*Journal of Causal Inference*

by Judea Pearl

__Introduction__

This collection of 14 short articles represents adventurous ideas and semi-heretical thoughts that emerged when, in 2013, I was given the opportunity to edit a fun section of the *Journal of Causal Inference* called “Causal, Casual, and Curious.”

This direct contact with readers, unmediated by editors or reviewers, had a healthy liberating effect on me and has unleashed some of my best, perhaps most mischievous explorations. I thank the editors of the *Journal of Causal Inference* for giving me this opportunity to undertake this adventure and for trusting me to manage it as prudently as I could.

May 2013

“Linear Models: A Useful “Microscope” for Causal Analysis,” *Journal of Causal Inference*, 1(1): 155–170, May 2013.

Abstract: This note reviews basic techniques of linear path analysis and demonstrates, using simple examples, how causal phenomena of non-trivial character can be understood, exemplified and analyzed using diagrams and a few algebraic steps. The techniques allow for swift assessment of how various features of the model impact the phenomenon under investigation. This includes: Simpson’s paradox, case-control bias, selection bias, missing data, collider bias, reverse regression, bias amplification, near instruments, and measurement errors.

December 2013

“The Curse of Free-will and the Paradox of Inevitable Regret” *Journal of Causal Inference*, 1(2): 255-257, December 2013.

Abstract: The paradox described below aims to clarify the principles by which population data can be harnessed to guide personal decision making. The logic that permits us to infer counterfactual quantities from a combination of experimental and observational studies gives rise to situations in which an agent knows he/she will regret whatever action is taken.

March 2014

“Is Scientific Knowledge Useful for Policy Analysis? A Peculiar Theorem says: No,” *Journal of Causal Inference*, 2(1): 109–112, March 2014.

Abstract: Conventional wisdom dictates that the more we know about a problem domain the easier it is to predict the effects of policies in that domain. Strangely, this wisdom is not sanctioned by formal analysis, when the notions of “knowledge” and “policy” are given concrete definitions in the context of nonparametric causal analysis. This note describes this peculiarity and speculates on its implications.

September 2014

“Graphoids over counterfactuals” *Journal of Causal Inference*, 2(2): 243-248, September 2014.

Abstract: Augmenting the graphoid axioms with three additional rules enables us to handle independencies among observed as well as counterfactual variables. The augmented set of axioms facilitates the derivation of testable implications and ignorability conditions whenever modeling assumptions are articulated in the language of counterfactuals.

March 2015

“Conditioning on Post-Treatment Variables,” *Journal of Causal Inference*, 3(1): 131-137, March 2015. Includes Appendix (appended to published version).

Abstract: In this issue of the Causal, Casual, and Curious column, I compare several ways of extracting information from post-treatment variables and call attention to some peculiar relationships among them. In particular, I contrast do-calculus conditioning with counterfactual conditioning and discuss their interpretations and scopes of applications. These relationships have come up in conversations with readers, students and curious colleagues, so I will present them in a question–answers format.

September 2015

“Generalizing experimental findings,” *Journal of Causal Inference*, 3(2): 259-266, September 2015.

Abstract: This note examines one of the most crucial questions in causal inference: “How generalizable are randomized clinical trials?” The question has received a formal treatment recently, using a non-parametric setting, and has led to a simple and general solution. I will describe this solution and several of its ramifications, and compare it to the way researchers have attempted to tackle the problem using the language of ignorability. We will see that ignorability-type assumptions need to be enriched with structural assumptions in order to capture the full spectrum of conditions that permit generalizations, and in order to judge their plausibility in specific applications.

March 2016

“The Sure-Thing Principle,” *Journal of Causal Inference*, 4(1): 81-86, March 2016.

Abstract: In 1954, Jim Savage introduced the Sure Thing Principle to demonstrate that preferences among actions could constitute an axiomatic basis for a Bayesian foundation of statistical inference. Here, we trace the history of the principle, discuss some of its nuances, and evaluate its significance in the light of modern understanding of causal reasoning.

September 2016

“Lord’s Paradox Revisited — (Oh Lord! Kumbaya!),” *Journal of Causal Inference*, Published Online 4(2): September 2016.

Abstract: Among the many peculiarities that were dubbed “paradoxes” by well meaning statisticians, the one reported by Frederic M. Lord in 1967 has earned a special status. Although it can be viewed, formally, as a version of Simpson’s paradox, its reputation has gone much worse. Unlike Simpson’s reversal, Lord’s is easier to state, harder to disentangle and, for some reason, it has been lingering for almost four decades, under several interpretations and re-interpretations, and it keeps coming up in new situations and under new lights. Most peculiar yet, while some of its variants have received a satisfactory resolution, the original version presented by Lord, to the best of my knowledge, has not been given a proper treatment, not to mention a resolution.

The purpose of this paper is to trace back Lord’s paradox from its original formulation, resolve it using modern tools of causal analysis, explain why it resisted prior attempts at resolution and, finally, address the general methodological issue of whether adjustments for preexisting conditions is justified in group comparison applications.

March 2017

“A Linear `Microscope’ for Interventions and Counterfactuals,” *Journal of Causal Inference*, Published Online 5(1): 1-15, March 2017.

Abstract: This note illustrates, using simple examples, how causal questions of non-trivial character can be represented, analyzed and solved using linear analysis and path diagrams. By producing closed form solutions, linear analysis allows for swift assessment of how various features of the model impact the questions under investigation. We discuss conditions for identifying total and direct effects, representation and identification of counterfactual expressions, robustness to model misspecification, and generalization across populations.

September 2017

“Physical and Metaphysical Counterfactuals” Revised version, *Journal of Causal Inference*, 5(2): September 2017.

Abstract: The structural interpretation of counterfactuals as formulated in Balke and Pearl (1994a,b) [1, 2] excludes disjunctive conditionals, such as “had X been x_{1} or x_{2},” as well as disjunctive actions such as do(X = x_{1} or X = x_{2}). In contrast, the closest-world interpretation of counterfactuals (e.g. Lewis (1973a) [3]) assigns truth values to all counterfactual sentences, regardless of the logical form of the antecedent. This paper leverages “imaging”–a process of “mass-shifting” among possible worlds, to define disjunction in structural counterfactuals. We show that every imaging operation can be given an interpretation in terms of a stochastic policy in which agents choose actions with certain probabilities. This mapping, from the metaphysical to the physical, allows us to assess whether metaphysically-inspired extensions of interventional theories are warranted in a given decision making situation.

March 2018

“What is Gained from Past Learning” *Journal of Causal Inference*, 6(1), Article 20180005, https://doi.org/10.1515/jci-2018-0005, March 2018.

Abstract: We consider ways of enabling systems to apply previously learned information to novel situations so as to minimize the need for retraining. We show that theoretical limitations exist on the amount of information that can be transported from previous learning, and that robustness to changing environments depends on a delicate balance between the relations to be learned and the causal structure of the underlying model. We demonstrate by examples how this robustness can be quantified.

September 2018

“Does Obesity Shorten Life? Or is it the Soda? On Non-manipulable Causes,” *Journal of Causal Inference*, 6(2), online, September 2018.

Abstract: Non-manipulable factors, such as gender or race have posed conceptual and practical challenges to causal analysts. On the one hand these factors do have consequences, and on the other hand, they do not fit into the experimentalist conception of causation. This paper addresses this challenge in the context of public debates over the health cost of obesity, and offers a new perspective, based on the theory of Structural Causal Models (SCM).

March 2019

“On the interpretation of do(x),” *Journal of Causal Inference*, 7(1), online, March 2019.

Abstract: This paper provides empirical interpretation of the *do(x)* operator when applied to non-manipulable variables such as race, obesity, or cholesterol level. We view *do(x)* as an ideal intervention that provides valuable information on the effects of manipulable variables and is thus empirically testable. We draw parallels between this interpretation and ways of enabling machines to learn effects of untried actions from those tried. We end with the conclusion that researchers need not distinguish manipulable from non-manipulable variables; both types are equally eligible to receive the *do(x)* operator and to produce useful information for decision makers.

September 2019

“Sufficient Causes: On Oxygen, Matches, and Fires,” *Journal of Causal Inference*, AOP, https://doi.org/10.1515/jci-2019-0026, September 2019.

Abstract: We demonstrate how counterfactuals can be used to compute the probability that one event was/is a sufficient cause of another, and how counterfactuals emerge organically from basic scientific knowledge, rather than manipulative experiments. We contrast this demonstration with the potential outcome framework and address the distinction between causes and enablers.

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The note below offers brief comments on Imbens’s five major claims regarding the superiority of potential outcomes [PO] vis a vis directed acyclic graphs [DAGs].

These five claims are articulated in Imbens’s introduction (pages 1-3). [Quoting]:

” … there are five features of the PO framework that may be behind its current popularity in economics.”

I will address them sequentially, first quoting Imbens’s claims, then offering my counterclaims.

I will end with a comment on Imbens’s final observation, concerning the absence of empirical evidence in a “realistic setting” to demonstrate the merits of the DAG approach.

Before we start, however, let me clarify that there is no such thing as a “DAG approach.” Researchers using DAGs follow an approach called Structural Causal Model (SCM), which consists of functional relationships among variables of interest, and of which DAGs are merely a qualitative abstraction, spelling out the arguments in each function. The resulting graph can then be used to support inference tools such as d-separation and do-calculus. Potential outcomes are relationships *derived* from the structural model and several of their properties can be elucidated using DAGs. These interesting relationships are summarized in chapter 7 of (Pearl, 2009a) and in a Statistical Survey overview (Pearl, 2009c)

Imbens’s Claim # 1*“First, there are some assumptions that are easily captured in the PO framework relative to the DAG approach, and these assumptions are critical in many identification strategies in economics. Such assumptions include**monotonicity ([Imbens and Angrist, 1994]) and other shape restrictions such as convexity or concavity ([Matzkin et al.,1991, Chetverikov, Santos, and Shaikh, 2018, Chen, Chernozhukov, Fernández-Val, Kostyshak, and Luo, 2018]). The instrumental variables setting is a prominent example, and I will discuss it in detail in Section 4.2.”*

Pearl’s Counterclaim # 1

It is logically impossible for an assumption to be “easily captured in the PO framework” and not simultaneously be “easily captured” in the “DAG approach.” The reason is simply that the latter embraces the former and merely enriches it with graph-based tools. Specifically, SCM embraces the counterfactual notation *Y _{x}* that PO deploys, and does not exclude any concept or relationship definable in the PO approach.

Take monotonicity, for example. In PO, monotonicity is expressed as

*Y _{x}* (

In the DAG approach it is expressed as:

*Y _{x}* (

(Taken from Causality pages 291, 294, 398.)

The two are identical, of course, which may seem surprising to PO folks, but not to DAG folks who know how to derive the counterfactuals *Y _{x }*from structural models. In fact, the derivation of counterfactuals in

terms of structural equations (Balke and Pearl, 1994) is considered one of the fundamental laws of causation in the SCM framework see (Bareinboim and Pearl, 2016) and (Pearl, 2015).

Imbens’s Claim # 2

Pearl’s Counterclaim #2

Not so. The term “potential outcome” is a late comer to the economics literature of the 20th century, whose native vocabulary and natural primitives were functional relationships among variables, not potential outcomes. The latters are defined in terms of a “treatment assignment” and hypothetical outcome, while the formers invoke only observable variables like “supply” and “demand”. Don Rubin cited this fundamental difference as sufficient reason for shunning structural equation models, which he labeled “bad science.”

While it is possible to give PO interpretation to structural equations, the interpretation is both artificial and convoluted, especially in view of PO insistence on manipulability of causes. Haavelmo, Koopman and Marschak would not hesitate for a moment to write the structural equation:

*Damage = f (earthquake intensity, other factors).*

PO researchers, on the other hand, would spend weeks debating whether earthquakes have “treatment assignments” and whether we can legitimately estimate the “causal effects” of earthquakes. Thus, what Imbens perceives as a helpful distinction is, in fact, an unnecessary restriction that suppresses natural scientific discourse. See also (Pearl, 2018; 2019).

Imbens’s Claim #3*“Third, many of the currently popular identification strategies focus on **models with relatively few (sets of) variables, where identification **questions have been worked out once and for all.”*

Pearl’s Counterclaim #3

First, I would argue that this claim is actually false. Most IV strategies that economists use are valid “conditional on controls” (see examples listed in Imbens (2014)) and the criterion that distinguishes “good controls” from “bad controls” is not trivial to articulate without the help of graphs. (See, A Crash Course in Good and Bad Control). It can certainly not be discerned “once and for all”.

Second, even if economists are lucky to guess “good controls,” it is still unclear whether they focus on relatively few variables because, lacking graphs, they cannot handle more variables, or do they refrain from using graphs to hide the opportunities missed by focusing on few pre-fabricated, “once and for all” identification strategies.

I believe both apprehensions play a role in perpetuating the graph-avoiding subculture among economists. I have elaborated on this question here: (Pearl, 2014).

Imbens’s Claim # 4*“Fourth, the PO framework lends itself well to accounting for treatment **effect heterogeneity in estimands ([Imbens and Angrist, 1994, Sekhon and **Shem-Tov, 2017]) and incorporating such heterogeneity in estimation and the design of optimal policy functions ([Athey and Wager, 2017, Athey, **Tibshirani, Wager, et al., 2019, Kitagawa and Tetenov, 2015]).”*

Pearl’s Counterclaim #4

Indeed, in the early 1990s, economists felt ecstatic liberating themselves from the linear tradition of structural equation models and finding a framework (PO) that allowed them to model treatment effect heterogeneity.

However, whatever role treatment heterogeneity played in this excitement should have been amplified ten-fold in 1995, when completely non parametric structural equation models came into being, in which non-linear interactions and heterogeneity were assumed a priori. Indeed, the tools developed in the econometric literature cover only a fraction of the treatment-heterogeneity tasks that are currently managed by SCM. In particular, the latter includes such problems as “necessary and sufficient” causation, mediation, external validity, selection bias and more.

Speaking more generally, I find it odd for a discipline to prefer an “approach” that rejects tools over one that invites and embraces tools.

Imbens’s claim #5*“Fifth, the PO approach has traditionally connected well with design, **estimation, and inference questions. From the outset Rubin and his coauthors provided much guidance to researchers and policy makers for practical implementation including inference, with the work on the propensity score ([Rosenbaum and Rubin, 1983b]) an influential example.”*

Pearl’s Counterclaim #5

The initial work of Rubin and his co-authors has indeed provided much needed guidance to researchers and policy makers who were in a state of desperation, having no other mathematical notation to express causal questions of interest. That happened because economists were not aware of the counterfactual content of structural equation models, and of the non-parametric extension of those models.

Unfortunately, the clumsy and opaque notation introduced in this initial work has become a ritual in the PO framework that has prevailed, and the refusal to commence the analysis with meaningful assumptions has led to several blunders and misconceptions. One such misconception has been propensity score analysis which researchers have taken as a tool for reducing confounding bias. I have elaborated on this misguidance in *Causality*, Section 11.3.5, “Understanding Propensity Scores” (Pearl, 2009a).

Imbens’s final observation: Empirical Evidence *“Separate from the theoretical merits of the two approaches, another reason for the lack of adoption in economics is that the DAG literature has not shown much evidence of the benefits for empirical practice in settings that are important in economics. The potential outcome studies in MACE, and the chapters in [Rosenbaum, 2017], CISSB and MHE have detailed empirical examples of the various identification strategies proposed. In realistic settings they demonstrate the merits of the proposed methods and describe in detail the corresponding estimation and inference methods. In contrast in the DAG literature, TBOW, [Pearl, 2000], and [Peters, Janzing, and Schölkopf, 2017] have no substantive empirical examples, focusing largely on identification questions in what TBOW refers to as “toy” models. Compare the lack of impact of the DAG literature in economics with the recent embrace of regression discontinuity designs imported from the psychology literature, or with the current rapid spread of the machine learning methods from computer science, or the recent quick adoption of synthetic control methods [Abadie, Diamond, and Hainmueller, 2010]. All came with multiple concrete examples that highlighted their benefits over traditional methods. In the absence of such concrete examples the toy models in the DAG literature sometimes appear to be a set of solutions in search of problems, rather than a set of solutions for substantive problems previously posed in social sciences.”*

Pearl’s comments on: Empirical Evidence

There is much truth to Imbens’s observation. The PO excitement that swept natural experimentalists in the 1990s came with outright rejection of graphical models. The hundreds, if not thousands, of empirical economists who plunged into empirical work, were warned repeatedly that graphical models may be “ill-defined,” “deceptive,” and “confusing,” and structural models have no scientific underpinning (see (Pearl, 1995; 2009b)). Not a single paper in the econometric literature has acknowledged the existence of SCM as an alternative or complementary approach to PO.

The result has been the exact opposite of what has taken place in epidemiology where DAGs became a second language to both scholars and field workers, [Due in part to the influential 1999 paper by Greenland, Pearl and Robins.] In contrast, PO-led economists have launched a massive array of experimental programs lacking graphical tools for guidance. I would liken it to a Phoenician armada exploring the Atlantic coast in leaky boats and no compass to guide its way.

This depiction might seem pretentious and overly critical, considering the pride with which natural experimentalists take in the results of their studies (though no objective verification of validity can be undertaken.) Yet looking back at the substantive empirical examples listed by Imbens, one cannot but wonder how much more credible those studies could have been with graphical tools to guide the way. These include a friendly language to communicate assumptions, powerful means to test their implications, and ample opportunities to uncover new natural experiments (Brito and Pearl, 2002).

Summary and Recommendation

The thrust of my reaction to Imbens’s article is simple:

*It is unreasonable to prefer an “approach” that rejects tools over one that invites and embraces tools.*

Technical comparisons of the PO and SCM approaches, using concrete examples, have been published since 1993 in dozens of articles and books in computer science, statistics, epidemiology, and social science, yet none in the econometric literature. Economics students are systematically deprived of even the most elementary graphical tools available to other researchers, for example, to determine if one variable is independent of another given a third, or if a variable is a valid IV given a set *S* of observed variables.

This avoidance can no longer be justified by appealing to “We have not found this [graphical] approach to aid the drawing of causal inferences” (Imbens and Rubin, 2015, page 25).

To open an effective dialogue and a genuine comparison between the two approaches, I call on Professor Imbens to assume leadership in his capacity as Editor in Chief of *Econometrica* and invite a comprehensive survey paper on graphical methods for the front page of his Journal. This is how creative editors move their fields forward.

Brito, C. and Pearl, J. “General instrumental variables,” In A. Darwiche and N. Friedman (Eds.), Uncertainty in Artificial Intelligence, *Proceedings of **the Eighteenth Conference*, Morgan Kaufmann: San Francisco, CA, 85-93, August 2002.

Bareinboim, E. and Pearl, J. “Causal inference and the data-fusion problem,” *Proceedings of the National Academy of Sciences*, 113(27): 7345-7352, 2016.

Greenland, S., Pearl, J., and Robins, J. “Causal diagrams for epidemiologic research,” *Epidemiology,* Vol. 1, No. 10, pp. 37-48, January 1999.

Pearl, J. “Causal diagrams for empirical research,” (With Discussions), *Biometrika*, 82(4): 669-710, 1995.

Pearl, J. “Understanding Propensity Scores” in J. Pearl’s *Causality: Models, **Reasoning, and Inference*, Section 11.3.5, Second edition, NY: Cambridge University Press, pp. 348-352, 2009a.

Pearl, J. “Myth, confusion, and science in causal analysis,” University of California, Los Angeles, Computer Science Department, Technical Report R-348, May 2009b.

Pearl, J. “Causal inference in statistics: An overview” Statistics Surveys, Vol. 3, 96–146, 2009c.

Pearl, J. “Are economists smarter than epidemiologists? (Comments on Imbens’s recent paper),” *Causal Analysis in Theory and Practice Blog*, October 27, 2014.

Pearl, J. “Trygve Haavelmo and the Emergence of Causal Calculus,” *Econometric Theory*, 31: 152-179, 2015.

Pearl, J. “Does obesity shorten life? Or is it the Soda? On non-manipulable causes,” *Journal of Causal Inference*, Causal, Casual, and Curious Section, 6(2), online, September 2018.

Pearl, J. “On the interpretation of do(x),” *Journal of Causal Inference*, Causal, Casual, and Curious Section, 7(1), online, March 2019.

Taking a closer look at the analysis of Anders and co-authors, and using their very same examples, we came to quite different conclusions. In those cases, transportability is not immediately inferable in a fully nonparametric structural model for a simple reason: it relies on *functional constraints* on the structural equation of the outcome. Once these constraints are properly incorporated in the analysis, all results flow naturally from the structural model, and selection diagrams prove to be indispensable for thinking about heterogeneity, for extrapolating results across populations, and for protecting analysts from unwarranted generalizations. See details in the full note.

**Scott Mueller and Judea Pearl**

This post introduces readers to Fréchet inequalities using modern visualization techniques and discusses their applications and their fascinating history.

Fréchet inequalities, also known as Boole-Fréchet inequalities, are among the earliest products of the probabilistic logic pioneered by George Boole and Augustus De Morgan in the 1850s, and formalized systematically by Maurice Fréchet in 1935. In the simplest binary case they give us bounds on the probability P(A,B) of two joint events in terms of their marginals P(A) and P(B):

- max{0, P(A) + P(B) − 1} ≤ P(A,B) ≤ min{P(A), P(B)}

The reason for revisiting these inequalities 84 years after their first publication is two-fold:

- They play an important role in machine learning and counterfactual reasoning (Ang and Pearl, 2019)
- We believe it will be illuminating for colleagues and students to see these probability bounds displayed using modern techniques of dynamic visualization

Fréchet bounds have wide application, including logic (Wagner, 2004), artificial intelligence (Wise and Henrion, 1985), statistics (Rüschendorf, 1991), quantum mechanics (Benavoli et al., 2016), and reliability theory (Collet, 1996). In counterfactual analysis, they come into focus when we have experimental results under treatment (X = x) as well as denial of treatment (X = x’) and our interests lie in individuals who are responsive to treatment, namely those who will respond if exposed to treatment and will not respond under denial of treatment. Such individuals carry different names depending on the applications. They are called compliers, beneficiaries, respondents, gullibles, influenceable, persuadable, malleable, pliable, impressionable, susceptive, overtrusting, or dupable. And as the reader can figure out, the applications in marketing, sales, recruiting, product development, politics, and health science is enormous.

Although narrower bounds can be obtained when we have both observational and experimental data (Ang and Pearl, 2019; Tian and Pearl, 2000), Fréchet bounds are nevertheless informative when it comes to concluding responsiveness from experimental data alone.

Below we present dynamic visualizations of Fréchet inequalities in various forms for events A and B. Hover or tap on an ⓘ icon for a short description of each type of plot. Click or tap on a type of plot to see an animation of the current plot morphing into the new plot. Hover or tap on the plot itself to see an informational popup of that location.

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The plots visualize probability bounds of two events using logical conjunction, P(A,B), and logical disjunction, P(A∨B), with their marginals, P(A) and P(B), as axes on the unit square. Bounds for particular values of P(A) and P(B) can be seen by clicking on a type of bounds next to conjunction or disjunction and tracing the position on the plot to a color between blue and red. The color bar next to the plot indicates the probability. Clicking a different type of bounds animates the plot to demonstrate how the bounds changes. Hovering over or tapping on the plot reveals more information about the position being pointed at.

The gap between upper bounds and lower bounds gets vanishingly narrow near the edges of the unit square, which means that we can accurately determine the probability of the intersection given the probability of the marginal probabilities. The range plots make this very clear and they are the exact same plots for both P(A,B) and P(A∨B). Notice that the center holds the widest gaps. Every plot is symmetric around the P(B) = P(A) diagonal, this should be expected as P(A) and P(B) play interchangeable rolls in Fréchet inequalities.

Assume you measure the probabilities of your friends liking math and liking chocolate. Let A stand for the event that a friend picked at random likes math and B for the event that a friend picked at random likes chocolate. It turns out P(A) = 0.9 (almost all of your friends like math!) and P(B) = 0.3. You want to know the probability of a friend liking both math and chocolate, in other words you want to know P(A,B). If knowing whether a friend likes math doesn’t affect the probability they like chocolate, then events A and B are independent and we can get the exact value for P(A,B). This is a logical conjunction of A and B, so next to “Conjunction” above the plot, click on “Independent.” Trace the location in the plot where the horizontal axis, P(A), is at 0.9 and the vertical axis, P(B), is at 0.3. You’ll see P(A,B) is about 0.27 according to the color bar on the right.

However, maybe enjoying chocolate makes it more likely you’ll enjoy math. The caffeine in chocolate could have something to do with this. In this case, A and B are dependent and we may not be able to get an exact value for P(A,B) without more information. Click on “Combined” next to “Conjunction”. Now trace (0.9,0.3) again on the plot. You’ll see P(A,B) is between 0.2 and 0.3. Without knowing how dependent A and B are, we get fairly narrow bounds for the probability a friend likes both math and chocolate.

Suppose we are conducting a marketing experiment and find 20% of customers will buy if shown advertisement 1, while 45% will buy if shown advertisement 2. We want to know how many customers will be swayed by advertisement 2 over advertisement 1. In other words, what percentage of customers buys if shown advertisement 2 and doesn’t buy when shown advertisement 1? To see this in the plot above, let A stand for the event that a customer won’t buy when shown advertisement 1 and B for the event that a customer will buy when shown advertisement 2: P(A) = 100% – 20% = 80% = 0.8 and P(B) = 45% = 0.45. We want to find P(A,B). This joint probability is logical conjunction, so click on “Lower bounds” next to “Conjunction.” Tracing P(A) = 0.8 and P(B) = 0.45 lands in the middle of the blue strip corresponding to 0.2 to 0.3. This is the lower bounds, so P(A,B) ≥ 0.25. Now click on “Upper bounds” and trace again. You’ll find P(A,B) ≤ 0.45. The “Combined” plot allows you to visualize both bounds at the same time. Hovering over or tapping on location (0.8,0.45) will display the complete bounds on any of the plots.

We might think that exactly 45% – 20% = 25% of customers were swayed by advertisement 2, but the plot shows us a range between 25% and 45%. This is because some people may buy if shown advertisement 1 and not buy if shown advertisement 2. As an example, if advertisement 2 convinces an entirely different segment of customers to buy than advertisement 1 does, then none of the 20% of customers who will buy after seeing advertisement 1 would buy if they had seen advertisement 2 instead. In this case, all 45% of the customers who will buy after seeing advertisement 2 are swayed by the advertisement.

Assume that we conduct a controlled randomized experiment (CRT) to evaluate the efficacy of some treatment X on survival Y, and find no effect whatsoever. For example, 10% of treated patients recovered, 90% died, and exactly the same proportions were found in the control group (those who were denied treatment), 10% recovered and 90% died.

Such treatment would no doubt be deemed ineffective by the FDA and other public policy makers. But health scientists and drug makers might be interested in knowing how the treatment affected individual patients: Did it have no effect on ANY individual or, perhaps, cured some and killed others. In the worst case, one can imagine a scenario where 10% of those who died under treatment would have been cured if not treated. Such a nightmarish scenario should surely be of grave concern to health scientists, not to mention patients who are seeking or using the treatment.

Let A stand for the event that patient John would die if given the treatment and B for the event that John would survive if denied treatment. The experimental data tells us that P(A) = 90% and P(B) = 10%. We are interested in the probability that John would die if treated and be cured if not treated, namely P(A,B).

Examining plot 1 we find that P(A,B), the probability that John is among those adversely reacting to the treatment is between zero and 10%. Quite an alarming finding, but not entirely unexpected considering the fact that randomized experiments deal with averages over populations and do not provide us information about an individual’s response. We may wish to ask what experimental results would assure John that he is not among the adversely affected. Examining the “Upper bound” plot we see that to guarantee a probability less than 5%, either P(A) or P(B) must be lower than 5%. This means that the mortality rate under either treatment or no-treatment should be lower than 5%.

In mathematical notation, the general Fréchet inequalities take the form:

- max{0, P(A
_{1}) + P(A_{2}) + … + P(A_{n}) − (n − 1)} ≤ P(A_{1},A_{2},…,A_{n}) ≤ min{P(A_{1}), P(A_{2}), …, P(A_{n})} - max{P(A
_{1}), P(A_{2}), …, P(A_{n})} ≤ P(A_{1}∨A_{2}∨…∨A_{n}) ≤ min{1, P(A_{1}) + P(A_{2}) + … + P(A_{n})}

The binary cases of these inequalities used in the plots are:

- max{0, P(A) + P(B) − 1} ≤ P(A,B) ≤ min{P(A), P(B)}
- max{P(A), P(B)} ≤ P(A∨B) ≤ min{1, P(A) + P(B)}

If events A and B are independent, then we can plot exact values:

- P(A,B) = P(A)·P(B)
- P(A∨B) = P(A) + P(B) – P(A)·P(B)

Maurice Fréchet was a significant French mathematician with contributions to topology of point sets, metric spaces, statistics and probability, and calculus (Wikipedia Contributors, 2019). Fréchet published his proof for the above inequalities in the French journal Fundamenta Mathaticae in 1935 (Fréchet, 1935). During that time, he was Professor and Chair of Differential and Integral Calculus at the Sorbonne (Sack, 2016).

Jacques Fréchet, Maurice’s father, was the head of a school in Paris (O’Connor and Robertson, 2019) while Maurice was young. Maurice then went to secondary school where he was taught math by the legendary French mathematician Jacques Hadamard. Hadamard would soon after become a professor at the University of Bordeaux. Eventually, Hadamard would become Fréchet’s advisor for his doctorate. An educator like his father, Maurice was a schoolteacher in 1907, a lecturer in 1908, and then a professor in 1910 (Bru and Hertz, 2001). Probability research came later in his life. Unfortunately, his work wasn’t always appreciated as the renowned Swedish mathematician Harald Cramér wrote (Bru and Hertz, 2001):

“In early years Fréchet had been an outstanding mathematician, doing pathbreaking work in functional analysis. He had taken up probabilistic work at a fairly advanced age, and I am bound to say that his work in this field did not seem very impressive to me.”

Nevertheless, Fréchet would go on to become very influential in probability and statistics. As a great response to Cramér’s former criticism, an important bound is named after both Fréchet and Cramér, the Fréchet–Darmois–Cramér–Rao inequality (though more commonly known as *Cramér–Rao bound*)!

The reason Fréchet inequalities are also known as Boole-Fréchet inequalities is that George Boole published a proof of the conjunction version of the inequalities in his 1854 book *An Investigation of the Laws of Thought* (Boole, 1854). In chapter 19, Boole first showed the following:

Major limit of n(xy) = least of values n(x) and n(y)

Minor limit of n(xy) = n(x) + n(y) – n(1).

The terms n(xy), n(x), and n(y) are the number of occurrences of xy, x, and y, respectively. The term n(1) is the total number of occurrences. The reader can see that dividing all n-terms by n(1) yields the binary Fréchet inequalities for P(x,y). Boole then arrives at two general conclusions:

1st. The major numerical limit of the class represented by any constituent will be found by prefixing n separately to each factor of the constituent, and taking the least of the resulting values.

2nd. The minor limit will be found by adding all the values above mentioned together, and subtracting from the result as many, less one, times the value of n(1).

This result was an exercise that was part of an ambitious scheme which he describes in “Proposition IV” of chapter 17 as:

Given the probabilities of any system of events; to determine by a general method the consequent or derived probability of any other event.

We know now that Boole’s task is super hard and, even today, we are not aware of any software that accomplishes his plan on any sizable number of events. The Boole-Fréchet inequalities are a tribute to his vision.

Boole’s conjunction inequalities preceded Fréchet’s by 81 years, so why aren’t these known as Boole inequalities? One reason is Fréchet showed, for both conjunction and disjunction, that they are the narrowest possible bounds when only the marginal probabilities are known (Halperin, 1965).

Boole wrote a footnote in chapter 19 of his book that Augustus De Morgan, who was a collaborator of Boole’s, first came up with the minor limit (lower bound) of the conjunction of two variables:

the minor limit of nxy is applied by Professor De Morgan, by whom it appears to have been first given, to the syllogistic form:

Most men in a certain company have coats.

Most men in the same company have waistcoats.

Therefore some in the company have coats and waistcoats.

De Morgan wrote about this syllogism in his 1859 paper “On the Syllogism, and On the Logic of Relations” (De Morgan, 1859). Boole and De Morgan became lifelong friends after Boole wrote to him in 1842 (Burris, 2010). Although De Morgan was Boole’s senior and published a book on probability in 1835 and on “Formal Logic” in 1847, he never reached Boole’s height in symbolic logic.

Predating Fréchet, Boole, and De Morgan is Charles Stanhope’s Demonstrator logic machine, an actual physical device, that calculates binary Fréchet inequalities for both conjunction and disjunction. Robert Harley wrote an article in 1879 in Mind: A Quarterly Review of Psychology and Philosophy (Harley, 1879) that described Stanhope’s instrument. In addition to several of these machines having been created, Stanhope had an unfinished manuscript of logic he wrote between 1800 and 1815 describing rules and construction of the machine for “discovering consequences in logic.” In Stanhope’s manuscript, he describes calculating the lower bound of conjunction with α, β, and μ, where α and β represent all, some, most, fewest, a number, or a definite ratio of part to whole (but not none), and μ is unity: “α + β – μ measures the extent of the consequence between A and B.” This gives the “minor limit.” Some examples are given by Harley. One of them is that some of 5 pictures hanging on the north side and some of 5 pictures are portraits tells us nothing about how many pictures are portraits hanging in the north. But if 3/5 are hanging in the north and 4/5 are portraits, then at least 3/5 + 4/5 – 1 = 2/5 are portraits on the north side. Similarly, with De Morgan’s coats syllogism, “(most + most – all) men = some men” have both coats and waistcoats.

The Demonstrator logic machine works by sliding red transparent glass from the right over a separate gray wooden slide from the left. The overlapping portion will look dark red. The slides represent probabilities, P(A) and P(B), where sliding the entire distance of the middle square represents a probability of 1. The reader can verify that the dark red (overlap) is equivalent to the lower bound, P(A) + P(B) – 1. To find the “major limit,” or upper bound, simply slide the red transparent glass from the left on top of the gray slide. Dark red will appear as the length of the shorter of the two slides, min{P(A), P(B)}!

Wikipedia Contributors, “Fréchet inequalities,” *en.wikipedia.org*, para. 1, Aug. 4, 2019. [Online]. Available: https://en.wikipedia.org/wiki/Fréchet_inequalities. [Accessed Oct. 7, 2019].

Ang Li and Judea Pearl, “Unit Selection Based on Counterfactual Logic,” UCLA Cognitive Systems Laboratory, Technical Report (R-488), June 2019. In *Proceedings of the Twenty-Eighth International Joint Conference on Artificial Intelligence (IJCAI-19)*, 1793-1799, 2019. [Online]. Available: http://ftp.cs.ucla.edu/pub/stat_ser/r488-reprint.pdf. [Accessed Oct. 11, 2019].

Carl G. Wagner, “Modus tollens probabilized,” *Journal for the Philosophy of Science*, vol. 55, pp. 747–753, 2004. [Online serial]. Available: http://www.math.utk.edu/~wagner/papers/2004.pdf. [Accessed Oct. 7, 2019].

Ben P. Wise and Max Henrion, “A Framework for Comparing Uncertain Inference Systems to Probability,” In Proc. of the First Conference on Uncertainty in Artificial Intelligence (UAI1985), 1985. [Online]. Available: https://arxiv.org/abs/1304.3430. [Accessed Oct. 7, 2019].

L. Rüschendorf, “Fréchet-bounds and their applications,” *Advances in Probability Distributions with Given Marginals, Mathematics and Its Applications*, pp. 151–187, 1991. [Online]. Available: https://books.google.com/books?id=4uNCdVrrw2cC. [Accessed Oct. 7, 2019].

Alessio Benavoli, Alessandro Facchini, and Marco Zaffalon, “Quantum mechanics: The Bayesian theory generalised to the space of Hermitian matrices,” *Physics Review A*, vol. 94, no. 4, pp. 1-26, Oct. 10, 2016. [Online]. Available: https://arxiv.org/abs/1605.08177. [Accessed Oct. 7, 2019].

J. Collet, “Some remarks on rare-event approximation,” *IEEE Transactions on Reliability*, vol. 45, no. 1, pp. 106-108, Mar 1996. [Online]. Available: https://ieeexplore.ieee.org/document/488924. [Accessed Oct. 7, 2019].

Wikipedia Contributors, “Maurice René Fréchet,” *en.wikipedia.org*, para. 1, Oct. 7, 2019. [Online]. Available: https://en.wikipedia.org/wiki/Maurice_René_Fréchet. [Accessed Oct. 7, 2019].

Maurice Fréchet, “Généralisations du théorème des probabilités totales,” *Fundamenta Mathematicae*, vol. 25, no. 1, pp. 379–387, 1935. [Online]. Available: http://matwbn.icm.edu.pl/ksiazki/fm/fm25/fm25132.pdf. [Accessed Oct. 7, 2019].

Harald Sack, “Maurice René Fréchet and the Theory of Abstract Spaces,” *SciHi Blog*, Sept. 2016. [Online]. Available: http://scihi.org/maurice-rene-frechet/. [Accessed Oct. 7, 2019].

J J O’Connor and E F Robertson, “René Maurice Fréchet,” *MacTutor History of Mathematics archive*. [Online]. Available: http://www-groups.dcs.st-and.ac.uk/history/Biographies/Frechet.html. [Accessed Oct. 7, 2019].

B. Bru and S. Hertz, “Maurice Fréchet,” *Statisticians of the Centuries*, pp. 331-334, Jan. 2001. [Online]. Available: https://books.google.com/books?id=6DD1FKq6fFoC&pg=PA331. [Accessed Oct. 7, 2019].

“Fréchet, Maurice,” *Encyclopedia of Mathematics*. [Online]. Available: https://www.encyclopediaofmath.org/index.php/Fr%C3%A9chet,_Maurice. [Accessed Oct. 7, 2019].

George Boole, *An Investigation of the Laws of Thought on Which are Founded the Mathematical Theories of Logic and Probabilities*, Cambridge: Macmillan and Co., 1854. [E-book] Available by Project Gutenberg: https://books.google.com/books?id=JBbkAAAAMAAJ&pg=PA201&lpg=PA201. [Accessed Oct. 11, 2019].

Theodore Hailperin, *The American Mathematical Monthly*, vol. 72, no. 4, pp. 343-359, April 1965. [Abstract]. Available: https://www.jstor.org/stable/2313491. [Accessed Oct. 11, 2019].

Augustus De Morgan, *On the Syllogism, and On the Logic of Relations*, 1859. Available: https://books.google.com/books?id=t02wDwAAQBAJ&pg=PA217. [Accessed Oct. 11, 2019].

Robert Harley, *Mind: A Quarterly Review of Psychology and Philosophy*, 1879. Available: https://books.google.com/books?id=JBbkAAAAMAAJ&pg=PA201. [Accessed Oct. 11, 2019].

Jin Tian and Judea Pearl, “Probabilities of causation: Bounds and identification.” In Craig Boutilier and Moises Goldszmidt (Eds.), *Proceedings of the Conference on Uncertainty in Artificial Intelligence (UAI-2000)*, San Francisco, CA: Morgan Kaufmann, 589–598, 2000. Available: http://ftp.cs.ucla.edu/pub/stat_ser/R271-U.pdf. [Accessed Oct. 31, 2019].

Stanley Burris, “George Boole,” *The Stanford Encyclopedia of Philosophy*, Summer 2018, Edward N. Zalta (ed.). Available: https://plato.stanford.edu/archives/sum2018/entries/boole/. [Accessed Oct. 11, 2019].

If you were trained in traditional regression pedagogy, chances are that you have heard about the problem of “bad controls”. The problem arises when we need to decide whether the addition of a variable to a regression equation helps getting estimates closer to the parameter of interest. Analysts have long known that some variables, when added to the regression equation, can produce unintended discrepancies between the regression coefficient and the effect that the coefficient is expected to represent. Such variables have become known as “bad controls”, to be distinguished from “good controls” (also known as “confounders” or “deconfounders”) which are variables that must be added to the regression equation to eliminate what came to be known as “omitted variable bias” (OVB).

Recent advances in graphical models have produced a simple criterion to distinguish good from bad controls, and the purpose of this note is to provide practicing analysts a concise and visible summary of this criterion through illustrative examples. We will assume that readers are familiar with the notions of “path-blocking” (or d-separation) and back-door paths. For a gentle introduction, see* d-Separation without Tears*.

In the following set of models, the target of the analysis is the average causal effect (ACE) of a treatment X on an outcome Y, which stands for the expected increase of Y per unit of a controlled increase in X. Observed variables will be designated by black dots and unobserved variables by white empty circles. Variable Z (highlighted in red) will represent the variable whose inclusion in the regression is to be decided, with “good control” standing for *bias reduction*, “bad control” standing for *bias increase* and “netral control” when the addition of Z *does not increase nor reduce bias*. For this last case, we will also make a brief remark about how Z could affect the *precision* of the ACE estimate.

*Models 1, 2 and 3 – Good Controls *

In model 1, Z stands for a common cause of both X and Y. Once we control for Z, we block the back-door path from X to Y, producing an unbiased estimate of the ACE.* *

In models 2 and 3, Z is not a common cause of both X and Y, and therefore, not a traditional “confounder” as in model 1. Nevertheless, controlling for Z blocks the back-door path from X to Y due to the unobserved confounder U, and again, produces an unbiased estimate of the ACE.

*Models 4, 5 and 6 – Good Controls*

When thinking about possible threats of confounding, one needs to keep in mind that common causes of X and any *mediator* (between X and Y) also confound the effect of X on Y. Therefore, models 4, 5 and 6 are analogous to models 1, 2 and 3 — controlling for Z blocks the backdoor path from X to Y and produces an unbiased estimate of the ACE.

*Model 7 – Bad Control*

We now encounter our first “bad control”. Here Z is correlated with the treatment and the outcome and it is also a “pre-treatment” variable. Traditional econometrics textbooks would deem Z a “good control”. The backdoor criterion, however, reveals that Z is a “bad control”. Controlling for Z will *induce bias* by opening the backdoor path X ← U_{1}→ Z← U_{2}→Y, thus spoiling a previously unbiased estimate of the ACE.

*Model 8 – Neutral Control (possibly good for precision)*

Here Z is not a confounder nor does it block any backdoor paths. Likewise, controlling for Z does not open any backdoor paths from X to Y. Thus, in terms of *bias*, Z is a “neutral control”. Analysis shows, however, that controlling for Z *reduces the variation of the outcome* *variable Y*, and helps improve the *precision* of the ACE estimate in finite samples.

*Model 9 – Neutral control (possibly bad for precision)*

Similar to the previous case, here Z is “neutral” in terms of bias reduction. However, controlling for Z *will reduce the variation of treatment variable X* and so may *hurt *the *precision* of the estimate of the ACE in finite samples.

*Model 10 – Bad control*

We now encounter our second “pre-treatment” “bad control”, due to a phenomenon called “bias amplification” (read more here). Naive control for Z in this model will not only fail to deconfound the effect of X on Y, but, in linear models, *will amplify any existing bias.*

*Models 11 and 12 – Bad Controls*

If our target quantity is the ACE, we want to leave all channels through which the causal effect flows “untouched”.

In Model 11, Z is a mediator of the causal effect of X on Y. Controlling for Z will block the very effect we want to estimate, thus biasing our estimates.

In Model 12, although Z is not itself a mediator of the causal effect of X on Y, controlling for Z is equivalent to partially controlling for the mediator M, and will thus bias our estimates.

Models 11 and 12 violate the backdoor criterion, which excludes controls that are descendants of the treatment along paths to the outcome.

*Model 13 – Neutral control (possibly good for precision)*

At first look, model 13 might seem similar to model 12, and one may think that adjusting for Z would bias the effect estimate, by restricting variations of the mediator M. However, the key difference here is that Z is a *cause, not an effect, *of the mediator (and, consequently, also a cause of Y). Thus, model 13 is analogous to model 8, and so controlling for Z will be neutral in terms of bias and may increase precision of the ACE estimate in finite samples.

*Model 14 – Neutral controls (possibly helpful in the case of selection bias)*

Contrary to econometrics folklore, not all “post-treatment” variables are inherently bad controls. In models 14 and 15 controlling for Z *does not* open any confounding paths between X and Y. Thus, Z is neutral in terms of bias. However, controlling for Z *does* reduce the variation of the treatment variable X and so may hurt the precision of the ACE estimate in finite samples. Additionally, in model 15, suppose one has only samples with W = 1 recorded (a case of selection bias). In this case, controlling for Z can help obtaining the W-specific effect of X on Y, by blocking the colliding path due to W.

*Model 16 – Bad control*

Contrary to Models 14 and 15, here controlling for Z is no longer harmless, since it opens the backdoor path X → Z ← U → Y and so biases the ACE.

*Model 17 – Bad Control*

Here, Z is not a mediator, and one might surmise that, as in Model 14, controlling for Z is harmless. However, controlling for the effects of the outcome Y will induce bias in the estimate of the ACE, making Z a “bad control”. A visual explanation of this phenomenon using “virtual colliders” can be found here.

Model 17 is usually known as a “case-control bias” or “selection bias”. Finally, although controlling for Z will generally bias* numerical estimates *of the ACE, it does have an exception when X has *no causal effect* on Y. In this scenario, X is still d-separated from Y even after conditioning on Z. Thus, adjusting for Z is valid for *testing* whether the effect of X on Y *is zero. *

This post aims to provide further insight to readers of “Book of Why” (BOW) (Pearl and Mackenzie, 2018) on Lord’s paradox and the simple way this decades-old paradox was resolved when cast in causal language. To recap, Lord’s paradox (Lord, 1967; Pearl, 2016) involves two statisticians, each using what seems to be a reasonable strategy of analysis, yet reaching opposite conclusions when examining the data shown in Fig. 1 (a) below.

**Figure 1:** Wainer and Brown’s revised version of Lord’s paradox and the corresponding causal diagram.

The story, in the form described by Wainer and Brown (2017) reads:

*“A large university is interested in investigating the effects on the students of the diet provided in the university dining halls …. Various types of data are gathered. In particular, the weight of each student at the time of his arrival in September and his weight the following June (W _{F}) are recorded.” *

The first statistician (named John) looks at the weight gains associated with the two dining halls, find them equally distributed, and naturally concludes that Diet has no effect on Gain. The second statistician (named Jane) uses the initial weight (*W _{I}*) as a covariate and finds that, for every level of

The Book of Why resolved this paradox using causal analysis. First, noting that at issue is “the effect of Diet on weight Gain”, a causal model is postulated, in the form of the diagram of Fig. 1(b). Second, noting the *W _{I}*is the only confounder of Diet and Gain, Jane was declared “unambiguously correct” and John “incorrect”.

**The Critics**

The simplicity of this solution invariably evokes skepticism among statisticians. “But how can we be sure of the diagram?” they ask. This kind of skepticism is natural since, statisticians are not trained in postulating causal assumptions, that is, assumptions that cannot be articulated in the language of mainstream statistics, and cannot therefore be tested using the available data. However, after reminding the critics that the contention between John and Jane surrounds the notion of “effect”, and that “effect” is a causal, not statistical notion, enlightened statisticians accept the idea that diagrams need to be drawn and that the one in Fig. 1(b) is reasonable; its main assumptions are: Diet does not affect the initial weight and the initial weight is the only factor affecting both Diet and final weight.

A series of recent posts by S. Senn, however, introduced a new line of criticism into our story (Senn, 2019). It focuses on the process by which the data of Fig. 1(a) was generated, and invokes RCT considerations such as block design, experiments with many halls, analysis of variance, standard errors, and more. Statisticians among my Twitter followers “liked” Senn’s critiques and I am not sure whether they were convinced by my argument that Lord’s paradox has nothing to do with experimental procedures. In other words, the conflict between John and Jane persists even when the data is generated by clean and un-complicated process, as the one depicted in Fig. 1(b).

Senn’s critiques can be summarized thus (quoted):

*“I applied John Nedler’s experimental calculus [5, 6] … and came to the conclusion that the second statistician’s solution is only correct given an untestable assumption and that even if the assumption were correct and hence the estimate were appropriate, the estimated standard error would almost certainly be wrong.”*

My response was:

Lord’s paradox is about causal effects of Diet. In your words: “diet has no effect” according to John and “diet does have an effect” according to Jane. We know that, inevitably, every analysis of “effects” must rely on causal, hence “untestable assumptions”. So BOW did a superb job in calling the attention of analysts to the fact that the nature of Lord’s paradox is causal, hence outside the province of mainstream statistical analysis. This explains why I agree with your conclusion that “the second statistician’s solution is only correct given an untestable assumption”. Had you concluded that we can decide who is correct without relying on “an untestable assumption”, you and Nelder would have been the first mortals to demonstrate the impossible, namely, that assumption-free correlation does imply causation.

Now let me explain why your last conclusion also attests to the success of BOW. You conclude: “even if the assumption were correct, … the estimated standard error would almost certainly be wrong.”

The beauty of Lord’s paradox is that it demonstrates the surprising clash between John and Jane in purely qualitative terms, with no appeal to numbers, standard errors, or confidence intervals. Luckily, the surprising clash persists in the asymptotic limit where Lord’s ellipses represent infinite samples, tightly packed into those two elliptical clouds.

Some people consider this asymptotic abstraction to be a “limitation” of graphical models. I consider it a blessing and a virtue, enabling us, again, to separate things that matter (clash over causal effects) from those that don’t (sample variability, standard errors, *p*-values etc.). More generally, it permits us to separate issues of estimation, that is, going from samples to distributions, from those of identification, that is, going from distributions to cause-effect relationships. BOW goes to great length explaining why this last stage presented an insurmountable hurdle to analysts lacking the appropriate language of causation.

Note that BOW declares Jane to be “unambiguously correct” in the context of the causal assumptions displayed in the diagram (Fig.1 (b)) where Diet is shown NOT to influence initial weight, and the initial weight is shown to be the (only) factor that makes students prefer one diet or another. Changing these assumptions may lead to another problem and another resolution but, once we agree with the assumptions our choice of Jane as the correct statistician is “unambiguously correct”

As an example (requested on Twitter) if dining halls have their own effect on weight gain (say Hall-A provides free weight-watching instructions to diners) our model will change as depicted in Fig 2. In this setup, *W _{I }*is no longer a sole confounder and both

**Figure 2:** Separating Diet from Hall in Lord’s Story

**New Insights**

The upsurge of interest in Lord’s paradox gives me an opportunity to elaborate on another interesting aspect of our Diet-weight model, Fig. 1.

Having concluded that Statistician-2 (Jane) is “unambiguously correct” and that Statistician-1 (John) is wrong, an astute reader would ask: “And what about the sure-thing principle? Isn’t the overall gain just an average of the stratum-specific gains?” (where each stratum represents a level of the initial weight *W _{I}*). Previously, in the original version of the paradox (Fig. 6.8 of BOW) we dismissed this intuition by noting that

*P*(*Y*|*do*(*Diet*)) = ∑_{WI}*P*(*Y*|*Diet*,*W _{I}*)

In other words, the overall gain resulting from administering a given diet to everyone is none other but the gain observed in a given diet-weight group, averaged over the weight. How is it possible then for the latter to be positive (as seen from the shifted ellipses) and, simultaneously, for the former to be zero (as seen by the perfect alignment of the ellipses along the *W _{I }*=

One would be tempted to suggest that data matching the ellipses of Fig 6.9(a) can never be generated by the model of Fig. 6.9(b) , in which *W _{I}*is the only confounder? But this could not possibly be the case, because we know that the model has no refuting implications, so it cannot be refuted by the position of the two ellipses.

The answer is that the sure-thing principle applies to causal effects, not to statistical associations. The perfect alignment of the ellipses does not mean that the effect of Diet on Gain is zero; it means only that the Gain is statistically independent of Diet:

*P*(*Gain*|*Diet*=*A*) = *P*(*Gain*|*Diet*=*B*)

not that Gain is causally unaffected by Diet. In other words, the equality above does not imply the equality

*P*(*Gain*|*do*(*Diet*=*A*)) = *P*(*Gain*|*do*(*Diet*=*B*))

which statistician-1 (John) wants us to believe.

Our astute student will of course question this explanation and, pointing to Fig. 1(b), will ask: How can Gain be independent of Diet when the diagram shows them connected? The answer is that the three paths connecting Diet and Gain cancel each other in such a way that an overall independence shows up in the data,

**Conclusions**

Lord’s paradox starts with a clash between two strong intuitions: (1) To get the effect we want, we must make “proper allowances” for uncontrolled preexisting differences between groups” (i.e. initial weights) and (2) The overall effect (of Diet on Gain) is just the average of the stratum-specific effects. Like the bulk of human intuitions, these two are CAUSAL. Therefore, to reconcile the apparent clash between them we need a causal language; statistics alone won’t do.

The difficulties that generations of statisticians have had in resolving this apparent clash stem from lacking a formal language to express the two intuitions as well as the conditions under which they are applicable. Missing were: (1) A calculus of “effects” and its associated causal sure-thing principle and (2) a criterion (back door) for deciding when “proper allowances for preexisting conditions” is warranted. We are now in possession of these two ingredients, and we should enjoy the power of causal analysis to resolve this paradox, which generations of statisticians have found intriguing, if not vexing. We should also feel empowered to resolve all the paradoxes that surface from the causation-association confusion that our textbooks have bestowed upon us.

**References**

Lord, F.M. “A paradox in the interpretation of group comparisons,” *Psychological Bulletin*, 68(5):304-305, 1967.

Pearl, J. “Lord’s Paradox Revisited — (Oh Lord! Kumbaya!)”, *Journal of Causal Inference*, Causal, Casual, and Curious Section, 4(2), September 2016. https://ftp.cs.ucla.edu/pub/stat_ser/r436.pdf

Pearl, J. and Mackenzie, D. *Book of Why*, NY: Basic Books, 2018. http://bayes.cs.ucla.edu/WHY/

Senn, S. “Red herrings and the art of cause fishing: Lord’s Paradox revisited” (Guest post) August 2, 2019. https://errorstatistics.com/2019/08/02/s-senn-red-herrings-and-the-art-of-cause-fishing-lords-paradox-revisited-guest-post/

Wainer and Brown, L.M., “Three statistical paradoxes in the interpretation of group differences: Illustrated with medical school admission and licensing data,” in C.R. Rao and S. Sinharay (Eds.), *Handbook of Statistics 26: Psychometrics*, North Holland: Elsevier B.V., pp. 893-918, 2007.

Dear Conrad,

Following your exchange with Judea, we would like to present concrete examples of how graphical tools can help determine whether a variable qualifies as an instrument. We use the example of job training program which Imbens used in his paper on instrumental variables.

In this example, the goal is to estimate the effect of a training program (X) on earnings (Y). Imbens suggested proximity (Z) as a possible instrument to assess the effect of X on Y. He then mentioned that the assumption that Z is independent of the potential outcomes {Yx} is a strong one, noting that this can be made more plausible by conditioning on covariates.

To illustrate how graphical models can be used in determining the plausibility of the exclusion restriction, conditional on different covariates, let us consider the following scenarios.

**Scenario 1.** Suppose that the training program is located in the workplace. In this case, proximity (Z) may affect the numbers of hours employees spend at the office (W) since they spend less time commuting, and this, in turn, may affect their earnings (Y).

**Scenario 2.** Suppose further that the efficiency of the workers (unmeasured) affects both the number of hours (W) and their salary (Y). (This is represented in the graph through the inclusion of a bidirected arrow between W and Y.)

**Scenario 3.** Suppose even further that this is a high-tech industry and workers can easily work from home. In this case, the number of hours spent at the office (W) has no effect on earnings (Y). (This is represented in the graph through the removal of the directed arrow from W to Y.)

**Scenario 4.** Finally, suppose that worker efficiency also affects whether they attend the program because less efficient workers are more likely to benefit from training. (This is represented in the graph through the inclusion of a bidirected arrow from W to X.)

The following figures correspond to the scenarios discussed above.

The reasons we like to work with graphs on such problems is, first, we can represent these scenarios clearly and unambiguously and, second, we can derive the answer in each of these scenarios by inspection of the causal graphs. Here are our answers: (We assume a linear model. For nonparametric, use LATE.)

**Scenario 1. **

Is the effect of X on Y identifiable? Yes

How? Using Z as an instrument conditioning on W and the effect is equal to r_{zy.w} / r_{zx.w}.

Testable implications? (W independent X given Z)

**Scenario 2. **

Is the effect of X on Y identifiable? No

How? n/a.

Testable implications? (W independent X given Z)

**Scenario 3. **

Is the effect of X on Y identifiable? Yes

How? Using Z as an instrument and the effect is equal to r_{zy} / r_{zx}.

Remark. Conditioning on W disqualifies Z as an instrument.

Testable implications? (W independent X given Z)

**Scenario 4. **

Is the effect of X on Y identifiable? Yes

How? Using Z as an instrument and the effect is equal to r_{zy} / r_{zx}.

Conditioning on W disqualifies Z as an instrument.

Testable implications?

In summary, the examples demonstrate Imben’s point that judging whether a variable (Z) qualifies as an instrument hinges on substantive assumptions underlying the problem being studied. Naturally, these assumptions follow from the causal story about the phenomenon under study. We believe graphs can be an attractive language to solve this type of problem for two reasons. First, it is a transparent representation in which researchers can express the causal story and discuss its plausibility. Second, as a formal representation of those assumptions, it allows us to apply mechanical procedures to evaluate the queries of interest. For example, whether a specific set Z qualifies as an instrument; whether there exists a set Z that qualifies as instrument; what are the testable implications of the causal story.

We hope the examples illustrate these points.

Bryant and Elias

*Summer Short Course “An Introduction to Causal Inference”*

**Date: June 3-7, 2019**

**Instructors: **Miguel Hernán, Judith Lok, James Robins, Eric Tchetgen Tchetgen & Tyler VanderWeele

This 5-day course introduces concepts and methods for causal inference from observational data. Upon completion of the course, participants will be prepared to further explore the causal inference literature. Topics covered include the g-formula, inverse probability weighting of marginal structural models, g-estimation of structural nested models, causal mediation analysis, and methods to handle unmeasured confounding. The last day will end with a “capstone” open Q&A session with the instructors.

**Prerequisites:** Participants are expected to be familiar with basic concepts in epidemiology and biostatistics, including linear and logistic regression and survival analysis techniques.

**Tuition:** $600/person, to be paid at the time of registration. A limited number of tuition waivers are available for students.

**Date/Location:** June 3-7, 2019 at the Harvard T.H. Chan School of Public Health.

**Details and registration:**https://www.hsph.harvard.edu/causal/shortcourse/

He also added that the Ulm Museum (where the Lion Man is on exhibit) is situated near the house where Albert Einstein was born in 1879.

This makes Ulm a home to two revolutions of human cognition.

]]>These discussions unveils some of our differences as well as some agreements. I am posting some of the discussions below, because Gelman’s blog represents the thinking of a huge segment of practicing statisticians who are, by and large, not very talkative about causation. It is interesting therefore to understand how they think, and what makes them tick.

**Judea Pearl says: January 12, 2019 at 8:24 am**

Andrew,

I appreciate your kind invitation to comment on your blog. Let me start with a Tweet that I posted on https://twitter.com/yudapearl

(updated 1.10.19)

1.8.19 @11:59pm – Gelman’s review of #Bookofwhy should be of interest because it represents an attitude that paralyzes wide circles of statistical researchers. My initial reaction is now posted on https://bit.ly/2H3BH3b Related posts: https://ucla.in/2sgzkPZ and https://ucla.in/2v72QK5

These postings speak for themselves but I would like to respond here to your recommendation: “Similarly, I’d recommend that Pearl recognize that the apparatus of statistics, hierarchical regression modeling, interactions, post-stratification, machine learning, etc etc solves real problems in causal inference.”

It sounds like a mild and friendly recommendation, and your readers would probably get upset at anyone who would be so stubborn as to refuse it.

But I must. Because, from everything I know about causation, the apparatus you mentioned does NOT, and CANNOT solve any problem known as “causal” by the causal-inference community (which includes your favorites Rubin, Angrist, Imbens, Rosenbaum, etc etc.). Why?

Because the solution to any causal problem must rest on causal assumptions and the apparatus you mentioned has no representation for such assumptions.

1. Hierarchical models are based on set-subset relationships, not causal relationships.

2. “interactions” is not an apparatus unless you represent them in some model, and act upon them.

3. “post-stratification” is valid only after you decide what you stratify on, and this requires a causal structure (which you claim above to be an unnecessary “wrapping” and complication”)

4. “Machine learning” is just fancy curve fitting of data see https://ucla.in/2umzd65

Thus, what you call “statistical apparatus” is helpless in solving causal problems. We came to this juncture several times in the past and, invariably, you pointed me to books, articles, and elaborated works which, in your opinion, do solve “real life causal problems”. So, how are we going to resolve our disagreement on whether those “real life” problems are “causal” and, if they are, whether your solution of them is valid. I suggested applying your methods to toy problems whose causal character is beyond dispute. You did not like this solution, and I do not blame you, because solving ONE toy problem will turn your perception of causal analysis upside down. It is frightening. So I would not press you. But I will add another Tweet before I depart:

1.9.19 @2:55pm – An ounce of advice to readers who comment on this “debate”: Solving one toy problem in causal inference tells us more about statistics and science than ten debates, no matter who the debaters are. #Bookofwhy

Addendum. Solving ONE toy problem will tells you more than dozen books and articles and multi-cited reports. You can find many such toy problems (solved in R) here: https://ucla.in/2KYYviP sample of solution manual: https://ucla.in/2G11xUE

For your readers convenience, I have provided free access to chapter 4 here: https://ucla.in/2G2rWBv It is about counterfactuals and, if I were not inhibited by modesty, I would confess that it is the best text on counterfactuals and their applications that you can find anywhere.

I hope you take advantage of my honesty.

Enjoy

Judea

*Andrew says: **January 12, 2019 at 11:37 am*

Judea:

We are in agreement. I agree that data analysis alone cannot solve any causal problems. Substantive assumptions are necessary too. To take a familiar sort of example, there are people out there who just think that if you fit a regression of the form, y = a + bx + cz + error, that the coefficients b and c can be considered as causal effects. At the level of data analysis, there are lots of ways of fitting this regression model. In some settings with good data, least squares is just fine. In more noisy problems, you can do better with regularization. If there is bias in the measurements of x, z, and y, that can be incorporated into the model also. But none of this legitimately gives us a causal interpretation until we make some assumptions. There are various ways of expressing such assumptions, and these are talked about in various ways in your books, in the books by Angrist and Pischke, in the book by Imbens and Rubin, in my book with Hill, and in many places. Your view is that your way of expressing causal assumptions is better than the expositions of Angrist and Pischke, Imbens and Rubin, etc., that are more standard in statistics and econometrics. You may be right! Indeed, I think that for some readers your formulation of this material is the best thing out there.

Anyway, just to say it again: We agree on the fundamental point. This is what I call in the above post the division of labor, quoting Frank Sinatra etc. To do causal inference requires (a) assumptions about causal structure, and (b) models of data and measurement. Neither is enough. And, as I wrote above:

I agree with Pearl and Mackenzie that typical presentations of statistics, econometrics, etc., can focus way too strongly on the quantitative without thinking at all seriously about the qualitative aspects of the problem. It’s usually all about how to get the answer given the assumptions, and not enough about where the assumptions come from. And even when statisticians write about assumptions, they tend to focus on the most technical and least important ones, for example in regression focusing on the relatively unimportant distribution of the error term rather than the much more important concerns of validity and additivity.

If all you do is set up probability models, without thinking seriously about their connections to reality, then you’ll be missing a lot, and indeed you can make major errors in casual reasoning . . .

Where we disagree is just on terminology, I think. I wrote, “the apparatus of statistics, hierarchical regression modeling, interactions, poststratification, machine learning, etc etc., solves real problems in causal inference.” When I speak of this apparatus, I’m *not* just talking about probability models; I’m also talking about assumptions that map those probability models to causality. I’m talking about assumptions such as those discussed by Angrist and Pischke, Imbens and Rubin, etc.—and, quite possibly, mathematically equivalent in these examples to assumptions expressed by you.

So, to summarize: To do causal inference, we need (a) causal assumptions (assumptions of causal structure), and (b) models or data analysis. The statistics curriculum spends much more time on (b) than (a). Econometrics focuses on (a) as well as (b). You focus on (a). When Angrist, Pischke, Imbens, Rubin, Hill, me, and various others do causal inference, we do both (a) and (b). You argue that if we were to follow your approach on (a), we’d be doing better work for those problems that involve causal inference. You may be right, and in any case I’m glad you and Mackenzie wrote this book which so many people have found helpful, just as I’m glad that the aforementioned researchers wrote their books on causal inference which so many have found helpful. A framework for causal inference—whatever that framework may be—is complementary to, not in competition with, data-analysis tools such as hierarchical modeling, poststratification, machine learning, etc.

P.S. I’ll ignore the bit in your comment where you say you know what is “frightening” to me.

*Judea Pearl says: **January 13, 2019 at 6:59 am*

Andrew,

I would love to believe that where we disagree is just on terminology. Indeed, I see sparks of convergence in your last post, where you enlighten me to understand that by “the apparatus of statistics, …’ you include the assumptions that PO folks (Angrist and Pischke, Imbens and Rubin etc.) are making, namely, assumptions of conditional ignorability. This is a great relief, because I could not see how the apparatus of regression, interaction, post-stratification or machine learning alone, could elevate you from rung-1 to rung-2 of the Ladder of Causation. Accordingly, I will assume that whenever Gelman and Hill talk about causal inference they tacitly or explicitly make the ignorability assumptions that are needed to take them

from associations to causal conclusions. Nice. Now we can proceed to your summary and see if we still have differences beyond terminology.

I almost agree with your first two sentences: “So, to summarize: To do causal inference, we need (a) causal assumptions (assumptions of causal structure), and (b) models or data analysis. The statistics curriculum spends much more time on (b) than (a)”.

But we need to agree that just making “causal assumptions” and leaving them hanging in the air is not enough. We need to do something with the assumptions, listen to them, and process them so as to properly guide us in the data analysis stage.

I believe that by (a) and (b) you meant to distinguish identification from estimation. Identification indeed takes the assumptions and translate them into a recipe with which we can operate on the data so as to produce a valid estimate of the research question of interest. If my interpretation of your (a) and (b) distinction is correct, permit me to split (a) into (a1) and (a2) where (a2) stands for identification.

With this refined-taxonomy, I have strong reservation to your third sentence: “Econometrics focuses on (a) as well as (b).” Not all of econometrics. The economists you mentioned, while commencing causal analysis with “assumptions” (a1), vehemently resist to organizing these assumptions in any “structure”, be it a DAG or structural equations (Some even pride themselves of being “model-free”). Instead, they restrict their assumptions to conditional ignorability statements so as to justify familiar estimation routines. [In https://ucla.in/2mhxKdO, I labeled them: “experimentalists” or “structure-free economists” to be distinguished from “structuralists” like Heckman, Sims, or Matzkin.]

It is hard to agree therefore that these “experimentalists” focus on (a2) — identification. They actually assume (a2) away rather than use it to guide data analysis.

Continuing with your summary, I read: “You focus on (a).” Agree. I interpret (a) to mean (a) = (a1) + (a2) and I let (b) be handled by smart statisticians, once they listen to the guidance of (a2).

Continuing, I read:

“When Angrist, Pischke, Imbens, Rubin, Hill, me, and various others do causal inference, we do both (a) and (b). Not really. And it is not a matter of choosing “an approach”. By resisting structure, these researchers a priori deprive themselves of answering causal questions that are identifiable by do-calculus and not by a single conditional ignorability assumption. Each of those questions may require a different estimand, which means that you cannot start doing the “data analysis” phase before completing the identification phase.

[Currently, even questions that are identifiable by conditional ignorability assumption cannot be answered by structure-free PO folks, because deciding on the conditioning set of covariates is intractable without the aid of DAGs, but this is a matter of efficiency not of essence.]

But your last sentence is hopeful:

“A framework for causal inference — whatever that that framework may be — is complementary to, not in competition with, data-analysis tools such as hierarchical modeling, post-stratification, machine learning, etc.”

Totally agree, with one caveat: the framework has to be a genuine “framework,” ie, capable of leverage identification to guide data-analysis.

Let us look now at why a toy problem would be frightening; not only to you, but to anyone who believes that the PO folks are offering a viable framework for causal inference.

Lets take the simplest causal problem possible, say a Markov chain X —>Z—>Y with X standing for Education, Z for Skill and Y for Salary. Let Salary be determined by Skill only, regardless of Education. Our research problem is to find the causal effect of Education on Salary given observational data of (perfectly measured) X,Y,Z.

To appreciate the transformative power of a toy example, please try to write down how Angrist, Pischke, Imbens, Rubin, Hill, would go about doing (a) and (b) according to your understanding of their framework. You are busy, I know, so let me ask any of your readers to try and write down step by step how the graph-less school would go about it. Any reader who tries this exercise ONCE will never be thesame. It is hard to believe unless you actually go through this frightening exercise, please try.

Repeating my sage-like advice: Solving one toy problem in causal inference tells us more about statistics and science than ten debates, no matter who the debaters are.

Try it.

*[Judea Pearl added in editing: I have received no solution thus far, not even an attempt. For readers of this blog, the chain is part of the front-door model which is treated in Causality pp. 232-4, in both graphical and potential outcome frameworks. I have yet to meet a PO researcher who can formulate this toy story in PO, let alone solve it. Not because they can’t, but because the very idea of listening to their understanding of a problem and translating that understanding to formal assumption is foreign to them, having been conditioned to assume ignorability and estimate a quantity that is easily estimable]*

*Andrew says:**January 13, 2019 at 8:26 pm*

Judea:

I think we agree on much of the substance. And I agree with you regarding “not all econometrics” (and, for that matter, not all of statistics, not all of sociology, etc.). As I wrote in my review of your book with Mackenzie, and in my review of Angrist and Pischke’s book, causal identification is an important topic and worth its own books.

In practice, our disagreement is, I think, that we focus on different sorts of problems and different sorts of methods. And that’s fine! Division of labor. You have toy problems that interest you, I have toy problems that interest me. You have applied problems that interest you, I have applied problems that interest me. I would not expect you to come up with methods of solving the causal inference problems that I work on, but that’s OK: your work is inspirational to many people and I can well believe it has been useful in certain applications as well as in developing conceptual understanding. I consider toy problems of my own for that same reason. I’m not particularly interested in your toy problems, but that’s fine; I doubt you’re particularly interested in the problems I focus on. It’s a big world out there.

In the meantime, you continue to characterize me as being frightened or lacking courage. I wish you’d stop doing that.

*[Judea Pearl added in editing: Gelman wants to move identification to separate books, because it is important, but the fact that one cannot start estimation before having an identifiable estimand is missing from his comment. Is he aware of it? Does he really do estimation before identification? I do not know, it is a foreign culture to me.]*

*Judea Pearl says: **January 13, 2019 at 10:51 pm*

Andrew,

Convergence is in sight, modulo two corrections:

1. You say:

“You [Pearl] have toy problems that interest you, I [Andrew] have toy problems that interest me. …I doubt you’re particularly interested in the problems I focus on. ”

Wrong! I am very interested in your toy problems, especially those with causal flavor. Why? Because I love to challenge the SCM framework with new tasks and new angles that other researchers found to be important, and see if SCM can be enriched with expanded scope. So, by all means, if you have a new twist, shoot. I have not been able to do it in the past, because your shots were not toy-like, e.g., 3-4 variables, clear task, with correct answer known.

2. You say:

“you continue to characterize me as being frightened or lacking courage” This was not my intention. My last remark on frightening toys was general, everyone is frightened by the honesty and transparency of toys — the adequacy of one’s favorite method is undergoing a test of fire. Who wouldn’t be frightened? But, since you prefer, I will stop using this metaphor.

3. Starting afresh, and the sake of good spirit: How about attacking a toy problem? Just for fun, just for sport.

*Andrew says: **January 13, 2019 at 11:24 pm*

Judea:

I’ve attacked a lot of toy problems.

For an example of a toy problem in causality, see pages 962-963 of this article.

But most of the toy problems I’ve looked at do not involve causality; see for example this paper, item 4 in this post, and this paper. This article on experimental design is simple enough that I think it could count as a toy problem: it’s a simple example without data which allows us to compare different methods. And here’s a theoretical paper I wrote awhile ago that has three toy examples. Not involving causal inference, though.

I’ve written lots of papers with causal inference, but they’re almost all applied work. This may be because I consider myself much more of a practitioner of causal inference than a researcher on causal inference. To the extent I’ve done research on causal inference, it’s mostly been to resolve some confusions in my mind (as in this paper).

This gets back to the division-of-labor thing. I’m happy for you and Imbens and Hill and Robins and VanderWeele and others to do research on fundamental methods for causal inference, while I do research on statistical analysis. The methods that I’ve learned have allowed my colleagues and I to make progress on a lot of applied problems in causal inference, and have given me some clarity in understanding problems with some naive formulations of causal reasoning (as in the first reference above in this comment).

*[Judea Pearl. Added in editing: Can one really make progress on a lot of applied problems in causal inference without dealing with identification Evidently, PO folks think so, at least those in Gelman’s circles]*

As I wrote in my above post, I think your book with Mackenzie has lots of great things in it; I just can’t go with a statement such as, “Using a calculus of cause and effect developed by Pearl and others, scientists now have the ability to answer such questions as whether a drug cured an illness, when discrimination is to blame for disparate outcomes, and how much worse global warming can make a heat wave”—because scientists have been answering such questions before Pearl came along, and scientists continue to answer such questions using methods other than Pearl’s. For what it’s worth, I don’t think the methods that my colleagues and I have developed are *necessary* for solving these or any problems. Our methods are helpful in some problems, some of the time, at least until something better comes along—I think that’s pretty much all that any of us can hope for! That, and we can hope that our writings inspire new researchers to come up with new methods that are useful in the future.

*Judea Pearl says:**January 14, 2019 at 2:18 am*

Andrew,

Agree to division of labor: causal inference on one side and statistical analysis on the other.

Assuming that you give me some credibility on the first, let me try and show you that even the publisher advertisement that you mock with disdain is actually true and carefully expressed. It reads: “Using a calculus of cause and effect developed by Pearl and others, scientists now have the ability to answer such questions as whether a drug cured an illness, when discrimination is to blame for disparate outcomes, and how much worse global warming can make a heat wave”.

First, note that it includes “Pearl and others”, which theoretically might include the people you have in mind. But it does not; it refers to those who developed mathematical formulation and mathematical tools to answer such questions. So let us examine the first question: “whether a a drug cured an illness”. This is a counterfactual “cause of effect” type question. Do you know when it was first formulated mathematically? [Don Rubin declared it non-scientific].

Now lets go to the second: “when discrimination is to blame for disparate outcomes,” This is a mediation problem. Care to guess when this problem was first formulated (see Book of Why chapter 9) and what the solution is Bottom line, Pearl is not as thoughtless as your review portrays him to be and, if you advise your readers to control their initial reaction: “Hey, statisticians have been doing it for centuries” they would value learning how things were first formulated, first solved and why statisticians were not always the first.

*Andrew says:**January 14, 2019 at 6:46 pm*

Judea:

I disagree with your implicit claim that, before your methods were developed, scientists were not able to answer such questions as whether a drug cured an illness, when discrimination is to blame for disparate outcomes, and how much worse global warming can make a heat wave. I doubt much will be gained by discussing this particular point further so I’m just clarifying that this is a point of disagreement.

Also, I don’t think in my review I portrayed you as thoughtless. My message was that your book with Mackenzie is valuable and interesting even though it has some mistakes. In my review I wrote about the positive part as well as the mistakes. Your book is full of thought!

*[Judea Pearl. Added in edit: Why can’t Gelman “go with a statement such as, “Using a calculus of cause and effect developed by Pearl and others, scientists now have the ability to answer such questions as whether a drug cured an illness, when discrimination is to blame for disparate outcomes, and how much worse global warming can make a heat wave”? His answer is: “because scientists have been answering such questions before Pearl came along” True, by trial and error, but not by mathematical analysis. And my statement marvels at the ability of doing it analytically. So why can’t Gelman acknowledge that a marvelous progress has been made, not by me, but by several researchers who realized that graph-less PO is a deadend.?]*