Isabelle Boutron, MD, PhD; David Moher, PhD; Douglas G. Altman, DSc; Kenneth F. Schulz, PhD, MBA; Philippe Ravaud, MD, PhD; CONSORT Group
Acknowledgment: The authors thank Lola Fourcade, who was responsible for preparing the minutes of the CONSORT meeting, and Lucie Ronceray, who developed the Web-based interface used for the preliminary survey. They also thank Drs. Homs and Siersema (Departments of Gastroenterology and Hepatology, Erasmus MC/University Medical Centre Rotterdam, Rotterdam, the Netherlands), who helped reconstruct Figure 2.
Grant Support: By the Département de la Recherche Clinique et du Développement, Assistance Publique des Hôpitaux de Paris; Département d'Epidémiologie, Biostatistique et Recherche Clinique, Hôpital Bichat-Claude Bernard; INSERM U738; and the Eli Lilly Institute. Dr. Moher is funded in part by a University of Ottawa Research Chair. Dr. Altman is supported by Cancer Research UK. Dr. Schulz is supported by Family Health International.
Potential Financial Conflicts of Interest: None disclosed.
Requests for Single Reprints: Isabelle Boutron, MD, PhD, Département d'Epidémiologie Biostatistique et Recherche Clinique, INSERM U738, AP-HP, Hôpital Bichat-Claude Bernard, Université Paris 7 Denis Diderot, 46 Rue Henri Huchard, 75018 Paris, France; e-mail, firstname.lastname@example.org.
Current Author Addresses: Drs. Boutron and Ravaud: Département d'Epidémiologie Biostatistique et Recherche Clinique, INSERM U738, AP-HP, Hôpital Bichat-Claude Bernard, Université Paris 7 Denis Diderot, 46 Rue Henri Huchard, 75018 Paris, France.
Dr. Moher: Chalmers Research Group, Children's Hospital of Eastern Ontario Research Institute, Faculty of Medicine, University of Ottawa, 401 Smyth Road, Room 210, Ottawa, Ontario, Canada.
Dr. Altman: Centre for Statistics in Medicine, University of Oxford, Wolfson College Annexe, Linton Road, Oxford OX2 6UD, United Kingdom.
Dr. Schulz: Quantitative Sciences, Family Health International, PO Box 13950, Research Triangle Park, NC 27709.
For contributors to the CONSORT Extension for Nonpharmacologic Treatment Interventions, see the Appendix.
Boutron I., Moher D., Altman D., Schulz K., Ravaud P., ; Extending the CONSORT Statement to Randomized Trials of Nonpharmacologic Treatment: Explanation and Elaboration. Ann Intern Med. 2008;148:295-309. doi: 10.7326/0003-4819-148-4-200802190-00008
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Published: Ann Intern Med. 2008;148(4):295-309.
Appendix: Contributors to the CONSORT Extension for Nonpharmacologic Treatment Interventions
Adequate reporting of randomized, controlled trials (RCTs) is necessary to allow accurate critical appraisal of the validity and applicability of the results. The CONSORT (Consolidated Standards of Reporting Trials) Statement, a 22-item checklist and flow diagram, is intended to address this problem by improving the reporting of RCTs. However, some specific issues that apply to trials of nonpharmacologic treatments (for example, surgery, technical interventions, devices, rehabilitation, psychotherapy, and behavioral intervention) are not specifically addressed in the CONSORT Statement. Furthermore, considerable evidence suggests that the reporting of nonpharmacologic trials still needs improvement. Therefore, the CONSORT group developed an extension of the CONSORT Statement for trials assessing nonpharmacologic treatments. A consensus meeting of 33 experts was organized in Paris, France, in February 2006, to develop an extension of the CONSORT Statement for trials of nonpharmacologic treatments. The participants extended 11 items from the CONSORT Statement, added 1 item, and developed a modified flow diagram.
To allow adequate understanding and implementation of the CONSORT extension, the CONSORT group developed this elaboration and explanation document from a review of the literature to provide examples of adequate reporting. This extension, in conjunction with the main CONSORT Statement and other CONSORT extensions, should help to improve the reporting of RCTs performed in this field.
The CONSORT (Consolidated Standards of Reporting Trials) Statement, published in 1996 and revised in 2001, is a set of guidelines designed to improve the reporting of randomized, controlled trials (RCTs) (1, 2). Use of this evidence-based guideline is associated with improved quality of reporting in RCTs (3). The CONSORT Statement has been extended to cover different designs, such as noninferiority and equivalence trials (4); types of interventions, such as herbal therapies (5); and data, such as the reporting of harms (6). However, despite the wide dissemination of the CONSORT Statement, inadequate reporting remains common.
Nonpharmacologic treatments include surgery, technical procedures, devices, rehabilitation, psychotherapy, behavioral interventions, and complementary and alternative medicine. Of all RCTs published in 2000, RCTs of nonpharmacologic therapies account for 1 in 4 publications (7). However, the CONSORT Statement does not address some specific issues that apply to nonpharmacologic trials (8–12). For example, blinding is more difficult to achieve in nonpharmacologic trials (13) and, when feasible, relies on complex methods and specific design (14). Nonpharmacologic trials usually test complex interventions involving several components. Such treatments are consequently difficult to describe, standardize, reproduce, and administer consistently to all patients. All of these variations could have an important impact on the estimate of the treatment effect. In addition, care providers' expertise and centers' volume of care can also influence the estimate of the treatment effect (15).
Consequently, the CONSORT Group decided to develop an extension of the CONSORT Statement for nonpharmacologic treatments. The methods and processes leading up to these reporting guidelines are described in detail in an accompanying paper available online only at www.annals.org(16). A major element of the process was a meeting of 33 individuals in February 2006, at which consensus was achieved on guidance for reporting RCTs of nonpharmacologic treatments; this guidance consists of extensions to 11 checklist items, addition of 1 item, and modification of and the flow diagram (Table 1 and Figure 1).
An extra box per intervention group relating to care providers has been added. For cluster randomized, controlled trials, authors should refer to the appropriate extension. IQR = interquartile range; max = maximum; min = minimum.
To facilitate better understanding and dissemination of this CONSORT extension, the meeting participants recommended developing an explanation and elaboration document, similar to those developed for the revised CONSORT Statement (2), STARD (Standards for Reporting of Diagnostic Accuracy) (17), and STROBE (Strengthening the Reporting of Observational Studies in Epidemiology) (18). As with those documents, this article uses a standard template: The modified checklist item is reported, along with the rationale, evidence base (whenever possible), and examples of good reporting provided in Table 2(19–38). An example of reporting in the modified flow diagram is provided in Figure 2(39). This document deals with only some of the CONSORT checklist items; it should thus be seen as an addendum to the main CONSORT explanatory paper (2) for trials of nonpharmacologic treatments. In this document, we have focused only on regular RCTs in which individual participants are randomly assigned to groups. Nonpharmacologic treatments can also be evaluated in cluster RCTs, and in these cases, the CONSORT extension for cluster trials should also be consulted (40).
This example was not reported in the article but was developed with the help of the authors (39). IQR = interquartile range; max = maximum; min = minimum.
Standard CONSORT item: How participants were allocated to interventions (for example, “random allocation,” “randomized,” or “randomly assigned”).
In addition, for nonpharmacologic trials: In the abstract, description of the experimental treatment, comparator, care providers, centers, and blinding status.
The quality of reporting titles and abstracts is essential because it helps indexers, such as those compiling the National Library of Medicine's MEDLINE database, to classify reports so they can be correctly identified electronically (41). Furthermore, abstracts are much more likely to be read than any other section of an article. Good evidence indicates that abstracts frequently underreport key features of trials assessing pharmacologic and nonpharmacologic treatments (41–49). The CONSORT guidelines for reporting journal and conference abstracts are forthcoming (50–52).
For nonpharmacologic trials, the abstract should also include data on centers or care providers, including, when applicable, details on the number of care providers participating in the trial and their expertise. The experimental and control procedures should also be clearly identified. Finally, authors should indicate who was blinded and, if blinding of participants and care providers was impossible, whether the outcome assessment was blinded. These details are necessary to allow an adequate appraisal of the internal and external validity of the trial.
Standard CONSORT item: Eligibility criteria for participants and the settings and locations where the data were collected.
In addition, for nonpharmacologic trials: When applicable, eligibility criteria for centers and those performing the interventions.
Evidence suggests that patient outcome can be associated with hospital and care providers' volume (15, 53–57). A systematic review of 135 trials (15) found that 71% observed a positive association between hospital volume and outcomes and 70% observed an association between care providers' volume and outcomes. Differential expertise of care providers in each treatment group can bias treatment effect estimates (58). Furthermore, a nonpharmacologic treatment might be found to be safe and effective in an RCT performed in high-volume centers by high-volume care providers, but could have different results in low-volume centers. For example, the Asymptomatic Carotid Atherosclerosis Study investigators excluded 40% of all possible care providers, selecting only those with good safety records. This resulted in a postoperative mortality rate that was 8 times lower than in other trials with less stringent selection criteria (59–61). In most nonpharmacologic trials, care providers' expertise and centers' volume of care will influence the treatment effect (15, 53–57, 62–72).
Reporting of eligibility criteria for care providers and centers in nonpharmacologic trials is often poor. One study of surgical reports found that the setting and the center's volume of activity was reported in only 7% and 3% of articles, respectively (79). Selection criteria were reported for care providers in 41% of the articles, and the number of care providers performing the intervention was reported in 32% (79).
A careful description of care providers involved in the trial, as well as details of the centers in which participants were treated, helps readers appraise the risk for bias and the applicability of the results. Selection criteria for centers typically relates to center volume for the procedure under investigation or similar procedures. Eligibility of care providers might include professional qualifications, years in practice, number of interventions performed, skill as assessed by level of complication when performing the intervention, and specific training before trial initiation. Eligibility criteria should be justified, because they will influence the applicability of the trial results (58, 73, 74).
Standard CONSORT item: Precise details of the interventions intended for each group and how and when they were actually administered.
In addition, for nonpharmacologic trials: Precise details of both the experimental treatment and comparator.
Description of the different components of the interventions and, when applicable, description of the procedure for tailoring the interventions to individual participants.
It is important to provide a detailed description of nonpharmacologic treatments, which are usually complex interventions involving several components (75), each of which may influence the estimated treatment effect (27–32). For example, arterial endarterectomy and reconstruction during carotid endarterectomy can be performed in a variety of ways, some aspects of which may influence the treatment effect. For example, use of local anesthesia and patch closure, compared with other techniques, has been shown to reduce the risk for harms after carotid endarterectomy (76, 77). Therefore, authors should report all the different components of the treatment procedure. These descriptions will help introduce the safest and most effective treatments into clinical practice. They are also necessary to facilitate study comparison, reproducibility, and inclusion in systematic reviews (78).
In nonpharmacologic trials, the control treatment can be placebo, usual care, an active treatment, or a waiting list. If the control treatment is usual care, authors should report all the components received by the control group. This information will allow readers to compare the intensity of usual care with the experimental intervention and with what is usually provided to participants in their own setting.
Interventions in nonpharmacologic trials are often poorly described. A systematic review of reports of RCTs assessing surgical procedures highlighted the lack of reporting of other important components: only 35% of studies reported anesthesia management, 15% reported preoperative care, and 49% reported postoperative care (79). In a review of behavioral medicine interventions, insufficient intervention detail was a barrier to assessment of evidence and development of guidelines (80–82). A systematic review of articles published in 6 medical rehabilitation journals in 1997 to 1998 found that information about the timing of the intervention relative to the onset of the disorder was absent from 32% of the 171 reports. Descriptions of the interventions were either brief or absent in one half of the articles and lacked an operational definition in 9% of the articles (83).
The information that is required for a complete description of nonpharmacologic treatments depends on the type of intervention being tested. For surgery, technical procedure, or implantable devices, full details of preoperative care, intraoperative care, configuration of any device, and postoperative care are needed. For nonimplantable devices, the configuration of the device should be detailed and a user's guide for the device should be prepared to enable reproducibility.
For rehabilitation, behavioral treatment, education, and psychotherapy, authors should report qualitative and quantitative data. Qualitative data describe the content of each session, how it is delivered (individual or group), whether the treatment is supervised, the content of the information exchanged with participants, and the instruments used to give information. Quantitative data describe the number of sessions, timing of each session, duration of each session, duration of each main component of each session, and overall duration of the intervention. It is also essential to report how the intervention was tailored to patients' comorbid conditions, tolerance, and clinical course.
To aid the provision of a clear description of these complex interventions, Perera and colleagues proposed a graphical depiction of the experimental and control interventions (84).
Details of how the interventions were standardized.
Assessment of nonpharmacologic treatments in RCTs presents special difficulties because of the complexity of the treatment and the variability found across care providers and centers (23). The variety of settings that characterizes multicenter trials only exacerbates these problems (78). Authors should describe any method used to standardize the intervention across centers or practitioners. In pragmatic trials (that is, trials attempting to show whether an intervention works under the usual conditions in which it will be applied), standardization might consist of simply informing care providers to perform the treatment as they usually do. In efficacy trials (that is, trials aiming to determine whether an intervention works when administered under ideal circumstances), standardization is likely to be more stringent, with the requirement of a certification process, for example (23). The description of any standardization methods is essential to allow adequate replication of the nonpharmacologic treatment. We recommend that authors allow interested readers to access the materials they used to standardize the interventions, either by including a Web appendix with their article or a link to a stable Web site. Such materials include written manuals, specific guidelines, and materials used to train care providers to uniformly deliver the intervention.
In a sample of 158 reports of surgical RCTs published in 2004 (79), only 5 reported the standardization of the intervention: 1 article reported the use of a protocol guideline, 1 article reported the use of a video of the surgical procedure to standardize the procedure, and 3 articles reported a developmental phase preceding standardization.
Details of how adherence of care providers with the protocol was assessed or enhanced.
Assessing treatment adherence is essential to appraising the feasibility and reproducibility of the intervention in clinical practice. Several methods have been used to assess treatment adherence, such as review of case report forms, videotapes, and audiotapes (23, 73, 82, 85, 86). Authors should report the use of any adherence-improving strategies, such as decertifying and excluding surgeons who did not submit a videotape of the intervention rated as acceptable by an independent committee (23). Such strategies should enhance treatment adherence and may influence the treatment effect. Readers must be aware of these methods and strategies in order to accurately transpose the results of the trial into clinical practice and appraise the applicability of the trial's results (82).
In a sample of 158 reports of surgical RCTs published in 2004 (79), only 4 articles reported care providers' compliance with the planned procedure.
Standard CONSORT item: How sample size was determined and, when applicable, explanation of any interim analyses and stopping rules.
In addition, for nonpharmacologic trials: When applicable, details of whether and how the clustering by care providers or centers was addressed.
Table 3 shows the rationale for the clustering effect (87–92). As with cluster randomized trials (40, 93), sample size estimates for individually randomized RCTs assessing nonpharmacologic treatments should ideally be adjusted for the clustering effect as estimated by the intracluster intraclass correlation coefficient. Authors should report whether and how they have incorporated these issues into the trial sample size calculations.
Standard CONSORT item: Methods used to generate the random allocation sequence, including details of any restriction (for example, blocking, stratification).
In addition, for nonpharmacologic trials: When applicable, how care providers were allocated to each trial group.
In conventional RCTs, especially pharmacologic trials, participants are randomly assigned to 1 of 2 (or more) treatments. The treatments compared are usually administered by the same care providers. That approach is not desirable in many nonpharmacologic trials. First, the expertise of care providers for each procedure may differ, or one procedure may be more challenging than the other. This issue may result in differential expertise between interventions and may bias the treatment effect estimates, especially in surgery. Second, care providers are frequently unblinded in nonpharmacologic trials, and they can have preferences or differential expectations for one of the interventions. Thus, they may unconsciously bias the trial: for example, when prescribing a co-intervention or when proposing crossover between groups (that is, the experimental treatment is offered to participants randomly assigned to the control group). A survey of 139 surgeons participating in a large conventional RCT comparing 2 surgical procedures for treating a tibial shaft fracture showed that statistically significantly more surgeons had no or limited experience with the more technically challenging procedure (58). Furthermore, 87% of surgeons believed that the less-challenging procedure was superior, and differential crossover occurred: 8% of the patients assigned to the more-challenging procedure received the less-challenging procedure, whereas fewer than 1% of patients assigned to the less-challenging procedure received the more-challenging procedure.
To overcome these problems, care providers participating in a trial might perform interventions only in their preferred treatment group (expertise-based RCT) (58). This design is mandatory when comparing 2 different types of interventions, such as surgery versus physiotherapy for back problems. However, that design might limit the applicability of the trial results. In trials assessing behavioral intervention, rehabilitation, and psychotherapy, some researchers proposed selecting a random sample of care providers to avoid biased results and improve the applicability.
Consequently, so that others can evaluate the internal and external validity of a trial, authors should report on how care providers were allocated to each treatment group.
11A. Standard CONSORT item: Whether or not participants, those administering the interventions, and those assessing the outcomes were blinded to group assignment.
In addition, for nonpharmacologic trials: Whether or not those administering co-interventions were blinded to group assignment.
Empirical evidence demonstrates that lack of reporting of blinding is associated with biased estimates of treatment effect (94–98). Blinding in trials is usually considered in relation to the participants, caregivers, and outcome assessors (14). In nonpharmacologic trials, the blinding status of other caregivers (for example, physicians administering co-interventions) should also be reported. In fact, other caregivers may have an important influence on the observed treatment effect. For example, in a trial assessing a surgical procedure, even if the surgeon cannot be blinded, the health care professionals following the participants after the procedure might be blinded, and contact between other caregivers and the surgeon could be avoided, thus limiting the risk for performance bias.
If blinded, method of blinding and description of the similarity of interventions.
At the most recent CONSORT Group meeting (Montebello, Québec, Canada, January 2007), the participants agreed to revise the 2001 CONSORT Statement. Item 11 of the checklist deals with reporting of blinding, and the wording of the item will be modified (Moher D. Personal communication.). Because blinding is an especially important issue for nonpharmacologic trials, we have used the wording of the revised checklist item on blinding for the nonpharmacologic extension. Part of the 2001 version states: “If done, how the success of blinding was evaluated.” This is now replaced by: “If blinded, method of blinding and description of the similarity of interventions.”
Blinding is often more difficult to carry out in trials assessing nonpharmacologic treatments (13), and the risk for unblinding is important (99, 100). A review of the methods of blinding in nonpharmacologic trials highlighted creative methods of blinding reported by some authors. Examples include use of sham procedures, such as simulation of surgical procedures, or partial blinding of participants, in which participants are blinded to the study hypothesis (14). The methods of blinding, as well as the similarity of treatments, should be highlighted.
Researchers are still working on how best to deal with some of these methodological challenges. In the meantime, authors should report how they have handled them in order to allow progress in understanding these potential biases.
Standard CONSORT item: Statistical methods used to compare groups for primary outcome(s). Methods for additional analyses, such as subgroup analyses and adjusted analyses.
Table 3 shows the rationale for centers' volume. In trials assessing nonpharmacologic treatments, the success of the intervention depends in part on the skill and training of care providers. As such, observations from participants treated by the same care provider or in the same center are correlated or clustered.
Standard methods of analysis that ignore clusters will result in incorrect estimation of treatment effect (87, 89, 101–104). Authors should use specific models that allow adjustment for participant characteristics while controlling for clustering effect (90, 91) in analyzing the results of this type of trial (91). Any allowance that was made in the analysis for the clustering of participants and care providers or care providers and center should be reported.
Standard CONSORT item: Flow of participants through each stage (a diagram is strongly recommended)—specifically, for each group, report the numbers of participants randomly assigned, receiving intended treatment, completing the study protocol, and analyzed for the primary outcome; describe protocol deviations from study as planned, together with reasons.
In addition, for nonpharmacologic trials: The number of care providers or centers performing the intervention in each group, and the number of patients treated by each care provider or in each center.
As outlined in the CONSORT Statement, the flow of individual participants through each stage of the trial should be reported: the number of persons evaluated for potential enrollment, randomly assigned to each group, who received treatment as allocated, who completed treatment as allocated, who completed follow-up as planned, and included in the main analyses in each group (2).
For trials assessing nonpharmacologic treatments, authors also should report information on the number of centers and care providers in each group and the distribution of participants treated by care providers or at each center. This information is crucial to allow others to critically appraise the applicability of the trial's results. For instance, if 50 surgeons are treating participants, it is important to know whether most patients are being treated by only 1 surgeon or whether all surgeons treated similar numbers of patients. Authors should report the median (interquartile range, minimum and maximum value) of participants treated by each care provider or center. This information could be reported in a figure (Figure 1).
New item, for nonpharmacologic trials: Details of the experimental treatment and comparator as they were implemented.
Although a nonpharmacologic intervention can be standardized (see item 4B), there may be differences between how it was intended to be administered and how it actually was administered—for example, because of lack of the reproducibility of the treatment (82). Furthermore, because participants and care providers are frequently not blinded to treatment assignment, a risk for unequal administration of additional treatments (co-intervention) and consequent “contamination” (that is, administration of the experimental treatment to the control group) might influence the estimates of treatment effect. Care providers may introduce part or all of the experimental intervention into the control program if they are convinced of its superiority. Participants in the control group may also treat themselves with the experimental intervention if they believe in its efficacy. Reporting how the intervention was actually administered is thus crucial to accurate evaluation of the results (22, 23).
Standard CONSORT item: Baseline demographic and clinical characteristics of each group.
In addition, for nonpharmacologic trials: When applicable, a description of care providers (case volume, qualification, expertise, etc.) and centers (volume) in each group.
Although the eligibility criteria (item 3) provide some information on care providers and centers participating in an RCT, further details of the characteristics of the care providers and the centers that recruited and treated participants are important to know.
A table can efficiently present this baseline information. The mean and SD can be used to summarize quantitative data for each group. When quantitative data have an asymmetrical distribution, a preferable approach may be to give the median and percentile range (perhaps the 25th and 75th percentiles). Authors should report numbers and proportions for categorical and qualitative data (2). These data are essential to appraise the risk for bias linked to care providers' expertise and the external validity of the results.
Standard CONSORT item: Interpretation of the results, taking into account the study hypotheses, sources of potential bias or imprecision, and the dangers associated with multiplicity of analyses and outcomes.
In addition, for nonpharmacologic trials: In addition, take into account the choice of the comparator, lack of or partial blinding, and unequal expertise of care providers or centers in each group.
Three aspects specific to nonpharmacologic trials should be addressed in the Discussion section. First, the choice of the comparator is important and will influence the observed treatment effect of the intervention (75, 105). In particular, debate surrounds the use of placebo interventions in trials assessing nonpharmacologic treatments, because these treatments may have a specific therapeutic effect associated with the relationship between participants and care providers. Consequently, trials with placebos might underestimate the treatment effect (14, 106). Some placebos are also questionable from an ethical perspective, such as the use of simulated or sham surgery (27, 37, 107).
Second, blinding issues associated with the feasibility of blinding, risk for blinding failure (13, 14, 108), and risk for bias when blinding is not feasible should be discussed (109, 110). When participants and care providers are not blinded, performance bias (that is, unequal provision of care according to the treatment administered) could occur; a discussion of co-interventions, contamination, and the rate of follow-up in each group is therefore useful. Lack of blinding of outcome assessors could be responsible for ascertainment bias. Any methods used to reduce bias should be discussed. For situations in which outcome assessors cannot be blinded, an objective primary outcome, such as mortality or assessment by an independent end point committee, could limit the risk for bias.
Finally, authors should discuss the possibility of differential expertise bias (58) linked to unequal expertise of care providers in each group (item 3).
Standard CONSORT item: Generalizability (external validity) of the trial findings.
In addition, for nonpharmacologic trials: Generalizability (external validity) of the trial findings according to the intervention, comparators, patients, care providers, and centers involved in the trial.
To be clinically useful, the results of RCTs should provide data on the external validity, also called generalizability and applicability. Lack of external validity is frequently cited as a reason why interventions found to be effective in clinical trials are underutilized in clinical practice (111). In trials comparing pharmacologic with nonpharmacologic treatment, the characteristics of the patients included, the trial setting, the treatment regimens, and the outcomes assessed should all be reported and discussed (2, 111). In nonpharmacologic trials, the health care system (112), selection of participating centers and care providers (59), and intervention actually administered are also essential to evaluate the external validity. For example, differences between health care systems affected the external validity in the European Carotid Surgery Trial (112), an RCT of endarterectomy for recently symptomatic carotid stenosis. In this international trial, countries differed in the speed with which patients were investigated. These differences were not mentioned in any of the publications for the European Carotid Surgery Trial, yet they probably had an important impact on the outcomes (111). Similarly, differences between countries in methods of diagnosis and management can affect the external validity of the trial results. Finally, the volume of centers and care providers can influence the treatment effect estimates, and exclusive participation of high-volume centers has obvious implications for external validity. Authors should clearly indicate whether the intervention evaluated could be performed in all settings by all centers or should be reserved for high-volume centers.
We developed this CONSORT extension to help improve the reporting of RCTs investigating nonpharmacologic treatments. This document provides explanation of and elaboration on the CONSORT checklist items specific to nonpharmacologic treatments. Authors should use this document in conjunction with the main CONSORT guidelines (2) when addressing all 22 items on the checklist. Depending on the type of trial conducted, authors may also find it useful to consult the CONSORT extensions for cluster trials (40) and noninferiority trials (4), and the detailed guidelines for reporting harms associated with interventions (6). All CONSORT guidelines can be found on the CONSORT Web site (http://www.consort-statement.org).
We hope that journals endorsing and enforcing CONSORT for reporting nonpharmacologic RCTs will recommend that authors also review this explanatory document. We believe that the promotion of this extension will improve the quality of reporting RCTs of nonpharmacologic treatments.
Douglas G. Altman (University of Oxford, Oxford, United Kingdom); Mohit Bhandari (McMaster University, Hamilton General Hospital, McMaster Clinic, Hamilton, Ontario, Canada); Isabelle Boutron (INSERM U738, AP-HP, Hôpital Bichat-Claude Bernard, and Université Paris 7 Denis Diderot, Paris, France); Marion Campbell (Health Services Research Unit, Aberdeen, United Kingdom); Philip Devereaux (McMaster University Health Sciences Centre, Hamilton, Ontario, Canada); Peter C. Gøtzsche (The Nordic Cochrane Centre, Copenhagen, Denmark), Teodor P. Grantcharov (Saint Michael's Hospital, Toronto, Ontario, Canada); Jeremy Grimshaw (Ottawa Health Research Institute, Ottawa, Ontario, Canada); Ethan A. Halm (Mount Sinai School of Medicine, New York, New York); Erik Hendriks (Maastricht University, Maastricht, the Netherlands); Asbjørn Hróbjartsson (The Nordic Cochrane Centre, Copenhagen, Denmark); John Ioannidis (University of Ioannina School of Medicine and Biomedical Research Institute, Foundation for Research and Technology–Hellas, Ioannina, Greece); Astrid James (The Lancet, London, United Kingdom); Giselle Jones (BMJ Editorial, London, United Kingdom); Richard J. Lilford (University of Birmingham, Edgbaston, Birmingham, United Kingdom); Robin McLeod (Annals of Surgery and Mount Sinai Hospital, Toronto, Ontario, Canada); David Moher (Chalmers Research Group, Children's Hospital of Eastern Ontario Research Institute, and University of Ottawa, Ottawa, Ontario, Canada); Andrew J. Molyneux (Neurovascular Research Unit, Radcliffe Infirmary, Oxford, United Kingdom); Victor M. Montori (Mayo Clinic College of Medicine, Rochester, Minnesota); Cynthia Mulrow (Annals of Internal Medicine, American College of Physicians, Philadelphia, Pennsylvania); Amy Plint (Children's Hospital of Eastern Ontario, Ottawa, Ontario, Canada); Philippe Ravaud (INSERM U738, AP-HP, Hôpital Bichat-Claude Bernard, and Université Paris 7 Denis Diderot, Paris, France); Drummond Rennie (JAMA, Chicago, Illinois, and University of California, San Francisco, San Francisco, California); Peter M. Rothwell (Radcliffe Infirmary, Oxford, United Kingdom); Paula P. Schnurr (Veterans Affairs Medical and Regional Office Center, White River Junction, Vermont); Kenneth F. Schulz (Quantitative Sciences, Family Health International, Research Triangle Park, North Carolina); Christoph M. Seiler (University of Heidelberg Medical School, Heidelberg, Germany); Judith Stephenson (Centre for Sexual Health and HIV Research, Research Unit, London, United Kingdom); Simon G. Thompson (Medical Research Council, Biostatistics Unit, Institute of Public Health, Cambridge, United Kingdom); Graham Thornicroft (Institute of Psychiatry, King's College London, London, United Kingdom); David Torgerson (University of York, York, United Kingdom); Tom Treasure (Guy's and St Thomas' Hospital, London, United Kingdom); Peter Tugwell (Journal of Clinical Epidemiology and University of Ottawa, Ottawa, Ontario, Canada).
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Ludovic G van Amelsvoort
School for Public Health and Primary Care (Caphri)
April 4, 2008
Time to upgrade the original CONSORT statement?
A recent publication of the CONSORT group in this journal presents the extension of the well-known CONSORT statement to trials of nonpharmacological treatment.(1) The development and adoption of the original statement have indisputably led to improved quality reporting of randomized controlled trials(2). Further transparency and quality improvement may be expected with it's increased application. The extensions to the items of the original statement, presented by Boutron et al., are unquestionably important and germane and will confidently lead to increased quality in reporting.
However, we do feel that several of the items presented as extensions should actually also be included in a revised version of the original CONSORT statement as they can be as relevant for pharmacological as well as non-pharmacological trials. In particular, reporting about, and adjusting for clustering is emphasized in many items of the extension (table 2, items 3, 4C, 7, 12, 13, 15, 20 and, 21). Authors are commended for clearly defining cluster effects in table 3. Based on a review of 42 trials(3), of which 38 had some form of clustering which was largely ignored in the analysis and interpretation of results, the authors conclude that clustering effects are often not recognized and underreported in nonpharmacological trials. This conclusion is clearly overstated. A closer examination of the cited study revealed that 11 of the included trials actually involved pharmacological intervention. Moreover, it is increasingly recognized that clustering should be taken into account in individual RCTs, also in pharmacological comparisons(4). The correlation of diagnostic quality, co-interventions, outcomes and exposures among patients within centers deserves more attention with the ever-increasing flow of multicenter studies and provides often unrecognized analytic challenges, especially in cases of differential numbers of recruited patients per center. Even when there is little apparent heterogeneity across clusters, it can still have a large impact on the estimation and interpretation of the treatment effect.(5)
The authors mention that the original 2001 CONSORT statement is planned to be revised on the item of blinding (item 11). Nonetheless, we contend that the original CONSORT statement should be updated with many of the additional items mentioned in the presented extension.
Two decades ago, uniform reporting was an exception, now it has become the rule on account of the CONSORT statement and extensions are warmly welcomed. Yet, the original statement, being the backbone of the extensions, needs to be state of the art and fully up-to-date.
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