STATISTICAL METHODS II
STATISTICAL METHODS II BIOS 544
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The Revised CONSORT Statement for Reporting Randomized Trials Explanation and Elaboration Douglas G Altman DSc Kenneth F Schulz PhD David Moher MSc Matthias Egger MD Frank Davidoff MD Diana Elbourne PhD Peter C Gotzsche MD and Thomas Lang MA for the CONSORT Grou AnnEIS of Internal Medicine 17 April 2001 Volume 134 Issue 8 Pages 663 694 Table of Contents Incomplete and Inaccurate Reporting 2 Improving the Reporting of RCTs The CONSORT t t 3 The Revised CONSORT Statement Explanation and E39 39 quot 4 Checklist Items 6 Title and Ahstrm t 6 ITEM 1 How participants were allocated to interventions 6 Introduction 6 ITEM 2 Scienti c background and explanation of rationale 6 Methods 7 ITEM 3a Eligibility criteria for participants 7 ITEM 3b The settings and locations where the data were collected 8 ITEM 4 Precise details of the interventions intended for each group and how and when they were actually administered 8 ITEM 5 Speci c 39J39 quot and 1 t1 9 ITEM 6a Clearly de ned primary and secondary outcome measures 9 ITEM 6b When applicable any methods used to enhance the quality of measurements 10 ITEM 7a How sample size was determined 10 ITEM 7b When applicable explanation of any interim analyses and stopping rules 11 ITEM 8a Method used to generate the random allocation sequence 11 ITEM 8b Details of any restriction of randomization e g blocking strati cation 13 ITEM 9 Method used to implement the random allocation sequence clarifying whether the sequence was concealed until interventions were assigned 14 ITEM 10 Who generated the allocation sequence who enrolled participants and who assigned participants to their ormlps ITEM 11a Whether or not participants those administering the interventions and those assessing the outcomes were blindedto group 39 t 15 ITEM 11b If done how the success ofblinding was evaluated 17 ITEM 12a Statistical methods used to compare groups for primary outcomes 17 ITEM 12b Methods for additional analyses such as subgroup analyses and adjusted analyses 18 R esnlts 19 ITEM 13a Flow of participants through each stage a diagram is strongly recommended Speci cally for each group reportthe numbers of participants randomly assigned receiving intendedtreatment completing the study protocol and analyzed for the primary outcome 19 ITEM 13b Describe protocol deviations from study as planned together with reasons 21 ITEM 14 Dates de ning the periods of recruitment and followup 22 ITEM 15 Baseline demographic and clinical characteristics of each group 22 ITEM 16 Number of participants denominator in each group included in each analysis and whether the analysis was by intention to treat State the results in absolute numbers when feasible eg 10 of 20 not 50 23 ITEM 17 For each primary and secondary outcome a summary of results for each group and the estimated effect size and its precision eg 95 con dence interval 25 wwwannalsorg 17 April 2001 Annals ofIntemalMedicine 134 8 ITEM 18 Address multiplicity by reporting any other analyses performed including subgroup analyses and adjusted analyses indicating those prespecif1ed and those exploratory 25 ITEM 19 All important adverse events or side effects in each intervention group P ITEM 21 Generalizability external validity of the trial findings 27 ITEM 22 General interpretation of the results in the context of current evidence 28 Comments 29 Glossa 30 Author and Article Information 34 f 34 T 39 Questions 41 Abstract of randomizedtrials Throughout the text terms Overwhelming evidence now indicates that the quality of reporting of randomized controlled trials RCTs is less than optimal Recent methodologic analyses indicate that inadequate reporting and design are associated with biased estimates of treatment effects Such systematic error is seriously damaging to RCTs which boast the elimination of systematic error as their primary hallmark Systematic error in RCTs re ects poor science and poor science threatens proper ethical standards A group of scientists and editors developed the CONSORT Consolidated Standards of Reporting Trials statement to improve the quality of reporting of RCTs The statement consists of a checklist and ow diagram that authors can use for reporting an RCT Many leading medical journals and major international editorial groups have adopted the CONSORT statement The CONSORT statement facilitates critical appraisal and interpretation of RCTs by providing guidance to authors about how to improve the reporting of their trials This explanatory and elaboration document is intended to enhance the use A 39 and dissemination of the CONSORT statement The meaning and rationale for each checklist item are presented For most items at least one published example of good reporting and where possible references to relevant empirical studies are provided Several examples of ow diagrams are included The CONSORT statement this explanatory and quot 39 J andthe quot A Web site httpwwwconsortstatementorgb should be helpful resources to improve reporting wwwannalsorg marked with an asterisk are defined at end of text The RCT is a very beautiful technique of wide applicability but as with everything else there are snags When humans have to make observations there is always the possibility of bias 1 Welldesigned and properly executed randomized controlled trials RCTs provide the best evidence on the efficacy of health care interventions but trials with inadequate 39 Fr 39 are 39 Jwith exaggerated treatment effects Biased results from poorly designed and reported trials can mislead decision making in health care at all levels from treatment decisions for the individual patient to formulation of national public health policies Critical appraisal of the quality of clinical trials is possible only if the design conduct and analysis of RCTs are thoroughly and accurately described in published articles Far from being transparent the reporting of RCTs is often 39 r39 69 r quot problems arising from poor methodology 110151 Incomplete and Inaccurate Reporting Many reviews have documented deficiencies in reports of clinical trials For example information on whether assessment of outcomes was blinded was reported in only 30 of 67 trial reports in four leading journals in 1979 and 1980 16 Similarly only 27 of 45 reports published in 1985 defined a primary end point and only 43 of 37 trials with 17 April 2001 Annals ofInternalMedicine 134 8 negative ndings published in 1990 reported a sample size calculation Reporting is not onlyf 1 quotJ 39 r39 but also quot inaccurate Of 119 reports stating that all participants were included in the analysis in the groups to which they were originally assigned intentiontotreat analysis 15 13 excluded patients or did not analyze all patients as allocated Many other reviews have found that inadequate reporting was common in specialty journals 11929 and journals published in languages other than English 130 31 1 Proper randomization eliminates selection biasf and is the crucial component of high quality RCTs Successful randomization hinges on two steps generation of an unpredictable allocation sequence and of this sequence from the investigators enrolling participants Table 1 Q A Unfortunately reporting of the methods used for allocation of participants to interventions is also generally inadequate For example at least 5 of 206 reports of supposed RCTs in obstetrics and gynecology journals described studies that were not truly randomized A This estimate is conservative as most reports do not at present provide adequate information about the method of allocation 2 21 23 25 30 391 Table 1 Treatment Allocation What s 80 Special about Randomization advantages 34 after assignment of treatments 35 randomization II 39 concealment 2 21 Proper The method used to assign treatment or other interventions to trial participants is a crucial aspect of clinical trial design Random assignment is the preferred method it has been successfully used in trials for more than 50 years 33 Randomization has three major First it eliminates bias in the assignment of treatments Without randomization treatment comparisons may be prejudiced whether consciously or not by selection of participants of a particular kind to receive a particular treatment Second random allocation facilitates blinding the identity of treatments to the investigators participants and evaluators possibly by use of a placebo which reduces bias Third random assignment permits the use of probability theory to express the likelihood that any difference in outcome between intervention groups merely re ects chance 36 Preventing selection and confounding biases is the most important advantage of Successful randomization in practice depends on two interrelated aspects adequate generation of an unpredictable allocation sequence and concealment of that sequence until assignment occurs 2 21 A key issue is whether the schedule is known or predictable by the people involved in allocating participants to the comparison groupsf 38 The treatment allocation system should thus be set up so that the person enrolling participants does not know in advance which treatment the next person will get a process termed allocation assignments whereas proper random sequences prevent correct anticipation of future assignments based on knowledge of past assignments I 1 39 shields 39 of forthcoming Terms marked with an asterisk are defined in the glossary at the end of the text Improving the Reporting of RCTs The CONSORT Statement DerSimonian and colleagues E suggested that editors could greatly improve the reporting of clinical trials by providing authors with a list of items that they expected to be strictly reported Early in the 1990s two groups of journal edi wwwannalsorg tors trialists and methodologists independently published recommendations on the reporting of trials 40 41 1 In a subsequent editorial Rennie urged the two groups to meet and develop a common set of recommendations the outcome was the CONSORT statement Consolidated Standards of Reporting Trials 1 17 April 2001 Annals ofInternalMedicine 134 8 The CONSORT statement or simply CON SORT comprises a checklist of essential items that should be included in reports of RCTs and a diagram for documenting the ow of participants through a trial It is aimed at first reports of twogroup parallel designs Most of CONSORT is also relevant to a wider class of trial designs such as equivalence factorial cluster and crossover trials Modi cations to the CONSORT checklist for reporting trials with these and other designs are in preparation The objective of CONSORT is to facilitate critical appraisal and interpretation of RCTs by providing guidance to authors about how to im prove the reporting of their trials Peer reviewers and editors can also use CONSORT to help them identify reports that are difficult to inter pret and those with potentially biased results 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 CON SORT should also be included in a report such as information about approval by an ethics committee obtaining of informed consent from participants existence of a data safety and monitoring committee and sources of funding In addition other aspects of a trial should be properly reported such as information pertinent to costeffectiveness analysis 144461 and qual ityoflife assessments 1 The Revised CONSORT Statement Explanation and Elaboration Since its publication in 1996 CONSORT has been supported by an increasing number of journals 148511 and several editorial groups including the International Committee of wwwannalsorg 4 Medical Journal Editors the Vancouver Group 2 Evidence is accumulatingthat the introduction of CONSORT has improved the quality of reports of RCTs 153 541 However CONSORT is an ongoing initiative and the statement is revised periodically Q The 1996 version of the statement received much comment and some criticism For example Meinert pointed out that the terminology used lacked clarity and that the information presented in the ow diagram was incomplete Work on a revised statement started in 1999 the revised checklist is shown in Table 2 and the revised ow diagram in Figure 1 15658 1 During 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 In this article we discuss the rationale and scientific background for each item Table 2 and provide published examples of good reporting For further examples see http wwwconsortstatementorg In these examples we have removed authors references to other publications to avoid confusion however relevant references should always be cited where needed such as to support unfamiliar methodologic approaches Where possible we describe the findings of relevant empirical studies Many excellent books on clinical trials offer fuller discussion of methodologic issues 1 5961 1 For convenience we sometimes refer to treatments and patients although we recognize that not all interventions evaluated in RCTs are technically treatments and the participants in trials are not always patients 17 April 2001 Annals ofIntemalMedicine 134 8 Table 2 Checklist of Items to Include When Reporting a Randomized Trial Table 2 Checklist of Items To Include When Reporting a Randomized Trial r Paper section and Topic llem Descriptor Reported on Number Page Number Title and abstract 1 eg quot A l t quot quotrandomrzedquot or randomly assigned lntrodudlon Background 2 Screntllrc background and explanatron ol ratronale Methods Particrpants 3 Etiglbrllty cnterra tor partlcrpants and the sottrngs and locatrens where the data were c He i lnterventrons 4 Precrse etarls ol the rnterventrons rntended tor each group and how and when they were actually adlnlrllst Oblecitves 5 5 iii ob ectrves and hyp theses Outcomes 5 Clearly elrne pnmary and secondary outcome measures and when appltcable any met o s used to enhance the quallty ol measurements leg multrple observattons trarnmg of assessors Sample srze 7 e srze A r n annitnhln l analyses and stoppmg rules Randomlzallon Sequence generatron a Method used lo generate the random allocatron sequence rncludrng detalls ol any restnctlon e g bloekmg strati catton Allocatlon concealment 9 Method used 39 5 L 4 central telannnn l H ere assi lmplementatron 10 who generated the allocatron sequence who enrolled partrcrpants and who assrgned partrclpants to their rou s Bllnding masklng 11 whether or not partictpanis those admlnlstellng the mterventloos and those assessing the outcomes were bllnded to group assrgnment lt done how the success of blmdrng was valuaied Statistrcal methods 12 Statlsllcat methods used to Compare groups or primary outcomets methods tor addrllonal analyses such as subgroup analyses and adlusied analyses Results Panicrparll llow 13 no L b L s Specilrcally r9 t a I nil 39 r srmant and analyzed for p Desulbe protocol devtatrons rrom study as planned together wlih reasons Recrultment 14 Dates de1mlng the penod of recruitment and tollowu aaselme data 15 Basellne demographrc and cllnlcal characterrstrcs ot each map Numbers analyzed 15 Number of partlmpants den or 39 eac roup rncluded ln each analysis and whether the analysts was by 391 ntro o treatquot State the results ln absolute numbers when leasrble e g 1 n 5 0 Outcomes and estimatton 17 For each primary and secondary outcome a summary of results lor each group and the cstrmated chest me and rts precisron eg 95 con dence rnterval Ancillary analyses 13 AM 39 uy p I d A a a t I r A L r Adverse events 19 All rmporrant adverse events or srde eflects ln each rnterventron group Drscussron lnterpretatron 20 lntcrpretatron ot the results talnng lnto account study hypotheses sources at potentral bras 0 mm r 39 quotH lt39rl39 a t Generalrzabrlrty 21 Generalrzabrhty external valrdrty ot the trral Ilndlngs Overall eyrdence 22 General rnterpretatron ol the results 1n the context of current evrdence I From rclbrcltcus 5658 WWW annals org 17 April 2001 Annals ofInternal Medicine 134 8 Figure 1 Revised template of the CONSORT Con solidated Standards 0 f R eporting T rials diagram showing the flow of participants through each stage of a randomized trial t56 582 Assessed or 6 not classify a report as an RCT if the authors do not explicitly report this information To help ensure that a study is appropriatelyindexed as an RCT authors should state explicitly in the abstract of their report that the participants were randomly assignedto the comparison groups Possible wordings include participants were ed to treatment was randomized or participants were assigned to interventions by using random allocation We also strongly encourage the use of the word randomized in the title of the report to permit In the mid1990s electronic searching of MEDLINE yielded only about half of all RCTs relevant to a topic 1 This de ciency has been remedied in part by the work of the Cochrane Collaboration which by 1999 had identi ed almost 100 000 RCTs that had not been indexed as such in MEDLINE These reports have been hmrld improve the accuracy of Checklist Items Title and Abstract ITEM 1 How participants were allocated to interventions e g random allocation andomized or randomly assigned Examples Title Smoking reduction with oral nicotine inhalers double blind randomised clinical trial of ef cacy and safety 1Q Abstract Design Randomized double blind placebocontrolled trial 1Q lana on The ability to identify a relevant report in an electronic database depends to a large extent on how it was indexed Indexers for the National Library of Medicine s MEDLINE database may wwwmmalsbrg We encourage the use of structured abstracts when a summary of the report is required Structured abstracts provide readers with a series of headings pertaining to the design conduct and analysis of a trial39 standardized information appears under each heading Some studies have found that structured abstracts are of higher quality than the more traditional descriptive abstracts and that they allow readers to nd information more easily Q Introduction ITEM 2 Scienti c background and explanation e eligibility i randomly ass1 Excluded n Did nut meal 5 In 39 criteria 139 gt n E Reins to participate n l allier mm in in tant lundamixed n E in n 73 Received allnuted Recelved alleesled g lnlervenilun n Intervention n 5 Did not receive annealed Did not receive allocated n w n re1ndexed 65 Adherence to this 3 lost tn followup n e Lust In lollowdlp n l a give reasons give reasons IHdexmg 1 the fume Discon nued lniewenzlon Dlsmntlnned lniew nttml lglve reasons in e give masans n of rational Example The carpal tunnel syndrome is caused by compression of the median nerve at the wrist and is a common cause of pain in the arm particularly in women Injection with corticosteroids is one of the many recommended treatrnen s One of the techniques for such injection entails injection just proximal to not into the carpal tunnel The rationale for this injection site is that there is often a 17 April 2001 ArmaLr ofImernal Medicine 134 8 swelling at the volar side of the forearm close to the carpal tunnel which might contribute to compression of the median nerve Moreover the risk of damaging the median nerve by injection at this site is lower than by injection into the narrow carpal tunnel The rationale for using lignocaine lidocaine together with corticosteroids is twofold the injection is painless and diminished sensation afterwards shows that the injection was properly carried out We investigated in a double blind randomised trial firstly whether symptoms disappeared after injection with corticosteroids proximal to the carpal tunnel and secondly how many patients remained free of symptoms at follow up after this treatment Q Explanation Typically the introduction consists of free owing text without a structured format in which authors explain the scientific background or context and the scientific rationale for their trial The rationale may be explanatory for example to compare the bioavailability of two formulations of a drug or assess the possible in uence of a drug on renal function or pragmatic for example to guide practice by comparing the clinical effects of two alternative treatments Authors should report the evidence of the benefits of any active intervention included in a trial They should also suggest a plausible explanation for how the intervention under investigation might work especially if there is little or no previous experience with the intervention E The Helsinki Declaration states that biomedical research involving people should be based on a thorough knowledge of the scientific literature A That is it is unethical to expose human subjects unnecessarily to the risks of research Some clinical trials have been shown to have been unnecessary because the question they addressed had been or could have been answered by a systematic review of the existing literature Q Thus the need for anew trial should be justified in the introduction Ideally wwwannalsorg 7 the introduction should include a reference to a systematic review of previous similar trials or a note of the absence of such trials E In the first part of the introduction authors should describe the problem that necessitated the work The nature scope and severity of the problem should provide the background and a compelling rationale for the study This information is often missing from reports Authors should then describe brie y the broad approach taken to studying the problem It may also be appropriate to include here the objectives of the trial item 5 Methods ITEM 3a Eligibility criteria for participants Example all women requesting an IUCD intrauterine contraceptive device at the Family Welfare Centre Kenyatta National Hospital who were menstruating regularly and who were between 20 and 44 years of age were candidates for inclusion in the study They were not admitted to the study if any of the following criteria were present 1 a history of ectopic pregnancy 2 pregnancy within the past 42 days 3 leiomyomata of the uterus 4 active PID pelvic in ammatory disease 5 a cervical or endometrial malignancy 6 a known hypersensitivity to tetracyclines 7 use of any antibiotics within the past 14 days or longacting inj ectable penicillin 8 an impaired response to infection or 9 residence outside the city of Nairobi insufficient address for followup or unwillingness to return for followup Explanation Every RCT addresses an issue relevant to some population with the condition of interest Trialists usually restrict this population by using eligibility criteria and by performing the trial in one or a few centers Typical selection criteria may relate to age sex clinical diagnosis and comorbid conditions exclusion criteria are often used to ensure patient safety Eligibility criteria 17 April 2001 Annals ofIntemalMedicine 134 8 should be explicitly de ned If relevant any known inaccuracy in patients diagnoses should be discussed because it can affect the power of the trial m The common distinction between inclusion and exclusion criteria is unnecessary 7 6 Careful descriptions of the trial participants and the setting in which they were studied are needed so that readers may assess the external validity generalizability of the trial results item 21 Of particular importance is the method of recruitment such as by referral or selfselection for example through advertisements Because they are applied before randomization eligibility criteria do not affect the internal validity of a trial but they do affect the external validity Despite their importance eligibility criteria are often not reported adequately For example 25 of 364 reports of RCTs in surgery did not specify the eligibility criteria Eight published trials leading to clinical alerts by the National Institutes of Health specified an average of 31 eligibility criteria Only 63 of the criteria were mentioned in the journal articles and only 19 were mentioned in the clinical alerts m The number of eligibility criteria in cancer trials increased markedly between the 1970s and 1990s 76 ITEM 3b The settings and locations where the data were collected Example Volunteers were recruited in London from four general practices and the ear nose and throat outpatient department of Northwick Park Hospital The prescribers were familiar with homoeopathic principles but were not experienced in homoeopathic immunotherapy B Explanation Settings and locations affect the external validity of a trial Health care institutions vary greatly in their organization experience and resources and the baseline risk for the medical condition under investigation Climate and other physical factors economics geography and the wwwannalsorg 8 social and cultural milieu can all affect a study s external validity Authors should report the number and type of settings and care providers involved so that readers can assess external validity They should describe the settings and locations in which the study was carried out including the country city and immediate environment for example community office practice hospital clinic or inpatient unit In particular it should be clear whether the trial was carried out in one or several centers multicenter trials This description should provide enough information that readers can judge whether the results of the trial are relevant to their own setting Authors should also report any other information about the settings and locations that could in uence the observed results such as problems with transportation that might have affected patient participation ITEM 4 Precise details of the interventions intended for each group and how and when they were actually administered Example Patients with psoriatic arthritis were randomised to receive either placebo or etanercept Enbrel at a dose of 25 mg twice weekly by subcutaneous administration for 12 weeks Etanercept was supplied as a sterile lyophilised powder in vials containing 25 mg etanercept 40 mg mannitol 10 mg sucrose and 172 mg tromethamine per vial Placebo was identically supplied and formulated except that it contained no etanercept Each vial was reconstituted with 1 mL bacteriostatic water for injection Explanation Authors should describe each intervention thoroughly including control interventions The characteristics of a placebo and the way in which it was disguised should also be reported It is especially important to describe thoroughly the usual care given to a control group or an intervention that is in fact a combination of interventions 17 April 2001 Annals ofIntemalMedicine 134 8 In some cases description of who administered treatments is critical because it may form part of the intervention For example with surgical interventions it may be necessary to describe the number training and experience of surgeons in addition to the surgical procedure itself Q When relevant authors should report details of the timing and duration of interventions especially if multiplecomponent interventions were given ITEM 5 Speci c objectives and hypotheses Example In the current study we tested the hypothesis that a policy of active management of nulliparous labour would 1 reduce the rate of caesarean section 2 reduce the rate of prolonged labour 3 not in uence maternal satisfaction with the birth experience Q Explanation Objectivesi 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 prespecified questions being tested to help meet the objectives Hypotheses are more specific than objectives and are amenable to explicit statistical evaluation In practice objectives and hypotheses are not always easily differentiated as in the example above Some evidence suggests that the majority of reports of RCTs provide adequate information about trial objectives and hypotheses a ITEM 6a Clearly defined primary and secondary outcome measures Example The primary endpoint with respect to efficacy in psoriasis was the proportion of patients achieving a 75 improvement in psoriasis activity from baseline to 12 weeks as measured by the PASI psoriasis area and severity index Additional analyses were done on the wwwannalsorg percentage change in PASI scores and improvement in target psoriasis lesions Explanation All RCTs assess response variables or outcomes for which the groups are compared Most trials have several outcomes some of which are of more interest than others The primary outcome measure is the prespecified outcome of greatest importance and is usually the one used in the sample size calculation item 7 Some trials may have more than one primary outcome Having more than one or two outcomes however incurs the problems of interpretation associated with multiplicityf of analyses see items 18 and 20 and is not recommended Primary outcomes should be explicitly indicated as such in the report of an RCT Other outcomes of interest are secondary outcomes There may be several secondary outcomes which often include unanticipated or unintended effects of the intervention item 19 All outcome measures whether primary or secondary should be identified and completely defined When outcomes are assessed at several time points after randomization authors should indicate the prespecified time point of primary interest It is sometimes helpful to specify who assessed outcomes for example if special skills are required to do so and how many assessors there were Many diseases have a plethora of possible outcomes that can be measured by using different scales or instruments Where available and appropriate previously developed and validated scales or consensus guidelines should be used 183 84 bothto enhance quality of measurement and to assist in comparison with similar studies For example assessment of quality of life is likely to be improved by using a validated instrument Authors should indicate the provenance and properties of scales More than 70 outcomes were used in 196 RCTs of nonsteroidal antiin ammatory drugs for rheumatoid arthritis A and 640 different instruments had been used in 2000 trials in schizophrenia of which 369 had been used only once 1 Investigation of 149 of those 2000 trials showed that unpublished scales were a 17 April 2001 Annals ofInternalMedicine 134 8 source of bias In nonpharmacologic trials one third of the claims of treatment superiority based on unpublished scales would not have been made ifa published scale had been used86 Similar evidence has been reported elsewhere 187 88 ITEM 6b When applicable any methods used to enhance the quality of measurements eg multiple observations training of assessors Examples The clinical end point committee evaluated all clinical events in a blinded fashion and end points were determined by unanimous decision Q Blood pressure diastolic phase 5 while the patient was sitting and had rested for at least ve minutes was measured by a trained nurse with a Copal UA25l or a Takeda UA75l electronic auscultatory blood pressure reading machine Andrew Stephens Brighouse West Yorkshire or with a Hawksley random zero sphygmomanometer Hawksley Lancing Sussex in patients with atrial brillation The rst reading was discarded and the mean of the next three consecutive readings with a coef cient of variation below 15 was used in the study with additional readings if required Explanation Authors should give full details of how the primary and secondary outcomes were measured and whether any particular steps were taken to increase the reliability of the measurements Some outcomes are easier to measure than others Death from any cause is usually easy to assess whereas blood pressure depression or quality of life are more dif cult Some strategies can be used to improve the quality of measurements For example assessment of blood pressure is more reliable if more than one reading is obtained and digit preference can be avoided by using a randomzero sphygmomanometer Assessments are more likely to be free of bias if the participant and assessor are blindedto group assignment item wwwannalsorg 10 1 la If a trial requires taking unfamiliar measurements formal standardized training of the people who will be taking the measurements can be bene cial ITEM 7a How sample size was determined Examples We believed that the incidence of symptomatic deep venous thrombosis or pulmonary embolism or death would be 4 in the placebo group and 15 in the ardeparin sodium group Based on 09 power to detect a signi cant difference P 005twosided 976 patients were required for each study group To compensate for nonevaluable patients we planned to enroll 1000 patients per group To have an 85 chance of detecting as signi cant at the two sided 5 level a ve point difference between the two groups in the mean SF36 Short Form 36 general health perception scores with an assumed standard deviation of 20 and a loss to follow up of 20 360 women 720 in total in each group were required Explanation For scienti c and ethical reasons the sample size for a trial needs to be planned carefully with a balance between clinical and statistical considerations Ideally a study should be large enough to have a high probability power of detecting as statistically signi cant 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 l the estimated outcomes in each group which implies the clinically important target difference between the intervention groups 2 the a type I error level 3 the statistical power or the type 11 error level and 4 for continuous outcomes the standard deviation of the measurements 1 17 April 2001 Annals ofIntemalMedicine 134 8 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 item 6a all the quantities used in the calculation and the resulting target sample size per comparison group It is preferable to quote the postulated results of each group rather than the expected difference between the groups Details should be given of any allowance made for attrition during the study In some trials interim analysesf are used to help decide whether to continue recruiting item 7b If the actual sample size differed from that originally intended 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 too few patients were studied to make such a claim Reviews of published trials have consistently found that a high proportion of trials have very low power to detect clinically meaningful treatment effects 117 951 In reality small but clinically valuable true differences are likely which require large trials to detect 1 The median sample size was 54 patients in 196 trials in arthritis A 46 patients in 73 trials in dermatology 1 and 65 patients in 2000 trials in schizophrenia 2 Many reviews have found that few authors report how they determined the sample size 18 14 25 39 There is little merit in calculating the statistical power once the results of the trial are known the power is then appropriately indicated by confidence intervals item 17 ITEM 7b When applicable explanation of any interim analyses and stopping rules Examples The results of the study were reviewed every six months to enable the study to be stopped early if as indeed occurred a clear result emerged wwwannalsorg Two interim analyses were performed during the trial The levels of significance maintained an overall P value of 005 and were calculated according to the O BrieniFleming stopping boundaries This final analysis used a Z score of 1985 with an associatedP value of 00471 2 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 However performing multiple statistical examinations of accumulating data without appropriate correction can lead to erroneous results and interpretations M If the accumulating data from a trial are examined at five interim analyses the overall falsepositive rate is nearer to 19 than to the nominal 5 Several group sequential statistical methods are available to adjust for multiple analyses 11011031 their use should be prespecified in the trial protocol With these methods data are compared at each interim analysis and a very small P value indicates statistical significance Some trialists use theseP values as an aid to decision making M 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 took multiple looks atthe data and if so how many there were the statistical methods used including any formal stopping rule and whether they were planned before the initiation of the trial or some time thereafter This information is frequently not included in publishedtrial reports ITEM 8a Method used to generate the random allocation sequence Example Independent pha1macists dispensed either active or placebo inhalers according to a computer generated randomization list Q 17 April 2001 Annals ofIntemalMedicine 134 8 Explanation Ideally participants should be assigned to comparison groups in the trial on the basis of a chance random process characterized by unpredictability Table 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 adequate However readers cannot judge adequacy from such terms as random allocation randomization or random without further elaboration Authors should specify the method of sequence generation such as arandomnumber table or a computerized randomnumber generator The sequence may be generated by the process of minimization a method of restricted randomizationf item 8b Ta Many methods of sequence generation are ble 3 Item 8b Restricted Iquot 39 39 quot Table 3 Randomization based on a single sequence of random assignments as described in item 8a is known as simple randomization Restricted randomization describes any procedure to control the randomization to achieve balance between groups in size or characteristics Blocking is used to ensure that comparison groups will be of approximately the same size stratificationf is used to ensure good balance of participant characteristics in each group Blocking Blocking can be used to ensure close balance of the numbers in each group at any time during the trial After a block of every 10 participants was assigned for example 5 would be allocated to each arm of the trial m 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 they discovered the block size 10 6 Blinding the interventions using larger block sizes and randomly varying the block size can ameliorate this problem Strati cation 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 w Such imbalances can be avoided without sacrificing the advantages of randomization Strati fication ensures that the numbers of participants receiving each intervention are closely bal anced within each stratum Stratified randomization is achieved by performing a separate randomization procedure within each of two or more subsets of participants for example those defining age smoking or disease severity Stratification by center is common in mul ticenter trials Stratification requires blocking within strata without blocking it is ineffective Minimization Minimization ensures balance between intervention groups for several patient factors 2 Randomization lists are not set up in advance The first patient is truly randomly allo cated for each subsequent patient the treatment allocation is identified which minimizes the imbalance between groups at that time That allocation may then be used or a choice may be made at random with a heavy weighting in favor of the intervention that would minimize im balance for example with a probability of 08 The use of a random component is generally preferable Minimization has the advantage of making small groups closely similar in terms of participant characteristics at all stages of the trial Minimization offers the only acceptable alternative to randomization and some have argued that it is superior M Trials that use minimization are 39 J J 39 39 39 39 J 39 J trials even when a random element is not incorporated J 1 wwwannalsorg Terms marked with an asterisk are defined in the glossary at the end of the text 17 April 2001 Annals ofIntemalMedicine 134 8 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 randomization ratio for example 21 The term random has a precise technical meaning With random allocation each partici pant has a known probability of receiving each treatment before one is assigned but the actual treatmentis determined by a chance process and cannot be predicted However random is often used inappropriately in the literature to describe trials in which nonrandom determi nistic allocation methods such as alternation hospital numbers or date of birth were used When investigators use such a method they should describe it exactly and should not use the term random or any variation of it Even the term quasirandom is questionable for such trials Empirical evidence H indicates that such trials give biased results Bias presumably arises from the inability to conceal these allocation systems adequately see item 9 Only 32 of reports published in specialty journals A and 48 of reports published in general medical journals 1 speci ed an adequate method for generating random numbers In almost all of these cases research ers used a randomnumber generator on a computer or a randomnumber table A review of one dermatology journal over 22 years found that adequate generation was reported in only 1 of 68 trials 1 ITEM 8b Details of any restriction of randomization e g blocking stratification Example Women had an equal probability of assignment to the groups The randomization code was developed using a computer random number generator to select random permuted blocks The block lengths were 4 8 and 10 varied randomly wwwannalsorg Explanation In large trials simple randomization can be trusted to generate similar numbers in the two trial groups and to generate groups that are roughly comparable in terms of known and unknown prognostic variables Restricted randomization describes procedures used to control the randomization to achieve balance between groups in size or characteristics Ta ble It is helpful to indicate whether no restriction was used such as by stating that simple randomization was done Otherwise the methods used to restrict the randomization along with the method used for random selection item 8a should be specified For block randomization authors should provide details on how the blocks were generated for example by using a permuted block design the block size or sizes and whether the block size was randomly varied Authors should specify whether stratification was used and if so which factors were involved and the methods used for blocking Although stratification is a useful technique especially for smaller trials it is complicated to implement if many stratifying factors are used If minimization Table 3 was used it should be explicitly identified as should the variables incorporated into the scheme Use of a random element should be indicated Stratification has been shown to increase the power of small randomized trials by up to 12 especially in the presence of a large intervention effect or strong prognostic stratifying variables m Minimization does not provide the same advantage m Only 9 of 206 reports of trials in specialty journals and 39 of 80 trials in general medical journals reported use of stratification g In each case only about half of the reports mentioned the use of restricted randomization Those studies and that of Adetugbo and Williams 1 found that the sizes of the treatment groups in many trials were very oftenthe same or quite similar yet blocking or stratification had not been mentioned One possible cause of this close balance in numbers is underreporting of the use of restricted randomization 17 April 2001 Annals ofInternalMedicine 134 8 ITEM 9 Method used to implement the random allocation sequence eg numbered containers or central telephone clarifying whether the sequence was concealed until interventions were assigned Example Women were assigned on an individual basis to both vitamins C and E or to both placebo treatments They remained on the same allocation throughout the pregnancy if they continued in the study A computergenerated randomisation list was drawn up by the statistician and given to the pharmacy departments The researchers responsible for seeing the pregnant women allocatedthe next available number on entry into the trial in the ultrasound department or antenatal clinic and each woman collected her tablets direct from the pharmacy department The code was revealed to the researchers once recruitment data collection and laboratory analyses were complete m Explanation Item 8 discussed generation of an unpredictable sequence of assignments Of considerable importance is how this sequence is applied when participants are enrolled into the trial A generated allocation schedule should ideally be implementedby using allocation concealment A a critical process that prevents foreknowledge of treatment assignment and thus shields those who enroll participants from being in uenced by this knowledge The decision to accept or reject a participant shouldbe made and informed consent should be obtained from the participant in ignorance of the next assignment in the sequence m Allocation concealment should not be confused with blinding item 11 Allocation concealment seeks to prevent selection bias protects the assignment sequence before and until allocation and can always be successfully implemented Q In contrast blinding seeks to prevent performance and ascertainment bias protects the sequence after allocation and wwwannalsorg 14 cannot always be implemented A Without adequate allocation concealment however even random unpredictable assignment sequences can be subverteng 1131 Decentralized or thirdparty assignment is especially desirable Many good approaches to allocation concealment incorporate external involvement Use of a pharmacy or central telephone randomization system are two common techniques Automated assignment systems are likely to become more common M When external involvement is not feasible an excellent method of allocation concealment is the use of numbered containers The interventions often medicines are sealed in sequentially numbered identical containers according to the allocation sequence 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 particularly if it is poorly executed Investigators should ensure that the envelopes are opened sequentially and only after the participant s name and other details are written on the appropriate envelope 10 6 Recent studies provide empirical evidence of bias leaking into trials Investigators assessed the quality of reporting of randomization in 250 controlled trials extracted from 33 meta analyses of topics in pregnancy and childbirth and then analyzed the associations between those assessments and the estimated effects of the intervention Q Trials in which the allocation sequence had been inadequately or unclearly concealed yielded larger estimates of treatment effects odds ratios were exaggerated on average by 30 to 40 than did trials in which authors reported adequate allocation concealment Three other studies had similar results 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 published reports frequently omit such details The mechanism used to allocate interventions was omitted in reports of 89 of trials in rheumatoid arthritis 1 48 of trials 17 April 2001 Annals ofIntemalMedicine 134 8 in obstetrics and gynecology journals A and 44 of trials in general medical journals 1 Only 5 of 73 reports of RCTs published in one dermatology journal between 1976 and 1997 reported the method used to allocate treatments g1 ITEM 10 Who generated the allocation sequence who enrolled participants and who assigned participants to their groups Example Determination of whether a patient would be treated by streptomycin and bedrest S case or by bedrest 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 coordinator and were contained in a set of sealed envelopes each bearing on the outside only the name of the hospital and a number 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 1 Explanation As noted in item 9 concealment of the allocated intervention at the time of enrollment 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 enrolling participants into a trial has two very different aspects generation and implementation Table 4 Although the same persons may carry out more than one process under each heading investigators should strive for complete separation of the people wwwannalsorg 15 involved in the generation and implementation of assignments Table 4 Generation and Implementation of a Random Sequence of Treatments Generation Implementation Preparation of the Enrolling participants random sequence Assessing eligibility Discussing the trial Obtaining informed consent Enrolling patient in trial Ascertaining treatment assignment such as by opening the next Preparation of an allocation system such as coded bot tles or envelopes envelope preferably designed Administering inter to be concealed from vention the person assigning participants to groups Whatever the methodologic quality of the randomization process failure to separate creation 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 fora trial Thus that person could bias the enrollment or assignment process regardless of the unpredictability of the assignment sequence Nevertheless the same person may sometimes have to prepare the scheme and also be involved in group assignment Investigators must then ensure that the assignment schedule is unpredictable and locked away from even the person who generated it The report of the trial should specify where the investigators stored the allocation list ITEM 11a Whether or not participants those administering the interventions and those assessing the outcomes were blindedto group assignment Example All study personnel and participants were blinded to treatment assignment for 17 April 2001 Annals ofIntemalMedicine 134 8 the duration of the study Only the study statisticians and the data monitoring committee saw unblinded data but none had any contact with study participants m1 Explanation In controlled trials the term blinding refers to keeping study participants health care providers and sometimes those collecting and analyzing clinical data unaware of the assigned intervention so that they will not be in uenced by that knowledge Blinding is important to prevent bias at several stages of a controlled trial although its relevance varies according to circumstances Blinding of patients is important because knowledge of group assignment may in uence responses to treatment Patients who know that they have been assigned to receive the new treatment may have favorable expectations or increased anxiety Patients assigned to standard treatment may feel discriminated against or reassured Use of placebo controls coupled with blinding of patients is intended to prevent bias resulting from nonspecific effects associated with receiving the intervention placebo effects Blinding of patients and health care providers prevents performance bias This type of bias can occur if additional therapeutic interventions sometimes called cointer ventions are provided or sought preferentially by trial participants in one of the comparison groups The decision to withdraw a participant from a study or to adjust the dose of medication could easily be in uenced by knowledge of the participant s group assignment Blinding of patients health care providers and other persons for example radiologists involved in evaluating outcomes minimizes the risk for detection bias also called observer ascertainment or assessment bias This type of bias occurs if knowledge ofa patient s assign ment in uences the process of outcome assess ment For example in a placebocontrolled multiple sclerosis trial assessments by unblinded but not blinded neurologists showed an apparent benefit of the intervention M Finally blinding of the data analyst can also prevent bias Knowledge of the interventions wwwannalsorg 16 received may in uence the choice of analytical strategies and methods M Trials without any blinding are known as open or if they are pharmaceutical trials openlabel This design is common in early investigations of a drug phase II trials Unlike allocation concealment item 10 blinding may not always be appropriate or possible An example is atrial comparing levels of pain associated with sampling blood from the ear orthumb M Blinding is particularly important when outcome measures involve some subjectivity such as assessment of pain or cause of death It is less important for objective criteria such as death from any cause when there is little scope for ascertainment bias Even then however lack of blinding in any trial can lead to other problems such as attrition Schulz KF Chalmers I Altman DG The landscape and lexicon of blinding Submitted for publication In certain trials especially surgical trials doubleblinding is difficult or impossible However blinded assessment of outcome can often be achieved even in open trials For example lesions can be photographed before and after treatment and be assessed by someone not involved in performance of the trial Some treatments have unintended effects that are so speci c that their occurrence will inevitably identify the treatment received to both the patient and the medical staff Blinded assessment of outcome is especially useful when such revelation is a risk Many trials are described as double blind Although this term implies that neither the caregiver nor the patient knows which treatment was received it is ambiguous with regard to blinding of other persons including those assessing patient outcome m1 Authors should state who was blinded for example participants care providers evaluators monitors or data analysts the mechanism of blinding for example capsules or tablets and the similarity of characteristics of treatments for example appearance taste and method of administration 140 121 1 They should also explain why any participants care providers or evaluators were not blinded 17 April 2001 Annals ofIntemalMedicine 134 8 Authors frequently do not report whether or not blinding was used 16 and when blinding is speci ed details are often missing For example reports of 51 of 506 trials in cystic brosis g 33 of 196 trials in rheumatoid arthritis 3 and 38 of 68 trials in dermatology 1 did not state whetherblinding was used Of 31 doubleblind trials in obstetrics and gynecology only 14 45 of the reports indicated the similarity of the treatment and control regimens Moreover only 5 16 stated explicitly that blinding had been successful m 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 methodologic sense appears to be understood worldwide and is acceptable for reporting clinical trials 119 123 1 ITEM 11b If done how the success of blinding was evaluated Example To evaluate patient blinding the questionnaire asked patients to indicate which treatment they believed they had received acupuncture placebo or don t know at 3 points in time If patients answered either acupuncture or placebo they were asked to indicate what led to that belief Explanation Just as we seek evidence of concealment to assure us that assignment was truly random we may seek evidence that blinding was successful Although description of the mechanism used for blinding may provide such assurance the success of blinding can sometimes be evaluated directly by asking participants caregivers or outcome assessors which treatment they think they received Prasad and colleagues Q reported a placebocontrolled trial of zinc lozenges for reducing the duration of symptoms of the common cold They carried out a separate study in healthy volunteers to check the comparability of taste of zinc or placebo lozenges They also asked participants in the main trial to try to wwwannalsorg 17 identify which treatment they were receiving They reported that at the end of the trial 56 of the zinc recipients and 26 of the placebo recipients correctly identified their group assignment P 009 In principle if blinding was successful the ability of participants to accurately guess their group assignment should be no betterthan chance In practice however if participants do successfully identify their assigned intervention more often than expected by chance it may not mean that blinding was unsuccessful Although adverse effects in particular may offer strong clues as to which intervention was received especially in studies of pharmacologic agents the clinical outcome may also provide clues Thus clinicians are likely to assume not always correctly that a patient who had a favorable outcome was more likely to have received the active intervention rather than control If the active intervention is indeed beneficial their guesses would be likely to be better than those produced by chance m Authors should report any failure of the blinding procedure such as placebo and active preparations that were not identical in appearance ITEM 12a Statistical methods used to compare groups for primary outcomes Example All data analysis was carried out according to a preestablished analysis plan Proportions were compared by using 12 tests with continuity correction or Fisher s exact test when appropriate Multivariate analyses were conducted with logistic regression The durations of episodes and signs of disease were compared by using proportional hazards regression Mean serum retinol concentrations were compared by t test and analysis of covariance Two sided significance tests were used throughout M Explanation Data can be analyzed in many ways some of which may not be strictly appropriate in a 17 April 2001 Annals ofInternalMedicine 134 8 particular situation It is essential to specify which statistical procedure was used for each analysis and further clari cation may be necessary in the results section of the report Almost all methods of analysis yield an estimate of the treatment effect which is a contrast between the outcomes in the comparison groups In addition authors should present a con dence interval for the estimated effect which indicates a range of uncertainty for the true treatment effect The confidence interval may also be interpreted as the range of values for the treatment effectthat is compatible with the observed data It is customary to present a 95 confidence interval which gives the range of uncertainty 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 differ Actual P values for example P 0003 are preferred to imprecise threshold reports P lt 005 146 127 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 differentparts of the body as in dentistry or rheumatology Data analysis should be based on counting each participant once 1128 129lor should be done by using more complex statistical procedures Incorrect analysis of multiple observations was seen in 123 63 of 196 trials in rheumatoid arthritis 3 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 MantelHaenszel X 2 test adjusted for the stratification variable methotrexate use wwwannalsorg it was planned to assess the relative benefit of CHART in an exploratory manner in subgroups age sex performance status stage site and histology To test for differences in the effect of CHART a chisquared test for interaction was performed or when appropriate a chisquared test for trend Explanation As is the case for primary analyses the method of subgroup analysis should be clearly specified The strongest analyses are those based on looking 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 m m A common but inferior 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 nonsignificantP value m Such inferences have a high falsepositive rate Because of the high risk for spurious findings subgroup analyses are often discouraged g 14 1351 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 prognostic variables are adjustedf for by using some form of multiple regression analysis Although the need for adjustment is much less in RCTs than in epidemiologic studies an adjusted analysis may be sensible especially if one or more prognostic variables seem important 136 Ideally adjusted analyses should be specified in the study protocol For example adjustment is often recommended for any stratification variables item 8b In RCTs the decision to adjust should not be determined by whether baseline differences are statistically significant 1133 1371 item 16 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 17 April 2001 Annals ofIntemalMedicine 134 8 continuous variables were handled and specify whether the analysis was plannedquot or suggested by the data Mullner M Matthews H Altman DG Reporting on statistical methods to adjust for confounding a cross sectional survey Submitted for publication Reviews of published studies show that reporting of adjusted analyses is inadequate with regard to all ofthese aspects 138140 Results ITEM 13a Flow of participants through each stage a diagramis strongly recommended Speci cally for each group report the numbers of participants randomly assigned receiving intendedtreatment completing the study protocol and analyzed for the primary outcome xamples Figure 2 Flow diagram ofa multicenter trial comparing implantation of heparincoated stents with percutaneous transluminal an io last TCA 253 with sucusslul PICA sci did not mm mm is lined 359 with sumssful implantation Na lulon n Hallwin 5km n 55 PICA Hluie lulled Lesion could not be crossed with use in 2 when wlIh quotA in 7 The diagram includes detailed information on the interventions received CABG coron artery bypass gra ing Adapted from reference M wwwannalsor 19 Figure 3 Flow diagram ofa trial of chiropractic manipulation of the cervical spine for treatment of episodic tensiontype headache 31 eligible panlrlpants 75 mndumly allmaud 3a iinuua to dilmpnc n as aiimm In phth imi manipulation mi quotusing and massage 27 received lloakd lntervm nn 1 did noticeable allowed lnlewen nn neck ininiy Follnwed up a Week 7 5 Week 35 Week 19 n as The diagram includes the number of patients active1y followed up at different times during the trial Adapted from reference m Figure 4 Flow diagram of a trial of the topoisomerasel inhibitor irinotecan in patients with metastatic colorectal cancer in whom fluorouracil chemotherapy had failed 279 pallznls mndnmly allocated 1 ilinalezan sun 250 mgmz supportive care alone 3quot Pl m39 quotr so meiva Iiomud is reamed allocated lnteiven an inim tion 5 did not receive allocated intervention v 5 lost to iniiowup 134 in analysis 123 died 5 los to followup is in miysi 71 dled si alive 14 zim 5 excluded last to lullawdip excluded last to ioiiawnipi The diagram includes the results for the main 17 April 2001 Annals ofInfernal Medicine 134 8 outcome overall survival Adapted from reference 146 Explanation The design and execution of some RCTs is straightforward and the ow of participants through each phase of the study canbe described adequately in a few sentences In more complex studies it may be dif th for readers to discern whether and why some participants did not receive the treatment as allocated were lost to followupquot or were excluded from the analysis 1 This information is crucial for several reasons Participants who were excluded a er allocation are unlikely to be representative of all participants in the study For example patients may not be available for followup evaluation because they experienced an acute exacerbation of their illness or severe side effectsquot of treatment 32 141 Attrition as a result of loss to follow up which is o en unavoidable needs to be distinguished from investigatordetermined 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 andimbalances in such omissions between groups may be especiallyindicative of bias 141143 Information about whether the investigators included in the analysis all p 39cipants who underwent randomization in the groups to which they were originally allocated intentiontotreat analysis item 16 20 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 persons assessed for eligibility should also be reported Although this number is relevant to external validity only andis arguably less important than the other counts 1 it is a useful indicator of whether trial participants were likely to be representative of all eligible participants A recent review of RCTs published in ve leading general and internal medicine journals in 1998 found that reporting ofthe ow of participants was o en incomplete particularly with regard to the number of participants receiving the allocatedintervention and the number lost to followup Even information as basic as the number of participants who underwent randomization and the number excluded from analyses was not available in up to 20 of articles Reporting was considerably more thorough in articles that included a diagram of the ow of participants through a trial as recommended by CONSORT This study informed the design of the revised ow diagram in the revised CONSORT statement 5658 The suggestedtemplate is wn in Figure 1 and the counts required are described in detail in Table 5 Table 5 Information Required To Document the Flow of Participants through Each Stage of a Randomized Controlled Trial Number of People Number of People Included Not Included or ch Rati Stage Enrollment People evaluated for potential enrollment People who met the People who did not meet the inclusion criteria ona e These counts indicate whether trial participants were likely to be representative of all patients seen they are inclusion criteria but relevant to assessment of dt be ext 39 39 decline enrolled Randomization Participants randomly igned o ernal validity only and Crucial count for de ning trial size and assessing whether a trial has been analyzed by intention to treat wwwannalsorg 17 April 2001 ArmaLr ofImermIJ Medicine 134 8 21 Number of People Number of People Not Included or Stage Included erlllded Rationale Treatment Participants who Participants who did Important counts for allocation received treatment not receive assessment of internal as allocated by treatment as validity and interpretation of study group allocated by study results reasons for not group receiving treatment as V allocated should be given Followup Participants who Participants who did Important counts for completed treatment not complete assessment of internal as allocated by treatment as validity and interpretation of study group allocated by study results reasons for not group completing treatment or Participants who Participants who did followup should be given completed followup not complete follow as planned by study up as planned by group study group Analysis Participants included in Participants excluded Crucial count for assessing main analysis by study group Some information such as the number of persons assessed for eligibility may not always be known and depending on the nature of a trial some counts may be more relevant than others It will therefore often be useful or necessary to adapt the structure of the ow diagram to a particular trial For example a multicenter trial compared implantation of heparincoated stents with standard percutaneous transluminal angioplasty in patients scheduled to undergo coronary angioplasty The nature of the intervention meant that a relatively large number of patients did not receive the allocated intervention In the ow diagram Figure 2 the box describing treatment allocation had to be expanded to re ect this In some situations other information may usefully be added For example the ow diagram of a trial of chiropractic manipulation of the cervical spine in the treatment of episodic tensiontype headache m showed the number of patients actively followed up at different times during the study Figure 3 The main results such as the number of events for the primary outcome may sometimes be added to the ow diagram For example the ow wwwannalsorg from main analysis by study group whether a trial has been analyzed by intention to treat reasons for excluding quot 39 should be given diagram of a trial of the topoisomerase I inhibitor irinotecan in patients with metastatic colorectal cancer in whom uorouracil chemotherapy had failed 14 6 included the number of deaths Figure 4 These examples illustrate that the exact form and content of the ow 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 ow throughout the study there is no specific prescribed format Inclusion of a diagram may be unnecessary for simple trials without losses to followup or exclusions ITEM 13b Describe protocol deviations from study as planned 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 17 April 2001 Annals ofIntemalMedicine 134 8 when there was no progress in the first stage of labour 1 147 1 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 Explanation Authors should report all departures from the protocol including unplanned changes to interventions examinations data collection and methods of analysis Some of these protocol deviations may be reported in the ow diagram item 13a for exampleparticipants who did not receive the intended intervention If participants were excluded after randomization because they were found not to meet eligibility criteria item 16 contrary to the intentionto treat principle they can be included in the ow diagram Use of the term protocol deviation in published articles is not sufficient to justify exclusion of participants after randomization The nature of the protocol deviation and the exact reason for excluding participants after randomization should always be reported ITEM 14 Dates defining the periods of recruitment and followup Example Ageeligible participants were recruited from February 1993 to September 1994 Participants attended clinic visits at the time of randomization baseline and at 6month intervals for 3 years m1 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 patients during a trial Knowing the rate at which participants were recruited may also be useful especially to other investigators The length of followup is not always a fixed period after randomization In many RCTs wwwannalsorg 22 in which the outcome is time to an event followup of all participants is ended on a specific date This date should be given and it is also useful to report the median duration of followup1149 1501 If the trial was stopped owing to results of interim analysis of the data item 7b this should be reported Early stopping will lead to a discrepancy between the planned and actual sample sizes In addition trials that stop early are likely to overestimate the treatment effect M In a review of reports in oncology journals that used survival analysis most of which were not RCTs Altman and associates m 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 followup ended ITEM 15 Baseline demographic and clinical characteristics of each group Example See Table 6 Explanation Although the eligibility criteria item 3 indicate who was eligible for the trial it is also important to know the characteristics of the participants who were actually recruited This information allows readers especially clinicians to judge how relevant the results of a trial might be to a particular patient Randomized controlled 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 g The study groups should be compared at baseline for important demographic and clinical characteristics so that readers can assess how comparable the groups were Baseline data may be especially valuable when the outcome measure can also be measured at the start of the trial 17 April 2001 Annals ofIntemalMedicine 134 8
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