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):

In life there can only be one best whatever, by definition. Best quarterback, best surgeon, best soldier, best mathematician, best chef.

But there’s usually more demand than the best can provide, and so there is an ongoing need for lots of good quarterbacks and good surgeons and good soldiers and good mathematicians and good chefs. Good enough ones, that is.

Because our own efforts are limited across the various facets of our lives, learning how to satisfice instead of optimize is good strategy.

In the late 1940s, the US Air Force had a problem with their pilots crashing too many airplanes. No one was quite sure why.

After some initial investigation, the design of the cockpit turned up as a major factor.

Some twenty years earlier, military engineers had standardize the dimensions of the cockpit based on measurements they had taken on hundreds of pilots. The size and shape of the seat, reach distance to the controls, and height of the windshield were all designed based on that hypothetic average pilot.

At first, there was a thought that pilots had gotten bigger, on average, since 1926. But it turned out the real problem was that none of the pilots were average!

A new set of 10 measurements of 4,063 pilots was taken -- and not a single individual pilot fit within the "normal" range on all 10 dimensions!

As Rose puts it: "If you’ve designed a cockpit to fit the average pilot, you’ve actually designed it to fit no one."

The solution was to make the cockpit adjustable, rather than standardized.

In the case of a cockpit, making it adjustable is relatively easy, compared to what might be necessary for customizing medical treatments. But some easy wins seem within reach. Initial doses based on body weight and composition rather than a fixed standard dose, for example.

Meanwhile, genome-based personalized medicine is a little bit like customizing cockpits based on blood type, hair color, and body temperature. (That is: highly unlikely to be effective.)

I'm over-simplifying, but I always have the pilot story in the back of my head when I think about personalized medicine.

Rose's chapter in excerpt: https://www.thestar.com/news/insight/when-u-s-air-force-discovered-the-flaw-of-averages/article_e3231734-e5da-5bf5-9496-a34e52d60bd9.html

And a video:

And another blog write-up: https://www.lesswrong.com/w/lt-gilbert-s-daniels-and-the-myth-of-averages

• Vitamin deficiency. Vitamin C has scarcely any measurable therapeutic effect, unless of course you are woefully deficient, in which case it will literally save your life.

• Happy drunks vs Mean drunks. This one is harder to pin down, but arguably the effect of alcohol on personality is person-dependent.

• Paradoxical side effects. In some people, a drug will do the opposite of what it is supposed to: https://en.wikipedia.org/wiki/Paradoxical_reaction. Can’t get more heterogeneous than that.

• Effect of large dose of heroin on heart rate. Heterogeneity at baseline implies heterogeneity of treatment effect, because the heart rate under treatment goes to zero for everyone.

• Multiplicative treatment effects. If a drug increases respirations by 20%, then variation in baseline respiration rate implies heterogeneity in the treatment effect measured as a difference. (On the log scale this treatment effect would be homogeneous.)

• Gender differences. Any gross anatomical differences will lead to manifest differences in how people respond to stimuli.

• Enzyme difference in drug metabolism. Known differences in enzyme production lead to big differences in how individual process, and hence respond to, certain drugs: see https://en.wikipedia.org/wiki/Alcohol_flush_reaction and https://pmc.ncbi.nlm.nih.gov/articles/PMC8657965 for details.

• Bacterial vs viral infections. On a population of people with rhinitis, response to antibiotics will differ dramatically according to if the rhinitis is bacterial or viral.

If these examples seem obvious to you, then you may be surprised that many sharp and knowledgable people contest it!

Reaching way back, Oxford physician L. J. Witts protested in 1959 that people have “an exaggerated belief in the uniqueness of the individual whether as patient or doctor…Empires may rise and empires may fall, but the dose of opium remains 1/2 to 3 grains.”

A more contemporary and influential voice, Stephen Senn, writes in his authoritative text on Drug Development: “[T]he statistician’s art is practised in the hope that the properties of aggregates have some relevance to the individual but with the fear that they may not…[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.”

However, the conceit of “finding the right scale” (a log-transformed analysis for multiplicative effects) could be elaborated to include “stipulating the right trial population”. In the examples above, we would only trial vitamin supplements on patients with known deficiencies, only trial antibiotics on verified bacterial infections, etc. But this amounts merely to assume that one *already knows* the relevant heterogeneities and can account for them appropriately.

How might investigate those sources of heterogeneity in the first place? Should we?

Senn, again: “[I]n assuming that the treatment effect acts identically for each patient, the statistician is simply adopting the simplest model consistent with the data: the statistical application of Occam’s razor….[M]uch of the hype regarding pharmacogenomics is posited on the false assumption that it has been demonstrated for most indications that patients respond differently to treatment. In fact, for most indications this is not known to be true because the types of trial that would be capable of demonstrating it have not been run.”

While Stephen and I agree that genomics is a fairly rotten first-stop in trying to uncover potential sources of heterogeneity, I cannot help but read his general stance as mistaking absence of evidence for evidence of absence. Surely just because “the types of trials that would be capable of demonstrating [heterogeneity]” isn’t a reason *not* to run such studies. Or even to poke around in our data to see if there should happen to be such evidence!

Subgroup differences are a chief observational mechanism by which we can glean hints about the physiological mechanisms underpinning our pharmaceuticals. Spot the outliers and look into what sets them apart. Does it always work: no. Is it worth doing? I think so.

This POV also has a long history, starting with French physician and physiologist Claude Bernard, who argued back in 1927 that statistics of efficacy alone “teach absolutely nothing about the mode of action of medicine nor the mechanics of cure in whom the remedy may have taken effect.” In a 1968 statistics textbook Lancelot Hogben elaborates on the point: “What Bernard rightly rejects is the now widely current practice of publishing as a discovery what is at best an encouragement to further examination.”

Discouragingly, this disinterest in “further examination” into “modes of action” and “mechanics of the cure” is perhaps a *motivated* disinterest. As I wrote in another essay “less knowledge about who specifically benefits from a drug can be to the advantage of the drug-maker so long as it is shown to be safe and effective on average, because they can then market it to more people. Lack of specificity in the target population is great for business.”

Senn himself acknowledges the business-case for Occam’s razor:

“If the treatment effect in a given subgroup is larger than the trial average, it will be smaller than average in another subgroup…It may be, of course, that such analysis can suggest in what sort of patients future trials might be run. This has two consequences. First, the potential market is less than supposed originally. Second, convincing proof of the efficacy of the drug, even in this subgroup, lies with future trials. It might be argued that even if a treatment is efficacious as a whole there is no proof of its efficacy in subgroups. This is, of course, true. However, believing a priori that subgroup differences will be relatively unimportant and continuing to concentrate on the results of a trial as a whole constitutes a consistent position. Looking for subgroup differences represents a retreat from this position and is potentially dangerous. It ought to be taken as an admission of a lack of confidence in the pooled estimate.“

We see that the blocked design gets no benefit from the regression adjustment — because the blocking has already leveraged the twin pair indictor implicitly. Meanwhile, the naive (no blocking) design benefits tremendously from accommodating the twin pair indictor variable (ex post), achieving nearly (but not quite) the same variance reduction as if the blocking had been done in advance.

Note: This simulation iterates over experiments with the same (homogeneous) treatment effect, but different hypothetical pairs of twins, with varying twin-specific baselines. This reflects a focus on external validity rather than internal validity for a fixed set of twin pairs; a simulation examining that would want to hold fixed the twin-specific baselines and only randomize over treatment assignment…which leads to somewhat less pretty histograms :-)

1. David Blackwell, "Basic Statistics".

An absolute gem of a book, teaching intro stats the Bayesian way.

2. Jim Berger, "Statistical Decision Theory and Bayesian Analysis".

Ironically, one of the most famous Bayesian is actually a frequentist in some sense (at least I concluded so the more conversations I had with him).

3. Mark Schervish, "Theory of Statistics".

This book gives equal coverage to the two dominant paradigms and in so doing, gives readers a great basis for deciding for themselves what Bayes is all about.

4. John Hartigan, "Bayes Theory"

A bit more mathematical in places, but the introduction alone is worth the price of admission. (I love it so much I'll probably dedicate a whole post to it in the near future.)

5. Peter Hoff, "A First Course in Bayesian Statistical Methods"

I've used this text in a course I teach for many years. Highly practical and concise.

6. Christian Robert, "The Bayesian Choice"

Great coverage of the foundational ideas in a relatively accessible style.

7. Bernardo and Smith, "Bayesian Theory”

This was "the Bible" during my Duke Statistics grad school days.

8. Markov Chain Monte Carlo: Stochastic Simulation for Bayesian Inference.

A go-to reference for modern Bayesian computation.

9. West and Harrison, "Bayesian Forecasting and Dynamic Linear Models".

This book is so good that the Appendices alone are fantastic.

10. Rossi, Allenby, and McCulloch, "Bayesian Statistics and Marketing”.

A nice introduction to applied Bayesian econometrics.

11. Gelman, et al. "Bayesian Data Analysis"

Many people's first and last book on Bayesian inference, but not my personal favorite.

12. Richard T. Cox, "The Algebra of Probable Inference".

And now we start to get into the hardcore subjectivist stuff.

13. E.T. Jaynes, "Probability Theory: The Logic of Science".

Brilliant and polemical. Don't start here unless you want to start a fight.

14. Richard Jeffrey, "Subjective Probability: The Real Thing".

A philosophy book with insights for anyone wanting to learn from data under uncertainty.

15. Leonard "Jimmie" Savage, "The Foundations of Statistics".

Proof that some very smart people thought a Bayesian approach made a lot of sense. David Blackwell has explained that it was Savage that converted him :-)

16. I.J. Good, “Good Thinking: The Foundations of Probability and Its Applications”.

In which the author famously enumerates all the different flavors of Bayesian that he recognizes as possible.

17. Box and Tiao, "Bayesian Inference in Statistical Analysis".

18. Edward Leamer, "Specification Searches: Ad Hoc Inference with Nonexperimental Data".

One of my personal favorites, from the author of the famous “Taking the Con out of Econometrics.”

19. Raiffa and Schlaifer, "Applied Statistical Decision Theory".

In which conjugate models are developed thoroughly because Harvard B-school students couldn’t be bothered with calculus.

20. Morris DeGroot, “Optimal Statistical Decision”.

I used this one heavily studying for my prelim exam (both times lol).

21. Bruno de Finetti, “Theory of Probability”.

I mostly learned my de Finetti from second-hand expositions, but going to the source is never a bad idea.

22. Anthony O'Hagan, “Bayesian Inference”.

Another one I kept on my desk during graduate school.

23. Richard McElreath, “Statistical Rethinking: A Bayesian Course with Examples in R and STAN”.

This one is added to the list by popular demand and is one I need to be sure to read myself now that I know about it. Definitely a crowd favorite.

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 a lot larger 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. This is usually 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, wanting 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, imo, is a focus on the prior predictive distribution: the range of possible data sets we believe we might see. So my prescriptive advice: do your modeling at the level of 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 and tune them 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 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/