Protocol deviation and its impact on stat analysis


First time poster here and grad student in health research methods. Quick question on methodology and how that impacts the statistical anlaysis (cox model):
If a trial with 3 arms makes a change in one of the arms half-way through the trial, how does this protocol deviation impact statistical analysis for primary endpoint, such as a composite of MI, stroke, death. Especially, if we find out later that the randomization was tampered with and at least one-fifth of the subjects were affected by it.
I am just having a hard time understanding why the authors didn’t take into account this deviation because there must be some impact of it.

Any thoughts?

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there have been some interesting cases recently of failed randomisation (new york times article) and changing outcome (circoutcomes) which both generated discussion. If changing the outcome is pre-specified and built into the design then ok, although it seems dubious to me. It will become more common with the popularity of composites, typically by adding more outcomes in the hope of gaining more power. In doing this it seems to me researchers are acknowledging that composites are opaque and a hodge podge of outcomes anyway, so why not throw another in the mix if event rates are unexpectedly low. Obviously the primary outcome should not be changed after unblinding (according to ICHE9). Regarding failed randomisation, I’ve had some experience with this - many years ago looking at pressure ulcers. Maybe mattress type was the ‘treatment’. In the hospital if the mattress type they were randomised to wasn’t available they just gave them the alternative. Needless to say you want to minimise this because the results from intention-to-treat and per protocol analyses are likely to depart. In this study we also had ‘false inclusions’ ie patients who did not meet the eligibility criteria were randomised to treatment (I think stephen senn had published an opinion on this at the time indicating these patients should be included in the analysis). We also make a record of patients requesting a switch to the other mattress. Incidentally, you didn’t describe how the treatment arm changed… I may have misunderstood your Q

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My instincts here are to throw away the data. Unless you can definitively isolate and discard the patients who were not randomised according to protocol, you have a bias of unknown size and direction.

If the treatment protocol change in one of the three arms, then you have a four-arm study, with two of the arms having the problem that they aren’t simultaneous, and they are smaller than the other.

I would concentrate on putting distance between my signature and any such study!


The main analysis from most trials is the intention-to-treat analysis. This compares outcomes between the, here, 3 trial arms, and is interpreted as the difference in outcome if everyone had been randomized to arm A vs B or B vs C or A vs C. Since the intention-to-treat effect is the effect of randomization, we don’t need to worry about changes to the intervention after baseline (changes to the outcome definition are an entirely different matter).

But usually we really want to know about effect of receiving one versus the other interventions. Now, changing the intervention partway through the trial is important to consider.

If everyone adhered perfectly, was not lost to follow-up, and there were no changes to the intervention, the intention-to-treat analysis will also be an estimate of the intervention effect. But, in this trial, since there are deviations after baseline, the intention-to-treat effect is no longer a good estimate of the intervention effect.

In a two arm trial with a placebo control, when the intention-to-treat effect is not a good estimate of the intervention effect, it is usually closer to the null. But in a three arm trial, or a trial with a comparison group that isn’t placebo, this won’t necessarily be true. So, we do know the intention-to-treat effect in this trial is a poor estimate of the effect of the intervention but we dont know if it is an under-estimate or an over-estimate of that effect.

Estimating the intervention effect would require (1) a clear definition of the interventions you want to compare (eg. should they include this deviation or not); (2) data on all predictors of intervention received, and this data needs to have been collected at baseline and over follow-up; (3) statistical methods that account for time-varying adherence-confounder feedback.

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in an itt analysis, eg oncology, we might consider the patient a “failure” at the time of switching treatments; i’m not sure if this contradicts what you’re describing. It’s more crude than using time-varying adherence but more persuasive to some

If treatment switching / failure is the outcome then definitely we need to know about that. But if the outcome is some other variable, then the intention-to-treat should not incorporate switching. Any analysis which incorporates switching (other than as an outcome) is not technically an intention-to-treat analysis anymore (although many incorrectly call it a modified intention-to-treat analysis), and is instead an attempt to estimate a per-protocol effect (i.e. the effect of the treatment protocol). All per-protocol effect estimation analyses need to adjust for predictors of switching in order to control for confounding, and these are probably post-randomization so need special statistical methods.

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itt is just about including all pts and preserving the randomisation. oncology trials often analyse survival outcomes and treat switching as failure, might be referred to as time-to-trt-failure, but it’s just time to progression with switching treated as progression, or could be considered a time-to-first composite, in any case it is itt. It’s not at all PP (data aren’t discarded), it’s just a conservative analysis, like a ‘worst case’ analysis, it’s crude but conservative, and there are a slew of supportive analyses that would be produced. I loathe the term ‘modified itt’, incidentally, think i’ve only seen it used once and never since

Unless I’m misunderstanding, it sounds like you mean that treatment switching is included as part as the outcome definition. Then certainly we need good information on treatment adherence in order to avoid outcome misclassification, and our main concern for the intention-to-treat effect estimate will be whether we have correctly identified all the switching/failure events.

Treatment switching should be possible to be reliably measured, and if the need for switching is driven by mainly objective things, it can be reasonable to do a simple analysis counting switching as a failure, e.g., Y = time to first of (clinical event, treatment switching). This provides the only estimand that everyone understands and requires few assumptions, I think.