Among 4,200 adults in the National Health and Nutrition Examination Survey (NHANES) of 2017 to 2018, 22.9% of the 1,182 former smokers report diagnosed diabetes, against 13.1% of the 3,018 who never smoked. Conditional Probability and the Law of Total Probability showed that much of that gap belongs to age, since former smokers are older; adjusting for age shrinks the risk ratio from 1.756 to about 1.2. Adjusting for age was right. Would adjusting for body mass index also be right, or for any other variable that differs between the groups, and how is that decided?
Confounding is a bias in a comparison of treated and untreated units that arises because the treatment and the outcome share a cause. The answer to the question is that whether a variable should be adjusted for is not a property of the data: the same table can call for adjustment under one account of the causes and forbid it under another. A causal diagram writes that account down, as a directed acyclic graph whose arrows point from causes to effects, and a few rules turn the graph into a list of the variables to adjust for. This article sets out those rules, proves the ones that are elementary, cites the ones that are not, and uses them on the running example.
The route is as follows. First the graph and the factorization it stands for, with the three structures from which every graph is built (chain, fork and collider), proved from the factorization. Then d-separation, which reads independence from a graph, and the effect of an intervention, defined by deleting an equation. Then the backdoor criterion, with a proof for the simplest valid adjustment set, and the adjustment formula proved from the potential-outcome conditions of Potential Outcomes and the Average Treatment Effect. Then Simpson's paradox read as confounding, and the two ways adjustment makes things worse: conditioning on a collider (Berkson's paradox and M-bias) and conditioning on a mediator. The article assumes conditional independence and the law of total probability; Matching and Propensity Scores takes up estimation once the adjustment set is chosen.
Notation and the question asked
The unit's notation is used throughout. A unit has a binary treatment $W$ (1 for treated, here a former smoker; 0 for untreated, a never smoker), potential outcomes $Y(1)$ and $Y(0)$, the outcomes the unit would have under each treatment, and pre-treatment covariates $X$. The observed outcome is $Y = W\,Y(1) + (1 - W)\,Y(0)$; this line is called consistency. Units are independent draws from a population. The average treatment effect is $\tau = E[Y(1) - Y(0)]$, and for a binary outcome the causal risk ratio is $E[Y(1)]/E[Y(0)]$. Independence is written $A \perp\!\!\!\perp B$ and conditional independence $A \perp\!\!\!\perp B \mid C$.
Potential Outcomes and the Average Treatment Effect proves that in a randomized experiment the difference in observed means estimates $\tau$ without bias. In observational data the treated and untreated may differ in their potential outcomes, and the question of this article is which covariates $X$ make them comparable once $X$ is held fixed. The formal version of "comparable" is conditional exchangeability:
$$Y(w) \perp\!\!\!\perp W \mid X \quad\text{for } w = 0, 1.$$
The propensity article calls the slightly stronger joint statement $\{Y(1), Y(0)\} \perp\!\!\!\perp W \mid X$ unconfoundedness. Neither can be checked from the data, because $Y(1)$ is never seen for an untreated unit. A causal diagram is a way to argue for or against it from knowledge of the causes.
Causal diagrams and what they assert
A directed acyclic graph (DAG) has nodes for variables and arrows between them, with no directed cycle: following arrows forward never returns to the start. The parents of a node are the nodes with arrows into it; its descendants are the nodes reached from it by following arrows forward; its ancestors are the nodes from which it is reached. A path between two nodes is a sequence of distinct nodes each joined to the next by an arrow in either direction.
A graph becomes a causal diagram through an assumption about how the data were generated. Pearl (1995, §2.2) takes each variable $V_i$ to be determined by its parents and an error term,
$$V_i = f_i(\mathrm{pa}_i, \varepsilon_i),$$
with the errors $\varepsilon_i$ mutually independent and the functions $f_i$ left unspecified. A variable that influences two or more others and is not measured must appear in the graph (as an unmeasured node, written $U$), since otherwise the errors would not be independent. A missing arrow is the strong claim: it says one variable has no direct effect on another.
Under this assumption the joint distribution of discrete variables factorizes over the graph (Pearl, 1995, eq. 2):
$$P(v_1, \ldots, v_n) = \prod_i P(v_i \mid \mathrm{pa}_i).$$
Each factor is a conditional probability of a variable given its parents. With densities the same product holds with conditional densities. Everything this article proves about graphs is proved from this product, and every result applies whenever the product holds.
The running diagram. Age affects whether an adult has ever smoked and quit (older adults have had longer to quit), and age affects diabetes. Smoking history may affect diabetes. Smoking history may also affect weight: Yeh and colleagues (2010) set out to test whether quitting raises the short-term risk of diabetes, possibly through the weight gained after quitting. Weight in turn affects diabetes. A minimal diagram is
$$\text{Age} \to W, \quad \text{Age} \to Y, \quad W \to Y, \quad W \to B, \quad B \to Y,$$
where $B$ is body mass index. It leaves out sex, income, physical activity and much else; the cautions near the end of the article return to them.
Three elementary structures
Every path is a chain of three-node pieces, and each piece has one of three forms. In a chain $A \to C \to B$ the middle node passes an influence along. In a fork $A \leftarrow C \to B$ the middle node is a common cause. In a collider $A \to C \leftarrow B$ two arrows meet head to head at the middle node, a common effect. Here is the idea in one sentence: a chain and a fork make $A$ and $B$ dependent until $C$ is held fixed, while a collider leaves them independent until $C$ is held fixed.
Theorem 1 (the three structures). Let three variables have a joint distribution that factorizes over the graph shown, with no other arrows.
- Chain $A \to C \to B$ and fork $A \leftarrow C \to B$: $A \perp\!\!\!\perp B \mid C$.
- Collider $A \to C \leftarrow B$: $A \perp\!\!\!\perp B$.
Proof. Take discrete variables; the same steps with densities cover the continuous case.
(1) For the chain the factorization is $P(a, b, c) = P(a)\,P(c \mid a)\,P(b \mid c)$. Wherever $P(c) > 0$, divide by $P(c)$ and use $P(a)P(c \mid a) = P(a, c)$:
$$P(a, b \mid c) = \frac{P(a, c)}{P(c)}\,P(b \mid c) = P(a \mid c)\,P(b \mid c).$$
For the fork the factorization is $P(a, b, c) = P(c)\,P(a \mid c)\,P(b \mid c)$, and dividing by $P(c)$ gives the same product.
(2) For the collider the factorization is $P(a, b, c) = P(a)\,P(b)\,P(c \mid a, b)$. Summing over $c$, and using $\sum_c P(c \mid a, b) = 1$,
$$P(a, b) = P(a)\,P(b)\sum_c P(c \mid a, b) = P(a)\,P(b). \qquad\square$$
The converse statements, that $A$ and $B$ are dependent in a chain or fork when $C$ is not fixed and dependent in a collider when $C$ is fixed, do not follow from the factorization alone: a factorization over a graph allows every independence the graph implies and may have more by numerical coincidence. They hold for most numbers the factors could take, and Proposition 1 below gives a collider where the dependence is computed and is never zero. The same holds for a descendant of a collider: holding fixed a variable caused by $C$ (a report, a hospital admission, a test result) is a partial version of holding $C$ fixed, and it too creates dependence between $A$ and $B$ (Hernán and Robins, 2020, Fine Point 6.1, rule 4).
Reading independence from a graph: d-separation
Paths longer than three nodes are judged one node at a time. Pearl (1995, Definition 1) gives the rule. Let $\mathcal X$, $\mathcal Y$ and $\mathcal Z$ be disjoint sets of nodes. A path between a node of $\mathcal X$ and a node of $\mathcal Y$ is blocked by $\mathcal Z$ if it contains a node $v$ such that either
- $v$ is a collider on the path (two arrowheads meet at it) and neither $v$ nor any descendant of $v$ is in $\mathcal Z$, or
- $v$ is not a collider on the path and $v$ is in $\mathcal Z$.
A path that is not blocked is open. $\mathcal Z$ d-separates $\mathcal X$ from $\mathcal Y$ if it blocks every path between them. Note that whether a node is a collider depends on the path: in the right panel of the figure, $M$ is a collider on $W \leftarrow U_1 \to M \leftarrow U_2 \to Y$ but would be a non-collider on a path that passed through it along one arrow in and one arrow out.
Theorem 2 (d-separation; cited). If $\mathcal Z$ d-separates $\mathcal X$ from $\mathcal Y$ in a DAG, then $\mathcal X \perp\!\!\!\perp \mathcal Y \mid \mathcal Z$ in every distribution that factorizes over the DAG. Conversely, if $\mathcal Z$ does not d-separate them, some distribution that factorizes over the DAG has $\mathcal X$ and $\mathcal Y$ dependent given $\mathcal Z$.
The first half is soundness and the second completeness. Pearl (1995, p. 671) states the correspondence between d-separation and the independences implied by the factorization, citing Geiger, Verma and Pearl (1990), whose abstract describes the soundness of the criterion and its completeness. Hernán and Robins (2020, Fine Point 6.1) state the first half as a theorem of Pearl (1988) under the causal Markov assumption. Theorem 1 is the three-node case of soundness. The assumption that independence holds only where the graph says (no numerical coincidences) is called faithfulness; it is needed to read a dependence from a graph, never to read an independence.
A mechanical test is equivalent (Lauritzen et al., 1990, as stated by Pearl, 1995, p. 672): keep only $\mathcal X \cup \mathcal Y \cup \mathcal Z$ and their ancestors, join every pair of nodes that share a child, drop the directions, and ask whether removing $\mathcal Z$ disconnects $\mathcal X$ from $\mathcal Y$. The article's script implements this test and uses it to check every adjustment set named below.
Interventions and the effect of a treatment
A comparison of treated and untreated units answers a question about the distribution as it is. A causal question asks what would happen if the treatment were set by intervention. Pearl (1995, Definition 2 and eq. 5) defines the effect of setting $W = w$ by deleting the equation for $W$ from the model and substituting $w$ wherever $W$ appears. For the factorization this deletes one factor, the probability of $W$ given its parents. The truncated factorization of the post-intervention distribution is
$$P_w(v) = \prod_{i:\ V_i \ne W} P(v_i \mid \mathrm{pa}_i)\,\Big|_{W = w},$$
for every configuration $v$ with $W = w$ (and zero otherwise). Pearl writes the resulting distribution of the outcome as $\mathrm{pr}(y \mid \check x)$. In the unit's notation the outcome of the modified model is the potential outcome $Y(w)$: Pearl (1995, §2.2) identifies the potential response of Rubin's model with the value the structural equation assigns when the treatment is fixed. The causal question is then about $P(Y(w) = y)$, and the statistical question is whether it can be computed from the distribution of the observed variables.
The first answer is the simplest one. Here is the idea in one sentence: holding fixed every direct cause of the treatment leaves no route by which anything else could make the treated and untreated differ.
Theorem 3 (adjusting for the parents of the treatment). Let all variables be discrete with a distribution that factorizes over a causal DAG, let $Z$ be the set of parents of $W$, and suppose $P(W = w \mid Z = z) > 0$ for every $z$ with $P(Z = z) > 0$. Then
$$P(Y(w) = y) = \sum_z P(Y = y \mid W = w, Z = z)\,P(Z = z).$$
Proof. Wherever $P(w \mid z) > 0$, the truncated factorization is the full factorization divided by the deleted factor:
$$P_w(v) = \frac{\prod_i P(v_i \mid \mathrm{pa}_i)}{P(w \mid z)} = \frac{P(v)}{P(w \mid z)}.$$
To get the distribution of $Y$, sum over all configurations with $Y = y$ and $W = w$. Group them by the value $z$ of the parents of $W$; within a group the denominator is constant. Let $R$ denote the remaining variables (all but $Y$, $W$ and $Z$). Then
$$P(Y(w) = y) = \sum_z \frac{1}{P(w \mid z)}\sum_r P(y, w, z, r) = \sum_z \frac{P(y, w, z)}{P(w \mid z)} = \sum_z \frac{P(y \mid w, z)\,P(w \mid z)\,P(z)}{P(w \mid z)},$$
which is the stated sum. $\square$
The parents of $W$ are often unmeasured, and other sets work as well; the next section says which.
The backdoor criterion
A path between $W$ and $Y$ that begins with an arrow into $W$ is a backdoor path. In the running diagram $W \leftarrow \text{Age} \to Y$ is one. Backdoor paths carry association that is not effect: the treated and untreated differ in age, and age differs in diabetes, whether or not smoking does anything.
Definition (Pearl, 1995, Definition 3). A set $Z$ of variables satisfies the backdoor criterion relative to $(W, Y)$ if
- no node of $Z$ is a descendant of $W$, and
- $Z$ blocks every path between $W$ and $Y$ that contains an arrow into $W$.
Theorem 4 (the backdoor adjustment; Pearl, 1995, Theorem 1; cited). If $Z$ satisfies the backdoor criterion relative to $(W, Y)$, and $P(W = w \mid Z = z) > 0$ wherever $P(Z = z) > 0$, the effect of $W$ on $Y$ is identifiable and
$$P(Y(w) = y) = \sum_z P(Y = y \mid W = w, Z = z)\,P(Z = z).$$
The parents of $W$ always satisfy the criterion (no parent of $W$ descends from $W$ in an acyclic graph, and every backdoor path enters $W$ through a parent, which is a non-collider on that path and is held fixed), so Theorem 3 is the special case $Z = \mathrm{pa}(W)$ of Theorem 4. The general proof uses the rules of Pearl's intervention calculus and is not given here. In the potential-outcome language, Hernán and Robins (2020, §7.2 and Technical Point 7.1) state that a set satisfying the backdoor criterion always implies conditional exchangeability $Y(w) \perp\!\!\!\perp W \mid Z$, even without faithfulness, and that the converse holds under faithfulness in the causal model they adopt. Pearl (1995, p. 671) describes the criterion as equivalent to the ignorability condition of Rosenbaum and Rubin (1983), a claim Sobel (1995, p. 701) disputed in the published discussion of the paper ("Neither condition implies the other"); the precise relation is the one just stated.
Example (the running diagram). The backdoor paths from $W$ to $Y$ are those through age. The set $\{\text{Age}\}$ satisfies the criterion. The set $\{\text{Age}, B\}$ does not, because $B$ is a descendant of $W$: condition 1 fails. The empty set does not, because $W \leftarrow \text{Age} \to Y$ is open. The script confirms all three with the d-separation test.
Example (M-structure). In the right panel, $W \leftarrow U_1 \to M \leftarrow U_2 \to Y$ is the only backdoor path, and $M$ is a collider on it, so the empty set satisfies the criterion: the crude comparison is unbiased. Adding $M$ violates condition 2, since holding a collider fixed opens the path. Adding $M$ together with $U_1$ or with $U_2$ satisfies it again, but $U_1$ and $U_2$ are unmeasured. The section on M-bias computes the damage.
The criterion is a sufficient condition for one formula, not a complete list of identification strategies. Pearl (1995, Theorem 2) gives a second, the front-door criterion, for effects that pass entirely through a measured intermediate, and the calculus of intervention in §4 of the same paper derives effect formulas for further graphs.
The adjustment formula from exchangeability
The backdoor formula can be proved directly, in the potential-outcome language, from three conditions on the population rather than from a graph. Here is the plan: average the potential outcome over the covariates, swap the conditioning on treatment in by exchangeability, and replace the potential outcome by the observed one by consistency. The result is the point-treatment case of the g-formula (the g-computation algorithm formula of Robins, 1986, as Hernán and Robins, 2020, §13.4, describe it), and in epidemiology it is standardization (Hernán and Robins, 2020, §2.3).
Theorem 5 (the g-formula). Suppose
- consistency: $Y = Y(w)$ whenever $W = w$;
- conditional exchangeability: $Y(w) \perp\!\!\!\perp W \mid X$;
- positivity: $P(W = w \mid X = x) > 0$ for every $x$ with $P(X = x) > 0$.
Then, for discrete $X$ and $\mu_w(x) = E[Y \mid W = w, X = x]$,
$$E[Y(w)] = \sum_x \mu_w(x)\,P(X = x).$$
For general $X$ the same steps give $E[Y(w)] = E[\mu_w(X)]$.
Proof. By the law of total expectation,
$$E[Y(w)] = \sum_x E[Y(w) \mid X = x]\,P(X = x).$$
For each $x$ with $P(X = x) > 0$, positivity makes the event $\{W = w, X = x\}$ have positive probability, so conditioning on it is defined. By conditional exchangeability, $Y(w)$ has the same distribution given $\{X = x\}$ as given $\{W = w, X = x\}$, so
$$E[Y(w) \mid X = x] = E[Y(w) \mid W = w, X = x].$$
On the event $W = w$ consistency gives $Y(w) = Y$, so the right side is $E[Y \mid W = w, X = x] = \mu_w(x)$. Substituting into the first display proves the formula. For general $X$, replace the sum by the tower property, $E[Y(w)] = E\{E[Y(w) \mid X]\}$, and the same two substitutions hold for almost every value of $X$. $\square$
Positivity is not a technicality. If no former smoker were 18 to 39 years old, $\mu_1(x)$ would be undefined for that age group, and no amount of data from the other groups would say what diabetes the young would have if they had smoked and quit. Hernán and Robins (2020, §3.3) treat positivity as an identifiability condition alongside exchangeability and consistency. Problem 2 shows what can still be identified when it fails in part.
The formula can be read for any population whose covariate distribution is used as the standard. The next result says whose effect each standard estimates.
Corollary 1 (the standard population decides the estimand). Under consistency and conditional exchangeability, if $P(W = w \mid X = x) > 0$ for every $x$ with $P(X = x \mid W = 1) > 0$, then
$$E[Y(w) \mid W = 1] = \sum_x \mu_w(x)\,P(X = x \mid W = 1),$$
and the same holds with $W = 0$ in place of $W = 1$ on both sides.
Proof. By total expectation within the treated, $E[Y(w) \mid W = 1] = \sum_x E[Y(w) \mid W = 1, X = x]\,P(X = x \mid W = 1)$. Exchangeability gives $E[Y(w) \mid W = 1, X = x] = E[Y(w) \mid X = x] = E[Y(w) \mid W = w, X = x]$, the last step by exchangeability again and the positivity assumed. Consistency turns the last expression into $\mu_w(x)$. $\square$
So standardizing both groups to the covariate distribution of the treated estimates the effect in the treated, $E[Y(1) - Y(0) \mid W = 1]$, which the unit writes $\tau_{\mathrm t}$; standardizing to the untreated estimates the effect in the untreated; and standardizing to the whole population estimates $\tau$. These are different quantities whenever the effect varies with $X$.
Simpson's paradox as confounding
Back to the smoking data. With $X$ the age group (18 to 39, 40 to 59, 60 and over) the table of Intervals and Adjustment for Relative Risks and Odds Ratios gives, in each group, the risk of diagnosed diabetes among former and never smokers: 6 of 205 and 21 of 1,145 among the young, 49 of 300 and 115 of 929 in middle age, 216 of 677 and 258 of 944 among the old. The age-specific risk ratios are 1.596, 1.319 and 1.167. The crude risks are 0.229 and 0.131, a difference of 9.9 percentage points and a ratio of 1.756, larger than every age-specific ratio.
The running diagram says that age is a common cause of $W$ and $Y$ and that $\{\text{Age}\}$ satisfies the backdoor criterion if nothing else confounds. Theorem 5 then turns the age-specific risks into standardized risks. With the age distribution of all 4,200 adults as the standard (shares 0.3214, 0.2926 and 0.3860),
$$\hat E[Y(1)] = 0.3214 \times \tfrac{6}{205} + 0.2926 \times \tfrac{49}{300} + 0.3860 \times \tfrac{216}{677} = 0.1803,$$
$$\hat E[Y(0)] = 0.3214 \times \tfrac{21}{1{,}145} + 0.2926 \times \tfrac{115}{929} + 0.3860 \times \tfrac{258}{944} = 0.1476.$$
The standardized risk ratio is 1.222 and the risk difference 3.3 percentage points. Corollary 1 explains the other two adjustments already on the site. The course page standardized to the never smokers' ages and found a ratio of 1.235 (difference 3.1 points): under the diagram, an estimate of the effect among never smokers. Its Problem 4 standardized to the former smokers' ages and found 1.200 (difference 3.8 points): an estimate of the effect among former smokers. The Mantel–Haenszel risk ratio of the intervals page, 1.208, is a weighted average of the age-specific ratios with weights chosen for precision rather than to describe a population. The Mantel–Haenszel Test proves the consistency of the corresponding odds-ratio estimator when the odds ratio is common to the strata, which these data only approximately satisfy.
Example (the paradox is in the reading, not the data). Simpson's paradox is a reversal or distortion of an association when the data are split by a third variable. Pearl (2014) argues that it is resolved by asking which of the aggregated or disaggregated tables answers the causal question, and that the backdoor criterion decides. He contrasts a case in which the third variable (gender) is a pre-treatment confounder, so the answer lies in the disaggregated tables, with one in which the third variable (plant height in an older example, blood pressure in his Figure 1) is affected by the treatment, so the answer lies in the aggregated table. Age cannot be affected by smoking history and is a common cause, so the diagram puts the answer in the age-specific tables. If the third variable were body mass index, which quitting may affect, condition 1 of the criterion would exclude it. The invented hospitals of the course page, where the better hospital in every severity group looks worse overall, are the same structure with severity as the common cause.
The course page also proves that the overall comparison cannot reverse the group comparisons when both groups have the same distribution over the groups. That is the randomization argument: Randomized Experiments makes the two distributions equal in expectation by design, because no arrow enters the treatment except from the coin, so there is no backdoor path to block.
Colliders and selection bias
The collider rule says that conditioning on a common effect creates association between its causes. This is the structure of many biases that look different: comparing patients within a hospital, analyzing only people who answered a survey, adjusting for a test result. Hernán, Hernández-Díaz and Robins (2004) argue that selection biases in case-control and cohort studies share it, and they call bias from conditioning on a common effect selection bias, keeping confounding for bias from a common cause. Elwert and Winship (2014) give the same graphical account for sociology.
Berkson's paradox in a hospital
Berkson (1946) pointed out that in hospital data the groups are formed after the effects have occurred, unlike the groups of a laboratory experiment, and that a fourfold table from a clinic or hospital may then call for a different interpretation. Pearl (2014) uses the name Berkson's paradox for the general fact that observing a common consequence of two independent causes makes the causes dependent. A simple model shows the mechanism. Let $A$ and $B$ be two diseases, independent in the population. A person with neither is admitted with probability $h_0$; each disease the person has independently adds a chance of admission, $h_A$ or $h_B$, so that the probability of not being admitted is a product (a "noisy-or" model):
$$1 - s(a, b) = (1 - h_0)(1 - h_A)^a (1 - h_B)^b, \qquad a, b \in \{0, 1\}.$$
Admission is a collider: $A \to S \leftarrow B$.
Proposition 1 (Berkson's paradox). If $0 < P(A), P(B) < 1$ and $0 < h_0, h_A, h_B < 1$, then among admitted people the odds ratio between $A$ and $B$ is below 1: having one disease makes the other appear less common.
Proof. Write $q_0 = 1 - h_0$, $q_A = 1 - h_A$, $q_B = 1 - h_B$, each strictly between 0 and 1. Among the admitted, $P(A = a, B = b \mid S = 1)$ is proportional to $P(A = a)\,P(B = b)\,s(a, b)$, so in the odds ratio the marginal probabilities cancel:
$$\mathrm{OR} = \frac{s(1,1)\,s(0,0)}{s(1,0)\,s(0,1)}.$$
The odds ratio is below 1 exactly when the numerator is below the denominator. Expanding with $s(1,1) = 1 - q_0q_Aq_B$, $s(0,0) = 1 - q_0$, $s(1,0) = 1 - q_0q_A$ and $s(0,1) = 1 - q_0q_B$:
$$s(1,1)\,s(0,0) - s(1,0)\,s(0,1) = 1 - q_0 - q_0q_Aq_B + q_0^2q_Aq_B - 1 + q_0q_A + q_0q_B - q_0^2q_Aq_B = -q_0(1 - q_A)(1 - q_B),$$
which is negative. $\square$
Example (two diseases). Let $P(A) = 0.1$, $P(B) = 0.2$, $h_0 = 0.05$ and $h_A = h_B = 0.5$. Then 0.1878 of the population is admitted. Among admitted patients with disease $B$, 0.139 have $A$; among admitted patients without $B$, 0.538 have $A$. The odds ratio among the admitted is 0.138, although in the population the two diseases are independent and the odds ratio is 1. A study of hospital patients would report a strong protective association that does not exist.
Selection on a sum
The same thing happens with continuous variables selected on their sum, as when an admissions committee looks at the total of two scores or a hospital admits on combined severity.
Proposition 2 (selection on a sum of normals). Let $X_1$ and $X_2$ be independent standard normal variables, $U = (X_1 + X_2)/\sqrt2$, and select the units with $U > a$. Write $\varphi$ and $\Phi$ for the standard normal density and distribution function and $\lambda = \varphi(a)/(1 - \Phi(a))$. Among the selected,
$$\operatorname{Corr}(X_1, X_2 \mid U > a) = \frac{\sigma^2 - 1}{\sigma^2 + 1}, \qquad \sigma^2 = \operatorname{Var}(U \mid U > a) = 1 + a\lambda - \lambda^2.$$
Proof. Let $V = (X_1 - X_2)/\sqrt2$. The pair $(U, V)$ is a linear transformation of independent normals, so it is jointly normal; $\operatorname{Var}(U) = \operatorname{Var}(V) = 1$ and $\operatorname{Cov}(U, V) = (1 - 1)/2 = 0$. Jointly normal and uncorrelated variables are independent (The Multivariate Normal Distribution). The selection event depends on $U$ only, so among the selected $V$ is still standard normal and independent of $U$. Since $X_1 = (U + V)/\sqrt2$ and $X_2 = (U - V)/\sqrt2$,
$$\operatorname{Cov}(X_1, X_2 \mid U > a) = \tfrac12\big[\operatorname{Var}(U \mid U > a) - \operatorname{Var}(V)\big] = \tfrac12(\sigma^2 - 1),$$
$$\operatorname{Var}(X_1 \mid U > a) = \operatorname{Var}(X_2 \mid U > a) = \tfrac12(\sigma^2 + 1),$$
and the ratio is the stated correlation. It remains to find $\sigma^2$. Since $\varphi'(u) = -u\varphi(u)$, $\int_a^\infty u\varphi(u)\,du = \varphi(a)$, so $E[U \mid U > a] = \lambda$. Integrating by parts, $\int_a^\infty u^2\varphi(u)\,du = [-u\varphi(u)]_a^\infty + \int_a^\infty \varphi(u)\,du = a\varphi(a) + 1 - \Phi(a)$, so $E[U^2 \mid U > a] = 1 + a\lambda$. Subtracting the squared mean gives $\sigma^2$. $\square$
A truncated normal has variance below 1, so the correlation is negative whatever the threshold.
Example (keeping the top fifth). Keep the 20% of units with the largest sum. Then $a = 0.842$ (the selection is $X_1 + X_2 > 1.190$), $\lambda = 1.400$ and $\sigma^2 = 0.2186$, so the correlation among the selected is $-0.641$. In 30 simulated populations of 10,000 independent pairs (seeds 26,000,000 to 26,000,029), the median correlation among the selected was $-0.639$ (interquartile range $-0.652$ to $-0.629$), and the median correlation over all 10,000 pairs of a population was 0.003.
M-bias: adjusting for a pre-treatment collider
A common rule of thumb says to adjust for every covariate measured before treatment. The M-structure is the counterexample (Greenland, Pearl and Robins, 1999; Hernán and Robins, 2020, §7.3, credit the name, for the shape of the graph, to Greenland, 2003). In the right panel of the first figure, $M$ is measured before treatment and is associated with both $W$ (through $U_1$) and $Y$ (through $U_2$), so it passes the traditional screening for a confounder, yet adjusting for it opens the only backdoor path. Hernán and Robins (2020, §7.3) use the example of physical activity, cervical cancer and a Pap smear; Ding (2024, §16.3) reports the debate over whether to adjust for all pre-treatment covariates.
How large is the damage? In a linear model it can be computed exactly.
Proposition 3 (M-bias in a linear model). Let $U_1$, $U_2$ and the errors $\varepsilon_W, \varepsilon_M, \varepsilon_Y$ be independent with mean 0 and variance 1, and
$$W = aU_1 + \varepsilon_W, \quad M = bU_1 + cU_2 + \varepsilon_M, \quad Y = \tau W + dU_2 + \varepsilon_Y.$$
The population least squares coefficient of $W$ in the regression of $Y$ on $W$ alone is $\tau$. In the regression of $Y$ on $W$ and $M$ it is
$$\tau - \frac{abcd}{\operatorname{Var}(W)\operatorname{Var}(M) - (ab)^2}, \qquad \operatorname{Var}(W) = a^2 + 1, \quad \operatorname{Var}(M) = b^2 + c^2 + 1.$$
Proof. $U_2$ and $\varepsilon_Y$ are independent of $W$, so $\operatorname{Cov}(Y, W) = \tau\operatorname{Var}(W)$ and the first coefficient is $\tau$. For the second, $Y = \tau W + dU_2 + \varepsilon_Y$, and $\varepsilon_Y$ is uncorrelated with $(W, M)$, so the population coefficients of $(W, M)$ in the regression of $Y$ are $(\tau, 0)$ plus $d$ times the coefficients of $(W, M)$ in the regression of $U_2$. Those solve the normal equations with covariance matrix of $(W, M)$ equal to $\begin{pmatrix} a^2 + 1 & ab \\ ab & b^2 + c^2 + 1\end{pmatrix}$ and covariances $\operatorname{Cov}(U_2, W) = 0$, $\operatorname{Cov}(U_2, M) = c$. By Cramer's rule the coefficient on $W$ is $(0 \cdot \operatorname{Var}(M) - ab \cdot c)/(\operatorname{Var}(W)\operatorname{Var}(M) - (ab)^2)$. Multiplying by $d$ gives the bias. $\square$
Example (strong arrows). With every path coefficient 0.8 and $\tau = 0.5$: $\operatorname{Var}(W) = 1.64$, $\operatorname{Var}(M) = 2.28$, the bias is $-0.1230$ and the adjusted coefficient is 0.3770. In 30 simulated data sets of 2,000 units (seeds 27,000,000 to 27,000,029) the crude coefficient had median 0.503 (interquartile range 0.481 to 0.515) and the adjusted one median 0.375 (0.362 to 0.388). For comparison, omitting a true confounder with the same arrows ($U \to W$ and $U \to Y$, each 0.8) would bias the crude coefficient by $ad/\operatorname{Var}(W) = 0.3902$, about three times as much. The bias is a product of four path coefficients, so it shrinks fast when the arrows are weaker: Problem 4 finds a ratio of about 13 at 0.3. Greenland (2003) suggests, from some simple causal models, that collider-stratification biases of this kind may tend to be much smaller than classical confounding, unlike the bias from stratifying on variables affected by exposure and disease. Ding and Miratrix (2015) show that in linear structural models M-bias tends to be relatively small compared with confounding bias, and that mild departures from the pure M-shape, in which the collider is also a confounder, favor adjusting (both from the abstracts). M-bias is a reason to draw the diagram, not a reason to stop adjusting for pre-treatment covariates.
Mediators: adjustment that removes part of the effect
A mediator is a variable on a causal path from treatment to outcome. Adjusting for it violates condition 1 of the backdoor criterion, and there are two separate harms. The first is that holding the mediator fixed blocks the part of the effect that passes through it, so the adjusted comparison estimates something other than the total effect (Hernán and Robins, 2020, §18.2, call this overadjustment for mediators when the total effect is the target). The second is that the mediator is a collider on any path through an unmeasured common cause of mediator and outcome, so conditioning on it can also create bias. A linear model shows both at once.
Proposition 4 (adjusting for a mediator). Let $W$, $U$ and the errors be independent with mean 0 and variance 1 (the treatment randomized, $U$ unmeasured), and
$$M = \alpha W + \gamma U + \varepsilon_M, \qquad Y = \delta W + \beta M + \eta U + \varepsilon_Y.$$
The total effect of $W$ on $Y$ is $\delta + \alpha\beta$, the coefficient of $W$ in the regression of $Y$ on $W$ alone. The coefficient of $W$ in the regression of $Y$ on $W$ and $M$ is
$$\delta - \frac{\alpha\gamma\eta}{1 + \gamma^2}.$$
Proof. Substituting $M$ gives $Y = (\delta + \alpha\beta)W + (\beta\gamma + \eta)U + \beta\varepsilon_M + \varepsilon_Y$, and every term after the first is uncorrelated with $W$, so the first coefficient is $\delta + \alpha\beta$; setting $W$ by intervention changes $Y$ by the same amount per unit. For the second regression, $Y = \delta W + \beta M + \eta U + \varepsilon_Y$ with $\varepsilon_Y$ uncorrelated with $(W, M)$, so the coefficients are $(\delta, \beta)$ plus $\eta$ times the coefficients of $(W, M)$ in the regression of $U$. The covariance matrix of $(W, M)$ is $\begin{pmatrix} 1 & \alpha \\ \alpha & \alpha^2 + \gamma^2 + 1 \end{pmatrix}$, with determinant $1 + \gamma^2$, and $\operatorname{Cov}(U, W) = 0$, $\operatorname{Cov}(U, M) = \gamma$. By Cramer's rule the coefficient on $W$ is $-\alpha\gamma/(1 + \gamma^2)$. $\square$
When $\gamma = 0$ (nothing unmeasured affects both mediator and outcome) the adjusted coefficient is exactly the direct effect $\delta$, a meaningful quantity but not the total effect. When $\gamma \ne 0$ it is not even the direct effect.
Example. With $\delta = 0.3$, $\alpha = \gamma = \eta = 0.6$ and $\beta = 0.5$, the total effect is 0.60, the direct effect 0.3, and the coefficient after adjusting for $M$ is $0.3 - 0.1588 = 0.1412$, below both. In 30 simulated randomized trials of 2,000 units (seeds 28,000,000 to 28,000,029) the unadjusted coefficient had median 0.603 (interquartile range 0.572 to 0.629) and the adjusted one 0.145 (0.123 to 0.168). Adjusting a randomized comparison for a variable measured after treatment can manufacture bias where there was none.
Example (body mass index in the running data). Former smokers have a higher mean body mass index than never smokers, 30.7 against 29.4. Yeh and colleagues (2010) set out to test whether quitting raises the short-term risk of diabetes "possibly owing to cessation-related weight gain"; in their cohort, further adjustment for weight change and leukocyte count "attenuated these risks substantially" (their abstract), the risks being those of former smokers, new quitters and continuing smokers against never smokers. In the NHANES adults, standardizing to the age-group-by-sex distribution of all 4,200 (six strata) gives a risk ratio of 1.129 and a risk difference of 2.0 percentage points. Adding four groups of body mass index (under 25, 25 to 30, 30 to 35, 35 and over; 24 strata) gives 1.057 and 0.9 points. If body mass index lies on the path from quitting to diabetes, the second adjustment removes part of the effect being estimated. If instead weight before quitting influenced who quit, body mass index measured afterward would also carry confounding, as a stand-in for that earlier weight, and some adjustment for it would be wanted. The data alone cannot say which. The diagram can, and it is a claim about the world that has to be argued for.
The two standardizations also show that sex confounds the comparison: adding it to age moves the ratio from 1.222 to 1.129, because former smokers are more often men and men more often report diabetes in these data. Matching and Propensity Scores adds race and Hispanic origin, education and income.
Two cautions about the running example
- The data are cross-sectional. Some former smokers may have quit after their diagnosis, which is an arrow from $Y$ to $W$ and makes "former smoker" partly a consequence of diabetes. No adjustment set repairs that; it needs a design that fixes the order of events, such as a cohort with smoking recorded before the diagnosis.
- Westreich and Greenland (2013) warn against reading the coefficients of the adjustment variables in the same model as effects of those variables (the "Table 2 fallacy"): the coefficient of age in a model built to estimate the effect of smoking history is adjusted for smoking history, which lies on a path from age to diabetes in the running diagram, so it estimates at most a direct effect of age; and the coefficient of a covariate can be confounded even when the exposure's is not (their abstract). Each causal question needs its own diagram and its own adjustment set.
What is proved, what is cited, what the experiment shows
Proved on this page: the conditional independences of chains and forks and the marginal independence of colliders, from the factorization (Theorem 1); adjustment for the parents of the treatment, from the truncated factorization (Theorem 3); the g-formula from consistency, conditional exchangeability and positivity, and the reading of the standard population as the population whose effect is estimated (Theorem 5, Corollary 1); Berkson's paradox under the noisy-or admission model (Proposition 1); the exact correlation induced by selecting on a sum of normals (Proposition 2); the exact M-bias and the exact effect of adjusting for a mediator in linear models (Propositions 3 and 4).
Cited or stated: the factorization implied by a causal diagram and the definition of an intervention (Pearl, 1995); the soundness and completeness of d-separation (Pearl, 1995; Geiger, Verma and Pearl, 1990); the moralization test (Lauritzen et al., 1990, through Pearl, 1995); the backdoor theorem (Pearl, 1995, Theorem 1); the link between the backdoor criterion and conditional exchangeability (Hernán and Robins, 2020, Technical Point 7.1); the structural account of selection bias (Hernán, Hernández-Díaz and Robins, 2004); the relative size of M-bias (Greenland, 2003; Ding and Miratrix, 2015, from their abstracts); Simpson's paradox resolved by the backdoor criterion (Pearl, 2014); the cohort findings on quitting, weight and diabetes (Yeh et al., 2010, abstract).
What the experiments show: the simulated correlation after selection matched Proposition 2 to the third decimal of its median; the simulated M-bias and mediator coefficients matched Propositions 3 and 4 within their interquartile ranges. On the NHANES adults, adjustment for age moved the risk ratio of former against never smokers from 1.756 to between 1.200 and 1.235 depending on the standard population, adding sex moved it to 1.129, and adding body mass index to 1.057. These are associations in a cross-sectional survey; which of them is an effect depends on a diagram the data cannot check.
Worked problems
The problems were written for this article; every number is computed and checked by the article's script, which also enumerates the adjustment sets of Problem 1 with the d-separation test.
Problem 1 (every valid adjustment set). Pearl (1995, Fig. 2) uses a graph with treatment $X_i$, outcome $X_j$ and ten arrows: $X_1 \to X_3$, $X_1 \to X_4$, $X_2 \to X_4$, $X_2 \to X_5$, $X_3 \to X_i$, $X_4 \to X_i$, $X_4 \to X_j$, $X_5 \to X_j$, $X_i \to X_6$, $X_6 \to X_j$. Which subsets of $\{X_1, \ldots, X_5\}$ satisfy the backdoor criterion, and why is $X_6$ never allowed?
Solution. $X_6$ is a descendant of $X_i$, so condition 1 excludes it; the other five are not descendants. The backdoor paths enter $X_i$ through $X_3$ or $X_4$:
- $X_i \leftarrow X_4 \to X_j$, a fork at $X_4$;
- $X_i \leftarrow X_3 \leftarrow X_1 \to X_4 \to X_j$, non-colliders $X_3$, $X_1$ and $X_4$;
- $X_i \leftarrow X_4 \leftarrow X_2 \to X_5 \to X_j$, non-colliders $X_4$, $X_2$ and $X_5$;
- $X_i \leftarrow X_3 \leftarrow X_1 \to X_4 \leftarrow X_2 \to X_5 \to X_j$, with $X_4$ a collider and $X_3$, $X_1$, $X_2$ and $X_5$ non-colliders.
The first path has only $X_4$ in its interior, so every valid set contains $X_4$, which also blocks the second and third. With $X_4$ in the set, the fourth path is open at the collider, so the set must contain at least one of its non-colliders $X_1$, $X_2$, $X_3$ or $X_5$. Conversely any set containing $X_4$ and one of these blocks all four paths. The valid sets are therefore the sets containing $X_4$ and at least one of four other nodes: $2^4 - 1 = 15$ admissible sets, of which the minimal ones are $\{X_1, X_4\}$, $\{X_2, X_4\}$, $\{X_3, X_4\}$ and $\{X_4, X_5\}$. Pearl names $\{X_3, X_4\}$ and $\{X_4, X_5\}$ as valid and $\{X_4\}$ as invalid, for the reason given by the fourth path.
Problem 2 (positivity failing in part). Suppose no former smoker were under 40, so that only the two older age groups had both former and never smokers. Can the effect of having quit on the risk of diabetes be estimated for anyone, and what is the estimate?
Solution. The average effect over all adults needs $\mu_1(x)$ for the young, which would not exist, so Theorem 5 does not apply. Corollary 1 needs positivity only on the covariate values of the population it describes. Among the former smokers, all aged 40 and over in this scenario, it estimates the effect in the former smokers. Their risk is $(49 + 216)/(300 + 677) = 265/977 = 0.2712$. Their age shares are 0.3071 (40 to 59) and 0.6929 (60 and over), so the never smokers' risks standardized to those ages are $0.3071 \times 115/929 + 0.6929 \times 258/944 = 0.2274$. The ratio is 1.193, an estimate of the effect among former smokers aged 40 and over, under the diagram. The same argument, applying Theorem 5 within the adults aged 40 and over, identifies the average effect in that whole age range, former and never smokers together, since positivity is needed only on the covariate values of the population described. Their age shares are 0.4312 and 0.5688, the standardized risks $0.4312 \times 49/300 + 0.5688 \times 216/677 = 0.2519$ and $0.4312 \times 115/929 + 0.5688 \times 258/944 = 0.2088$, and the ratio 1.206. A failure of positivity narrows the population about which anything can be said; it does not remove every answer.
Problem 3 (another hospital). With $P(A) = 0.1$, $P(B) = 0.2$, $h_0 = 0.1$, $h_A = 0.3$ and $h_B = 0.6$, find the odds ratio between the two diseases among admitted patients, and $P(A \mid B)$ and $P(A \mid \text{not } B)$ among them.
Solution. The admission probabilities are $s(1,1) = 1 - 0.9 \times 0.7 \times 0.4 = 0.748$, $s(1,0) = 1 - 0.9 \times 0.7 = 0.37$, $s(0,1) = 1 - 0.9 \times 0.4 = 0.64$ and $s(0,0) = 0.1$. By the formula of Proposition 1 the odds ratio is $0.748 \times 0.1/(0.37 \times 0.64) = 0.316$. Among admitted patients, $P(A \mid B) = 0.1 \times 0.748/(0.1 \times 0.748 + 0.9 \times 0.64) = 0.115$ and $P(A \mid \text{not } B) = 0.1 \times 0.37/(0.1 \times 0.37 + 0.9 \times 0.1) = 0.291$. The sign agrees with Proposition 1, since $-q_0(1 - q_A)(1 - q_B) = -0.9 \times 0.3 \times 0.6 < 0$.
Problem 4 (M-bias with weak arrows). Repeat the M-bias example with every path coefficient 0.3, and compare the bias with that from omitting a confounder with the same two arrows.
Solution. Here $\operatorname{Var}(W) = 1.09$ and $\operatorname{Var}(M) = 1.18$. By Proposition 3 the bias of adjusting for $M$ is $-0.3^4/(1.09 \times 1.18 - 0.09^2) = -0.0081/1.2781 = -0.00634$. Omitting a confounder $U$ with $U \to W$ and $U \to Y$ both 0.3 biases the crude coefficient by $0.3 \times 0.3/1.09 = 0.0826$, about 13 times as much. At moderate strengths, failing to adjust for a real confounder costs far more than adjusting for an M-shaped collider.
Summary
| Result | Statement |
|---|---|
| Chain, fork | $A \perp\!\!\!\perp B \mid C$ |
| Collider | $A \perp\!\!\!\perp B$; dependent given $C$ or a descendant of $C$, in general |
| d-separation | blocked paths imply conditional independence (cited) |
| Backdoor criterion | no descendant of $W$; every path into $W$ blocked |
| Adjustment (g-formula) | $E[Y(w)] = \sum_x \mu_w(x)\,P(X = x)$ under consistency, exchangeability, positivity |
| Standard population | covariates of the treated give the effect in the treated |
| Berkson | $\mathrm{OR} = s_{11}s_{00}/(s_{10}s_{01}) < 1$ among the admitted |
| Selection on a sum | $\operatorname{Corr} = (\sigma^2 - 1)/(\sigma^2 + 1)$, $\sigma^2 = 1 + a\lambda - \lambda^2$ |
| M-bias (linear) | $-abcd/(\operatorname{Var}W\operatorname{Var}M - a^2b^2)$ |
| Mediator (linear) | adjusted coefficient $\delta - \alpha\gamma\eta/(1 + \gamma^2)$ |
What we have learned
Whether to adjust for a variable is decided by the causes, not by the data: a common cause of treatment and outcome must be held fixed, while a common effect of anything related to them, or anything on the causal path, must be left alone. The backdoor criterion turns a diagram into a list of valid adjustment sets, the g-formula turns a valid set into an estimate, and the population used as the standard decides whose effect is estimated. In the smoking data age is a confounder, sex is another, and body mass index may be a mediator; adjustment for age and sex brings the risk ratio from 1.756 to about 1.13.
Adjusting for one or two covariates by standardization is easy. With race and Hispanic origin, education and income added, the strata outnumber the adults in many of them. Matching and Propensity Scores shows how a single number, the probability of treatment given the covariates, does the work of all of them.
References
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