But, I think it is wrong.

Specifically, I disagree with Professor Tennant’s claim about regression to the mean, despite agreeing with him entirely on the broader point. That point, as I understand it, is that an improvement under a sham treatment cannot be interpreted as a benefit due to the sham treatment. In particular, in a two-armed trial, one group (the treatment group/arm) receives the treatment under investigation and the other group (the control group) receives a sham treatment. In that sort of two group comparison, an observed improvement of the control group cannot be attributed to the sham treatment for the basic reason that we don’t know what would have happened to those patients in the absence of the sham treatment.

A fix for this state of ignorance would be three-armed trials with a treatment group, a sham treatment group, and a true do-nothing group. Surprisingly, scholarly papers have been written about this seemingly commonsensical observation[1]. In any event, such studies are relatively uncommon.

Anyway, this is simply the usual problem of causal inference, where we don’t know the counterfactual — what would have happened — in the absence of intervention; even if that intervention is a sham intervention. There is a possibility, which we should keep firmly in mind, that the patients would have improved come-what-may and therefore the apparent benefit is in fact just the so-called “natural history” of the disease course.

That’s all well and good, but my claim is that there is no further value in describing this possibility in terms of “regression to the mean”. In fact, based on what I have seen, I suspect that most invocations of regression to the mean are technically incorrect.

First things first, then, what is regression to the mean? Originally, regression to the mean was related to Galton’s famous observation that children of very tall parents tend to be shorter than their parents, which can be stated in symbols as

overall average height < E(child’s height | parent’s height) < parent’s height

Without knowing anything specific about the genetic mechanisms of inheritance, we may note that the joint distribution of a child’s height and a parent’s height can be well-represented as a bivariate Gaussian distribution. From this vantage point, regression to the mean is simply a geometric fact about the shape of this joint distribution. Specifically, the regression line for predicting the child’s height from the parent’s height has a shallower slope than the principal axis, which lies along the diagonal (assuming that generation over generation the population height distribution isn’t changing).

But this fact about the bivariate Gaussian (with common marginal distributions) is not a universal property. Indeed, the image below shows a distribution for which conditioning on some values of one variable entails a prediction for the other variable that is above the diagonal — you predict a higher value than the one you saw.

So then, if regression to the mean is not a universal property, what is the value in invoking it at all? Well, on the one hand it might just be that we think it is a common enough property that it is worth mentioning. Fair enough, although we must stress in that event that it need not be so. That possibility is no more valid as a “what if” than any other unobserved counterfactual (more on this below).

To me, the real value of regression to the mean as an idea is that it offers a powerful rhetorical device. Used in this capacity, the most important part of the regression to the mean concept can be stated in a way that doesn’t have anything to do with the mean (average), per se. The bigger idea is related to the Gambler’s Fallacy.

The Gambler’s Fallacy consists in claiming, on the one hand, that observations are independent but that, on the other hand, some set of observations seen so far makes certain outcomes more or less likely. So you say that the roulette wheel spins are independent, but in the same breath you say that eight blacks in a row makes the next spin more likely to land on red. Or black; either way the fallacy is that you’re contradicting yourself.

We may think of regression to the mean in similar terms: the probability of two consecutive independent observations from the same distribution has the property that, in cases where the first observation was exceptionally large (or small), the next observation is highly likely to be more modest. In an independent draw you are not so likely to be exceptional, by the very definition of exceptional: the probability of getting an outcome below the 99th percentile is, after all 99%.

That is, the rhetorical value of this observation is this: events which are acknowledged to be independent can nonetheless appear to be related simply by the way one frames the comparison.

Perhaps the most famous example of regression to the mean is used precisely in this capacity as a sort of reductio ad absurdum. The example comes from econ Nobelist Daniel Kahneman [2]. Suppose that military flight instructors have a policy of berating pilots who make bad landings. They notice that good landings met with praise mostly result in subsequently less-good landings, while bad landings met with harsh criticism mostly result in subsequently improved landings. Therefore, they say, the evidence suggests that “sticks are better than carrots”. Is this interpretation of the evidence sensible?

To stress test our reasoning, we consider the ostensible evidence in light of the null hypothesis that subsequent landings are in fact independent of one another, regardless of criticism or praise. We are not claiming that they actually are independent, but merely asking what the world would look like if they were. That is, contrary to the assumptions of the instructors, we suppose that each landing is independent of subsequent landings, irrespective of both feedback or the quality of the previous landing). We imagine that each individual landing is the product of the stable skill of the pilot as well as random fluctuations that vary from occasion to occasion. When a good pilot makes an exceptional landing, she is unlikely to best it on her next landing. For this reason, praise appears unlikely to “work” even though landings are — by stipulation — independent of one another! For a poor pilot a similar argument holds. When he makes a very poor landing, he is unlikely to do worse on his next landing. For this reason, criticism appears likely to “work” even though landings are independent.

The thought experiment of independent landings and no treatment effect shows that what we had been interpreting as evidence for efficacy (of criticism opposed to praise) was in fact entirely irrelevant to that claim because such evidence is equally consistent with an uninteresting hypothetical world where the treatment was assumed to do nothing at all.

If the flight instructors had instead randomly praised or criticized and considered the goodness of the subsequent landing in absolute, rather than relative, terms, they could have properly compared the carrot and the stick. Regression to the mean is being invoked here as a competing “what if” thought experiment to help us calibrate how impressive the observed evidence is in favor of a some alternative hypothesis. It is emphatically not a claim that the landings were, in fact, independent of one another.

Getting back to clinical trials, let’s consider a 2021 editorial in Acta Orthopedica titled ”When the placebo effect is not an effect” [3]. In discussing a number of famous studies [4] in which patients were given actual knee surgeries versus sham knee surgeries (which involved incisions and sedation, but no actual arthroscopic intervention) Dr. Harris seeks to make a distinction between “natural history” and “regression to the mean” (emphasis added):

Natural history (what would happen regardless of treatment) explains, for example, the eventual resolution of symptoms from the common cold. It also explains most or all of the improvement in pain that occurs after injuries. Natural history also confounds the treatment of fluctuating conditions such as multiple sclerosis. Without considering natural history in trials of surgery, we may falsely attribute improvement that occurs post-surgery as being due to the surgery (the fallacy of post hoc ergo propter hoc: it follows, therefore it is because of).

Regression to the mean occurs when we select patients who are currently at one end of a spectrum and follow them. Over time, they will fall closer to the mean.

He then goes on to recount the Kahneman pilots story, failing to appreciate the thought-experiment nature of it by asserting that “both groups were simply regressing to the mean” (emphasis added). Not so! The point is merely that they could have been regressing to the mean under the uninteresting model of independence. Whether they were or not is a separate matter and, in fact, it is not hard to imagine the actual pattern of landings to be “sticky” in various ways. Harris’s assertion that “Over time, they will fall closer to the mean” is unjustified — it is, indeed, “question begging” in that it presumes the thing that it claims to show. Crucially, we need a third trial arm to prove regression to the mean just as much as we need it to show treatment effect of a sham treatment.

Concretely, in the case of the sham knee surgeries I would like to argue that invoking regression to the mean provides no rhetorical benefit above and beyond considering hypothetical natural histories, whatever they may be. To see this, we may imagine a number of different natural histories, each of which tells a different story.

In Scenario A, patients suddenly go from healthy to unhealthy — as in the case of an acute injury — and then gradually the body returns to a state of health.

In Scenario B, patients gradual see a degradation in their knee health followed by a gradual return to healthy status.

In Scenario C, patients see an acute deterioration in their knee health followed by persistent impairment and no return to health.

In Scenario D, patients see a gradual deterioration in their knee health followed by persistent impairment and no return to health.

In Scenario E, patients exhibit a haphazard (random) pattern of knee symptoms about some common level.

Now suppose that our study selected participants on the condition that their most recent observation was in a state of impairment, and suppose further that our sham treatment group saw a return to health, on average. The chief difficulty in interpreting this result is that we do not know if we are in situations A or B versus C or D. Under A or B the improvement of the sham surgery group implies no treatment effect; under the C or D scenarios the improvement of the sham surgery group does indicate a treatment effect. Without a proper do-nothing group in our study, we can’t well say which of those two regimes we are in. Moreover, intelligent people can disagree about which scenarios seem more likely.

However, it is primarily Scenario E where the regression to the mean concept usually derives its rhetorical force. But in this context, and in many others, such as win-loss records in sports, the null hypothesis of independent and identically distributed outcomes is inappropriate even as a straw man. Indeed, in the knee surgery study it was not a spontaneous bad knee day that led to enrollment, but rather a persistent history of knee problems.

To summarize, the next time you want to say “they might have gotten better anyway”, or some variant thereof, just say that and don’t bother invoking regression to the mean unless it adds something concrete to the case at hand. Throwing it in there because it sounds good is “math washing”, which is also a rhetorical device but one we should probably avoid.

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[1] Hróbjartsson A, Gøtzsche PC. Is the placebo powerless? An analysis of clinical trials comparing placebo with no treatment. New England Journal of Medicine. 2001;344(21):1594–1602.

[2] Kahneman D. Thinking, fast and slow. New York: Farrar, Straus and Giroux; 2011.

[3] Harris I. When the placebo effect is not an effect. Acta Orthopaedica. 2021;92(5):501–502. Acta Orthopaedica

[4] Moseley JB et al. A controlled trial of arthroscopic surgery for osteoarthritis of the knee. New England Journal of Medicine. 2002;347(2):81–88.

If you’re like me, you think there is something importantly different about those two examples of thought experiments. In particular, the roulette example is “realizable” in the sense that we could in fact sit down and play roulette for many, many spins and “realize” the probability (or prove it wrong, perhaps). What I mean is that if our thought experiment was accurate, we would be able to take advantage of it by doing the thing the thought experiment was about. The second example, not so much. In my opinion, de Finetti (and also Jimmie Savage) made a mistake in insisting that these cases were fundamentally the same; I think they are both thought experiments, but that the difference between them (realizable vs unrealizable) is critical and shouldn’t be ignored.

How does this distinction matter in practice? Well, it’s relevant for the Frequentist vs Bayesian divide that we still see chatter about from time to time on LinkedIn and elsewhere. I can’t believe I’m wading into this, but here goes.

Firstly, I think it is unprofitable to talk of Frequentist methods and Bayesian methods. Rather, any data analysis method has Frequentist properties and Bayesian properties. A Frequentist property is a probability statement about a method that holds averaging over possible data X, for any underlying distribution (indexed by a parameter) theta. A Bayesian property is a probability statement about a method that holds averaging over both possible data X and possible distributions (indexed by a parameter) theta. So they are both thought experiments, but they are different thought experiments.

Now, on the one hand a Frequentist property is stronger than a Bayesian property in that if something holds for every theta, it will obviously hold on average with respect to any distribution over theta. So when a Frequentist property is available, great! That’s a Good Thing. Case closed, right?

Well, the wrinkle is that the quality of the available Frequentist property might be worse than the quality of the Bayesian property (with respect to a given prior). If we have an “inductive bias”, that can be super helpful. Maybe we think a regression function is smooth, or a certain coefficient has a restricted sign. Bayesian methods are a natural way (but not the only way, see below) to incorporate such “hints”. (Using hints is smart in the real world and refusing to do so in a stubborn bid for aesthetic purity is silly IMO.)

Another issue is that the available Frequentist property might only be provable asymptotically, which might not be a good representative of finite-sample operating characteristics at all. Moreover, in practice we are not doing Frequentist thought experiments in the sense that we don’t get repeated size-n samples from a fixed theta. Rather, we get a theta, we get a sample, repeat — that’s the Bayesian thought experiment, integrating over X’s and thetas. So if we knew the “true” prior, Bayesian methods are the way to go! Case closed right?

Well, no, because we don’t usually know the prior. Still, I have found myself in the past saying to colleagues: “I trust my approximation of the prior more than I trust your asymptotic approximation of the sampling distribution.” Or maybe you do have finite-sample guarantees, but the intervals are absurdly large because you weren’t willing to hedge a little with prior information. It’s a trade-off that should be made on a case-by-case basis.

In any event, after many years of thinking about these issues I think there are two under-appreciated facts that help bridge the divide between the Frequentist and Bayesian perspectives. One is that just like Bayesian methods have Frequentist properties, any method can have Bayesian properties. What makes a method Bayesian is just that it is theoretically optimal with respect to a given prior. But with Bayesian methods being a bear to fit in some cases (especially Bayesian non-parametric models) I think it is worth thinking about evaluating tractable methods relative to their so-called Bayes risk. That is, I’m a proponent of “Bayesian evaluation of non-Bayesian estimators/models/methods”. This amounts to doing Monte Carlo simulations with respect to a particular prior. Typically, this is a lot easier than fitting a full Bayesian model for that same prior. And — the big benefit — you can make priors more realistic and focus on estimators that have better computational properties.

Lots of people have studied the Frequentist properties of Bayesian estimators, but I’m walking in the other direction, proposing to investigate the Bayesian properties of tractable estimators with respect to realistic priors. When you aren’t chained to using a Bayesian estimator, you are no longer tempted to fudge your model/prior for reasons of convenience. This Monte Carlo Bayes risk idea should, IMO be the default instead of over-used industry benchmarks or toy datasets. (I think this is true for evaluating these LLM models too….using fixed benchmarks just invites over-fitting.)

Interestingly, I like to think of this aapproach as "computational de Finetti" because the big thing de Finetti got right, to my mind is a focus on the prior predictive distribution: the range of possible data sets we believe we might see. So my prescriptive advice is this: do your modeling at the level of the prior predictive, basing it in creative and flexible ways on historical data sets and whatever modeling tools are available; do your estimation/inference with whatever tools are flexible and practical; tune these procedures so that they work well with respect to the prior predictive you specified, which can and should be as gnarly as you want it to be.

The second under-appreciated fact is that it is sometimes possible, and often interesting, to pursue a Frequentist analysis without ignoring relevant real-world information, i.e constraints on the data generating process. In other words, you can get closer to evaluating the realizable performance of a method without having to swallow an entire prior, by doing a frequentist style for-all-theta analysis, but subject to some constraints. Restrict your regressions to monotone functions, or unimodal densities, or particular signal-to-noise ratios, or with a restricted support. You don’t think the stock market will grow 10x in a single day? Then your statistical method doesn’t have to accommodate that possibility.

This idea of restricting the "hypothesis class" is a cornerstone of statistical learning theory, but in that context the restrictions are rather abstract (smoothness classes in function space and so forth). An intersting area for future work is to figure out ways to bake in substantive domain-specific assumptions without fully committing to a parametric model or a specific prior. I believe Gile Hooker’s idea of “data augmented regression” is promising in this regard.

But wait, there’s more! It was a discussion paper, and the contributing discussants read like a Who’s Who of causal inference. In no particular order: Andy Gelman, Guido Imbens, Judea Pearl, John Ioannidis, Nicholas Schork, Stephen Raudenbush, Tyler J. VanderWeele, to name just a few.

I particularly liked the contributions of Ralph Horwitz, who I was not previously familiar with. His introduction (with Burton Singer) “What Works? And for whom?” is a source of great motivation for me as someone who works on algorithms for discovering heterogeneous treatment effects.

Link to the Journal Issue (unfortunately paywalled): https://www.sciencedirect.com/journal/social-science-and-medicine/vol/210/suppl/C

Additionally, here is a comment on the paper by Stephen Senn (always worth reading): https://errorstatistics.com/2018/01/13/s-senn-being-a-statistician-means-never-having-to-say-you-are-certain-guest-post/

I work on machine learning for causal inference (causal ML) and, quite frankly, it hasn’t proven as useful as we all had hoped, at least not yet. But why? Does machine learning for causal inference feel unsuccessful to me simply because it remains underused at present, or is it little used because it has failed to deliver on its promise on those occasions that it has been used so far? Would further attempts redeem it?

Discussing this issue requires understanding some of the inherent limitations of the method as well as some common unjustified biases against ML for causal inference. Here, I am going to present six lemmas that form an important conceptual foundation for any discussion of whether or not machine learning has a rightful place among the tools of applied causal inference. At the end we will briefly litigate ML’s standing in causal inference using these six lemmas as touchpoints.

To read this article with proper math formatting, go here.

Notation

We will be using some equations in this one. The target audience is graduate students in statistics, computer science, epidemiology, policy evaluation, etc.

Let Z denote the treatment, X be a vector of pretreatment covariates, Y(z) be the potential outcome under treatment z, and Y=Y(Z).

For binary treatment,

In what follows I will bounce between four possible configurations of two independent aspects of the problem: is Z randomized or not, and is Z continuous or dichotomous? I will announce what setting we are in whenever we switch it up.

It is always helpful to have concrete examples in mind, but in this essay I am not always going to pick one for you, but I do encourage you to fill in your own.

Lemma 1: identification can be local

Conditional exchangeability may hold for some covariate values and fail for others. Identification status can therefore be heterogeneous.

Here Z is dichotomous and not randomized. It is common to state identification assumptions in terms of random variables. For example,

identifies the average treatment effect (ATE). But the ATE may fail to be identified, while certain conditional effects are identified.

Card and Krueger (1994)

In Card and Krueger’s famous minimum wage study [“Employment effects of minimum and subminimum wages: Panel data on state minimum wage laws”.” ILR Review 47, no. 3 (1994): 487-497] which helped popularize the difference-in-differences estimator, they studied fast food restaurants in New Jersy and Pennsylvania. They discuss, at some length, why this particular sector is more likely to satisfy the required parallel trends assumption. In the end, their result was not about all companies in the country, nor was it about all companies in NJ and PA, nor was it about small restaurants in those states, it was narrowly about fast food restraurants in NJ and PA.

There will always be tension between internal validity and external validity, but that is all the more reason to contemplate, at length, whether or not causal assumptions are plausible for some limited sub-population of your data. This is not a machine learning lesson, per se, but it speaks to the need to think always conditionally, which is at the heart of the machine learning ethos.

Local average treatment effect

After many years of using the ratio estimator in IV problems with binary treatment and binary instrument, it was discovered that this estimator was not estimating the treatment effect people had perhaps hoped that it was estimating; it was not estimating the overall average treatment effect. So what was it estimating?

A few lines of algebra show that the identification strategy underpinning the ratio estimator only works for individual for whom the value of the instrument actually changes their behavior with respect to treatment [cf. Imbens & Angrist (1994). “Identification and estimation of local average treatment effects.” Econometrica, 62(2), 467–475]. This can be formalized using the idea of principle strata, which partitions the study population based on how they respond to the instrument. For concreteness, let’s consider an encouragement design, where the instrument is an inducement to seek treatment, such as a reminder to get a flu shot.

The latent strata consist of the so-called Always Takers, Never Takers, Compliers and Defiers. The names are pretty self-explanatory. Some folks would always take the treatment no matter what the value of the instrument, and some folks would never do so. Meanwhile, Compliers and Defiers are swayed by the value of the instrument, but in opposite directions. Compliers take the instrument’s “advice” while the Defiers do the opposite of whatever they are encouraged to do. Without getting into the math here, it’s easy enough to convince yourself that if we have Defiers in our population we’re screwed. So we usually assume them away. And what is left-over then is the LATE, or local average treatment effect, also called, more appropriately in my opinion, the complier average treatment effect (but of course the acronym CATE is already spoken for, where the C means “conditional”). “Local” here means holding for one subgroup and not the others.

Now, if we believe the treatment effect is basically the same across these patient types, then the lack of identification is not so troubling; we may simply estimate the treatment effect for the group where it is identified and then assume that that estimate applies to everyone else. Is this reasonable? Well, it certainly doesn’t have to be the case — in our flu encouragement example it is easy to imagine that Always takers are the concientious sort of people whose overall health is better than average and who therefore benefit less from a flu shot for the simple reason that their outcomes without treatment are better than the other strata.

Again, principle strata are not inherently a machine learning concept, but stratifying the population already arises as a key component of these causal identification strategies and that opens the door to think about stratifying based on observables, which is what machine learning is all about. In particular, it should feel deeply unsatisfying to be able to estimate the treatment effect for a subpopulation that is utterly indistinguishable.

Lemma 2: observational adjustment is function learning

Under conditional deconfoundedness and overlap,

Identification means that these functions are estimable; but still, they must actually be estimated.

Here we have non-randomized Z which may be either continuous or dichotomous, but let’s focus on the dichotomous case.

For statisticians, it is fairly common that one’s first exposure to causal inference ideas comes via the concept of omitted variables bias and, more specifically, omitted variables bias in the context of a linear regression model. Here’s what that looks like. Suppose the model is

Because X strongly determines the probability of treatment, a linear regression of Y on Z will systematically misjudge the treatment effect (which here should be 2). In fact, the amount by which it is off is easy to see in this totally linear case:

That 25/7 is called the “omitted variable bias” — the penalty we pay for forgetting to include X in our linear model. If we include X, as God intended, then we recover the true treatment effect no problem.

This narrative was always a little to pat for me, on the grounds that if I don’t include X in the model then the coefficient I am estimating has a totally different meaning. It isn’t that it’s biased, it’s just a totally different quantity! The “biased” term is, in fact, the one appearing in the Best Linear Unbiased Predictor based on only Z. The fact that it doesn’t give us what we want is because prediction is different than causal inference, a fact that I intuited as a student but didn’t yet have the language to articulate. The problem, to my mind, of calling this a biased estimator is How the hell is the math supposed to know what we had hoped to estimate? It just estimated what we told it to.

The econometricians have a slightly tidier way of looking at it, which is to absorb the missing covariate into the error term that we told the model was supposed to be uncorrelated with the treatment variable but wasn’t, due to the X hiding inside of it now:

The reason this story is nicer than blaming it on an omitted variable, in my opinion, is because it makes clear that what needs to happen is not only that “X was included in the model” or even “the model was totally correctly specified”. Instead, it is this narrower thing where the error needs to be independent of the treatment variable. By not including X we violated that condition. But there are other ways that condition can be violated.

Which brings us, at long last, to nonlinearity. Because, see, the important thing is not just that the confounders are in the model, it is that the confounders are in the model in a way that renders that error term unrelated to Z as required. And that can fail to be achieved even if X is included, if it is included in the wrong way.

For example, modifying the model to

entails that OLS with X included only as a linear term, still gets the wrong answer. The ATE is 2 still. The model with no X at all estimates it at about 14.3. A linear adjustment in X gives about 15.3. An adjustment with the correct quadratic term gives about the correct value of 2 (up to sampling variability).

What we see in this example is that residual confounding can be functional-form error. Flexible regression is therefore a robustness device. If the truth is simple, regularization can keep the variance cost modest. If the truth is nonlinear, flexibility can prevent mis-estimation due to identification failures arising from misspecification.

The “linear in the parameters” riposte

Now, econometricians are fond of specifying models that are “linear in the parameters”. Which is to say that they have included the correct variable transformations and interactions into the model, rendering OLS appropriate — as in our example above where the problem is solved if you know to include the cubic term in the model. Regression would be easy if the correct basis were known! But it is almost always unknown! Treating it as known…it’s basically cheating, if you are a theorist, and self-delusion, if you are an empirical researcher.

Including all of the transformations and interactions in your model, and then relying on regularization to pick out the right ones for you, well, that’s a form of machine learning…but it’s a poor one. There are better options (tree ensembles come to mind) and empirical researchers should not be discouraged from using them just because it’s easier to prove things when you assume everything is “linear in the parameters”.

PS: stochtree rules.

Lemma 3: Under randomized treatment, OLS estimates an average slope, not the average slope

Randomization ensures no confounding between treatment level (which we will think of as “dose” in what follows) and potential outcomes, but randomization does not linearize the dose-response curve and OLS does not estimate the average slope across doses.

First, note that nonlinearity in the control variables, as in lemma 2, and nonlinearity of the outcome as a function of dose, as presently discussed, are distinct issues. For a randomized continuous dose Z, let

The slope from a linear regression of Y on Z is generally a design-weighted average derivative

where w(z) is, in general, not the population density of the treatment, meaning that

with the expectation taken with respect to the randomization distribution of Z.

Here’s a small example. For

with mean dose mu, standard deviation sigma, and skewness gamma,

The OLS slope is

In the example below, we see that a symmetric dose distribution gives 1.70 for both the true average partial effect and OLS, while a right-skewed distribution gives 0.90 versus 1.11, a 23% discrepancy.

When I show this example to people, particularly econometricians, the conversation almost instantly turns into an apologia for OLS. The first question is, “Well, maybe it isn’t exact but maybe it isn’t too far off?” The answer depends on how extreme the nonlinearity is and where it is nonlinear compared to the distribution of Z. It ought to be troubling that the goodness or badness of the approximation depends on stuff we can’t know because we decided to fit a linear model. Some clever folks will point out the usual saving grace of testing, which is that if we only want to show that it’s non-zero, a non-zero average derivative will do the trick. In any case, lots of ink has been spilled trying to answer this question in defending OLS; check it out:

• Angrist, J. D., & Pischke, J.-S. (2009). Mostly Harmless Econometrics: An Empiricist’s Companion. Princeton University Press.

• Aronow, P. M., & Samii, C. (2016). Does regression produce representative estimates of causal effects? American Journal of Political Science, 60(1), 250–267.

• Graham, B. S., & Pinto, C. C. de X. (2022). Semiparametrically efficient estimation of the average linear regression function. Journal of Econometrics, 226(1), 115–138.

• Powell, J. L., Stock, J. H., & Stoker, T. M. (1989). Semiparametric estimation of index coefficients. Econometrica, 57(6), 1403–1430.

• Stoker, T. M. (1986). Consistent estimation of scaled coefficients. Econometrica, 54(6), 1461–1481.

• White, H. (1980). Using least squares to approximate unknown regression functions. International Economic Review, 21(1), 149–170.

• Yitzhaki, S. (1996). On using linear regressions in welfare economics. Journal of Business & Economic Statistics, 14(4), 478–486.

These references were taken from a recent LinkedIn post by Diogo Ribeiro. I’ve read the Yitzhaki (1996) reference closely and have long been familiar with the OLS-first approach spelled out in Angrist and Pischke’s popular textbook, but I haven’t read all of the others. Between you and me, it’s a sort of boring question because we could have just fit a nonlinear response!

A brief tangent on denial of nonlinearity

Lemma 3 explains why a misspecified linear model provides a summary that can be hard to interpret. But there is another possibility, which is just that everyone denies the possibility of a nonlinear curve at all. Or at least in the range of doses of interest. Toxicology provides an interesting case study. While it is well known that therapeutic drugs have a “therapeutic window”, above which there begin to be deleterious effects (think acetaminophen and liver toxicity), the field of academic toxicology has predominately used linear or thresholded linear models. In particular, for several decades there was denial of so-called “hormesis”, which is the phenomenon where minor exposure to a toxin can produce health benefits before higher doses exhibit the expected toxicities. One reason for the initial hesitancy was the lack of a plausible mechanism, nevermind theory is supposed to explain empirical facts, not dictate them. One reason for the persistent denial was that the intial hesitancy led to a proliferation of research based on the linear models; hormesis tended not to be observed because the models that mediated our observations did not allow it.

Lemma 4: heterogeneity may be unavoidable

Treatment-effect heterogeneity can be scale-dependent: a constant effect on one scale can vary on another; but sometimes, no homogenizing scale exists.

Here we are in the setting of randomized, dichotomous Z. The question we are considering is if there is heterogeneity on observables X. In particular, we want to consider the claim made by prominent biostatisticians that heterogeneous treatment effects are somehow fundamentally illusory on the hope, or insistence, that things would be homogeneous if only we could find the right scale.

Researchers frequently make the mistake of examining variation in absolute risk reduction by subgrouping, one day shouting “older patients get more benefit” and another day concluding “patients with comorbidities get more benefit”, but these are illusory. It is often the case that anything giving the patient more risk will be related to enhancing absolute treatment benefit. It is an error in labeling to attribute these effects to a specific variable.

—Frank Harrell

[A]n important goal of statistical analysis is to find an additive scale: a system of measurement which has the property that treatment effects so defined are constant from patient to patient.

—Stephen Senn

An important goal indeed. But can it always be done? As a mathematical fact, the answer is “no”, which we can see by smashing together an additive model and multiplicative model. To wit:

where the multiplicative error xi is mean 1 and the additive error epsilon is mean 0. Here r and delta are constant structural treatment parameters.

On the one hand, when r = 0, we have an additive model with a homogeneous treatment effect delta. On the other hand, if those latter three terms are identically zero, delta = A(X) = epsilon = 0, we have a multiplicative model with homogeneous treatment effect xi on the log scale.

However, in general, this combined model will be homogeneous neither on original scale nor the log scale. On the difference scale,

and the effect varies with x whenever B(x) does.

Harrell’s quote from above is claiming that a homogeneous treatment effect on the log scale only looks heterogeneous if you look at the absolute scale because of that B(x) term; taking logs like a gentleman would give you that sweet, sweet homogeneous r parameter. Ah, but in this hybrid model the log-scale treatment effect also remains heterogeneous:

depends on both B(x) and/or A(x). The nonlinear ratio prevents the additive and multiplicative pieces from separating. (A similar argument can be applied to any invertible transformation, cf. Box-Cox, etc.)

Now, it’s an empirical question as to how common such a model might be, and the answer might well be that they are not common at all. That said, I’m not sure how we would ever know, because we typically don’t look out for them very often. Certainly it is not too hard to imagine some biological process with both additive and multiplicative components.

Lemma 5: treatment causality and moderator causality require separate identification strategies

In general, a CATE describes a causal effect in the treatment variable but not in moderator variable(s). More formally:

Note the cheeky mixing of potential outcomes and Pearl’s “do” notation. I think it’s worth the risk of starting an argument with a pedant because the point is expressed so clearly this way.

Anyway, here’s the same claim, but in the form of a story. Suppose that customers who buy an electic vehicle (EV) are eligible for a government rebate. The observational units are zip codes, the dichotomous treatment variable is whether or not a rebate was offered, and the outcome variable is the number of cars sold per capita. Suppose further that the rebate is less effective where electricity is expensive, because a one-time savings can’t offset, in the mind of consumers, the persistent lower savings of the EV in those locations.

Now, if electricity prices are omitted from our model, but for some reason ice cream sales are included, well, we’d find that ice-cream sales predict the rebate effect. Why? It’s the classic confounding story that both ice cream sales and electricity prices rise with higher temperatures. The point here is that a CATE indexed by ice cream sales correctly reflects the causal effects of the rebate. But they only predict the causal effect; the popular new ice cream shop in town won’t make those rebates any less effective, ceteris paribus.

To be clear, I think non-causal CATEs are still super useful, which I discuss elsewhere. But we don’t do anyone any favors by misinterpreting them.

Lemma 6: Heterogeneity may be fully, partially, or not at all predictable

Cross-sectional studies cannot identify individual treatment effects (ITEs).

It is useful to distinguish three components of treatment-effect heterogeneity:

1. covariate-stable effects, meaning effects that are predictable from observed characteristics X;

2. person-stable effects not captured by those characteristics; and

3. occasion-specific, transient effects.

A conditional average treatment effect (CATE) concerns the first component. An individual treatment effect may contain all three.

Let X_i denote observed, stable characteristics of person i, and let t index occasions. Write the treated potential outcome as

and the untreated potential outcome as

Equivalently,

For the observed treatment Z_{it}, this becomes

Suppose that the residuals are normalized so that, for each treatment condition,

The expectation here averages over both persons with covariate value x and also over occasions. It follows that

Thus, tau(x) is the covariate-stable average treatment effect: people with the same observed x have the same predicted average effect. This does not imply that they have identical person-specific or occasion-specific effects.

The occasion-averaged effect for person i is

where the expectation is over occasions for that person. Define

Then

The term delta_i is stable across occasions but is not predicted by the observed covariates. Under the normalization above,

but delta_i need not be zero for a particular person.

The causal effect on a particular occasion is

This can be decomposed further as

where

and

The three terms correspond to covariate-predictable heterogeneity, stable residual person-level heterogeneity, and transient occasion-level heterogeneity.

Mean zero does not require the residual to be the same under z=0 andz=1. The conditions

are separate centering conditions for two different potential residuals. These distinct error terms may have different variances, different distributions, say, from different environmental causes.

For instance, suppose that treatment changes a person’s location. Under z=0, the person remains in a location where the principal stochastic hazard is radon exposure. Under z=1, the person moves to a location where the relevant hazards include arsenic in the water or airborne particulates (and no radon). The mean health consequences of changing locations can be included in tau(x), while the residuals describe occasion-specific departures from those means (different hypothetical lives lived).

Using this decomposition, we se that under the usual causal assumptions, a parallel-group randomized trial identifies the two marginal potential-outcome distributions and thereby permits estimation of \tau(x). It does not identify the joint counterfactual pair for the same person and occasion. Consequently, neither the distribution of \tau_i nor that of \tau_{it} is identified without assumptions about the unobserved coupling of the two potential outcomes.

With only one outcome per person, stable individual heterogeneity \delta_i and transient occasion specific heterogeneity \nu_{it} are observationally confounded. Repeated measurements, crossover trials, repeated randomization, and n-of-1 designs can make aspects of this decomposition learnable. In an ordinary parallel-group trial, however, treatment-effect heterogeneity can be real even when it is only partially predictable — or not predictable at all — from the observed covariates.

See Senn’s “Mastering variation: Variance components and personalised medicine. Statistics in Medicine, 35(7), 966–977” for a traditional ANOVA perspective on this issue.

Summary

Let’s look now, very briefly, at how these lemma should inform the discussion about ML’s usefulness in applied causal inference.

Lemma 1 encourages us to think conditionally in any event, machine learning or not. Too often it is assumed that “the effect” is identified or not, and that ATEs are easier than CATEs. But it’s not true, often a CATE is identified whereas the average is not.

Lemma 2 says that if your goal is estimating an average causal effect from observational data you should definitely be using machine learning in some fashion. There’s no reason not to. It’s a robustness argument. Incorrectly assuming linearity can lead to marked bias, while fitting a nonlinear model when the true data generating process is linear incurs only a small variance penalty.

Lemma 3 tells us that if nonlinear dose response is possible you should conduct your inference accordingly, even if the study is randomized. Some fields refuse to do this and/or settle for single-coefficient summaries, but there’s really no reason for it.

Lemma 4 cautions us that assuming additivity isn’t logically justified. Perhaps it is empirically justified, but it is hard to know on what basis, since the default advice is not to look!

Lemma 5 works in the other direction: people claiming that machine learning is finding “modifiable risk factors” are overclaiming. Don’t blame these misunderstandings on the methods — that’s pure user error.

Lemma 6 is very similar to lemma 4 in pointing out an empirical bias people implicitly impose. The lemma shows that not all heterogeneity is predictable, but what people often assert is that most heterogeneity (or maybe all) is unpredictable. That doesn’t follow, of course, and certainly isn’t a good reason not to look for predictable heterogeneity.

So where does this all leave us? My opinion is that there are two definite upshots. One is that ML should be used as a routine tool for causal inference. It may not produce earth-shattering discoveries or reinvent whole fields, but it does protect against unnecessary model misspecification that can lead to severe bias. ML shouldn’t have to prove that it is always better than OLS. The argument is rather that it is just as good as OLS when it works, and sometimes is dramatically better. It can find interactions and nonlinearities that stock linear models are blind to, and when those phenomena arent’ there, it also does fine. The point of ML is not having to fret about model misspecification — use a flexible model, carefully, and sleep easy at night.

Two, to the extent that ML hasn’t made a big splash in causal inference/treatment effect estimation I think it is because we are not giving it the best chance to do so. If we expressly study problems in regimes where we expect them to be homogeneous and linear, then it is maybe no surprise that our ML models don’t pick up anything interesting. Concretely, lemmas 4 and 6 suggest that we need to measure richer covariate sets if we want to find interesting patterns. Boring covariates will lead to boring findings, and that should hardly count as compelling evidence that there is no heterogeneity. Likewise, lemma 3 suggests we should try a broader range of doses if we wan the best chance to find surprising nonlinearities. I think we forget, the point of science isn’t to chose phenomena where we have a good chance at fitting the right model, the point is to study phenomena we don’t understand and hope that our models help us discover new things about it.

I’m teaching hypothesis testing to undergraduates again.

I always feel like the better I explain it the more they don’t understand why that’s a useful way of thinking about things.

Which got me thinking about types of uncertainty.

I find it helpful in teaching and practicing statistics to distinguish between two types of uncertainty:

— Reducible uncertainty: uncertainty that can, in principle, be shrunk by more information, better measurement, better design, or better modeling.

— Irreducible uncertainty: uncertainty that remains even after all such improvements, relative to the level of description one has chosen.

If you like fancy terms, these two categories roughly correspond to what is known as “epistemic” uncertainty and “aleatoric” uncertainty, respectively. You can look those up.

Statistics, broadly, aims to reduce the reducible part of uncertainty, ideally isolating a residual irreducible component. The reducible-irreducible dichotomy helps us understand various notions of “error” in statistical lingo.

— estimation error is mostly about reducible uncertainty
— prediction error usually mixes reducible and irreducible parts
— measurement error may be reducible, irreducible, or partly both

It also helps us understand some of the major traditions in statistics.

Frequentist inference begins with aleatoric randomness in sampling and uses it to “discipline” statements about unknown fixed quantities.

Bayesian statistics, on the other hand, collapses everything to epistemic uncertainty: it’s “turtles all the way down”. Which on some philosophical level is probably defensible, but on the other hand ignores useful practical distinctions (imo).

The frequentist stance has the opposite problem: it claims to only use aleatoric calibration, but essentially anyone who has ever interpreted a p-value or inspected a confidence interval is basically obliged to use it in an epistemic way.

The company line is “this procedure has such-and-such long-run behavior under repeated sampling.” The practical user (or student!) then immediately asks the epistemic question: “what should I now think about this hypothesis (parameter, effect, etc)?”

Fisher himself tried to square this circle, and his efforts are widely seen as unsuccessful.

Oh, and then there is Knightian uncertainty, which reminds us that sometimes we don’t even understand enough about the world to put down any kind of probability distribution.

See also:

Methodological Virtue is Use-Specific

Distinct methodological cultures arise from different communities working on distinct use-cases. Because the uses of data analysis are many, the subcultures are many. Indeed, subject matter areas independently developing statistical methodology has a long history: biometrics, psychometrics, econometrics, and now data science, among others. In his famous essay "Statistical Modeling: The Two Cultures" Leo Breiman considered the two data analysis cultures he was most familiar with, classical statisticians and algorithm-first proto-data-scientists. But a broader look is also instructive, because there are in fact far more than two cultures these days and my claim is that these cultures are best understood not in terms of the methods they use, but in terms of the goals they develop those methods towards. Understand the demands of a particular use-case and you will understand why certain methods are favored in a given culture. With this in mind, let's consider four dimensions along which data analytic cultures can vary: the estimands they consider, the manner in which their data are acquired, which modeling assumptions they embrace, and their treatment of statistical uncertainty.

Estimands

Estimating averages conditional on observed covariates (what is now called “supervised learning”) calls for different methods than estimating a population (marginal) average. Estimating quantiles or distributions requires different methods than estimating means.

One major dichotomy among estimands is whether they are purely predictive or causal: Do we care about prediction or causalprediction? That is, do we want to predict someone’s salary based on where they went to college, or do we want to predict what someone’s salary would be if everything else about them remained the same, but they were forced to attend a certain college? It could be argued that this distinction animates much of the discussion in Breiman’s essay, although implicitly. Looking back, the “models vs. algorithms” framing of Breiman’s essay obfuscates the prediction versus causal prediction distinction, because both models and algorithms can be used to estimate causal quantities. (Although at the time it was written causal inference was almost exclusively model-based, this was mainly just because the algorithmic approach was so new.)

Data acquisition

Another major difference between cultures is how their data are obtained. For example, econometricians have historically had very little use for design-of-experiments because their data are usually passively observed (e.g. economic indicators or outcomes of non-randomized social programs). Conversely, biostatisticians’ focus on estimating average treatment effects from randomized controlled trials explains their interest in power calculations rather than methods for dealing with omitted confounder bias. Missing or censored data is a further example of a complication arising from the data acquisition process that completely dominates methodological discussion in some fields (e.g. polling and survival analysis) but are effectively absent in others (quality control).

Modeling

Different cultures also vary substantially in terms of what sorts of modeling assumptions are standard versus those which are taboo. Some of these differences are intrinsic to the use-case. For example, astronomical data from optical telescopes or measurements from physical chemistry might naturally be analyzed using a theoretically-motivated deterministic physical model along with a measurement error component for which independent, homoskedastic Gaussian errors are well-justified. By contrast, a recommender system for suggesting products to online consumers doesn’t admit any plausible theoretical model and the patterns of variability are substantially more complex. At the far other end of the spectrum agent-based models and differential equations based models make extremely strong assumptions about the inter-relationship between observations over time.

To complicate the matter even more, an assumption does not need to be correct to be useful (or at least, not actively harmful). George Box’s oft-quoted slogan “all models are wrong, some are useful” conveys this essential fact, but its pithiness obscures an important nuance: the same model can be useful for one task and useless for another! For example, linear regression is a suitable method even if the true conditional expectation isn’t linear, provided that the estimand of interest is the average partial effect of a particular variable (and assuming other conditions are satisfied). This is more-or-less the vantage point championed by Joshua Angrist in his popular econometrics textbook Mastering 'Metrics. On the other hand, if the goal is out-of-sample prediction, then a linear model would be inferior to a more flexible one if the conditional expectation is, in fact, nonlinear. Thus, modeling assumptions within a culture are driven by matters of use-specific adequacy as well as matters of subject-specific fact.

Uncertainty quantification (inference)

Cultures also differ in whether, how, and how much they account for estimation uncertainty. As with our other criteria, these differences are driven by the subject-area. For instance, the stringency of statistical standards varies dramatically from field to field. While a 5% level has long been the conventional standard in the medical literature, particle physicists demand a much higher level of evidence, requiring orders of magnitude smaller p-values before rejecting a null hypothesis. Largely, this disparity results from whether or not a statistical analysis is intended to be the final word on a scientific or policy question. In medicine, perhaps, and certainly in the social sciences, a “statistically significant” designation primarily flags a finding as worthy of follow-up study. In particle physics, it means something closer to “we can finally stop running all of these resource intensive experiments and put our discovery into the textbooks”. To their credit, psychometrics studiously distinguishes between “exploratory” and “confirmatory” analysis, with the understanding that neither alone is sufficient to do good science. The replicability crisis in the social sciences can, in some sense, be put down to the fact that “statistically significant” was never supposed to mean “known for sure”.

In a somewhat different vein, meteorological and epidemiological models based on differential equations are deterministic, but for unknown inputs. Such models are “calibrated” rather than “estimated”, and the approach to uncertainty quantification is much closer to a sensitivity analysis than traditional inference. Here, the impact of model misspecification is likely far greater than any classical sampling uncertainty, but debates about the model can be investigated, to some extent anyway, by other forms of scientific inquiry based on first principles. Moreover, it is rarely clear that the parameter values are uniquely identified by the available data, even if sample sizes were arbitrarily large. But, if the goal is short-term weather forecasts, such concerns are largely academic and some form of back-testing provides satisfactory data for estimating forecast accuracy. Model invalidity and non-identification are substantially more worrisome if one wants to make climate policy recommendations on the basis of such models.

Similarly, algorithmic prediction models can now be furnished with rigorous prediction intervals via conformal inference methods, but parameter estimation in such models is challenged by lack of identification. Likewise, uncertainty estimates arising from, say, a statistical learning analysis (VC dimension) typically provide impractically large intervals (unless the hypothesis class is severely restricted). Bayesian uncertainty represents yet another approach to uncertainty quantification that is increasingly popular but still, many decades on, not yet mainstream. Here is not the place to dive into that long-standing debate, but it is interesting to note that Bayesian methods have mainly been adopted for problems which the traditional paradigm simply wasn’t able to provide reasonable answers in a practicable way. For example, Alan Gelfand -- popularizer of the Gibbs sampler -- told me once that his work on applied spatial statistics led him to a Bayesian approach, because no other methods could give answer to the questions of interest.

FALSE VIRTUES

Focusing on use-case highlights that there is no one “right way” to do things. Of course, such “methodological ecumenicalism” does not mean that just anything goes. Rather, it suggests that poor methodology arises mainly when one loses sight of the intended application. Sometimes this happens for mundane reasons, such as habit. For example, medical researchers often apply linear logistic regression reflexively and uncritically, to estimate propensity scores. With flexible regression models widely available, banking one’s results on the validity of a linear model is as unnecessary as it is commonplace.

However, sometimes particular methods are favored on the basis of false virtues, meaning that the properties endorsing the method are unactualized in practice. Examining such situations can be instructive, as it fosters an understanding of why methods are sometimes applied inappropriately, rather than laying blame on a misguided “culture”. Below we consider a (partial) list of common false virtues and give examples of popular methods that boast them.

Ineffectual theory

By “ineffectual”, I mean theoretical results whose conclusions are practically irrelevant, which can happen for a variety of reasons.

Unrealistic assumptions about the data. To take a high-profile example of unrealistic assumptions, consider the LASSO method for performing variable selection in linear regression models. The LASSO is one of the most highly cited applied mathematics papers of all time. Tracing its intellectual history provides some illuminating context for evaluating the LASSO’s merit. The LASSO has its roots in an earlier method called compressed sensing, which was effectively a result in the design of experiments. It explained that to perfectly reconstruct an image, one needed only a logarithmic number of observations, provided that the original signal was sparse in a certain sense and if the observations were (essentially) taken at random. In this application, the first condition was an explicit, but plausible assumption, and the second condition was achievable by the researcher!

When this mathematical result is ported over to the applied statistics context, and applied to observational data, the first assumption is more dubious and the second condition is flat out preposterous! As such, with inapplicable theory behind it, the LASSO isn’t any better than older heuristic approaches such as forward selection, which are more straightforward to motivate and teach and which exhibit comparable empirical performance.

Unreliable asymptotics. "Causal random forests” is a prominent recent example of asymptotic theory that can’t be cashed out in practice. This hugely influential paper made a splash for being the first to furnish confidence intervals (i.e. “inference”) for treatment effect estimates arising from non-linear machine learning models (specifically, a version of random forests). However, simulations with straight-forward data generating processes reveals that the finite-sample performance of the method was not even remotely close to the nominal asymptotic coverage (sometimes as low as 50% coverage on a nominal 95% interval). To be sure, the theory surrounding causal random forests is interesting in its own right, but it should not be taken in any way as an endorsement to use those intervals in practice. (Incidentally, a famous LASSO-related result also falls into this inapplicable asymptotics category: Poetscher and Loeb wrote a number of articles pointing out that the so-called “oracle property” of the adaptive LASSO was non-uniform, meaning that the necessary sample sizes for the result to hold could be arbitrarily large.)

Unrealistic assumptions about the method. An especially common form of a methodological false virtue is when theoretical development persists on simplified versions of a method simply because the simpler thing admits to theoretic study. This mis-match can cut both ways. On the one hand, it means that a theoretical result may not be about a method that is actually being used. For example, a result might be about the case where the variance is assumed known, when in practice it never is. Or it may be assumed that the model is linear because “nonlinear functions are just linear models with the appropriate interaction terms included”. Or maybe the theoretical result applies for a fixed regularization parameter, whereas in practice the regularization parameter is determined empirically via a resampling or data splitting method such as cross-validation.

On the other hand -- and probably worse -- you may have empirical researchers avoiding more sophisticated methods because they are compelled professionally to stick to methods for which there is theory that can be cited. Until quite recently (a decade or less, I would say), some subfields of applied economics could not get away with analyzing their data with anything but linear models for lack of theory. My esteemed colleague Rob McCulloch once quipped that restricting the models you use to the ones you have formal theory for is like riding a bicycle instead of a car on the grounds that you don’t know how to fix the car yourself. But note the irony: the inapplicable theory from the Causal Random Forests paper had the net positive that it gives empirical researchers a bogus license to use a method that was subject to an equally bogus prohibition. You might say that an insistence on formal theory incentivizes counterfeits.

Non-constructive theorems. Yet another way that a theoretical result can be impracticable is if it is fundamentally non-constructive. For example, a fascinating result by Wenxin Jiang shows that boosting algorithms are capable of overfitting (contrary to some folklore), but goes on to show that somewhere along the path towards overfitting, the optimal prediction is achieved. I personally find this result fascinating and reading the paper was edifying, but it’s a good example of a result that is fundamentally non-actionable.

Unrepresentative empirical evaluations

The simulation studies of the causal forest method above were sufficient to show the inadequacy of the theory because the coverage rates should not depend on the underlying DGP. But conversely, a method that performs exceptionally well on a single simulation study does not earn much bragging rights. Virtually all methodology papers these days contain a simulation study and it should surprise no one that the new method always seems to shine! A simulation study is only as valid as its data is truly representative of practice.

Similarly, the field of machine learning has embraced a relatively small number of easily accessible and, hence, horribly overused benchmark data sets. To take a famous example, the MNIST data set of handwritten digits was introduced by Yann LeCunn in 1994 and has been used thousands and thousands of times to evaluate this or that modification of popular supervised learning methods. The current state-of-the-art has an astounding accuracy that is nearly flawless (99.8% accuracy) and substantially above human-level performance (96%). As far as I am concerned, these demonstrations mainly prove to me that a given method is really good at the MNIST data, and perhaps that the MNIST data ought to be retired at this point.

Novelty for its own sake

Methodologists are compelled to create new methods, both out of sincere intellectual curiosity as well as for more mundane reasons like fulfilling career ambitions. The result, sometimes anyway, is the creation of methods in need of an application. Methods researchers, especially young researchers, are often more interested in seeing if something can be done than considering whether doing so would be useful to anyone (other than their resumes). It is much easier to tweak an existing method -- to minimal practical effect -- than it is to tackle the harder problems, the fruit hanging halfway up the tree, as it were. These incremental advances are not infrequently accompanied by overreaching claims about superiority. Whereas some economists were admonished above for clinging to the tradition of linear models long past when promising alternatives like random forests were available, some data scientists often reach immediately for the deep neural network when a logistic regression would probably do. Riding a bike instead of a car is stubborn in one way, using a Lamborghini as a family sedan is another kind of misjudgement.

CONCLUSION

It may seem to a reader that this essay started out with a call for empathy and understanding and midway through had a change of heart and reverted to finger pointing. But although the tone change was real, from sympathetic to scolding, I believe the logic to be consistent. The point I am trying to make, in both sections, is that methods should be judged by their usefulness for analyzing data. Methodologists who do not believe their work should be judged by its usefulness to data analysis should be forced to announce it in their abstracts and social media posts. In the first part of this essay, I pointed out that it was unfair to criticize a method for not being good at a task for which it wasn’t designed or intended. The second part of the paper took that same claim and turned it around: a method should not be embraced and widely-deployed on the basis of solving problems other than the ones its ostensible users actually face.

I once spoke with a highly-regarded time series researcher who has done consulting work for the Federal Reserve. He nonchalantly explained to me that the methods he used in his consulting work and the methods he published comprise mutually exclusive sets. He was not lamenting this -- the claim was not that the Fed was missing out on the good stuff. Rather, the published stuff simply wasn’t appropriate for applied work and even novel methods that were invented for practical applications weren’t suitable for publication as a matter of academic fashion. As a young, optimistic new methods researcher, I found this heartbreaking. Was the whole field merely lip-service? Are our theorems just mathematical rosary beads? Is developing a popular method more important than developing a principled one? I don’t claim to have answers to these questions, but the more methodologists who ponder them the better for the integrity of the field.

Introductory/survey

Philosophy of Science: A Very Short Introduction. This slim volume captures the spirit of philosophy of science in an accessible but rigorous way — Okasha has produced a small masterpiece.

Philosophy of Science: The Central Issues. An anthology is a good way to get to know an area of philosophy, as the very nature of the field invites disagreements and nuance. As hefty as Okasha is concise.

Seminal

An Enquiry Concerning Human Understanding. The one that started it all (IMO). Hume perceived the major paradoxes of learning from the world and his insights will still be fresh for many readers today.

Logical Positivism (not fashionable, but still worthwhile)

Language, Truth, and Logic. A bold, engaging statement of the logical positivists’ program.

Tractatus Logico Philosophicus. The OG hipster philosopher, this book is later disavowed by its author (see below), but still has many memorable and provocative ideas, such as its famous final sentence: “Whereof one cannot speak, thereof one must be silent.”

Probability, Statistics, and Truth. A pioneer wrestling with the contradictions of his subject.

Beyond Logical Positivism (aka, science is hard)

Empiricism and The Philosophy of Mind. Wildly under-appreciated. Your favorite philosopher’s favorite philosopher’s favorite philosopher.

The Structure of Scientific Revolutions. Science progresses one funeral at a time.

Philosophical Investigations. Gnomic, but brilliant. This book probably changed the way I think about the world more than any other single book.

The Logic of Scientific Discovery. Popper was well aware of the troubles with naive falsificationism: refutability is necessary but not sufficient for sound scientific inquiry.

Fact, Fiction, and Forecast. Famous for its “New Riddle of Induction”: Even if the past is like the future, in what respect(s) will it be so?

“Contemporary”

Inference to the Best Explanation. What even *is* an explanation?

Error and the Growth of Experimental Knowledge. A robust and programatic defense of frequentism.

The Logic of Reliable Inquiry (Kelly). The intersection of epistemology and computability theory. Super cool stuff.

Probability and Inductive Logic. I tried using this as a textbook for a business statistics class one year. Live and learn.

Special Topics

Philosophical Foundations of Neuroscience. More people should read this in the age of modern LLM-based AI. Its core message: brains (cf. computers) don’t think, whole people do.

Philosophy of Physics: Quantum Theory. This area of contemporary philosophy has no consensus, which makes it exciting to read, especially from a vigorous and opinionated thinker like Maudlin.

Physics and Chance. Quantum physics: I’m the trickiest area of physics, conceptually. Statistical mechanics: Hold my beer

.

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Often when I post on social media about using machine learning to estimate heterogeneous treatment effects, someone shows up in the comments to explain to me why I’m wrong. Sometimes it’s because genomics-based personalized medicine has been an abject failure and it is expensive. Sometimes it’s because they think n-of-1 trials are superior for personalized medicine.

I find these exchanges frustrating because I agree with them 100%. I’m a vocal opponent of the hype around “digital twins” in clinical trials and personalized medicine. I do not think we understand most diseases well enough to replace concurrent controls with synthetic patients, nor do I think a sufficiently elaborate model can reliably tell us what will happen to a particular person. I think genetics-first personalization is a dead end. I think n-of-1 trials are amazing and under-utilized.

So yes, CATE cannot do many of the things claimed for it. But I’m not one of the people making those claims. Saying CATE is useless because it cannot deliver certain knowledge about one patient is like saying cars are useless because they do a bad job of flying. I never said cars could fly.

By CATE I mean a conditional average treatment effect: an average effect among observations sharing recorded characteristics. Those characteristics can belong to a patient, such as tumor subtype, or to an occasion, such as a concurrent medication. In principle, CATE estimation can use either or both. But it remains an average. Conditioning more finely does not reveal what would happen to one specific patient under both treatment and control.

If we want to learn how a particular patient responds, a more direct tool is an n-of-1 trial.

What n-of-1 can and cannot do

An n-of-1 trial (cf. cross-over designs, switchback experiments, and within-subject designs) repeatedly exposes one patient to different treatment conditions, ideally in randomized and blinded periods. The patient serves as their own control. Challenge–dechallenge procedures and dose titration can sometimes function as quasi-n-of-1 experiments, although they usually have fewer controls.

These designs work best when outcomes are repeatedly measurable and treatment effects are reversible. Blood sugar is a natural example. Mortality is not: a patient cannot die under treatment, wash out, and cross over to control. N-of-1 trials are therefore powerful within a limited domain. I discuss their uses at greater length in Mean Medicine.

Even within that domain, saying that an n-of-1 trial estimates “the individual treatment effect” is shorthand. A person’s response can vary across occasions because the context changes. An n-of-1 trial estimates a persistent patient-level response by averaging over those occasions; it does not necessarily uncover a perfectly fixed effect carried around by the patient. Repeated periods also cannot show treatment and control on the same occasion, so counterfactual ambiguity persists. I develop that distinction in a separate note, Stable and Stochastic Components of Treatment-Effect Heterogeneity.

This qualification cuts both ways. If stable differences between people dominate, individualized treatment is highly promising. If occasion-to-occasion variation dominates, a baseline personalization algorithm will have limited predictive power. N-of-1 trials can help us learn which situation we are in.

What CATE is for

CATE, to my mind, answers a fundamentally different question. Its main scientific value, I believe, is not direct personalization but rather pattern discovery. If patients with a particular phenotype respond differently, that is a clue about mechanism. If the same patients respond differently under different circumstances, that is a clue about context. Neither kind of modifier must itself be causal. A modifier tells us where to look; it does not tell us what we will find.

Another way to say it is that CATE serves an essentially exploratory role, which means that subgroup patterns should not be presented as established findings merely because a model flagged them. But that does not mean we should refuse to look! A prespecified analysis can answer a trial’s confirmatory question, after which the same data can generate questions for future studies. I make the longer case for this sequence in Popper versus Tukey and the Battle for the Heart of Statistical Data Analysis.

A story (that I’ve told before) about laboratory mice illustrates both points. After an NIH animal room was refurbished, hexobarbital sedation suddenly lasted 16 minutes rather than 35. Investigators traced the change to red-cedar bedding, which increased the activity of drug-metabolizing enzymes. Bedding was an occasion-specific effect modifier: it changed the treatment context, not the type of mouse. Had a model identified cage assignment instead, that variable would have been a useful proxy rather than a cause. Either way, the pattern would have supplied a question rather than an answer. The original Science report gives the experimental details.

The mice also illustrate why rich measurement matters. No one could have solved the mystery without knowing that the environment had changed. Human trials likewise need enough patient and occasion-level information for unexpected patterns to become visible. To emphasize: this information need not be in the form of expensive and causally distant genotype information, but can be mundane and more causally proximate phenotype information such as immune status or dietary intake.

Why pooling n-of-1 trials helps CATE

CATE and n-of-1 are therefore not competing approaches. Better still, they can help each other.

Suppose we conduct a coordinated series of n-of-1 trials. To the extent that each trial estimates an idiosyncratic patient response, that response no longer sits in the pooled data as unexplained noise. A CATE analysis can then look more efficiently for systematic patterns associated with patient-specific variables or treatment occasions. In plain language, n-of-1 trials can denoise the data before we ask what generalizes.

Repetition also makes a temporary fluctuation less likely to alias a stable patient difference. A pooled analysis can borrow information across patients without pretending they are identical. This does not resolve the usual problems of carryover and unobserved counterfactuals, which may be impossible for certain treatments. But where repeated switching makes sense, CATE analysis of pooled n-of-1 data is about as good as it gets.

A single n-of-1 trial can help choose treatment for one patient. Pooling many of them can help explain why patients and occasions differ—and can give a future patient a more informed starting-point.

BiDil: a question left unanswered

The story of the heart disease treatment (drug combination) BiDil shows what CATE can contribute and also illustrates why it often doesn’t live up to its scientific potential in practice.

In the 1980s and 1990s, the V-HeFT trials studied hydralazine plus isosorbide dinitrate (BiDil) for heart failure. The combination therapy did not provide a convincing benefit compared to another drug, enalapril and was therefore not approved by the FDA. However, a subsequent re-analysis of the trial data showed a statistically significant survival benefit for black patients (Racial Differences in Response to Therapy for Heart Failure).

That observation prompted the African-American Heart Failure Trial, which enrolled self-identified Black patients and compared fixed-dose hydralazine–isosorbide dinitrate with placebo (in addition to standard therapy for both groups). Mortality was 6.2% with the drug combination and 10.2% with placebo, and the trial was stopped early for patent benefit. In 2005, the FDA approved BiDil for self-identified Black patients with heart failure.

Combination of Isosorbide Dinitrate and Hydralazine in Blacks with Heart Failure

Some might see this story as a direct vindication of CATE exploration. And, narrowly, it was a clinical success. However, I contend that it was in a larger respect a scientific failure. They didn’t pursue the pattern far enough. A-HeFT established benefit in the population it enrolled; it did not establish why race predicted comparative response in the earlier data. Was self-identified race marking nitric-oxide biology or some feature of treatment context, perhaps mediated by lifestyle? The question was not resolved — it wasn’t even seriously entertained. A proxy was operationalized rather than explained. What the FDA saw as actionable evidence, I see as squandered opportunity for scientific discovery.

A heterogeneous treatment pattern is a surprising fact. A scientific program should then collect the information and run the studies needed to make it unsurprising (Cf. Peirce on abduction). CATE is useful not because demographic subgroups are satisfying endpoints, but because they may lead us toward better causal understanding.

A missing middle

Drug research often separates molecular theory from empirical efficacy. One group studies targets; another asks whether a treatment moves a primary endpoint in an explanatory trial. Comparatively little work connects treatment response in actual patients back to a detailed account of how a drug works.

Pharmacometrics is a partial exception because it uses repeated human measurements to learn about dose and response. A larger role for pharmacometrics and pooled n-of-1 designs would strengthen this middle level of science.

N-of-1 trials remain a direct route to personalization when repeated experimentation is possible. CATE estimation remains a route to identifying systematic patterns that might generalize. Neither substitutes for the other. Used together, they can help patients now while building knowledge to benefit those in the future.

All too often, the discourse about randomized controlled trials looks like an intractable rivalry between two tribes, the RCT-or-bust tribe and the RCTs-have-critical-flaws tribe. The former brook no criticism and look down their noses at the poor misguided souls who don’t see the obvious superiority of RCTs over virtually any other method, and the latter decry the imperfections of RCTs without offering much in the way of constructive alternatives. The cause of the impasse is simple enough: RCTs are simultaneously superior to alternatives and inadequate by themselves to move science forward. RCTs are necessary but not sufficient. To the extent that the first group implies that RCTs are sufficient, they are wrong; to the extent that the second group suggests that RCTs are unnecessary, they are wrong. Conversely, the first group is right that RCTs are necessary and the second group is right that RCTs are insufficient. Which group speaks to you has to do with whether you are more struck by the great strengths of RCTs relative to alternatives or the ways in which they fall short of answering the questions that matter to you most.

With this starting point in mind, this essay takes a small step towards a detente by seeking a better understanding of the necessity of RCTs and why specifically they almost always fall short of being sufficient.

In the first place, the key point is that RCTs are demonstrations of effectiveness in at least one situation (the one defined by the study itself). They do not — despite it frequently being stated as such — prove that a drug works “on average”. This misconception (of which I was myself, until recently, guilty) is a source of a lot of talking past one another. Part I explores several classic papers on this theme throughout the years.

In the second place, RCTs are often mere demonstrations of effectiveness in that they do very little in and of themselves to illuminate the reasons why a drug (or policy, etc) is effective, which, as a consequence, limits our ability to say much about the specific situations where a drug will work well or only a little bit or not at all or even do harm. For critics of RCTs this lack of generalizability looms large; many defenders of RCTs read this criticism (wrongly) as suggesting that RCTs should be abandoned.

Before reading on, note that I do not cover the main strength — indeed, superpower — of RCTs here, which is their ability to handle the confounding that otherwise plagues observational studies. For that, I recommend any introductory text on causal inference, but I’ll single out some course notes of my own and Stephen Senn’s explanation over at Deborah Mayo’s Error Statistics Blog. Likewise, I do not cover the history of RCTs, for which I recommend Robert Matthews three part article (part 1, part 2, part 3).

A common confusion regarding what RCTs actually accomplish.

Sometimes people talk about randomized controlled trials as if they were experiments. Sometimes they talk about them as if they were surveys. They are, in part, both. Schwartz and Lellouch (1967) called attention to these two roles, calling them “explanatory” and “pragmatic”, respectively.

“The first [type of trial] allows us to compare two groups which are alike from the [theoretical] point of view and which differ solely in the presence or absence of the drug. It therefore provides an assessment of the sensitising effect of the drug and gives valuable information at a biological level. The second [type of trial] enables us to compare two treatments under the conditions in which they would be applied in practice. We distinguish the two procedures as stemming from two different approaches to the trial, the first explanatory, the second pragmatic.”

The survey versus experiment terminology is due to Longford and Nelder (1999):

“[Consider] the impact of the population treatment heterogeneity on the validity of clinical trials. We conclude that a clinical trial should be regarded not only as an experiment, but also as a population survey, with the recruitment process governed by a haphazard sampling design. We do not advocate employing any probabilistic control (such as in simple random sampling), but point out that the lack of control over the recruitment process is a potential source of bias, more serious the greater the extent of treatment heterogeneity.”

Kravitz, Duan and, Braslow (2004) expand on this distinction.

“Longford and Nelder (1999) characterized a clinical trial as an experiment and a survey rolled into one. Although randomized controlled trials (RCTs) usually are good experiments, they often are poor surveys. A good survey sample is representative of the target population, so that the parameters estimated in the sample can be generalized to the target population. By convenience, RCTs are usually characterized by narrow inclusion criteria and recruitment. Under these conditions, the heterogeneity of treatment effects may be dramatically underestimated, and even assiduous investigators can be misled into thinking that their results are more generalizable than they actually are.”

(Spoiler: in the following section I will argue that many RCTs are often bad experiments as well.)

Many debates about RCTs stall out when one of the discussants thinks the RCT should be doing the work of a survey and the other discussant believes it should be thought of as an experiment. Most people working on RCTs in industry think of them as experiments. As a result, proponents of the experiment point-of-view will use that perspective as defense against the claim that typical parallel groups RCTs merely estimate average treatment effects. “No, no, they say, it isn’t an average. It’s an experiment.” It sounds like an airtight alibi, but really it’s a little like arguing that the patient can’t possibly be sick because he’s dead. The critique was that perhaps the individual patient in question isn’t well-represented by the average that the RCT estimated. That critique is not avoided by the claim that the study population is, in fact, unrepresentative of any population whatsoever. Put another way, “the average might not be good enough” is a statement that worries about lack of generalizability (from the study to an individual) due to latent heterogeneity of the treatment effect (i.e. the drug works differently for different people). The fact that the RCT was run on an idiosyncratic population means that lack of generalizability might be a problem even if the treatment effect were homogeneous in the target population. The defense actually confesses that the situation is potentially worse than imagined by the initial criticism.

In any event, average versus individual, it turns out, is a red herring. The true issue is one of internal versus external validity. But — and this is a major caveat — non-generalizability is also a weakness of any other kind of empirical study, of course (cf. Gelman’s comments here ). So it isn’t a unique weakness of RCTs and not a reason to abandon them.

Statisticians Stephen Senn and Frank Harrell both approvingly quote Yates and Cochran (1938) at length:

“Agronomic experiments are undertaken with two different aims in view, which may roughly be termed the technical and the scientific. Their aim may be regarded as scientific insofar as the elucidation of the underlying laws is attempted, and as technical insofar as empirical rules for the conduct of practical agriculture are sought. The two aims are, of course, not in any sense mutually exclusive, and the results of most well-conducted experiments on technique serve to add to the structure of general scientific law, or at least to indicate places where the existing structure is inadequate, while experiments on questions of a more fundamental type will themselves provide the foundation for further technical advances.

…At present it is usually impossible to secure a set of sites selected entirely at random. An attempt can be made to see that the sites actually used are a “representative” selection, but averages of the responses from such a collection of sites cannot be accepted with the same certainty as would the average from a random collection.

On the other hand, comparisons between the responses on different sites are not influenced by the lack of randomness in the selection of sites (except insofar as an estimate of the variance of the response is required) and indeed for the purpose of determining the exact or empirical natural laws governing the responses, the deliberate inclusion of sites representing extreme conditions may be of value. Lack of randomness is then only harmful insofar as it results in the omission of sites of certain types and in the consequent arbitrary restrictions of the range of conditions. In this respect scientific research is easier than technical research.”

This quote is eminently reasonable, but it is not the exoneration of typical RCTs that Harrell and Senn seem to take it to be. The critique is precisely that, as commonly conducted, RCTs absolutely do “result in the omission of sites [patients] of certain types” and therefore have “arbitrary restrictions on the range of conditions”! Likewise, if we suspect heterogeneity, we should care about “an estimate of the variance of the response” in the actual population. This is one way that science progresses; we want to be able say under what conditions different treatments will work. We’ve learned well when our subpopulations have approximately homogeneous effect and heterogeneity between them. That ability to assort is certification of the science. The precision of our groupings marks the gradation between knowing that versus knowing why.

To be sure, sussing out precise sub-populations may not be possible in some cases. But we should still try to look for them. That science works at all is sort of miraculous, but we didn’t learn what we know today by not trying to figure the world out on account of we might fail. I’m not exactly sure where this idea of needing guarantees of success before proceeding (I guess because science is increasingly expensive). Lou Lasagna put it well:

“[I]t’s a pity that we don’t have more naturalistic studies, because the clinical trials, randomized clinical trial, while wonderful for giving you reliable information on whether you have a drug that’s worth studying, is such a hothouse approach to life with, you know, screened patients and informed consent and fairly expert researchers – and then the drug is marketed. Everything changes. You have unscreened patients, physicians of varying talents and experience, multiple drugs often being involved, multiple diseases…”

Note that what Lasagna calls “naturalistic studies” are what Schwartz and Lellouch called “pragmatic trials” and what Longford and Nelder called “surveys” and what Yates and Cochran called “technical”. In contradistinction to “explanatory trials”, “experiments”, and a “scientific” approach, respectively. In other words, Lasagna concedes that most RCTs are being run in “explanatory”, “experimental”, or “scientific” mode, which he refers to, by analogy, as a “hothouse”. Similarly, Nicholas Lewin-Koh refers to RCTs (done in this mode, which is typical) as “wind tunnels” — acknowledged approximations to real world use, but hopefully not in ways that are importantly different (but which may be).

To recap, when critics decry the limitations of RCTs in medical research, they often phrase these criticisms in terms of averages. But that is not how trialists actually think of their own work, which makes the critique easy to dismiss. But if one reads carefully, what the critiques are lamenting is that RCTs are often weak as experiments. When the critics say “averages do not provide reasons” the mention of averages isn’t the key thing, the lack of reasons is.

The actual criticism: RCTs often show that a drug works without speaking to why it works.

Demonstrating an effect in the study population is not enough to provide a reason, regardless of whether or not the study participants are representative in the sense of a survey. You need to be able to say if the effect would work in other groups and which other groups and in what circumstances and why. Attacking the inadequacy of the average was a rhetorical mistake that is too easy to dismiss, when the real objection is the lack of explanatory power, which is far harder to dismiss. We will now look at several extended quotes through this lens, intentionally ignoring mentions of “averages” or “statistics” and focusing on the inability of typical efficacy RCTs to illuminate mechanism.

“A great surgeon performs operations for stone by a single method; later he makes a statistical summary of deaths and recoveries, and he concludes from these statistics that the mortality law for this operation is two out of five. Well, I say that this ratio means literally nothing scientifically and gives us no certainty in performing the next operation; for we do not know whether the next case will be among the recoveries or the deaths. What really should be done, instead of gathering facts empirically, is to study them more accurately, each in its special determinism. We must study cases of death with great care and try to discover in them the cause of mortal accidents, so as to master the cause and avoid the accidents. Thus, if we accurately know the cause of recovery and the cause of death, we shall always have a recovery in a definite case. We cannot, indeed, admit that cases with different endings were identical at every point. In the patient who succumbed, the cause of death was evidently something which was not found in the patient who recovered ; this something we must determine, and then we can act on the phenomena or recognize and foresee them accurately.

But not by statistics shall we succeed in this ; never have statistics taught anything, and never can they teach anything about the nature of phenomena. I shall further apply what I have just said to all the statistics compiled with the object of learning the efficacy of certain remedies in curing diseases. Aside from our inability to enumerate the sick who recover of themselves in spite of a remedy, statistics teach absolutely nothing about the mode of action of medicine nor the mechanics of cure in those in whom the remedy may have taken effect...I do not therefore reject the use of statistics in medicine, but I condemn not trying to get beyond them.”

Claude Bernard (An Introduction to the Study of Experimental Medicine, 1865)

“The statement that a solution of iodine in KI makes starch paste blue in 75 plus or minus 1.5 percent of samples examined will not commend itself to a chemist. He will wish to know what impurities or what range of pH values, etc, determine when the reaction does or does not occur. Such has been the attitude in which physiologists have hitherto undertaken the investigation of animal behavior. If we abandon it, we are lowering our standards. “

Lancelot Hogben (Statistical Theory: The Relationship of Probability, Credibility, and Error, 1968)

“[RCTs are] better than giving a new drug to a bunch of doctors and saying, “Play around with it and tell us what you think”…[But] in a sense we’ve sort of oversold, and I’m partially responsible for that, because I was trying to get them to do it at all. And now, with the passage of time, I’ve also become more sophisticated. I still feel that [RCTs are] the way you’ve got to start out. What I object to is ending with that…the goal of therapeutics ought to be individualization, not homogenization and yet we’ve done very little in that regard.”

Lou Lasagna (Interview, 1995)

“In the case of a new drug, it is usual to describe the patient population for which the drug is suitable. However, this specification may be quite general. We know the drug’s benefits and the risks might vary according to individual characteristics, but lack a theory or sufficient data to determine any ‘recognizable subsets’ of the general population. So, we default to the main effect in the hope that it provides the best guidance for the clinician until and unless we can determine otherwise.

The fundamental flaw in this logic is the implicit assumption that the context is only weakly relevant…However, for most of the events or properties studied today in the biomedical or social sciences, the causal processes involve complex interactions between the individual and the environment. For instance, a new medication to control the progression of diabetes or heart disease can hardly be expected to have the same impact on all individuals…In this light, the main effect may not necessarily be a first-order conclusion subject to possible further refinement; it may be virtually meaningless! Moreover, if the main effect happens to be weak or nonexistent, potentially fruitful research to identify individual differences may be abandoned prematurely

The conventional wisdom at the moment is to focus primarily on main effects because that is the best we can do, at least for now…When the contextual information is limited or weakly relevant, statistical information is indeed very difficult to beat. But it is a mistake to assume that there are no relevant subsets just because we cannot recognize them at present.’’

Herbert Weisberg (Willful Ignorance: The Mismeasure of Uncertainty, 2014)

As all of these quotes eloquently explain, the key problem with RCTs — specifically those designed narrowly for approval — is that many people seem to have mistaken the minimal amount of evidence for the very pinnacle of evidence. When regulatory approval is the goal, “explanatory” trials potentially offer no explanations! Note the irony: they are neither explanatory (scientific) nor pragmatic (technical). They are “proof of concept” under “ideal” conditions. Which is super important! But, conceptually speaking, it is a fairly low bar. As Hardie and Cartwright say in “Evidence-Based Policy” from 2012: “’[I]t worked somewhere’ is just a starting point. It is a long road from ‘it works somewhere’ to the conclusion you need—‘it will work here,’ and it is not an easy one to traverse.”

Now, strictly speaking, evidence of heterogeneity is not the same thing as an understanding of mechanism. Indeed, a patently silly approach to individualization would be to run ever more massive RCTs in a brute force effort to isolate subgroups who respond to treatment differently, perhaps via more complicated cross-over designs or by intentionally enrolling an extreme diversity of patients. But this naive approach has the same flaw that is being ascribed to run-of-mill parallel groups approval studies: there is no route to extrapolation. In this, people have got my own advocacy for seeking conditional average treatment effects exactly backwards. The goal is not to definitively establish distinct subgroups via the same austere method by which we demonstrate effectiveness in a less diverse study. Rather, it is that patterns we spot in how different patients respond to treatment are suggestive of mechanisms, which provide an avenue to legitimately valid extrapolation. We don’t want to prove heterogeneous response case-by-case, rather we look to heterogeneity for clues to an understanding that would make case-by-case demonstrations unnecessary! You must first notice that black patients respond different than white patients in order to ask why and with the understanding of why you may deduce that it will work or not for this or that other group without running a costly, dedicated trial.

But, if RCT’s are only the first part of the puzzle — the edge and corner pieces, if you will — who fills in the middle? Lou Lasagna again gets this right:

“I think that one of the things that we could be doing is more what I call naturalistic studies. The drug is on the market. Okay. Now, just track how it’s performing. Just how happy are doctors as they -– as the doctor compares personal experience with what the randomized control trial data said and what the labeling says. Are they synchronous or are there big discrepancies? And if there’s a discrepancy, can you explain it? Now who should be doing those studies? Well, I suppose the sponsor ought to be at least interested in the phenomenon. But they tend not to be, and up until now, companies have usually been blissfully happy if they have big sales.”

Put in modern terms, Lasagna is stumping for the importance of “real world evidence” (RWE) — not as a replacement for RCTs, but as an indispensable supplement to them.

Meanwhile, trials could be designed to investigate mechanism, making them “explanatory” and “scientific” in the senses that those words were originally invoked by Schwartz and Lellouch and Yates and Cochran. But appetite for such studies is not what one may wish. See here from the National Institute for Health and Care Research (NIHR):

The Efficacy and Mechanism Evaluation (EME) Programme is jointly funded by NIHR and the Medical Research Council. It primarily supports clinical trials and other research studies that test the efficacy of an intervention. The intervention(s) must have the potential to improve patient care or benefit the public. EME also supports hypothesis-driven studies looking to show how an intervention works (the mechanism(s)).

Efficacy asks the question “does the intervention work in a defined human population?” Mechanism is an assessment of how an intervention works. Assessment of mechanism must be driven by a hypothesis.

— Most of the proposals supported by the EME Programme test the efficacy of an intervention.

— Some of these efficacy studies include mechanism studies testing how the intervention works.

— A small number of applications only test the mechanism of an intervention.

Importantly, applications to the EME Programme do not have to contain mechanism.

Despite having “mechanism” in the title of the program, they go out of their way to remind everyone that applications to the program do not have to contain a mechanism!

Of course, not everyone is content with showing “that” rather than “why”. A paper published in the European Journal of Physiology this year titled “First-in-human to proof-of-concept: why experimental medicine studies remain essential in human physiology and drug development” makes the case for mechanism-focused trials:

Experimental medicine studies, small, mechanistically focused investigations, have historically driven key discoveries in human physiology and pharmacology. Despite their foundational role, these studies are increasingly marginalised in today’s drug development environment due to economic pressures, regulatory conservatism, and an overemphasis on statistical endpoints from large-scale trials…Integrating mechanistic insights with statistical power is not superfluous, but essential, particularly in complex diseases like CKD where understanding why and how interventions work may matter as much as whether they do. We acknowledge that achieving this vision necessitates overcoming significant structural, economic, and cultural barriers within the current drug development environment; however, the costs of inaction, manifest as trial failures, patient harm, and missed therapeutic opportunities, are potentially much greater.

Unsurprisingly, the paper starts out with a quote from none other than Claude Bernard.

Bernard, C. (1927). An introduction to the study of experimental medicine (H. C. Greene, Trans.). Macmillan. (Original work published 1865).

Cartwright, N., & Hardie, J. (2012). Evidence-based policy: A practical guide to doing it better. Oxford University Press.

Hogben, L. (1968). Statistical theory: The relationship of probability, credibility, and error. W. W. Norton.

Kravitz, R. L., Duan, N., & Braslow, J. (2004). Evidence-based medicine, heterogeneity of treatment effects, and the trouble with averages. The Milbank Quarterly, 82(4), 661–687.

Lasagna, L. C. (1995, September 8). Interview by Marcia L. Meldrum [Oral history transcript]. History of Pain Collection, University of California, Los Angeles.

Longford, N. T., & Nelder, J. A. (1999). Statistics versus statistical science in the regulatory process. Statistics in Medicine, 18(17–18), 2311–2320.

Schwartz, D., & Lellouch, J. (1967). Explanatory and pragmatic attitudes in therapeutical trials. Journal of Chronic Diseases, 20(8), 637–648.

Unwin, R. J., Challis, B., Wagner, C., Capasso, G., & Carlsson, S. (2026). First-in-human to proof-of-concept: Why experimental medicine studies remain essential in human physiology and drug development. European Journal of Physiology, 478, Article 53.

Weisberg, H. I. (2014). Willful ignorance: The mismeasure of uncertainty. Wiley.

Yates, F., & Cochran, W. G. (1938). The analysis of groups of experiments. The Journal of Agricultural Science, 28(4), 556–580.

“The social acceptance of a knowledge claim always serves to benefit certain interest groups in the society and to disadvantage others”

— STEVE FULLER, Social Epistemology

More specifically, both books detail the various ways that the current equilibrium between doctors who practice evidence-based medicine, the FDA, and the drug-making industry can hinder the very production of high quality information about drugs and their side effects. Where Avorn and Goldacre (from the previous installment) are concerned with patient safety and cost directly, Abramson and Healy (and yours truly) are concerned with the distortion of science, as a process, which in turn can have profound downstream consequences for patient safety and health.

One of the main lessons of these two books is that one doesn’t have to believe that drug-makers are greedy, callous, or unscrupulous to believe that they presumably need more than altruistic incentive to conduct extremely costly randomized controlled trials. That said, there’s also no reason to suppose that the sort of evidence that is best for business looks anything like the sort of evidence that is best for individual patients or for long-term scientific progress. The egregious cases get the most attention, of course, as when a neurologist remarks of Neurontin in Sickening “There is no other drug being used to treat so many different conditions with so little benefit.” But compromised evidence comes in many shades, and one wonders on the basis of the extreme cases what exaggerations and misrepresentations go widely unnoticed.

The main strength of Abramson’s book is its organization and straightforward writing. In fact, in his acknowledgments, he writes “my editor…remained unflinchingly committed to this project from the beginning. His response to the first draft of this manuscript was enormously encouraging — he expressed “admiration and gratitude” for my work. This was followed by an eleven-page single-spaced editorial memo that explained its deficiencies.” The editor put in good work; indeed, Sickening is particularly easy to read among books in this genre.

The specific examples covered by Abramson include Vioxx, Neurontin, statins, and insulin, for significant overlap with the books by Avorn and Stossel that I previously reviewed. He also pays special attention to the role of drug-maker marketing on the availability and interpretation of evidence. If I had to recommend only a single book on the broad topic of drug-makers’ impact on patient care it would probably be this one.

My personal favorite, however, might be Healy’s Pharmaggedon because of its rich exploration of historical matters. For example, it was from Healy that I first learned of the key role that Dr. Lou Lasagna played in the 1962 Kefauver-Harris amendments:

“The third medical requirement of the 1962 amendments was that companies demonstrate their products worked in well-controlled clinical trials. This was smuggled into the final bill through the efforts of Louis Lasagna, a professor of pharmacology and a believer in controlled trials, who was attempting at the time to encourage some use of controlled trials, rather than trying to make them mandatory. Lasagna himself had undertaken the only controlled trial of thalidomide ever done, through which it sailed—an effective hypnotic free of significant side effects.”

This is notable because I had come across Lasagna’s work on the placebo effect in my research activities as well as a more-than-passing familiarity with the famous Kefauver-Harris law, but had not previously known that the two were related. I subsequently went on to learn much more about Lasagna’s career and thinking, which I will write about in the future.

Like Sickening, Pharmageddon devotes a good deal of time to the role of marketing and how it influences doctors and patients:

“Where the research and development budgets of large pharmaceutical companies like Lilly and Pfizer were once much greater than their marketing budgets, the reverse is now true. The pharmaceutical industry, for example, now spends $30 billion annually on marketing in the United States alone. ”

This shared focus again underscores the common epistemological theme.

Note that Pharmageddon bends towards psychiatric examples, as that is his Healy’s specialty. Also, I did find one substantive quantitative error in Healy’s book, which I wrote about elsewhere, but it does not undermine the larger narrative.

The weakest part of both books, unsurprisingly, are the concluding sections where authors feel obliged to propose solutions rather than merely point out problems. But the problems in this case might well be insoluble. Reliable scientific knowledge is not cheap to come by, deploying that knowledge in the clinic is not without risks, and any system we dream up would have their faults in practice. Nonetheless, I do think it is important to be clear-eyed about the limitations of our current knowledge systems, even if alternatives are not in sight, and readers of these two books will have the scales fall from their eyes regarding the ostensible irreproachability of evidence-based medicine.

PS I had planned to include here a longer exploration of my own thoughts on the role of industry-funded RCTs in establishing the evidence-based of modern medicine, but it grew to much longer than the original book reviews and came to include mentions of many additional books. So I’ve separated that out as a future essay.

Goldacre was a young physician from the UK, just 38 years old when the book was released. Three years earlier he had published his first book, Bad Science. Although he is a licensed physician, Goldacre seems to be a journalist first and a doctor second, and his style is broadly in the muckraking tradition. From the introduction: “The stories in this [book] go from antidepressants, through statins, cancer drugs, diet pills, and right up to Tamiflu.”

The title gives away the over-arching narrative: Drug companies are bad, doctors are good, patients are victims. This narrative goes down smooth, I think, because most people know and like a doctor or two, but almost no one knows a Mr. Burns-esque pharma CEO (moreover, if you murder one in the street it’s seen by some folks as basically okay). But, as the more scholarly accounts above show, this narrative isn’t entirely accurate, at least in terms of fully exonerating the doctors.

Goldacre’s main contention is that science as conducted by pharma is not transparent enough to count as true science. He argues that by cherry picking data and designing studies in a favorable way, drug companies can more or less manufacture the result they want. In all likelihood this is a gross overstatement — the drugs we have do seem to work, at least somewhat for some conditions. And most of the folks working in the industry genuinely believe they are working for the betterment of society. But on the count of whether or not science would benefit from less proprietary data and studies that are not narrowly designed to satisfy the demands of regulatory approval, I find that hard to argue with.

For me, one of the most memorable parts of Bad Pharma recounts Goldacre’s and others attempts to scrutinize the clinical trial data for the drug Tamiflu. Goldacre relates a maddening series of stall tactics on the part of the manufacturer, Roche, a pattern of delaying, then partially complying, and then repeating ad infinitum. A colleague of mine who works in the industry asserts that “the Roche critics made unreasonable demands regarding data-access” but I’m not sure what exactly was unreasonable. The data needs to be available, fundamentally, otherwise it isn’t science, or, at least, we don’t know that it is. I get that there are legitimate business reasons for not divulging the data, but those reasons are not good scientific reasons.

Briefly: Tamiflu was developed by Gilead and licensed to Roche. The FDA approved it in 1999 to treat uncomplicated flu, and later for prevention in some settings. It could shorten flu symptoms modestly (approximately one day shorter), but the larger public claims around it went further: that it might prevent serious complications, hospitalizations, deaths, or transmission during a pandemic. Governments bought huge stockpiles after fears about avian flu and later H1N1. The controversy erupted when independent reviewers — the Cochrane group and BMJ — pressed Roche to release the full clinical trial reports. Their 2014 review found that Tamiflu shortened symptoms only slightly and did not clearly show the big public-health benefits often claimed, while also causing side effects such as nausea and vomiting. The resulting litigation was not a mass injury case but a fraud-style case: Dr. Tom Jefferson (the lead of Cochrane’s Tamiflu report) alleged that Roche had misled governments into buying stockpiles. The U.S. government later declined to pursue the case and moved to dismiss it1.

A more recent, and less melodramatic, entry in this genre is “Rethinking Medications” by Jerry Avorn, MD. Dr. Avorn runs the Division of Pharmacoepidemiology and Pharmacoeconomics (DoPE) at Harvard University. With jacket blurbs by Paul Starr (see above), Eric Topol, and Mark Cuban, Avorn is a heavy hitter in this space, with Topol referring to him as “the conscience of the drug industry”.

Chapter 1 begins with the Aduhelm story. Aduhelm (aducanumab) was designed to remove amyloid plaques from the brains of people with early Alzheimer’s disease, motivated by the long-standing, now embattled, “amyloid hypothesis” — the idea that clearing amyloid might slow the disease. The clinical evidence was weak and conflicted. Two major trials were stopped early for futility; later, Biogen reanalyzed the data and argued that one trial showed benefit at a high dose, while the other did not. The drug also carried risks, especially brain swelling/bleeding. Avorn recounts: “The advisory committee agreed unanimously with the FDA’s statisticians that the drug didn’t help patients; not a single member voted for approval. Then, Janet Woodcock, the senior FDA official responsible for making the decision, overruled them all.”

By leading with this story Avorn lays his cards on the table. Broadly, I take his argument to be that if only the FDA would do its job — and were allowed to do its job — everything would be fine. Aduhelm is a story of regulatory failure, and that is where Avorn’s interests seem to lie, whereas Goldacre was more interest in frank moral scolding and Greene (from the previous post) was more interested in how market forces shape public conceptions of health.

Chapter 3 takes on the weaknesses of progression-free-survival as an appropriate endpoint for oncology meds. In short, progression-free-survival can seem to show a benefit without any associated benefit to survival nor quality-of-life. This is, to me, an interesting example because it is not clear who exactly is responsible for the flawed decision-making. I suppose Avorn feels the FDA simply oughtn’t allow companies to use such loosely validated proxy metrics. From the industry perspective it is clear why they are favored, or at least why no one internally is exactly clamoring for more soul-searching about if progression-free-survival is the “right” metric.

Several chapters feature the Vioxx saga prominently. Merck’s Vioxx was a pain and arthritis drug, approved by the FDA in 1999. It was part of a new class of drugs intended to reduce stomach bleeding compared with older anti-inflammatories. I was working as a pharmacy tech when Vioxx came out and I remember it flying off the shelves. But soon after approval, studies began showing a possible increased risk of heart attacks and strokes. Over time, evidence against Vioxx grew, including observational studies and Merck’s own later trial of Vioxx for colon-polyp prevention. In September 2004, Merck withdrew Vioxx worldwide after that trial showed increased cardiovascular risk. Litigation then exploded, with patients and families claiming Merck had failed to warn users soon enough. Merck fought many cases but eventually agreed to a multibillion-dollar settlement, and later paid a separate federal penalty over improper marketing. Vioxx became a landmark example of how a drug can look promising at approval, become widely used, and only later reveal serious risks that shorter pre-approval trials were not able— nor designed—to detect. Avorn gives a front row seat to the proceedings as he was a key witness for the prosecution, having published evidence on the cardiovascular risks prior to Merck pulling the drug — research Merck had certainly been aware of.

Again, Avorn’s emphasis is strikingly different than Goldacre’s — the narrative is not “drug companies are evil scoundrels”, but more “how could this have happened on the FDA’s ostensibly benevolent watch?” I don’t take it that Avorn is an industry apologist so much as he takes financial (dis)incentives to be so obvious as to be unworthy of condemnation; the fact that drug companies require profits to function is not, in his eyes, anything worth being scandalized over at this point in his career. How to prevent those incentives from harming patients is the only worthy question and the answer, in the main, is more effective regulations and, more specifically, sounder institutional governance (because the FDA does not come off blameless, as in its baffling approval of Aduhlem).

Goldacre reads like a young physician who has recently lost his naivety and wants to bring others into the seeing light to share his indignation; Avorn reads like the seasoned physician who is seeking real world solutions to real world problems.

And now, as Monty Python would say, for something completely different.

Coming to the defense of the pharmaceutical industry against all of us whiny ingrates is Thomas Stossel with his book Pharmaphobia: How the Conflict of Interest Myth Undermines American Medical Innovation. Whereas Avorn can be glossed as “if only the FDA would to do its job…”, Stossel’s counterpoint is “just stop meddling and industry would provide amazing drugs”. I suspect that these diametrically opposed narratives speak more to the authors’ underlying political belief systems than they do with the facts of the matter. In particular, they are plainly comparing the current state of the world to entirely different counterfactuals: what if drug companies were compelled to behave according to a wise, benevolent government versus what if beneficent drug companies were allowed to conduct their business unfettered by misguided meddlers? On balance, Avorn’s book is the more sober and balanced of the two; Stossel’s is frankly childish in the way it mounts an extended rhetorical attack on a movement — the “conflict of interest movement” — rather than directly approaching the question of “could drug development be more efficient in benefitting society”? As a result of this oppositional stance, the overall message comes across as “just be thankful we give you any scientific advances at all, the way you try to steal our profits from us.” The book was written while Stossel was a visiting scholar at the American Enterprise Institute.

Even Stossel’s analysis of the same stories as the other books come to opposite conclusions. On Vioxx he writes: “The never-ending mantra that ‘more research’ should precede product approvals and continue post- approval ignores that resources do not exist to pay for such research. And, it was Merck’s research attempting to extend Vioxx’s uses that finally established its adverse side effects definitively.”

Meanwhile, the concrete examples Stossel provides that are not in other books I also did not find compelling. For example, he relates how his brother-in-law Patrick had a gastrointestinal stromal tumor (GIST), initially removed surgically, which later recurred and became metastatic. A drug called imatinib (brand name Gleevec) was at that time being tested for GIST. Patrick entered a clinical trial, his pelvic tumor shrank markedly within months, later residual tumors were removed surgically, and Stossel reports that Patrick remained free of progression years later while continuing imatinib at an annual cost of $123,000, paid by insurance. Stossel uses his brother-in-law’s story with imatinib to argue against what he sees as a simplistic “public science discovered it, Novartis exploited it” narrative. He grants that academic science identified the mechanism underlying imatinib, but argues (correctly) that converting the basic science into a reliable and approved treatment was a costly and messy process and that the dramatic human benefit was not predictable until clinical trials were run. Stossel’s position boils down to a flat assertion that any steep markup should be treated as self-vindicating simply because a drug is medically valuable.

It isn’t that Stossel doesn’t make good points here and there, and he tells interesting stories from his years in the trenches at the interface of academia and industry. But his rhetorical style plainly telegraphs that his arguments are not in good faith; it is an unsubtle apologia for industry. He is looking to score points on some imaginary scorecard against perceived “enemies of industry”; I believe that, to some extent, the book was an outgrowth of “counterpoint” style op-eds that Stossel has published in major newspapers. Stossel’s book gives Ayn Rand, as the kids might say. (And I say that as a sometimes Ayn Rand apologist, incidentally.) One can imagine Stossell telling Goldacre to “grow up”.

Comparing Goldacre to Avorn to Stossell reminds me a bit of when someone lamenting some very real social ill is met with the claim that “the world is better off than it has ever been in terms of safety, health, and prosperity”; call it the Steven Pinker maneuver. It’s true, but it misses the point — we didn’t get to this apex of safety, health, and prosperity from people turning a self-satisfied blind eye to present-day ills.

Three of the books I read were proper history books. By this I mean that they are not directly putting forth an argument or any kind of call to action. Instead, they mostly make it their business to understand and present in detail the actual goings on that led to the modern day healthcare economy. These books describe the deeply symbiotic relationship between healthcare (broadly construed) and drug-makers, historically, conceptually, and politically.

Paul Starr’s The Social Transformation of American Medicine serves to remind the reader that physicians are not a group of altruistic public servants, but rather comprise a professional guild — a “sovereign profession” in Starr’s words — which actively seeks to protect both its economic fortunes and its broader societal influence. In particular, it must be remembered that medical doctors in the US organized to secure exclusive prescribing rights (on more than one occasion). We take the physician-prescriber model for granted now, but it is a crucial part of the Big Pharma backstory that could have gone a different way. This is neither good nor bad per se, but I find it helpful when assessing the present state of affairs to hold in mind two crazy facts: 1) tuberculosis accounted for one out of every four deaths in 1816, and one out of six deaths a century later and 2) Coca Cola used to have actual cocaine in it which you could buy at the corner store. That is the chaos from which the modern debates about Big Pharma emerged.

Starr tells the story of how American medicine evolved from an early hodgepodge of lay healers (purveyors of medicinal plants, midwives, self-care manuals authors) in addition to physicians. Over time, as sickness and its treatment became a larger business opportunity, physicians worked at, and succeeded in, displacing patent-medicine companies and other rivals to medical authority. The book spends a good deal of time analyzing the role of the Flexner report in “consolidating medical authority”. Control over pharmaceutical use was another big part of this power play.

In 1905 the American Medical Association formed the Council on Pharmacy and Chemistry, which evaluated drugs, controlled access to medical-journal advertising, pressured drug firms to stop public advertising, and promoted drug purchasing through physicians. In 1924, the AMA Council ruled that a drug could be denied approval if the drug maker earned much of its money from products that violated AMA guidelines. In 1938, with the passage of the Federal Food, Drug, and Cosmetic Act, the FDA began identifying drugs, such as sulfas, that “would require a prescription from a physician.” The unresolved boundary between prescription and over-the-counter drugs was subsequently settled by the 1951 Durham-Humphrey Amendment, which defined the kinds of drugs that could not be used safely without medical supervision and limited their sale to prescription.

This summary does not do the complexity of the evolving fault lines justice, however, as there were many forces at work shaping the landscape of medical care in the 1900s. For instance, we see a power struggle between doctors and public health agencies. Starr notes that the availability of effective antibiotics strengthened the cause of private clinical medicine by allowing physicians to reclaim functions such as the treatment of venereal disease and tuberculosis which prior to that seemed only addressable by public health preventive measures.

Similarly, the rise of private health insurance1 redefined the doctor-patient relationship as well as the balance of power. On the one hand, doctors lost (and continue to lose) autonomy at the hands of centralized payers, but on the other hand insurers use of physicians as gatekeepers reinforced medical doctors’ centrality compared to alternative forms of healthcare which eventually came to be regarded as fringe (despite never fully going away for better or worse; e.g. chiropractors and acupuncture).

Jeremy Greene’s Prescribing by Numbers: Drugs and the Definition of Disease focuses on the recognizable modern pharma company beginning in the 1950s. Green describes how the powerful marketing departments of large drug makers effectively orchestrated a re-definition of health and illness in the image of their drug portfolios. Although Greene himself bends over backwards to strike an impartial tone, the story he tells is a proper scandal. He recounts the following anecdote.

The scene is two days before Halloween in 1957, Boca Raton Florida, a hotel ballroom set up to host a professional convention. It’s the annual meeting of the American Drug Manufacturer’s Association, and the audience is listening intently to the vision being described for the future of their industry by the man at the podium. Charles Mottley, an executive for Pfizer, was laying out an ingenious — and a little bit diabolical — plan for financial domination, based on the following insight: drugs that are too effective aren’t long-run profitable. Antibiotics makers had essentially killed their own market share just as they had saved their customers’ lives. “There seems to be an important lesson here for the drug industry. As the industry does a good job of producing efficacious drugs and helps to win a given campaign...the net result is to limit the potential market.” Businesses need growth markets, not dwindling markets. “Trends are developing in the cause of death statistics which indicate that ‘tomorrow’ greater proportions of people are likely to… be afflicted with diseases, such as cancer and cardiovascular involvements, for which there are, as yet, no really effective drugs.”In the expanding prevalence of chronic diseases, Mottley saw a tremendous opportunity. Patients with chronic conditions are sick, but they neither die nor improve enough to discontinue treatment. They need your product forever.

Greene’s book covers three cases: high blood pressure, diabetes (and “pre-diabetes”), and high cholesterol. He lays out how new pharmaceutical products helped shape the very concept of what it meant to be healthy or diseased. And how prevention thereby became billable. You know the saying “an ounce of prevention is worth a pound of cure?” Well, Mottley and gang were savvy enough to realize that profits were a function of both price and sales and that a subscription model to wellness was a boon.

We see here echoes of the way physicians usurped responsibility for infectious disease from public health agencies with the advent of antibiotics. Greene makes the point by examining the history of statins. Here we have doctors encroaching on the very notion of preventive health. Surely that is the purview of public health campaigns? No longer. With large RCTs showing a decrease risk of cardiovascular events in patients taking statins, drug companies can now sell drugs to the presently healthy patient to, you know, make sure they stay that way. A sort of medico-emotional “protection money” which only doctors can prescribe: pay us for this office visit and this pill or we will foretell your premature death.

The public health versus individual doctor angle is enlightening, I think, because it highlights some paradoxes of the ongoing debate about the appropriate role of statins. A recent controversy has erupted around a paper reporting that statins are essentially adverse-event free. Skeptics point out the paper was funded by the very companies who manufacture those products, laundered through nested research institutes. Even taken at face value the Lancet study raises the question: if statins are so safe and effective, shouldn’t they be added to the water supply? Or at least be available OTC and perhaps subsidized by federal public health agencies?

Greene’s book can be summed up by a Korean adage (병 주고 약 준다, byeong jugo yak junda) “Sell the disease, then sell the cure.” Without rashly pointing fingers or casting anyone as a villain, Prescribing by Numbers raises the reasonable question of whether or not the people selling the cure should be trusted to dispassionately determine what it even means to be healthy or sick.

Finally, Pills, Power, and Policy by Dominique Tobbell, outlines the various ways that physicians, as a professional body, have worked with the drug industry and academic researchers to resist various attempts at policy reform. To quote from the introduction “the shared interests of academic researchers and the pharmaceutical industry and the industry’s responsiveness to the needs of the biomedical community led the pharmaceutical industry, organized medicine, and certain leading academic physicians to join forces against pharmaceutical reformers in the 1960s and 1970s. By describing the history of this pharmaceutical-medical alliance, Pills, Power, and Policy documents the economic and intellectual influence of pharmaceutical industry interests on research universities and medical schools in the second half of the twentieth century.”

Tobbell’s book essentially zooms in on themes established by Starr, while zooming out from the specific case studies presented by Greene. I personally find that mid-level analysis less compelling — it reads a bit like a raw chronology — but Tobbell’s book is nonetheless a welcome documentation of the ways doctors, drug makers, and academics collaborate in an enterprise that is simultaneously profitable (like, really profitable), important (huge public health consequences), and immensely challenging (scientifically).

In part two I will take a look at three lay audience books, Ben Goldacre’s Bad Pharma, Jerry Avorn’s Rethinking Medications, and Tom Stossel’s Pharmaphobia.

1. The stand-in

1.1
A model is something that stands in for something else.

1.2
A crash-test dummy stands in for a human body in a collision. It does not stand in for a human being at breakfast.

1.3
A dressmaker’s dummy stands in for a torso. It is useful because it does not breathe, object, fidget, or leave.

1.4
The model’s usefulness comes partly from its defect. It is useful because it is not the thing.

1.5
The question is not: “Is the dummy human?” The question is: “For this crash, does it preserve what matters?”

1.6
This question must follow every model, however mundane or grand: What does it preserve? What does it omit? Are the omissions harmless?

2. The map

2.1
The map is not the land. This is not a complaint about maps.

2.2
A map that included every stone, leaf, rut, puddle, smell, and noise would not guide us. It would be another country.

2.3
The map earns its keep by leaving things out. So does the model.

2.4
The first error is forgetting that omission is not an accident of modeling — it is the method.

2.5
The second error is to forget that omissions must be defended.

3. The license

3.1
A model often carries a license of scientific authority. But is the license warranted?

3.2
Equations, code, confidence intervals, simulations, randomized trials, causal diagrams, or Greek letters are not automatically validation. True scientific authority is licensed by demonstrated adequacy, not by technical appearance.

3.3
The license says: “This is no longer mere opinion.” Sometimes it is lying.

3.4
It is as if, having invented the microscope, we decided that anything viewed through it had become biology. Lint under a microscope is still lint.

3.5
A trivial question analyzed by a sophisticated method is not thereby made important. A weak argument written in equations is not thereby made scientific.

4. The Box Defense

4.1
“All models are wrong, but some are useful.” It was wise when George Box said it, but cringe when a grad student says it at seminar.

4.2
The first half sounds like humility, but then gives way to self-indulgence in the second half. The speaker says: “All models are wrong.” Tacitly they add: “But mine is useful.”

4.3
The missing question is: useful for what?

4.4
A model may clarify a mechanism and fail as a prediction.

4.5
A model may predict locally and fail when transported.

4.6
A model may fit old data because it was built to fit old data.

4.7
A model may be mathematically elegant and empirically inert.

4.8
The better articulation is stricter: all models are wrong; most are useless; some are useful for particular tasks under particular conditions.

5. Oreskes’s warning

5.1
Oreskes’s early work is instructive here. It says: numerical models of open natural systems cannot be “verified” or “validated” in the strong sense. The systems are not closed, input data are incomplete, different model structures may produce similar outputs.

5.2
This is an important warning against inflated language. But the warning can itself be misused (just like Box’s quote).

5.3
One may say: “Perfect validation is impossible.” But then there is a temptation to say (or imply): “Therefore you should not press too hard on whether this model is adequate.”

5.4
The impossibility of perfect validation does not relieve us of the burden of showing adequacy for purpose.

5.5
If no map is the land, it still matters whether this map is of Paris or Pittsburgh.

6. Experiments on the model

6.1
A numerical experiment is an experiment on a model. It may be useful or illuminating. But it is not, without more, an experiment on the world.

6.2
Waldmann’s complaint about DSGE models belongs here. If one must experimentally probe a model to discover how it behaves, the model may have ceased to clarify thought.

6.3
It has become a second object of inquiry. That object may be interesting. But it is not the economy, the aquifer, the climate, the aircraft, or the patient.

7. Deterministic vs Probabilistic Models

7.1
Some models speak in the grammar of necessity. Given these assumptions and these inputs, this follows. These are deterministic models.

7.2
Other models speak in the grammar of probability. Given these assumptions and these inputs, this distribution follows. These are probabilistic models.

7.3
The deterministic model borrows authority from implication. The probabilistic model borrows authority from measured uncertainty. Both remain conditional (contingent).

7.4
The deterministic model says: if the world is like this, this must happen. The probabilistic model says: if the world is like this, these chances follow.

7.5
The phrase “if the world is like this” is where the whole trouble lives.

8. Probability

8.1
Probability is not a cure for ignorance. It is a way of arranging ignorance.

8.2
Error bars may describe uncertainty within a model while hiding uncertainty about whether the model is the right one.

8.3
A risk score may be precise because its calculation is precise. That does not make the world precise.

8.4
A person does not contain a small dial reading “14 percent ten-year risk.”

8.5
Numerical risks arise from: a model, a reference population, a time horizon, predictors, endpoints, measurement rules, and background decisions.

8.6
Change the endpoint, and the risk changes. Change the population, and the risk changes. Change the treatment environment, and the risk changes.

8.7
Risk is not a diagnosis.

9. Screening

9.1
Cancer screening begins with an attractive premise. Cancer is bad. Earlier detection is better than later detection. Therefore screening saves lives.

9.2
What this narrative overlooks: over-diagnosis, over-treatment, incidental findings, surgical harms, anxiety, and the fact that some detected cancers would never have mattered.

9.3
The South Korean thyroid-cancer case makes the point.

9.4
Ultrasound screening exposed a large reservoir of subclinical thyroid cancers. Many small papillary thyroid cancers would not produce symptoms during a person’s lifetime; surgery created lifelong thyroid replacement for many and complications for some. The NEJM report notes surgery complications including hypoparathyroidism and vocal-cord paralysis in insurance-claims data, and describes large incidence increases without corresponding mortality increases.

9.5
The screening machine found disease. But much of what it found was disease only because the machine had found it.

9.6
Patients became survivors of cancers that may never have harmed them.

10. David M. Eddy

10.1
Was David M. Eddy a reformer or a huckster?

10.2
He was right to object to medicine by custom, eminence, and ritual. He pushed medicine toward evidence, formal analysis, and explicit policy reasoning. This was all to the good.

10.3
Evidence rules that ask whether screening improves health outcomes are good rules. They are also attractive to institutions that wish to pay for less screening.

10.4
Once inside an institution, a model may stop being a tool for thought and become a tool for permission. Permission to screen. Permission not to screen. Permission to cover. Permission to deny.

10.5
Eddy’s Archimedes model is a flagrant over-promise: it did not purport merely to summarize evidence, but to simulate bodies, diseases, treatments, care processes, costs, and policy choices all at once.

10.6
Archimedes was a map that claimed to be the land.

10.7
Real trials are slow, expensive, narrow, and ethically constrained. A virtual trial is fast, cheap, repeatable, tractable. But tractability is not truth.

10.8
In the Wired profile Zeke Emanuel called the model “sophisticated but speculative.

10.9
Thousands of variables and equations shoved inside a black box, the assumptions hidden away. This is Waldmann’s critique in a white coat. If the model is nearly as mysterious as the patient, it may no longer be clarifying thought.

11. Framingham and All of Us

11.1
Framingham insinuates that medicine should no longer asks only: what disease does this patient have? It may now also ask: what future disease does this patient resemble? It is like that Tom Cruise movie Minority Report.

11.2
Risk-factor medicine is actuarial medicine.

11.3
But a high-risk person is not yet a sick person (and may never be).

11.4
A low-risk score is not a talisman.

11.5
All of Us is the newer, shinier model year.

11.6
Collect enough data. Measure genomes. Monitor behavior. Consider environment.
Then medicine will become personal. Like how MySpace could represent you perfectly if you listed all your favorite bands or how custom Nikes could represent you with just the right color-way.

11.7
NIH describes All of Us as a program to collect and study data from one million or more people, with the aim of enabling individualized prevention, treatment, and care. Did they forget the quality over quality adage?

11.8
Tabery’s critique is useful because it asks what disappears when medicine becomes enchanted with genetic risk: social determinants, public health, environmental exposure, access to care, and commercial incentives.

11.9
The larger map may still be the wrong map. A map with more streets is not better if the question concerns the river.

12. The gloomy prospect

12.1
All of Us over-promises, in my opinion. It’s looking in the wrong places. But epidemiology says “don’t bother looking at all.”

12.2
George Davey Smith argues that much “individual risk” may not be further refinable in any useful epidemiological sense.

12.3
Causes may exist. But they may include events too fine, too contingent, too interactional, too biographical to recover. The causes may be accidental.

12.4
One woman smokes for decades and lives to one hundred. Another doesn’t smokes at all and dies of lung cancer.

12.5
The population fact remains: smoking causes lung cancer (on balance).

12.6
Individual causation is brutally difficult.

12.7
Some causes might be unlearnable. But that does not mean all are. Just like in the Serenity Prayer we must ask for the wisdom to know what causes we just need to look harder for (and where to look).

13. Constructive skepticism

13.1
My concern with science is that we stop our investigations too early. But we may stop prematurely for two different reasons.

13.2
The first reason is to wrongly conclude that our model is already good enough. We already have a perfectly adequate map. It surely is an impressive looking map, but did we bother to check that it gets us around successfully?

13.3
The second reason is to despair that our map is rubbish and not try to undertake a new survey of the land. In other words, to quit. (To settle for vague risk predictions.)

13.4
Progress demands dissatisfaction disciplined by new evidence.

13.5 Bioinformatics is too optimistic about what we have and can learn; trialists are too pessimistic about what is possible (too expensive). I say give the bioinformatics money to the trialists and see what happens.

14. Politics

14.1
A model may discipline policy-making, but it cannot replace judgment.

14.2
Dotson’s warning belongs here: attempts to “scientifically rationalize” policy can go wrong when they treat science as purified of politics and experts as possessing complete and neutral knowledge.

14.2
A model can estimate deaths, costs, risks, benefits, and uncertainties.

14.3
It cannot decide, by itself, what risks are acceptable, whose harms count, how much uncertainty a society should bear.

14.4
Those decisions are not anti-scientific. They are the place where science meets judgment.

15. The license examined

15.1
The license of scientific authority must be periodically renewed.

15.2
It should expire when transported beyond its domain and should state clearly the use for which it was granted.

15.3
It should not be automatically transferable from “predicts one trial” to “replaces trials” or from “estimates group risk” to “diagnoses the individual” or from “finds more cancers” to “saves more lives” or “encodes current knowledge” to “discovers what current knowledge lacks.”

15.4
A useful model should make thought more honest. It does this by exposing assumptions, not burying them.

15.5
A useful model should generate hypotheses, not counterfeit findings. It should guide measurement, not excuse its absence. It should improve judgment, not issue verdicts.

15.6
A model’s authority depends on it remaining answerable to the world.

15.7
Asking the world to answer to the model is arrogance, folly, or both. (Is someone trying to sell you the model?)

This “poem” was created from a rough draft based on a long, detailed, rambling prompt to ChatGPT Pro 5.5, as well as several uploaded essays and LinkedIn posts of mine and several specific articles by Eddy, Oreskes, Dotson and others (I will add reference links in the near future.) After a long conversation where I was conducting a web search on these themes, I asked the robot to summarize our discussion in the style of Ludwig Wittgenstein. The result delighted me so much that I then spent a couple of hours editing it line by line. It was perhaps more fun to create than it is to read.

I think I managed to make most of these points, but wanted to share this consolidated articulation with others.

WHY HTE DISCOVERY?

In discussing treatment effect heterogeneity I find it is helpful not only to abstractly acknowledge the possibility of HTE, but to fix some concrete examples:

• Caffeine metabolizers. It is well-known that people are affected by caffeine differently and that, in this case, it comes down to how effective the body is at metabolizing the drug.

• Bacterial vs Viral infections treated by antibiotics. Viral infections do not respond to antibiotics, so an infection with similar, or indistinguishable symptoms, will lead to very different treatment effects on this basis.

• Vitamin C and scurvy. Similarly, a condition defined by a vitamin deficiency will show profound improvement upon supplementation of that vitamin, whereas people without that deficiency will see scarcely any health benefit at all.

• Drugs that kill and their effect on heart rate. Taking a fatal dose of a drug will result in the patient’s heart rate being pegged at exactly zero; therefore the numerical treatment effect will vary from patient to patient as a result of what their heart rate would have been had they not taken the fatal dose, and it is well known that resting heart rates vary greatly from person to person and from time to time.

• Multiplicative effects measured on non-log scale. More generally, a drug that has a multiplicative effect on some physiological measurement (e.g. respirations or white blood cell count) will have a treatment effect on the raw scale that is heterogeneous, but homogeneous on the log scale.

So, given that there are widely-agreed-upon instances of marked heterogeneity, why is there any question at all about whether or not we should bother looking for them when developing new drugs? Well, it’s because such investigations are costly and uncovering strong evidence of heterogeneity from any particular trial is quite difficult, as a statistical matter. Most studies are not adequately powered to provide decisive results for any particular subgroup.

But the latter fact (estimating HTEs is difficult) does not invalidate the former (HTEs do exist and sometimes the heterogeneity is clinically significant). And this duality raises the question: how many non-obvious cases could we suss out if we had the right data and bothered to look? It is a logical error to insist that personalization must either be obvious, as in my leading examples, or completely intractable and therefore never worth looking for. Stephen’s rhetoric (in his prodigious writing) against personalized medicine can come across (at least to me) as pooh poohing any heterogeneity-on-observables. Which I think is scientifically wasteful. It prevents us from pursuing a more refined mechanistic understanding of how treatments work.

So what exactly is the argument for not looking for HTEs? Essentially it boils down to what economists call “opportunity costs”: Stephen writes “Resources are finite and for me, the question is always, ‘given that the treatment appeared to work in the trials that we ran, and that other treatments are waiting to be studied, does studying this treatment in yet another subgroup make the cut?’. …the answer will often be ‘no’.”

His argument, as I interpret it, goes like this:

1. We want to show the regulators (FDA, etc) that our drug works somehow, therefore

2. We should focus on ATE in our convenience sample because that is the estimand with highest power.

3. This strategy is justified because we believe the effects for any population we might treat will be zero or positive (no so-called “qualitative” interactions).

4. We shouldn’t look at CATE or subgroups because it risks undermining our positive findings in the aggregate.

It’s the fourth point that I primarily take issue with. It would be a shame if expensive RCTs were only permitted to address a single question at a time. Of course they should be designed to answer one question carefully and primarily, but that data has other uses: observation is the very grist of scientific conjecture.

HTE estimation does not need to be part of the initial approval analysis. Data from any primary analysis should be able to underpin a subsequent exploratory analysis, of which HTE discovery is a key component. This will then inform decision about *future studies*. So poking around for HTE does not invalidate 1-3 and therefore sidesteps objection 4.

My claim isn’t that we should always be able to find HTE from any given RCT — we shouldn’t expect that. But by not looking we will never find strong, surprising effects for follow-up. As Wayne Gretzky quipped “You miss every shot you don’t take.” In particular, I believe that we ought to measure more baseline and environmental conditions. Specifically, what I am advocating for is investigating more homely potential moderators — body weight, white blood cell counts, ethnicity, co-morbidities — stuff that in many cases we explicitly screened out of our present studies (because it provides a weaker “wind tunnel” proof-of-concept).

The main barriers to this sort of post-hoc discovery — which I admit are non-trivial — are logistical and financial. But I worry that folks working under those logistical and financial constraints are presenting the challenges as a scientific one, when in fact they are operational. As a result, novel hypothesis are forced to come from ad hoc observations, rather than from our hard-won (even if underpowered) RCT data.

To reiterate: My goal in pursuing HTE discovery is not more efficient studies. Rather, the case for HTE estimation is that we dramatically impoverish subsequent studies if we “hardheadedly” insist that the only licit object of inquiry is the (sample) ATE.

How to Do it: Tree Ensembles for HTE Discovery

Presumably I was invited to comment on this topic because I have made some contributions to methodology, and software, for performing HTE estimation, and I have been publicly adamant that our software has been designed to be useful in practice. In reading Stephen’s work, I have come to believe that the statistical approach my coauthors and I have taken for HTE estimation is consistent with his perspective, but that we use specific tools that are not yet commonplace in drug development. Specifically, in his textbook Senn has a nice, brief technical appendix explaining that a blended estimator of conditional average treatment effects (CATEs) is usually ideal. That is, if you consider estimating a subgroup effect (on a pre-specified subgroup) you are often better off using a weighted average of the pooled estimator of the overall average effect and an unbiased estimator of the unpooled estimator of the subgroup effect — a so-called “partially pooled” estimator. The ideal degree of partial pooling will depend on the sample sizes of the two groups and the true difference (if any) between the average effect and the subgroup effect. As he notes, Bayesian hierarchical models are probably the right tool for this.

Regression tree ensembles, like those that underly our Bayesian Causal Forest software, are an extension of Bayesian partial pooling estimators that adaptively shrink subgroup effects towards the overall average, but do so without needing to pre-specify the subgroups. Informative priors bias the estimates towards homogeneous effects, but strong subgroup effects in the data can overcome this bias. We must not forget that power is relative to a given effect size. Not looking for subgroup effects from already gathered data, because you expect that subgroup effects won’t be large enough to be statistically discernible, means that you for sure won’t see effects that in fact are statistically discernible, at any level.

(Clarification: it sometimes seems to me that people think of subgroup effect hunting as a way to salvage studies that show an unworkably small average effect. But my vision of HTE discovery is that we should run it on any study and perhaps especially on treatments that do appear to work well on average. Specifically, a moderately large treatment effect can occur if a small population has a staggeringly large effect and I think it is unethical to proceed to treat everyone in that case; but this perhaps contradicts business principles.)

THE RELATIONSHIP BETWEEN DIAGNOSIS AND HTEs

Two of my leading examples of HTE were “diagnosis-based”. Vitamin C is life-saving among people with severe vitamin C deficiency (scurvy). And yet an RCT in a random sample of the population (or most non-specific convenience samples) would show scarcely any effect on any vital sign of interest. The interesting heterogeneity is part-and-parcel of the very definition of the disease. Likewise, the viral versus bacterial infection example has this same flavor. Indeed, in cases where it is not clear if an infection is viral or bacterial one can “diagnosis via treatment”. If the patient improves with antibiotics, it was a bacterial infection!

Stephen wrote to me once that: “The progress of treatment for testicular cancer has been brilliant in my lifetime but for lung cancer extremely disappointing…but is differentiating between testicles and lungs really what we mean by personalisation?” And my response was “Yes?”

Indeed, as we learn more about cancer it seems very much like it isn’t one homogeneous disease at all, but a wide family of related diseases that differ significantly enough in their etiology that some are very treatable and others are vexingly resistant.

I am a bit puzzled by the apparently widespread belief that personalized medicine must be based on attributes that are distantly removed from the disease itself; it is part of what makes personalization seem like magic. But I would urge that we think of personalization much more open-mindedly, to include any attributes that yield higher success of treatments — and such attributes are very likely to be related to stratifying on symptomatology.

CONCLUDING REMARKS

To conclude, I’d like to highlight 4 points of what I believe to be strong agreement between Stephen and I:

• We both think propensity scores are overused — and often misused — and that direct outcome regression adjustment is a superior way to incorporate covariates into a causal analysis.

• We both feel that genomics is an unpromising approach to discovering exploitable heterogeneity. (Stephen’s work describing “phenotypic squeeze” is worth everyone’s time to read.)

• We are both proponents of dosing by body weight and randomization to dose in experiments. (One of my questions for Stephen: why is the industry so reluctant to act on this obviously sound idea?)

• I think we are both proponents of cross-over trials, where appropriate (Stephen literally wrote the book on this one); n-of-1 studies being a special case.

Alas, it’s basically the question I’ve been pondering lately, except not about comedy, but about science. As a statistics professor, a core chunk of what I teach is hypothesis testing. As a group of professional scolds, statisticians are quick to remind everyone that there are Right and Wrong ways to use data to test your hypotheses. There’s a whole intellectual edifice built up around the idea that there are rules we ought to follow so that we don’t trick ourselves into believing theories that are actually wrong. It’s a nice system, all things told, but it really only works if we have a ready supply of hypotheses at hand. Statisticians, for the most part, are conspicuously mute on this topic.

There’s a hint of a paradox here, because supposedly there are Right and Wrong ways to use our data and scrutinizing the data in order to dream up explanations for the patterns we see is certainly not the Right way, according to the textbook orthodoxy. And yet, if our ideas (hypotheses, theories, etc) don’t come from data, how could they possibly explain anything about the actual world we live in? Dumb luck?

Karl Popper

This friction between data for ideation and data for theory testing actually predates the widespread adoption of the hypothesis testing framework and is explored in great depth in the work of philosopher Karl Popper (as well as his critics), particularly his 1959 book The Logic of Scientific Discovery (translated by Popper from an earlier German-language book of his from 1934). One of the major goals of Popper’s book was to develop a theory of “demarcation” which would allow us to separate scientific inquiries from nonscientific ones. The button-down hypothesis testing stuff is Science, with a capital S, and the hypothesis formulation is groping or stumbling around in the dark.

Lest you think I’m exaggerating, let me quote Daniel Lakens, a well-respected modern day Popperian (emphasis added):

“External replication often reveals that we were wrong…and the only approach we know to discover how we were wrong is to stumble across it.”

And, “If you show you have achieved [correct predictions], that is where we hand out awards. Not for the exploration part. That is just a first simple necessary step. The easy, albeit essential, first step is not what should be impressive.”

He goes on to clarify that “Exploratory just means you cannot control error rates of claims.”

Naturally, I find this approach misguided. Categorically calling anything that does not control error rates “exploration” is a mistake, I feel. It’s like saying “anything that is not classically composed music is noise, therefore jazz must be easy, just a matter of stumbling upon any old notes.” This is not how any scientist I know thinks about their work. Exploration can, and should, be much more directed than that, even if it doesn’t control error rates.

Meanwhile, as Lakens is out there denigrating the creative (yuck) side of science, the philosophers have more or less moved on. It turns out that the theory of demarcation is devilishly hard to defend and modern philosophers of science basically acknowledge that and have turned their attention to other problems. (Take the neglect of an idea by professional philosophers for what you will.) At root, the difficulty is that the line between a theory and an observation is surprisingly blurry. From the Internet Encyclopedia of Philosophy:

“Popper’s proposed criterion of demarcation […] holds that scientific theories must allow for the deduction of basic sentences whose truth or falsity can be ascertained by appropriately located observers. If, contrary to Popper’s account, there is no distinct category of basic sentences within actual scientific practice, then his proposed method for distinguishing science from non-science fails.”

Modern acolytes of Popper, particularly in the social, behavioral, and health sciences, side-step this objection by simply elevating everything to the level of a theory. These fields have settled for verification of “findings”, deploying the apparatus of hypothesis testing for this purpose and proceeding to call it science because it is “falsifiable” in the narrow sense of being able to be rejected via a hypothesis test. (Popper himself conspicuously does not write about hypothesis testing, despite it being developed squarely during his professional lifetime.)

In a phrase (and painting with a rhetorically broad brush) much of contemporary psychology would have us believe that it is enough to show that some association is true without any manifest interest in why it might true. This vantage point has its clearest exemplification in the modern business of Online Experiments where, say, different colored web page buttons are “scientifically tested” against each other to see which leads to higher online sales.

It’s worth taking a look at the sleight of hand that underlies this move from theories to mere findings. If I have a data set and I observe that in my data there is a strong association between the color of the button and the frequency with which users click the button, that’s pretty uncontroversially a “basic fact” in Popper’s terminology. What requires “testing”, in the statistical sense, is whether or not this correlation persists if we looked at larger or different groups of users. Whether or not this pattern generalizes does not (in my opinion) constitutes a scientific theory in any full-blooded sense of the term, but because it is falsifiable (subject to assumptions about the sampling frame and other details), it counts as scientific by some weak definition. From this perspective, all it takes to be scientific is to have statistical control of the error rate of our claims. And, moreover, this is the only kind of procedure that we are licensed to use if we are to call ourselves scientists. It is an empty suit caricature of science.

To recap, maybe it’s okay to call A/B testing scientific inasmuch as it employs an uninspired form of falsifiability. But we must recognize that it’s an impoverished form of science. Not just anything should count as science just because it is falsifiable. (Sabine Hossenfelder has repeatedly made this same point about flimsy justifications for building ever-larger particle colliders.) Conversely, maybe you don’t want to call data analysis methods that aren’t falsifiable (in either the broader sense or narrower sense of having control of error rates) Science (capital S), but surely there are better and worse ways to plumb our data for ideas — and surely not plumbing them at all just because we cannot guarantee error control is the dumbest possible way to do this.

Which brings me to John Tukey. A giant of contemporary science, Tukey was responsible for many brilliant ideas that we still use today. He coined the word “bit”. He invented (or reinvented, after Gauss hid it in a desk drawer) the fast Fourier transform. He gave us the witticism: “Far better an approximate answer to the right question, which is often vague, than an exact answer to the wrong question, which can always be made precise.” He also has a number of well-known statistical tests named after him.

But for the purposes of this essay, Tukey’s big idea was Exploratory Data Analysis (EDA). In 1977, Tukey published a book of that title, which is today remembered as an early contribution to statistical graphics. It introduced the box-and-whisker plot! Tukey championed EDA as a collection of techniques to facilitate the formulation of hypotheses that could lead to new data collection and experiments. It’s the answer to the Eget-esque question: where do scientists get their ideas from?

Tukey was expressly interested in nontrivial data analysis procedures that could be used to generate hypotheses to fuel Popper’s falsifiability game, to stock the shelves with hypotheses for our trusty t-tests to operate upon.

Notably, Tukey worked on many real scientific problems — far more than Popper did. He had first-hand knowledge of where our theories come from and the answer — obviously! — is data. If analyzing our data in a non-error-controlled way is frowned upon, we are that much worse off in terms of finding interesting theories to test. Right?

Not everyone sees it that way. And I think I know why — it’s because the professional scientific culture is expecting us to report the results of our labors and when issuing these report we want to report results (“findings”) rather than conjectures. In most cases our findings won’t be taken seriously unless they are corroborated with a formal statistical test. So we end up with a situation where, to the extent that you’ve done some sort of exploratory analysis, you pretend that you didn’t and then report the results of the t-test, which has the establishment’s blessings. (Ed Leamer talked about this dilemma in the memorable, and memorably-titled, paper “Let’s Take the Con Out of Econometrics”.) Conversely, we have people whose results don’t rise to the level of statistical significance, but who still find the result interesting or suggestive scientifically who end up skirting the rules and describing things as “nearly significant” or “approaching significance” — which they then get pilloried for in social media by the Righteous Gatekeepers (see screenshot).

This state of affairs is obviously undesirable. The testing purists propose to fix it by demanding pre-registration and formal replication and scorning scientists who do “mere” EDA. On the one hand, this is fine for confirmatory analysis, although I think it would lead to more Leamer-style evasion. But for exploratory analysis, it isn’t so clear that pre-registration is even possible. This, I claim, is a big part of why scientists are inclined (persistently!) to mis-use statistical tests.

Science works best when it is iterative. That is, we learn most about the world when our experiments and observations build on and reinforce (or contradict) one another. The stringent error-control purism really doesn’t encourage this at all, simply because falsifiability alone is a horribly weak requirement. It is why after decades of rigorous A/B testing for online experiments we are no closer to a theory of online consumer behavior.

Of course, throwing out statistical standards wholesale doesn’t solve the problem either. Tukey recognized all of this decades and decades ago. He was perfectly explicit that EDA shouldn’t be done on the same data that was then used for a subsequent confirmatory analysis (a la Leamer’s essay). Lots of introductory textbooks get this point wrong, suggesting that EDA is the first step in any data analysis. Making basic plots and acknowledging missing data and reformatting as necessary should be considered “prepatory analysis” rather than “exploratory”, and too many texts do not make this critical distinction.

In any case, explicitly embracing iterative science solves many problems. Confirmatory analysis (orthodox error-controlled hypothesis testing) should be done on a data set for one set of questions (arising, presumably, from a previous EDA on an earlier data set). For these questions, pre-registration and replication attempts are welcome! But that data has more life in it yet — that same data can then be used for a subsequent EDA, which would inform a subsequent CDA of yet a third distinct data set. EDA should come after CDA on a given data set, but before CDA on subsequent data sets. Ideally, a public record of all of this would be kept somewhere for later cross-referencing.

Perhaps a concrete example (or two) will make my case better than abstract arguments.

You may have read something recently about the non-profit research organization Every Cure, which has been reported on in the New York Times and in dozens of social media posts and popular health and science podcasts. The story of Dr. David Fajgenbaum’s — Every Cure’s mastermind — bears on the present discussion. The high level version is that after being diagnosed with an often-fatal, treatment-resistant, rare condition called “idiopathic Castleman’s disease” Dr. Fajgenbaum set out to find an off-label drug to cure his disease and — miraculously — he succeeded. The drug he found was called sirolimus and he didn’t find it by sheer trial and error.

Sirolimus (also called rapamune) was FDA-approved in 1999 to help prevent host rejection after organ transplantation. It works by inhibiting a biological process referred to as the “mTOR pathway” (which stands for “mammalian target for rapamycin”). This “mechanism of action” is what tipped Fajgenbaum off that sirolimus might work. From extensive self-testing — performing experiments on his own lymph node tissues and blood samples — Fajgenbaum learned that his mTOR signaling pathway was over-activated and therefore a potential drug target. He then searched for FDA approved drugs for treating mTOR hyperactivation; sirolimus was one of these drugs. And it worked. Since beginning the experimental treatment seven years ago he has been in full remission. While the drug does not seem to work for all Castleman patients, it has apparently cured a number of others besides Dr. Fajgenbaum. There are now clinical trials in progress to demonstrate efficacy and safety via the usual channels and methods (randomized trials and error-controlled statistical analysis).

But take note: Dr. Fajgenbaum’s initial life-saving discovery 1) did not utilize any statistical hypothesis tests, and 2) neither was it blind luck that he thought to try sirolimus. There was data collection and data analysis and a hypothesis and a very practical test of that hypothesis (self-treatment). I hope we can all agree that this was obviously a scientific investigation. But it wasn’t an RCT and it didn’t have error controlled procedures. What it did have is a putative mechanistic justification (the mTOR pathway) based on previous confirmatory studies in other contexts .

Fajgenbaum’s t-test-free science success story has many, many historical precedents, of course. As Cosma Shalizi writes in his (mostly glowing) review of Deborah Mayo’s “Error and the Growth of Experimental Knowledge”:

“[T]here was lots of good science long before there were statistical tests; Galileo had reliable experimental knowledge if anyone did, but error analysis really began two centuries after his time. (If we allow engineers and artisans to have experimental knowledge within the meaning of the act, we can push this back essentially as far as we please.) If experimental knowledge is reached through severe tests, and the experimenters knew not statistical inference, then the apparatus of that theory isn’t necessary to formulating severe tests.”

Fajgenbaum’s story shows that statistics isn’t necessary for science. Here is story which may help convey that statistical methodology isn’t sufficient either.

In 2010, a small psychology experiment (n=42) was conducted and reported in a peer-reviewed paper. The finding was that “power posing” (standing like Superman, arms akimbo, or like Captain Morgan) has measurable physiological effects: raises testosterone, lowers cortisol, and increases subjective feelings of power. The associated TED talk in 2012 and a subsequent popular science book in 2015 went viral and the idea of power posing entered the business lexicon. Consultants and trial lawyers ate that shit up.

However, in the same year the book came out, additional academic work came out showing that in the meantime the original result didn’t replicate — colleagues repeating the experiment could not reproduce the result. The paper’s first author was sufficiently convinced by the new work to disavowed the theory. Ron Kohavi (whom I paraphrased this timeline from) reports that in the last year the TED talk has received an additional 2.1M views. Kohavi uses this story as a cautionary tale about underpowered studies, noting that the initial study had power of only approximately 6%.

While I think we can all agree that higher powered studies are better than lower powered ones ceterus paribus, I think there were far better reasons to disbelieve the initial study, which is simply that it was a frivolous and implausible hypothesis in the first place. This is what happens, I would argue, when we allow “findings” to be reported as science instead of actual theories. In other words, the power pose research was bad science and also bad statistics, not bad science simply because it was bad statistics. Better power alone wouldn’t (or shouldn’t) have made it an attention-worthy paper.

A defining feature of Tukey’s EDA is that it was “model free” and many people associate it with rank-based analyses. So it may come as a surprise that I advocate for Bayesian machine learning as a modern incarnation of Tukey’s program. The reason I think it works is that, to my mind, the spirit of Tukeyian model-free EDA was primarily about being flexible and robust rather than being model-free per se. Bayesian machine learning can bring both of these qualities, if done with care.

The value-add of going the Bayesian machine learning route is the ability to be systematic about measuring the degree-of-support of which hypotheses to follow-up on, which inevitably must be made, without artificially or arbitrarily limiting the scope of hypotheses under consideration. Subjective priors can frankly be used in this context, while shrinkage/regularization (broadly construed) prevent one from reading too much into the tea leaves. Type I/II error control is too much to ask of an EDA, but we will still want to prevent gross-overfitting and chasing of noise.

Typically, EDA is either ignored (everything is treated like a CDA), or worse, it is done prior to a CDA on the same data set (tsk tsk). Hypothesis generation is treated as a purely intuitive endeavor in which case we call it an art (for other less rigor-minded folks to waste their time with) and leave the serious science for (ourselves) later. To my mind, Bayesian machine learning seems strictly better than any either of these options.

(Of course, lots of Bayesian machine learning is done poorly, but we must not judge an approach by its worst exemplars — if we did that, no one would recommend any form of statistical analysis, ever!)

With this in mind, let’s look at three virtues of Bayesian machine learning for EDA: flexibility, prior information, borrowing of information (analogies)

Flexibility

In my opinion, modern machine learning is best viewed as a massive leap forward in EDA technology. It’s a tool specifically for finding patterns in data. Why wouldn’t we want to use that?

Here is a metaphor to ponder: machine learning is like a microscope.

Widely regarded as one of the major breakthroughs of contemporary science, the invention of the microscope involved no prediction and no control of error rates. Instead, it gave us the ability to see things we simply couldn’t see before. (The analogy may be extended to include all manner of optical augmentation devices — telescopes, X-rays, etc.) Machine learning does the same thing. We cannot “by eye” see if various combinations of dozens of factors show strong associations with some response variable (in our data). But machine learning algorithms can — it’s what they were designed to do.

Like a microscope, ML must be used intentionally. A microscope doesn’t do its thing automatically — we have to prepare the slides and mount them and look through the eyepiece. And decide what to examine. And do follow-up experiments and interpretation. Same is true of machine learning. To avail ourselves of the machine learning “microscope”, studies should be designed explicitly to collect a richer set of environmental and other contextual factors. A commitment to expanding our record keeping would provide the grist for the machine learning mill.

Knowing which factors to record relies — as ever — on the results of previous experiments and theory-laden guesses; there’s no free lunch there. But to make no effort in this direction would be like not using the microscope because it doesn’t come with an instruction manual telling us what to look at with it.

This vantage point nicely captures, I think, Breiman’s advocacy for machine learning methods in his famous “Two Cultures” paper. The value of machine learning over parametric statistical models is that they are able to accommodate and reveal unanticipated patterns.

Regularization

This is not to say, of course, that exploratory analyses should be held to no standards – that would invite overwhelming the literature with chance associations (albeit in the name of “hypotheses” rather than “findings”). While I regard the derision with which some statisticians greet claims of “marginal significance” as a counterproductive form of bullying, the methodological anarchism of mainstream bioinformatics and digital medicine is a bridge too far. Just because your algorithm made a pretty picture doesn’t mean that the science is done. One, you want some kind of notion of uncertainty associated with that pretty picture — we do, after all, have to weigh our opportunity costs when deciding what leads to follow-up on. And two, that follow-up ought to involve a more buttoned-down and narrower confirmatory study.

The Bayesian framework is ideal for conducting flexible pattern discovery while reigning in the risk of over-fitting with regularization priors. Moreover, the regularization can be imposed in subtle ways. For example, it can be used to bias estimates towards particular values such as biasing an average treatment effect estimate towards zero (no effect) or towards the values of previous studies, but it can also be used to impose bias towards structures, such as “shrinking” towards homogeneity or additivity. We can fit a nonlinear model but bias towards a linear model, or fit a model with either additive or multiplicative errors, but bias towards additivity. We can permit higher-order interactions if the data strongly suggest it, but explicitly pre-register a “preference” towards a model with only main effects.

Additionally, the Bayesian framework yields uncertainty quantification, meaning that our microscope clearly indicates its resolution on the console, informing us of its own limits. What to do with ambiguous posteriors is not necessarily straightforward, but the alternative is what, to not use our pattern discovery machine when formulating our hypotheses and to not query that machine’s reported resolution?

In summary, my sales pitch is this: careful Bayesian machine learning can incorporate statistical uncertainty to EDA in a principled way, fully marshaling the available data without inciting wild-goose chases.

Borrowing information

A particular strength of Bayesian statistics in an exploratory (flexible, empirical, hypothesis generation) context is its ability to allow analogical data analysis. That is, via informative prior distributions over our data generating process, we can intentionally inject information from previous studies not directly related to the present data set.

For instance, when trying to infer the reproduction number describing the covid-19 pandemic, one might want to acknowledge that it is a respiratory virus from a family that we had previously studied. One of my major frustrations with the scientific establishment’s treatment of these questions during the pandemic was the pretense that covid-19 was entirely sui generis — entirely without precident — when in fact there were many analogies with other virus, including the common flu, that ought to have reasonably informed our decision-making.

This sort of analogy-based reasoning plays an important role in scientific inquiry — new drugs are similar to old drugs, new treatments are similar to previous treatments, new learning strategies are similar to traditional learning strategies, public policies in one place are similar to other public policies in other places. There is a conceit that serious science is “objective” in the naive sense of beginning with a blank slate at each analysis. But this is neither an accurate portrayal of science nor a desirable one. We want our knowledge of the world to compound, and using earlier investigations to steer the course of our future directions is not only licit, but advantageous. During confirmatory science, we can disregard our biases to get a “pure” measure of evidence, but to ignore those hard-earned biases during our exploratory phase is simply inefficient use of information.

Pharmacometrician James Rogers writes: “The discipline of statistics tends to be very focused on design and analysis methodologies, and the methodology of scientific argumentation involves more than just design and analysis. Scientific argumentation also involves consideration of multiple lines of evidence, holding them in tension, evaluating how they do or don’t corroborate each other, triangulating the truth (more or less: what belongs in the Discussion section of a scientific paper). In my experience, statistical training doesn’t put a lot of emphasis on that part of the scientific process, and that’s where “hints” and “marginally significant” results can be particularly important. “Hints” are rightly down-weighted when definitive statistical confirmation is on the line, but there is a lot more to science than just confirmation. “

Bayesian statistics — specifically nonparametric Bayesian models — is basically ideally designed to do what Rogers describes.

Frankly, I have something of a hard time understanding why anyone would object to this framing. The choice isn’t between error-controlled frequentist hypothesis testing and Bayesian machine learning. I’m happy to abide by the orthodox rules of statistical significance before declaring any particular finding trustworthy. The choice, rather, is at the hypothesis generation phase, and it’s a choice between raw intuition and intuition guided — disciplined, informed, and augmented — by Bayesian (machine learning) data analysis.

For more on Popper and Bayesian statistics, please read the excellent paper by Gelman and Shalizi, which I read many years ago and revisited closely in preparing this essay.

I know of Frisch’s work from my dissertation research on latent factor models. I discovered it through the lovely dissertation manuscript of Maryam Fazel (from which the image is excerpted) on the topic of Rank Minimization problems.

Frisch realized that even if a covariance matrix describing the linear relationships between several random variables were known exactly, extracting these linear relationships in a parsimonious way could be quite challenging if those variables were measured with noise.

More specifically, the covariance matrix might have full rank with relatively “flat” eigenvalues, but if you could subtract off the diagonal matrix describing the noise variances, the left over associations might be describable in terms of a much smaller number of factors. (See the image for a more technical description.)

Frisch’s observation points out why principal component regression can sometimes fail when factor modeling would succeed.

This rank minimization formulation also points out that estimation is sometimes only half the battle when it comes to understanding the relationships in our data — even with perfect reduced-form parameter values in hand it can require substantial further effort to extract meaningful underlying relationships.

On a personal note, when I was at University of Chicago I once checked out one of Frisch’s books from the stacks. Imagine my surprise when I found out it was signed on the inside cover by Ragnar Frisch himself! The inscription was a brief personal note to a colleague who worked at U Chicago and the book was later donated to the library from his personal collection.

I was very tempted to keep the book for myself and pay the fine of having “lost” it. Instead, I alerted the library to the historical significance and advised them to put it in a special collection. Honestly, given how much I would enjoy having that volume, I’m not 100% sure I made the right decision all these years later.

Monty Hall by itself is mostly a curiosity, teachingwise. But as a coding assignment it can be revelatory. Probability ideas become tangible. The power of simulation becomes palpable. The assignment really drives home the importance of procedural thinking — how crucial it is to be perfectly explicit about specifying the rules of game.

This year, for the first time, I had a number of students come to office hours with claims that “their code isn’t working”. Which turned out to mean that ChatGPT’s code wasn’t working.

In one case, the code declared a function that set a variable to TRUE and then called itself, leading to an infinite recursion and a program crash.

Of course, this is NOT how it is supposed to go -- it is not how it has ever gone in the past.

Here’s what I ended up telling my students: There are some cases where it makes sense to hire someone else to cook your food; but there are essentially no cases where it makes sense to hire someone else to eat your food for you.

Using AI on the Monty Hall programming assignment is like having the chef eat the food for you: you don’t get any of the nutrients yourself.

Understanding can’t be outsourced.

I knew his work from grad school, where his JASA paper on Stochastic Search Variable Selection paper with Ed George was required reading for several of my courses.

When I was learning Bayesian econometrics, his textbook Bayesian Statistics in Marketing was a major influence on my thinking.

I was also influenced by his paper with Ron Gallant: “On the Determination of General Scientific Models With Application to Asset Pricing”.

Rob’s first impression of me was not good, probably because I tend to make either too little or too much eye contact and am often too fast to criticize. In the end though we became friends and I’m proud to count him as a mentor.

Shortly before we met, Rob had written (with Ed George and Hugh Chipman) the Bayesian Additive Regression Trees paper. This paper became, and continues to be, a major driver of my own research.

Learning about BART from one of its creators was a big benefit to me. But even more imporant has been to hear that my extensions to BART have his approval/admiration. That sort of validation helps the constant rejections in academia sting less.

Rob and I share a common statistical short-hand; talking shop with him is effortless and efficient. In particular, Rob and I share a prediction-first approach to Bayesian statistics, which he picked up from his PhD advisor (another idol of mine) Seymour Geisser.

After Rob left for Arizona State University around 2016 I jumped at the opportunity to rejoin him a year later.

Rob has a rare intellectual integrity — judging his colleagues on the basis of their actual work, actually reading it, rather than outsourcing that judgement to publications or grant counts. He’d much rather talk about the ideas themselves than the trappings of the profession (hiring, awards, funding, logistics, etc). I’m so grateful to know that successful people with this attitude are even possible!

To myself and my graduate students, Rob is not only a scholarly role model, but a life role model, particularly his zeal for learning new skills. In the time I have known him, he has learned white water kayaking, skiing, and is presently learning surfing (all after the age of 60).

He got really into minimalist footwear around the time he moved to Arizona, and goes on long hikes amidst the thorny cacti wearing flimsy rubber sandals.

He has played competitive hockey for many years and roller blades across campus from class to class, which he always schedules back to back to back.

Rob likes to joke that he’s the second most successful academic in his family: his father Ernest McCulloch discovered stem cells in the early 1960s.

Here’s Rob’s web page to learn more about what he’s up to lately.

And don't forget his books! Advanced Data Analysis from an Elementary Point of View is perhaps the best introduction to modern data science that I know of. And his monster volume on empirical processes has the hilarious title: Almost None of the Theory of Stochastic Processes (poking fun at the excellent pair of books by his brilliant colleague Larry Wasserman: All of Statistics and All of Nonparametric Statistics).

I've had a few professional interactions with Professor Shalizi over the years, but my favorite was that I had the good sense to solicit a review of Imbens and Rubin's causal inference textbook from him. In one of my better moments, I had the idea to solicit three separate reviews of the book, which were all published together. The variety in them is remarkable and Shalizi's is my personal favorite. Read all three of them here (Matias Cattaneo and Kosuke Imai are the other two reviewers):