Causal Analysis in Theory and Practice

Judea Pearl writes:

Recently, there have been several articles and many blog entries concerning the question of what measurements should be incorporated in various methods of causal analysis.The statement below is offered by way of a resolution that (1) summarizes the discussion thus far, (2) settles differences of opinion and  (3) remains faithful to logic and facts as we know them today.

The resolution is reached by separating the discussion into three parts:  1.  Propensity score matching  2. Bayes analysis 3. Other techniques

1. Propensity score matching. Everyone is in the opinion that one should screen variables before including them as predictors in the propensity-score function.We know that, theoretically, some variables are capable of increasing bias (over and above what it would be without their inclusion,) and some are even guaranteed to increase such bias.

1.1 The identity of those bias-raising variables is hard to ascertain in practice. However, their
general features can be described in either graphical terms or in terms of the "assignment mechanism", P(W|X, Y0,Y1),if such is assumed.

1.2 In light of 1.1, it is recommend that the practice of adjusting for as many measurements as possible should be approached with great caution. While most available measurements are bias-reducing, some are bias-increasing.The criterion of producing "balanced population" for
matching, should not be the only one in deciding whether a measurement should enter the propensity score function.

2. Bayes analysis. If the science behind the problem, is properly formulated as constraints over the prior distribution of the "assignment mechanism" P(W|X, Y, Y0,Y1), then one need not exclude any measurement in advance; sequential updating will properly narrow the posteriors to reflect both the science and the available data.

2.1 If one can deduce from the "science" that certain covariates are "irrelevant" to the problem at hand,there is no harm in excluding them from the Bayesian analysis. Such deductions can be derived either analytically, from the algebraic description of the constraints, or graphically, from the diagramatical description of those constraints.

2.2 The inclusion of irrelevant variables in the Bayesian analysis may be advantageous from certain perspectives (e.g., provide evidence for missing data) and dis-advantageous from others (e.g, slow convergence, increase in problem dimensionality, sensitivity to misspecification).

2.3 The status of intermediate variables (and M-Bias) fall under these considerations. For example, if the chain Smoking ->Tar-> Cancer represents the correct specification of the problem, there are advantages (e.g., reduced variance (Cox, 1960?)) to including Tar in the analysis even though the causal effect (of smoking on cancer) is identifiable without measuring Tar, if Smoking is randomized. However, misspecification of the role of Tar, may lead to bias.

3. Other methods. Instrumental variables, intermediate variables and confounders can be identified, and harnessed to facilitate effective causal inference using other methods, not involving propensity score matching or Bayes analysis. For example, the measurement of Tar in the example above, can facilitate a consistent estimate of the causal effect (of Smoking on Cancer) even in the presence of unmeasured confounding factors, affecting both smoking and cancer. Such analysis can be done by either graphical methods (Causality, page 81-88) or counterfactual algebra (Causality, page 231-234).

Thus far, I have not heard any objection to any of these conclusions, so I consider it a resolution of what seemed to be a major disagreement among experts. And this supports what Aristotle said (or should have said): Causality is simple.

Judea

Judea Pearl writes to Andrew Gelman about differences between Donald Rubin's and Pearl's approaches.

Dear Andrew,

I think our discussion could benefit from the distinction between "theories" and “approaches." A theory T is a set of mathematical constraints on what can and cannot be deduced from a set of premises. An approach is what you do with those constraints, how you apply them, at what sequence, and in what language.
 
In the context of this distinction I say that Rubin’s theory T is equivalent to Pearl’s. While the approach is different, equivalence of theories means that there cannot be a clash of claims, and this is a proven fact. In other words if there is ever a clash about a given problem, it means one of two things, either the theory was not applied properly or additional information about the problem was assumed by one investigator that was not assumed by the other.
 
Now to the "approach". Below is my analysis of the two approaches, please check if it coincide with your understanding of Rubin's approach.
 
Pearl says, let us start with the science behind each problem, e.g., coins, bells, seat-belts, smoking etc.. Our theory tells us that no causal claim can ever be issued if we know nothing about the science, even if we take infinite samples. Therefore, let us articulate what we do know about the science, however meager, and see what we can get out of the theory.  This calls for encoding the relationships among the relevant entities, coins, bells and seat-belts, in some language, call it L, thus creating a "problem description" L(P). L(P) contains variables, observed and unobserved factors, equations, graphs, physical constraints, processes, influences, lack of influences, dependencies, etc, whatever is needed to encode our understanding of the science behind the problem P.
 
Now we are ready to solve the problem. We take L(P) and appeal to our theory T:Theory, theory on the wall, how should we solve L(P)? The theory says: Sorry, I don’t speak L, I speak T.
 
What do we do? Pearl's approach says: take the constraints from T, and translate them into new constraints, formulated in language L, thus creating a set of constraints L(T) that echo T and tell us what can and what cannot be deduced from certain premises encoded in L(P).Next, we deduced a claim C in L(P) (if possible)or we proclaim C to be "non-deducible". Done.
 
Rubin's approach is a bit different. We again look at a problem P but, instead of encoding it in L, we skip that part and translate P directly into a language that the theory can recognize; call it T(P). (It looks like P(W|X, Y₁, Y₂) according to Rubin's SIM article (2007)) Now we ask: Theory, theory on the wall, how should we solve T(P)? The theory answers: Easy, man! I speak T. So, the theory produces a claim C in T, and everyone is happy.
 
To summarize, Pearl brings the theory to the problem, Rubin takes the problem to the theory.
 
To an observer from the outside the two approaches would look identical, because the claims produced are identical and the estimation procedures they dictate are identical. So, one should naturally ask, how can there ever be a clash in claims like the one concerning covariate selection?
 
Differences will show up when researchers begin to deviate from the philosophies that govern either one of the two approaches. For example, researchers might find it too hard to go from P to T(P). So hard in fact that they give up on thinking about P, and appeal directly to the theory: Theory, theory on the wall, we don’t know anything about the problem, actually, we do know, but we don’t feel like thinking about it. Can you deduce claim C for us?
 
If asked, the theory would answer: "No, sorry, nothing can be deduced without some problem description. "But some researchers may not wish to talk directly to the theory, it is too taxing to write a story and coins and bells in language of P(W|X, Y₁, Y₂)..So what do they do? They fall into a lazy mode, like: "Use whatever routines worked for you in the past. If propensity scores worked for you, use it, take all available measurements as predictors. the more the better." Lazy thinking forms subcultures, and subcultures tend to isolate themselves from the rest of the scientific community because nothing could be more enticing than methods and habits, especially when they reinforced by respected leaders, And especially when habits are supported by convincing metaphors. For example, how can you go wrong by "balancing" treated and untreated units on more and more covariates. Balancing, we all know, is a good thing to have; is even present in randomized trials. So, how can we go wrong? An open-minded student of such subculture should ask: "The more the better? Really? How come? Pearl says some covariates might increase bias? And there should be no clash in claims between the two approaches. "An open minded student would also be so bold as to take a pencil and paper and consult the theory T directly, asking: Do I have to worry about increased bias in my specific problem?" And the theory would answer: You might have to worry, yes, but I can only tell you where the threats are if you tell me something about the problem, which you refuse to do.
 
Or the theory might answer: If you feel so shy about describing your problem, why don’t you use the Bayesian method; this way, even if you end up with unidentified situation, the method would not punish you for not thinking about the problem, it would just produce a very wide posterior, The more you think, the narrower the posterior. Isn't this a fair play?
 
To summarize:
 
One theory has spawned two approaches, The two approaches have spawned two subcultures.Culture-1 solves problems in L(P) by the theoretical rules of L(T) that were translated from T into L. Culture-2 avoids describing P, or thinking about P, and relies primarily on metaphors, convenience of methods and guru's advise.
 
Once in a while, when problems are simple enough, (like the binary Instrumental Variable problem), someone from culture 2 would formulate a problem in T and derive useful results. But, normally, problem-description avoidance is the rule of the day. So much so, that even 2-coins-one-bell problems are not analyzed mathematically by rank and file researches; they are sent to the gurus for opinion.
 
I admit that I was not aware of the capability of Bayesian methods to combine two subpopulations in which a quantity is unidentified and extract a point estimate of the average, when such average is identified. I am still waiting for the bell-coins example worked out by this method — it would enrich by arsenal of techniques. But this would still not alter my approach, namely, to formulate problems in a language close to their source: human experience.
 
In other words, even if the Bayesian method will be shown capable of untangling the two subpopulations, thus giving researchers the assurance that they have not ignored any data, I would still prefer to encode a problem in L(P), then ask L(T): Theory, theory on the wall, look at my problem and tell me if perhaps there are measurements that are redundant. If the answer is Yes, I would save the effort of measuring them, and the increased dimensionality of regressing on them, and just get the answer that I need from the essential measurements. Recall that, even if one insists on going the Bayesian route, the task of translating a problem into T remains the same. All we gain is the luxury of not thinking in advance about which measurements can be avoided, we let the theory do the filtering
automatically.   I am now eager to see how this is done; two-cons and  one bell. Everyone knows the answer: coin-1 has no causal effect on coin-2 no matter if we listen to the bell or not. Lets see Rev. Bayes advise us correctly: ignore the bell.

Andrew Gelman wrote a follow up to his original post:

To follow up on yesterday's discussion, I wanted to go through a bunch of different issues involving graphical modeling and causal inference.

Contents:
– A practical issue: poststratification
– 3 kinds of graphs
– Minimal Pearl and Minimal Rubin
– Getting the most out of Minimal Pearl and Minimal Rubin
– Conceptual differences between Pearl's and Rubin's models
– Controlling for intermediate outcomes
– Statistical models are based on assumptions
– In defense of taste
– Argument from authority?
– How could these issues be resolved?
– Holes everywhere
– What I can contribute

Andrew Gelman (Columbia) recently wrote a blog post motivated by Judea Pearl's paper, "Myth, Confusion, and Science in Causal Analysis. " In response, Pearl writes:

Dear Andrew,

Thank you for your blog post dated July 5. I appreciate your genuine and respectful quest to explore the differences between the approaches that I and Don Rubin are taking to causal inference.

In general, I would be the first to rally behind your call for theoretical pluralism (e.g., "It make sense that other theoretical perspectives such as Pearl's could be useful too.") We know that one can prove a theorem in geometry by either geometrical or algebraic methods, depending on the problem and the perspective one prefers to take–only the very dogmatic would label one of the methods "unprincipled".

My article, "Myth, confusion and Science in Causal Analysis", is written with this dual perspective in mind, fully accommodating the graphical and potential-outcome conceptualizations as interchangeable, "A theorem in one approach is a theorem in another," I wrote.

However, when adherents of the one-perspective approach make claims that mathematically contradict those derived from the dual-perspective approach, one begins to wonder whether there is something more fundamental at play here.

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A letter from Judea Pearl to the Editor of Statistics in Medicine:

Dear Editor,

I read with great interest Donald Rubin’s paper "The design versus the analysis of observational studies for causal effects: Parallels with the design of randomized trials" (2007, 26(1):20-36) [1], as well as the Letter To The Editor by Ian Shrier (2008, 27(14):2740-2741) [2], and Author Reply by Don Rubin (2008, 27(14):2741-2742) [3].

Shrier’s Letter posed an important question which remains unanswered in Rubin’s reply. I here venture to answer this question and to clarify related issues concerning the interpretation of propensity scores (PS) and their role in causal inference.

Shrier’s question was whether, asymptotically, the use of PS methods as described by Rubin may actually increase, not decrease, bias over and above a crude, unadjusted comparison between treated and untreated subjects. The answer is: Yes, and the M-graph cited by Shrier (see also [4, 5]) provides an extreme such example; the crude estimate is bias-free, while PS methods introduce new bias.

This occurs when treatment is strongly ignorable to begin with and becomes non-ignorable at some levels of e. In other words, although treated and untreated units are balanced in each stratum of e, the balance only holds relative to the covariates measured; unobserved confounders may be highly unbalanced in each stratum of e, capable of producing significant bias. Moreover, such imbalance may be dormant in the crude estimate and awakened throughthe use of PS methods.

There are other features of PS methods that are worth emphasizing.

First, the propensity score e is a probabilistic, not a causal concept. Therefore, in the limit of very large sample, PS methods are bound to produce the same bias as straight stratification on the same set of measured covariates. They merely offer an effective way of approaching the asymptotic estimate which, due to the high dimensionality of X, is practically unattainable with straight stratification. Still, the asymptotic estimate is the same in both cases, and may or may not be biased, depending on the set of covariates chosen.

Second, the task of choosing a sufficient (i.e., bias-eliminating) set of covariates for PS analysis requires qualitative knowledge of the causal relationships among both observed and unobserved covariates. Given such knowledge, finding a sufficient set of covariates or deciding whether a sufficient set exists are two problems that can readily be solved by graphical methods [6, 7, 4].

Finally, experimental assessments of the bias-reducing potential of PS methods (such as those described in Rubin, 2007 [1]) can only be generalized to cases where the causal relationships among covariates, treatment, outcome and unobserved confounders are the same as in the experimental study. Thus, a study that proves bias reduction through the use of covariate set X does not justify the use of X in problems where the influence of unobserved confounders may be different.

In summary, the effectiveness of PS methods rests critically on the choice of covariates, X, and that choice cannot be left to guesswork; it requires that we understand, at least figuratively, what relationships may exist between observed and unobserved covariates and how the choice of the former can bring about strong ignorability or a reasonable approximation thereof.

Judea Pearl
UCLA

REFERENCES

1. Rubin D. The design versus the analysis of observational studies for causal effects: Parallels with the designof randomized trials. Statistics in Medicine 2007; 26:20–36.
2. Shrier I. Letter to the editor. Statistics in Medicine 2008; 27:2740–2741.
3. Rubin D. Author’s reply (to Ian Shrier’s Letter to the Editor). Statistics in Medicine 2008; 27:2741–2742.
4. Greenland S, Pearl J, Robins J. Causal diagrams for epidemiologic research. Epidemiology 1999; 10(1):37–48.
5. Greenland S. Quantifying biases in causal models: Classical confounding vs. collider-stratification bias.pidemiology 2003; 14:300–306.
6. Pearl J. Comment: Graphical models, causality, and intervention. Statistical Science 1993; 8(3):266–269.
7. Pearl J. Causality: Models, Reasoning, and Inference. Cambridge University Press: New York, 2000.

Clark Glymour writes:

Nancy Cartwright devotes half of her new book, Hunting Causes and Using Them, to criticizing "Bayes Net Methods"–as she calls them–and what she takes to be their assumptions. All of her critical claims are false or at best fractionally true. This paper reviews the literature she addresses but appears not to have met. Please click here to read further.

For related discussion, please see a previous post by Judea Pearl.

Judea Pearl writes:

A new book on causality came out last month, Hunting Causes and Using Them by Nancy Cartwright (Cambridge University Press, 2007.) Cartwright is a renown philosopher of science who has given much thought to the methodology of econometrics, and I was keenly curious to read her take on the current state of causality in economics.

Cartwright summarizes what economists such as Heckman, Hoover, Leroy and Hendry said and wrote about causal analysis in economics, she occasionally criticizes their ideas, and further discusses related works by philosophers such as Hausman and Woodward, but what I found surprising is that she rarely tells us how WE OUGHT to think about causes and effects in economic models. Given that economists admit to the chaotic state of affairs in their court, the role of philosophy should be, in my opinion, to instill clarity and provide coherent unification of the field. This I could not find in the book.

Additionally, and this naturally is my main concern, Cartwright rejects the surgery method as the basis of counterfactual and causal analysis and, in so doing, unveils and reinforces some of the most serious misconceptions that have hindered causal analysis in the past half century (see my earlier posting on Heckman's articles.)

I will focus on the latter point, for this will illuminate others.

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In his 2005 article "The Scientific Model of Causality" (Sociological Methodology, vol. 35 (1) page 40,) Jim Heckman reviews the historical development of causal notions in econometrics, and paints an extremely complimentary picture of the current state of this development.

As an illustration of econometric methods and concepts, Heckman discusses the classical problem of estimating the causal effect of Y₂ on Y₁ in the following systems of equations

Y₁ = a₁ + c₁₂Y₂ + b₁₁X₁ + b₁₂ X₂ + U₁     (16a)
Y₂ = a₂ + c₂₁Y₁ + b₂₁X₁ + b₂₂ X₂ + U₂     (16b)

where Y₁ and Y₂ represent, respectively, the consumption levels of two interacting agents, and X₁, X₂, the levels of their income.

Unexpectedly, on page 44, Heckman makes a couple of remarks that almost threw me off my chair; here they are:

"Controlled variation in external (forcing) variables is the key to defining causal effects in nonrecursive models. It is of some interest to readers of Pearl (2000) to compare my use of the standard simultaneous equations model of econometrics in defining causal parameters to his. In the context of equations (16a) and (16b), Pearl defines a causal effect by "shutting one equation down" or performing "surgery" in his colorful language."

"He implicitly assumes that "surgery," or shutting down an equation in a system of simultaneous equations, uniquely fixes one outcome or internal variable (the consumption of the other person in my example). In general, it does not. Putting a constraint on one equation places a restriction on the entire set of internal variables. In general, no single equation in a system of simultaneous equation uniquely determines any single outcome variable. Shutting down one equation might also affect the parameters of the other equations in the system and violate the requirements of parameter stability."

I wish to bring up for blog discussion the following four questions:

1. Is Heckman right in stating that in nonrecursive systems one should not define causal effect by surgery?
2. What is the causal effect of Y₂ on Y₁ in the model of Eqs. (16a -16b) ??
3. What does Heckman mean when he objects to surgery as the basis for defining causal parameters?
4. What did he have in mind when he offered "… the standard simultaneous equations model of econometrics" as an alternative to surgery "in defining causal parameters"?

The following are the best answers I could give to these questions, but I would truly welcome insights from other participants, especially economists and social scientists (including Jim Heckman, of course).

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