The Book of Why: The New Science of Cause and Effect

by Judea Pearl

At the first level, association, we are looking for regularities in observations. This is what an owl does when observing how a rat moves and figuring out where the rodent is likely to be a moment later, and it is what a computer Go program does when it studies a database of millions of Go games so that it can figure out which moves are associated with a higher percentage of wins. We say that one event is associated with another if observing one changes the likelihood of observing the other. The first rung of the ladder calls for predictions based on passive observations. It is characterized by the question “What if I see …?” For instance, imagine a marketing director at a department store who asks, “How likely is a customer who bought toothpaste to also buy dental floss?”

As these examples illustrate, the defining query of the second rung of the Ladder of Causation is “What if we do…?” What will happen if we change the environment? We can write this kind of query as P(floss | do(toothpaste)), which asks about the probability that we will sell floss at a certain price, given that we set the price of toothpaste at another price. Another popular question at the second level of causation is “How?,” which is a cousin of “What if we do…?” For instance, the manager may tell us that we have too much toothpaste in our warehouse. “How can we sell it?” he asks. That is, what price should we set for it? Again, the question refers to an intervention, which we want to perform mentally before we decide whether and how to do it in real life. That requires a causal model.

While reasoning about interventions is an important step on the causal ladder, it still does not answer all questions of interest. We might wonder, My headache is gone now, but why? Was it the aspirin I took? The food I ate? The good news I heard? These queries take us to the top rung of the Ladder of Causation, the level of counterfactuals, because to answer them we must go back in time, change history, and ask, “What would have happened if I had not taken the aspirin?” No experiment in the world can deny treatment to an already treated person and compare the two outcomes, so we must import a whole new kind of knowledge. Counterfactuals have a particularly problematic relationship with data because data are, by definition, facts. They cannot tell us what will happen in a counterfactual or imaginary world where some observed facts are bluntly negated. Yet the human mind makes such explanation-seeking inferences reliably and repeatably.

The laws of physics, for example, can be interpreted as counterfactual assertions, such as “Had the weight on this spring doubled, its length would have doubled as well” (Hooke’s law). This statement is, of course, backed by a wealth of experimental (rung-two) evidence, derived from hundreds of springs, in dozens of laboratories, on thousands of different occasions. However, once anointed as a “law,” physicists interpret it as a functional relationship that governs this very spring, at this very moment, under hypothetical values of the weight. All of these different worlds, where the weight is x pounds and the length of the spring is Lx inches, are treated as objectively knowable and simultaneously active, even though only one of them actually exists.

The main point is this: while probabilities encode our beliefs about a static world, causality tells us whether and how probabilities change when the world changes, be it by intervention or by act of imagination.

Galton had started gathering a variety of “anthropometric” statistics: height, forearm length, head length, head width, and so on. He noticed that when he plotted height against forearm length, for instance, the same phenomenon of regression to the mean took place. Tall men usually had longer-than-average forearms—but not as far above average as their height. Clearly height is not a cause of forearm length, or vice versa. If anything, both are caused by genetic inheritance. Galton started using a new word for this kind of relationship: height and forearm length were “co-related.” Eventually, he opted for the more normal English word “correlated.”

Later he realized an even more startling fact: in generational comparisons, the temporal order could be reversed. That is, the fathers of sons also revert to the mean. The father of a son who is taller than average is likely to be taller than average but shorter than his son (see Figure 2.2). Once Galton realized this, he had to give up any idea of a causal explanation for regression, because there is no way that the sons’ heights could cause the fathers’ heights.

Belief propagation formally works in exactly the same way whether the arrows are noncausal or causal. Nevertheless, you may have the intuitive feeling that we have done something more meaningful in the latter case than in the former. That is because our brains are endowed with special machinery for comprehending cause-effect relationships (such as cancer and mammograms). Not so for mere associations (such as tea and scones).

A B C. This junction is the simplest example of a “chain,” or of mediation. In science, one often thinks of B as the mechanism, or “mediator,” that transmits the effect of A to C. A familiar example is Fire Smoke Alarm. Although we call them “fire alarms,” they are really smoke alarms.

A B C. This kind of junction is called a “fork,” and B is often called a common cause or confounder of A and C. A confounder will make A and C statistically correlated even though there is no direct causal link between them. A good example (due to David Freedman) is Shoe Size Age of Child Reading Ability. Children with larger shoes tend to read at a higher level. But the relationship is not one of cause and effect. Giving a child larger shoes won’t make him read better! Instead, both variables are explained by a third, which is the child’s age. Older children have larger shoes, and they also are more advanced readers. We can eliminate this spurious correlation, as Karl Pearson and George Udny Yule called it, by conditioning on the child’s age. For instance, if we look only at seven-year-olds, we expect to see no relationship between shoe size and reading ability. As in the case of chain junctions, A and C are conditionally independent, given B.

A B C. This is the most fascinating junction, called a “collider.” Felix Elwert and Chris Winship have illustrated this junction using three features of Hollywood actors: Talent Celebrity Beauty. Here we are asserting that both talent and beauty contribute to an actor’s success, but beauty and talent are completely unrelated to one another in the general population. We will now see that this collider pattern works in exactly the opposite way from chains or forks when we condition on the variable in the middle. If A and C are independent to begin with, conditioning on B will make them dependent. For example, if we look only at famous actors (in other words, we observe the variable Celebrity = 1), we will see a negative correlation between talent and beauty: finding out that a celebrity is unattractive increases our belief that he or she is talented. This negative correlation is sometimes called collider bias or the “explain-away” effect.

We really mean that any prior causes of A can be adequately summarized in the prior probability P(A) that A is true. For example, in the Disease Test example, family history might be a cause of Disease. But as long as we are sure that this family history will not affect the variable Test (once we know the status of Disease), we need not represent it as a node in the graph. However, if there is a cause of Disease that also directly affects Test, then that cause must be represented explicitly in the diagram. In the case where the node A has a parent, A has to “listen” to its parent before deciding on its own state. In our mammogram example, the parent of Test was Disease. We can show this “listening” process with a 2 × 2 table (see Table 3.2). For example, if Test “hears” that D = 0, then 88 percent of the time it will take the value T = 0, and 12 percent of the time it will take the value T = 1. Notice that the second column of this table contains the same information we saw earlier from the Breast Cancer Surveillance Consortium: the false positive rate (upper right corner) is 12 percent, and the sensitivity (lower right corner) is 73 percent. The remaining two entries are filled in to make each row sum to 100 percent. TABLE 3.2. A simple conditional probability table.

In the last chapter, we looked at three rules that tell us how to stop the flow of information through any individual junction. I will repeat them for emphasis: (a) In a chain junction, A B C, controlling for B prevents information about A from getting to C or vice versa. (b) Likewise, in a fork or confounding junction, A B C, controlling for B prevents information about A from getting to C or vice versa. (c) Finally, in a collider, A B C, exactly the opposite rules hold. The variables A and C start out independent, so that information about A tells you nothing about C. But if you control for B, then information starts flowing through the “pipe,” due to the explain-away effect. We must also keep in mind another fundamental rule: (d) Controlling for descendants (or proxies) of a variable is like “partially” controlling for the variable itself. Controlling for a descendant of a mediator partly closes the pipe; controlling for a descendant of a collider partly opens the pipe. Now, what if we have longer pipes with more junctions, like this: A B C D E F G H I J? The answer is very simple: if a single junction is blocked, then J cannot “find out” about A through this path. So we have many options to block communication between A and J: control for B, control for C, don’t control for D (because it’s a collider), control for E, and so forth. Any one of these is sufficient. This is why the usual statistical procedure of controlling for everything that we can measure is so misguide...

In fact, the full model in Forbes’ paper has a few more variables and looks like the diagram in Figure 4.7. Note that Game 5 is embedded in this model in the sense that the variables A, B, C, X, and Y have exactly the same relationships. So we can transfer our conclusions over and conclude that we have to control for A and B or for C; but C is an unobservable and therefore uncontrollable variable. In addition we have four new confounding variables: D = parental asthma, E = chronic bronchitis, F = sex, and G = socioeconomic status. The reader might enjoy figuring out that we must control for E, F, and G, but there is no need to control for D. So a sufficient set of variables for deconfounding is A, B, E, F, and G. FIGURE 4.7. Andrew Forbes’s model of smoking (X) and asthma (Y).

Several studies had already shown that the babies of smoking mothers weighed less at birth on average than the babies of nonsmokers, and it was natural to suppose that this would translate to poorer survival. Indeed, a nationwide study of low-birth-weight infants (defined as those who weigh less than 5.5 pounds at birth) had shown that their death rate was more than twenty times higher than that of normal-birth-weight infants. Thus, epidemiologists posited a chain of causes and effects: Smoking Low Birth Weight Mortality. What Yerushalmy found in the data was unexpected even to him. It was true that the babies of smokers were lighter on average than the babies of nonsmokers (by seven ounces). However, the low-birth-weight babies of smoking mothers had a better survival rate than those of nonsmokers. It was as if the mother’s smoking actually had a protective effect. If Fisher had discovered something like this, he probably would have loudly proclaimed it as one of the benefits of smoking. Yerushalmy, to his credit, did not. He wrote, much more cautiously, “These paradoxical findings raise doubts and argue against the proposition that cigarette smoking acts as an exogenous factor which interferes with intrauterine development of the fetus.” In short, there is no causal path from Smoking to Mortality. Modern epidemiologists believe that Yerushalmy was wrong. Most believe that smoking does increase neonatal mortality—for example, because it interferes with oxygen transfer acr...

In 1946, Joseph Berkson, a biostatistician at the Mayo Clinic, pointed out a peculiarity of observational studies conducted in a hospital setting: even if two diseases have no relation to each other in the general population, they can appear to be associated among patients in a hospital. To understand Berkson’s observation, let’s start with a causal diagram (Figure 6.3). It’s also helpful to think of a very extreme possibility: neither Disease 1 nor Disease 2 is ordinarily severe enough to cause hospitalization, but the combination is. In this case, we would expect Disease 1 to be highly correlated with Disease 2 in the hospitalized population. FIGURE 6.3. Causal diagram for Berkson’s paradox. By performing a study on patients who are hospitalized, we are controlling for Hospitalization. As we know, conditioning on a collider creates a spurious association between Disease 1 and Disease 2. In many of our previous examples the association was negative because of the explain-away effect, but here it is positive because both diseases have to be present for hospitalization (not just one). However, for a long time epidemiologists refused to believe in this possibility. They still didn’t believe it in 1979, when David Sackett of McMaster University, an expert on all sorts of statistical bias, provided strong evidence that Berkson’s paradox is real. In one example (see Table 6.3), he studied two groups of diseases: respiratory and bone. About 7.5 percent of people in the general p...

Try this experiment: Flip two coins simultaneously one hundred times and write down the results only when at least one of them comes up heads. Looking at your table, which will probably contain roughly seventy-five entries, you will see that the outcomes of the two simultaneous coin flips are not independent. Every time Coin 1 landed tails, Coin 2 landed heads. How is this possible? Did the coins somehow communicate with each other at light speed? Of course not. In reality you conditioned on a collider by censoring all the tails-tails outcomes.

The study was observational, not randomized, with sixty men and sixty women. This means that the patients themselves decided whether to take or not to take the drug. Table 6.4 shows how many of each gender received Drug D and how many were subsequently diagnosed with heart attack. Let me emphasize where the paradox is. As you can see, 5 percent (one in twenty) of the women in the control group later had a heart attack, compared to 7.5 percent of the women who took the drug. So the drug is associated with a higher risk of heart attack for women. Among the men, 30 percent in the control group had a heart attack, compared to 40 percent in the treatment group. So the drug is associated with a higher risk of heart attack among men. Dr. Simpson was right. TABLE 6.4. Fictitious data illustrating Simpson’s paradox. But now look at the third line of the table. Among the control group, 22 percent had a heart attack, but in the treatment group only 18 percent did. So, if we judge on the basis of the bottom line, Drug D seems to decrease the risk of heart attack in the population as a whole. Welcome to the bizarre world of Simpson’s paradox!

The diagram in Figure 6.4 encodes the crucial information that gender is unaffected by the drug and, in addition, gender affects the risk of heart attack (men being at greater risk) and whether the patient chooses to take Drug D. In the study, women clearly had a preference for taking Drug D and men preferred not to. Thus Gender is a confounder of Drug and Heart Attack. For an unbiased estimate of the effect of Drug on Heart Attack, we must adjust for the confounder. We can do that by looking at the data for men and women separately, then taking the average: FIGURE 6.4. Causal diagram for the Simpson’s paradox example. • For women, the rate of heart attacks was 5 percent without Drug D and 7.5 percent with Drug D. • For men, the rate of heart attacks was 30 percent without Drug D and 40 percent with. • Taking the average (because men and women are equally frequent in the general population), the rate of heart attacks without Drug D is 17.5 percent (the average of 5 and 30), and the rate with Drug D is 23.75 percent (the average of 7.5 and 40). This is the clear and unambiguous answer we were looking for. Drug D isn’t BBG, it’s BBB: bad for women, bad for women, and bad for people.

So far most of our examples of Simpson’s reversal and paradox have involved binary variables: a patient either got Drug D or didn’t and either had a heart attack or didn’t. However, the reversal can also occur with continuous variables and is perhaps easier to understand in that case because we can draw a picture. Consider a study that measures weekly exercise and cholesterol levels in various age groups. When we plot hours of exercise on the x-axis and cholesterol on the y-axis, as in Figure 6.6(a), we see in each age group a downward trend, indicating perhaps that exercise reduces cholesterol. On the other hand, if we use the same scatter plot but don’t segregate the data by age, as in Figure 6.6(b), then we see a pronounced upward trend, indicating that the more people exercise, the higher their cholesterol becomes. Once again we seem to have a BBG drug situation, where Exercise is the drug: it seems to have a beneficial effect in each age group but a harmful effect on the population as a whole. To decide whether Exercise is beneficial or harmful, as always, we need to consult the story behind the data. The data show that older people in our population exercise more. Because it seems more likely that Age causes Exercise rather than vice versa, and since Age may have a causal effect on Cholesterol, we conclude that Age may be a confounder of Exercise and Cholesterol. So we should control for Age. In other words, we should look at the age-segregated data and conclude that...

In this approach we pretend that the data came from some unknown random source and use standard statistical methods to find the line (or, in this case, plane) that best fits the data. The output of such an approach might be an equation that looks like this: S = $65,000 + 2,500 × EX + 5,000 × ED (8.1) Equation 8.1 tells us that (on average) the base salary of an employee with no experience and only a high school diploma is $65,000. For each year of experience, the salary increases by $2,500, and for each additional educational degree (up to two), the salary increases by $5,000. Accordingly, a regression analyst would claim, our estimate of Alice’s salary, if she had a college degree, is $65,000 + $2,500 × 6 + $5,000 × 1 = $85,000. The ease and familiarity of such imputation techniques explain why Rubin’s conception of causal inference as a missing-data problem has enjoyed broad popularity. Alas, as innocuous as these interpolation methods appear, they are fundamentally flawed. They are data driven, not model driven. All the missing data are filled in by examining other values in the table. As we have learned from the Ladder of Causation, any such method is doomed to start with; no methods based only on data (rung one) can answer counterfactual questions (rung three).

Now let’s see how a structural causal model would treat the same data. First, before we even look at the data, we draw a causal diagram (Figure 8.3). The diagram encodes the causal story behind the data, according to which Experience listens to Education and Salary listens to both. In fact, we can already tell something very important just by looking at the diagram. If our model were wrong and EX were a cause of ED, rather than vice versa, then Experience would be a confounder, and matching employees with similar experience would be completely appropriate. With ED as the cause of EX, Experience is a mediator. As you surely know by now, mistaking a mediator for a confounder is one of the deadliest sins in causal inference and may lead to the most outrageous errors. The latter invites adjustment; the former forbids it. FIGURE 8.3. Causal diagram for the effect of education (ED) and experience (EX) on salary (S).

Unlike Kruskal, we can draw a diagram and see exactly what the problem is. Figure 9.5 shows the causal diagram representing Kruskal’s counterexample. Does it look slightly familiar? It should! It is exactly the same diagram that Barbara Burks drew in 1926, but with different variables. One is tempted to say, “Great minds think alike,” but perhaps it would be more appropriate to say that great problems attract great minds. FIGURE 9.5. Causal diagram for Berkeley admissions paradox—Kruskal’s version. Kruskal argued that the analysis in this situation should control for both the department and the state of residence, and a look at Figure 9.5 explains why this is so. To disable all but the direct path, we need to stratify by department. This closes the indirect path Gender Department Outcome. But in so doing, we open the spurious path Gender Department State of Residence Outcome, because of the collider at Department. If we control for State of Residence as well, we close this path, and therefore any correlation remaining must be due to the (discriminatory) direct path Gender Outcome. Lacking diagrams, Kruskal had to convince Bickel with numbers, and in fact his numbers showed the same thing. If we do not adjust for any variables, then females have a lower admission rate. If we adjust for Department, then females appear to have a higher admission rate. If we adjust for both Department and State of Residence, then once again the numbers show a lower admission rate for females.

This is not a Simpson’s paradox situation. It doesn’t matter whether we aggregate the data or stratify it; in every severity category, as well as in the aggregate, survival was slightly greater for soldiers who did not get tourniquets. (The difference in survival rates was, however, too small to be statistically significant.) What went wrong? One possibility, of course, is that tourniquets aren’t better. Our belief in them could be a case of confirmation bias. When a soldier gets a tourniquet and survives, his doctors and his buddies will say, “That tourniquet saved his life.” But if the soldier doesn’t get a tourniquet and survives, nobody will say, “Not putting on a tourniquet saved his life.” So tourniquets might get more credit than their due, and nonintervention doesn’t get any credit. But there was another possible bias in this study, which Kragh himself pointed out: the doctors only collected data on those soldiers who survived long enough to get to the hospital in the first place. To see why this matters, let’s draw a causal diagram (Figure 9.13). FIGURE 9.13. Causal diagram for tourniquet example. The dashed line is a hypothetical causal effect (not supported by the data). In this figure, we can see that Injury Severity is a confounder of all three variables, the treatment (Tourniquet Use), the mediator (Pre-Admission Survival), and the outcome (Post-Admission Survival). It is therefore appropriate and necessary to condition on Injury Severity, as Kragh did in his...

Suppose we want to know the effect of an online advertisement (X) on the likelihood that a consumer will purchase the product (Y)—say, a surfboard. We have data from studies in five different places: Los Angeles, Boston, San Francisco, Toronto, and Honolulu. Now we want to estimate how effective the advertisement will be in Arkansas. Unfortunately, each population and each study differs slightly. For example, the Los Angeles population is younger than our target population, and the San Francisco population differs in click-through rate. Figure 10.1 shows the unique characteristics of each population and each study. Can we combine the data from these remote and disparate studies to estimate the ad’s effectiveness in Arkansas? Can we do it without taking any data in Arkansas? Or perhaps by measuring merely a small set of variables or conducting a pilot observational study? FIGURE 10.1. The transportability problem. Figure 10.2 translates these differences into graphical form. The variable Z represents age, which is a confounder; young people may be more likely to see the ad and more likely to buy the product even if they don’t see the ad. The variable W represents clicking on a link to get more information. This is a mediator, a step that must take place in order to convert “seeing the advertisement” into “buying the product.” The letter S, in each case, stands for a “difference-producing” variable, a hypothetical variable that points to the characteristic by which the two p...