Final FDA Guidance "Adjusting for Covariates in Randomized Clinical Trials for Drugs and Biological Products" - what we learned?

In May 2023, FDA published the final guidance for industry "Adjusting for Covariates in Randomized Clinical Trials for Drugs and Biological Products". This final version was based on the draft guidance with the same title that was released 4 years ago in April 2019 (see a previous post "FDA and EMA Guidance on Adjusting for Covariates in Randomized Clinical Trials".

FDA created guidance snapshot below:

The final guidance provided the general guidelines on several issues related to the covariates or baseline covariates. 

Both unadjusted analysis and analysis adjusted for baseline covariates are acceptable. However, if analysis is adjusted for baseline covariates, the details about the covariates need to be pre-specified in the statistical analysis plan before the study unblinding. Our experience is that the details about which baseline covariates to be included and whether the baseline covariates are continuous or categorized need to be pre-specified. 

Usually, the analysis adjusted for baseline covariates leads to efficiency gain and is more powerful than the unadjusted analysis. 

It is acceptable to calculate the sample size based on adjusted analysis, but perform the final analysis based on analysis adjusted for baseline covariates. In practice, the sample size calculation is commonly based on adjusted analysis regardless of the final analysis. For example, for a study to compare two group means, the sample size may be calculated based on t-test approach, but the analysis may be based on analysis of covariates where the adjustment for baseline covariates are used. 

For studies with stratified randomization where the randomization is stratified by one or more baseline covariates (categorical), the stratification factors are usually included in the analysis model even though the treatment assignments are generally balanced within each stratum. 

For studies with stratified randomization, it is not uncommon that incorrect stratification may occur where the treatment assignment is picked from the incorrect stratum. When this occurs, there will be two sets of the randomization stratification information (two different strata variables): strata as randomized versus actual strata. It is acceptable to use either strata variable as randomized (intention-to-treat principle) or actual strata variable (correct strata information for all patients). When mis-stratification occurs, there should be any attempt to go back to the randomization systems (such as IRT, IVR, IWR) to correct the stratification allocation. Once randomized, it is randomized. While the incorrect stratification is used for randomization, the correct stratification can be recorded on the case report form or EDC (electronic data capture). See a previous post "Handling Randomization Errors in Clinical Trials with Stratified Randomization".

For studies with continuous outcome measures, the endpoint is usually the change from baseline to a specific visit. Baseline covariate is used in the change from baseline calculation. In the analysis adjusted for baseline covariate, the baseline covariate can still be included in the model even though it gives an impression that the baseline measure is used twice. 

The guidance contains additional guidelines on linear models and non-linear models. For example, for linear models, the issue related to treatment group by covariate interactions is discussed: 

For non-linear models, binary outcome (logistic regression), ordinal outcome (generalized linear model), count outcome (Poisson regression), or time-to-event outcome (Cox regression) are analyzed. The estimators like odds ratio and hazard ratio are called are non-collapsible effect measures. Non-collapsibility implies that the effect parameter is not the same for different sets of covariates that are conditioned on, even if these covariates are independent of the exposure. Even when all subgroup treatment effects are identical, this subgroup specific conditional treatment effect can differ from the unconditional treatment effect. 

References: raps.org: FDA finalizes guidance on adjusting for covariates in randomized trials

Comparing assumptions for sample size estimation with the interim and final results

Sample size estimation is one of the critical aspects of the clinical trial design. The sample size estimation is usually based on the primary efficacy endpoint. If the primary efficacy endpoint measure is a continuous variable, the sample size estimation will need to be based on assumptions about the effect size (for example, the difference in means) and the common standard deviation If the primary efficacy endpoint measure is a rate and proportion, the sample size estimation will need to be based on the effect size (for example, the difference in responder rate) and the rate/proportion in the control group. 

Sometimes, the sample size estimations can be grossly inaccurate primarily because the assumptions used for the sample size calculation deviate from the observed data. This is especially true in planning pivotal studies with no or insufficient early-phase clinical trial data. 

It is important to check the assumptions for sample size estimation during the study and adjust the sample size when the observed data suggests the inaccuracy of these assumptions. The process is essentially the "Adaptations to the Sample Size" described in FDA's guidance "Adaptive Designs for Clinical Trials"

"Accumulating outcome data can provide a useful basis for trial adaptations. The analysis of outcome data without using treatment assignment is sometimes called pooled analysis. The most widely used category of adaptive design based on pooled outcome data involves sample size adaptations (sometimes called blinded sample size re-estimation). Sample size calculations in clinical trials depend on several factors: the desired significance level, the desired power, the assumed or targeted difference in outcome due to treatment assignment, and additional nuisance parameters—values that are not of primary interest but may affect the statistical comparisons. In trials with binary outcomes such as a response or an undesirable event, the probability of response or event in the control group is commonly considered a nuisance parameter. In trials with continuous outcomes such as symptom scores, the variance of the scores is a nuisance parameter. By using accumulating information about nuisance parameters, sample sizes can be adjusted according to prespecified algorithms to ensure the desired power is maintained. In some cases, these techniques involve statistical modeling to estimate the value of the nuisance parameter, because the parameter itself depends on knowledge of treatment assignment. These adaptations generally do not inflate the Type I error probability. However, there is the potential for limited Type I error probability inflation in trials incorporating hypothesis tests of non-inferiority or equivalence. Sponsors should evaluate the extent of inflation in these scenarios." 

 "One adaptive approach is to prospectively plan modifications to the sample size based on interim estimates of nuisance parameters from analyses that utilize treatment assignment information. For example, there are techniques that estimate the variance of a continuous outcome incorporating estimates of the variances on the individual treatment arms, or that estimate the probability of a binary outcome on the control arm based on only data from that arm. These approaches generally have no effect, or a limited effect, on the Type I error probability. However, unlike adaptations based on non-comparative pooled interim estimates of nuisance parameters, these adaptations involve treatment assignment information and, therefore, require additional steps to maintain trial integrity.

Another adaptive approach is to prospectively plan modifications to the sample size based on comparative interim results (i.e., interim estimates of the treatment effect). This is often called unblinded sample size adaptation or unblinded sample size re-estimation. Sample size determination depends on many factors, such as the event rate in the control arm or the variability of the primary outcome, the Type I error probability, the hypothesized treatment effect size, and the desired power to detect this effect size. In section IV., we described potential adaptations based on non-comparative interim results to address uncertainty at the design stage in the variability of the outcome or the event rate on the control arm. In contrast, designs with sample size adaptations based on comparative interim results might be used when there is considerable uncertainty about the true treatment effect size. Similar to a group sequential trial, a design with sample size adaptations based on comparative interim results can provide adequate power under a range of plausible effect sizes, and therefore, can help ensure that a trial maintains adequate power if the true magnitude of treatment effect is less than what was hypothesized, but still clinically meaningful. Furthermore, the addition of prespecified rules for modifying the sample size can provide efficiency advantages with respect to certain operating characteristics in some settings."

One thing that is often neglected is to compare the final results with the assumptions. When a clinical trial is concluded, it is always good to check how different the final results are from the assumptions. If the final results are positive (indicating the success of the trials), people tend to ignore the assumptions made during the trial planning stage. Only if the final results are negative (indicating the failure of the trials), do people tend to go back to the assumptions and claim that the trial failed due to inaccurate assumptions leading to the lack of statistical power. 

Biogen's Tofersen for SOD1-ALS

Biogen designed a Valor study as the pivotal study to investigate the effect of tofersen for the treatment of patients with Amyotrophic Lateral Sclerosis (ALS) associated with mutations in the superoxide dismutase 1 (SOD1) gene (SOD1-ALS) - a subset of general ALS population. The primary efficacy endpoint is  the ALSFRS-R score and the sample size for the study was based on assumptions about the ALSFRS-R score. 

"We calculated that a sample size of 60 participants (2:1 randomization ratio) in the faster-progression primary analysis subgroup would provide 84% power to detect a between-group difference on the basis of the joint rank test (described below), assuming a change in the ALSFRS-R score from baseline to week 28 of −4.8 in the tofersen group and −24.7 in the placebo group, with a standard deviation of 20.39 and survival of 90% in the tofersen group and 82% in the placebo group, at a two-sided alpha level of 0.05."

The final results indicated that assumptions were so inaccurate. In the placebo group, the change from baseline to week 28 is -8.14 (versus assumed -24.7).

Usually, it is the sponsor's responsibility to ensure that the assumptions for sample size calculation are as accurate as possible. If inaccurate assumptions are used in sample size calculation that leads to the failure of the trial, the regulatory agency may request the sponsor to do additional trials (with more accurate assumptions). However, in Biogen's Tofersen Vilor trial, FDA came to the defense of Biogen why the trial failed in the primary efficacy endpoint in ALSFRS-R score so that they could potentially approve a drug based on the positive results in biomarker and discredit the fact that the study failed in clinical endpoint. In FDA's briefing book for the advisory committee to discuss the Tofersen in SOD1-ALS, the following was mentioned:

Comparing the assumptions for sample size estimation with the analysis results can be complicated by the fact that different statistical methods are used. Sample size estimation may be based on a two-sample t-test while the actual data will be analyzed using more complicated methods (analysis of covariance, mixed model repeated measures, random coefficient model, non-parametric methods,...). For studies with a time-to-event primary efficacy endpoint, the sample size calculation may be based on the log-rank test, and the statistical analyses may be based on the Cox regression where analyses are adjusted for multiple explanatory variables. 

However, it is always good to compare the assumptions for the sample size estimation with the observed data (during the study or at the conclusion of the study). 

Another successful trial with randomized withdrawal design

Biotech company PTC Therapeutics announced today that their phase III study of Sepiapterin in PKU patients achieved the primary efficacy endpoint.

PTC Therapeutics Announces APHENITY Trial Achieved Primary Endpoint 

with Sepiapterin in PKU Patients

PKU (Phenylketonuria) is a rare, inherited metabolic disease, which affects the brain. It is caused by a defect in the gene that helps create the enzyme needed to break down phenylalanine. If left untreated or poorly managed, phenylalanine – an essential amino acid found in all proteins and most foods – can build up to harmful levels in the body. This causes severe and irreversible disabilities, such as permanent intellectual disability, seizures, delayed development, memory loss, and behavioral and emotional problems. There are an estimated 58,000 people with phenylketonuria globally.

The pivotal license trial is called APHENITY trial and the randomized withdrawal design was used for the trial even though the randomized withdrawal design was not explicitly mentioned. According to PTC's new release, the APHENITY study is described as the following:

APHENITY was a global double-blind, placebo-controlled, registration-directed study which enrolled 156 children and adults with PKU. Participants were randomized to receive sepiapterin or placebo for six weeks with the primary endpoint being reduction in blood phenylalanine levels. The trial consisted of two parts. Part 1 was a run-in phase, during which all screened subjects received sepiapterin for two weeks. Only those subjects who demonstrated a reduction in phenylalanine levels of 15% or more from baseline in Part 1 were randomized to receive either sepiapterin or placebo in Part 2 of the clinical trial. The primary analysis population consists of those who had greater than 30% reduction in phenylalanine levels from baseline during Part 1 of the trial. The primary outcome measure is the reduction of blood phenylalanine levels from baseline compared to Weeks 5 and 6 in patients from Part 2 of the clinical trial. All patients are eligible to enroll in an open label long term clinical trial designed to further evaluate the long-term safety and durable effect of sepiapterin.

The study design (randomized withdrawal design) can be depicted in the following diagram: 

Through the APHENITY trial, it is demonstrated that the randomized withdrawal design can be successfully used in the pivotal study of the rare, inherited metabolic disease.

Refer to the previous posts on randomized withdrawal design:

• Randomized withdrawal design and randomized discontinuation trial
• Randomized Withdrawal Design - Examples for Defining the Criteria for Run-in and Randomized Withdrawal Periods
• Randomized withdrawal design in action - Accord trial in Alzheimer's agitation

Violin plot versus Box-Whisker Plot

A box and whisker plot (Also called: box plot, box-whisker diagram) is defined as a graphical method of displaying variation in a set of data. In most cases, a histogram provides a sufficient display, but a box and whisker plot can provide additional detail while allowing multiple sets of data to be displayed in the same graph. The box-whisker plot displays the following in the data set. 

1. Minimum value: The smallest value in the data set
2. Second quartile: The value below which the lower 25% of the data are contained
3. Median value: The middle number in a range of numbers
4. Third quartile: The value above which the upper 25% of the data are contained
5. Maximum value: The largest value in the data set

The box-whisker plot can also indicate the mean value (the dot). The difference between the mean value and the median value can indicate how skewed the data is. 

The box and whisker plot can also include the outliers where outliers are defined as values below Q1 - 1.5 * IQR or values above Q3 + 1.5 IQR (Q1 is 25th percentile and Q3 is 75th percentile, IQR - Interquartile is the distance between 25th percentile and 75th percentile). 

Boxplot can include the only box with lower, upper quartile and median, but not include the min and max values. In a paper by White et al "Combination Therapy with Oral Treprostinil for Pulmonary Arterial Hypertension A Double-Blind Placebo-controlled Clinical Trial", the boxplots without min and max were used to present the NT-proBNP data (a measure with skewed distribution). 

Recently, I see several papers using violin plots to display the data distribution. According to Wikipedia:

A violin plot is a statistical graphic for comparing probability distribution. It is similar to a box plot, with the addition of a rotated kernel density plot on each side.

Violin plots are similar to box plots, except that they also show the probability density of the data at different values, usually smoothed by a kernel density estimator. Typically a violin plot will include all the data that is in a box plot: a marker for the median of the data; a box or marker indicating the interquartile range; and possibly all sample points, if the number of samples is not too high.

A violin plot is more informative than a plain box plot. While a box plot only shows summary statistics such as mean/median and interquartile ranges, the violin plot shows the full distribution of the data. The difference is particularly useful when the data distribution is multimodal (more than one peak). In this case a violin plot shows the presence of different peaks, their position and relative amplitude.

Like box plots, violin plots are used to represent comparison of a variable distribution (or sample distribution) across different "categories" (for example, temperature distribution compared between day and night, or distribution of car prices compared across different car makers).

A violin plot can have multiple layers. For instance, the outer shape represents all possible results. The next layer inside might represent the values that occur 95% of the time. The next layer (if it exists) inside might represent the values that occur 50% of the time.

Although more informative than box plots, they are less popular. Because of their unpopularity, they may be harder to understand for readers not familiar with them. In this case, a more accessible alternative is to plot a series of stacked histograms or kernel density distributions.

in a paper by Chen et al "Efficacy of transcutaneous electrical acupoint stimulationcombined with general anesthesia for sedation andpostoperative analgesia in minimally invasive lung cancersurgery: A randomized, double-blind, placebo-controlled trial", violin plots were used to display the distribution of the VAS measure. 

In a paper by Colli et al "Burden of Nonsynonymous Mutations amongTCGA Cancers and Candidate Immune CheckpointInhibitor Responses", the violin plot was used to display the distribution for r the number of NsM (log10) across different tumor types. 

SAS has a procedure Proc BOXPLOT to generate the box-whisker plots and SAS codes are also provided for generating the Violin plots. Other data analysis software including R have packages to generate the box-whisker plot and violin plot.