Randomized controlled trial: Difference between revisions

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imported>Robert Badgett
imported>Robert Badgett
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===Interim analysis - stopping trials early===
===Interim analysis - stopping trials early===
Trials are increasingly stopped early<ref name="pmid16264162">{{cite journal |author=Montori VM, Devereaux PJ, Adhikari NK, ''et al'' |title=Randomized trials stopped early for benefit: a systematic review |journal=JAMA |volume=294 |issue=17 |pages=2203–9 |year=2005 |month=November |pmid=16264162 |doi=10.1001/jama.294.17.2203 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=16264162 |issn=}}</ref>; however, this may induce a bias. Data safety and monitoring boards that are independent of the trial are commissioned to conduct interim analyses and make decisions about stopping trials early.<ref>Trotta, F., G. Apolone, S. Garattini, and G. Tafuri. 2008. Stopping a trial early in oncology: for patients or for industry? Ann Oncol mdn042. http://dx.doi.org/10.1093/annonc/mdn042</ref> <ref name="pmid15014189">{{cite journal |author=Slutsky AS, Lavery JV |title=Data Safety and Monitoring Boards |journal=N. Engl. J. Med. |volume=350 |issue=11 |pages=1143–7 |year=2004 |month=March |pmid=15014189 |doi=10.1056/NEJMsb033476 |url=http://content.nejm.org/cgi/pmidlookup?view=short&pmid=15014189&promo=ONFLNS19 |issn=}}</ref>
Trials are increasingly stopped early<ref name="pmid16264162">{{cite journal |author=Montori VM, Devereaux PJ, Adhikari NK, ''et al'' |title=Randomized trials stopped early for benefit: a systematic review |journal=JAMA |volume=294 |issue=17 |pages=2203–9 |year=2005 |month=November |pmid=16264162 |doi=10.1001/jama.294.17.2203 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=16264162 |issn=}}</ref>; however, this may induce a bias that exaggerates results<ref>{{Cite journal | doi = 10.1001/jama.2010.310 | volume = 303 | issue = 12
| pages = 1180-1187 | last = Bassler | first = Dirk | coauthors = Matthias Briel, Victor M. Montori, Melanie Lane, Paul Glasziou, Qi Zhou, Diane Heels-Ansdell, Stephen D. Walter, Gordon H. Guyatt, and the STOPIT-2 Study Group | title = Stopping Randomized Trials Early for Benefit and Estimation of Treatment Effects: Systematic Review and Meta-regression Analysis | journal = JAMA | accessdate = 2010-03-25 | date = 2010-03-24 | url = http://jama.ama-assn.org/cgi/content/abstract/303/12/1180
}}</ref><ref name="pmid16264162">{{cite journal |author=Montori VM, Devereaux PJ, Adhikari NK, ''et al'' |title=Randomized trials stopped early for benefit: a systematic review |journal=JAMA |volume=294 |issue=17 |pages=2203–9 |year=2005 |month=November |pmid=16264162 |doi=10.1001/jama.294.17.2203 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=16264162 |issn=}}</ref>. Data safety and monitoring boards that are independent of the trial are commissioned to conduct interim analyses and make decisions about stopping trials early.<ref>Trotta, F., G. Apolone, S. Garattini, and G. Tafuri. 2008. Stopping a trial early in oncology: for patients or for industry? Ann Oncol mdn042. http://dx.doi.org/10.1093/annonc/mdn042</ref> <ref name="pmid15014189">{{cite journal |author=Slutsky AS, Lavery JV |title=Data Safety and Monitoring Boards |journal=N. Engl. J. Med. |volume=350 |issue=11 |pages=1143–7 |year=2004 |month=March |pmid=15014189 |doi=10.1056/NEJMsb033476 |url=http://content.nejm.org/cgi/pmidlookup?view=short&pmid=15014189&promo=ONFLNS19 |issn=}}</ref>


Reasons to stop a trial early are efficacy, safety, and futility.<ref name="pmid18398083">{{cite journal |author=Borer JS, Gordon DJ, Geller NL |title=When should data and safety monitoring committees share interim results in cardiovascular trials? |journal=JAMA |volume=299 |issue=14 |pages=1710–2 |year=2008 |month=April |pmid=18398083 |doi=10.1001/jama.299.14.1710 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=18398083 |issn=}}</ref><ref name="pmid18226746">{{cite journal |author=Bassler D, Montori VM, Briel M, Glasziou P, Guyatt G |title=Early stopping of randomized clinical trials for overt efficacy is problematic |journal=J Clin Epidemiol |volume=61 |issue=3 |pages=241–6 |year=2008 |month=March |pmid=18226746 |doi=10.1016/j.jclinepi.2007.07.016 |url=http://linkinghub.elsevier.com/retrieve/pii/S0895-4356(07)00292-2 |issn=}}</ref>
Reasons to stop a trial early are efficacy, safety, and futility.<ref name="pmid18398083">{{cite journal |author=Borer JS, Gordon DJ, Geller NL |title=When should data and safety monitoring committees share interim results in cardiovascular trials? |journal=JAMA |volume=299 |issue=14 |pages=1710–2 |year=2008 |month=April |pmid=18398083 |doi=10.1001/jama.299.14.1710 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=18398083 |issn=}}</ref><ref name="pmid18226746">{{cite journal |author=Bassler D, Montori VM, Briel M, Glasziou P, Guyatt G |title=Early stopping of randomized clinical trials for overt efficacy is problematic |journal=J Clin Epidemiol |volume=61 |issue=3 |pages=241–6 |year=2008 |month=March |pmid=18226746 |doi=10.1016/j.jclinepi.2007.07.016 |url=http://linkinghub.elsevier.com/retrieve/pii/S0895-4356(07)00292-2 |issn=}}</ref>
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Regarding efficacy, various rules exist that adjust alpha to decide when to stop a trial early.<ref name="pmid16264167">{{cite journal |author=Pocock SJ |title=When (not) to stop a clinical trial for benefit |journal=JAMA |volume=294 |issue=17 |pages=2228–30 |year=2005 |month=November |pmid=16264167 |doi=10.1001/jama.294.17.2228 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=16264167 |issn=}}</ref><ref name="pmid15885299">{{cite journal |author=Schulz KF, Grimes DA |title=Multiplicity in randomised trials II: subgroup and interim analyses |journal=Lancet |volume=365 |issue=9471 |pages=1657–61 |year=2005 |pmid=15885299 |doi=10.1016/S0140-6736(05)66516-6 |url=http://linkinghub.elsevier.com/retrieve/pii/S0140-6736(05)66516-6 |issn=}}</ref><ref name="pmid15345605">{{cite journal |author=Grant A |title=Stopping clinical trials early |journal=BMJ |volume=329 |issue=7465 |pages=525–6 |year=2004 |month=September |pmid=15345605 |doi=10.1136/bmj.329.7465.525 |url=http://bmj.com/cgi/pmidlookup?view=long&pmid=15345605 |issn=}}</ref><ref name="pmid497341">{{cite journal |author=O'Brien PC, Fleming TR |title=A multiple testing procedure for clinical trials |journal=Biometrics |volume=35 |issue=3 |pages=549–56 |year=1979 |month=September |pmid=497341 |doi= |url= |issn=}}</ref><ref name="pmid7786985">{{cite journal |author=Bauer P, Köhne K |title=Evaluation of experiments with adaptive interim analyses |journal=Biometrics |volume=50 |issue=4 |pages=1029–41 |year=1994 |month=December |pmid=7786985 |doi= |url= |issn=}} This method was used by PMID: 18184958</ref> A commonly recommended rules are the O'Brien-Fleming (the O'Brien-Fleming rule requires a varying p-value depending on the number of interim analyses) and the Haybittle-Peto (the Haybittle-Peto which requires p<0.001 to stop a trial early) rule.<ref name="pmid16264167"/><ref name="pmid15885299"/><ref name="isbn0-471-48986-7">{{cite book |author=DeMets, David L.; Susan S. Ellenberg; Fleming, Thomas J. |authorlink= |editor= |others= |title=Data Monitoring Committees in Clinical Trials: a Practical Perspective |edition= |language= |publisher=J. Wiley & Sons |location=New York |year=2002 |origyear= |pages= |quote= |isbn=0-471-48986-7 |oclc= |doi= |url=http://books.google.com/books?isbn=0471489867 |accessdate=}}</ref>
Regarding efficacy, various rules exist that adjust alpha to decide when to stop a trial early.<ref name="pmid16264167">{{cite journal |author=Pocock SJ |title=When (not) to stop a clinical trial for benefit |journal=JAMA |volume=294 |issue=17 |pages=2228–30 |year=2005 |month=November |pmid=16264167 |doi=10.1001/jama.294.17.2228 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=16264167 |issn=}}</ref><ref name="pmid15885299">{{cite journal |author=Schulz KF, Grimes DA |title=Multiplicity in randomised trials II: subgroup and interim analyses |journal=Lancet |volume=365 |issue=9471 |pages=1657–61 |year=2005 |pmid=15885299 |doi=10.1016/S0140-6736(05)66516-6 |url=http://linkinghub.elsevier.com/retrieve/pii/S0140-6736(05)66516-6 |issn=}}</ref><ref name="pmid15345605">{{cite journal |author=Grant A |title=Stopping clinical trials early |journal=BMJ |volume=329 |issue=7465 |pages=525–6 |year=2004 |month=September |pmid=15345605 |doi=10.1136/bmj.329.7465.525 |url=http://bmj.com/cgi/pmidlookup?view=long&pmid=15345605 |issn=}}</ref><ref name="pmid497341">{{cite journal |author=O'Brien PC, Fleming TR |title=A multiple testing procedure for clinical trials |journal=Biometrics |volume=35 |issue=3 |pages=549–56 |year=1979 |month=September |pmid=497341 |doi= |url= |issn=}}</ref><ref name="pmid7786985">{{cite journal |author=Bauer P, Köhne K |title=Evaluation of experiments with adaptive interim analyses |journal=Biometrics |volume=50 |issue=4 |pages=1029–41 |year=1994 |month=December |pmid=7786985 |doi= |url= |issn=}} This method was used by PMID: 18184958</ref> A commonly recommended rules are the O'Brien-Fleming (the O'Brien-Fleming rule requires a varying p-value depending on the number of interim analyses) and the Haybittle-Peto (the Haybittle-Peto which requires p<0.001 to stop a trial early) rule.<ref name="pmid16264167"/><ref name="pmid15885299"/><ref name="isbn0-471-48986-7">{{cite book |author=DeMets, David L.; Susan S. Ellenberg; Fleming, Thomas J. |authorlink= |editor= |others= |title=Data Monitoring Committees in Clinical Trials: a Practical Perspective |edition= |language= |publisher=J. Wiley & Sons |location=New York |year=2002 |origyear= |pages= |quote= |isbn=0-471-48986-7 |oclc= |doi= |url=http://books.google.com/books?isbn=0471489867 |accessdate=}}</ref>


Using a more conservative stopping rule reduces the chance of a statistical alpha (Type I) error; however, these rules do not alter that the effect size may be exaggerated.<ref name="pmid2605969">{{cite journal |author=Pocock SJ, Hughes MD |title=Practical problems in interim analyses, with particular regard to estimation |journal=Control Clin Trials |volume=10 |issue=4 Suppl |pages=209S–221S |year=1989 |month=December |pmid=2605969 |doi= |url= |issn=}}</ref><ref name="pmid15885299">{{cite journal |author=Schulz KF, Grimes DA |title=Multiplicity in randomised trials II: subgroup and interim analyses |journal=Lancet |volume=365 |issue=9471 |pages=1657–61 |year=2005 |pmid=15885299 |doi=10.1016/S0140-6736(05)66516-6 |url=http://linkinghub.elsevier.com/retrieve/pii/S0140-6736(05)66516-6 |issn=}}</ref> According to Bassler, "the more stringent the P-value threshold results must cross to justify  stopping the trial, the more likely it is that a trial stopped early will  overestimate the treatment effect."<ref name="pmid18226746">{{cite journal |author=Bassler D, Montori VM, Briel M, Glasziou P, Guyatt G |title=Early stopping of randomized clinical trials for overt efficacy is problematic |journal=J Clin Epidemiol |volume=61 |issue=3 |pages=241–6 |year=2008 |month=March |pmid=18226746 |doi=10.1016/j.jclinepi.2007.07.016 |url=http://linkinghub.elsevier.com/retrieve/pii/S0895-4356(07)00292-2 |issn=}}</ref> A review of trials stopped early found that the earlier a trial was stopped the larger was its reported treatment effect.<ref name="pmid16264162">{{cite journal |author=Montori VM, Devereaux PJ, Adhikari NK, ''et al'' |title=Randomized trials stopped early for benefit: a systematic review |journal=JAMA |volume=294 |issue=17 |pages=2203–9 |year=2005 |month=November |pmid=16264162 |doi=10.1001/jama.294.17.2203 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=16264162 |issn=}}</ref> Accordingly, examples exists of trials whose interim analyses were significant, but the trial was continued and the final analysis was less significant or was insignificant.<ref name="pmid15894981">{{cite journal |author=Pocock S, Wang D, Wilhelmsen L, Hennekens CH |title=The data monitoring experience in the Candesartan in Heart Failure Assessment of Reduction in Mortality and morbidity (CHARM) program |journal=Am. Heart J. |volume=149 |issue=5 |pages=939–43 |year=2005 |month=May |pmid=15894981 |doi=10.1016/j.ahj.2004.10.038 |url=http://linkinghub.elsevier.com/retrieve/pii/S0002870305000189 |issn=}}</ref><ref name="pmid12559643">{{cite journal |author=Wheatley K, Clayton D |title=Be skeptical about unexpected large apparent treatment effects: the case of an MRC AML12 randomization |journal=Control Clin Trials |volume=24 |issue=1 |pages=66–70 |year=2003 |month=February |pmid=12559643 |doi= |url=http://linkinghub.elsevier.com/retrieve/pii/S0197245602002738 |issn=}}</ref><ref name="pmid12851279">{{cite journal |author=Abraham E, Reinhart K, Opal S, ''et al'' |title=Efficacy and safety of tifacogin (recombinant tissue factor pathway inhibitor) in severe sepsis: a randomized controlled trial |journal=JAMA |volume=290 |issue=2 |pages=238–47 |year=2003 |month=July |pmid=12851279 |doi=10.1001/jama.290.2.238 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=12851279 |issn=}}</ref>  
Using a more conservative stopping rule reduces the chance of a statistical alpha (Type I) error; however, these rules do not alter that the effect size may be exaggerated.<ref name="pmid2605969">{{cite journal |author=Pocock SJ, Hughes MD |title=Practical problems in interim analyses, with particular regard to estimation |journal=Control Clin Trials |volume=10 |issue=4 Suppl |pages=209S–221S |year=1989 |month=December |pmid=2605969 |doi= |url= |issn=}}</ref><ref name="pmid15885299">{{cite journal |author=Schulz KF, Grimes DA |title=Multiplicity in randomised trials II: subgroup and interim analyses |journal=Lancet |volume=365 |issue=9471 |pages=1657–61 |year=2005 |pmid=15885299 |doi=10.1016/S0140-6736(05)66516-6 |url=http://linkinghub.elsevier.com/retrieve/pii/S0140-6736(05)66516-6 |issn=}}</ref> According to Bassler, "the more stringent the P-value threshold results must cross to justify  stopping the trial, the more likely it is that a trial stopped early will  overestimate the treatment effect."<ref name="pmid18226746">{{cite journal |author=Bassler D, Montori VM, Briel M, Glasziou P, Guyatt G |title=Early stopping of randomized clinical trials for overt efficacy is problematic |journal=J Clin Epidemiol |volume=61 |issue=3 |pages=241–6 |year=2008 |month=March |pmid=18226746 |doi=10.1016/j.jclinepi.2007.07.016 |url=http://linkinghub.elsevier.com/retrieve/pii/S0895-4356(07)00292-2 |issn=}}</ref> A review of trials stopped early found that the earlier a trial was stopped the larger was its reported treatment effect<ref name="pmid16264162">{{cite journal |author=Montori VM, Devereaux PJ, Adhikari NK, ''et al'' |title=Randomized trials stopped early for benefit: a systematic review |journal=JAMA |volume=294 |issue=17 |pages=2203–9 |year=2005 |month=November |pmid=16264162 |doi=10.1001/jama.294.17.2203 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=16264162 |issn=}}</ref>, especially if the trial had less than 500 total events<ref>{{Cite journal | doi = 10.1001/jama.2010.310 | volume = 303 | issue = 12
| pages = 1180-1187 | last = Bassler | first = Dirk | coauthors = Matthias Briel, Victor M. Montori, Melanie Lane, Paul Glasziou, Qi Zhou, Diane Heels-Ansdell, Stephen D. Walter, Gordon H. Guyatt, and the STOPIT-2 Study Group | title = Stopping Randomized Trials Early for Benefit and Estimation of Treatment Effects: Systematic Review and Meta-regression Analysis | journal = JAMA | accessdate = 2010-03-25 | date = 2010-03-24 | url = http://jama.ama-assn.org/cgi/content/abstract/303/12/1180
}}</ref>. Accordingly, examples exists of trials whose interim analyses were significant, but the trial was continued and the final analysis was less significant or was insignificant.<ref name="pmid15894981">{{cite journal |author=Pocock S, Wang D, Wilhelmsen L, Hennekens CH |title=The data monitoring experience in the Candesartan in Heart Failure Assessment of Reduction in Mortality and morbidity (CHARM) program |journal=Am. Heart J. |volume=149 |issue=5 |pages=939–43 |year=2005 |month=May |pmid=15894981 |doi=10.1016/j.ahj.2004.10.038 |url=http://linkinghub.elsevier.com/retrieve/pii/S0002870305000189 |issn=}}</ref><ref name="pmid12559643">{{cite journal |author=Wheatley K, Clayton D |title=Be skeptical about unexpected large apparent treatment effects: the case of an MRC AML12 randomization |journal=Control Clin Trials |volume=24 |issue=1 |pages=66–70 |year=2003 |month=February |pmid=12559643 |doi= |url=http://linkinghub.elsevier.com/retrieve/pii/S0197245602002738 |issn=}}</ref><ref name="pmid12851279">{{cite journal |author=Abraham E, Reinhart K, Opal S, ''et al'' |title=Efficacy and safety of tifacogin (recombinant tissue factor pathway inhibitor) in severe sepsis: a randomized controlled trial |journal=JAMA |volume=290 |issue=2 |pages=238–47 |year=2003 |month=July |pmid=12851279 |doi=10.1001/jama.290.2.238 |url=http://jama.ama-assn.org/cgi/pmidlookup?view=long&pmid=12851279 |issn=}}</ref>  


Methods to correct for exaggeration exists.<ref name="pmid3231947">{{cite journal |author=Hughes MD, Pocock SJ |title=Stopping rules and estimation problems in clinical trials |journal=Stat Med |volume=7 |issue=12 |pages=1231–42 |year=1988 |month=December |pmid=3231947 |doi= |url= |issn=}}</ref><ref name="pmid2605969">{{cite journal |author=Pocock SJ, Hughes MD |title=Practical problems in interim analyses, with particular regard to estimation |journal=Control Clin Trials |volume=10 |issue=4 Suppl |pages=209S–221S |year=1989 |month=December |pmid=2605969 |doi= |url= |issn=}}</ref> A Bayesian approach to interim analysis may help reduce bias and adjust the estimate of effect.<ref name="pmid17577008">{{cite journal |author=Goodman SN |title=Stopping at nothing? Some dilemmas of data monitoring in clinical trials |journal=Ann. Intern. Med. |volume=146 |issue=12 |pages=882–7 |year=2007 |month=June |pmid=17577008 |doi= |url=http://www.annals.org/cgi/content/full/146/12/882 |issn=}}</ref>
Methods to correct for exaggeration exists.<ref name="pmid3231947">{{cite journal |author=Hughes MD, Pocock SJ |title=Stopping rules and estimation problems in clinical trials |journal=Stat Med |volume=7 |issue=12 |pages=1231–42 |year=1988 |month=December |pmid=3231947 |doi= |url= |issn=}}</ref><ref name="pmid2605969">{{cite journal |author=Pocock SJ, Hughes MD |title=Practical problems in interim analyses, with particular regard to estimation |journal=Control Clin Trials |volume=10 |issue=4 Suppl |pages=209S–221S |year=1989 |month=December |pmid=2605969 |doi= |url= |issn=}}</ref> A Bayesian approach to interim analysis may help reduce bias and adjust the estimate of effect.<ref name="pmid17577008">{{cite journal |author=Goodman SN |title=Stopping at nothing? Some dilemmas of data monitoring in clinical trials |journal=Ann. Intern. Med. |volume=146 |issue=12 |pages=882–7 |year=2007 |month=June |pmid=17577008 |doi= |url=http://www.annals.org/cgi/content/full/146/12/882 |issn=}}</ref>

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"A clinical trial is defined as a prospective scientific experiment that involves human subjects in whom treatment is initiated for the evaluation of a therapeutic intervention. In a randomized controlled clinical trial, each patient is assigned to receive a specific treatment intervention by a chance mechanism."[1] The theory behind these trials is that the value of a treatment will be shown in an objective way, and, though usually unstated, there is an assumption that the results of the trial will be applicable to the care of patients who have the condition that was treated.

Trials of potential treatments, for ethical reasons, tend to involve multiple stages, starting with small safety tests of the drug or other therapy. Once there is evidence of safety, and preliminary clinical trials, the effort moves to a larger scale: large multicentre clinical trials that are randomised, controlled, and double-blind using a control group of patients (i.e., "arm" of the trial) and an experimental arm.

Trials should be large, so that serious adverse events might be detected even when they occur rarely. Multi-centre trials minimise problems that can arise when a single geographical locus has a population that is not fully representative of the global population, and they can minimise the effect of geographical variations in environment and health care delivery. Randomisation (if the study population is large enough) should mean that the study groups are unbiased. A double-blind trial is one in which neither the patient nor the deliverer of the treatment is aware of the nature of the treatment offered to any particular individual, and this avoids bias caused by the expectations of either the doctor or the patient.

Ethical trials exist in a framework. Before any work with human subjects begins, an appropriate independent review board evaluates the proposed experiment, the risks and benefits to subjects, and way in which informed consent will be given to participation. During the trial, an external safety board monitors progress; it has access to the actual, not double-blinded, data. If the experimental arm of the treatment, in the judgment of the board, is significantly more dangerous than existing therapy, the board can stop the trial. If the experimental treatment is strikingly better than the control arm,

Major developments in randomized controlled trials

International Conference on Harmonization

In 1990, the steering committee was formed for the International Conference on Harmonization.[2] This led to the recommendations for Good Clinical Practices in the conduct of trials.[3] Some have considered these guidelines to be burdensome.[4]

Consort Statement

The quality of reporting of the conduct of randomized controlled trials remains problematic.[5]

In 1996, the Consort Statement was published which improved how trials are reported.[6] The statement was revised in 2001[7] and 2010[8]. As of 2005, among high impact journals, "CONSORT was mentioned in the instructions of 36 (22%) journals (see bmj.com), more often in general and internal medicine journals (8/15; 53%) than in specialty journals (28/152; 18%)".[9] Changes in 2010 includes reporting of trial registration, availability of the original protocol, and funding.

Trial registration

In 2004, the International Committee of Medical Journal Editors (ICMJE) announced that all trials starting enrollment after July 1, 2005 must be registered prior to consideration for publication in one of the 12 member journals of the Committee.[10]

Disclosure of Competing Interests

In 2009, the International Committee of Medical Journal Editors (ICMJE) announced a Uniform Format for Disclosure of Competing Interests in ICMJE Journals.[11]

Control group

"Control", according to the current Declaration of Helsinki ethical guides, may or may not involve a placebo. If there is no accepted treatment, or the disease is mild and self-limiting, placebo controls may be ethical. If there is accepted treatment, the best accepted treatment becomes the control arm. Trials that are controlled, but not by a placebo, still generate arguments about information value versus ethics.

Placebo controls are important, because the placebo effect can often be strong. The more value a subject believes an unknown drug has, but more placebo effect is has.[12] The use of historical rather than concurrent controls may lead to exaggerated estimated of effect.[13]

Placebo effect can be seen in controlled trials of surgical interventions with the control group received a sham procedure.[14][15][16]

The Hawthorne effect is the improvements seen in control subjects simply from participating in research.[17]

Blinding

Blinding is important, especially for trials that have subjective outcomes.[18] Trials that are not blinded tend to report more favorable results.[19]

Variations in design

Cluster-randomized trials

In some settings, health care providers, or healthcare institutions should be randomized rather than randomizing the research subjects.[20] This should occur when the intervention targets the provider or institutions and thus the results from each subject are not truly independent, but will cluster within the health care provider or healthcare institution. Guidelines exist for conducting cluster randomised trials.[21] Cluster-randomized trials are not always correctly designed and executed.[22]

Designing an adequately sized cluster-randomized trial is based on several factors. One factor is the intraclass (intracluster) correlation coefficient (ICC).[23][24] The ICC between clusters in analogous to the variance between subject in a randomized controlled trial. Just as in Student's t-test for randomized controlled trial more variance between subjects means a larger study is needed, the less correlation between clusters means more clusters are needed.

Before-after studies

Uncontrolled before-after studies and controlled before-after studies probably should not be considered variations of a randomized controlled trial, yet if carefully done offer advantages to observational studies.[25] As in a true cluster-randomized trial, the intervention group can be randomly assigned; however, unlike a cluster-randomized trial, the before-after study does not have enough clusters or groups. An interrupted time series analysis can try to improve plausibility of causation; however, interrupted time series are commonly performed incorrectly.[26]

Crossover trial

For more information, see: Cross-over study.

In crossover trials, patients start in intervention and controls, but later all patients switch groups.[27][28]

Delayed start trial

In this design, one group is randomized to receive treatment before the control group.[29] This design allows analysis for disease-modifying effects of treatments. An example of this design was a trial of rasagiline for Parkinson Disease.[30]

Dose ranging studies

Various study designs exit to determine the optimal dose of a new drug.

  • Crossover designs have been used.[31]
  • Designs that test doses in sequence, such as up and down studies[32] and adaptive dose-ranging trials[33], depend upon being able to measure an outcome from the medication that occurs quickly, and the drug's does can be titrated to achieve the effect.[34][35] An example of this type of outcome is blood pressure.
  • Parallel designs such as multi-level factorial studies have been used.[36] Special sample size calculations exist for these designs.[36]

Factorial design

Factorial randomized controlled trial: number of treatment failures due to severe hallucinations or alcohol withdrawal.[37]
Chlordiazepoxide
Given Not given
Propranolol Given 1 4
Not given 0 4
Notes:
1. There were 15 patients in each group.

A factorial design allows two interventions to be be studied with ability to measure the treatment effect of each intervention in isolation and in combination.[38][39] Interaction between the two treatments can be displayed with "interaction ratios or odds ratios accompanied by their confidence intervals"[38] and can be measured with the method of Gail and Simon[40] or the Breslow-Day test for homogeneity.

Many examples of factorial trials exist.[41] [42]

n of 1 trial

In a "n of 1" trial, also called single-subject randomized trials, a single patient randomly proceeds through multiple blinded crossover comparisons. This address the concerns that traditional randomized controlled trials may not generalize to a specific patient.[43]

Underlining the difficulty in extrapolating from large trials to individual patients, Sackett proposed the use of N of 1 randomized controlled trials. In these, the patient is both the treatment group and the placebo group, but at different times. Blinding must be done with the collaboration of the pharmacist, and treatment effects must appear and disappear quickly following introduction and cessation of the therapy. This type of trial can be performed for many chronic, stable conditions.[44] The individualized nature of the single-subject randomized trial, and the fact that it often requires the active participation of the patient (questionnaires, diaries), appeals to the patient and promotes better insight and self-management[45][46] as well as patient safety,[43] in a cost-effective manner.

Noninferiority and equivalence randomized trials

Noninferiority and equivalency randomized controlled trials.

As stated in The Declaration of Helsinki by the World Medical Association it is unethical to give any patient a placebo treatment if an existing treatment option is known to be beneficial.[47][48] Many scientists and ethicists consider that the U.S. Food and Drug Administration, by demanding placebo-controlled trials, encourages the systematic violation of the Declaration of Helsinki.[49] In addition, the use of placebo controls remains a convenient way to avoid direct comparisons with a competing drug.

The appropriate use of placebo is being revised.[50][51] When guidelines suggest a placebo is an unethical control, then an "active-control noninferiority trial" may be used.[52] To establish non-inferiority, the following three conditions should be - but frequently are not - established:[52]

  1. "The treatment under consideration exhibits therapeutic noninferiority to the active control."
  2. "The treatment would exhibit therapeutic efficacy in a placebo-controlled trial if such a trial were to be performed."
  3. "The treatment offers ancillary advantages in safety, tolerability, cost, or convenience."

Noninferiority and equivalence randomized trial are difficult to execute well.[52] Guidelines exists for noninferiority and equivalence randomized trials.[53] In planning the trial, the investigators should choose "a noninferiority or equivalence criterion, and specifying the margin of equivalence with the rationale for its choice."[53] In reporting the outcomes, the authors should present the confidence intervals to show the reader whether the result was within their noninferiority or equivalence criterion.[53]

Add-on design

"Sometimes a new agent can be assessed by using an 'add-on' study design in which all patients are given standard therapy and are randomly assigned to also receive either new agent or placebo."[50]

Pragmatic trials

Consort has described pragmatic trials and standards for their reporting.[54] CONSORT describes a pragmatic trial as addressing "does the intervention work when used in normal practice" as opposed to an "explanatory trial" that addresses "can the intervention work." CONSORT states the there is not a dichotomy of trial designs, but that pragmatic reflects an attitude in the design. CONSORT offers an example of a pragmatic trial[55] and an explanatory trial.[56]

The cohort multiple randomised controlled trial may be a practical variation of this design.[57]

Ethical issues

Background

The Belmont Report was released in 1979 by the National Commission for the Protection of Human Subjects in Biomedical and Behavioral Research.

The Declaration of Helsinki requires informed consent for participation in a trial. In the United States, there is an approval procedure for clinical trials in human subjects, whether for research only or for potential approval of a commercial drug. Most industrialized countries have such procedures; some permit reciprocal approvals.

In the United States, the Code of Federal Regulations (45 CFR 46.102(d)) regulates human subjects research.

Ethics of randomizing subjects

The appropriate use of placebo is being revised.[50][51][58] One tension is the balance between using placebo to increase scientific rigor versus the unnessessary deprival of active treatment to patients. This is the conundrum faced by Martin Arrowsmith in the book by the same name.[59][60]

Comparing a new intervention to a placebo control may not be ethical when an accepted, effective treatment exists. In this case, the new intervention should be compared to the active control to establish whether the standard of care should change.[61] The observation that industry sponsored research may be more likely to conduct trials that have positive results suggest that industry is not picking the most appropriate comparison group.[62] However, it is possible that industry is better at predicting which new innovations are likely to be successful and discontinuing research for less promising interventions before the trial stage.

There are times when placebo control is appropriate even when there is accepted, effective treatment.[50][51][58]

There are ethical concerns in comparing a surgical intervention to sham surgery; however, this has been done.[63][16] Guidelines by the American Medical Association address the use of placebo surgery.[64]

Interim analysis - stopping trials early

Trials are increasingly stopped early[65]; however, this may induce a bias that exaggerates results[66][65]. Data safety and monitoring boards that are independent of the trial are commissioned to conduct interim analyses and make decisions about stopping trials early.[67] [68]

Reasons to stop a trial early are efficacy, safety, and futility.[69][70]

Regarding efficacy, various rules exist that adjust alpha to decide when to stop a trial early.[71][72][73][74][75] A commonly recommended rules are the O'Brien-Fleming (the O'Brien-Fleming rule requires a varying p-value depending on the number of interim analyses) and the Haybittle-Peto (the Haybittle-Peto which requires p<0.001 to stop a trial early) rule.[71][72][76]

Using a more conservative stopping rule reduces the chance of a statistical alpha (Type I) error; however, these rules do not alter that the effect size may be exaggerated.[77][72] According to Bassler, "the more stringent the P-value threshold results must cross to justify stopping the trial, the more likely it is that a trial stopped early will overestimate the treatment effect."[70] A review of trials stopped early found that the earlier a trial was stopped the larger was its reported treatment effect[65], especially if the trial had less than 500 total events[78]. Accordingly, examples exists of trials whose interim analyses were significant, but the trial was continued and the final analysis was less significant or was insignificant.[79][80][81]

Methods to correct for exaggeration exists.[82][77] A Bayesian approach to interim analysis may help reduce bias and adjust the estimate of effect.[83]

As an alternative to the alpha rules, conditional power can help decide when to stop trials early.[84][85]

Seeding trials

Seeding trials are studies sponsored by industry whose "apparent purpose is to test a hypothesis. The true purpose is to get physicians in the habit of prescribing a new drug."[86]

Measuring outcomes

Subjectively assessed outcomes are more susceptible to bias in trials with inadequate allocation concealment.[87]

Missing data

Regarding assigning an outcome to the patient, using a 'last observation carried forward' (LOCF) analysis may introduce biases.[88]

Crossover between experimental groups

Regarding group assignment, a 'per protocol' analysis may introduce bias compared to an 'intention to treat' analysis. Intention to treat is not always adequately described.[89] This bias may be due to the observations that research subjects who adhere to therapy, whether the therapy be an active treatment or placebo, have a reduction in mortality.[90][91] Thus excluding non-compliant subjects would appear to exaggerate the effects of treatment; however the bias can go both directions.[92]

Surrogate outcomes

The costs and efforts required to measure primary endpoints such as morbidity and mortality make using surrogate outcomes an option. An example is in the treatment of osteoporosis, the primary outcomes are fractures and mortality whereas the surrogate outcome is changes in bone mineral density.[93][94] Other examples of surrogate outcomes are tumor shrinkage or changes in cholesterol level, blood pressure, HbA1c, CD4 cell count.[95] Surrogate markers might be acceptable when "the surrogate must be a correlate of the true clinical outcome and fully capture the net effect of treatment on the clinical outcome".[95]

Composite outcomes

Composite outcomes are problematic if the components of the composite vary in their magnitude and contribution to the composite.[96] [97] [98]

Overdiagnosis

For more information, see: Overdiagnosis.

In trials of mass screening, overdiagnosis is the diagnosis of non-harmful disease. [99] Overdiagnosis inflates the importance of the screening problem.

Adverse outcomes

Adverse effects may be discovered only after a trial is concluded, or in the larger populations to which a drug, approved for general release based on trial data, is used. Postmarketing surveillance is intended to detect hazards that the trials are not powerful enough to find.

Analysis

For more information, see: Statistics and Statistical significance.

Dichotomous outcomes may be summarized with relative risk reduction, absolute risk reduction, or the number needed to treat.

Planning analyses prior to conducting the trial

When protocols for trials are publicly accessible, discrepancies between planned and actual analyses may occur.[100][101]

Subgroup analyses

Subgroup analyses can be misleading due to failure to prespecify hypotheses and to account for multiple comparisons.[102][72][103]

Statistical methods exist for assessing the importance of subgroups.[104]

Assessing the quality of a trial

A comparison of the Cochrane Collaboration Tool, the Jadad score, and the Schulz approach found that the Cochrane Collaboration Tool required more time to complete, contained some subjective items, and did not well correlate with the Jadad score or Schulz approach.[105]

Cochrane bias scale

The Cochrane Collaboration uses a six item tool.[106] Trials that have high or uncertain bias are more likely to report large effect sizes.[105]

In using the Cochrane tool, if any of the first three items are low quality (randomization, allocation concealment before and during enrollment, blinding), the trial may be considered high or uncertain bias.[107]

Jadad score

For more information, see: Jadad score.

The Jadad score may be used to assess quality.[108] The scale focuses on three attributes: randomization, blinding, and dropouts.

Schulz

The Schulz approach assess the quality of allocation concealment.[109]

Publication bias

For more information, see: Publication bias.

Publication bias refers to the tendency that trials that show a positive significant effect are more likely to be published than those that show no effect or are inconclusive.

Trial registration

At the same time, in September 2004, the International Committee of Medical Journal Editors (ICMJE) announced that all trials starting enrollment after July 1, 2005 must be registered prior to consideration for publication in one of the 12 member journals of the Committee.[10] This move was to reduce the risk of publication bias as negative trials that are unpublished would be more easily discoverable.

Available trial registries include:

It is not clear how effective trial registration is because many registered trials are never completely published.[110]

External validation

Judging external validity is more difficult than judging internal validity. "External validity refers to the question whether results are generalizable to persons other than the population in the original study."[111] A framework for assessing external validity proposes:[111]

  1. "The study population might not be representative for the eligibility criteria that were intended. It should be addressed whether the study population differs from the intended source population with respect to characteristics that influence outcome."
  2. "The target population will, by definition, differ from the study population with respect to geographical, temporal and ethnical conditions. Pondering external validity means asking the question whether these differences may influence study results."
  3. "It should be assessed whether the study's conclusions can be generalized to target populations that do not meet all the eligibility criteria."

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