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Phase III Design

Phase III Design. The Gold Standard of Medical Research R. Chappell, BMI 542 - Spring 2018. INTRODUCTION. The foundation for the design of controlled experiments established for agricultural experiments

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Phase III Design

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  1. Phase III Design The Gold Standard of Medical Research R. Chappell, BMI 542 - Spring 2018

  2. INTRODUCTION • The foundation for the design of controlled experiments established for agricultural experiments • The need for control groups in clinical studies recognized, but not widely accepted until 1950s • No comparison groups needed when results dramatic: • Penicillin for pneumococcal pneumonia • Rabies vaccine(?) • Use of proper control group necessary due to: • Natural history of most diseases • Variability of a patient's response to intervention

  3. Outline: Designs for Randomized CTs • Choice of Control Group and Related Issues • Common Randomized Designs • Biomarker-Based Designs (Future Lecture & Precision Case Study) • Non-Inferiority Trials (Future Lecture)

  4. Outline: A. Choice of Control Group and Related Issues • Purpose of Control Group • Types of Control Groups • Significance of Control Group • Blinding / Masking

  5. 1. Purpose of Control Group • To allow discrimination of patient outcomes caused by test treatment from those caused by other factors • Natural progression of disease • Observer/patient expectations • Other treatment • Regression to the mean • Fair comparisons

  6. Considerations in Choice of Control Group • Available standard therapies • Adequacy of the evidence for the chosen design • Ethical considerations - E.g., Parkinson Study Group Trial:

  7. Parkinson Study Group Trial “Pramipexole vs Levodopa as Initial Treatment for Parkinson Disease”, PSG, JAMA. 2000; 284:1931-1938. From the Abstract: “Subjects were randomly assigned to receive pramipexole, 0.5 mg 3 times per day, with levodopa placebo (n = 151); or carbidopa/levodopa, 25/100 mg 3 times per day, with pramipexole placebo (n = 150).

  8. Furthermore: “For patients with residual disability, the dos- age was escalated during the first 10 weeks.” and “From week 11 to month 23.5, investigators were permitted to add open-label levodopa to treat continuing or emerging disability.” The results were significantly in favor of pramipexole.

  9. The results were significantly in favor of pramipexole. How do we interpret them?

  10. The results were significantly in favor of pramipexole. How do we interpret them? “Pramipexole, 0.5 mg 3 times per day, potentially escalated for lack of efficacy during the first 10 weeks and augmented with levadopa as needed between 11 weeks and 2 years, is superior to carbidopa/levodopa, 25/100 mg 3 times per day, similarly escalated and augmented as needed.”

  11. 2. Type of Controls • External • Historical • Concurrent, not randomized • Internal and concurrent • Placebo (Negative) • No treatment • Dose-response • Active (Positive) • Multiple • Active and placebo • Multiple doses of test drug and of an active control

  12. 3. Significance of Control Group • Inference drawn from the trial • Ethical acceptability of the trial • Degree to which bias is minimized • Type of subjects • Kind of endpoints that can be studies • Credibility of the results • Acceptability of the results by regulatory authorities • Other features of the trial, its conduct, and interpretation

  13. Use of Placebo Control • The “placebo effect” is well documented • When a new treatment is compared with no-treatment, use of placebo is necessary to demonstrate a non-placebo effect • Matched placebos are necessary so patients and investigators cannot decode the treatment assignment • E.g. Vitamin C trial for common cold • Placebo was used, but was distinguishable • Many on placebo dropped out of study • Those who knew they were on vitamin C reported fewer cold symptoms and duration than those on vitamin who didn't know

  14. Changes in Definitions

  15. Age-adjusted Death Rates for Selected Causes: United States, 1950-76 Time Trend

  16. Comparing Treatments • Fundamental principle • Groups must be alike in all important aspects and only differ in the treatment each group receives • In practical terms, “comparable treatment groups” means“alike on the average” • Randomization • Each patient has the same chance of receiving any of thetreatments under study • Allocation of treatments to participants is carried out using a chance mechanism so that neither the patient nor the physician know in advance which therapy will be assigned • Blinding (Masking) • Avoidance of psychological influence • Fair evaluation of outcomes

  17. 4. Blinding or Masking • No Blind • All patients know treatment • Single Blind • Patient does not know treatment • Double Blind • Neither patient nor health care provider know treatment • Triple Blind • Patient, physician and statistician/monitors do not know treatment – see Meinert’s “Blind Stupidity” • Double blind recommended when possible

  18. Blinding or Masking • Assures that subjects are similar with regard to post-treatment variables that could affect outcomes • Minimizes the potential biases resulting from differences in management, treatment, or assessment of patients, or interpretation of results • Avoids subjective assessment and decisions by knowing treatment assignment

  19. Feasibility of Masking • Ethics: The double-masking procedure should not result in any harm or undue risk to a patient • Practicality: It may be impossible to mask some treatments. Examples of heroic efforts: • NCCAM trial of acupuncture in peripheral neuropathy • Autologous CD133+ cells in critical limb ischemia • Vitamin K supplement study – double dummy design (see case study) • Gait quality in stroke victims • Avoidance of bias: Masked studies require extra effort (manufacturing look-alike pills, setting up coding systems, etc.)

  20. Feasibility of Masking, cont. • Compromise: Sometimes partial masking, e.g., independent masked evaluators, can be sufficient to reduce bias in treatment comparison. • Although masked trials require extra effort, sometimes they are the only way to obtain an objective answer to a clinical question. • Which kinds of questions are in greater need of blinding, and which don’t need it?

  21. Reasons for Subject Masking • Those on “no-treatment” or standard treatment may be discouraged or drop out of the study • Those on the new drug may exhibit a “placebo” effect, i.e., the new drug may appear better when it is actually not • Subject reporting and cooperation may be biased depending on how the subject feels about the treatment

  22. Unbiased Evaluation Subject Bias (NIH Cold Study) (Karlowski, 1975) Duration of Cold (Days) Blinded Unblinded Subjects Subjects Placebo 6.3 8.6 Ascorbic Acid 6.5 4.8

  23. Reasons for Treatment Team Masking • Treatment decisions can be biased by knowledge of the treatment, especially if the treatment team has preconceived ideas about either treatment • Dose modifications • Intensity of patient examination • Need for additional treatment • Influence on patient attitude through enthusiasm (or not) shown regarding the treatment

  24. Reasons for Evaluator Masking • If endpoint is subjective, evaluator bias will lead to recording more favorable responses on the preferred treatment • Even supposedly “hard” endpoints often require clinical judgment, e.g., blood pressure, MI

  25. Reasons for Monitoring Committee Masking • Treatments can be objectively evaluated • Recommendations to stop the trial for “ethical” reasons will not be based on personal biases • Triple-mask studies are hard to justify for reasons of safety and ethics • See “Blind Stupidity”, by Meinert.

  26. Masked monitoring (Meinert) • Years ago I wrote a piece entitled "Masked monitoring in clinical trials - Blind stupidity?" (NEJM 1998; 338:1381-2). I thought it ill-advised then and still do. Why the practice continues is beyond me. My fundamental problem with it is that it reduces the competency of the monitoring process in order to create the trappings of contrived objectivity. • It is imperative in meeting the ethical requirement for doing trials that somebody has unfettered access to study data without masking. If it is not the investigators, than it has to be the DSMC.

  27. B. Common Phase II or III Designs • Parallel • Factorial • Withdrawal • Group/Cluster • Randomized Consent (Response-Adaptive Randomization) • Cross Over • Sequential (as in Simon or Group-Sequential) C. Biomarker Based (separate lecture) D. Equivalence/Non-inferiority (separate lecture)

  28. Fundamental Design (2 arms) R A N D O M I Z E Yes Yes A Eligible Consent No B No Dropped Dropped Comment: Compare A with B

  29. 1. Parallel Design Screen Trt A Randomize - Trt B • H0: A vs. B • Advantage • Simple, General Use • Valid Comparison • Disadvantage • Few Questions/Study

  30. Run-In Problem: • Non-compliance by patient may seriously impair efficiency and possibly distort conclusions Possible Solutions: • Assign all eligible patients a placebo to be taken for a “brief” period of time. Patients who are “judged” compliant are enrolled into the study. This period of study is often referred to as the “Run-In” period.

  31. Run-In Possible Solutions, cont.: • Assign all eligible patients an active treatment before randomization; use those who are compliant, as before. Is this ethical? • Use some other intervention as a run-in; e.g., Vit D/Calcium in Vitamin K Bone Loss Case Study. See “Are placebo run ins justified?” Senn, BMJ 313, 1191-5. 1997.

  32. Run-In Design R A N D O M I Z E Run-In Period Satisfactory Screen & Consent A B Unsatisfactory Dropped Note: It is assumed that all patient entering the run-in period are eligible and have given consent

  33. 2. Factorial • Vary two or more factors simultaneously, randomize equal numbers (implying balance) to all combinations (implying completeness). • Designs result in “two [or more]” for the price of one analyses. • No free lunch – analyses assume that there is not interaction between treatments • Examples: • Women’s Health Study (imbalanced) • See “Factorial” Case Study

  34. Factorial Design • Schema A vs. Placebo B vs. Placebo

  35. 3. Withdrawal Study I Trt A Trt A -> II Not Trt A • H0: How long should TRT A continue? • Advantage • Easy Access to Subjects • Show continued Tx Beneficial • Disadvantage • Selected Population • Different Disease Stage

  36. Withdrawal Study See • Sorafenib & Renal Ca: Ratain, et al. JCO 24, 2505-2512. 2006. • Statler, Mol Cancer Ther 6: 1180-1185. 2007. • Comments for Clinicians: Friedlin & Simon. JCO 22, 5094-5098. 2005.

  37. 4. Cluster Randomization Designs • Groups (clinics, communities) are randomized to treatment or control • Examples: • Community trials on fluoridization of water • Breast self examination programs in different clinic setting in USSR • Smoking cessation intervention trial in different school district in the state of Washington

  38. 4. Cluster Randomization Designs, cont. • Advantages • Sometimes logistically more feasible • Avoid ”marketing contagion”. • Allow mass intervention, thus “public health trial” • Disadvantages • Effective sample size less than number of subjects • Many units must participate to overcome unit-to-unit variation,thus requires larger sample size • Need cluster sampling methods

  39. 5. Randomized Consent DesignZelen (NEJM, 1979) Group I: Regular Care (TRT A) Patient Randomize Group II: Experimental Consent (TRT B) NO (TRT A) YES (TRT B)

  40. 5. Randomized Consent, cont. Usual Order Proposed Order Screen Screen Consent Randomize Randomize Consent (from Exp. Group only) • Advantages • Easier Recruitment • Disadvantages • Need Low Refusal Rate • Control Must Be Standard • Unblinded • Ethical? How about no consent (Baxter blood study)?

  41. 6. Crossover DesignH0: A vs. B Scheme for the simplest “AB vs. BA” design Period Group I II AB 1 TRT A TRT B BA 2 TRT B TRT A • See Senn’s book (item G. in the course references).

  42. 6. Crossover Design, cont. • Advantage • Each patient their own control • Smaller sample size • Disadvantage • Not useful for acute disease • Disease must be stable • Assumes no treatment carry over • If carryover, have a study half sized • Need appropriate washout between periods

  43. 6. Crossover Design, cont. • Assumes no treatment carry over • What happens if A is ineffective and B has only delayed effectiveness? • What happens if A is ineffective and B is immediately and permanently effective? • Note that we cannot practically use the data to test for carryover. We would need enough subjects to do a parallel arm trial, obviating the need for a crossover study.

  44. 7. Sequential Design • Continue to randomize subjects until H0 is either rejected or “accepted” • A large statistical literature • Developed for industrial setting • Modified for clinical trials (e.g. Armitage 1975, Sequential Medical Trials)

  45. Classical Sequential Design • Continue to randomize subjects until H0 is either rejected or “accepted” • Classic Trt Better Continue Net Trt Effect 20  Accept H0 0 -20 Continue Trt Worse 100 200 300 No. of Paired Observations

  46. Classical Sequential Design • Assumptions • Acute Response • Paired Subjects • Continuous Testing • Fully sequential design ot widely used • Modified for group sequential designs

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