Individual response

I am not sure what Judea Pearl was trying to do by offering this example based on alleles and tasty medication. His and Scott’s paper contains the necessary data to illustrate their argument of how to place bounds on the probabilities of 4 counterfactual situations of (1) survival on control and treatment (2) no survival on control but survival on treatment (‘benefit’), (3) survival on control but not on treatment (‘harm’) and non-survival on control and treatment. I proposed one hypothetical narrative that would make sense of their data from a clinical point of view (see Individual response - #65 by HuwLlewelyn). With imagination, there could be many such appealing narratives but the allele / tasty drug example as proposed by Judea Pearl does not appear to be one of them.

It seems to me that dreaming up appealing illustrative narratives is not the issue. From my viewpoint there are 4 important questions:

  1. The paper’s use of the word ‘benefit’ and ‘harm’ in a counterfactual situation differs from that used when describing the probabilities of an outcome conditional on control and treatment and designating the treatment beneficial or harmful.
  2. If we could derive probabilities for the above, how would they be used to make medical decisions by also taking into account probabilities of adverse effects and their various utilities (i.e. effects on well-being)? In other words, what is the purpose of calculating probabilities of these 4 counterfactual situations?
  3. They are estimating the probabilities of counterfactual situations that are by definition inaccessible for the purposes of verification or calibration, unlike other models of prediction for example.
  4. In view of (3) are their assumptions and reasoning about using various results from RCTs and observational studies to arrive at inequality probabilities of these counterfactual situations sound, culminating on page 8 of the paper?

@Pavlos_Msaouel I want to rethink this and disagree with you a bit.

The problem with overall survival (OS) in oncology studies stems solely from the existence of rescue therapy that can prevent or delay death (and can also prevent cancer recurrence but we are talking mainly about post-recurrence changes in therapy). I posit that most any method that tries to estimate OS will be hard to interpret. The only easy clinical interpretation comes from estimating things like the probability of either the need for rescue therapy or death. A state transition model can easily distinguish between need for rescue therapy with and without a later death, and it can count death as worse than rescue therapy. State occupany probabilities can be computed, by treatment, for death, rescue tx or death, rescue tx and alive, etc.

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Love it! Obviously there are currently differences but this is an open problem and glad to see you using your skills and experience to address it your way.

In fact, if I recall correctly, part of the motivation for writing that DFS vs OS post at the time was that you had posted a comment on another datamethods thread at the time talking about your state transition model approach in the context of COVID-19 trials. Intuitively I can see connections but unable to go deeper, in part also because the cancer that truly motivates my research (renal medullary carcinoma) is highly aggressive and we are not yet at the point therapeutically where we need to use new methods for survival estimation. Thus, I think about this topic far less than I do other challenges.

While our team has very elaborate and efficient Bayesian non-parametric models we use to attack this problem, it is not certain that they will be the optimal approach. A major reason why is that they are time-consuming, hard to intuit/interpret, and lack user-friendly tools. On the other hand, you are an expert with decades of experience at creating popular and powerful modeling tools for the community. Would love to see your group approach these problems.

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Thanks Pavlos. Ordinal longitudinal Markov state transition models have lots of advantages of interpretation as detailed here, besides being very true to the data generation process. Advantages come from the variety of causal estimands through the use of state occupancy probabilities, and the fact that all of these estimands are simple unconditional (except for conditioning on treatment and baseline covariates) probabilities. What I thin k is needed to make this work in your context are

  • rescue therapies must have a clinical consensus around them to be considered for the list (and note that you can distinguish various levels of “rescue” with an ordinal outcome, e.g. surgical vs chemo vs radiation vs chemo+rad)
  • in a multi-center RCT the practice patterns for use of rescue therapy are fairly uniform or can be somewhat dictated by a protocol

To me the only problems that are really hard to solve in this context are the existence of non-related follow-up therapies and non-related causes of death such as accidental death.

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I think these excellent considerations deserve an ongoing discussion/panel particularly with regulators such as the FDA because the challenge is becoming progressively more common across diseases.

Right now I’m trying to start just such a project at FDA but for neurodegenerative disease.

Presently at FDA rescue therapy is somethat that is worked around rather than directly addressed, thinking of it as more of a censoring event than an outcome. That always makes results hard to interpret to me.

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I have gone over the paper again carefully. The assumption on which the whole paper is based is ‘consistency’. To quote from the paper: “At the individual level, the connection between behaviors in the two studies relies on an assumption known as ‘consistency’ (Pearl, 2009, 2010), asserting that an individual response to treatment depends entirely on biological factors, unaffected by the settings in which treatment is taken. In other words, the outcome of a person choosing the drug would be the same had this person been assigned to the treatment group in an RCT study. Similarly, if we observe someone avoiding the drug, their outcome is the same as if they were in the control group of our RCT. In terms of our notation, consistency implies: P(yt|t) = P(y|t), P(yc|c) = P(y|c).”

However, according to their example data for females:
P(yt|t) = 489/1000 = 0.489, P(y|t)= 378/1000 =0.378, P(yc|c) = 210/1000=0.210, P(y|c)=420/600 = 0.7
So that P(yt|t) ≠ P(y|t), P(yc|c) ≠ P(y|c)

According to their example data for males:
P(yt|t) = 49/1000 = 0.49, P(y|t)= 980/1400 = 0.7, P(yc|c) = 210/100=0.210, P(y|c)=420/600=0.7
So that P(yt|t) ≠ P(y|t), P(yc|c) ≠ P(y|c)

This means that the assumption of consistency is not applicable to the paper’s example data of their RCT and observational study. However, they go on to make the calculations nevertheless “based on this assumption (i.e. of ‘consistency’), and leveraging both experimental and observational data, Tian and Pearl (Tian and Pearl, 2000) derived the following tight bounds on the probability of benefit, as defined in equation (3): P(benefit) = P(yt, y′c). Therefore the estimated probability bounds in their inequality equation (5) do not follow from their assumptions and reasoning. However, by applying these probability bounds they arrive at point estimates of the probability of counterfactual ‘benefit’ and ‘harm’ (the latter are defined in my previous post (Individual response - #205 by HuwLlewelyn).

I created new example data for males and females where the RCT data were identical and the proportions choosing to take the drug and not to take it were the same as in their observational example. However in my new observational study data, P(yt|t) = P(y|t) and P(yc|c) = P(y|c) so that the assumption of ‘consistency’ could be applied. I then applied their calculations to this data that I had created.

Instead of getting point estimates I got probability ranges. For females the probability of ‘benefit’ counterfactually (e.g. by giving treatment, turning the clock back and giving placebo) was between 0.279 and 0.489 and the probability of ‘harm’ was between 0 and 0.21. For males the probability of ‘benefit’ was between 0.28 and 0.49 and the probability of ‘harm’ was between 0 and 0.21. (p(Harm) = p(Benefit) – CATE, which was 0.279 and 0.28 for females and males respectively). The calculations are in the Appendix below. If the assumption of consistency is valid, we can tell all this from the RCT alone: p(Benefit) ≥ Pr(yt) - Pr(yc) and P(Benefit) ≤ Pr(yt) and p(Harm) = p(Benefit) - (Pr(yt) - Pr(yc)), so that the observational study adds nothing in this context. As we have discussed already, observational studies can be useful in other ways such as detecting adverse effects.

Female RCT and ‘consistent’ observational study

Calculations for females (replacing those on pages 8 and 9 in the paper), when Pr indicates that the probability is from the RCT and Po indicates that the probability is derived form the observation study:
P(Benefit) ≥ 0
P(Benefit) ≥ Pr(yt) - Pr(yc) = 489/1000 -210/1000 = 279/1000 = CATE = 0.279
P(Benefit) ≥ Po(y) - Pr(yc) = 0.4053 – 0.21 = 0.1953
P(Benefit) ≥ Pr(yt) - Po(y) = 0.489-0.4053 = 0.0807

P(Benefit) ≤ Pr(yt) = 489/1000 = 0.489
P(Benefit) ≤ Pr(y’c) = 790/1000 = 0.79
P(Benefit) ≤ Po(t, y) + Po(c, y’) = 686/2000 + 474/2000 = 0.343 +0.237 = 0.58
P(Benefit) ≤ Pr(yt) − Pr(yc) + Po(t, y′) + Po(c, y) = 0.489-0.21 +0.357+0.063 = 0.6997
0.279 ≤ p(Benefit) ≤ 0.489 and (0.279-0.279) = 0 ≤ p(Harm) ≤ 0.21 = (0.489-0.279)

Male RCT and ‘consistent’ observational study

Calculations for Males (replacing those on pages 8 and 9 in the paper):
P(Benefit) ≥ 0
P(Benefit) ≥ Pr(yt) - Pr(yc) = 490/1000 -210/1000 = 280/1000 = 0.28 = CATE = 0.28
P(Benefit) ≥ Po(y) - Pr(yc) = 0.406 – 0.21 = 0.196
P(Benefit) ≥ Pr(yt) - Po(y) = 0.49-0.406 = 0.084

P(Benefit) ≤ Pr(yt) = 49/1000 = 0.49
P(Benefit) ≤ Pr(y’c) = 790/1000 = 0.79
P(Benefit) ≤ Po(t, y) + Po(c, y’) = 686/2000 + 474/2000 = 0.343+0.237 = 0.58
P(Benefit) ≤ Pr(yt) − Pr(yc) + Po(t, y′) + Po(c, y) = 0.49-0.21 +0.357+0.63 = 0.7

0.28 ≤ p(Benefit) ≤ 0.49 and (0.28-0.28) = 0 ≤ p(Harm) ≤ 0.21 = (0.49-0.28)


I agree. To use the words of Gelman, I think it’s helpful to develop statistical methods in the context of applications, and also to work toward theoretical understanding, as Pearl has been doing. However, the push towards theoretical understanding from Pearl has been around for a long time yet it lacks any concrete practical application (except for the theoretical ones like in this thread). No clinician in this thread so far has endorsed any of this as helpful for clinical decision making so I wonder where we are heading? It would be good if someone on this thread could post a real world example of where a problem has been solved using the theoretical explanations posted in this thread.


Thank you @s_doi. There seem to be many reasons for the failure to implement these theoretical ideas. One is difficulties in communication. For example, ‘benefit’ and ‘harm’ as an individual response in the context of counterfactual situations has a completely different meaning to benefit and harm arising from the use of an intervention. This is illustrated in the paper’s conclusion that in females the probability of individual ‘harm’ from treatment is zero when more people die on the treatment than on placebo. The latter describes the response of groups of individuals and is subject to stochastic variation, which as @Stephen pointed out, prevents estimation of individual response. The probabilities of outcomes can be substantiated by experiment whereas we cannot in reality turn the clock back and create a counterfactual situation to substantiate individual response.

We have a rationale for making decisions based on outcome probabilities but it not clear how probabilities of ‘individual benefit’ or ‘individual harm’ would change these decisions. From my calculations, it does not change the information available to us from RCTs at all as p(Benefit) ≥ Pr(yt) - Pr(yc) and P(Benefit) ≤ Pr(yt) and p(Harm) = p(Benefit) - (Pr(yt) - Pr(yc)). What we need is better predictive information (e.g. when everyone dies by using parachute with a big hole in the canopy but no one dies with a proper parachute). In this situation an observational study would be as good as an RCT but reason alone as good as both, making the studies unethical! However, the reasoning must be sound, which includes checking that the assumptions about the data are consistent with the data (or at least not clearly inconsistent).


Thanks @HuwLlewelyn , I think your summary brings great clarity to this discussion and makes a lot of sense. It also reminds me of a quote in some other thread attributed to Vineet Tiruvadi that seems to apply to the framework in this thread “if you start with the wrong framework then the ability to do complex analyses may seem like it’s giving insight, but what you’re mostly doing is studying how wrong your framework is


This discussion is incredibly helpful. @HuwLlewelyn joins @Stephen Senn in being the most impressive scientists I’ve known in their abilities to cut through arguments of others and to make cogent new arguments. It confirms what @Stephen has argued repeatedly that principles of experimental and clinical trial design must be brought to causal inference about treatment effects. The discussion also confirms my previous feeling that outside of special situations (such as analysis of treatment effects within RCTs compensating for non-adherence to treatment) causal inference remains a theoretical nicety and a great thought organizer but has not yet been translated to practical application in treatment evaluation. Hence the lack of uptake on the challenge put at


One area where causal inference might be translated to a practical application in treatment evaluation is when taking HTE into consideration. This was a tweet that I addressed to Judea Pearl recently to which he did not reply:

In RCTs Irbesartan reduces risk of nephropathy. HbA1c & AER are risk factors. According to ‘causal’ medical theory, Irbesartan should reduce AER but not HbA1c. For HTE, should risk reduction be estimated due to that of AER alone & not HbA1c? How does CI notation express this?

How would @Stephen and others in this discussion design a study to answer this question?

I have yet to study Huw’s reply in detail but on a brief read I think that it gets to the nub of the argument. It seems baffling to me that consistency is considered to be reasonable or practical. However, I wonder if in fact M&P depends on more than just “that an individual response to treatment depends entirely on biological factors, unaffected by the settings in which treatment is taken”. The individuals contributing information from the observational studies are not the same individuals as in the RCTs. Thus we have to be able to assume that the two sets of individual are exchangeable to the extent needed in order to be able to solve for the unknowns. I do not consider this to be a reasonable assumption and referred to “study effects” as being a problem. The TARGET study is an excellent example of the problem Lessons from TGN1412 and TARGET: implications for observational studies and meta‐analysis - Senn - 2008 - Pharmaceutical Statistics - Wiley Online Library
The way that study effects are dealt with in conventional statistical approaches is either by declaring them as fixed and hence eliminating them by contrasts or as declaring them as random and then trying to estimate the variance component. All of this was extensively developed in connection with incomplete block designs by the Rothamsted school in the period 1925-1945.
My view is that adding observational data does not pull the rabbit out of the hat. Adding extra equations does not necessarily render a system identifiable, in particular, if in doing so one adds more unknowns.


I would like to sum up following @Stephen’s and my latest skirmish with Judea Pearl on Twitter. He wrote that I was wrong to assume that p(Yt) from the RCT should have been equal to p(y|t) from the observation study. However he reasserted that p(y|t) was equal to p(yt|t), the latter being the result of a ‘Level 3’ or imaginary RCT result that applies to choosers (it can be imagined after reasoning from other established beliefs but cannot be done in realty). It seems that the assumption of ‘consistency’ is therefore a Level 3 or imagined result of p(yt|t) that is equal to (y|t) the observation study result. This assumption of ‘consistency’ is therefore unverifiable and un-refutable by study and based on personal belief leading to a forceful assertion.

The only probabilities supported by reliable data are the results of the RCT. If we are only prepared to rely on the RCT results (but not rely on forceful assertions based on imagination) then all we can conclude is that from counterfactual concepts, p(Individual Benefit) ≥ Pr(yt) - Pr(yc) and P(Individual Benefit) ≤ Pr(yt) and p(Individual Harm) = p(Individual Benefit) - (Pr(yt) - Pr(yc)) as I explained in a previous post. However, the latter probabilities of imaginary individual counterfactual outcomes do not seem to make any difference to practical decisions, which result in the reasoning set out in @Stephen’s Twitter response [See].

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Huw, I and others greatly appreciate your diligence on this incredibly important topic. I tried my very best to get Judea to join us here so that he could try to expand his arguments and provide details as you have done, and also to carefully read all the posts here, but to no avail. But your posts, like those of @Stephen are also highly useful for citing in tweets. If you haven’t done this already, clicking on the 3 dots at the bottom of the post pulls up a chain link symbol that can be clicked on to get the URL that leads directly to a specific reply, for inclusion in a tweet.

I agree that it is a pity that Judea Pearl does not engage in our discussions on this site. I suppose he can still follow links to find out what we are writing; I will link my Twitter posts to this site more consistently from now on! He has now responded in a general way this morning to my question about how to verify his assumptions about consistency and I have asked for a link or reference to his source. You will have learnt from my recent post on ‘solid causal inferences’ [Examples of solid causal inferences from purely observational data - #26 by HuwLlewelyn] that I have spent a lot of thought and time on how we can use post licensing ‘observational’ studies learn how to apply RCT results to patient care and to monitor our effectiveness. I am hoping that my diligence in participating in these discussions will help me to learn how best to explain my own ideas to the statistical and CI communities (as in addition to clinicians in my own community).

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@Pavlos_Msaouel - this new R package is relevant: Multi-State Models for Oncology

Very nice. Would prefer if the survival curves show the confidence bands for the difference as per your approach, e.g., here.

You may also find interesting how we modeled disease status here in an oncology phase I-II design scenario.