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1 On multiplicity problems related to multiple endpoints of controlled clinical trials Mohammad F. Huque, Ph.D. Div of Biometrics IV, Office of Biostatistics OTS, CDER/FDA JSM, Vancouver, August 2010 Disclaimer This presentation expresses my personal views on this topic and must not be interpreted as the regulatory views or the policy of the FDA 2
2 Clinical trials poses diverse multiplicity problems For example: investigate treatment effects for more than one endpoint measured at different time points evaluate treatments at several dose levels compare treatment to control for non-inferiority and superiority on multiple endpoints and doses. perform subgroup analysis carry out analysis by baseline and demographic factors assess regional differences select models conduct interim analysis make design modifications, etc. These and other multiple testing activities pose multiplicity problems of different complexity 3 Evolution of creative statistical methods Clinical trial multiple testing problems can be framed into testing of hierarchical families of hypotheses (F 1 F 2 F n ) A number of new methods and concepts since the two articles: 1. Westfall and Krishen (JSPI, 2001): Optimally weighted, fixed sequnence, and gatekeeping multiple testing procedures 2. Dmitrienko, Offen and Westfall (Stat in Med, 2003): Gatekeeping strategies that do not require all primary effects to be significant 4
3 Last 3 years new useful statistical methods on Recycling of alpha from one family to the next (on using Bonferroni and truncated Holm s method) Graphical approaches Hybrid methods (e.g., combining the Bonferroni and Holm s critical values) and the concept of separability Computation of adjusted p-values for any complex hierarchical testing method, e.g., gatekeeping testing schemes Lower limit for 1-sided confidence intervals for step-up and stepdown procedures Adaptive alpha allocation approach (the 4A method) Partitioning principle based testing strategies Methods for subgroup analysis Consistency ensured (adaptive) methods Others (e.g., related to interim analyses and adaptive designs) 5 Some key statistical principles/ concepts underlying new methods Union-Intersection (UI) and Intersection-Union (IU) testing principles Closed testing principle Partitioning principle Gatekeeping principles Graphical concept of transporting alpha from one hypothesis to others (has led to improvements in the fallback methods) Separability concept for recycling of unused alpha from one family to the next Adaptive alpha allocation concept 6
4 Rest of the presentation on: multiple endpoints of confirmatory trials Outline Distinction between primary and secondary endpoints Concept of clinical win for efficacy When is it necessary to adjust for multiplicity and when is it not? Types of FWER control for treatment benefit claims Methods for primary endpoints The issue of Type I error adjustments for secondary endpoints Co-primary and composite endpoints issues Concluding remarks 7 Distinction between primary and secondary endpoints Primary endpoints: These are critical endpoints such that unless there is clinically meaningful and statistically significant evidence of efficacy in one or more of these endpoints for the study treatment, there is no justification for a claim. These endpoints can either form a single family or multiple hierarchical families depending for example on their relative importance and power considerations, and the win criteria 8
5 Distinction between primary and secondary endpoints (cont d) Primary endpoints: A primary endpoint is a primary endpoint, it can not be called a secondary or key secondary E.g., If mortality is a primary endpoint for an oncology indication, It can not be a key secondary or secondary because of power considerations. In this case, it can take the position of the second primary endpoint in the hierarchy, the first primary endpoint will then be the one that will have greater likelihood of success No efficacy claim: if no statistically significant and clinically meaningful evidence of treatment benefit on one or more primary endpoints 9 Secondary endpoints Not sufficient to support efficacy in the absence of an effect on one or more primary endpoints. However, the secondary endpoints can provide additional claims and other important clinical information 10
6 Efficacy win criteria Simply triaging endpoints to primary and secondary is not sufficient. The trial should specify a win scenario for the set of primary endpoints that determines whether or not the trial has met its efficacy objectives. Examples of efficacy win criteria: 1) All specified primary endpoints needs to show clinically meaningful and statistically significant treatment efficacy 2) At least one of the specified primary endpoints need to show clinically meaningful and statistically significant treatments efficacy 3) A pre-specified subset of primary endpoints need to show clinically meaningful and statistically significant treatment efficacy. (More examples in Chapter 1 of the book: Multiple testing problems in pharmaceutical statistics; Edts., Dmitrienko, Tamhane and Bretz, 2010, CRC Press), 11 When multiplicity adjustments are not necessary 1. When the trial specifies a single primary or single composite endpoint for a claim of treatment efficacy 2. All specified primary endpoints need to show clinically relevant treatment benefits. o No type I error rate inflation concern, but concern about the type II error rate. 3. Primary endpoints are hierarchically ordered and are tested in a fixed-sequence. o If the earlier endpoints in the sequence are under powered, the procedure is likely to stop early and miss the opportunity to evaluate treatment effects for latter potentially useful endpoints. 12
7 Multiple analyses for the ITT data set (for the same endpoint and the method) Irregularities are common in the intention-to-treat (ITT) data set because of: Some patients may drop early Some may fail protocol criteria Some may not take medications as prescribed Some may take concomitant medications Usual Dilemma: How to deal with these irregularities? As the true endpoint measurements for these cases are unknown, there is a usual concern about bias in the result. Therefore, multiple analyses are done for same endpoint on varying the assumptions about these unknown measurements As the purpose of these analyses is to investigate the extent of bias, there is no multiplicity adjustment. 13 Analyses of the same endpoint data by alternative methods Analysis of the same endpoint by alternative methods, in addition to the analysis by the pre-specified method, e.g., analysis of the same time-to-event endpoint by log-rank test and by the generalized Wilcoxon test analysis of variance on excluding/including certain design factors. analysis by the parametric and non-parametric methods Technically, one can adjust for these multiple analyses if they were pre-specified. However, this is rarely done, as the purpose of these analyses is usually to demonstrate that the results found are robust and hold regardless of different methods applied 14
8 Other situations Correction for bias: imbalance in certain key risk factors (pre-specification needed) Performing a less conservative after a conservative analysis (e.g., ITT analysis ) is significant: for better estimate of the size of the treatment effect and the statistical strength Descriptive analyses: E.g., for interpreting the result of an analysis of a primary or a secondary endpoint. E.g., After the result for a continuous endpoint is significant showing the results by response categories E.g., Forest plot for a visual demonstration of consistency of results by baseline risk factor or by center and region (caution: some results may go in wrong direction by chance) 15 When is it necessary to adjust for multiplicity? When the type I error rate inflates as a result of multiple ways to achieve a successful outcome Example: CHF trial with 2 PEs (death, hospitalizations) Success criterion: superiority of the treatment to control for at least one of the two endpoints; Each endpoint tested at the 0.05 level FWER can be as high as ; an unaccepted trial alpha level for making regulatory decisions. 16
9 The issue of FWER control for the primary and secondary endpoint families Should there be separate FWER control for the primary endpoint families and separate FWER control for the secondary endpoint families? E.g., Allocate alpha = 0.05 for the primary endpoint families Allocate separate alpha = 0.05 for the secondary endpoint families. But test secondary endpoints only after statistically significant and clinically meaningful evidence of treatment benefit by one or more primary endpoints 17 Benefits? Reduction in type II error for secondary endpoint analyses after the drug can be approved based on the results of one or more primary endpoints No influence of the secondary endpoints on the results of the primary endpoints 18
10 FWER control concepts: weak or strong? Concepts easy for statisticians with some training in multiplicity Difficult for statisticians without training in multiplicity Concepts very difficult for clinicians 19 Weak and strong FWER control approaches differ in critical respects Strong FWER control: Assure that conclusion of success on an endpoint can be interpreted as a conclusion that alpha for that endpoint is < 0.05, regardless of the size of the treatment effects in other endpoints. Statistically: the probability of at least one type I error < 0.05 across null hypotheses configurations (complete and partial ones) Weak FWER control: Control of alpha at level 0.05 for the conclusion that some endpoints (either individually or collectively) have treatment effects. Null hypothesis: no effect in any endpoint No intention to identify or to claim as to which endpoints have treatments or which win scenario makes it. 20
11 Regulatory applications Require strong FWER control for the primary as well as secondary families Except perhaps in rare situations for serious diseases, when weak FWER control may be OK E.g., treatment of stroke trials; Tilley et al., 1996) 21 Which analysis methods for primary endpoint families? Methods should be valid for independent as well as for correlated endpoints and for any joint distribution of test statistics or p-values Examples: Bonferroni Holm s PAAS (for positively correlated endpoints) Sequential testing method Bonferroni based gatekeeping procedures (Dmitrienko et al. and others) (Sequentially rejective) graphical approach (Bretz et al., 2009) Other methods (e.g., truncated Holm s, fallback, etc.) Note: Hochberg procedure generally not recommended: Known to fail FWER control in the strong sense for some correlation structures 22
12 About the Bonferroni method Not all that conservative When the number of endpoints m = 2 to 5, and correlation = 0.3 or less Alpha adjustments (i.e., 0.05/m) may seem much but the type II error can be small if success criterion is to win in at least one of the m endpoints. Example (2-arm trial, 2 endpoints): Consider a single endpoint trial: alpha = 0.025, test = 1-sided Z-test, power = 90%, and delta (per unit s.d.) = 0.5, then n = 84 per treatment arm. Consider a 2-enpoint trial, each endpoint test at level alpha = 0.025/2 = , delta1 = delta 2 =0.5, r = 0.6, assume n = 84 per treatment arm, then Power (win in at least one of the two endpoints) = 92.7% 23 Benefits of the Bonferroni or Bonferronibased methods Simple to explain to non-statisticians A finding that survives a Bonferroni adjustment is generally considered a credible trial outcome Complex gatekeeping methods simplifies to simple useful shortcut methods. Its critical values can combine with the critical values of alpha-exhaustive methods (e.g., Holm s) leading to (truncated) tests with more power and flexibility to test subsequent families Confidence intervals computation easy. (Very much needed for benefit-risk assessments) Etc. 24
13 Use of resampling methods for endpoints with high correlations (e.g. 0.60) A popular a resampling based step-down procedure: Step 1: Rejects H (1) associated with p (1) if Pr{ min(p 1, P 2,, P m ) p (1) } α Step j = 2,, m: Rejects H (j) associated with p (i) if Pr{ min(p j, P j+1,, P m ) p (j) } α Step m: Rejects H (m) associated with p (m) if Pr{ P m p (m) } α Stop further testing when 1 st time condition not met Probabilities calculated from the resampling distributions of the minimum P-value test statistics 25 Concerns regarding resampling methods Results approximate, requiring large sample sizes and usually simulations are required to validate the results Computation can be difficult (e.g., for time-to-event endpoints) Strong control of the overall type I error rate is achieved under the assumption of subset pivotality condition - hard to justify for some cases Ref: Westfall and Troendle (2008; multiple testing with minimal assumptions); Huang et al. (2006; Bioinformatics; permute or not to permute) 26
14 Co-primary endpoints No reverse multiplicity issue; test each endpoint at 0.05 level to control FWER at the 0.05 level Inflation of the type II error recognized. Limit the number of co-primary endpoints to 2 for the claimed indication (if clinically acceptable) 27 Co-primary endpoints (cont d) More than two co-primary endpoints: When clinically necessary to do so Expected effect sizes are such that trial sample sizes are practical. Cases of strong treatment effects in some (e.g., p-value < 0.01), but weak in some (i.e., p-values slightly > 0.05): OK on case-by-case basis if replicated evidence or presence of other clinical evidence. 28
15 Composite event endpoint as a primary endpoint (Several motivations; Moye, 2003) Reduces multiple endpoints to a single PE (if clinically meaningful to do so) Can reduce the size of the trial if certain conditions met Components increase the number of events in non-overlapping manner (i.e., an event is not a direct consequence of the other) Some homogeneity of treatment effects across components, or components jointly enhance the overall treatment effect Can addresses a broader aspects of a multifaceted disease Can change the focus of the trial in discovering clinically meaningful small treatment effects that collectively demonstrate a statistically significant benefit of the treatment 29 Interpretation of the composite PE result? Example 1: 2-arm trial: treatment A versus control, composite PE = (death, MI and revascularization) Results: Composite: in favor of treatment A (2p=0.008). OR = 0.67 death: in favor of control (2p=0.07) OR = 1.8 MI: no difference (2p=0.9) OR = 0.98 revascularization: in favor of treatment A (2p=0.0001). OR = 0.34 Comment: The composite PE result provides an inflated (and misleading in this case) notion of benefit of treatment A. Clinically relevant component is going in the wrong direction. 30
16 Some ideas (previous example) 1. Do the heterogeneity analysis and reject the composite analysis: No evidence of favorable treatment effect in clinically important components (either individually or jointly) which are like primary endpoints, and Result of the composite driven by soft endpoints which are like secondary endpoints clinically not relevant unless some movement in the direction of benefit for clinically important components E.g., analyze the sub-composite of clinically important components which are like primary endpoints 31 More ideas (composite endpoints) 2. The conventional composite analysis assumes equal weight for the components. Assign clinical utility weights, e.g., death weighted as 0.7, MI as 0.2 and revascularization as 0.1: Issue: How will this impact the power of the study when down weighting the most frequent component? 3. All components clinically important but some occur less frequently: Analyze components and accept p<0.05 for the most frequent component and set a margin for acceptable inferiority for the most relevant (least prevalent) component e.g., upper CI for mortality odds ratio not to exceed
17 Example 2: PROactive trial in type II diabetes (Lancet 2005) Composite (endpoint A)= (all-cause mortality, non-fatal MI, stroke, acute coronary syndrome, endovascular or surgical intervention in the coronary or leg arteries, and amputation above the ankle) Endpoint B = (all-cause mortality, non-fatal MI and stroke). Results: P A = and P B = Statistical methods: Fixed sequence method (problematic), No test for B Fallback method (α = 0.05, α A = 0.04, α B = 0.01), Not Significant 4A method (α = 0.05, α A = 0.04, α B = 0.032), Significant Consistency-ensured method (1-sided test): (α = 0.025, α A = 0.02, α B = ), α* = 0.10), Significant 33 Concluding Remarks 1. PEs vs. SEs differ in concept and purpose Efficacy of a treatment is derived on demonstrating clinically meaningful and statistically results in one or more primary endpoints that satisfies a pre-defined clinical win scenario. Secondary endpoints are not suitable for this special purpose. 2. Multiplicity in efficacy analyses kicks in when multiple ways to win for efficacy Causes inflation of the type I error rate requiring statistical adjustments for its control Many useful statistical approaches to handle this 3. Clinical trials also pose multiple testing situations when multiplicity adjustment in not necessary 34
18 Concluding Remarks 4. Multiplicity adjustment approaches: Necessary to use methods that control FWER control in strong sense for making endpoint specific claims of treatment benefits. The strategy of separate FWER control for the family of secondary endpoints may be reasonable, after clinically meaningful and statistically significant treatment efficacy already concluded based on primary endpoint. For primary endpoint families: use methods that are valid for independent as well as for correlated endpoints and for any joint distribution of test statistics Resampling based methods may not be used for primary endpoints reasons addressed Bonferroni or Bonferroni-based gatekeeping methods have advantages 35 Concluding Remarks 5. Co-primary endpoints issues: No reverse multiplicity adjustment. Control of alpha necessary at 0.05 level. Some flexibility on the case-by-case basis when number of co-primary endpoints greater than 2 with some additional sources of evidence 6. Composite endpoint issues Widespread interest, particularly, for cardiovascular trials Interpretation difficulties when: components of widely different importance; low frequency for important and high frequency for less important components; marked heterogeneity of treatment effects across components Some statistical approaches but more research needed 36
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