Randomized controlled trial: Difference between revisions

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Various rules exist for 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> A commonly recommended rule is the Haybittle-Peto which requires p<0.001 to stop a trial early.<ref name="pmid16264167"/><ref name="pmid15885299"/>
Various rules exist for 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> A commonly recommended rule is the Haybittle-Peto which requires p<0.001 to stop a trial early.<ref name="pmid16264167"/><ref name="pmid15885299"/>
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.


==Measuring outcomes==
==Measuring outcomes==

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Template:TOC-right "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.

The best trials are large multicentre clinical trials that are randomised, placebo-controlled, and double-blind. 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.

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.[2]

Variations in design

Cluster-randomized trials

In some settings, health care providers, or healthcare institutions should be randomized rather than randomizing the research subjects.[3] 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.[4] Cluster-randomized trials are not always correctly designed and executed.[5]

Designing an adequately sized cluster-randomized trial is based on several factors. One factor is the intraclass (intracluster) correlation coefficient (ICC).[6][7] 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.[8] 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.[9]

Crossover trial

In crossover trials, patients start in intervention and controls, but later all patients switch groups.[10]

Factorial design
Intervention A
Given Not given
Intervention B Given Group 1 Group 2
Not given Group 3 Group 4

Factorial design

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.

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.[11]

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.[12] 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[13][14] as well as patient safety,[11] in a cost-effective manner.

Noninferiority and equivalence randomized trials

In the treatment of the sick person, the physician must be free to use a new diagnostic and therapeutic measure, if in his or her judgment it offers hope of saving life, re-establishing health or alleviating suffering.

The potential benefits, hazards and discomfort of a new method should be weighed against the advantages of the best current diagnostic and therapeutic methods.

In any medical study, every patient- including those of a control group, if any- should be assured of the best proven diagnostic and therapeutic method.

The physician can combine medical research with professional care, the objective being the acquisition of new medical knowledge,only to the extent that medical research is justified by its potential diagnostic or therapeutic value for the patient.

From The Declaration of Helsinki [15]

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.[16][17] 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.[18] 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.[19][20] When guidelines suggest a placebo is an unethical control, then an "active-control noninferiority trial" may be used.[21] To establish non-inferiority, the following three conditions should be - but frequently are not - established:[21]

  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.[21] Guidelines exists for noninferiority and equivalence randomized trials.[22]

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."[19]

Ethical issues

Ethics of randomizing subjects

The appropriate use of placebo is being revised.[19][20][23]

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.[24] 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.[25] 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.[19][20][23]

There are ethical concerns in comparing a surgical intervention to sham surgery; however, this has been done.[26][27] Guidelines by the American Medical Association address the use of placebo surgery.[28]

Stopping trials early

Trials are increasingly stopped early[29]; however, this may induce a bias.[30]

Various rules exist for when to stop a trial early.[31][32][33][34] A commonly recommended rule is the Haybittle-Peto which requires p<0.001 to stop a trial early.[31][32]

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.

Measuring outcomes

Subjectively assessed outcomes are more susceptible to bias in trials with inadequate allocation concealment.[35]

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

Surrogate measures

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.[36][37] Other examples of surrogate outcomes are tumor shrinkage or changes in cholesterol level, blood pressure, HbA1c, CD4 cell count.[38] 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".[38]

Subgroup analyses

Subgroup analyses can be misleading due to failure to prespecify hypotheses and to account for multiple comparisons.[39][40]

Assessing the quality of a trial

The Jadad score may be used to assess quality and contains three items:[41]

  1. Was the study described as randomized (this includes the use of words such

as randomly, random, and randomization)?

  1. Was the study described as double blind?
  2. Was there a description of withdrawals and dropouts?

Each question is scored one point for a yes answer. In addition, for questions and 2, a point is added if the method was appropriate and a point is deducted if the method is not appropriate (e.g. not effectively randomized or not effectively double-blinded).

External validation

References

  1. ↑ Stanley K (2007). "Design of randomized controlled trials". Circulation 115 (9): 1164–9. DOI:10.1161/CIRCULATIONAHA.105.594945. PMID 17339574. Research Blogging.
  2. ↑ Waber, Rebecca L., Baba Shiv, Ziv Carmon, and Dan Ariely. 2008. Commercial Features of Placebo and Therapeutic Efficacy. JAMA 299, no. 9:1016-1017.
  3. ↑ Wears RL (2002). "Advanced statistics: statistical methods for analyzing cluster and cluster-randomized data". Academic emergency medicine : official journal of the Society for Academic Emergency Medicine 9 (4): 330–41. PMID 11927463. [e]
  4. ↑ Campbell MK, Elbourne DR, Altman DG (2004). "CONSORT statement: extension to cluster randomised trials". BMJ 328 (7441): 702–8. DOI:10.1136/bmj.328.7441.702. PMID 15031246. Research Blogging.
  5. ↑ Eldridge, S., Ashby, D., Bennett, C., Wakelin, M., & Feder, G. (2008). Internal and external validity of cluster randomised trials: systematic review of recent trials. BMJ, http://www.bmj.com/cgi/content/full/bmj.39517.495764.25v1 DOI:10.1136/bmj.39517.495764.25 10.1136/bmj.39517.495764.25.
  6. ↑ Campbell MK, Fayers PM, Grimshaw JM (2005). "Determinants of the intracluster correlation coefficient in cluster randomized trials: the case of implementation research". Clin Trials 2 (2): 99–107. PMID 16279131. [e]
  7. ↑ Campbell M, Grimshaw J, Steen N (2000). "Sample size calculations for cluster randomised trials. Changing Professional Practice in Europe Group (EU BIOMED II Concerted Action)". J Health Serv Res Policy 5 (1): 12–6. PMID 10787581. [e]
  8. ↑ Wyatt JC, Wyatt SM (2003). "When and how to evaluate health information systems?". Int J Med Inform 69 (2-3): 251–9. DOI:10.1016/S1386-5056(02)00108-9. PMID 12810128. Research Blogging.
  9. ↑ Ramsay CR, Matowe L, Grilli R, Grimshaw JM, Thomas RE (2003). "Interrupted time series designs in health technology assessment: lessons from two systematic reviews of behavior change strategies". Int J Technol Assess Health Care 19 (4): 613–23. PMID 15095767. [e]
  10. ↑ Sibbald B, Roberts C (1998). "Understanding controlled trials. Crossover trials". BMJ 316 (7146): 1719. PMID 9614025. [e]
  11. ↑ 11.0 11.1 Mahon J, Laupacis A, Donner A, Wood T (1996). "Randomised study of n of 1 trials versus standard practice". BMJ 312 (7038): 1069–74. PMID 8616414. [e] Cite error: Invalid <ref> tag; name "pmid8616414" defined multiple times with different content
  12. ↑ Guyatt G et al (1988). "A clinician's guide for conducting randomized trials in individual patients". CMAJ 139: 497–503. PMID 3409138. [e]
  13. ↑ Brookes ST et al. (2007). ""Me's me and you's you": Exploring patients' perspectives of single patient (n-of-1) trials in the UK". Trials 8: 10. DOI:10.1186/1745-6215-8-10. PMID 17371593. Research Blogging.
  14. ↑ Langer JC et al. (1993). "The single-subject randomized trial. A useful clinical tool for assessing therapeutic efficacy in pediatric practice". Clinical Pediatrics 32: 654–7. PMID 8299295. [e]
  15. ↑ World Medical Organization. (1996) Declaration of Helsinki. BMJ 313:1448-1449. hosted at cirp.org
  16. ↑ World Medical Association. Declaration of Helsinki: Ethical Principles for Medical Research Involving Human Subjects. Retrieved on 2007-11-17.
  17. ↑ (1997) "World Medical Association declaration of Helsinki. Recommendations guiding physicians in biomedical research involving human subjects". JAMA 277: 925–6. PMID 9062334. [e]
  18. ↑ Michels KB, Rothman KJ (2003). "Update on unethical use of placebos in randomised trials". Bioethics 17: 188–204. PMID 12812185. [e]
  19. ↑ 19.0 19.1 19.2 19.3 Temple R, Ellenberg SS (2000). "Placebo-controlled trials and active-control trials in the evaluation of new treatments. Part 1: ethical and scientific issues". Ann Intern Med 133: 455–63. PMID 10975964. [e]
  20. ↑ 20.0 20.1 20.2 Ellenberg SS, Temple R (2000). "Placebo-controlled trials and active-control trials in the evaluation of new treatments. Part 2: practical issues and specific cases". Ann Intern Med 133: 464–70. PMID 10975965. [e]
  21. ↑ 21.0 21.1 21.2 Kaul S, Diamond GA (2006). "Good enough: a primer on the analysis and interpretation of noninferiority trials". Ann Intern Med 145: 62–9. PMID 16818930. [e] Cite error: Invalid <ref> tag; name "pmid16818930" defined multiple times with different content
  22. ↑ Piaggio G, Elbourne DR, Altman DG, Pocock SJ, Evans SJ (2006). "Reporting of noninferiority and equivalence randomized trials: an extension of the CONSORT statement". JAMA 295 (10): 1152–60. DOI:10.1001/jama.295.10.1152. PMID 16522836. Research Blogging.
  23. ↑ 23.0 23.1 Emanuel EJ, Miller FG (2001). "The ethics of placebo-controlled trials--a middle ground". N. Engl. J. Med. 345 (12): 915–9. PMID 11565527. [e]
  24. ↑ Rothman KJ, Michels KB (1994). "The continuing unethical use of placebo controls". N. Engl. J. Med. 331 (6): 394–8. PMID 8028622. [e]
  25. ↑ Djulbegovic B, Lacevic M, Cantor A, et al (2000). "The uncertainty principle and industry-sponsored research". Lancet 356 (9230): 635–8. PMID 10968436. [e]
  26. ↑ Cobb LA, Thomas GI, Dillard DH, Merendino KA, Bruce RA: An evaluation of internal-mammary-artery ligation by a double-blind technique. N Engl J Med 1959;260:1115-1118.
  27. ↑ Moseley JB, O'Malley K, Petersen NJ, et al (2002). "A controlled trial of arthroscopic surgery for osteoarthritis of the knee". N. Engl. J. Med. 347 (2): 81–8. DOI:10.1056/NEJMoa013259. PMID 12110735. Research Blogging.
  28. ↑ Tenery R, Rakatansky H, Riddick FA, et al (2002). "Surgical "placebo" controls". Ann. Surg. 235 (2): 303–7. PMID 11807373. [e]
  29. ↑ Montori VM, Devereaux PJ, Adhikari NK, et al (November 2005). "Randomized trials stopped early for benefit: a systematic review". JAMA 294 (17): 2203–9. DOI:10.1001/jama.294.17.2203. PMID 16264162. Research Blogging.
  30. ↑ 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
  31. ↑ 31.0 31.1 Pocock SJ (November 2005). "When (not) to stop a clinical trial for benefit". JAMA 294 (17): 2228–30. DOI:10.1001/jama.294.17.2228. PMID 16264167. Research Blogging.
  32. ↑ 32.0 32.1 Schulz KF, Grimes DA (2005). "Multiplicity in randomised trials II: subgroup and interim analyses". Lancet 365 (9471): 1657–61. DOI:10.1016/S0140-6736(05)66516-6. PMID 15885299. Research Blogging.
  33. ↑ Grant A (September 2004). "Stopping clinical trials early". BMJ 329 (7465): 525–6. DOI:10.1136/bmj.329.7465.525. PMID 15345605. Research Blogging.
  34. ↑ O'Brien PC, Fleming TR (September 1979). "A multiple testing procedure for clinical trials". Biometrics 35 (3): 549–56. PMID 497341. [e]
  35. ↑ Wood, Lesley; Matthias Egger, Lise Lotte Gluud, Kenneth F Schulz, Peter Juni, Douglas G Altman, Christian Gluud, Richard M Martin, Anthony J G Wood, Jonathan A C Sterne (2008-03-15). "Empirical evidence of bias in treatment effect estimates in controlled trials with different interventions and outcomes: meta-epidemiological study". BMJ 336 (7644): 601-605. DOI:10.1136/bmj.39465.451748.AD. Retrieved on 2008-03-14. Research Blogging.
  36. ↑ Li Z, Chines AA, Meredith MP (2004). "Statistical validation of surrogate endpoints: is bone density a valid surrogate for fracture?". J Musculoskelet Neuronal Interact 4 (1): 64–74. DOI:10.1081/BIP-120024209. PMID 15615079. Research Blogging.
  37. ↑ Li Z, Meredith MP (2003). "Exploring the relationship between surrogates and clinical outcomes: analysis of individual patient data vs. meta-regression on group-level summary statistics". J Biopharm Stat 13 (4): 777–92. DOI:10.1081/BIP-120024209. PMID 14584722. Research Blogging.
  38. ↑ 38.0 38.1 Fleming TR, DeMets DL (1996). "Surrogate end points in clinical trials: are we being misled?". Ann. Intern. Med. 125 (7): 605–13. PMID 8815760. [e]
  39. ↑ Wang R, Lagakos SW, Ware JH, Hunter DJ, Drazen JM (2007). "Statistics in medicine--reporting of subgroup analyses in clinical trials". N. Engl. J. Med. 357 (21): 2189–94. DOI:10.1056/NEJMsr077003. PMID 18032770. Research Blogging.
  40. ↑ Yusuf S, Wittes J, Probstfield J, Tyroler HA (1991). "Analysis and interpretation of treatment effects in subgroups of patients in randomized clinical trials". JAMA 266 (1): 93–8. PMID 2046134. [e]
  41. ↑ Jadad AR, Moore RA, Carroll D, et al (1996). "Assessing the quality of reports of randomized clinical trials: is blinding necessary?". Control Clin Trials 17 (1): 1–12. DOI:10.1016/0197-2456(95)00134-4. PMID 8721797. Research Blogging.

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