and pragmatic trials
      • Zwarenstein M.
      • Treweek S.
      • Gagnier J.J.
      • Altman D.G.
      • Tunis S.
      • Haynes B.
      • et al.
      Improving the reporting of pragmatic trials: an extension of the CONSORT statement.
      . Additional extensions are forthcoming: for those and for up to date references relevant to this checklist, see www.consort-statement.org.
      Figure thumbnail gr1
      Fig. 1Flow diagram of the progress through the phases of a parallel randomised trial of two groups (that is, enrolment, intervention allocation, follow-up, and data analysis) [
      • Moher D.
      • Schulz K.F.
      • Altman D.G.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials.
      ,
      • Moher D.
      • Schulz K.F.
      • Altman D.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials.
      ,
      • Moher D.
      • Schulz K.F.
      • Altman D.G.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomised trials.
      ].

      3. The CONSORT 2010 Statement: explanation and elaboration

      During the 2001 CONSORT revision, it became clear that explanation and elaboration of the principles underlying the CONSORT statement would help investigators and others to write or appraise trial reports. The CONSORT explanation and elaboration article [
      • Altman D.G.
      • Schulz K.F.
      • Moher D.
      • Egger M.
      • Davidoff F.
      • Elbourne D.
      • et al.
      The revised CONSORT statement for reporting randomized trials: explanation and elaboration.
      ] was published in 2001 alongside the 2001 version of the CONSORT statement. It discussed the rationale and scientific background for each item and provided published examples of good reporting. The rationale for revising that article is similar to that for revising the statement, described above. We briefly describe below the main additions and deletions to this version of the explanation and elaboration article.

      4. The CONSORT 2010 Explanation and Elaboration: changes

      We have made several substantive and some cosmetic changes to this version of the CONSORT explanatory document (full details are highlighted in the 2010 version of the CONSORT statement [
      • Schulz K.F.
      • Altman D.G.
      • Moher D.
      for the CONSORT Group
      CONSORT 2010 Statement: updated guidelines for reporting parallel group randomised trials.
      ]). Some reflect changes to the CONSORT checklist; there are three new checklist items in the CONSORT 2010 checklist—such as item 24, which asks authors to report where their trial protocol can be accessed. We have also updated some existing explanations, including adding more recent references to methodological evidence, and used some better examples. We have removed the glossary, which is now available on the CONSORT website (www.consort-statement.org). Where possible, we describe the findings of relevant empirical studies. Many excellent books on clinical trials offer fuller discussion of methodological issues [
      • Pocock S.J.
      Clinical trials: a practical approach.
      ,
      • Meinert C.L.
      Clinical trials: design, conduct and analysis.
      ,
      • Friedman L.M.
      • Furberg C.D.
      • DeMets D.L.
      Fundamentals of clinical trials.
      ]. Finally, for convenience, we sometimes refer to “treatments” and “patients,” although we recognise that not all interventions evaluated in RCTs are treatments and not all participants are patients.

      5. Checklist items

      5.1 Title and abstract

      5.1.1 Item 1a. Identification as a randomised trial in the title

      Example—“Smoking reduction with oral nicotine inhalers: double blind, randomised clinical trial of efficacy and safety”[
      • Bolliger C.T.
      • Zellweger J.P.
      • Danielsson T.
      • van Biljon X.
      • Robidou A.
      • Westin A.
      • et al.
      Smoking reduction with oral nicotine inhalers: double blind, randomised clinical trial of efficacy and safety.
      ].
      Explanation—The ability to identify a report of a randomised trial in an electronic database depends to a large extent on how it was indexed. Indexers may not classify a report as a randomised trial if the authors do not explicitly report this information [
      • Dickersin K.
      • Manheimer E.
      • Wieland S.
      • Robinson K.A.
      • Lefebvre C.
      • McDonald S.
      Development of the Cochrane Collaboration's CENTRAL Register of controlled clinical trials.
      ]. To help ensure that a study is appropriately indexed and easily identified, authors should use the word “randomised” in the title to indicate that the participants were randomly assigned to their comparison groups.

      5.1.2 Item 1b. Structured summary of trial design, methods, results, and conclusions

      For specific guidance see CONSORT for abstracts [
      • Hopewell S.
      • Clarke M.
      • Moher D.
      • Wager E.
      • Middleton P.
      • Altman D.G.
      • et al.
      CONSORT for reporting randomized controlled trials in journal and conference abstracts: explanation and elaboration.
      ,
      • Hopewell S.
      • Clarke M.
      • Moher D.
      • Wager E.
      • Middleton P.
      • Altman D.G.
      • et al.
      CONSORT for reporting randomised trials in journal and conference abstracts.
      ].
      Explanation—Clear, transparent, and sufficiently detailed abstracts are important because readers often base their assessment of a trial on such information. Some readers use an abstract as a screening tool to decide whether to read the full article. However, as not all trials are freely available and some health professionals do not have access to the full trial reports, healthcare decisions are sometimes made on the basis of abstracts of randomised trials [
      The impact of open access upon public health.
      ].
      A journal abstract should contain sufficient information about a trial to serve as an accurate record of its conduct and findings, providing optimal information about the trial within the space constraints and format of a journal. A properly constructed and written abstract helps individuals to assess quickly the relevance of the findings and aids the retrieval of relevant reports from electronic databases [
      • Harbourt A.M.
      • Knecht L.S.
      • Humphreys B.L.
      Structured abstracts in MEDLINE, 1989-1991.
      ]. The abstract should accurately reflect what is included in the full journal article and should not include information that does not appear in the body of the paper. Studies comparing the accuracy of information reported in a journal abstract with that reported in the text of the full publication have found claims that are inconsistent with, or missing from, the body of the full article [
      • Harris A.H.
      • Standard S.
      • Brunning J.L.
      • Casey S.L.
      • Goldberg J.H.
      • Oliver L.
      • et al.
      The accuracy of abstracts in psychology journals.
      ,
      • Pitkin R.M.
      • Branagan M.A.
      • Burmeister L.F.
      Accuracy of data in abstracts of published research articles.
      ,
      • Ward L.G.
      • Kendrach M.G.
      • Price S.O.
      Accuracy of abstracts for original research articles in pharmacy journals.
      ,
      • Gotzsche P.C.
      Believability of relative risks and odds ratios in abstracts: cross sectional study.
      ]. Conversely, omitting important harms from the abstract could seriously mislead someone's interpretation of the trial findings [
      • Ioannidis J.P.
      • Evans S.J.
      • Gotzsche P.C.
      • O'Neill R.T.
      • Altman D.G.
      • Schulz K.
      • et al.
      Better reporting of harms in randomized trials: an extension of the CONSORT statement.
      ,
      • Ioannidis J.P.
      • Lau J.
      Completeness of safety reporting in randomized trials: an evaluation of 7 medical areas.
      ].
      A recent extension to the CONSORT statement provides a list of essential items that authors should include when reporting the main results of a randomised trial in a journal (or conference) abstract (see Table 2) [
      • Hopewell S.
      • Clarke M.
      • Moher D.
      • Wager E.
      • Middleton P.
      • Altman D.G.
      • et al.
      CONSORT for reporting randomized controlled trials in journal and conference abstracts: explanation and elaboration.
      ]. We strongly recommend the use of structured abstracts for reporting randomised trials. They provide readers with information about the trial under a series of headings pertaining to the design, conduct, analysis, and interpretation [
      • Haynes R.B.
      • Mulrow C.D.
      • Huth E.J.
      • Altman D.G.
      • Gardner M.J.
      More informative abstracts revisited.
      ]. Some studies have found that structured abstracts are of higher quality than the more traditional descriptive abstracts [
      • Taddio A.
      • Pain T.
      • Fassos F.F.
      • Boon H.
      • Ilersich A.L.
      • Einarson T.R.
      Quality of nonstructured and structured abstracts of original research articles in the British Medical Journal, the Canadian Medical Association Journal and the Journal of the American Medical Association.
      ,
      • Wager E.
      • Middleton P.
      Technical editing of research reports in biomedical journals.
      ] and that they allow readers to find information more easily [
      • Hartley J.
      • Sydes M.
      • Blurton A.
      Obtaining information accurately and quickly: Are structured abstracts more efficient?.
      ]. We recognise that many journals have developed their own structure and word limit for reporting abstracts. It is not our intention to suggest changes to these formats, but to recommend what information should be reported.
      Table 2Items to include when reporting a randomised trial in a journal abstract
      ItemDescription
      AuthorsContact details for the corresponding author
      Trial designDescription of the trial design (such as parallel, cluster, non-inferiority)
      Methods:
       ParticipantsEligibility criteria for participants and the settings where the data were collected
       InterventionsInterventions intended for each group
       ObjectiveSpecific objective or hypothesis
       OutcomeClearly defined primary outcome for this report
       RandomisationHow participants were allocated to interventions
       Blinding (masking)Whether participants, care givers, and those assessing the outcomes were blinded to group assignment
      Results:
       Numbers randomisedNumber of participants randomised to each group
       RecruitmentTrial status
       Numbers analysedNumber of participants analysed in each group
       OutcomeFor the primary outcome, a result for each group and the estimated effect size and its precision
       HarmsImportant adverse events or side effects
      ConclusionsGeneral interpretation of the results
      Trial registrationRegistration number and name of trial register
      FundingSource of funding

      5.2 Introduction

      5.2.1 Item 2a. Scientific background and explanation of rationale

      Example—“Surgery is the treatment of choice for patients with disease stage I and II non-small cell lung cancer (NSCLC) … An NSCLC meta-analysis combined the results from eight randomised trials of surgery versus surgery plus adjuvant cisplatin-based chemotherapy and showed a small, but not significant (p=0.08), absolute survival benefit of around 5% at 5 years (from 50% to 55%). At the time the current trial was designed (mid-1990s), adjuvant chemotherapy had not become standard clinical practice … The clinical rationale for neo-adjuvant chemotherapy is three-fold: regression of the primary cancer could be achieved thereby facilitating and simplifying or reducing subsequent surgery; undetected micro-metastases could be dealt with at the start of treatment; and there might be inhibition of the putative stimulus to residual cancer by growth factors released by surgery and by subsequent wound healing … The current trial was therefore set up to compare, in patients with resectable NSCLC, surgery alone versus three cycles of platinum-based chemotherapy followed by surgery in terms of overall survival, quality of life, pathological staging, resectability rates, extent of surgery, and time to and site of relapse”[
      • Gilligan D.
      • Nicolson M.
      • Smith I.
      • Groen H.
      • Dalesio O.
      • Goldstraw P.
      • et al.
      Preoperative chemotherapy in patients with resectable non-small cell lung cancer: results of the MRC LU22/NVALT 2/EORTC 08012 multicentre randomised trial and update of systematic review.
      ].
      Explanation—Typically, the introduction consists of free flowing text, in which authors explain the scientific background and rationale for their trial, and its general outline. It may also be appropriate to include here the objectives of the trial (see item 2b). The rationale may be explanatory (for example, to assess the possible influence of a drug on renal function) or pragmatic (for example, to guide practice by comparing the benefits and harms of two treatments). Authors should report any evidence of the benefits and harms of active interventions included in a trial and should suggest a plausible explanation for how the interventions might work, if this is not obvious [
      • Sandler A.D.
      • Sutton K.A.
      • DeWeese J.
      • Girardi M.A.
      • Sheppard V.
      • Bodfish J.W.
      Lack of benefit of a single dose of synthetic human secretin in the treatment of autism and pervasive developmental disorder.
      ].
      The Declaration of Helsinki states that biomedical research involving people should be based on a thorough knowledge of the scientific literature [

      World Medical Association. Declaration of Helsinki: ethical principle for medical research involving human subjects. 59th WMA General Assembly, Seoul 2008; www.wma.net/e/policy/b3.htm (accessed 2 June 2009).

      ]. That is, it is unethical to expose humans unnecessarily to the risks of research. Some clinical trials have been shown to have been unnecessary because the question they addressed had been or could have been answered by a systematic review of the existing literature [
      • Lau J.
      • Antman E.M.
      • Jimenez-Silva J.
      • Kupelnick B.
      • Mosteller F.
      • Chalmers T.C.
      Cumulative meta-analysis of therapeutic trials for myocardial infarction.
      ,
      • Fergusson D.
      • Glass K.C.
      • Hutton B.
      • Shapiro S.
      Randomized controlled trials of aprotinin in cardiac surgery: could clinical equipoise have stopped the bleeding?.
      ]. Thus, the need for a new trial should be justified in the introduction. Ideally, it should include a reference to a systematic review of previous similar trials or a note of the absence of such trials [
      • Savulescu J.
      • Chalmers I.
      • Blunt J.
      Are research ethics committees behaving unethically? Some suggestions for improving performance and accountability.
      ].

      5.2.2 Item 2b. Specific objectives or 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”[
      • Sadler L.C.
      • Davison T.
      • McCowan L.M.
      A randomised controlled trial and meta-analysis of active management of labour.
      ].
      Explanation—Objectives are the questions that the trial was designed to answer. They often relate to the efficacy of a particular therapeutic or preventive intervention. Hypotheses are pre-specified 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 differentiated. Most reports of RCTs provide adequate information about trial objectives and hypotheses [
      • Bath F.J.
      • Owen V.E.
      • Bath P.M.
      Quality of full and final publications reporting acute stroke trials: a systematic review.
      ].

      5.3 Methods

      5.3.1 Item 3a. Description of trial design (such as parallel, factorial) including allocation ratio

      Example—“This was a multicenter, stratified (6 to 11 years and 12 to 17 years of age, with imbalanced randomisation [2:1]), double-blind, placebo-controlled, parallel-group study conducted in the United States (41 sites)”[
      • Blumer J.L.
      • Findling R.L.
      • Shih W.J.
      • Soubrane C.
      • Reed M.D.
      Controlled clinical trial of zolpidem for the treatment of insomnia associated with attention-deficit/hyperactivity disorder in children 6 to 17 years of age.
      ].
      Explanation—The word “design” is often used to refer to all aspects of how a trial is set up, but it also has a narrower interpretation. Many specific aspects of the broader trial design, including details of randomisation and blinding, are addressed elsewhere in the CONSORT checklist. Here we seek information on the type of trial, such as parallel group or factorial, and the conceptual framework, such as superiority or non-inferiority, and other related issues not addressed elsewhere in the checklist.
      The CONSORT statement focuses mainly on trials with participants individually randomised to one of two “parallel” groups. In fact, little more than half of published trials have such a design [
      • Chan A.W.
      • Altman D.G.
      Epidemiology and reporting of randomised trials published in PubMed journals.
      ]. The main alternative designs are multi-arm parallel, crossover, cluster [
      • Campbell M.K.
      • Elbourne D.R.
      • Altman D.G.
      CONSORT statement: extension to cluster randomised trials.
      ], and factorial designs. Also, most trials are set to identify the superiority of a new intervention, if it exists, but others are designed to assess non-inferiority or equivalence [
      • Piaggio G.
      • Elbourne D.R.
      • Altman D.G.
      • Pocock S.J.
      • Evans S.J.
      Reporting of noninferiority and equivalence randomized trials: an extension of the CONSORT statement.
      ]. It is important that researchers clearly describe these aspects of their trial, including the unit of randomisation (such as patient, GP practice, lesion). It is desirable also to include these details in the abstract (see item 1b).
      If a less common design is employed, authors are encouraged to explain their choice, especially as such designs may imply the need for a larger sample size or more complex analysis and interpretation.
      Although most trials use equal randomisation (such as 1:1 for two groups), it is helpful to provide the allocation ratio explicitly. For drug trials, specifying the phase of the trial (I-IV) may also be relevant.

      5.3.2 Item 3b. Important changes to methods after trial commencement (such as eligibility criteria), with reasons

      Example—“Patients were randomly assigned to one of six parallel groups, initially in 1:1:1:1:1:1 ratio, to receive either one of five otamixaban … regimens … or an active control of unfractionated heparin … an independent Data Monitoring Committee reviewed unblinded data for patient safety; no interim analyses for efficacy or futility were done. During the trial, this committee recommended that the group receiving the lowest dose of otamixaban (0·035 mg/kg/h) be discontinued because of clinical evidence of inadequate anticoagulation. The protocol was immediately amended in accordance with that recommendation, and participants were subsequently randomly assigned in 2:2:2:2:1 ratio to the remaining otamixaban and control groups, respectively”[
      • Sabatine M.S.
      • Antman E.M.
      • Widimsky P.
      • Ebrahim I.O.
      • Kiss R.G.
      • Saaiman A.
      • et al.
      Otamixaban for the treatment of patients with non-ST-elevation acute coronary syndromes (SEPIA-ACS1 TIMI 42): a randomised, double-blind, active-controlled, phase 2 trial.
      ].
      Explanation—A few trials may start without any fixed plan (that is, are entirely exploratory), but the most will have a protocol that specifies in great detail how the trial will be conducted. There may be deviations from the original protocol, as it is impossible to predict every possible change in circumstances during the course of a trial. Some trials will therefore have important changes to the methods after trial commencement.
      Changes could be due to external information becoming available from other studies, or internal financial difficulties, or could be due to a disappointing recruitment rate. Such protocol changes should be made without breaking the blinding on the accumulating data on participants’ outcomes. In some trials, an independent data monitoring committee will have as part of its remit the possibility of recommending protocol changes based on seeing unblinded data. Such changes might affect the study methods (such as changes to treatment regimens, eligibility criteria, randomisation ratio, or duration of follow-up) or trial conduct (such as dropping a centre with poor data quality) [
      • Grant A.M.
      • Altman D.G.
      • Babiker A.B.
      • Campbell M.K.
      • Clemens F.J.
      • Darbyshire J.H.
      • et al.
      Issues in data monitoring and interim analysis of trials.
      ].
      Some trials are set up with a formal “adaptive” design. There is no universally accepted definition of these designs, but a working definition might be “a multistage study design that uses accumulating data to decide how to modify aspects of the study without undermining the validity and integrity of the trial”[
      • Gallo P.
      • Krams M.
      PhRMA Working Group on adaptive designs, “White Paper.”.
      ]. The modifications are usually to the sample sizes and the number of treatment arms and can lead to decisions being made more quickly and with more efficient use of resources. There are, however, important ethical, statistical, and practical issues in considering such a design [
      • Brown C.H.
      • Ten Have T.R.
      • Jo B.
      • Dagne G.
      • Wyman P.A.
      • Muthen B.
      • et al.
      Adaptive designs for randomized trials in public health.
      ,
      • Kelly P.J.
      • Sooriyarachchi M.R.
      • Stallard N.
      • Todd S.
      A practical comparison of group-sequential and adaptive designs.
      ].
      Whether the modifications are explicitly part of the trial design or in response to changing circumstances, it is essential that they are fully reported to help the reader interpret the results. Changes from protocols are not currently well reported. A review of comparisons with protocols showed that about half of journal articles describing RCTs had an unexplained discrepancy in the primary outcomes [
      • Dwan K.
      • Altman D.G.
      • Arnaiz J.A.
      • Bloom J.
      • Chan A.W.
      • Cronin E.
      • et al.
      Systematic review of the empirical evidence of study publication bias and outcome reporting bias.
      ]. Frequent unexplained discrepancies have also been observed for details of randomisation, blinding [
      • Pildal J.
      • Chan A.W.
      • Hrobjartsson A.
      • Forfang E.
      • Altman D.G.
      • Gotzsche P.C.
      Comparison of descriptions of allocation concealment in trial protocols and the published reports: cohort study.
      ], and statistical analyses [
      • Chan A.W.
      • Hrobjartsson A.
      • Jorgensen K.J.
      • Gotzsche P.C.
      • Altman D.G.
      Discrepancies in sample size calculations and data analyses reported in randomised trials: comparison of publications with protocols.
      ].

      5.3.3 Item 4a. Eligibility criteria for participants

      Example—“Eligible participants were all adults aged 18 or over with HIV who met the eligibility criteria for antiretroviral therapy according to the Malawian national HIV treatment guidelines (WHO clinical stage III or IV or any WHO stage with a CD4 count <250/mm3) and who were starting treatment with a BMI <18.5. Exclusion criteria were pregnancy and lactation or participation in another supplementary feeding programme”[
      • Ndekha M.J.
      • van Oosterhout J.J.
      • Zijlstra E.E.
      • Manary M.
      • Saloojee H.
      • Manary M.J.
      Supplementary feeding with either ready-to-use fortified spread or corn-soy blend in wasted adults starting antiretroviral therapy in Malawi: randomised, investigator blinded, controlled trial.
      ].
      Explanation—A comprehensive description of the eligibility criteria used to select the trial participants is needed to help readers interpret the study. In particular, a clear understanding of these criteria is one of several elements required to judge to whom the results of a trial apply—that is, the trial's generalisability (applicability) and relevance to clinical or public health practice (see item 21) [
      • Rothwell P.M.
      External validity of randomised controlled trials: “to whom do the results of this trial apply?”.
      ]. A description of the method of recruitment, such as by referral or self selection (for example, through advertisements), is also important in this context. Because they are applied before randomisation, eligibility criteria do not affect the internal validity of a trial, but they are central to its external validity.
      Typical and widely accepted selection criteria relate to the nature and stage of the disease being studied, the exclusion of persons thought to be particularly vulnerable to harm from the study intervention, and to issues required to ensure that the study satisfies legal and ethical norms. Informed consent by study participants, for example, is typically required in intervention studies. The common distinction between inclusion and exclusion criteria is unnecessary; the same criterion can be phrased to include or exclude participants [
      • Fuks A.
      • Weijer C.
      • Freedman B.
      • Shapiro S.
      • Skrutkowska M.
      • Riaz A.
      A study in contrasts: eligibility criteria in a twenty-year sample of NSABP and POG clinical trials. National Surgical Adjuvant Breast and Bowel Program. Pediatric Oncology Group.
      ].
      Despite their importance, eligibility criteria are often not reported adequately. For example, eight published trials leading to clinical alerts by the National Institutes of Health specified an average of 31 eligibility criteria in their protocols, but only 63% of the criteria were mentioned in the journal articles, and only 19% were mentioned in the clinical alerts [
      • Shapiro S.H.
      • Weijer C.
      • Freedman B.
      Reporting the study populations of clinical trials. Clear transmission or static on the line?.
      ]. Similar deficiencies were found for HIV clinical trials [
      • Gandhi M.
      • Ameli N.
      • Bacchetti P.
      • Sharp G.B.
      • French A.L.
      • Young M.
      • et al.
      Eligibility criteria for HIV clinical trials and generalizability of results: the gap between published reports and study protocols.
      ]. Among 364 reports of RCTs in surgery, 25% did not specify any eligibility criteria [
      • Hall J.C.
      • Mills B.
      • Nguyen H.
      • Hall J.L.
      Methodologic standards in surgical trials.
      ].

      5.3.4 Item 4b. Settings and locations where the data were collected

      Example—“The study took place at the antiretroviral therapy clinic of Queen Elizabeth Central Hospital in Blantyre, Malawi, from January 2006 to April 2007. Blantyre is the major commercial city of Malawi, with a population of 1 000 000 and an estimated HIV prevalence of 27% in adults in 2004”[
      • Ndekha M.J.
      • van Oosterhout J.J.
      • Zijlstra E.E.
      • Manary M.
      • Saloojee H.
      • Manary M.J.
      Supplementary feeding with either ready-to-use fortified spread or corn-soy blend in wasted adults starting antiretroviral therapy in Malawi: randomised, investigator blinded, controlled trial.
      ].
      Explanation—Along with the eligibility criteria for participants (see item 4a) and the description of the interventions (see item 5), information on the settings and locations is crucial to judge the applicability and generalisability of a trial. Were participants recruited from primary, secondary, or tertiary health care or from the community? Healthcare institutions vary greatly in their organisation, experience, and resources and the baseline risk for the condition under investigation. Other aspects of the setting (including the social, economic, and cultural environment and the climate) may also affect a study's external validity.
      Authors should report the number and type of settings and describe the care providers involved. They should report the locations in which the study was carried out, including the country, city if applicable, 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 centres (“multicentre trials”). This description should provide enough information so that readers can judge whether the results of the trial could be relevant to their own setting. The environment in which the trial is conducted may differ considerably from the setting in which the trial's results are later used to guide practice and policy [
      • Rothwell P.M.
      External validity of randomised controlled trials: “to whom do the results of this trial apply?”.
      ,
      • Weiss N.S.
      • Koepsell T.D.
      • Psaty B.M.
      Generalizability of the results of randomized trials.
      ]. Authors should also report any other information about the settings and locations that could have influenced the observed results, such as problems with transportation that might have affected patient participation or delays in administering interventions.

      5.3.5 Item 5. The interventions for each group with sufficient details to allow replication, including how and when they were actually administered

      Examples—“In POISE, patients received the first dose of the study drug (ie, oral extended-release metoprolol 100 mg or matching placebo) 2–4 h before surgery. Study drug administration required a heart rate of 50 bpm or more and a systolic blood pressure of 100 mm Hg or greater; these haemodynamics were checked before each administration. If, at any time during the first 6 h after surgery, heart rate was 80 bpm or more and systolic blood pressure was 100 mm Hg or higher, patients received their first postoperative dose (extended-release metoprolol 100 mg or matched placebo) orally. If the study drug was not given during the first 6 h, patients received their first postoperative dose at 6 h after surgery. 12 h after the first postoperative dose, patients started taking oral extended-release metoprolol 200 mg or placebo every day for 30 days. If a patient's heart rate was consistently below 45 bpm or their systolic blood pressure dropped below 100 mm Hg, study drug was withheld until their heart rate or systolic blood pressure recovered; the study drug was then restarted at 100 mg once daily. Patients whose heart rate was consistently 45–49 bpm and systolic blood pressure exceeded 100 mm Hg delayed taking the study drug for 12 h”[
      • Devereaux P.J.
      • Yang H.
      • Yusuf S.
      • Guyatt G.
      • Leslie K.
      • Villar J.C.
      • et al.
      Effects of extended-release metoprolol succinate in patients undergoing non-cardiac surgery (POISE trial): a randomised controlled trial.
      ].
      “Patients were randomly assigned to receive a custom-made neoprene splint to be worn at night or to usual care. The splint was a rigid rest orthosis recommended for use only at night. It covered the base of the thumb and the thenar eminence but not the wrist (Figure 1). Splints were made by 3 trained occupational therapists, who adjusted the splint for each patient so that the first web could be opened and the thumb placed in opposition with the first long finger. Patients were encouraged to contact the occupational therapist if they felt that the splint needed adjustment, pain increased while wearing the splint, or they had adverse effects (such as skin erosion). Because no treatment can be considered the gold standard in this situation, patients in the control and intervention groups received usual care at the discretion of their physician (general practitioner or rheumatologist). We decided not to use a placebo because, to our knowledge, no placebo for splinting has achieved successful blinding of patients, as recommended”[
      • Rannou F.
      • Dimet J.
      • Boutron I.
      • Baron G.
      • Fayad F.
      • Mace Y.
      • et al.
      Splint for base-of-thumb osteoarthritis: a randomized trial.
      ].
      Explanation—Authors should describe each intervention thoroughly, including control interventions. The description should allow a clinician wanting to use the intervention to know exactly how to administer the intervention that was evaluated in the trial [
      • Glasziou P.
      • Meats E.
      • Heneghan C.
      • Shepperd S.
      What is missing from descriptions of treatment in trials and reviews?.
      ]. For a drug intervention, information would include the drug name, dose, method of administration (such as oral, intravenous), timing and duration of administration, conditions under which interventions are withheld, and titration regimen if applicable. If the control group is to receive “usual care” it is important to describe thoroughly what that constitutes. If the control group or intervention group is to receive a combination of interventions the authors should provide a thorough description of each intervention, an explanation of the order in which the combination of interventions are introduced or withdrawn, and the triggers for their introduction if applicable.
      Specific extensions of the CONSORT statement address the reporting of non-pharmacologic and herbal interventions and their particular reporting requirements (such as expertise, details of how the interventions were standardised) [
      • Boutron I.
      • Moher D.
      • Altman D.G.
      • Schulz K.F.
      • Ravaud P.
      Extending the CONSORT statement to randomized trials of nonpharmacologic treatment: explanation and elaboration.
      ,
      • Gagnier J.J.
      • Boon H.
      • Rochon P.
      • Moher D.
      • Barnes J.
      • Bombardier C.
      Reporting randomized, controlled trials of herbal interventions: an elaborated CONSORT statement.
      ]. We recommend readers consult the statements for non-pharmacologic and herbal interventions as appropriate.

      5.3.6 Item 6a. Completely defined pre-specified primary and secondary outcome measures, including how and when they were assessed

      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”[
      • Mease P.J.
      • Goffe B.S.
      • Metz J.
      • VanderStoep A.
      • Finck B.
      • Burge D.J.
      Etanercept in the treatment of psoriatic arthritis and psoriasis: a randomised trial.
      ].
      Explanation—All RCTs assess response variables, or outcomes (end points), for which the groups are compared. Most trials have several outcomes, some of which are of more interest than others. The primary outcome measure is the pre-specified outcome considered to be of greatest importance to relevant stakeholders (such a patients, policy makers, clinicians, funders) and is usually the one used in the sample size calculation (see item 7). Some trials may have more than one primary outcome. Having several primary outcomes, however, incurs the problems 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 (additional outcomes). There may be several secondary outcomes, which often include unanticipated or unintended effects of the intervention (see item 19), although harms should always be viewed as important whether they are labelled primary or secondary.
      All outcome measures, whether primary or secondary, should be identified and completely defined. The principle here is that the information provided should be sufficient to allow others to use the same outcomes [
      • Glasziou P.
      • Meats E.
      • Heneghan C.
      • Shepperd S.
      What is missing from descriptions of treatment in trials and reviews?.
      ]. When outcomes are assessed at several time points after randomisation, authors should also indicate the pre-specified time point of primary interest. For many non-pharmacological interventions it is helpful to specify who assessed outcomes (for example, if special skills are required to do so) and how many assessors there were [
      • Boutron I.
      • Moher D.
      • Altman D.G.
      • Schulz K.F.
      • Ravaud P.
      Extending the CONSORT statement to randomized trials of nonpharmacologic treatment: explanation and elaboration.
      ].
      Where available and appropriate, the use of previously developed and validated scales or consensus guidelines should be reported [
      • McDowell I.
      • Newell C.
      Measuring health: a guide to rating scales and questionnaires.
      ,
      • Streiner D.
      • Norman C.
      Health measurement scales: a practical guide to their development and use.
      ], both to enhance quality of measurement and to assist in comparison with similar studies [
      • Clarke M.
      Standardising outcomes for clinical trials and systematic reviews.
      ]. For example, assessment of quality of life is likely to be improved by using a validated instrument [
      • Sanders C.
      • Egger M.
      • Donovan J.
      • Tallon D.
      • Frankel S.
      Reporting on quality of life in randomised controlled trials: bibliographic study.
      ]. Authors should indicate the provenance and properties of scales.
      More than 70 outcomes were used in 196 RCTs of non-steroidal anti-inflammatory drugs for rheumatoid arthritis [
      • Gotzsche P.C.
      Methodology and overt and hidden bias in reports of 196 double-blind trials of nonsteroidal antiinflammatory drugs in rheumatoid arthritis.
      ], and 640 different instruments had been used in 2000 trials in schizophrenia, of which 369 had been used only once [
      • Thornley B.
      • Adams C.
      Content and quality of 2000 controlled trials in schizophrenia over 50 years.
      ]. Investigation of 149 of those 2000 trials showed that unpublished scales were a source of bias. In non-pharmacological trials, a third of the claims of treatment superiority based on unpublished scales would not have been made if a published scale had been used [
      • Marshall M.
      • Lockwood A.
      • Bradley C.
      • Adams C.
      • Joy C.
      • Fenton M.
      Unpublished rating scales: a major source of bias in randomised controlled trials of treatments for schizophrenia.
      ]. Similar data have been reported elsewhere [
      • Jadad A.R.
      • Boyle M.
      • Cunnigham C.
      • Kim M.
      • Schachar R.
      Treatment of Attention-Deficit/Hyperactivity Disorder. Evidence Report/Technology Assessment No. 11.
      ,

      Schachter HM, Pham B, King J, Langford S, Moher D. The efficacy and safety of methylphenidate in attention deficit disorder: A systematic review and meta-analyis. Prepared for the Therapeutics Inititiative, Vancouver, B.C., and the British Columbia Ministry for Children and Families, 2000.

      ]. Only 45% of a cohort of 519 RCTs published in 2000 specified the primary outcome [
      • Chan A.W.
      • Altman D.G.
      Epidemiology and reporting of randomised trials published in PubMed journals.
      ]; this compares with 53% for a similar cohort of 614 RCTs published in 2006 [
      • Hopewell S.
      • Dutton S.
      • Yu L.M.
      • Chan A.W.
      • Altman D.G.
      The quality of reports of randomised trials in 2000 and 2006: comparative study of articles indexed in PubMed.
      ].

      5.3.7 Item 6b. Any changes to trial outcomes after the trial commenced, with reasons

      Example—“The original primary endpoint was all-cause mortality, but, during a masked analysis, the data and safety monitoring board noted that overall mortality was lower than had been predicted and that the study could not be completed with the sample size and power originally planned. The steering committee therefore decided to adopt co-primary endpoints of all-cause mortality (the original primary endpoint), together with all-cause mortality or cardiovascular hospital admissions (the first prespecified secondary endpoint)”[
      • Dargie H.J.
      Effect of carvedilol on outcome after myocardial infarction in patients with left-ventricular dysfunction: the CAPRICORN randomised trial.
      ].
      Explanation—There are many reasons for departures from the initial study protocol (see item 24). Authors should report all major changes to the protocol, including unplanned changes to eligibility criteria, interventions, examinations, data collection, methods of analysis, and outcomes. Such information is not always reported.
      As indicated earlier (see item 6a), most trials record multiple outcomes, with the risk that results will be reported for only a selected subset (see item 17). Pre-specification and reporting of primary and secondary outcomes (see item 6a) should remove such a risk. In some trials, however, circumstances require a change in the way an outcome is assessed or even, as in the example above, a switch to a different outcome. For example, there may be external evidence from other trials or systematic reviews suggesting the end point might not be appropriate, or recruitment or the overall event rate in the trial may be lower than expected [
      • Dargie H.J.
      Effect of carvedilol on outcome after myocardial infarction in patients with left-ventricular dysfunction: the CAPRICORN randomised trial.
      ]. Changing an end point based on unblinded data is much more problematic, although it may be specified in the context of an adaptive trial design [
      • Gallo P.
      • Krams M.
      PhRMA Working Group on adaptive designs, “White Paper.”.
      ]. Authors should identify and explain any such changes. Likewise, any changes after the trial began of the designation of outcomes as primary or secondary should be reported and explained.
      A comparison of protocols and publications of 102 randomised trials found that 62% of trials reports had at least one primary outcome that was changed, introduced, or omitted compared with the protocol [
      • Chan A.W.
      • Hrobjartsson A.
      • Haahr M.T.
      • Gotzsche P.C.
      • Altman D.G.
      Empirical evidence for selective reporting of outcomes in randomized trials: comparison of protocols to published articles.
      ]. Primary outcomes also differed between protocols and publications for 40% of a cohort of 48 trials funded by the Canadian Institutes of Health Research [
      • Chan A.W.
      • Krleza-Jeric K.
      • Schmid I.
      • Altman D.G.
      Outcome reporting bias in randomized trials funded by the Canadian Institutes of Health Research.
      ]. Not one of the subsequent 150 trial reports mentioned, let alone explained, changes from the protocol. Similar results from other studies have been reported recently in a systematic review of empirical studies examining outcome reporting bias [
      • Dwan K.
      • Altman D.G.
      • Arnaiz J.A.
      • Bloom J.
      • Chan A.W.
      • Cronin E.
      • et al.
      Systematic review of the empirical evidence of study publication bias and outcome reporting bias.
      ].

      5.3.8 Item 7a. How sample size was determined

      Examples—“To detect a reduction in PHS (postoperative hospital stay) of 3 days (SD 5 days), which is in agreement with the study of Lobo et al [
      • Hopewell S.
      • Dutton S.
      • Yu L.M.
      • Chan A.W.
      • Altman D.G.
      The quality of reports of randomised trials in 2000 and 2006: comparative study of articles indexed in PubMed.
      ] with a two-sided 5% significance level and a power of 80%, a sample size of 50 patients per group was necessary, given an anticipated dropout rate of 10%. To recruit this number of patients a 12-month inclusion period was anticipated”[
      • Vermeulen H.
      • Hofland J.
      • Legemate D.A.
      • Ubbink D.T.
      Intravenous fluid restriction after major abdominal surgery: a randomized blinded clinical trial.
      ].
      “Based on an expected incidence of the primary composite endpoint of 11% at 2.25 years in the placebo group, we calculated that we would need 950 primary endpoint events and a sample size of 9650 patients to give 90% power to detect a significant difference between ivabradine and placebo, corresponding to a 19% reduction of relative risk (with a two-sided type 1 error of 5%). We initially designed an event-driven trial, and planned to stop when 950 primary endpoint events had occurred. However, the incidence of the primary endpoint was higher than predicted, perhaps because of baseline characteristics of the recruited patients, who had higher risk than expected (e.g., lower proportion of NYHA class I and higher rates of diabetes and hypertension). We calculated that when 950 primary endpoint events had occurred, the most recently included patients would only have been treated for about 3 months. Therefore, in January 2007, the executive committee decided to change the study from being event-driven to time-driven, and to continue the study until the patients who were randomised last had been followed up for 12 months. This change did not alter the planned study duration of 3 years”[
      • Fox K.
      • Ford I.
      • Steg P.G.
      • Tendera M.
      • Ferrari R.
      Ivabradine for patients with stable coronary artery disease and left-ventricular systolic dysfunction (BEAUTIFUL): a randomised, double-blind, placebo-controlled trial.
      ].
      Explanation—For scientific and ethical reasons, the sample size for a trial needs to be planned carefully, with a balance between medical and statistical considerations. Ideally, a study should be large enough to have a high probability (power) of detecting as statistically significant a clinically important difference of a given size if such a difference exists. The size of effect deemed important is inversely related to the sample size necessary to detect it; that is, large samples are necessary to detect small differences. Elements of the sample size calculation are (1) the estimated outcomes in each group (which implies the clinically important target difference between the intervention groups); (2) the α (type I) error level; (3) the statistical power (or the β (type II) error level); and (4), for continuous outcomes, the standard deviation of the measurements [
      • Campbell M.J.
      • Julious S.A.
      • Altman D.G.
      Estimating sample sizes for binary, ordered categorical, and continuous outcomes in two group comparisons.
      ]. The interplay of these elements and their reporting will differ for cluster trials [
      • Campbell M.K.
      • Elbourne D.R.
      • Altman D.G.
      CONSORT statement: extension to cluster randomised trials.
      ] and non-inferiority and equivalence trials [
      • Piaggio G.
      • Elbourne D.R.
      • Altman D.G.
      • Pocock S.J.
      • Evans S.J.
      Reporting of noninferiority and equivalence randomized trials: an extension of the CONSORT statement.
      ].
      Authors should indicate how the sample size was determined. If a formal power calculation was used, the authors should identify the primary outcome on which the calculation was based (see item 6a), all the quantities used in the calculation, and the resulting target sample size per study group. It is preferable to quote the expected result in the control group and the difference between the groups one would not like to overlook. Alternatively, authors could present the percentage with the event or mean for each group used in their calculations. Details should be given of any allowance made for attrition or non-compliance during the study.
      Some methodologists have written that so called underpowered trials may be acceptable because they could ultimately be combined in a systematic review and meta-analysis [
      • Guyatt G.H.
      • Mills E.J.
      • Elbourne D.
      In the era of systematic reviews, does the size of an individual trial still matter.
      ,
      • Schulz K.F.
      • Grimes D.A.
      Sample size calculations in randomised trials: mandatory and mystical.
      ,
      • Halpern S.D.
      • Karlawish J.H.
      • Berlin J.A.
      The continuing unethical conduct of underpowered clinical trials.
      ], and because some information is better than no information. Of note, important caveats apply—such as the trial should be unbiased, reported properly, and published irrespective of the results, thereby becoming available for meta-analysis [
      • Schulz K.F.
      • Grimes D.A.
      Sample size calculations in randomised trials: mandatory and mystical.
      ]. On the other hand, many medical researchers worry that underpowered trials with indeterminate results will remain unpublished and insist that all trials should individually have “sufficient power.” This debate will continue, and members of the CONSORT Group have varying views. Critically however, the debate and those views are immaterial to reporting a trial. Whatever the power of a trial, authors need to properly report their intended size with all their methods and assumptions [
      • Schulz K.F.
      • Grimes D.A.
      Sample size calculations in randomised trials: mandatory and mystical.
      ]. That transparently reveals the power of the trial to readers and gives them a measure by which to assess whether the trial attained its planned size.
      In some trials, interim analyses are used to help decide whether to stop early or to continue recruiting sometimes beyond the planned trial end (see item 7b). If the actual sample size differed from the originally intended sample size for some other reason (for example, because of poor recruitment or revision of the target sample size), the explanation should be given.
      Reports of studies with small samples frequently include the erroneous conclusion that the intervention groups do not differ, when in fact too few patients were studied to make such a claim [
      • Altman D.G.
      • Bland J.M.
      Absence of evidence is not evidence of absence.
      ]. Reviews of published trials have consistently found that a high proportion of trials have low power to detect clinically meaningful treatment effects [
      • Moher D.
      • Dulberg C.S.
      • Wells G.A.
      Statistical power, sample size, and their reporting in randomized controlled trials.
      ,
      • Freiman J.A.
      • Chalmers T.C.
      • Smith Jr., H.
      • Kuebler R.R.
      The importance of beta, the type II error and sample size in the design and interpretation of the randomized control trial. Survey of 71 "negative" trials.
      ,
      • Charles P.
      • Giraudeau B.
      • Dechartres A.
      • Baron G.
      • Ravaud P.
      Reporting of sample size calculation in randomised controlled trials: review.
      ]. In reality, small but clinically meaningful true differences are much more likely than large differences to exist, but large trials are required to detect them [
      • Yusuf S.
      • Collins R.
      • Peto R.
      Why do we need some large, simple randomized trials?.
      ].
      In general, the reported sample sizes in trials seem small. The median sample size was 54 patients in 196 trials in arthritis [
      • Gotzsche P.C.
      Methodology and overt and hidden bias in reports of 196 double-blind trials of nonsteroidal antiinflammatory drugs in rheumatoid arthritis.
      ], 46 patients in 73 trials in dermatology [
      • Adetugbo K.
      • Williams H.
      How well are randomized controlled trials reported in the dermatology literature?.
      ], and 65 patients in 2000 trials in schizophrenia [
      • Thornley B.
      • Adams C.
      Content and quality of 2000 controlled trials in schizophrenia over 50 years.
      ]. These small sample sizes are consistent with those of a study of 519 trials indexed in PubMed in December 2000 [
      • Chan A.W.
      • Altman D.G.
      Epidemiology and reporting of randomised trials published in PubMed journals.
      ] and a similar cohort of trials (n=616) indexed in PubMed in 2006 [
      • Hopewell S.
      • Dutton S.
      • Yu L.M.
      • Chan A.W.
      • Altman D.G.
      The quality of reports of randomised trials in 2000 and 2006: comparative study of articles indexed in PubMed.
      ], where the median number of patients recruited for parallel group trials was 80 across both years. Moreover, many reviews have found that few authors report how they determined the sample size [
      • Adetugbo K.
      • Williams H.
      How well are randomized controlled trials reported in the dermatology literature?.
      ,
      • Pocock S.J.
      • Hughes M.D.
      • Lee R.J.
      Statistical problems in the reporting of clinical trials. A survey of three medical journals.
      ,
      • Altman D.G.
      • Dore C.J.
      Randomisation and baseline comparisons in clinical trials.
      ,
      • Thornley B.
      • Adams C.
      Content and quality of 2000 controlled trials in schizophrenia over 50 years.
      ,
      • Charles P.
      • Giraudeau B.
      • Dechartres A.
      • Baron G.
      • Ravaud P.
      Reporting of sample size calculation in randomised controlled trials: review.
      ].
      There is little merit in a post hoc calculation of statistical power using the results of a trial; the power is then appropriately indicated by confidence intervals (see item 17) [
      • Goodman S.N.
      • Berlin J.A.
      The use of predicted confidence intervals when planning experiments and the misuse of power when interpreting results.
      ].

      5.3.9 Item 7b. When applicable, explanation of any interim analyses and stopping guidelines

      Examples—“Two interim analyses were performed during the trial. The levels of significance maintained an overall P value of 0.05 and were calculated according to the O'Brien-Fleming stopping boundaries. This final analysis used a Z score of 1.985 with an associated P value of 0.0471”[
      • Galgiani J.N.
      • Catanzaro A.
      • Cloud G.A.
      • Johnson R.H.
      • Williams P.L.
      • Mirels L.F.
      • et al.
      Comparison of oral fluconazole and itraconazole for progressive, nonmeningeal coccidioidomycosis. A randomized, double-blind trial. Mycoses Study Group.
      ].
      “An independent data and safety monitoring board periodically reviewed the efficacy and safety data. Stopping rules were based on modified Haybittle-Peto boundaries of 4 SD in the first half of the study and 3 SD in the second half for efficacy data, and 3 SD in the first half of the study and 2 SD in the second half for safety data. Two formal interim analyses of efficacy were performed when 50% and 75% of the expected number of primary events had accrued; no correction of the reported P value for these interim tests was performed”[
      • Connolly S.J.
      • Pogue J.
      • Hart R.G.
      • Hohnloser S.H.
      • Pfeffer M.
      • Chrolavicius S.
      • et al.
      Effect of clopidogrel added to aspirin in patients with atrial fibrillation.
      ].
      Explanation—Many trials recruit participants over a long period. If an intervention is working particularly well or badly, the study may need to be ended early for ethical reasons. This concern can be addressed by examining results as the data accumulate, preferably by an independent data monitoring committee. However, performing multiple statistical examinations of accumulating data without appropriate correction can lead to erroneous results and interpretations [
      • Geller N.L.
      • Pocock S.J.
      Interim analyses in randomized clinical trials: ramifications and guidelines for practitioners.
      ]. If the accumulating data from a trial are examined at five interim analyses that use a P value of 0.05, the overall false positive rate is nearer to 19% than to the nominal 5%.
      Several group sequential statistical methods are available to adjust for multiple analyses [
      • Berry D.A.
      Interim analyses in clinical trials: classical vs. Bayesian approaches.
      ,
      • Pocock S.J.
      When to stop a clinical trial.
      ,
      • DeMets D.L.
      • Pocock S.J.
      • Julian D.G.
      The agonising negative trend in monitoring of clinical trials.
      ], and their use should be pre-specified in the trial protocol. With these methods, data are compared at each interim analysis, and a P value less than the critical value specified by the group sequential method indicates statistical significance. Some trialists use group sequential methods as an aid to decision making [
      • Buyse M.
      Interim analyses, stopping rules and data monitoring in clinical trials in Europe.
      ], whereas others treat them as a formal stopping rule (with the intention that the trial will cease if the observed P value is smaller than the critical value).
      Authors should report whether they or a data monitoring committee took multiple “looks” at the data and, if so, how many there were, what triggered them, the statistical methods used (including any formal stopping rule), and whether they were planned before the start of the trial, before the data monitoring committee saw any interim data by allocation, or some time thereafter. This information is often not included in published trial reports [
      • Sydes M.R.
      • Altman D.G.
      • Babiker A.B.
      • Parmar M.K.
      • Spiegelhalter D.J.
      Reported use of data monitoring committees in the main published reports of randomized controlled trials: a cross-sectional study.
      ], even in trials that report stopping earlier than planned [
      • Montori V.M.
      • Devereaux P.J.
      • Adhikari N.K.
      • Burns K.E.
      • Eggert C.H.
      • Briel M.
      • et al.
      Randomized trials stopped early for benefit: a systematic review.
      ].

      5.3.10 Item 8a. Method used to generate the random allocation sequence

      Examples—“Independent pharmacists dispensed either active or placebo inhalers according to a computer generated randomisation list”[
      • Bolliger C.T.
      • Zellweger J.P.
      • Danielsson T.
      • van Biljon X.
      • Robidou A.
      • Westin A.
      • et al.
      Smoking reduction with oral nicotine inhalers: double blind, randomised clinical trial of efficacy and safety.
      ].
      “For allocation of the participants, a computer-generated list of random numbers was used”[
      • Coutinho I.C.
      • Ramos de Amorim M.M.
      • Katz L.
      • Bandeira de Ferraz A.A.
      Uterine exteriorization compared with in situ repair at cesarean delivery: a randomized controlled trial.
      ].
      Explanation—Participants should be assigned to comparison groups in the trial on the basis of a chance (random) process characterised by unpredictability (see Box 1). Authors should provide sufficient information that the reader can assess the methods used to generate the random allocation sequence and the likelihood of bias in group assignment. It is important that information on the process of randomisation is included in the body of the main article and not as a separate supplementary file; where it can be missed by the reader.
      The term “random” has a precise technical meaning. With random allocation, each participant has a known probability of receiving each intervention before one is assigned, but the assigned intervention is determined by a chance process and cannot be predicted. However, “random” is often used inappropriately in the literature to describe trials in which non-random, deterministic allocation methods were used, such as alternation, hospital numbers, or date of birth. When investigators use such non-random methods, they should describe them precisely and should not use the term “random” or any variation of it. Even the term “quasi-random” is unacceptable for describing such trials. Trials based on non-random methods generally yield biased results [
      • Schulz K.F.
      • Chalmers I.
      • Hayes R.J.
      • Altman D.G.
      Empirical evidence of bias. Dimensions of methodological quality associated with estimates of treatment effects in controlled trials.
      ,
      • Moher D.
      CONSORT: an evolving tool to help improve the quality of reports of randomized controlled trials. Consolidated Standards of Reporting Trials.
      ,
      • Kjaergard L.L.
      • Villumsen J.
      • Gluud C.
      Quality of randomised clinical trials affects estimates of intervention efficacy.
      ,
      • Juni P.
      • Altman D.G.
      • Egger M.
      Assessing the quality of controlled clinical trials.
      ] Bias presumably arises from the inability to conceal these allocation systems adequately (see item 9).
      Many methods of sequence generation are adequate. However, readers cannot judge adequacy from such terms as “random allocation,” “randomisation,” or “random” without further elaboration. Authors should specify the method of sequence generation, such as a random-number table or a computerised random number generator. The sequence may be generated by the process of minimisation, a non-random but generally acceptable method (see Box 2).
      Randomisation and minimisation
      Simple randomisation—Pure randomisation based on a single allocation ratio is known as simple randomisation. Simple randomisation with a 1:1 allocation ratio is analogous to a coin toss, although we do not advocate coin tossing for randomisation in an RCT. “Simple” is somewhat of a misnomer. While other randomisation schemes sound complex and more sophisticated, in reality, simple randomisation is elegantly sophisticated in that it is more unpredictable and surpasses the bias prevention levels of all other alternatives.
      Restricted randomisation—Any randomised approach that is not simple randomisation. Blocked randomisation is the most common form. Other means of restricted randomisation include replacement, biased coin, and urn randomisation, although these are used much less frequently [
      • Schulz K.F.
      • Grimes D.A.
      The Lancet handbook of essential concepts in clinical research.
      ].
      Blocked randomisation—Blocking is used to ensure that comparison groups will be generated according to a predetermined ratio, usually 1:1 or groups of approximately the same size. Blocking can be used to ensure close balance of the numbers in each group at any time during the trial. For every block of eight participants, for example, four would be allocated to each arm of the trial [
      • Altman D.G.
      • Bland J.M.
      How to randomise.
      ]. Improved balance comes at the cost of reducing the unpredictability of the sequence. Although the order of interventions varies randomly within each block, a person running the trial could deduce some of the next treatment allocations if he or she knew the block size [
      • Schulz K.F.
      Subverting randomization in controlled trials.
      ]. Blinding the interventions, using larger block sizes, and randomly varying the block size can ameliorate this problem.
      Stratified randomisation—Stratification is used to ensure good balance of participant characteristics in each group. By chance, particularly in small trials, study groups may not be well matched for baseline characteristics, such as age and stage of disease. This weakens the trial's credibility [
      • Enas G.G.
      • Enas N.H.
      • Spradlin C.T.
      • Wilson M.G.
      • Wiltse C.G.
      Baseline comparability in clinical trials: prevention of poststudy anxiety.
      ]. Such imbalances can be avoided without sacrificing the advantages of randomisation. Stratification ensures that the numbers of participants receiving each intervention are closely balanced within each stratum. Stratified randomisation is achieved by performing a separate randomisation procedure within each of two or more subsets of participants (for example, those defining each study centre, age, or disease severity). Stratification by centre is common in multicentre trials. Stratification requires some form of restriction (such as blocking within strata). Stratification without blocking is ineffective.
      Minimisation—Minimisation ensures balance between intervention groups for several selected patient factors (such as age) [
      • Altman D.G.
      ,
      • Pocock S.J.
      Clinical trials: a practical approach.
      ]. The first patient is truly randomly allocated; for each subsequent participant, the treatment allocation that minimises the imbalance on the selected factors between groups at that time is identified. That allocation may then be used, or a choice may be made at random with a heavy weighting in favour of the intervention that would minimise imbalance (for example, with a probability of 0.8). The use of a random component is generally preferable. Minimisation has the advantage of making small groups closely similar in terms of participant characteristics at all stages of the trial. Minimisation offers the only acceptable alternative to randomisation, and some have argued that it is superior [
      • Treasure T.
      • MacRae K.D.
      Minimisation: the platinum standard for trials? Randomisation doesn't guarantee similarity of groups; minimisation does.
      ]. On the other hand, minimisation lacks the theoretical basis for eliminating bias on all known and unknown factors. Nevertheless, in general, trials that use minimisation are considered methodologically equivalent to randomised trials, even when a random element is not incorporated.
      In some trials, participants are intentionally allocated in unequal numbers to each intervention: for example, to gain more experience with a new procedure or to limit costs of the trial. In such cases, authors should report the randomisation ratio (for example, 2:1 or two treatment participants per each control participant) (see item 3a).
      In a representative sample of PubMed indexed trials in 2000, only 21% reported an adequate approach to random sequence generation [
      • Chan A.W.
      • Altman D.G.
      Epidemiology and reporting of randomised trials published in PubMed journals.
      ]; this increased to 34% for a similar cohort of PubMed indexed trials in 2006 [
      • Hopewell S.
      • Dutton S.
      • Yu L.M.
      • Chan A.W.
      • Altman D.G.
      The quality of reports of randomised trials in 2000 and 2006: comparative study of articles indexed in PubMed.
      ]. In more than 90% of these cases, researchers used a random number generator on a computer or a random number table.

      5.3.11 Item 8b. Type of randomisation; details of any restriction (such as blocking and block size)

      Examples—“Randomization sequence was created using Stata 9.0 (StataCorp, College Station, TX) statistical software and was stratified by center with a 1:1 allocation using random block sizes of 2, 4, and 6”[
      • Creinin M.D.
      • Meyn L.A.
      • Borgatta L.
      • Barnhart K.
      • Jensen J.
      • Burke A.E.
      • et al.
      Multicenter comparison of the contraceptive ring and patch: a randomized controlled trial.
      ].
      “Participants were randomly assigned following simple randomization procedures (computerized random numbers) to 1 of 2 treatment groups”[
      • Tate D.F.
      • Jackvony E.H.
      • Wing R.R.
      Effects of internet behavioral counseling on weight loss in adults at risk for type 2 diabetes: a randomized trial.
      ].
      Explanation—In trials of several hundred participants or more simple randomisation can usually be trusted to generate similar numbers in the two trial groups [
      • Lachin J.M.
      Properties of simple randomization in clinical trials.
      ] and to generate groups that are roughly comparable in terms of known and unknown prognostic variables [
      • Peto R.
      • Pike M.C.
      • Armitage P.
      • Breslow N.E.
      • Cox D.R.
      • Howard S.V.
      • et al.
      Design and analysis of randomized clinical trials requiring prolonged observation of each patient. I. Introduction and design.
      ]. For smaller trials (see item 7a)—and even for trials that are not intended to be small, as they may stop before reaching their target size—some restricted randomisation (procedures to help achieve balance between groups in size or characteristics) may be useful (see Box 2).
      It is important to indicate whether no restriction was used, by stating such or by stating that “simple randomisation” was done. Otherwise, the methods used to restrict the randomisation, along with the method used for random selection, should be specified. For block randomisation, authors should provide details on how the blocks were generated (for example, by using a permuted block design with a computer random number generator), the block size or sizes, and whether the block size was fixed or randomly varied. If the trialists became aware of the block size(s), that information should also be reported as such knowledge could lead to code breaking. Authors should specify whether stratification was used, and if so, which factors were involved (such as recruitment site, sex, disease stage), the categorisation cut-off values within strata, and the method used for restriction. Although stratification is a useful technique, especially for smaller trials, it is complicated to implement and may be impossible if many stratifying factors are used. If minimisation (see Box 2) was used, it should be explicitly identified, as should the variables incorporated into the scheme. If used, a random element should be indicated.
      Only 9% of 206 reports of trials in specialty journals [
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ] and 39% of 80 trials in general medical journals reported use of stratification [
      • Altman D.G.
      • Dore C.J.
      Randomisation and baseline comparisons in clinical trials.
      ]. In each case, only about half of the reports mentioned the use of restricted randomisation. However, these studies and that of Adetugbo and Williams [
      • Adetugbo K.
      • Williams H.
      How well are randomized controlled trials reported in the dermatology literature?.
      ] found that the sizes of the treatment groups in many trials were the same or quite similar, yet blocking or stratification had not been mentioned. One possible explanation for the close balance in numbers is underreporting of the use of restricted randomisation.

      5.3.12 Item 9. Mechanism used to implement the random allocation sequence (such as sequentially numbered containers), describing any steps taken to conceal the sequence until interventions were assigned

      Examples—“The doxycycline and placebo were in capsule form and identical in appearance. They were prepacked in bottles and consecutively numbered for each woman according to the randomisation schedule. Each woman was assigned an order number and received the capsules in the corresponding prepacked bottle”[
      • Sinei S.K.
      • Schulz K.F.
      • Lamptey P.R.
      • Grimes D.A.
      • Mati J.K.
      • Rosenthal S.M.
      • et al.
      Preventing IUCD-related pelvic infection: the efficacy of prophylactic doxycycline at insertion.
      ].
      “The allocation sequence was concealed from the researcher (JR) enrolling and assessing participants in sequentially numbered, opaque, sealed and stapled envelopes. Aluminium foil inside the envelope was used to render the envelope impermeable to intense light. To prevent subversion of the allocation sequence, the name and date of birth of the participant was written on the envelope and a video tape made of the sealed envelope with participant details visible. Carbon paper inside the envelope transferred the information onto the allocation card inside the envelope and a second researcher (CC) later viewed video tapes to ensure envelopes were still sealed when participants’ names were written on them. Corresponding envelopes were opened only after the enrolled participants completed all baseline assessments and it was time to allocate the intervention”[
      • Radford J.A.
      • Landorf K.B.
      • Buchbinder R.
      • Cook C.
      Effectiveness of low-Dye taping for the short-term treatment of plantar heel pain: a randomised trial.
      ].
      Explanation—Item 8a discussed generation of an unpredictable sequence of assignments. Of considerable importance is how this sequence is applied when participants are enrolled into the trial (see Box 1). A generated allocation schedule should be implemented by using allocation concealment [
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ], a critical mechanism that prevents foreknowledge of treatment assignment and thus shields those who enroll participants from being influenced by this knowledge. The decision to accept or reject a participant should be made, and informed consent should be obtained from the participant, in ignorance of the next assignment in the sequence [
      • Chalmers T.C.
      • Levin H.
      • Sacks H.S.
      • Reitman D.
      • Berrier J.
      • Nagalingam R.
      Meta-analysis of clinical trials as a scientific discipline. I: Control of bias and comparison with large co-operative trials.
      ].
      The allocation concealment should not be confused with blinding (see item 11). Allocation concealment seeks to prevent selection bias, protects the assignment sequence until allocation, and can always be successfully implemented [
      • Schulz K.F.
      • Chalmers I.
      • Hayes R.J.
      • Altman D.G.
      Empirical evidence of bias. Dimensions of methodological quality associated with estimates of treatment effects in controlled trials.
      ]. In contrast, blinding seeks to prevent performance and ascertainment bias, protects the sequence after allocation, and cannot always be implemented [
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ]. Without adequate allocation concealment, however, even random, unpredictable assignment sequences can be subverted [
      • Schulz K.F.
      • Chalmers I.
      • Hayes R.J.
      • Altman D.G.
      Empirical evidence of bias. Dimensions of methodological quality associated with estimates of treatment effects in controlled trials.
      ,
      • Pocock S.J.
      Statistical aspects of clinical trial design.
      ].
      Centralised or “third-party” assignment is especially desirable. Many good allocation concealment mechanisms incorporate external involvement. Use of a pharmacy or central telephone randomisation system are two common techniques. Automated assignment systems are likely to become more common [
      • Haag U.
      Technologies for automating randomized treatment assignment in clinical trials.
      ]. When external involvement is not feasible, an excellent method of allocation concealment is the use of numbered containers. The interventions (often drugs) are sealed in sequentially numbered identical containers according to the allocation sequence [
      • Piaggio G.
      • Elbourne D.
      • Schulz K.F.
      • Villar J.
      • Pinol A.P.
      • Gulmezoglu A.M.
      The reporting of methods for reducing and detecting bias: an example from the WHO Misoprostol Third Stage of Labour equivalence randomised controlled trial.
      ]. Enclosing assignments in sequentially numbered, opaque, sealed envelopes can be a good allocation concealment mechanism if it is developed and monitored diligently. This method can be corrupted, however, particularly if it is poorly executed. Investigators should ensure that the envelopes are opaque when held to the light, and opened sequentially and only after the participant's name and other details are written on the appropriate envelope [
      • Schulz K.F.
      Subverting randomization in controlled trials.
      ].
      A number of methodological studies provide empirical evidence to support these precautions [
      • Pildal J.
      • Hrobjartsson A.
      • Jorgensen K.J.
      • Hilden J.
      • Altman D.G.
      • Gotzsche P.C.
      Impact of allocation concealment on conclusions drawn from meta-analyses of randomized trials.
      ,
      • Wood L.
      • Egger M.
      • Gluud L.L.
      • Schulz K.F.
      • Juni P.
      • Altman D.G.
      • et al.
      Empirical evidence of bias in treatment effect estimates in controlled trials with different interventions and outcomes: meta-epidemiological study.
      ]. Trials in which the allocation sequence had been inadequately or unclearly concealed yielded larger estimates of treatment effects than did trials in which authors reported adequate allocation concealment. These findings provide strong empirical evidence that inadequate allocation concealment contributes to bias in estimating treatment effects.
      Despite the importance of the mechanism of allocation concealment, published reports often omit such details. The mechanism used to allocate interventions was omitted in reports of 89% of trials in rheumatoid arthritis [
      • Gotzsche P.C.
      Methodology and overt and hidden bias in reports of 196 double-blind trials of nonsteroidal antiinflammatory drugs in rheumatoid arthritis.
      ], 48% of trials in obstetrics and gynaecology journals [
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ], and 44% of trials in general medical journals [
      • Altman D.G.
      • Dore C.J.
      Randomisation and baseline comparisons in clinical trials.
      ]. In a more broadly representative sample of all randomised trials indexed on PubMed, only 18% reported any allocation concealment mechanism, but some of those reported mechanisms were inadequate [
      • Chan A.W.
      • Altman D.G.
      Epidemiology and reporting of randomised trials published in PubMed journals.
      ].

      5.3.13 Item 10. Who generated the allocation sequence, who enrolled participants, and who assigned participants to interventions

      Examples—“Determination of whether a patient would be treated by streptomycin and bed-rest (S case) or by bed-rest alone (C case) was made by reference to a statistical series based on random sampling numbers drawn up for each sex at each centre by Professor Bradford Hill; the details of the series were unknown to any of the investigators or to the co-ordinator … After acceptance of a patient by the panel, and before admission to the streptomycin centre, the appropriate numbered envelope was opened at the central office; the card inside told if the patient was to be an S or a C case, and this information was then given to the medical officer of the centre”[
      Streptomycin treatment of pulmonary tuberculosis: a Medical Research Council investigation.
      ].
      “Details of the allocated group were given on coloured cards contained in sequentially numbered, opaque, sealed envelopes. These were prepared at the NPEU and kept in an agreed location on each ward. Randomisation took place at the end of the 2nd stage of labour when the midwife considered a vaginal birth was imminent. To enter a women into the study, the midwife opened the next consecutively numbered envelope”[
      • McCandlish R.
      • Bowler U.
      • van Asten H.
      • Berridge G.
      • Winter C.
      • Sames L.
      • et al.
      A randomised controlled trial of care of the perineum during second stage of normal labour.
      ].
      “Block randomisation was by a computer generated random number list prepared by an investigator with no clinical involvement in the trial. We stratified by admission for an oncology related procedure. After the research nurse had obtained the patient's consent, she telephoned a contact who was independent of the recruitment process for allocation consignment”[
      • Webster J.
      • Clarke S.
      • Paterson D.
      • Hutton A.
      • van Dyk S.
      • Gale C.
      • et al.
      Routine care of peripheral intravenous catheters versus clinically indicated replacement: randomised controlled trial.
      ].
      Explanation—As noted in item 9, concealment of the allocated intervention at the time of enrolment is especially important. Thus, in addition to knowing the methods used, it is also important to understand how the random sequence was implemented—specifically, who generated the allocation sequence, who enrolled participants, and who assigned participants to trial groups.
      The process of randomising participants into a trial has three different steps: sequence generation, allocation concealment, and implementation (see Box 3). Although the same people may carry out more than one process under each heading, investigators should strive for complete separation of the people involved with generation and allocation concealment from the people involved in the implementation of assignments. Thus, if someone is involved in the sequence generation or allocation concealment steps, ideally they should not be involved in the implementation step.
      Steps in a typical randomisation process

         Sequence generation

      • Generate allocation sequence by some random procedure

         Allocation concealment

      • Develop allocation concealment mechanism (such as numbered, identical bottles or sequentially numbered, sealed, opaque envelopes)
      • Prepare the allocation concealment mechanism using the allocation sequence from the sequence generation step

         Implementation

      • Enrol participants:
        • Assess eligibility
        • Discuss the trial
        • Obtain informed consent
        • Enrol participant in trial
      • Ascertain intervention assignment (such as opening next envelope)
      • Administer intervention
      Even with flawless sequence generation and allocation concealment, failure to separate creation and concealment of the allocation sequence from assignment to study group may introduce bias. For example, the person who generated an allocation sequence could retain a copy and consult it when interviewing potential participants for a trial. Thus, that person could bias the enrolment or assignment process, regardless of the unpredictability of the assignment sequence. Investigators must then ensure that the assignment schedule is unpredictable and locked away (such as in a safe deposit box in a building rather inaccessible to the enrolment location) from even the person who generated it. The report of the trial should specify where the investigators stored the allocation list.

      5.3.14 Item 11a. If done, who was blinded after assignment to interventions (for example, participants, care providers, those assessing outcomes) and how

      Examples—“Whereas patients and physicians allocated to the intervention group were aware of the allocated arm, outcome assessors and data analysts were kept blinded to the allocation”[
      • Smith S.A.
      • Shah N.D.
      • Bryant S.C.
      • Christianson T.J.
      • Bjornsen S.S.
      • Giesler P.D.
      • et al.
      Chronic care model and shared care in diabetes: randomized trial of an electronic decision support system.
      ].
      “Blinding and equipoise were strictly maintained by emphasising to intervention staff and participants that each diet adheres to healthy principles, and each is advocated by certain experts to be superior for long-term weight-loss. Except for the interventionists (dieticians and behavioural psychologists), investigators and staff were kept blind to diet assignment of the participants. The trial adhered to established procedures to maintain separation between staff that take outcome measurements and staff that deliver the intervention. Staff members who obtained outcome measurements were not informed of the diet group assignment. Intervention staff, dieticians and behavioural psychologists who delivered the intervention did not take outcome measurements. All investigators, staff, and participants were kept masked to outcome measurements and trial results”[
      • Sacks F.M.
      • Bray G.A.
      • Carey V.J.
      • Smith S.R.
      • Ryan D.H.
      • Anton S.D.
      • et al.
      Comparison of weight-loss diets with different compositions of fat, protein, and carbohydrates.
      ].
      Explanation—The term “blinding” or “masking” refers to withholding information about the assigned interventions from people involved in the trial who may potentially be influenced by this knowledge. Blinding is an important safeguard against bias, particularly when assessing subjective outcomes [
      • Wood L.
      • Egger M.
      • Gluud L.L.
      • Schulz K.F.
      • Juni P.
      • Altman D.G.
      • et al.
      Empirical evidence of bias in treatment effect estimates in controlled trials with different interventions and outcomes: meta-epidemiological study.
      ].
      Benjamin Franklin has been credited as being the first to use blinding in a scientific experiment [
      • Kaptchuk T.J.
      Intentional ignorance: a history of blind assessment and placebo controls in medicine.
      ]. He blindfolded participants so they would not know when he was applying mesmerism (a popular “healing fluid” of the 18th century) and in so doing showed that mesmerism was a sham. Based on this experiment, the scientific community recognised the power of blinding to reduce bias, and it has remained a commonly used strategy in scientific experiments.
      Box 4, on blinding terminology, defines the groups of individuals (that is, participants, healthcare providers, data collectors, outcome adjudicators, and data analysts) who can potentially introduce bias into a trial through knowledge of the treatment assignments. Participants may respond differently if they are aware of their treatment assignment (such as responding more favourably when they receive the new treatment) [
      • Wood L.
      • Egger M.
      • Gluud L.L.
      • Schulz K.F.
      • Juni P.
      • Altman D.G.
      • et al.
      Empirical evidence of bias in treatment effect estimates in controlled trials with different interventions and outcomes: meta-epidemiological study.
      ]. Lack of blinding may also influence compliance with the intervention, use of co-interventions, and risk of dropping out of the trial.
      Blinding terminology
      In order for a technical term to have utility it must have consistency in its use and interpretation. Authors of trials commonly use the term “double blind” and, less commonly, the terms “single blind”or “triple blind.” A problem with this lexicon is that there is great variability in clinician interpretations and epidemiological textbook definitions of these terms [
      • Devereaux P.J.
      • Manns B.J.
      • Ghali W.A.
      • Quan H.
      • Lacchetti C.
      • Montori V.M.
      • et al.
      Physician interpretations and textbook definitions of blinding terminology in randomized controlled trials.
      ]. Moreover, a study of 200 RCTs reported as double blind found 18 different combinations of groups actually blinded when the authors of these trials were surveyed, and about one in every five of these trials—reported as double blind—did not blind participants, healthcare providers, or data collectors [
      • Haahr M.T.
      • Hrobjartsson A.
      Who is blinded in randomized clinical trials? A study of 200 trials and a survey of authors.
      ].
      This research shows that terms are ambiguous and, as such, authors and editors should abandon their use. Authors should instead explicitly report the blinding status of the people involved for whom blinding may influence the validity of a trial.
      Healthcare providers include all personnel (for example, physicians, chiropractors, physiotherapists, nurses) who care for the participants during the trial. Data collectors are the individuals who collect data on the trial outcomes. Outcome adjudicators are the individuals who determine whether a participant did experience the outcomes of interest.
      Some researchers have also advocated blinding and reporting the blinding status of the data monitoring committee and the manuscript writers [
      • Gotzsche P.C.
      Blinding during data analysis and writing of manuscripts.
      ]. Blinding of these groups is uncommon, and the value of blinding them is debated [
      • Meinert C.L.
      Masked monitoring in clinical trials—blind stupidity?.
      ].
      Sometimes one group of individuals (such as the healthcare providers) are the same individuals fulfilling another role in a trial (such as data collectors). Even if this is the case, the authors should explicitly state the blinding status of these groups to allow readers to judge the validity of the trial.
      Unblinded healthcare providers may introduce similar biases, and unblinded data collectors may differentially assess outcomes (such as frequency or timing), repeat measurements of abnormal findings, or provide encouragement during performance testing. Unblinded outcome adjudicators may differentially assess subjective outcomes, and unblinded data analysts may introduce bias through the choice of analytical strategies, such as the selection of favourable time points or outcomes, and by decisions to remove patients from the analyses. These biases have been well documented [
      • Gotzsche P.C.
      Believability of relative risks and odds ratios in abstracts: cross sectional study.
      ,
      • Wood L.
      • Egger M.
      • Gluud L.L.
      • Schulz K.F.
      • Juni P.
      • Altman D.G.
      • et al.
      Empirical evidence of bias in treatment effect estimates in controlled trials with different interventions and outcomes: meta-epidemiological study.
      ,
      • Guyatt G.H.
      • Pugsley S.O.
      • Sullivan M.J.
      • Thompson P.J.
      • Berman L.
      • Jones N.L.
      • et al.
      Effect of encouragement on walking test performance.
      ,
      • Gotzsche P.C.
      Blinding during data analysis and writing of manuscripts.
      ,
      • Karlowski T.R.
      • Chalmers T.C.
      • Frenkel L.D.
      • Kapikian A.Z.
      • Lewis T.L.
      • Lynch J.M.
      Ascorbic acid for the common cold. A prophylactic and therapeutic trial.
      ,
      • Noseworthy J.H.
      • Ebers G.C.
      • Vandervoort M.K.
      • Farquhar R.E.
      • Yetisir E.
      • Roberts R.
      The impact of blinding on the results of a randomized, placebo-controlled multiple sclerosis clinical trial.
      ].
      Blinding, unlike allocation concealment (see item 10), may not always be appropriate or possible. An example is a trial comparing levels of pain associated with sampling blood from the ear or thumb [
      • Carley S.D.
      • Libetta C.
      • Flavin B.
      • Butler J.
      • Tong N.
      • Sammy I.
      An open prospective randomised trial to reduce the pain of blood glucose testing: ear versus thumb.
      ]. Blinding is particularly important when outcome measures involve some subjectivity, such as assessment of pain. Blinding of data collectors and outcome adjudicators is unlikely to matter for objective outcomes, such as death from any cause. Even then, however, lack of participant or healthcare provider blinding can lead to other problems, such as differential attrition [
      • Schulz K.F.
      • Chalmers I.
      • Altman D.G.
      The landscape and lexicon of blinding in randomized trials.
      ]. In certain trials, especially surgical trials, blinding of participants and surgeons is often difficult or impossible, but blinding of data collectors and outcome adjudicators is often achievable. For example, lesions can be photographed before and after treatment and assessed by an external observer [
      • Day S.J.
      • Altman D.G.
      Statistics notes: blinding in clinical trials and other studies.
      ]. Regardless of whether blinding is possible, authors can and should always state who was blinded (that is, participants, healthcare providers, data collectors, and outcome adjudicators).
      Unfortunately, authors often do not report whether blinding was used [
      • Montori V.M.
      • Bhandari M.
      • Devereaux P.J.
      • Manns B.J.
      • Ghali W.A.
      • Guyatt G.H.
      In the dark: the reporting of blinding status in randomized controlled trials.
      ]. For example, reports of 51% of 506 trials in cystic fibrosis [
      • Cheng K.
      • Smyth R.L.
      • Motley J.
      • O'Hea U.
      • Ashby D.
      Randomized controlled trials in cystic fibrosis (1966-1997) categorized by time, design, and intervention.
      ], 33% of 196 trials in rheumatoid arthritis [
      • Gotzsche P.C.
      Methodology and overt and hidden bias in reports of 196 double-blind trials of nonsteroidal antiinflammatory drugs in rheumatoid arthritis.
      ], and 38% of 68 trials in dermatology [
      • Adetugbo K.
      • Williams H.
      How well are randomized controlled trials reported in the dermatology literature?.
      ] did not state whether blinding was used. Until authors of trials improve their reporting of blinding, readers will have difficulty in judging the validity of the trials that they may wish to use to guide their clinical practice.
      The term masking is sometimes used in preference to blinding to avoid confusion with the medical condition of being without sight. However, “blinding” in its methodological sense seems to be understood worldwide and is acceptable for reporting clinical trials [
      • Day S.J.
      • Altman D.G.
      Statistics notes: blinding in clinical trials and other studies.
      ,
      • Lang T.
      Masking or blinding? An unscientific survey of mostly medical journal editors on the great debate.
      ]

      5.3.15 Item 11b. If relevant, description of the similarity of interventions

      Example—“Jamieson Laboratories Inc provided 500-mg immediate release niacin in a white, oblong, bisect caplet. We independently confirmed caplet content using high performance liquid chromatography … The placebo was matched to the study drug for taste, color, and size, and contained microcrystalline cellulose, silicon dioxide, dicalcium phosphate, magnesium stearate, and stearic acid”[
      • Mills E.
      • Prousky J.
      • Raskin G.
      • Gagnier J.
      • Rachlis B.
      • Montori V.M.
      • et al.
      The safety of over-the-counter niacin. A randomized placebo-controlled trial [[ISRCTN18054903]].
      ].
      Explanation—Just as we seek evidence of concealment to assure us that assignment was truly random, we seek evidence of the method of blinding. In trials with blinding of participants or healthcare providers, authors should state the similarity of the characteristics of the interventions (such as appearance, taste, smell, and method of administration) [
      A proposal for structured reporting of randomized controlled trials. The Standards of Reporting Trials Group.
      ,
      • Schulz K.F.
      • Grimes D.A.
      • Altman D.G.
      • Hayes R.J.
      Blinding and exclusions after allocation in randomised controlled trials: survey of published parallel group trials in obstetrics and gynaecology.
      ]
      Some people have advocated testing for blinding by asking participants or healthcare providers at the end of a trial whether they think the participant received the experimental or control intervention [
      • Fergusson D.
      • Glass K.C.
      • Waring D.
      • Shapiro S.
      Turning a blind eye: the success of blinding reported in a random sample of randomised, placebo controlled trials.
      ]. Because participants and healthcare providers will usually know whether the participant has experienced the primary outcome, this makes it difficult to determine if their responses reflect failure of blinding or accurate assumptions about the efficacy of the intervention [
      • Sackett D.L.
      Turning a blind eye: why we don't test for blindness at the end of our trials.
      ]. Given the uncertainty this type of information provides, we have removed advocating reporting this type of testing for blinding from the CONSORT 2010 Statement. We do, however, advocate that the authors report any known compromises in blinding. For example, authors should report if it was necessary to unblind any participants at any point during the conduct of a trial.

      5.3.16 Item 12a. Statistical methods used to compare groups for primary and secondary outcomes

      Example—“The primary endpoint was change in bodyweight during the 20 weeks of the study in the intention-to-treat population … Secondary efficacy endpoints included change in waist circumference, systolic and diastolic blood pressure, prevalence of metabolic syndrome … We used an analysis of covariance (ANCOVA) for the primary endpoint and for secondary endpoints waist circumference, blood pressure, and patient-reported outcome scores; this was supplemented by a repeated measures analysis. The ANCOVA model included treatment, country, and sex as fixed effects, and bodyweight at randomisation as covariate. We aimed to assess whether data provided evidence of superiority of each liraglutide dose to placebo (primary objective) and to orlistat (secondary objective)”[
      • Astrup A.
      • Rossner S.
      • Van Gaal L.
      • Rissanen A.
      • Niskanen L.
      • Al H.M.
      • et al.
      Effects of liraglutide in the treatment of obesity: a randomised, double-blind, placebo-controlled study.
      ].
      Explanation—Data can be analysed in many ways, some of which may not be strictly appropriate in a particular situation. It is essential to specify which statistical procedure was used for each analysis, and further clarification may be necessary in the results section of the report. The principle to follow is to, “Describe statistical methods with enough detail to enable a knowledgeable reader with access to the original data to verify the reported results” (www.icmje.org). It is also important to describe details of the statistical analysis such as intention-to-treat analysis (see Box 6).
      Almost all methods of analysis yield an estimate of the treatment effect, which is a contrast between the outcomes in the comparison groups. Authors should accompany this by a confidence interval for the estimated effect, which indicates a central range of uncertainty for the true treatment effect. The confidence interval may be interpreted as the range of values for the treatment effect that is compatible with the observed data. It is customary to present a 95% confidence interval, which gives the range expected to include the true value in 95 of 100 similar studies.
      Study findings can also be assessed in terms of their statistical significance. The P value represents the probability that the observed data (or a more extreme result) could have arisen by chance when the interventions did not truly differ. Actual P values (for example, P=0.003) are strongly preferable to imprecise threshold reports such as P<0.05 [
      • Lang T.A.
      • Secic M.
      How to report statistics in medicine. Annotated guidelines for authors, editors, and reviewers.
      ,
      • Altman D.G.
      • Gore S.M.
      • Gardner M.J.
      • Pocock S.J.
      Statistical guidelines for contributors to medical journals.
      ].
      Standard methods of analysis assume that the data are “independent.” For controlled trials, this usually means that there is one observation per participant. Treating multiple observations from one participant as independent data is a serious error; such data are produced when outcomes can be measured on different parts of the body, as in dentistry or rheumatology. Data analysis should be based on counting each participant once [
      • Altman D.G.
      • Bland J.M.
      Statistics notes. Units of analysis.
      ,
      • Bolton S.
      Independence and statistical inference in clinical trial designs: a tutorial review.
      ] or should be done by using more complex statistical procedures [
      • Greenland S.
      Principles of multilevel modelling.
      ]. Incorrect analysis of multiple observations per individual was seen in 123 (63%) of 196 trials in rheumatoid arthritis [
      • Gotzsche P.C.
      Methodology and overt and hidden bias in reports of 196 double-blind trials of nonsteroidal antiinflammatory drugs in rheumatoid arthritis.
      ].

      5.3.17 Item 12b. Methods for additional analyses, such as subgroup analyses and adjusted analyses

      Examples—“Proportions of patients responding were compared between treatment groups with the Mantel-Haenszel χ2 test, adjusted for the stratification variable, methotrexate use”[
      • Mease P.J.
      • Goffe B.S.
      • Metz J.
      • VanderStoep A.
      • Finck B.
      • Burge D.J.
      Etanercept in the treatment of psoriatic arthritis and psoriasis: a randomised trial.
      ].
      “Pre-specified subgroup analyses according to antioxidant treatment assignment(s), presence or absence of prior CVD, dietary folic acid intake, smoking, diabetes, aspirin, hormone therapy, and multivitamin use were performed using stratified Cox proportional hazards models. These analyses used baseline exposure assessments and were restricted to participants with nonmissing subgroup data at baseline”[
      • Albert C.M.
      • Cook N.R.
      • Gaziano J.M.
      • Zaharris E.
      • MacFadyen J.
      • Danielson E.
      • et al.
      Effect of folic acid and B vitamins on risk of cardiovascular events and total mortality among women at high risk for cardiovascular disease: a randomized trial.
      ].
      Explanation—As is the case for primary analyses, the method of subgroup analysis should be clearly specified. The strongest analyses are those that look for evidence of a difference in treatment effect in complementary subgroups (for example, older and younger participants), a comparison known as a test of interaction [
      • Matthews J.N.
      • Altman D.G.
      Interaction 3: How to examine heterogeneity.
      ,
      • Assmann S.F.
      • Pocock S.J.
      • Enos L.E.
      • Kasten L.E.
      Subgroup analysis and other (mis)uses of baseline data in clinical trials.
      ]. A common but misleading approach is to compare P values for separate analyses of the treatment effect in each group. It is incorrect to infer a subgroup effect (interaction) from one significant and one non-significant P value [
      • Matthews J.N.
      • Altman D.G.
      Statistics notes. Interaction 2: Compare effect sizes not P values.
      ]. Such inferences have a high false positive rate.
      Because of the high risk for spurious findings, subgroup analyses are often discouraged [
      • Pocock S.J.
      • Hughes M.D.
      • Lee R.J.
      Statistical problems in the reporting of clinical trials. A survey of three medical journals.
      ,
      • Oxman A.D.
      • Guyatt G.H.
      A consumer's guide to subgroup analyses.
      ]. Post hoc subgroup comparisons (analyses done after looking at the data) are especially likely not to be confirmed by further studies. Such analyses do not have great credibility.
      In some studies, imbalances in participant characteristics are adjusted for by using some form of multiple regression analysis. Although the need for adjustment is much less in RCTs than in epidemiological studies, an adjusted analysis may be sensible, especially if one or more variables is thought to be prognostic [
      • Steyerberg E.W.
      • Bossuyt P.M.
      • Lee K.L.
      Clinical trials in acute myocardial infarction: should we adjust for baseline characteristics?.
      ]. Ideally, adjusted analyses should be specified in the study protocol (see item 24). For example, adjustment is often recommended for any stratification variables (see item 8b) on the principle that the analysis strategy should follow the design. In RCTs, the decision to adjust should not be determined by whether baseline differences are statistically significant (see item 16) [
      • Assmann S.F.
      • Pocock S.J.
      • Enos L.E.
      • Kasten L.E.
      Subgroup analysis and other (mis)uses of baseline data in clinical trials.
      ,
      • Altman D.G.
      Adjustment for covariate imbalance.
      ]. The rationale for any adjusted analyses and the statistical methods used should be specified.
      Authors should clarify the choice of variables that were adjusted for, indicate how continuous variables were handled, and specify whether the analysis was planned or suggested by the data [
      • Mullner M.
      • Matthews H.
      • Altman D.G.
      Reporting on statistical methods to adjust for confounding: a cross-sectional survey.
      ]. Reviews of published studies show that reporting of adjusted analyses is inadequate with regard to all of these aspects [
      • Mullner M.
      • Matthews H.
      • Altman D.G.
      Reporting on statistical methods to adjust for confounding: a cross-sectional survey.
      ,
      • Concato J.
      • Feinstein A.R.
      • Holford T.R.
      The risk of determining risk with multivariable models.
      ,
      • Bender R.
      • Grouven U.
      Logistic regression models used in medical research are poorly presented.
      ,
      • Khan K.S.
      • Chien P.F.
      • Dwarakanath L.S.
      Logistic regression models in obstetrics and gynecology literature.
      ].

      5.4 Results

      5.4.1 Item 13. Participant flow (a diagram is strongly recommended)

      5.4.1.1 Item 13a. For each group, the numbers of participants who were randomly assigned, received intended treatment, and were analysed for the primary outcome

      Examples—See Fig. 2, Fig. 3.
      Figure thumbnail gr2
      Fig. 2Flow diagram of a multicentre trial of fractional flow reserve versus angiography for guiding percutaneous coronary intervention (PCI) (adapted from Tonino et al
      [
      • Tonino P.A.
      • De Bruyne B.
      • Pijls N.H.
      • Siebert U.
      • Ikeno F.
      • Veer M.
      • et al.
      Fractional flow reserve versus angiography for guiding percutaneous coronary intervention.
      ]
      ). The diagram includes detailed information on the excluded participants.
      Figure thumbnail gr3
      Fig. 3Flow diagram of minimal surgery compared with medical management for chronic gastro-oesophageal reflux disease (adapted from Grant et al
      [
      • Grant A.M.
      • Wileman S.M.
      • Ramsay C.R.
      • Mowat N.A.
      • Krukowski Z.H.
      • Heading R.C.
      • et al.
      Minimal access surgery compared with medical management for chronic gastro-oesophageal reflux disease: UK collaborative randomised trial.
      ]
      ). The diagram shows a multicentre trial with a parallel non-randomised preference group.
      Explanation—The design and conduct of some RCTs is straightforward, and the flow of participants, particularly were there are no losses to follow-up or exclusions, through each phase of the study can be described adequately in a few sentences. In more complex studies, it may be difficult for readers to discern whether and why some participants did not receive the treatment as allocated, were lost to follow-up, or were excluded from the analysis [
      • Egger M.
      • Juni P.
      • Bartlett C.
      Value of flow diagrams in reports of randomized controlled trials.
      ]. This information is crucial for several reasons. Participants who were excluded after allocation are unlikely to be representative of all participants in the study. For example, patients may not be available for follow-up evaluation because they experienced an acute exacerbation of their illness or harms of treatment [
      • Altman D.G.
      ,
      • Sackett D.L.
      • Gent M.
      Controversy in counting and attributing events in clinical trials.
      ].
      Attrition as a result of loss to follow up, which is often unavoidable, needs to be distinguished from investigator-determined exclusion for such reasons as ineligibility, withdrawal from treatment, and poor adherence to the trial protocol. Erroneous conclusions can be reached if participants are excluded from analysis, and imbalances in such omissions between groups may be especially indicative of bias [
      • Sackett D.L.
      • Gent M.
      Controversy in counting and attributing events in clinical trials.
      ,
      • May G.S.
      • DeMets D.L.
      • Friedman L.M.
      • Furberg C.
      • Passamani E.
      The randomized clinical trial: bias in analysis.
      ,
      • Altman D.G.
      • Cuzick J.
      • Peto J.
      More on zidovudine in asymptomatic HIV infection.
      ]. Information about whether the investigators included in the analysis all participants who underwent randomisation, in the groups to which they were originally allocated (intention-to-treat analysis (see item 16 and Box 6)), is therefore of particular importance. Knowing the number of participants who did not receive the intervention as allocated or did not complete treatment permits the reader to assess to what extent the estimated efficacy of therapy might be underestimated in comparison with ideal circumstances.
      If available, the number of people assessed for eligibility should also be reported. Although this number is relevant to external validity only and is arguably less important than the other counts [
      • Meinert C.L.
      Beyond CONSORT: need for improved reporting standards for clinical trials. Consolidated Standards of Reporting Trials.
      ], it is a useful indicator of whether trial participants were likely to be representative of all eligible participants.
      A review of RCTs published in five leading general and internal medicine journals in 1998 found that reporting of the flow of participants was often incomplete, particularly with regard to the number of participants receiving the allocated intervention and the number lost to follow-up [
      • Egger M.
      • Juni P.
      • Bartlett C.
      Value of flow diagrams in reports of randomized controlled trials.
      ]. Even information as basic as the number of participants who underwent randomisation and the number excluded from analyses was not available in up to 20% of articles [
      • Egger M.
      • Juni P.
      • Bartlett C.
      Value of flow diagrams in reports of randomized controlled trials.
      ]. Reporting was considerably more thorough in articles that included a diagram of the flow of participants through a trial, as recommended by CONSORT. This study informed the design of the revised flow diagram in the revised CONSORT statement [
      • Moher D.
      • Schulz K.F.
      • Altman D.G.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials.
      ,
      • Moher D.
      • Schulz K.F.
      • Altman D.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomized trials.
      ,
      • Moher D.
      • Schulz K.F.
      • Altman D.G.
      The CONSORT statement: revised recommendations for improving the quality of reports of parallel-group randomised trials.
      ]. The suggested template is shown in Fig 1, and the counts required are described in detail in Table 3.
      Table 3Information required to document the flow of participants through each stage of a randomised trial
      StageNumber of people includedNumber of people not included or excludedRationale
      EnrolmentPeople evaluated for potential enrolmentPeople who did not meet the inclusion criteria or met the inclusion criteria but declined to be enrolledThese counts indicate whether trial participants were likely to be representative of all patients seen; they are relevant to assessment of external validity only, and they are often not available.
      RandomisationParticipants randomly assignedCrucial count for defining trial size and assessing whether a trial has been analysed by intention to treat
      Treatment allocationParticipants who completed treatment as allocated, by study groupParticipants who did not complete treatment as allocated, by study groupImportant counts for assessment of internal validity and interpretation of results; reasons for not receiving treatment as allocated should be given.
      Follow-upParticipants who completed treatment as allocated, by study groupParticipants who did not complete treatment as allocated, by study groupImportant counts for assessment of internal validity and interpretation of results; reasons for not completing treatment or follow-up should be given.
      Participants who completed follow-up as planned, by study groupParticipants who did not complete follow-up as planned, by study group
      AnalysisParticipants included in main analysis, by study groupParticipants excluded from main analysis, by study groupCrucial count for assessing whether a trial has been analysed by intention to treat; reasons for excluding participants should be given.
      Some information, such as the number of individuals assessed for eligibility, may not always be known [
      • Pocock S.J.
      • Hughes M.D.
      • Lee R.J.
      Statistical problems in the reporting of clinical trials. A survey of three medical journals.
      ], and, depending on the nature of a trial, some counts may be more relevant than others. It will sometimes be useful or necessary to adapt the structure of the flow diagram to a particular trial. In some situations, other information may usefully be added. For example, the flow diagram of a parallel group trial of minimal surgery compared with medical management for chronic gastro-oesophageal reflux also included a parallel non-randomised preference group (see Fig 3) [
      • Grant A.M.
      • Wileman S.M.
      • Ramsay C.R.
      • Mowat N.A.
      • Krukowski Z.H.
      • Heading R.C.
      • et al.
      Minimal access surgery compared with medical management for chronic gastro-oesophageal reflux disease: UK collaborative randomised trial.
      ].
      The exact form and content of the flow diagram may be varied according to specific features of a trial. For example, many trials of surgery or vaccination do not include the possibility of discontinuation. Although CONSORT strongly recommends using this graphical device to communicate participant flow throughout the study, there is no specific, prescribed format.

      5.4.1.2 Item 13b. For each group, losses and exclusions after randomisation, together with reasons

      Examples—“There was only one protocol deviation, in a woman in the study group. She had an abnormal pelvic measurement and was scheduled for elective caesarean section. However, the attending obstetrician judged a trial of labour acceptable; caesarean section was done when there was no progress in the first stage of labour”[
      • van Loon A.J.
      • Mantingh A.
      • Serlier E.K.
      • Kroon G.
      • Mooyaart E.L.
      • Huisjes H.J.
      Randomised controlled trial of magnetic-resonance pelvimetry in breech presentation at term.
      ].
      “The monitoring led to withdrawal of nine centres, in which existence of some patients could not be proved, or other serious violations of good clinical practice had occurred”[
      • Brown M.J.
      • Palmer C.R.
      • Castaigne A.
      • de Leeuw P.W.
      • Mancia G.
      • Rosenthal T.
      • et al.
      Morbidity and mortality in patients randomised to double-blind treatment with a long-acting calcium-channel blocker or diuretic in the International Nifedipine GITS study: Intervention as a Goal in Hypertension Treatment (INSIGHT).
      ].
      Explanation—Some protocol deviations may be reported in the flow diagram (see item 13a)—for example, participants who did not receive the intended intervention. If participants were excluded after randomisation (contrary to the intention-to-treat principle) because they were found not to meet eligibility criteria (see item 16), they should be included in the flow diagram. Use of the term “protocol deviation” in published articles is not sufficient to justify exclusion of participants after randomisation. The nature of the protocol deviation and the exact reason for excluding participants after randomisation should always be reported.

      5.4.2 Item 14a. Dates defining the periods of recruitment and follow-up

      Example—“Age-eligible participants were recruited … from February 1993 to September 1994 … Participants attended clinic visits at the time of randomisation (baseline) and at 6-month intervals for 3 years”[
      • LaCroix A.Z.
      • Ott S.M.
      • Ichikawa L.
      • Scholes D.
      • Barlow W.E.
      Low-dose hydrochlorothiazide and preservation of bone mineral density in older adults. A randomized, double-blind, placebo-controlled trial.
      ].
      Explanation—Knowing when a study took place and over what period participants were recruited places the study in historical context. Medical and surgical therapies, including concurrent therapies, evolve continuously and may affect the routine care given to participants during a trial. Knowing the rate at which participants were recruited may also be useful, especially to other investigators.
      The length of follow-up is not always a fixed period after randomisation. In many RCTs in which the outcome is time to an event, follow-up of all participants is ended on a specific date. This date should be given, and it is also useful to report the minimum, maximum, and median duration of follow-up [
      • Shuster J.J.
      Median follow-up in clinical trials.
      ,
      • Altman D.G.
      • de Stavola B.L.
      • Love S.B.
      • Stepniewska K.A.
      Review of survival analyses published in cancer journals.
      ].
      A review of reports in oncology journals that used survival analysis, most of which were not RCTs [
      • Altman D.G.
      • de Stavola B.L.
      • Love S.B.
      • Stepniewska K.A.
      Review of survival analyses published in cancer journals.
      ], found that nearly 80% (104 of 132 reports) included the starting and ending dates for accrual of patients, but only 24% (32 of 132 reports) also reported the date on which follow-up ended.

      5.4.3 Item 14b. Why the trial ended or was stopped

      Examples—“At the time of the interim analysis, the total follow-up included an estimated 63% of the total number of patient-years that would have been collected at the end of the study, leading to a threshold value of 0.0095, as determined by the Lan-DeMets alpha-spending function method … At the interim analysis, the RR was 0.37 in the intervention group, as compared with the control group, with a p value of 0.00073, below the threshold value. The Data and Safety Monitoring Board advised the investigators to interrupt the trial and offer circumcision to the control group, who were then asked to come to the investigation centre, where MC (medical circumcision) was advised and proposed … Because the study was interrupted, some participants did not have a full follow-up on that date, and their visits that were not yet completed are described as “planned” in this article”[
      • Auvert B.
      • Taljaard D.
      • Lagarde E.
      • Sobngwi-Tambekou J.
      • Sitta R.
      • Puren A.
      Randomized, controlled intervention trial of male circumcision for reduction of HIV infection risk: the ANRS 1265 Trial.
      ].
      “In January 2000, problems with vaccine supply necessitated the temporary nationwide replacement of the whole cell component of the combined DPT/Hib vaccine with acellular pertussis vaccine. As this vaccine has a different local reactogenicity profile, we decided to stop the trial early”[
      • Diggle L.
      • Deeks J.
      Effect of needle length on incidence of local reactions to routine immunisation in infants aged 4 months: randomised controlled trial.
      ].
      Explanation—Arguably, trialists who arbitrarily conduct unplanned interim analyses after very few events accrue using no statistical guidelines run a high risk of “catching” the data at a random extreme, which likely represents a large overestimate of treatment benefit [
      • Pocock S.
      • White I.
      Trials stopped early: too good to be true?.
      ].
      Readers will likely draw weaker inferences from a trial that was truncated in a data-driven manner versus one that reports its findings after reaching a goal independent of results. Thus, RCTs should indicate why the trial came to an end (see Box 5). The report should also disclose factors extrinsic to the trial that affected the decision to stop the trial, and who made the decision to stop the trial, including reporting the role the funding agency played in the deliberations and in the decision to stop the trial [
      • Montori V.M.
      • Devereaux P.J.
      • Adhikari N.K.
      • Burns K.E.
      • Eggert C.H.
      • Briel M.
      • et al.
      Randomized trials stopped early for benefit: a systematic review.
      ].
      Early stopping
      RCTs can end when they reach their sample size goal, their event count goal, their length of follow-up goal, or when they reach their scheduled date of closure. In these situations the trial will stop in a manner independent of its results, and stopping is unlikely to introduce bias in the results. Alternatively, RCTs can stop earlier than planned because of the result of an interim analysis showing larger than expected benefit or harm on the experimental intervention. Also RCTs can stop earlier than planned when investigators find evidence of no important difference between experimental and control interventions (that is, stopping for futility). In addition, trials may stop early because the trial becomes unviable: funding vanishes, researchers cannot access eligible patients or study interventions, or the results of other studies make the research question irrelevant.
      Full reporting of why a trial ended is important for evidence based decision making (see item 14b). Researchers examining why 143 trials stopped early for benefit found that many failed to report key methodological information regarding how the decision to stop was reached—the planned sample size (n=28), interim analysis after which the trial was stopped (n=45), or whether a stopping rule informed the decision (n=48) [
      • Montori V.M.
      • Devereaux P.J.
      • Adhikari N.K.
      • Burns K.E.
      • Eggert C.H.
      • Briel M.
      • et al.
      Randomized trials stopped early for benefit: a systematic review.
      ]. Item 7b of the checklist requires the reporting of timing of interim analyses, what triggered them, how many took place, whether these were planned or ad hoc, and whether there were statistical guidelines and stopping rules in place a priori. Furthermore, it is helpful to know whether an independent data monitoring committee participated in the analyses (and who composed it, with particular attention to the role of the funding source) and who made the decision to stop. Often the data safety and monitoring committee makes recommendations and the funders (sponsors) or the investigators make the decision to stop.
      Trials that stop early for reasons apparently independent of trial findings, and trials that reach their planned termination, are unlikely to introduce bias by stopping [
      • Psaty B.M.
      • Rennie D.
      Stopping medical research to save money: a broken pact with researchers and patients.
      ]. In these cases, the authors should report whether interim analyses took place and whether these results were available to the funder.
      The push for trials that change the intervention in response to interim results, thus enabling a faster evaluation of promising interventions for rapidly evolving and fatal conditions, will require even more careful reporting of the process and decision to stop trials early [
      • Temple R.
      FDA perspective on trials with interim efficacy evaluations.
      ].
      A systematic review of 143 RCTs stopped earlier than planned for benefit found that these trials reported stopping after accruing a median of 66 events, estimated a median relative risk of 0.47 and a strong relation between the number of events accrued and the size of the effect, with smaller trials with fewer events yielding the largest treatment effects (odds ratio 31, 95% confidence interval 12 to 82) [
      • Montori V.M.
      • Devereaux P.J.
      • Adhikari N.K.
      • Burns K.E.
      • Eggert C.H.
      • Briel M.
      • et al.
      Randomized trials stopped early for benefit: a systematic review.
      ]. While an increasing number of trials published in high impact medical journals report stopping early, only 0.1% of trials reported stopping early for benefit, which contrasts with estimates arising from simulation studies [
      • Hughes M.D.
      • Pocock S.J.
      Stopping rules and estimation problems in clinical trials.
      ] and surveys of data safety and monitoring committees [
      • Kiri A.
      • Tonascia S.
      • Meinert C.L.
      Treatment effects monitoring committees and early stopping in large clinical trials.
      ]. Thus, many trials accruing few participants and reporting large treatment effects may have been stopped earlier than planned but failed to report this action.

      5.4.4 Item 15. A table showing baseline demographic and clinical characteristics for each group

      Example—See Table 4
      Table 4Example of reporting baseline demographic and clinical characteristics
      Data are means (SD) or numbers (%).
      Adapted from Table 1 of Yusuf et al
      • Yusuf S.
      • Teo K.
      • Anderson C.
      • Pogue J.
      • Dyal L.
      • Copland I.
      • et al.
      Effects of the angiotensin-receptor blocker telmisartan on cardiovascular events in high-risk patients intolerant to angiotensin-converting enzyme inhibitors: a randomised controlled trial.
      .
      Telmisartan (N=2954)Placebo (N=2972)
      Age (years)66.9 (7.3)66.9 (7.4)
      Sex (female)1280 (43.3%)1267 (42.6%)
      Smoking status:
       Current293 (9.9%)289 (9.7%)
       Past1273 (43.1%)1283 (43.2%)
      Ethnic origin:
       Asian637 (21.6%)624 (21.0%)
       Arab37 (1.3%)40 (1.3%)
       African51 (1.7%)55 (1.9%)
       European1801 (61.0%)1820 (61.2%)
       Native or Aboriginal390 (13.2%)393 (13.2%)
       Other38 (1.3%)40 (1.3%)
      Blood pressure (mm Hg)140.7 (16.8/81.8) (10.1)141.3 (16.4/82.0) (10.2)
      Heart rate (beats per min)68.8 (11.5)68.8 (12.1)
      Cholesterol (mmol/l):
       Total5.09 (1.18)5.08 (1.15)
       LDL3.02 (1.01)3.03 (1.02)
       HDL1.27 (0.37)1.28 (0.41)
      Coronary artery disease2211 (74.8%)2207 (74.3%)
      Myocardial infarction1381 (46.8%)1360 (45.8%)
      Angina pectoris1412 (47.8%)1412 (47.5%)
      Peripheral artery disease349 (11.8%)323 (10.9%)
      Hypertension2259 (76.5%)2269 (76.3%)
      Diabetes1059 (35.8%)1059 (35.6%)
      Data are means (SD) or numbers (%).
      Explanation—Although the eligibility criteria (see item 4a) indicate who was eligible for the trial, it is also important to know the characteristics of the participants who were actually included. This information allows readers, especially clinicians, to judge how relevant the results of a trial might be to an individual patient.
      Randomised trials aim to compare groups of participants that differ only with respect to the intervention (treatment). Although proper random assignment prevents selection bias, it does not guarantee that the groups are equivalent at baseline. Any differences in baseline characteristics are, however, the result of chance rather than bias [
      • Altman D.G.
      • Dore C.J.
      Randomisation and baseline comparisons in clinical trials.
      ]. The study groups should be compared at baseline for important demographic and clinical characteristics so that readers can assess how similar they were. Baseline data are especially valuable for outcomes that can also be measured at the start of the trial (such as blood pressure).
      Baseline information is most efficiently presented in a table (see Table 4). For continuous variables, such as weight or blood pressure, the variability of the data should be reported, along with average values. Continuous variables can be summarised for each group by the mean and standard deviation. When continuous data have an asymmetrical distribution, a preferable approach may be to quote the median and a centile range (such as the 25th and 75th centiles) [
      • Altman D.G.
      • Gore S.M.
      • Gardner M.J.
      • Pocock S.J.
      Statistical guidelines for contributors to medical journals.
      ]. Standard errors and confidence intervals are not appropriate for describing variability—they are inferential rather than descriptive statistics. Variables with a small number of ordered categories (such as stages of disease I to IV) should not be treated as continuous variables; instead, numbers and proportions should be reported for each category [
      • Lang T.A.
      • Secic M.
      How to report statistics in medicine. Annotated guidelines for authors, editors, and reviewers.
      ,
      • Altman D.G.
      • Gore S.M.
      • Gardner M.J.
      • Pocock S.J.
      Statistical guidelines for contributors to medical journals.
      ].
      Unfortunately significance tests of baseline differences are still common [
      • Schulz K.F.
      • Chalmers I.
      • Grimes D.A.
      • Altman D.G.
      Assessing the quality of randomization from reports of controlled trials published in obstetrics and gynecology journals.
      ,
      • Altman D.G.
      • Dore C.J.
      Randomisation and baseline comparisons in clinical trials.
      ,
      • Senn S.
      Base logic: tests of baseline balance in randomized clinical trials.
      ]; they were reported in half of 50 RCTs trials published in leading general journals in 1997 [
      • Assmann S.F.
      • Pocock S.J.
      • Enos L.E.
      • Kasten L.E.
      Subgroup analysis and other (mis)uses of baseline data in clinical trials.
      ]. Such significance tests assess the probability that observed baseline differences could have occurred by chance; however, we already know that any differences are caused by chance. Tests of baseline differences are not necessarily wrong, just illogical [
      • Altman D.G.
      Comparability of randomised groups.
      ]. Such hypothesis testing is superfluous and can mislead investigators and their readers. Rather, comparisons at baseline should be based on consideration of the prognostic strength of the variables measured and the size of any chance imbalances that have occurred [
      • Altman D.G.
      Comparability of randomised groups.
      ].

      5.4.5 Item 16. For each group, number of participants (denominator) included in each analysis and whether the analysis was by original assigned groups

      Examples—“The primary analysis was intention-to-treat and involved all patients who were randomly assigned”[
      • Heit J.A.
      • Elliott C.G.
      • Trowbridge A.A.
      • Morrey B.F.
      • Gent M.
      • Hirsh J.
      Ardeparin sodium for extended out-of-hospital prophylaxis against venous thromboembolism after total hip or knee replacement. A randomized, double-blind, placebo-controlled trial.
      ].
      “One patient in the alendronate group was lost to follow up; thus data from 31 patients were available for the intention-to-treat analysis. Five patients were considered protocol violators … consequently 26 patients remained for the per-protocol analyses”[
      • Haderslev K.V.
      • Tjellesen L.
      • Sorensen H.A.
      • Staun M.
      Alendronate increases lumbar spine bone mineral density in patients with Crohn's disease.
      ].
      Explanation—The number of participants in each group is an essential element of the analyses. Although the flow diagram (see item 13a) may indicate the numbers of participants analysed, these numbers often vary for different outcome measures. The number of participants per group should be given for all analyses. For binary outcomes, (such as risk ratio and risk difference) the denominators or event rates should also be reported. Expressing results as fractions also aids the reader in assessing whether some of the randomly assigned participants were excluded from the analysis. It follows that results should not be presented solely as summary measures, such as relative risks.
      Participants may sometimes not receive the full intervention, or some ineligible patients may have been randomly allocated in error. One widely recommended way to handle such issues is to analyse all participants according to their original group assignment, regardless of what subsequently occurred (see Box 6). This “intention-to-treat” strategy is not always straightforward to implement. It is common for some patients not to complete a study—they may drop out or be withdrawn from active treatment—and thus are not assessed at the end. If the outcome is mortality, such patients may be included in the analysis based on register information, whereas imputation techniques may need to be used if other outcome data are missing. The term “intention-to-treat analysis” is often inappropriately used—for example, when those who did not receive the first dose of a trial drug are excluded from the analyses [
      • Hollis S.
      • Campbell F.
      What is meant by intention to treat analysis? Survey of published randomised controlled trials.
      ].
      Intention-to-treat analysis
      The special strength of the RCT is the avoidance of bias when allocating interventions to trial participants (see Box 1). That strength allows strong inferences about cause and effect that are not justified with other study designs. In order to preserve fully the huge benefit of randomisation we should include all randomised participants in the analysis, all retained in the group to which they were allocated. Those two conditions define an “intention-to-treat” analysis, which is widely recommended as the preferred analysis strategy [
      • Hollis S.
      • Campbell F.
      What is meant by intention to treat analysis? Survey of published randomised controlled trials.
      ,
      • Herman A.
      • Botser I.B.
      • Tenenbaum S.
      • Chechick A.
      Intention-to-treat analysis and accounting for missing data in orthopaedic randomized clinical trials.
      ]. Intention-to-treat analysis corresponds to analysing the groups exactly as randomised. Strict intention-to-treat analysis is often hard to achieve for two main reasons—missing outcomes for some participants and non-adherence to the trial protocol.

         Missing outcomes

      • Many trialists exclude patients without an observed outcome. Often this is reasonable, but once any randomised participants are excluded the analysis is not strictly an intention-to-treat analysis. Indeed, most randomised trials have some missing observations. Trialists effectively must choose between omitting the participants without final outcome data or imputing their missing outcome data [
        • Altman D.G.
        Missing outcomes in randomised trials: addressing the dilemma.
        ]. A “complete case” (or “available case”) analysis includes only those whose outcome is known. While a few missing outcomes will not cause a problem, in half of trials more than 10% of randomised patients may have missing outcomes [
        • Wood A.M.
        • White I.R.
        • Thompson S.G.
        Are missing outcome data adequately handled? A review of published randomized controlled trials in major medical journals.
        ]. This common approach will lose power by reducing the sample size, and bias may well be introduced if being lost to follow-up is related to a patient's response to treatment. There should be concern when the frequency or the causes of dropping out differ between the intervention groups.
      • Participants with missing outcomes can be included in the analysis only if their outcomes are imputed (that is, their outcomes are estimated from other information that was collected). Imputation of the missing data allows the analysis to conform to intention-to-treat analysis but requires strong assumptions, which may be hard to justify [
        • Streiner D.L.
        Missing data and the trouble with LOCF.
        ]. Simple imputation methods are appealing, but their use may be inadvisable. In particular, a widely used method is “last observation carried forward” in which missing final values of the outcome variable are replaced by the last known value before the participant was lost to follow up. This is appealing through its simplicity, but the method may introduce bias [
        • Molnar F.J.
        • Hutton B.
        • Fergusson D.
        Does analysis using "last observation carried forward" introduce bias in dementia research?.