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(22/22) Intercurrent events do not create the need for a formal definition of causality or a formal identification argument. They expose a need that was already present in the uncomplicated trial.

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(21/22) Partial-identification bounds on P[S(1)=S(0)] can also be used. So assumptions capable of solving this problem are not necessarily untestable. The formalism makes that easy to see.

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(20/22) S(1)=S(0) is Fisher’s sharp null and has testable implications. In particular, it implies P(S=1|A=1)=P(S=1|A=0), so the assumption is falsifiable.

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(19/22) Therefore, E[Y|A=1,S=1]−E[Y|A=0,S=1]=E[Y(1)−Y(0)|S=1]. Under S(1)=S(0), the proposed survivor contrast identifies a well-defined causal effect. That is the theorem.

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(18/22) For each a, consistency gives E[Y|A=a,S=1]=E[Y(a)|A=a,S=1]. Since S=S(a), randomization gives E[Y(a)|A=a,S=1]=E[Y(a)|S=1].

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(17/22) It follows that E[Y(1)−Y(0)|S=1] is a well-defined average causal effect among observed survivors.

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(16/22) Now assume S(1)=S(0) almost surely. In words, treatment changes no individual’s survival at m. By consistency, S=S(A)=S(1)=S(0). Both potential weights therefore exist for everyone with S=1.

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(15/22) We therefore first need to say what “causal effect” means. I use “average causal effect” to mean the mean difference between the same individuals’ potential outcomes, in a population where both outcomes are defined.

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(14/22) An observed survivor could die under the other treatment, so one of Y(1),Y(0) may be undefined. The causal effect may not even exist.

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(13/22) Here is the solution: let S(a) and Y(a) be survival and weight under assignment a. Y(a) exists only if S(a)=1.

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(12/22) As a patient, I might be denied important information that could help me make a treatment decision because an analysis was dismissed without a rigorous causal argument.

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(11/22) As a collaborator, I would be disappointed if a possible solution to my problem was missed because the formalism was rejected.

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(10/22) As the student in this example, I would be disappointed to learn that I had been taught something incorrect because my training lacked sufficient rigor.

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(9/22) This lack of rigor in a mathematical discipline is concerning. The consequences of rejecting formalism extend beyond this point on RCTs.

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(8/22) In the same way, no one can be certain why RCTs “are causal by design” without the formalism Neyman gave us 100 years ago.

(7/22) He couldn’t have been certain about that without formalism, but it is false. Below I show a simple solution using potential outcomes.

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(6/22) I did not get a straight answer, but one of his responses was that any assumptions needed to solve the problem would necessarily be untestable.

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(5/22) Can Frank give the student conditions under which E[Y|A=1,S=1]−E[Y|A=0,S=1] identifies a causal effect?

(4/22) Consider a randomized antidepressant trial examining the effect on weight Y at month m. Some participants die before m. Let A be treatment and S survival. A student proposes comparing arms only among those with S=1.

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(3/22) He rejected even the potential outcomes framework, the first formalization (100 y/o) for why “RCTs are causal by design”. To delve into that position, I posed a problem to him:

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(2/22) @f2harrell and others claim that no formal causal models are needed in RCTs.

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Iván Díaz @idiaz.bsky.social · 03/08/2026

(1/22) Over the last few days I have been discussing the role of formal causal inference in RCTs, and in general the role of formalism and rigor in statistics in twitter with @f2harrell.bsky.social. Thread with an example for why both are fundamental for biomedical research:

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neither, instrumental variable(s) is an identification strategy 😅

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Iván Díaz @idiaz.bsky.social · 15/07/2026

One example I’ve come across is the effect of anti depressants on weight. Most of the literature looks at weight gain. I’m not a pharmacoepidemiologist and so have little basis to critique relevance, but it is what the literature looks at and it makes sense to me.

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Iván Díaz @idiaz.bsky.social · 15/07/2026

Clinical relevance is debatable, and your quote about a patient with a good score at baseline who remains steady is sensible, but there are often questions of safety for which that reasoning may not apply. This is not my central point though, my point is about correctness of analysis.

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Iván Díaz @idiaz.bsky.social · 15/07/2026

We come from very different schools of thought (model vs estimand first) so it will be hard to find agreements, but there are two issues you bring up in the post: clinical relevance and statistical correctness. One can definitely design a correct analysis of change scores.

I agree with the first part, but not with the solution. If there is a correct and an incorrect way to use a method, then as methodologists that is what we should teach. I find this more effective than proscribing the method.

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Yes, but my insistence is because I find it easier to use methods that are correct for change scores than to argue why they may or may not be clinically relevant... And to do the former it does not help to have people implying (incorrectly) that there is any sort of consensus to avoid change scores

I don't think banning our way out of people's misuse of tools is the way... But, if you accept E[Delta(1) - Delta(0)] as a valid (albeit trivial) estimand, do you accept E[Delta(1)] / E[Delta(0)] ?

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Thus my point that the outcome definition itself tells you nothing about correctness of the trial!!

ANCOVA only works for linear models (which is why I prefer to speak of cover adjustment), but let's focus on it. In an RCT, can I not run Delta ~ trt + Y_pre and get correct and efficient estimators to the three estimands I listed above? Nothing wrong with an outcome defined as change score.

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Efficiency is a property of estimators, not of estimands. I did not talk about estimators, but sure, you should always use efficient estimators and use covariate adjustment, I have written a few articles developing methods for it.

My general point is that I see nothing wrong with the following setup. Data are Y_pre, T, Y_post. Define Delta = Y_post - Y_pre, and then define, identify, and report the estimates of E[Delta(1)] and E[Delta(0)] and their difference.

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I am not distinguishing RCTs from obs data, BTW. RCTs often have covariate dependent randomization which induce a lot of the issues of obs. data. Of course a within-arm comparison does not give a treatment effect. But within-arm outcome means are often reported, along with effects.

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Not at all, I think. There are often interpretive reasons to report change scores. And since careful analysis can always yield correct estimates, I do not really see much of a reason to ban analyzing change scores...

Don't you also need to know how the change score was analyzed before concluding that using it was a bad decision?

I keep coming back because the contortions in the writing are fascinating. Take the claim that “science alone cannot guide public health decision-making,” which appears a few sentences after “religious participation itself seems to result in better health” is supported by citations to science

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Iván Díaz @idiaz.bsky.social · 23/06/2026

I am open to arguing the merits of political affirmative action in science, but this has to be a joke when it is the conservatives in power currently destroying public health.

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Any package that implements estimators for the longitudinal g-computation formula can do this. E.g., lmtp or ltmle in R.

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Whether NDE/NIE are falsifiable or not under this standard probably depends on the specific question. BTW, the original slide mentions verifiability, not falsifiability (!)

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Exactly, falsifiability in the CI literature has been incorrectly equated to testability with experiments, but that's a narrower definition than other scientific fields use. Falsifiability should only require empirical evidence that contradicts the predictions of a theory.

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Not all causal modeling! This is actually a debated issue even if it is sometimes presented as fact.

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But this is cultural! Many scientists in other fields are happy drawing knowledge from mathematical models under mathematical manipulation (intervention) without the need for correspondence to actions in the real world. We could be them.

Yes, that’s the core of the issue and the debate would be richer if it focused on that. Something that the interventions have failed to explain convincingly is why they believe different standards should be applied to clinical/social sciences compared to other sciences.

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then, of course, it may be the case that nde/nie are not identified, in which case you may be able to use partial identification, but that requires accepting nd/nie as legitimate scientific objects, which the agential view of causal inference does not

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it turns out that assessing identifiability of nde/nie requires the same type of knowledge, specifically they are identified under no unmeasured confounding and no post-treatment confounding, which are structural assumptions that imply cross-world

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identify, I should have said

Are you comfortable assessing the assumptions necessary to estimate controlled direct effects with a post-treatment mediator-outcome confounder?

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