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Clinical Trials Potpourri: Databases, Trials and Meta-Analysis

Clinical Trials Potpourri: Databases, Trials and Meta-Analysis. Oh My!. Outline. Why Trials and Not Databases? Trial Design Randomization Proper Controls Intention To Treat Exclusions Withdrawals Metanalyses vs. Big And Simple Trials. Outline. Why Trials and Not Databases?

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Clinical Trials Potpourri: Databases, Trials and Meta-Analysis

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  1. Clinical Trials Potpourri:Databases, Trials and Meta-Analysis Oh My!

  2. Outline • Why Trials and Not Databases? • Trial Design • Randomization • Proper Controls • Intention To Treat • Exclusions • Withdrawals • Metanalyses vs. Big And Simple Trials

  3. Outline • Why Trials and Not Databases? • Trial Design • Randomization • Proper Controls • Intention To Treat • Exclusions • Withdrawals • Metanalyses vs. Big And Simple Trials

  4. LIMITATIONS OF DATABASES • Prospective approach not used • Randomization not used • “Selection Bias” should be assumed regardless of direction of treatment effect. • Regimen depends on: • patient presentation • severity of disease • Treated and controls systematically differ

  5. LIMITATIONS OF DATABASES • Adjustment for covariates inadequate • Unknown covariates affect outcome • Relevant covariates unavailable • Incomplete collection covariate data • Covariate errors compromise adjustment • Mismodeling -- never really known

  6. LIMITATIONS OF DATABASES • “Time Zero” not identified. • All patients or random sample? • Inadequate test of new therapy Databases serve as hypothesis generation for clinical trials

  7. Trial Design

  8. PREREQUISITES FOR SUCCESSFUL CLINICAL TRIALS • Trial Needs to be Done - Equipoise • Question is appropriate, unambiguous • Trial architecture is valid • Inclusion/Exclusion criteria balance efficiency and generalizability • Feasible • Administration effective Sacket 1983.

  9. KEY POINT OF TRIALS:PROPER CONTROL “Group against which intervention group is compared” • Placebo or “standard of care” • Modified slightly for Clinical Trials • Identifying and maintaining control group? • Can be an extremely difficult problem • Serious consequences if not done

  10. RANDOMIZATION PROCESS • Produce comparable study groups • Known and unknown risk factors • Removes bias in subject allocation • Guarantees statistical tests will have valid significance levels • Trialist’s most powerful weapon against bias

  11. EMPIRICAL EVIDENCE OF BIASCochrane Collaboration • Objective: Determine if inadequate randomized control design and execution are associated bias in estimating treatment effects. • Design: 250 controlled trials from 33 meta-analyses • Outcomes Tests: • Inadequate allocation • Inadequate sequence generation • Exclusions after randomization • Lack of double blind design KF Schulz, et al: JAMA 1995;273:408-412

  12. Inadequate Blinding and Bias KF Schulz, et al: JAMA 1995;273:408-412

  13. Inadequate Blinding and Bias Inadequate concealing (bliniding) of data associated with bias that cannot be controlled for KF Schulz, et al: JAMA 1995;273:408-412

  14. APPROPRIATE CONTROLS • Difficult to obtain unbiased sample • What is the appropriate control group? • Comparison groups similar as possible • Example: Select a number 0 - 9.

  15. RESULTS OF SELECTION: NUMBERS 0-9 • 0 and 9 usually under-represented • The extremes are not as often selected • Seeming preference for odd numbers • 3, 5, 7 will be more often selected

  16. INTENTION TO TREAT“ONCE IN, ALWAYS COUNTED” • Intention to treat analysis avoids bias • Excluding randomized subjects on the basis of outcome or response variables is worst kind of bias • Bias of unknown magnitude and direction • Intention to treat safeguards against erroneous efficacy when excluding subjects who do not adhere to protocol

  17. INTENTION TO TREAT“ONCE IN, ALWAYS COUNTED” Randomized controlled trials with outcome endpoints should all be intention to treat design

  18. EFFICACY (ON TREATMENT) ANALYSIS • Expected in pharmaceutical industry. • Precisely described • Denominator in two analyses will not be the same • Estimated benefit between two analyses • Should be reported without p-value

  19. EXCLUSION FROM TRIALS Pro Con Affects generalizability of results Investigators need to ensure group comparability • Before Randomization • Rationale: Eligibility criteria not met • No bias in comparison of group results • Follow-up those excluded? • Commonly as a registry

  20. EXCLUSION OF SOME EVENT • Prevention Trials - Immediate Events • Understand intervention? • Adverse effects may occur earlier • Present both analyses • Really a withdrawal trial. Do Not Do This!

  21. Outline • Why Trials and Not Databases? • Trial Design • Randomization • Proper Controls • Intention To Treat • Exclusions • Withdrawals • Metanalyses vs. Big And Simple Trials

  22. WITHDRAWALS • Similar to non-adherence, but more detrimental • Loss of information on treatment tolerance, efficacy • Can affect endpoints critically if no further follow up • Intention to treat will regard as censored

  23. STUDY POLICY ON WITHDRAWALS If done, should be done: • with methods stated a-priori • blinded • early in the study • but minimizing the number May still be challenged!

  24. EXAMPLES OF DESIGN POLICIES RELATED TO WITHDRAWALS • Enroll only those with secure diagnosis. • Enroll confirmed and unconfirmed, later withdraw those with diagnostic error. • Enroll confirmed and unconfirmed, allow no withdrawals.

  25. WITHDRAWALS INELIGIBILITY • Clerical error - Canadian Cooperative Trial • Definition - Surgical vs Medical Therapy in Bilateral Carotid Stenosis • Laboratory error - BHAT • Misinterpretation - MILIS • Mis-classificaiton - ANTURANE

  26. WITHDRAWALS INELIGIBILITY • Clerical error - Canadian Cooperative Trial • Definition - Surgical vs Medical Therapy in Bilateral Carotid Stenosis • Laboratory error - BHAT • Misinterpretation - MILIS • Misclassification - ANTURANE

  27. Withdrawals SURGICAL VERSUS MEDICAL THERAPY BILATERAL CAROTID STENOSIS Definition: “alive and stroke free after hospitalization”

  28. Withdrawals SURGICAL VERSUS MEDICAL THERAPY BILATERAL CAROTID STENOSIS Definition: “alive and stroke free after hospitalization”

  29. WITHDRAWALSEffects on Trial Outcomes a-priori definition for withdrawal - interpreted differently • Reanalysis: 19 deaths found in ineligibles • Original 10 vs. 4 death. Reanalysis 12 vs. 7 deaths • p using eligibles=0.07p using all =0.20 Mortality by study group and eligibility status: anturane (sulfinpyrazone) re-infarction trial

  30. POOR QUALITY OR MISSING DATA • Lost to follow-up – No endpoint ascertainment • Complete or near complete ascertainment is possible on clinical events Trials N Missing CDP 4 LRC 0 PHS 0 SHEP 6

  31. POOR QUALITY OR MISSING DATA • Other response variables • Imputation of missing data • 20% increase in efficacy • Survival analysis - time to event • Removal of outliers - similar results? • Worst case analysis

  32. Outline • Why Trials and Not Databases? • Trial Design • Randomization • Proper Controls • Intention To Treat • Exclusions • Withdrawals • Metanalyses vs. Big And Simple Trials

  33. Meta-Analysis Once upon a time, there were many magnesium trials…

  34. HOW DO WE USE META-ANALYSIS? SMALL TO MODERATE SIZED TRIALS AND LARGE SIMPLE TRIALS Studies: Effect of magnesium on mortality in immediate post-myocardial infarction Sequence of Investigations Meta-analysis - 1991Moderate Size Trial - 1992Mega Trial - 1995 Large Trial-2002

  35. INITIAL META-ANALYSISMAGNESIUM AND DEATH POST MI • 7 trials: 1301 participants • 657 (25) magnesium • 644 (53) controls • 55% relative reduction in mortality • 95% CI 0.28-0.71, p<0.001 • Biologically plausible result: • Ventricular arrhythmia reduced: 7 versus 109 • Adverse effects rare

  36. MAGNESIUM AND DEATH POST MIIncluded Trial Characteristics • All randomized, 6 blinded • Baseline characteristics balanced • 99.4% follow-up for mortality (8 patients) • Similar administration and dose • Treatment usually started within 12 hours • Dosage varied from 30-90 mmols • Infusion over 24-48 hours. Some bolus • Baseline and follow-up Mg levels similar • 1year mortality: 20% vs 32% from 2 studies

  37. MAGNESIUM TRIAL META-ANALYSIS

  38. MAGNESIUM TRIAL META-ANALYSIS

  39. Leicester Intravenous Magnesium Intervention Trial (LIMIT-2) • N= 2316 patients with suspected acute MI • Blinded placebo controlled • 65% confirmation of MI in both groups • 8 mmol over 5 minutes; 65 mmol over 24 hrs • Primary outcome - total mortality @ 28 days • 99.3% ascertainment • 24% mortality reduction(95%CI: 0.57-0.99,p = 0.04) • 25% reduction in left ventricular failure(95% CI = 0.61 - 0.91, p = 0.009)

  40. LIMIT- 2

  41. MAGNESIUM TRIAL META-ANALYSIS

  42. ISIS 4: INTERNATIONAL STUDY OF INFARCT SURVIVAL • N= 58,050 Participants • Entry up to 24 hours after onset of chest pain. • 2x2x2 factorial design: Treatments vs. Placebo • 1 month, up to 100 mg/d captopril • 1 month, controlled-release nitrate 60 mg/d • 24 hours magnesium. • 8 mmolsbolus, 72 mmols infusion • Primary End Point: All cause mortality

  43. MORTALITY IN DAYS 0-35 SUBDIVIDED BY OTHER RANDOMLY ALLOCATED STUDY TREATMENTS

  44. SYSTEMATIC OVERVIEW OF EFFECTS ON SHORT-TERM MORTALITY OF STARTING INTRAVENOUS MAGNESIUM EARLY IN ACUTE MYOCARDIAL INFARCTION

  45. Meta-AnalysesWHAT WENT WRONG?WHAT SHOULD WE BELIEVE? • Previous meta-analysis and clinical trial - small numbers • 99% CI in LIMIT-2 - no benefit • Increase in deaths ISIS-4 • p 0.07, 95% CI = +12-0% • No convergence or divergence - 1 year • 23,000 given bolus within 6 hours7.9% magnesium, 7.6% control • 17,000 no fibrinolytic therapy - no change • ISIS an open trial - no apparent problems

  46. LIMITATION OF META-ANALYSIS • Numbers per study is small • Number of outcomes (deaths) small • Potentially biased patient selection • Publication bias • Selection of endpoints - problematic • Duration of follow up: • Generally covered hospital stay • Limited long-term

  47. META-ANALYSIS • A systematic way of combining data to get a more precise estimate of the effect of a therapy. • Positives • Combine all available data. • Larger numbers of events available. • Estimate of therapeutic benefits possible. • Negatives • Loss of equipoise • Outcome numbers may be small • Uncritical examination • Importance • Sample size estimates • FDA submissions • Medical policy formulation

  48. CUMULATIVE META-ANALYSIS “The Performance Of Updating A Meta-Analysis Every Time A New Trial Appears” • Goal – Evaluating the results as a continuum. • Outcome – Supply practitioners with up-to-date information • Methods • “Fixed effects model” (Mantel-Haenszel Statistic) • “Random effects model” (DerSimonian-Laird Statistic) • Methods Evaluation – Little difference in results • Recommendation – Use both methods Lau et al – NEJM 1992:327: 248-254

  49. THROMBOLYTIC TRIALS

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