Statistical Issues at FDAStatistical Issues at FDAStatistical Issues at FDAStatistical Issues at FDA

Greg Soon, Ph.D.

Statistical Team Leader for Anti-viral Products

FDA/CDER/OB/DBIII

2006.3.2. 3:30-4:30 University of Maryland

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DisclaimerDisclaimerDisclaimerDisclaimer

The opinions expressed are those of the author and do not necessarily reflect those of the FDA.

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OverviewOverviewOverviewOverview

• Statistical Issues at FDA– General discussion

• Computer Intensive and Re-randomization Tests in Clinical Trials

• From Intermediate endpoint to final endpoint: a conditional power approach for accelerated approval and interim analysis

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1. Statistical Issues at FDA1. Statistical Issues at FDA1. Statistical Issues at FDA1. Statistical Issues at FDA

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Statistician in FDAStatistician in FDAStatistician in FDAStatistician in FDA

• Review clinical trial protocols to ensure the design, conduct and analysis will meet regulatory requirements

• Review New Drug Applications to determine if the trial outcome meet regulatory standard for marketing approval

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Statistician in FDAStatistician in FDAStatistician in FDAStatistician in FDA• Submissions are reviewed by clinicians, statisticians,

chemists, toxicologists, pharmacologists and microbiologists

• CDER Has about 100 statisticians

• Statisticians are organized in teams and divisions, each team serve one therapeutic area, like anti-viral drug products

– Anti-viral deals with HIV, hepatitis, flu, cold, and herpes

– Anti-viral team has 5 statistical reviewers– The team deal with about 160 protocol reviews and

20 new drug applications each year

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Approval “Requirements”Approval “Requirements”Approval “Requirements”Approval “Requirements”

• Evidence equivalent to two clinical trials each meet a significance level of 0.05

• Controlling Type I error is the first order of business

• Actual approval will be based on both efficacy and safety

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RandomizationRandomizationRandomizationRandomization

• Central randomization vs. restricted by sites– Less predictable but may be less efficient

• Block– Balance in small center vs. predictability

• Dynamic allocation– Does forced balance on margins really

beneficial?

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BiasesBiasesBiasesBiases

• Open-label biases– The knowledge of treatment will impact patient

behavior, physician’s judgment, and outcome assessment

• Trials design to show similarity of drugs can be manipulated– Poor conduct, poor data collection, poor

assessment, and random manipulation can drive the results in favor of drug sponsor

• Interim looks or adaptation can introduce biases– May affect future enrollment of patients– May affect the existing patients’ decision of

continuing or terminating current trial

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Interim Analysis and Adaptive Interim Analysis and Adaptive DesignsDesigns

Interim Analysis and Adaptive Interim Analysis and Adaptive DesignsDesigns

• Interim analysis: Multiple looks of the data before the trial is over.

• Adaptive Design: Alter the trial design in the process based on accumulated information. For example, dropping one arm, increase sample size

• Both pose challenge in controlling type I error. They may also pose challenge for the effect size estimation.

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Statistical Issues with Statistical Issues with EndpointEndpoint

Statistical Issues with Statistical Issues with EndpointEndpoint

• Surrogate endpoint: searching and validation

• Robustness of endpoint vs. Sensitivity

• Composite endpoints

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Multiple ComparisonsMultiple ComparisonsMultiple ComparisonsMultiple Comparisons

• Multiple Endpoints

• Subgroup analysis

• Multiple analysis

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Missing Data and Missing Data and DiscontinuationsDiscontinuationsMissing Data and Missing Data and DiscontinuationsDiscontinuations

• Almost always informative– MCAR or even MAR not hold

• Missing can be imputed– Robustness to credible imputations

• Discontinuations are outcomes, not missing data– need to be interpreted– Efficacy had they continued does not

answer regulatory question

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Example 1: Multiple Example 1: Multiple comparison adjustmentcomparison adjustment

Example 1: Multiple Example 1: Multiple comparison adjustmentcomparison adjustment

• A clinical trial containing three arms, new Drug X at a low dose, new Drug X at a higher dose, and placebo. The objective of the trial is to gain evidence for the approval of drug X. Do we need to adjust for multiple comparisons?

• The sponsor proposes to test the high dose vs. placebo first. – If p-value<0.05 then compare low dose vs.

placebo at significance level 0.05.– If p-value>0.05, stop.

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Example 2: Multiple Example 2: Multiple comparison adjustmentcomparison adjustment

Example 2: Multiple Example 2: Multiple comparison adjustmentcomparison adjustment

• A clinical trial containing three arms, new Drug X, new Drug Y, and placebo. The objective of the trial is to gain evidence for the approval of drug X and Y. Do we need to adjust for multiple comparisons?

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Example: Method for Example: Method for StratificationStratification

Example: Method for Example: Method for StratificationStratification

• A clinical trial containing two arms, new Drug X and placebo. The randomization are being stratified by clinical sites. The clinical sites ranges from very small to very large. The sponsor proposes to estimate and test the mean differences using the following statistic (minimum variance estimator):

1

1/ var( )

K

i iiC

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Combination TherapyCombination TherapyCombination TherapyCombination Therapy

• A Full factorial design: P AB A+B

• To approve A, A>P• To approve B, B>P• To approve A+B, A+B>A & A+B>B

• Any multiple comparison issue?

2. COMPUTER INTENSIVE AND 2. COMPUTER INTENSIVE AND RE-RANDOMIZATION TESTS RE-RANDOMIZATION TESTS

IN CLINICAL TRIALSIN CLINICAL TRIALS

Joint with Thomas Hammerstrom, Ph.D.Joint with Thomas Hammerstrom, Ph.D.

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OBJECTIVE OF TALKOBJECTIVE OF TALKOBJECTIVE OF TALKOBJECTIVE OF TALKDiscuss role of randomization and deliberate

balancing in experimental design.

Compare standard and computer intensive tests to examine robustness of level and power of common tests with deliberately balanced assignments when assumed distribution of responses is not correct.

Discuss role of randomization and deliberate balancing in experimental design.

Compare standard and computer intensive tests to examine robustness of level and power of common tests with deliberately balanced assignments when assumed distribution of responses is not correct.

OUTLINE OF TALKOUTLINE OF TALK

1. Testing with Deliberately Balanced Assignment

2. Common Mistakes in Views on Randomization and Balance

3. Robustness Studies on Inference in Deliberately Balanced Designs

1. TESTING WITH DYNAMIC 1. TESTING WITH DYNAMIC ALLOCATIONALLOCATION

DYNAMIC ASSIGNMENTSDYNAMIC ASSIGNMENTS

1. Identify several relevant, discrete covariates, e.g., age, sex, CD4 count

2. Change randomization probabilities at each assignment to get each level of each covariate split nearly 50-50 between arms

DYNAMIC ASSIGNMENTSDYNAMIC ASSIGNMENTS

1. 2. 3. Change randomization probabilities at

each assignment to get each level of each covariate split nearly 50-50 between arms. Assign new subject randomly if all covariates are balanced assign deterministically or with unequal probabilities to move toward marginal balance if not currently balanced

ISSUES WITH DYNAMIC ISSUES WITH DYNAMIC ASSIGNMENTSASSIGNMENTS

1. Why bother with this elaborate procedure?

2. Are the levels of tests for treatment effect preserved when standard tests are used with dynamic (minimization) assignments?

3. Does the use of minimization increase power in the presence of both treatment and covariate effects?

II. COMMON MISTAKES IN II. COMMON MISTAKES IN ANALYSIS OF BASELINE ANALYSIS OF BASELINE

COVARIATESCOVARIATES

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Mistake 1. Purpose of Randomization is to Create Balance in Baseline Covariates

Fact: Purpose of Randomization is to Guarantee Distributional Assumptions of Test Statistics and Estimators

Mistake 1. Purpose of Randomization is to Create Balance in Baseline Covariates

Fact: Purpose of Randomization is to Guarantee Distributional Assumptions of Test Statistics and Estimators

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Mistake 2. It is good practice in a

randomized trial to test for equality between arms of a baseline covariate.

Fact: All observed differences between arms in baseline covariates are known with certainty to be due to chance. There is no alternative hypothesis whose truth can be supported by such a test.

Mistake 2. It is good practice in a randomized trial to test for equality between arms of a baseline covariate.

Fact: All observed differences between arms in baseline covariates are known with certainty to be due to chance. There is no alternative hypothesis whose truth can be supported by such a test.

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Mistake 3. If a test for equality between

arms of a baseline covariate is significant, then one should worry.

Fact: Such test statistics are not even good descriptive statistics since p-values depend on sample size, not just the magnitude of the difference.

Mistake 3. If a test for equality between arms of a baseline covariate is significant, then one should worry.

Fact: Such test statistics are not even good descriptive statistics since p-values depend on sample size, not just the magnitude of the difference.

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Mistake 4. Observed Imbalances in Baseline Covariates cast Doubt on the Reality of Statistically Significant Findings in the Primary Analysis.

Fact: The standard error of the primary statistic is large enough to insure that such imbalances create significant treatment effects no more frequently than the nominal level of the test.

Mistake 4. Observed Imbalances in Baseline Covariates cast Doubt on the Reality of Statistically Significant Findings in the Primary Analysis.

Fact: The standard error of the primary statistic is large enough to insure that such imbalances create significant treatment effects no more frequently than the nominal level of the test.

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Mistake 5. Type I Errors can be Reduced by Replacing the Primary Analysis with one Based on Stratifying on Baseline Covariates Observed Post Facto to be Unbalanced.

Fact: The Operating Characteristics of Procedures Selected on the Basis of Observation of the Data are not generally Quantifiable.

Mistake 5. Type I Errors can be Reduced by Replacing the Primary Analysis with one Based on Stratifying on Baseline Covariates Observed Post Facto to be Unbalanced.

Fact: The Operating Characteristics of Procedures Selected on the Basis of Observation of the Data are not generally Quantifiable.

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If the Agency approved of Post Hoc Fixing of Type I Errors by Adding New Covariates to the Analysis (or by other Adjustments to ‘Fix Randomization Failures’),

Then it should also Approve of Similar Post Hoc Fixing of Type II Errors when ‘Failure of Randomization’ Leads to Imbalance in Favor of the Control Arm.

If the Agency approved of Post Hoc Fixing of Type I Errors by Adding New Covariates to the Analysis (or by other Adjustments to ‘Fix Randomization Failures’),

Then it should also Approve of Similar Post Hoc Fixing of Type II Errors when ‘Failure of Randomization’ Leads to Imbalance in Favor of the Control Arm.

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Mistake 6. If the same Random Assignment Method gave more even Balance in Trial A than in Trial B, then one should place more trust in a Rejection of the Null Hypothesis from Trial A.

Fact: Balance on Baseline Covariates Decreases the Variance of Test Statistics and Estimators. It Increases the Power of Tests when the Alternative Hypothesis is True. It has no Effect on Type I Error.

Mistake 6. If the same Random Assignment Method gave more even Balance in Trial A than in Trial B, then one should place more trust in a Rejection of the Null Hypothesis from Trial A.

Fact: Balance on Baseline Covariates Decreases the Variance of Test Statistics and Estimators. It Increases the Power of Tests when the Alternative Hypothesis is True. It has no Effect on Type I Error.

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Mistake 7. Balance on Baseline Covariates Leads to Important Reductions in Variances.

Fact: Even without Balance, the Variance of Tests and Estimators are of size O(1/N) where N = sample size.

Balancing on p Baseline Covariates Decreases these variances by Subtracting a Term of size O(p/N2)

Mistake 7. Balance on Baseline Covariates Leads to Important Reductions in Variances.

Fact: Even without Balance, the Variance of Tests and Estimators are of size O(1/N) where N = sample size.

Balancing on p Baseline Covariates Decreases these variances by Subtracting a Term of size O(p/N2)

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Typical model for Continuous Response:

Yik = mi + g1x1ik + … + gpxp

ik + eik

where eik ~ N(0, s2)

mi = treatment effect,

Xik = (x1ik,…,xp

ik) = vector of covariatesg1 ,…, gp = unknown vector of covariate effects

Typical model for Continuous Response:

Yik = mi + g1x1ik + … + gpxp

ik + eik

where eik ~ N(0, s2)

mi = treatment effect,

Xik = (x1ik,…,xp

ik) = vector of covariatesg1 ,…, gp = unknown vector of covariate effects

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s2 * Precision of Estimate of (m1-m0 ) =

N/2 - Z’Z where N = number per arm,

Z = V-1(X1. - X0.),

V2 = matrix of cross-products of X/2N, and randomization distribution of

(X1. - X0.) ~ N( 0, V2), of Z ~ N(0, Ip),

of Z’Z ~ Chi-square(p)Precision with Balance = N/2,E(Precision without Balance) = N/2 - O(p)

s2 * Precision of Estimate of (m1-m0 ) =

N/2 - Z’Z where N = number per arm,

Z = V-1(X1. - X0.),

V2 = matrix of cross-products of X/2N, and randomization distribution of

(X1. - X0.) ~ N( 0, V2), of Z ~ N(0, Ip),

of Z’Z ~ Chi-square(p)Precision with Balance = N/2,E(Precision without Balance) = N/2 - O(p)

III. ROBUSTNESS STUDIES III. ROBUSTNESS STUDIES ON INFERENCE IN ON INFERENCE IN

DELIBERATELY BALANCED DELIBERATELY BALANCED DESIGNSDESIGNS

A. MODELS USED TO COMPARE METHODS

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METHODS COMPAREDMETHODS COMPAREDMETHODS COMPAREDMETHODS COMPARED

1. Dynamic Allocation analyzed by F-statistic from ANCOVA based on arm and covariates

2. Dynamic Allocation analyzed by re-randomization test, using difference in means

3. Randomized Pairs, analyzed by F-statistic from ANCOVA using arm and covariates

1. Dynamic Allocation analyzed by F-statistic from ANCOVA based on arm and covariates

2. Dynamic Allocation analyzed by re-randomization test, using difference in means

3. Randomized Pairs, analyzed by F-statistic from ANCOVA using arm and covariates

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BASIC FORM OF SIMULATED BASIC FORM OF SIMULATED DATADATA

BASIC FORM OF SIMULATED BASIC FORM OF SIMULATED DATADATA

1. Control & test arms, N subjects randomized 1:1

2. X1j, …, X7j = binary covariates for subject j

3. ej = unobserved error for subject j

4. Yj = observed response for subject j

5. I1j = 1 if subject j in arm 1, test arm

6. Yj = mj I1j + ej + d k=17Xkj

1. Control & test arms, N subjects randomized 1:1

2. X1j, …, X7j = binary covariates for subject j

3. ej = unobserved error for subject j

4. Yj = observed response for subject j

5. I1j = 1 if subject j in arm 1, test arm

6. Yj = mj I1j + ej + d k=17Xkj

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MODELS FOR ERRORSMODELS FOR ERRORSMODELS FOR ERRORSMODELS FOR ERRORS1. ej ~ N( 0 , 1 ) Normal

2. ej ~ exp( N( 0 , 1 )) Lognormal

3. ej ~ N( 4j/N , 1 ) Trend

4. ej ~ .9 N( 0 , 1) + .1 N( 0, 25 ) Mixed

5. ej ~ N( 0 , 4j/N ) Hetero

6. ej ~ N( cos(2j/N) , 1 ) Sine wave

7. ej ~ N( 0 , 1 ) if j<J

~ N(4, 1) if j>=J Step

1. ej ~ N( 0 , 1 ) Normal

2. ej ~ exp( N( 0 , 1 )) Lognormal

3. ej ~ N( 4j/N , 1 ) Trend

4. ej ~ .9 N( 0 , 1) + .1 N( 0, 25 ) Mixed

5. ej ~ N( 0 , 4j/N ) Hetero

6. ej ~ N( cos(2j/N) , 1 ) Sine wave

7. ej ~ N( 0 , 1 ) if j<J

~ N(4, 1) if j>=J Step

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MODELS FOR COVARIATESMODELS FOR COVARIATESMODELS FOR COVARIATESMODELS FOR COVARIATESX1j, …, X7j are

1. independent with p1, …, p7 constant in j

2. correlated with p1, …, p7 constant

3. independent with p1, …, p7 monotone in j

4. independent with p1, …, p7 sinusoid in j

Coefficient d = 1 or 0

X1j, …, X7j are

1. independent with p1, …, p7 constant in j

2. correlated with p1, …, p7 constant

3. independent with p1, …, p7 monotone in j

4. independent with p1, …, p7 sinusoid in j

Coefficient d = 1 or 0

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MODELS FOR TREATMENTMODELS FOR TREATMENTMODELS FOR TREATMENTMODELS FOR TREATMENT

1. Treatment effect mj = m, constant over j

2. Treatment effect mj = m * (4j/N), increasing over j

1. Treatment effect mj = m, constant over j

2. Treatment effect mj = m * (4j/N), increasing over j

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COMPARISONSCOMPARISONSCOMPARISONSCOMPARISONS

1. Select one of the models2. Generate 200 sets of covariates and

unobserved errors3. For each set, construct I1j once by

dynamic & once by randomized pairs4. Compute the 200 p-values for

different tests and assignment methods

1. Select one of the models2. Generate 200 sets of covariates and

unobserved errors3. For each set, construct I1j once by

dynamic & once by randomized pairs4. Compute the 200 p-values for

different tests and assignment methods

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SIMULATED DATA FOR COX SIMULATED DATA FOR COX REGRESSIONREGRESSION

SIMULATED DATA FOR COX SIMULATED DATA FOR COX REGRESSIONREGRESSION

1. Control & test arms, N subjects randomized 1:1

2. X1j, …, X7j = binary covariates for subject j

3. YLj = observed response for subject j on arm L = 0 or 1

4. YLi /[ dL( 1+ k=17Xkj )] ~ FL, L = 0 or 1

5. FL = Exponential or Weibull

6. Censoring ~ Exp with scale large or small

1. Control & test arms, N subjects randomized 1:1

2. X1j, …, X7j = binary covariates for subject j

3. YLj = observed response for subject j on arm L = 0 or 1

4. YLi /[ dL( 1+ k=17Xkj )] ~ FL, L = 0 or 1

5. FL = Exponential or Weibull

6. Censoring ~ Exp with scale large or small

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RESULTS WITH COX RESULTS WITH COX REGRESSIONREGRESSION

RESULTS WITH COX RESULTS WITH COX REGRESSIONREGRESSION

1. Assign subjects by dynamic allocation.2. Estimate treatment effect by proportional

hazards regression3. Re-randomize and compute new ph reg

estimates many times.4. Compare parametric p-value with

percentile of real estimate among all rerandomized treatment estimates

1. Assign subjects by dynamic allocation.2. Estimate treatment effect by proportional

hazards regression3. Re-randomize and compute new ph reg

estimates many times.4. Compare parametric p-value with

percentile of real estimate among all rerandomized treatment estimates

III. ROBUSTNESS STUDIES III. ROBUSTNESS STUDIES ON INFERENCE IN ON INFERENCE IN

DELIBERATELY BALANCED DELIBERATELY BALANCED DESIGNSDESIGNS

B. RESULTS OF SIMULATIONS

SIMULATION RESULTS SIMULATION RESULTS

1. In most cases considered, the gold standard but computer intensive re-randomization test gave the same power curve as the standard ANCOVA F-test for the dynamic allocation. Both level, when H0 was true, and power, otherwise, were the same.

SIMULATION RESULTS SIMULATION RESULTS

2. In most cases considered, the ANCOVA F-test gave the same power curve whether the subjects were assigned by dynamic allocation or randomized pairs. Deliberate balance on baseline covariates gave no improvement in power.

SIMULATION RESULTS SIMULATION RESULTS

3. There was one clear exception to the above findings. When covariates showed a trend with time of enrollment, the ANCOVA F-test for treatment gave incorrectly low power.

SIMULATION RESULTS SIMULATION RESULTS

4. In most cases considered with time to event data with dynamic allocation, the re-randomization test gave the same results as the Cox regression.

SUMMARYSUMMARY1. Modifying a Randomization Method to Achieve

Deliberate Balance Serves Mainly Cosmetic Purposes & Should be Discouraged

2. Balance on Covariates Reduces Variance of Test Stats & Estimators but Only by Small Amounts

Var( trt effect) = O(1/N) when balancedWhen unbalanced , Var is larger by a term =

O(p/N2)

SUMMARYSUMMARY3. Rerandomization analyses based on

Finite Population Models are gold standard for randomized trials

4. IID Error models are only approximations5. Approximation is adequate for level with

common minimization allocations under a wide variety of potential violations of the assumptions.

SUMMARYSUMMARY

6. Deliberate Balance Allocations and Simple Tests Require Belief that God is Randomizing Your Subjects’ Responses.

Randomization and Finite Population Based Tests Protect You if the Devil is Determining the Order of Your Subjects’ Responses