Randomized controlled trial: Difference between revisions

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==Variations in design==
==Variations in design==
===Cluster-randomized trials===
===Cluster-randomized trials===
In some settings, health care providers, or healthcare institutions should be randomized rather than randomizing the research subjects.<ref name="pmid-11927463">{{cite journal |author=Wears RL |title=Advanced statistics: statistical methods for analyzing cluster and cluster-randomized data |journal=Academic emergency medicine : official journal of the Society for Academic Emergency Medicine |volume=9 |issue=4 |pages=330–41 |year=2002 |pmid=11927463 |doi=}}</ref> 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.<ref name="pmid-15031246">{{cite journal |author=Campbell MK, Elbourne DR, Altman DG |title=CONSORT statement: extension to cluster randomised trials |journal=BMJ |volume=328 |issue=7441 |pages=702–8 |year=2004 |pmid=15031246 |doi=10.1136/bmj.328.7441.702|url=http://www.bmj.com/cgi/content/full/328/7441/702}}</ref> Cluster-randomized trials are not always correctly designed and executed.<ref> 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}}.
In some settings, health care providers, or healthcare institutions should be randomized rather than randomizing the research subjects.<ref name="pmid-11927463">{{cite journal |author=Wears RL |title=Advanced statistics: statistical methods for analyzing cluster and cluster-randomized data |journal=Academic emergency medicine : official journal of the Society for Academic Emergency Medicine |volume=9 |issue=4 |pages=330–41 |year=2002 |pmid=11927463 |doi=}}</ref> 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.<ref name="pmid-15031246">{{cite journal |author=Campbell MK, Elbourne DR, Altman DG |title=CONSORT statement: extension to cluster randomised trials |journal=BMJ |volume=328 |issue=7441 |pages=702–8 |year=2004 |pmid=15031246 |doi=10.1136/bmj.328.7441.702|url=http://www.bmj.com/cgi/content/full/328/7441/702}}</ref> Cluster-randomized trials are not always correctly designed and executed.<ref> 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}}.</ref>
 
</ref>


Designing an adequately sized cluster-randomized trial is based on several factors. One factor is the intraclass (intracluster) correlation coefficient (ICC).<ref name="pmid16279131">{{cite journal |author=Campbell MK, Fayers PM, Grimshaw JM |title=Determinants of the intracluster correlation coefficient in cluster randomized trials: the case of implementation research |journal=Clin Trials |volume=2 |issue=2 |pages=99–107 |year=2005 |pmid=16279131 |doi=}}</ref><ref name="pmid10787581">{{cite journal |author=Campbell M, Grimshaw J, Steen N |title=Sample size calculations for cluster randomised trials. Changing Professional Practice in Europe Group (EU BIOMED II Concerted Action) |journal=J Health Serv Res Policy |volume=5 |issue=1 |pages=12–6 |year=2000 |pmid=10787581 |doi=}}</ref> 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.
Designing an adequately sized cluster-randomized trial is based on several factors. One factor is the intraclass (intracluster) correlation coefficient (ICC).<ref name="pmid16279131">{{cite journal |author=Campbell MK, Fayers PM, Grimshaw JM |title=Determinants of the intracluster correlation coefficient in cluster randomized trials: the case of implementation research |journal=Clin Trials |volume=2 |issue=2 |pages=99–107 |year=2005 |pmid=16279131 |doi=}}</ref><ref name="pmid10787581">{{cite journal |author=Campbell M, Grimshaw J, Steen N |title=Sample size calculations for cluster randomised trials. Changing Professional Practice in Europe Group (EU BIOMED II Concerted Action) |journal=J Health Serv Res Policy |volume=5 |issue=1 |pages=12–6 |year=2000 |pmid=10787581 |doi=}}</ref> 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.
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"Sometimes a new agent can be assessed by using an 'add-on' study design in which all patients
"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."<ref name="pmid10975964">{{cite journal |author=Temple R, Ellenberg SS |title=Placebo-controlled trials and active-control trials in the evaluation of new treatments. Part 1: ethical and scientific issues |journal=Ann Intern Med |volume=133 |pages=455–63 |year=2000 |pmid=10975964 |doi=|url=http://www.annals.org/cgi/content/full/133/6/455}}</ref>
are given standard therapy and are randomly assigned to also receive either new agent or placebo."<ref name="pmid10975964">{{cite journal |author=Temple R, Ellenberg SS |title=Placebo-controlled trials and active-control trials in the evaluation of new treatments. Part 1: ethical and scientific issues |journal=Ann Intern Med |volume=133 |pages=455–63 |year=2000 |pmid=10975964 |doi=|url=http://www.annals.org/cgi/content/full/133/6/455}}</ref>
===Pragmatic trials===
[http://www.consort-statement.org/ Consort] has described pragmatic trials and standards for their reporting.<ref name="pmid19001484">{{cite journal |author=Zwarenstein M, Treweek S, Gagnier JJ, ''et al'' |title=Improving the reporting of pragmatic trials: an extension of the CONSORT statement |journal=BMJ |volume=337 |issue= |pages=a2390 |year=2008 |pmid=19001484 |doi= |url=http://bmj.com/cgi/pmidlookup?view=long&pmid=19001484 |issn=}}</ref> 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<ref name="pmid16980316">{{cite journal |author=Thomas KJ, MacPherson H, Thorpe L, ''et al'' |title=Randomised controlled trial of a short course of traditional acupuncture compared with usual care for persistent non-specific low back pain |journal=BMJ |volume=333 |issue=7569 |pages=623 |year=2006 |month=September |pmid=16980316 |pmc=1570824 |doi=10.1136/bmj.38878.907361.7C |url=http://bmj.com/cgi/pmidlookup?view=long&pmid=16980316 |issn=}}</ref> and an explanatory trial.<ref name="pmid1852179">{{cite journal |author= |title=Beneficial effect of carotid endarterectomy in symptomatic patients with high-grade carotid stenosis. North American Symptomatic Carotid Endarterectomy Trial Collaborators |journal=N. Engl. J. Med. |volume=325 |issue=7 |pages=445–53 |year=1991 |month=August |pmid=1852179 |doi= |url= |issn=}}</ref>


==Ethical issues==
==Ethical issues==

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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

Variations on the standard AB, BA design have been proposed.[11][12][13][14]

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.[15]

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.[16] 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[17][18] as well as patient safety,[15] 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[19]

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.[20][21] 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.[22] 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.[23][24] When guidelines suggest a placebo is an unethical control, then an "active-control noninferiority trial" may be used.[25] To establish non-inferiority, the following three conditions should be - but frequently are not - established:[25]

  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.[25] Guidelines exists for noninferiority and equivalence randomized trials.[26]

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."[23]

Pragmatic trials

Consort has described pragmatic trials and standards for their reporting.[27] 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[28] and an explanatory trial.[29]

Ethical issues

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.

Ethics of randomizing subjects

The appropriate use of placebo is being revised.[23][24][30] 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.[31][32]

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.[33] 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.[34] 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.[23][24][30]

There are ethical concerns in comparing a surgical intervention to sham surgery; however, this has been done.[35][36] Guidelines by the American Medical Association address the use of placebo surgery.[37]

Interim analysis - stopping trials early

Trials are increasingly stopped early[38]; 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.[39] [40]

Reasons to stop a trial early are efficacy, safety, and futility.[41][42]

Regarding efficacy, various rules exist that adjust alpha to decide when to stop a trial early.[43][44][45][46] 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.[43][44][47]

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.[48][44] 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."[42] A review of trials stopped early found that the earlier a trial was stopped the larger was its reported treatment effect.[38] 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.[49][50][51] Methods to correct for exaggeration exists.[52][48]

As an alternative to the alpha rules, conditional power can help decide when to stop trials early.[53][54]

Measuring outcomes

Subjectively assessed outcomes are more susceptible to bias in trials with inadequate allocation concealment.[55]

Missing data

Missing data created decisions regarding what outcome to assign to that patient and what experimental group to assign the patient to.

  • Regarding assigning an outcome to the patient, using a 'last observation carried forward' (LOCF) analysis may introduce biases.[56]
  • Regarding group assignment, a 'per protocol' analysis may introduce bias compared to an 'intention to treat' analysis.

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.[57][58] Other examples of surrogate outcomes are tumor shrinkage or changes in cholesterol level, blood pressure, HbA1c, CD4 cell count.[59] 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".[59]

Analysis

For more information, see: Statistics.

When protocols for trials are publicly accessible, discrepancies between planned and actual analyses may be found.[60]

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

Subgroup analyses

Subgroup analyses can be misleading due to failure to prespecify hypotheses and to account for multiple comparisons.[61][44][62]

Assessing the quality of a trial

Cochrane bias scale

The Cochrane Collaboration uses a six item tool.[63]

Jadad score

The Jadad score may be used to assess quality and contains three items:[64]

  1. Was the study described as randomized (this includes the use of words such as randomly, random, and randomization)?
  2. Was the study described as double blind?
  3. 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).

Publication bias

For more information, see: Publication bias.

On September 30, 2004, Merck withdrew the cyclooxygenase 2 inhibitor medication rofecoxib from the market. This led to discovery that the manufacturer of rofecoxib, Merck, might have withheld information about adverse effects from the New England Journal of Medicine when the VIGOR randomized controlled trial was published.[65].

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.[66] This move was to reduce the risk of publication bias as negative trials that are unpublished would be more easily discoverable.

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. ↑ Laska E, Meisner M, Kushner HB (December 1983). "Optimal crossover designs in the presence of carryover effects". Biometrics 39 (4): 1087–91. PMID 6671121. [e]
  12. ↑ Boon PC, Roes KC (March 1999). "Design and analysis issues for crossover designs in phase I clinical studies". J Biopharm Stat 9 (1): 109–28. PMID 10091913. [e]
  13. ↑ Ebbutt AF (March 1984). "Three-period crossover designs for two treatments". Biometrics 40 (1): 219–24. PMID 6733230. [e]
  14. ↑ Matthews JN (December 1994). "Multi-period crossover trials". Stat Methods Med Res 3 (4): 383–405. PMID 7889228. [e]
  15. ↑ 15.0 15.1 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
  16. ↑ Guyatt G et al (1988). "A clinician's guide for conducting randomized trials in individual patients". CMAJ 139: 497–503. PMID 3409138. [e]
  17. ↑ 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.
  18. ↑ 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]
  19. ↑ Rickham PP (July 1964). "Human Experimentation. Code of Ethics of the World Medical Association. Declaration of Helsinki". British Medical Journal 2 (5402): 177. PMID 14150898. PMC 1816102. [e]
  20. ↑ World Medical Association. Declaration of Helsinki: Ethical Principles for Medical Research Involving Human Subjects. Retrieved on 2007-11-17.
  21. ↑ (1997) "World Medical Association declaration of Helsinki. Recommendations guiding physicians in biomedical research involving human subjects". JAMA 277: 925–6. PMID 9062334. [e]
  22. ↑ Michels KB, Rothman KJ (2003). "Update on unethical use of placebos in randomised trials". Bioethics 17: 188–204. PMID 12812185. [e]
  23. ↑ 23.0 23.1 23.2 23.3 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]
  24. ↑ 24.0 24.1 24.2 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]
  25. ↑ 25.0 25.1 25.2 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
  26. ↑ 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.
  27. ↑ Zwarenstein M, Treweek S, Gagnier JJ, et al (2008). "Improving the reporting of pragmatic trials: an extension of the CONSORT statement". BMJ 337: a2390. PMID 19001484. [e]
  28. ↑ Thomas KJ, MacPherson H, Thorpe L, et al (September 2006). "Randomised controlled trial of a short course of traditional acupuncture compared with usual care for persistent non-specific low back pain". BMJ 333 (7569): 623. DOI:10.1136/bmj.38878.907361.7C. PMID 16980316. PMC 1570824. Research Blogging.
  29. ↑ (August 1991) "Beneficial effect of carotid endarterectomy in symptomatic patients with high-grade carotid stenosis. North American Symptomatic Carotid Endarterectomy Trial Collaborators". N. Engl. J. Med. 325 (7): 445–53. PMID 1852179. [e]
  30. ↑ 30.0 30.1 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]
  31. ↑ Hausler, Thomas (2008-05-01). "In retrospect: When business became biology's plague". Nature 453 (7191): 38. DOI:10.1038/453038a. ISSN 0028-0836. Retrieved on 2008-11-12. Research Blogging.
  32. ↑ Pastor, John (2008-06-26). "The ethical basis of the null hypothesis". Nature 453 (7199): 1177. DOI:10.1038/4531177b. ISSN 0028-0836. Retrieved on 2008-11-12. Research Blogging.
  33. ↑ Rothman KJ, Michels KB (1994). "The continuing unethical use of placebo controls". N. Engl. J. Med. 331 (6): 394–8. PMID 8028622. [e]
  34. ↑ Djulbegovic B, Lacevic M, Cantor A, et al (2000). "The uncertainty principle and industry-sponsored research". Lancet 356 (9230): 635–8. PMID 10968436. [e]
  35. ↑ 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.
  36. ↑ 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.
  37. ↑ Tenery R, Rakatansky H, Riddick FA, et al (2002). "Surgical "placebo" controls". Ann. Surg. 235 (2): 303–7. PMID 11807373. [e]
  38. ↑ 38.0 38.1 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.
  39. ↑ 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
  40. ↑ Slutsky AS, Lavery JV (March 2004). "Data Safety and Monitoring Boards". N. Engl. J. Med. 350 (11): 1143–7. DOI:10.1056/NEJMsb033476. PMID 15014189. Research Blogging.
  41. ↑ Borer JS, Gordon DJ, Geller NL (April 2008). "When should data and safety monitoring committees share interim results in cardiovascular trials?". JAMA 299 (14): 1710–2. DOI:10.1001/jama.299.14.1710. PMID 18398083. Research Blogging.
  42. ↑ 42.0 42.1 Bassler D, Montori VM, Briel M, Glasziou P, Guyatt G (March 2008). "Early stopping of randomized clinical trials for overt efficacy is problematic". J Clin Epidemiol 61 (3): 241–6. DOI:10.1016/j.jclinepi.2007.07.016. PMID 18226746. Research Blogging.
  43. ↑ 43.0 43.1 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.
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