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Thirteen Clinical Trial Design Questions and Answers

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1 Thirteen Clinical Trial Design Questions and Answers
Peter A. Lachenbruch DB Cynthia Rask DCEPT

2 Usual Disclaimer The views expressed here are those of the authors and may not reflect those of the FDA We have been asked to address 13 questions (unlucky?)

3 Orientation The NIAID requested that we discuss some questions regarding clinical trial design principles. There are many books on the basics of clinical trial design and analysis Pocock Freedman Furberg and DeMets Piantadosi

4 Orientation (2) FDA has many guidance documents on their web site Consult these for further details. The International Conference on Harmonization (ICH) has issued many reports that worldwide regulatory agencies will abide by. Web site: See E9, E10, E3, E6, and E5 for particularly useful documents

5 General Statistical Ideas
Clarity of approach Full disclosure of design, sample size calculations Analysis methods Distinction between CONFIRMATORY and Exploratory analyses If “new” methods are used, there should be peer-reviewed citation

6 Statistical Ideas (2) Must be analytically appropriate
Maintain size (α level) Maintain blinding as appropriate Have endpoints (outcomes) that are appropriate Show a clinical benefit Reliable and valid Minimize missing data and provide plan for dealing with them when they occur

7 Question 1 What pitfalls do the FDA see when information from pre-clinical data (or early clinical data on a similar investigational product) is formulated into a Phase I protocol?

8 Q1: (1) Safety issues A main use of pre-clinical data is to ascertain basic safety information. If animal data is limited, the FDA may ask for further study The choice of animal model is important – if it is not accepted as appropriate, there may be need to obtain further information or information on another model

9 Q1: (2) Need to characterize the product Potency assays Purity
Identity All specifications need to have at least a start at understanding leading to full GMP compliance

10 Q1: (3) It is recognized that proof of concept studies in pre-clinical studies may be limited. However, there should not be evidence of poorer outcomes than comparators.

11 Q2: What are the various types of study designs available when there are more than two comparators?

12 Q2: Depends on purpose of study
Testing 2 or more dosage levels versus control Parallel group design – may wish to account for ordering of dosages in the analysis Testing both schedule and dose Factorial design (high and low levels of each dose crossed) – allows examination of interactions in the analysis

13 Q2: (2) Test amount of adjuvant and dose
Factorial design Crossover designs are generally not used in vaccine trials because the immune system is permanently affected (or at least affected for a long time). Thus, carry over effects are always present

14 Q3: What controls are appropriate when there cannot be any blinding in the trial?

15 Q3: Almost any control is reasonable: placebo, standard of care
In some cases, historical controls may be used, but these are rare The endpoint / outcome variable that is being used and how it’s evaluated is most important A subjective endpoint is usually a problem, so we expect that a blinded evaluator will be used. An objective endpoint (e.g., confirmed disease by laboratory measures) is preferable

16 Q4: What are the problems seen by the FDA with randomization in trials?

17 Q4: Randomization is absolutely essential in vaccine trials Issues
Too many strata make is unlikely that there will be sufficient numbers in each stratum for precise estimation. The number of strata is the product of the number of levels in each stratum (Sex (2), Age (4), Ethnicity (3) = 24 strata)

18 Q4: (2) Issues (continued) Inadequate number of strata
age<2, 2 ≤ age <12, 12 ≤ age < 18, 18 ≤ age < 50, ≤ age often important in vaccine studies Cheating – unblinding the treatment assignment – need to have robust way of preventing this Introduction of bias Not accounting for the design of the study in the analysis – just because you have stratified, you still must account for the stratification in the analysis.

19 Q5: What are the steps in designing a dose-ranging/dose-escalation study?

20 Q5: Goals: To establish maximum tolerated dose (MTD), dose limiting toxicities, and/or maximum feasible dose To establish minimum effective dose Designs One dose per subject, gradual increase by fixed amount (typically half log increases, with rules for stopping) What’s the right starting dose?

21 Q5: (2) Dose ranging / dose escalation
Multiple doses per subject for short (3-7 days) or long (1-4 weeks or greater) periods What is range that generates useful levels of antibodies? What level has adverse events? Dose Escalation Give successively larger doses or number of doses (booster doses) until subject responds May not be helpful with vaccines because of permanent effect of a vaccine

22 Q5: (3) For a vaccine both dose and schedule need to be determined
A factorial design may be useful Test all doses and all schedules Can look for interactions to see if the response is additive or not The specific adjuvant may be important This may be expanded to look at a response surface Useful for first trials to pick a dose-schedule combination for later trials

23 Q6: How does one deal with multiple variables that will affect the outcome measure (with an understanding of fixed randomization schemes and adaptive/dynamic randomization schemes)

24 Q6: If there are strata, including study sites, these always should be included in the analysis model. Common covariates include (if not made strata) age, sex, ethnicity, disease stage Usual method is to conduct an analysis of covariance – some covariates may not be ordered, often they are

25 Q6: (2) The analysis of covariance does an analysis of variance on the adjusted response. Assumptions: Normal distribution of residual error Covariates not affected by treatment – measure at baseline! Parallelism – no interaction of treatment and slope – i.e. the response treatment rate of change is same for all covariate combinations Less commonly used in vaccine trials. May be used for immunogenicity studies. Worry about normality assumptions – may need to transform.

26 Q6a: Fixed and Adaptive Randomization Schemes
Fixed scheme Same proportion assigned to each treatment group Often 1:1 allocation, but may become 2:1 or 3:1 Smallest variance of treatment effect associated with 1:1 allocation, but it may be important to gain understanding of safety profile, so a more extreme allocation may be used. More extreme than 3:1 is not very useful and leads to much larger sample size

27 Q6a: (2) Here are total sample sizes for α=0.5, =0.1, mean difference=1, =3 1:1 allocation 380 2:1 allocation % increase 3:1 allocation % increase 5:1 allocation % increase Thus, the unbalanced allocation leads to a substantial increase in sample size and consequent budget

28 Q6a: (3) Adaptive randomization
Next randomization depends on outcome of prior subjects in the trial Need fairly early response in trial. May be possible with skin or other reactions (if they occur within a few hours of immunization), a bit less so with immunogenicity (outcome after first series of immunizations that may take 6 months), unlikely with clinical outcome (occurs after series of immunizations and a relatively long follow up period)

29 Q6a: (4) Another form of adaptive randomization attempts to balance covariates (e.g., minimization) This can be done with vaccine studies Needs to have a measure of imbalance Must adjust for covariates used in imbalance score Potential for manipulation? May be problems in appropriate analysis model – considerable disagreement

30 Q7: What factors are used to estimate sample size?

31 Q7: What factors are used to estimate sample size?
Most popular question to statisticians Factors (using a two group test as an example) Significance level (α, often 0.05) Type 2 error (, often 0.2 or 0.1; 1- is the power) Standard deviation of observation () Difference in means (1 - 2 ) Allocation ratio

32 Q7: (2) Significance level, type 2 error and allocation ratio are relatively easy to determine Mean difference and standard deviation are usually based on preliminary studies and may be quite uncertain. I find it useful to take these preliminary differences and halve them What is really needed is the ratio of treatment difference to the standard deviation Halve them because a) regression toward the mean, b) preliminary studies aren’t usually conducted as well as the phase 3 studies, c) too optimistic

33 Q7: (3) In vaccines we often want to estimate the vaccine efficacy and find a confidence interval with a lower bound that gives us assurance the vaccine is working well Where IV is the incidence rate for the vaccine group and IC is the incidence rate for the control group Lower bound must be substantially greater than 0

34 Q7: (4) It’s easy to find an expression for the confidence interval and then one sets the lower bound of the interval to the desired level (set in consultation with FDA) Often ¾ of the observed VE, and VE is set by needs of clinical prevention. For example if the target VE is 0.8 (or 80%) the lower bound would be 60% These are not absolute criteria! We never want to show a vaccine has better than 0 VE. That’s not enough

35 Q8: How does the investigator choose the margin of equivalence or non-inferiority (delta or ) in comparative clinical trials?

36 Q8: Demonstrate that active control has assay sensitivity – that is, it consistently shows itself better than placebo – need evidence of this. Is the control an appropriate one? Compare to best licensed product, not worst What is clinically important? Depends on context of disease Note I try to avoid the word “significant”

37 Q8: (2) When citing a % difference for VE (or anything) be sure to clarify whether you mean 10 percentage points or 10% of the comparator If comparator has a VE of 80%, do we want the estimated VE of the new vaccine to be 72% or 70% if we choose a 10% margin? Or do we want the relative VE (vaccine vs. control) to be at least 90% It’s easy to become confused so it’s good to be specific

38 Q9: How does the investigator deal with missing data?

39 Q9: Don’t have any Don’t have very much (under 5% is my initial break point) Discuss how you will deal with it prospectively!!! Complete cases analysis (ugh!) Last Observation Carried Forward (LOCF) Mean values for replacement Regression models for replacement Imputation models Will not discuss complete cases analysis further – only useful if fraction of missing is small

40 Q9: (2) Types of missing values
Patient misses visit, and an ‘interior’ value is missing Patient drops out, and a series of values at the end are missing (Some) Covariates are missing in one or more visits

41 Q9: (3) Last Observation Carried Forward
Is almost always a problem for me It ignores any trends in data It reduces variability arbitrarily Was suggested about 25 years ago and has been a pain in the neck ever since.

42 Q9: (4) Mean values imputation
Need to be sure you don’t increase the apparent sample size (i.e., replaced values don’t give a more precise estimate) This doesn’t account for patient specific characteristics This can be especially tricky if a long series of values is imputed Mean of patient values or mean of other patients at that visit?

43 Q9: (5) Regression models
Determine what variables are “good” predictors of the missing value – usually useful to have a small number of such variables so they won’t have a lot of missing value issues Predict missing value using a regression model (try to show that variance of predicted value isn’t too big)

44 Q9: (6) More sophisticated imputation models have been developed recently Determine classes of similar patients (“propensity scores”) Fill in missing values by selecting randomly from observations in the same class. Do this multiple times, (5 to 10 is usually enough) Analyze the data and pool results Multiple imputation – get within imputation and between imputation variation – can get fairly reliable results

45 Q10: How does an investigator determine what data should and should not be included in analyses (especially in the cases of protocol violations, withdrawals and drop-outs)?

46 Q10: The fundamental efficacy data set includes all subjects as randomized Note this does not say “ignore patients who didn’t get medication” – doing this messes up the randomization plan and allows data shaping This is called Intent to Treat (ITT) Modified ITT relaxes this to patients who have had at least one immunization (treatment)

47 Q10: (2) Per Protocol Data set
Subjects who had no protocol violations (completed study, etc) Can provide various analysis data sets that may be subsets – e.g. no protocol violations, no withdrawals or dropouts Important to examine comparability of groups and outcomes to ITT, mITT

48 Q10: (3) Data to be included will depend on the purposes of the analysis. All substantial differences from total population need to be explained E.g., Immunogenicity analysis had only 48% of the total sample because only 50% of subjects were solicited for bleeding FDA will expect to have access to all data and may audit some of it.

49 Q11: What types of analyses should be used when there are multiple time points (multiple observations) of data collection (there is no dichotomous outcome/endpoint)?

50 Q11: There has been an active area of statistical research on longitudinal data analysis in the past few years In vaccines research, the common issue is in immunogenicity levels over time. These are often in log(GMC) or log(titer). These look like multiple continuous measurements Can also have whether a four-fold increase in titer has been achieved at various times. This is a series of dichotomous variables (yes or no)

51 Q11: (2) Longitudinal analysis accounts for subject, treatment, other covariates and time in the analysis Measurements made at different times are correlated Must determine appropriate correlation structure Shape of response curve (linear over time? Curve? )

52 Q11: (3) Longitudinal analysis Alternatives – may be appropriate
GEE models provide great flexibility Dichotomous variables (e.g., seroconversion at different times) can be handled with GEE Alternatives – may be appropriate Change from baseline to final observation (usually need to have a common last time) - does this depend on baseline? Should we use last observation with baseline as covariate? Don’t use change with baseline as covariate – there’s a built in correlation. Bias is last value with base as covariate

53 Q12: In analyzing data from clinical trials involving multiple sites, should site be treated as a fixed or random effect?

54 Q12: The site should be included in the analysis model, especially if randomization is stratified. If it’s not stratified, you may not wish to include it if sites are generally small. With small sites, the d.f. that are used up reduces the precision of the comparison

55 Q12: (2) If we include sites, they are random effects rather than fixed effects since the intent is to generalize beyond those sites in the trial With random effects, the inference extends to all possible sites (i.e., the population of sites) With fixed effects, the population is just the sites that have enrolled patients Main idea is to analyze the data according to the way in which they have been collected

56 Q12: (3) Interesting question (at least for statisticians!)
How can we regard the sites as a random sample of all sites if we have selected them because they have talented and committed physicians conducting the research there? No decent answer – but we have little interest in drawing conclusions that apply only to the sites that have entered patients

57 Q13: When should a planned interim analysis (for safety and/or efficacy and/or sample size re-estimation) be appropriate? What are the pros and cons? What are the methods used?

58 Q13: There are three reasons for doing an interim analysis:
Examine the safety of the vaccine at an early time to ensure that we are not harming subjects - either stop or continue Examine efficacy of the vaccine at an early time – may stop because vaccine is very good or very bad, or may continue Re-estimate sample size – learn that study is too small to show a difference (variability too large, treatment effect is too small) – probably don’t want to increase sample size by more than 50% total

59 Q13: (2) All interim analyses carry a risk of unblinding the study
If study stops, all is known If study continues, a reasonable inference is that the study has a small p-value (>0.05) since we would have stopped if there was little hope of showing a difference Someone might inadvertently (or deliberately) let information slip out

60 Q13: (3) These require adjustment of the critical values. It is complicated and several programs (EaST, PEST, SPlus for sequential analysis) are available All interim analyses or sample size re-estimation analyses need to be specified a priori in the protocol

61 Thank You

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