I am working on a multi-site randomized, placebo-controlled, double-blind, parallel-design trial. The trial population will be made up of two cohorts: cohort 1 who meet a specific inclusion criteria (N) and cohort 2 who do not (n=10% of N). Randomization will be stratified by site, cohort and opting into a separate sub-study. The outcome is a score obtained 6 months after randomization.
The question I wanted to raise is regarding the definition of the ITT analysis population. Previously, we have analyzed patients based on the group they are randomized to if they received at least a single dose of study drug – so a modified intent-to-treat analysis. The investigators feel like the study will have more rigor if the primary ITT analysis population were made up only of the N participants who meet a specific inclusion criteria (cohort 1), and the secondary analysis could be the entire trial population of N+n. However, I haven’t come across many trials where the ITT analysis population is defined based on an inclusion criteria vs post randomization variables such as receipt of at least a single dose of drug etc. Has anyone come across a similar study or does anyone have any thoughts regarding this.
At least in my experience, I have not seen this particular design in the past.
Part of what I am wrestling with is that the 10% cohort would otherwise normally be considered screen failures, and not part of your primary analysis cohort, as they would typically not proceed in the study, and would not receive study treatments.
I presume that the 10% who do not conform to the specific inclusion criteria do not risk some kind of safety or ethical issue due to the exposure to the study treatments, since you are allowing them to proceed in the study.
One initial question for you:
How are you powering the study in terms of the estimated sample size? Only based upon those who conform to the specific inclusion criteria (the 90%), or for all patients including those who do not (90% + 10%)?
If the former, then my first thought is that your mITT cohort are the patients that conform to the inclusion criteria and get at least one dose of the study treatment. The other 10% constitute a secondary, exploratory group of sorts to be analyzed together with the 90%, and/or perhaps even separately, depending upon the intent of their inclusion in the study to begin with.
If the latter, then your full 90% + 10%, that get at least one study treatment is your mITT cohort, albeit, you then have to consider the potential for, first, confounding due to the inclusion of patients that fail to meet the inclusion criteria of interest in the 10%, and second, an analysis of the 90% alone being underpowered.
Thank you for your thoughts. Agreed, the 10% would typically be considered screen failures in other trials. However, the investigative team is interested in enrolling and studying this specific group as well as long as they meet other inclusion criteria.
The study was powered based upon the 90% who conform to all the inclusion criteria - so we will have adequate power if that was our mITT analysis cohort. I appreciate the response.
A follow-up question: if the intent was to only study/analyze cohort 1 then why recruit cohort 2 and stratify the randomization scheme by cohort?
I’m not a fan of the industry way of defining the analysis set for analyzing efficacy data, which is often based on some modification of the ITT population that deviates from the randomized population. I tend to agree with the “once randomized always analyzed” approach. You could run the analysis on the randomized population and include cohort as a covariate. Defining the ITT population based on any post randomization variable is not allowed for RCTs.
Those are good points, but if a patient fails to return even for the first follow-up visit what do you do?
Agree that loss to follow-up (LFU) is an issue. Ideally we would want to find out about the patient’s outcome even if they early terminate from the study so that there is no missing data (ie, consider during protocol development that the primary efficacy data will continue to be collected after early termination). If not possible, a conservative approach would be to assign the worst outcome for missing data due to LFU. One may also consider inverse probability weighting to correct for the bias due to LFU to some extent.
Do you have other recommendations? Thanks!
For the “no follow-up data” case (dropout right after randomization) there’s not much you can do. For other cases, either measure the response so frequently that you will capture what’s happening before the actual dropout (which allows you to make the missing at random assumption and analyze all available data (but not with GEE)), or using an ordinal longitudinal model with dropout as a bad part of the ordinal outcome scale.