9  Potential Outcomes and Identification

The statistics of Part I lets us describe a joint distribution of covariates, treatments, and outcomes, and from samples of that distribution it lets us estimate conditional expectations such as \(\mathbb{E}[Y\mid T=t,X=x]\) and marginal expectations such as \(\mathbb{E}[Y]\) (recall the conditional expectation of Definition 4.4 and the estimators of Chapter 5). We can predict, classify, and quantify uncertainty. What we cannot yet do is answer a counterfactual question: how would a patient’s outcome have changed had she received treatment \(B\) instead of treatment \(A\)? The patient who received \(A\) supplies her outcome under \(A\), which we observe; her outcome under \(B\) is unobserved, and it is unobservable in principle from this patient, because she did not in fact receive \(B\) and cannot be assigned to both treatments at once. This unobservability is the fundamental problem of causal inference, and no amount of data from a single patient resolves it.

Every indirect treatment comparison, however elaborate, is ultimately a statement about such counterfactuals: it claims that treatment \(B\) would do better or worse than treatment \(C\) in some target population, even though no trial randomized those two treatments head to head. Before we can compare treatments across studies, we must be able to say precisely what a treatment effect is and under what conditions a population can recover it from data. That is the work of this chapter. We develop the Neyman-Rubin potential-outcomes model (a bookkeeping device that gives every patient two outcomes, one per treatment), which separates what we want to know, the counterfactual contrast, from what we observe, the factual outcome under the received treatment. We state the stable-unit-treatment-value assumption (the condition that makes “a patient’s outcome under her own treatment” a well-defined object) and the consistency identity (the algebra that links the observed outcome to the potential ones) that bind the two together. We define the estimands an indirect comparison might target: the average treatment effect, the effect on the treated, the effect on the controls, and the conditional average treatment effect. We then isolate the two assumptions, ignorability (treatment is as good as random within covariate strata) and positivity (every covariate stratum contains both treated and control patients), that turn an unobservable counterfactual mean into an observable functional of the data, and we prove the identification theorem for the average treatment effect by iterated expectation. Finally we prove that the naive treatment-minus-control contrast equals the effect on the treated plus a selection-bias term, which makes precise why adjustment is needed when treatment is not randomized.

Throughout we use the causal notation of Notation: \(Y(0)\) and \(Y(1)\) are the potential outcomes under control and active treatment, \(T\in\{0,1\}\) is the treatment indicator, \(X\in\mathcal{X}\) collects baseline covariates, \(e(x)=P(T=1\mid X=x)\) is the propensity score, \(\mu_t(x)=\mathbb{E}[Y(t)\mid X=x]\) is the conditional mean potential outcome, \(\tau(x)=\mu_1(x)-\mu_0(x)\) is the conditional average treatment effect, and \(\tau=\mathbb{E}[\tau(X)]\) is the average treatment effect. Two symbols we will lean on heavily deserve to be named now, since they are not in the notation chapter: \(P_X\) denotes the marginal distribution (law) of the covariates \(X\), and \(\mathbb{E}_X[\,\cdot\,]\) denotes an expectation taken over that covariate distribution (so \(\mathbb{E}_X[h(X)]=\int h(x)\,dP_X(x)\)). Both are spelled out again where they first do real work. The development follows Hernán and Robins (2020) and Rosenbaum and Rubin (1983), and it corresponds to items B.1 through B.5 of the companion proof catalogue.

Two navigational notes before we begin. First, several results carry a bracketed [machine-checked: ...] tag naming the corresponding lemma in the companion Coq development; those tags are for readers auditing the formalization and can be safely skipped on a first reading. Second, the probability facts we borrow from Part I (the tower property Theorem 4.4, dominated convergence Theorem 4.2, the graphoid axioms Theorem 4.5) are cited by number as we use them, so you can follow the causal argument without re-deriving the underlying probability.

9.1 A running clinical example

We anchor the whole chapter in one small clinical picture and return to it at every turn. Imagine a single center studying a new drug (\(T=1\)) against standard care (\(T=0\)) for a chronic disease. The outcome \(Y\) is a physical-function score at six months, on a scale where higher is better. Each patient has a baseline prognostic status \(X\), coarsened to two levels: \(X=1\) for favorable baseline, \(X=0\) for poor baseline.

Consider two patients. Alice has favorable baseline (\(X=1\)). If she takes the new drug she would score \(Y(1)=24\); if she takes standard care she would score \(Y(0)=20\). Her personal benefit from the new drug is \(24-20=4\) points. Bob has poor baseline (\(X=0\)), with \(Y(1)=14\) and \(Y(0)=10\), again a benefit of \(4\) points. The catch is structural: Alice can be given only one treatment, so we ever see only one of her two numbers. If she takes the new drug we record \(24\) and her \(20\) stays hidden forever; if she takes standard care we record \(20\) and her \(24\) is the counterfactual we can never observe. The same holds for Bob and for every patient.

These two patients are representatives of the two covariate strata of the fully worked population in Example 9.2, whose stratum means are exactly Alice’s and Bob’s numbers. We will use Alice and Bob to make each definition concrete, and near the end we will put real probabilities on this population and watch a naive analysis report a benefit of \(9\) when the truth is \(4\). Keep the picture in mind: two hidden numbers per patient, one revealed, and a chapter’s worth of machinery devoted to recovering averages of the hidden ones.

9.2 The Neyman-Rubin model

The framework begins by positing, for each unit, not one outcome but two: the outcome that would be realized under each of the two treatments. These are the potential outcomes. They live on the same probability space as the observed data, and they are ordinary random variables; what distinguishes them is that only one of the two is ever revealed for any given unit.

Before the formal definition, fix the picture the formalism encodes. Think of \(\omega\) as one patient, and of the probability space \((\Omega,\mathcal{F},P)\) as the mathematical version of the sentence “draw a patient at random from the population.” The set \(\Omega\) is the population of patients; \(P\) says how likely each kind of patient is to be drawn; a random variable is any number attached to a patient (her covariates, her treatment, her outcome). In this language Alice and Bob are two particular points \(\omega\in\Omega\), and a potential outcome is just a rule that assigns each patient the score she would get under a given treatment.

Definition 9.1 (Potential outcomes) Fix a probability space \((\Omega,\mathcal{F},P)\) whose points \(\omega\in\Omega\) index the units of a population. A pair of potential outcomes is a pair of random variables \[ Y(0):\Omega\to\mathbb{R},\qquad Y(1):\Omega\to\mathbb{R}, \] where \(Y(1)(\omega)\) is the outcome unit \(\omega\) would experience under active treatment and \(Y(0)(\omega)\) the outcome it would experience under control. More generally, for a treatment label \(t\in\{0,1\}\) we write \(Y(t)\) for the potential outcome under treatment \(t\), so that \(Y(t)=t\,Y(1)+(1-t)\,Y(0)\) as a function of the label. Both \(Y(0)\) and \(Y(1)\) are assumed to be well-defined, measurable, and (unless stated otherwise) integrable, that is, \(Y(0),Y(1)\in L^1(P)\). \(\blacktriangleleft\)

[machine-checked: theories/PotentialOutcomes.v, Record potential_outcomes, Definition potential_outcome]

Reader translation. Every patient carries two numbers, the outcome she would get under the new drug and the outcome she would get under standard care. For Alice these are \(Y(1)(\omega)=24\) and \(Y(0)(\omega)=20\). Only the one matching the treatment she actually receives is ever seen; the other is hidden but no less real. A note on the two kinds of “\(t\)”: a lowercase \(t\in\{0,1\}\) is a fixed label we choose (as in “the potential outcome \(Y(t)\) under treatment \(t\)”), whereas the uppercase \(T\) we meet next is the random treatment a patient actually receives. Watching this lowercase-versus-uppercase distinction (notation convention 2 of Notation) saves a great deal of confusion; the switch is doing real work every time it appears.

The causal effect of treatment on a single unit is the difference between that unit’s two potential outcomes. We name it because it is the quantity an idealized experiment on one patient, repeated in two parallel worlds, would measure.

Definition 9.2 (Individual treatment effect) The individual treatment effect (ITE) for unit \(\omega\) is \[ \tau(\omega)=Y(1)(\omega)-Y(0)(\omega). \] It is itself a random variable on \(\Omega\), measurable whenever \(Y(0)\) and \(Y(1)\) are. \(\blacktriangleleft\)

Reader translation. The ITE is one patient’s personal benefit or harm from treatment, the difference between her two hidden numbers. Alice’s ITE is \(24-20=4\) and Bob’s is \(14-10=4\). It is the thing we would most like to report to a patient, and, by the very next theorem, exactly the thing no data set can ever deliver.

The individual effect is exactly what we would like to know and exactly what we can never observe. The reason is structural, not a matter of sample size: for each unit, one of the two potential outcomes is realized and the other is counterfactual, the outcome under the treatment the unit did not receive. The next theorem makes this precise. In plain words it says: two different worlds can produce identical observed data yet have different causal effects, so no analysis of the observed data alone can recover the effect. Formally, two genuinely different populations, differing in their individual effects and even in their average effect, can produce identical observed data, so no procedure that reads only the observed data can recover the individual effect.

Theorem 9.1 (The fundamental problem of causal inference) Let the observed outcome under a treatment assignment \(T:\Omega\to\{0,1\}\) be \(Y=Y(T)\), that is, \(Y(\omega)=Y(T(\omega))(\omega)\). There exist two pairs of potential outcomes \((Y(0),Y(1))\) and \((Y'(0),Y'(1))\) on a common space, and a common assignment \(T\), such that the observed data \((T,Y)\) and \((T,Y')\) have the same joint distribution, yet the individual treatment effects differ at some unit: \[ Y(1)-Y(0)\;\not\equiv\;Y'(1)-Y'(0). \] Consequently no function of the observed data \((T,Y)\) alone equals the individual treatment effect, and no such function equals the average individual effect either.

[machine-checked: theories/PotentialOutcomes.v, Lemma ITE_unobservable]

Proof. We exhibit two worlds that agree on everything observable and disagree on the effect. Take any nonempty \(\Omega\) and let every unit be treated, \(T(\omega)=1\) for all \(\omega\). Define \[ \text{World A:}\quad Y(1)\equiv 1,\ Y(0)\equiv 0, \qquad \text{World B:}\quad Y'(1)\equiv 1,\ Y'(0)\equiv 1 . \] Because \(T\equiv 1\), in both worlds the observed outcome is the potential outcome under treatment: \(Y=Y(1)\equiv 1\) in World A and \(Y'=Y'(1)\equiv 1\) in World B. Hence \((T,Y)\) and \((T,Y')\) are both the constant pair \((1,1)\) and have identical joint laws. The individual effects, however, are \(Y(1)-Y(0)\equiv 1\) in World A and \(Y'(1)-Y'(0)\equiv 0\) in World B, which differ at every unit; the average effects \(\mathbb{E}[Y(1)-Y(0)]=1\) and \(\mathbb{E}[Y'(1)-Y'(0)]=0\) differ as well.

Now suppose some measurable functional \(\Psi\) of the observed data satisfied \(\Psi(T,Y)=Y(1)-Y(0)\) in every world. Applied to the two worlds above, \(\Psi\) receives the same argument \((1,1)\) in both, so it returns the same value; but the targets \(Y(1)-Y(0)\) and \(Y'(1)-Y'(0)\) differ. This contradiction shows no such \(\Psi\) exists. The identical argument with the constant targets replaced by their expectations rules out a functional returning the average effect. \(\square\)

Why this matters. This impossibility is the logical warrant for the entire book. Because no method, however clever, can recover an individual effect from observed data, every estimand we pursue afterward, in regression, in network meta-analysis, and in indirect treatment comparison alike, is a population average rather than a person-level prediction. When a later chapter targets an average effect and not a personalized one, this theorem is the reason. The rest of the present chapter is the disciplined response to it: recover averages when individual effects are hopeless.

The construction in the proof is deliberately extreme: with everyone treated there are no controls, so the control outcome \(Y(0)\) is pure counterfactual and the data carry no information about it. The remainder of the chapter is the disciplined response to this problem. We cannot recover individual effects, but with the right structural assumptions we can recover averages. The first such assumption concerns how the observed outcome is generated from the potential ones.

9.3 SUTVA and the consistency identity

Writing \(Y=Y(T)\) already smuggles in an assumption. It presumes that the outcome a unit displays under its received treatment is its own potential outcome under that treatment, unaffected by which treatments other units received and unambiguous as to which “version” of the treatment was given. These are the two components of the stable-unit-treatment-value assumption. Before the formal statement: SUTVA is what lets us pretend each patient lives in her own bubble, with one clearly defined “new drug” and one clearly defined “standard care”, so that her observed score is simply whichever of her two potential scores matches the treatment she got.

Definition 9.3 (Stable unit treatment value assumption (SUTVA)) Let the population receive an assignment vector \(\mathbf{t}=(t_\omega)_{\omega\in\Omega}\in\{0,1\}^\Omega\), and let \(Y_\omega(\mathbf{t})\) denote the outcome unit \(\omega\) would experience under the full vector \(\mathbf{t}\). The stable unit treatment value assumption consists of two parts.

• (SUTVA-1) No interference. Each unit’s outcome depends on the assignment vector only through that unit’s own component: for all \(\mathbf{t},\mathbf{t}'\) and all \(\omega\), \[ t_\omega=t'_\omega\ \Longrightarrow\ Y_\omega(\mathbf{t})=Y_\omega(\mathbf{t}'). \]
• (SUTVA-2) No hidden versions. There is a single, well-defined version of each treatment level, so that the label \(t\in\{0,1\}\) determines the intervention unambiguously.

\(\blacktriangleleft\)

[machine-checked: theories/CausalAssumptions.v, Definition SUTVA, Lemma no_interference_unit_level]

Reader translation. SUTVA says two things in plain clinical terms. First, no interference: my outcome depends on the treatment I take, not on who else in the study happened to be treated. Second, no hidden versions: “the new drug” names one well-defined intervention, not a grab-bag of different doses or regimens masquerading under one label. Only when both hold does it make sense to write a patient’s observed outcome as her own potential outcome under her own assignment, \(Y=Y(T)\).

SUTVA is an assumption, not a theorem; it constrains the world, and it can fail. Interference fails in a vaccine trial where one unit’s vaccination lowers another unit’s infection risk through reduced transmission; hidden versions fail when “surgery” silently bundles several distinct procedures of differing efficacy. The failure that most threatens indirect comparison is the second one across studies: in a network of oncology trials, if one trial’s “chemotherapy” arm delivers a higher dose than another’s, the single label “chemotherapy” hides two different interventions, SUTVA-2 fails, and the shared anchor on which the indirect comparison depends is no longer one well-defined treatment. When you later read that two trials must share a common comparator, this is the assumption being invoked. What SUTVA-1 buys, mathematically, is the reduction from a vector-indexed family of outcomes to the two-potential-outcomes setup of Definition 9.1: under no interference there is a function \(Y(\cdot)(\cdot):\{0,1\}\times\Omega\to\mathbb{R}\) with \(Y_\omega(\mathbf{t})=Y(t_\omega)(\omega)\) for every assignment vector, because \(Y_\omega(\mathbf{t})\) depends on \(\mathbf{t}\) only through \(t_\omega\). The witness is \(Y(t)(\omega):=Y_\omega(\mathbf{t})\) evaluated at any \(\mathbf{t}\) with \(t_\omega=t\), for instance the constant vector \(\mathbf{t}\equiv t\); no interference guarantees this does not depend on the choice. We may therefore speak of \(Y(0)\) and \(Y(1)\) as unit-level random variables, exactly as the catalogue records (corresponds to B.1 in the proof catalogue).

The bookkeeping is easiest to see in a table. Three patients, each with two potential scores, are assigned a treatment; we observe the score in the assigned column and the other is counterfactual.

Patient	Baseline \(X\)	Assigned \(T\)	\(Y(0)\)	\(Y(1)\)	Observed \(Y=Y(T)\)	Hidden (counterfactual)
Alice	\(1\) (favorable)	\(1\) (new drug)	\(20\)	\(24\)	\(24\)	\(Y(0)=20\)
Bob	\(0\) (poor)	\(0\) (standard care)	\(10\)	\(14\)	\(10\)	\(Y(1)=14\)
Carol	\(1\) (favorable)	\(0\) (standard care)	\(20\)	\(24\)	\(20\)	\(Y(1)=24\)

Each row shows the fundamental problem in miniature: exactly one number per patient is observed and one is forever hidden. The next result is simply the algebra of the “Observed \(Y\)” column.

With the two potential outcomes in hand and a treatment indicator \(T\), the observed outcome is determined by a case split: a treated unit shows its treated potential outcome, a control unit shows its control potential outcome. The next result records this and its algebraic encoding, which is the workhorse of every identification proof to come.

Theorem 9.2 (Consistency identity) Under SUTVA, with \(T\in\{0,1\}\) the treatment indicator and \(Y=Y(T)\) the observed outcome, \[ Y = T\,Y(1) + (1-T)\,Y(0) \qquad\text{pointwise on }\Omega. \tag{9.1}\] Equivalently, \(Y=Y(t)\) holds on the event \(\{T=t\}\) for each \(t\in\{0,1\}\). Moreover the treatment-masked identities \[ T\,Y = T\,Y(1), \qquad (1-T)\,Y = (1-T)\,Y(0) \tag{9.2}\] hold pointwise.

[machine-checked: theories/PotentialOutcomes.v, Definition consistency, Lemma consistency_equiv, Lemma consistency_expectation]

Proof. Fix \(\omega\) and split on the value of \(T(\omega)\in\{0,1\}\). If \(T(\omega)=1\), the right-hand side of Equation 9.1 is \(1\cdot Y(1)(\omega)+0\cdot Y(0)(\omega)=Y(1)(\omega)\), which equals \(Y(\omega)=Y(T(\omega))(\omega)=Y(1)(\omega)\); SUTVA-1 makes \(Y(1)(\omega)\) depend only on \(\omega\)’s own assignment and SUTVA-2 makes it unambiguous, so this potential outcome is well-defined. If \(T(\omega)=0\), the right-hand side is \(0\cdot Y(1)(\omega)+1\cdot Y(0)(\omega)=Y(0)(\omega)=Y(\omega)\). In both cases the two sides agree, proving Equation 9.1; the statement \(Y=Y(t)\) on \(\{T=t\}\) is the same case split read one branch at a time.

For the masked identities, multiply Equation 9.1 by \(T\) and use that \(T\) takes values in \(\{0,1\}\), so \(T^2=T\) and \(T(1-T)=0\): \[ T\,Y = T\bigl(T\,Y(1)+(1-T)\,Y(0)\bigr) = T^2\,Y(1) + T(1-T)\,Y(0) = T\,Y(1). \] Multiplying instead by \(1-T\) and using \((1-T)^2=1-T\) and \((1-T)T=0\) gives \((1-T)Y=(1-T)Y(0)\). \(\square\)

Why this matters. The consistency identity is the single hinge that connects what we observe to what we want. Every identification formula in this book, and every indirect-comparison estimator built on it, passes through it: it is the one licensed move from an observed \(Y\) to a potential outcome \(Y(t)\).

The identity Equation 9.1 is, in the epidemiological literature, called consistency, a word that unfortunately also names the convergence of an estimator; the two senses are unrelated and we keep them apart by always saying “consistency identity” for the causal one. Its importance is that it lets us trade the observed outcome for a potential outcome inside conditional expectations, on the event where the corresponding treatment was received. This swap is the single bridge across which all identification travels. The masked forms Equation 9.2 may look like a pointless multiplication by \(T\), but the point is to isolate a single arm: \(TY=TY(1)\) keeps only the treated units and equates their observed outcome with their treated potential outcome, discarding the controls. That is exactly the algebra behind the inverse-probability-weighting estimator of the next chapter (Theorem 10.3), which reconstructs \(\mathbb{E}[Y(1)]\) from the treated arm alone; the masked identity is what makes that arm-by-arm reconstruction legitimate.

Corollary 9.1 (Outcome swap under consistency) Under SUTVA, for each \(t\in\{0,1\}\) and any covariate \(X\), \[ \mathbb{E}[Y\mid T=t,X] = \mathbb{E}[Y(t)\mid T=t,X] \qquad\text{a.s. on }\{P(T=t\mid X)>0\}. \tag{9.3}\]

[machine-checked: theories/PotentialOutcomes.v, Lemma consistency_treated_mean, Lemma consistency_control_mean]

Proof. By Theorem 9.2, \(Y=Y(t)\) everywhere on the event \(\{T=t\}\). The claim is then an instance of a general fact: a conditional expectation given \((T=t,X)\) depends on its integrand only through the integrand’s values on the event \(\{T=t\}\). To see why, recall the defining property of conditional expectation (Definition 4.4 and Equation 4.5): \(\mathbb{E}[\,\cdot\mid T=t,X]\) is characterized by its integrals against test sets of the form \(\{T=t\}\cap B\) with \(B\) an \(X\)-measurable set. For two integrands \(f\) and \(g\) that agree on \(\{T=t\}\) we have \(f\mathbf{1}_{\{T=t\}\cap B}= g\mathbf{1}_{\{T=t\}\cap B}\) pointwise, so their defining integrals coincide for every such test set; by the uniqueness clause of Definition 4.4 the two conditional expectations are therefore a.s. equal. Applying this with \(f=Y\) and \(g=Y(t)\), which agree on \(\{T=t\}\) by consistency, gives Equation 9.3 wherever the conditioning event has positive probability. \(\square\)

Reader translation. The corollary says: among patients with covariates \(X\) who actually received treatment \(t\), their observed outcome and their potential outcome under \(t\) have the same average. The proviso is the honest limitation: this only speaks about patient types who are sometimes given treatment \(t\). It says nothing about the treated potential outcome of a patient type who is never treated, because there is simply no one to average. The proviso \(P(T=t\mid X)>0\) is exactly the positivity condition of Section 9.5; without it the conditioning event \(\{T=t,X=x\}\) can be null and the left-hand conditional mean is not defined there.

9.4 Estimands

We cannot recover individual effects, so we target averages. Which average depends on the question. This section names the standard estimands; the rest of the chapter is about identifying the first of them from data. All are defined directly from the potential outcomes, with no reference yet to how treatment was assigned, so they are properties of the population, not of any estimator.

One word carries a lot of weight here: which population. The “population” in each average is whichever population the covariates \(X\) are drawn from. In a randomized trial it is the enrolled sample; in a cohort study it is the source population; in an indirect treatment comparison it is the decision maker’s target population, which may be neither trial’s. An effect that is correct in one population can be wrong in another, so keeping track of which population an estimand refers to is the single most important habit for the rest of the book.

Definition 9.4 (Average treatment effect) The average treatment effect (ATE) is the population mean of the individual treatment effect, \[ \tau := \mathbb{E}[Y(1)-Y(0)] = \mathbb{E}[Y(1)] - \mathbb{E}[Y(0)]. \tag{9.4}\] It is the expected change in outcome if the entire population were switched from control to active treatment. \(\blacktriangleleft\)

[machine-checked: theories/PotentialOutcomes.v, Definition ATE, Lemma ATE_split]

Reader translation. The ATE answers “if we treated everyone in this population instead of no one, how would the average score change?” In the running example it will turn out to be \(4\): the average patient gains \(4\) function points from the new drug.

The second equality in Equation 9.4 is linearity of expectation, the same step that the Coq lemma ATE_split records; it already shows that the ATE is built from the two marginal mean potential outcomes \(\mathbb{E}[Y(0)]\) and \(\mathbb{E}[Y(1)]\), each of which we will identify separately. Restricting the average to the units who actually received treatment gives a different estimand, the one most relevant when a regulator asks what a drug did for the patients who took it.

Definition 9.5 (Average treatment effect on the treated) The average treatment effect on the treated (ATT) is \[ \tau_{\mathrm{T}} := \mathbb{E}[Y(1)-Y(0)\mid T=1], \tag{9.5}\] the mean individual effect among units with \(T=1\). The symmetric average treatment effect on the controls (ATC) is \(\tau_{\mathrm{C}}:=\mathbb{E}[Y(1)-Y(0)\mid T=0]\). \(\blacktriangleleft\)

[machine-checked: theories/PotentialOutcomes.v, Definition ATT, Definition ATC]

Reader translation. The ATT restricts the question to the patients who did take the new drug: “for those actually treated, how much did treatment help on average?” The ATC asks the mirror question of those who received standard care. These differ from the ATE whenever the treated and untreated are different kinds of patient, which is the usual situation outside a randomized trial.

Definition 9.6 (Conditional average treatment effect) For covariates \(X\), the conditional average treatment effect (CATE) is the function \[ \tau(x) := \mathbb{E}[Y(1)-Y(0)\mid X=x] = \mu_1(x)-\mu_0(x), \qquad \mu_t(x)=\mathbb{E}[Y(t)\mid X=x], \tag{9.6}\] the mean effect within the covariate stratum \(X=x\). \(\blacktriangleleft\)

Reader translation. The CATE is the effect within a stratum of patients: the average benefit among favorable-baseline patients, and separately among poor-baseline patients. In the running example both strata have CATE \(4\), so the effect happens to be constant; in general it varies with \(x\), and that variation, called effect modification, is what makes an effect fail to carry from one population to another. The CATE is therefore the building block of every cross-population argument later in the book.

The CATE refines the ATE by covariates, and the ATE is its average: by the tower property (Theorem 4.4), \[ \tau = \mathbb{E}[Y(1)-Y(0)] = \mathbb{E}\bigl[\,\mathbb{E}[Y(1)-Y(0)\mid X]\,\bigr] = \mathbb{E}[\tau(X)], \tag{9.7}\] which is the relation recorded in Notation. This averaging is benign here because we are on the identity (mean-difference) scale, where the average of a constant stratum effect is that constant. You do not need this yet, but a signpost for later: on a nonlinear scale such as the odds ratio, a constant stratum effect need not average to itself, a phenomenon called non-collapsibility. We flag it only so the reader is not surprised in Definition 7.7 and Definition 11.6, where it is developed properly; on the identity scale of this chapter Equation 9.7 holds with no caveat.

It helps to see the four estimands side by side, together with where each surfaces in indirect comparison.

Estimand	Symbol	Question it answers	Role in ITC
Average treatment effect	\(\tau\)	Effect if the whole target population switched control to treatment	The marginal, population-average target most population-adjustment methods aim at
Effect on the treated	\(\tau_{\mathrm{T}}\)	Effect among patients who actually received treatment	The estimand when the question is specifically about the treated subgroup
Effect on the controls	\(\tau_{\mathrm{C}}\)	Effect among patients who received control	The mirror image; appears in some transport arguments
Conditional effect	\(\tau(x)\)	Effect within covariate stratum \(X=x\)	The building block that carries effect modification across populations

For orientation: most population-adjustment methods in this book, MAIC and STC in Part IV and ML-NMR in Part V, target a marginal treatment effect (an ATE-type estimand) in a specified target population, on a stated effect scale. The CATE is the object that makes such transport possible, because it is what changes across populations when effect modifiers are distributed differently. The three population-level averages are tied together by the proportion treated.

Proposition 9.1 (Decomposition of the ATE over treatment groups) Let \(p=P(T=1)\). Then \[ \tau = p\,\tau_{\mathrm{T}} + (1-p)\,\tau_{\mathrm{C}}. \tag{9.8}\]

[machine-checked: theories/PotentialOutcomes.v, Lemma ATE_decomposition]

Proof. Apply the law of total expectation (Corollary 4.1) to the integrable variable \(Y(1)-Y(0)\), using the partition \(\{T=1\}\cup\{T=0\}\) of \(\Omega\): \[ \tau=\mathbb{E}[Y(1)-Y(0)] = P(T=1)\,\mathbb{E}[Y(1)-Y(0)\mid T=1] + P(T=0)\,\mathbb{E}[Y(1)-Y(0)\mid T=0], \] which is \(p\,\tau_{\mathrm{T}}+(1-p)\,\tau_{\mathrm{C}}\) by Equation 9.5 and the definition of \(\tau_{\mathrm{C}}\). \(\square\)

Why this matters. The decomposition says the population effect is a weighted blend of the effect in the treated and the effect in the controls. It holds with no assumptions whatsoever; in particular the ATE, ATT, and ATC need not coincide. They coincide precisely when the individual effect is mean-independent of treatment assignment, which is the situation a randomized experiment engineers and which the ignorability assumption of the next section formalizes.

9.5 Identifying assumptions: ignorability and positivity

The estimands of Section 9.4 are defined from potential outcomes, but data report only \((X,T,Y)\). Identification is the act of writing an estimand as a functional of the observed-data distribution alone, so that it could in principle be computed if we had infinitely much data. Two glosses are worth pinning down, because a beginner can slip on both. A functional here means a map whose input is a whole probability distribution and whose output is a number; identification asks whether the estimand is pinned down by the distribution of the observable triple \((X,T,Y)\). This is a different question from estimation, which asks how to compute a good approximation from a finite sample. Identification is the infinite-data question; every estimator in later chapters presupposes that the answer to the identification question is yes. Without further assumptions the ATE is not identified: Theorem 9.1 already produced two populations with the same observed-data law and different ATEs. Two assumptions close the gap. The first asserts that, within strata of the measured covariates, treatment is assigned as if at random, independently of the potential outcomes. It comes in three strengths, and it is worth saying up front why there are three: the identification proof below needs only the weakest (mean ignorability); randomization delivers the strongest (strong ignorability) for free; and the balancing-score theory of the next chapter needs the strongest. Keeping the three apart lets us assume exactly as much as each result requires.

Definition 9.7 (Ignorability (strong, weak, mean)) Let \(X\) be baseline covariates. Three nested forms of ignorability, also called no unmeasured confounding or conditional exchangeability, are:

• Strong ignorability: \(\bigl(Y(0),Y(1)\bigr)\perp T \mid X\), the joint law of the two potential outcomes is conditionally independent of treatment given \(X\).
• Weak ignorability for \(Y(t)\): \(Y(t)\perp T\mid X\) for the single label \(t\) in question.
• Mean ignorability for \(Y(t)\): \(\mathbb{E}[Y(t)\mid T,X]=\mathbb{E}[Y(t)\mid X]\) a.s.

Conditional independence is meant in the sense of Definition 4.6. \(\blacktriangleleft\)

[machine-checked: theories/CausalAssumptions.v, Definition strong_unconfoundedness, Definition weak_unconfoundedness, Lemma strong_implies_weak_unconf]

Reader translation. In clinical words, ignorability says: once we know a patient’s covariates \(X\), knowing which treatment she was given tells us nothing about what her outcome would have been under either treatment. Within a stratum of \(X\), the treated and untreated are exchangeable, as if a coin decided their treatment. This is what randomization guarantees by design; in an observational study it is a hope, namely that \(X\) contains every characteristic that influenced both the treatment decision and the outcome. The three forms differ in how much exchangeability they demand, summarized here:

Form	Statement	Plain meaning	What it buys
Strong	\(\bigl(Y(0),Y(1)\bigr)\perp T\mid X\)	Within a stratum, treatment is as-if-random with respect to both potential outcomes jointly	Identifies both arms; underwrites the balancing-score and propensity theory of Chapter 10
Weak (for \(Y(t)\))	\(Y(t)\perp T\mid X\)	Same, but only for the single arm \(t\)	Identifies the mean potential outcome \(\mathbb{E}[Y(t)]\) for that one arm
Mean (for \(Y(t)\))	\(\mathbb{E}[Y(t)\mid T,X]=\mathbb{E}[Y(t)\mid X]\)	Within a stratum, the average \(Y(t)\) is the same among treated and untreated	The minimum needed to identify the ATE

These three are genuinely different in strength, and the difference matters for which estimand can be identified. The following lemma orders them.

Lemma 9.1 (Hierarchy of ignorability) Strong ignorability implies weak ignorability for both \(t=0\) and \(t=1\); weak ignorability for \(Y(t)\) implies mean ignorability for \(Y(t)\), provided \(Y(t)\in L^1\).

Reader’s note: the proof below is the most technical in the chapter. Its message is simply that the three forms sit in a chain, strong \(\Rightarrow\) weak \(\Rightarrow\) mean. A reader meeting this material for the first time may take the chain on faith and skip to the “What to remember” paragraph after it; the machinery is here for completeness and for the Coq counterpart.

Proof. Strong implies weak. By symmetry (graphoid axiom G1 of Theorem 4.5, which says \(A\perp B\mid Z\iff B\perp A\mid Z\)) strong ignorability is \(T\perp\bigl(Y(0),Y(1)\bigr)\mid X\). The decomposition axiom (G2 of Theorem 4.5, which says that if \(T\) is independent of a pair given \(X\) then it is independent of each member given \(X\)) states that \(T\perp(U,W)\mid X\) implies \(T\perp U\mid X\); applying it with \(U=Y(t)\) and \(W=Y(1-t)\) yields \(T\perp Y(t)\mid X\), that is, weak ignorability for \(Y(t)\), for each \(t\).

Weak implies mean. Fix \(t\) and write \(V=Y(t)\). Conditional independence \(V\perp T\mid X\) in the sense of Equation 4.9 is equivalent to \(\mathbb{E}[f(V)\mid T,X]=\mathbb{E}[f(V)\mid X]\) a.s. for every bounded measurable \(f\). We must extend this from bounded \(f\) to the (possibly unbounded) identity function, and this is where \(V\in L^1\) enters. The idea is standard: approximate \(V\) by bounded functions of \(V\), apply the identity for each, and pass to the limit. For \(m\ge 1\) let \(f_m(v)=\max(-m,\min(m,v))\) be the truncation of \(v\) to the interval \([-m,m]\); each \(f_m\) is bounded and measurable, so \[ \mathbb{E}[f_m(V)\mid T,X]=\mathbb{E}[f_m(V)\mid X]\quad\text{a.s.} \] As \(m\to\infty\) the truncation is undone: \(f_m(V)\to V\) pointwise (once \(m\) exceeds \(|V(\omega)|\) the value is untouched), and \(|f_m(V)|\le|V|\in L^1\) provides a single integrable envelope for all \(m\). By the conditional form of dominated convergence (the conditional-expectation analogue of Theorem 4.2, obtained by applying that theorem inside each conditional expectation) the left side converges a.s. to \(\mathbb{E}[V\mid T,X]\) and the right side to \(\mathbb{E}[V\mid X]\). Hence \(\mathbb{E}[Y(t)\mid T,X]=\mathbb{E}[Y(t)\mid X]\) a.s., which is mean ignorability. \(\square\)

The converse implications fail: mean ignorability constrains only first moments and says nothing about the rest of the conditional law, while weak ignorability for one label says nothing about the other. A concrete illustration of the first gap: within a stratum \(X=x\), suppose the treated potential outcome \(Y(1)\) is distributed as follows.

Group	\(Y(1)\) takes values	\(\mathbb{E}[Y(1)\mid T,X=x]\)	\(\mathrm{Var}(Y(1)\mid T,X=x)\)
Treated (\(T=1\))	\(9\) or \(11\), each with probability \(\tfrac12\)	\(10\)	\(1\)
Untreated (\(T=0\))	\(5\) or \(15\), each with probability \(\tfrac12\)	\(10\)	\(25\)

The two conditional means are both \(10\), so mean ignorability for \(Y(1)\) holds; but the two conditional distributions differ (variances \(1\) versus \(25\)), so \(Y(1)\perp T\mid X\) fails. Mean ignorability is strictly weaker, and, as the identification proof will show, strictly enough. (Exercise 9.6 asks you to turn this picture into a fully specified joint law and to check that the ATE is still identified.)

What to remember. The practical distillation of the hierarchy is this. A randomized trial aims to make treatment independent of the potential outcomes, delivering strong ignorability for free. An observational analysis must instead condition on enough covariates to make treated and untreated patients comparable, and it can only hope for ignorability, never verify it. The ATE identification proof needs only the weakest form, mean ignorability of each arm; we nonetheless usually state the strong form, for two reasons. First, it is the natural output of randomization, so assuming it costs nothing there. Second, the balancing-score and propensity-score theory of the next chapter genuinely needs the full joint independence, not merely equal conditional means. So the extra strength is not wasted even though this one theorem does not use it. Finally, ignorability is untestable from the observed data, because it constrains the joint law of \(T\) with the partly unobserved potential outcomes. A concrete example makes the danger vivid: in rheumatoid arthritis or oncology, disease severity often drives both which treatment a clinician chooses and how the patient fares. If severity is recorded, we can condition on it; if it is unmeasured, no amount of modeling of the recorded covariates repairs the confounding, and no diagnostic run on the data can reveal the omission. In a randomized trial ignorability holds by design, with \(T\) assigned independently of everything, including unmeasured characteristics; in an observational study it demands that \(X\) contain every confounder.

The second assumption guarantees that every covariate stratum actually contains both treated and control units, so that the conditional means we will average are defined everywhere. The intuition is simple and worth stating before the inequalities: we cannot learn the treated outcome for a type of patient who is never treated, nor the control outcome for a type who is never a control. If, say, no frail patient ever receives the new drug, the data contain no treated outcomes for frail patients, and the active-arm mean for that stratum, hence the population ATE, cannot be recovered without extrapolation.

Definition 9.8 (Positivity (overlap)) With propensity score \(e(x)=P(T=1\mid X=x)\), positivity (or overlap) holds for treatment \(t\) if \[ P(T=t\mid X=x)>0 \qquad\text{for } P_X\text{-almost every } x\in\mathcal{X}, \tag{9.9}\] where \(P_X\) denotes the marginal distribution (law) of the covariates \(X\), so that “\(P_X\)-almost every \(x\)” means “for all \(x\) except possibly a set of covariate values that occurs with probability zero.” Equivalently, weak positivity for both treatments is \(0<e(x)<1\) a.s. Strict positivity strengthens this to a uniform bound: there is \(\varepsilon\in(0,\tfrac12)\) with \[ \varepsilon\le e(x)\le 1-\varepsilon\qquad\text{for } P_X\text{-almost every } x. \tag{9.10}\] The reason for the stronger, uniform version is estimation stability: estimators that divide by \(e(X)\) or \(1-e(X)\) (the weighting methods of the next chapter) have variance that blows up as the propensity nears \(0\) or \(1\), so a bound bounded away from the endpoints is what keeps them well-behaved. \(\blacktriangleleft\)

[machine-checked: theories/CausalAssumptions.v, Definition weak_positivity, Definition strong_positivity, Lemma strong_implies_weak]

Reader translation. Positivity says every kind of patient could, with some chance, have gone either way: each covariate stratum contains both treated and control patients. Weak positivity asks only that the chance be nonzero; strict positivity asks that it be bounded away from zero and one. In the indirect-comparison setting this same condition reappears as covariate overlap between studies. Picture a trial of drug \(B\) that enrolled only elderly patients and a trial of drug \(C\) that enrolled only young patients: there is no covariate region where both drugs are represented, so no reweighting can turn one trial’s population into the other’s, and the comparison of \(B\) and \(C\) rests entirely on extrapolation.

Strict positivity implies weak positivity: if \(\varepsilon\le e(x)\le 1-\varepsilon\) with \(0<\varepsilon<\tfrac12\) then \(0<\varepsilon\le e(x)\) and \(e(x)\le 1-\varepsilon<1\), so \(0<e(x)<1\). Weak positivity is what identification needs, because Corollary 9.1 and the iterated-expectation argument require \(P(T=t\mid X)>0\) almost everywhere; strict positivity is what stable estimation needs, for the variance reason just given. That failure of overlap is the formal reason matching-adjusted indirect comparison breaks down when trial populations barely overlap, taken up in Part IV, and it is the bridge to the transportability conditions of Definition 12.3. Together, ignorability and positivity are Rosenbaum and Rubin (1983)’s strong ignorability (corresponds to B.3 and B.4 in the proof catalogue).

9.6 Identification of the average treatment effect

We can now turn the unobservable ATE into an observable functional of the data. First, one piece of notation that is the conceptual hinge of the entire argument. We have two “conditional mean outcome” objects, and they look almost identical but mean very different things.

Definition 9.9 (Observed outcome regression) The observed outcome regression is \[ \mu_t^{\mathrm{obs}}(x) := \mathbb{E}[Y\mid T=t,X=x], \] the average observed outcome among units with covariates \(x\) who received treatment \(t\). It is to be contrasted with the potential mean \(\mu_t(x)=\mathbb{E}[Y(t)\mid X=x]\) of Definition 9.6, the average outcome those units would have under \(t\). \(\blacktriangleleft\)

Reader translation. \(\mu_t^{\mathrm{obs}}(x)\) is a plain regression you can actually fit from data: group patients by their covariates \(x\) and their received treatment \(t\), and average the outcomes you see. \(\mu_t(x)\) is the causal object we want but cannot see directly: the average outcome those patients would have under \(t\), treated and untreated alike. Identification is precisely the claim that, under ignorability and positivity, these two coincide, \(\mu_t(x)=\mu_t^{\mathrm{obs}}(x)\), so that a fittable regression equals an unfittable counterfactual mean. Alongside it we use \(\mathbb{E}_X[\,\cdot\,]\) for an expectation over the covariate distribution \(P_X\): in \(\mathbb{E}_X\bigl[\mu_t^{\mathrm{obs}}(X)\bigr]\) the outer \(\mathbb{E}_X\) averages the stratum-specific regression over the covariate distribution of the target population, not over the treated group and not over the control group. This outer averaging is the exact point where the choice of target population enters, and it is the bridge to population adjustment.

The engine of identification is a single chain of three equalities, applied to each potential-outcome mean: peel off the covariate by the tower property, swap the treatment-assignment conditioning by ignorability, swap the potential outcome for the observed one by consistency. We isolate the per-arm result first.

Lemma 9.2 (Identification of a mean potential outcome) Assume SUTVA (so the consistency identity Equation 9.1 holds), mean ignorability for \(Y(t)\), and positivity for treatment \(t\). Then \[ \mathbb{E}[Y(t)] = \mathbb{E}_X\bigl[\,\mathbb{E}[Y\mid T=t,X]\,\bigr]. \tag{9.11}\]

Proof. We chain three identities; each equality is labeled by the fact that licenses it.

Step 1 (tower property). By Theorem 4.4, equivalently Corollary 4.1, applied to \(Y(t)\in L^1\) and the \(\sigma\)-algebra generated by \(X\), \[ \mathbb{E}[Y(t)] = \mathbb{E}_X\bigl[\,\mathbb{E}[Y(t)\mid X]\,\bigr]. \]

Step 2 (ignorability). By mean ignorability for \(Y(t)\), \(\mathbb{E}[Y(t)\mid T,X]=\mathbb{E}[Y(t)\mid X]\); evaluating on the event \(\{T=t\}\), which by positivity has positive probability for \(P_X\)-almost every \(x\), gives \(\mathbb{E}[Y(t)\mid X]=\mathbb{E}[Y(t)\mid T=t,X]\) a.s., so \[ \mathbb{E}[Y(t)] = \mathbb{E}_X\bigl[\,\mathbb{E}[Y(t)\mid T=t,X]\,\bigr]. \]

Step 3 (consistency). By the outcome swap of Corollary 9.1, \(\mathbb{E}[Y(t)\mid T=t,X]=\mathbb{E}[Y\mid T=t,X]\) on the positivity event, and substituting yields Equation 10.5. Every conditional mean on the right-hand side is a functional of the observed-data law of \((X,T,Y)\), so \(\mathbb{E}[Y(t)]\) is identified. \(\square\)

Subtracting the two arms gives the central identification theorem of the chapter, the result on which standardization, inverse-probability weighting, and the entire machinery of Part IV ultimately rest.

Theorem 9.3 (Identification of the ATE (adjustment formula)) Assume SUTVA, mean ignorability for both \(t=0\) and \(t=1\) (in particular, strong ignorability suffices), and positivity for both treatments. Then the average treatment effect is identified by the adjustment formula (also called the g-formula or standardization formula) \[ \tau = \mathbb{E}_X\bigl[\,\mathbb{E}[Y\mid T=1,X] - \mathbb{E}[Y\mid T=0,X]\,\bigr]. \tag{9.12}\] In the notation of Definition 9.9, this is \(\tau=\mathbb{E}_X[\mu_1^{\mathrm{obs}}(X)-\mu_0^{\mathrm{obs}}(X)]\).

[machine-checked: theories/CausalAssumptions.v, Theorem ATE_identification]

Proof. Apply Lemma 9.2 once with \(t=1\) and once with \(t=0\), which is legitimate because the hypotheses hold for both labels, to obtain \(\mathbb{E}[Y(1)]=\mathbb{E}_X[\mu_1^{\mathrm{obs}}(X)]\) and \(\mathbb{E}[Y(0)]=\mathbb{E}_X[\mu_0^{\mathrm{obs}}(X)]\). By Definition 9.4 and linearity of expectation (Theorem 4.4 gives the outer expectation, linearity gives the subtraction), \[ \tau=\mathbb{E}[Y(1)]-\mathbb{E}[Y(0)] =\mathbb{E}_X[\mu_1^{\mathrm{obs}}(X)]-\mathbb{E}_X[\mu_0^{\mathrm{obs}}(X)] =\mathbb{E}_X\bigl[\mu_1^{\mathrm{obs}}(X)-\mu_0^{\mathrm{obs}}(X)\bigr], \] which is Equation 9.12. \(\square\)

Why this matters. The adjustment formula is the population target that every estimator in Part II and every population-adjustment method later (G-computation, inverse-probability weighting, MAIC, STC, ML-NMR) is built to estimate. Read it as a recipe: within each covariate stratum, take the difference of the observed treated and control means; then average those stratum differences using the target population’s covariate distribution. When you later meet a “standardized” or “population-adjusted” indirect comparison, this equation is what it is approximating. Because a numerical grip helps before the general theory settles, we preview the running population immediately.

Example 9.1 (The adjustment formula at a glance) Take the two-stratum population of Example 9.2 (developed in full below): \(X\in\{0,1\}\) with \(P(X=0)=P(X=1)=\tfrac12\), observed regressions \(\mu_0^{\mathrm{obs}}(0)=10\), \(\mu_1^{\mathrm{obs}}(0)=14\), \(\mu_0^{\mathrm{obs}}(1)=20\), \(\mu_1^{\mathrm{obs}}(1)=24\), and treatment three times more likely in the favorable stratum. The adjustment formula Equation 9.12 averages the stratum differences over the population covariate split \(\tfrac12,\tfrac12\): \[ \tau=\tfrac12(14-10)+\tfrac12(24-20)=\tfrac12\cdot4+\tfrac12\cdot4=4 . \] The naive treatment-minus-control contrast, which instead averages over each arm’s own (imbalanced) covariate mix, will come out to \(9\). The gap between \(4\) and \(9\) is the selection bias the next section isolates; the full arithmetic, including the within-arm mixes, is in Example 9.2. \(\blacktriangleleft\)

The adjustment formula is the population statement; it tells an analyst with infinite data exactly how to combine observable conditional means into the ATE. It also dictates the estimators of the next chapter, of which two are central. G-computation models the inner regression \(\mu_t^{\mathrm{obs}}(x)\) and averages it over the empirical covariate distribution; it is identified by exactly this theorem and developed as Theorem 10.4. Inverse-probability weighting instead models the propensity score and reweights, recovering the same target through Theorem 10.3, since the masked identity Equation 9.2 gives \(\mathbb{E}[TY/e(X)]=\mathbb{E}[Y(1)]\), another route to \(\mathbb{E}[Y(1)]=\mathbb{E}_X[\mu_1^{\mathrm{obs}}(X)]\). You will meet these two first in the next chapter, and afterward their combination, the doubly robust estimator Theorem 10.5, together with the dimension-reducing balancing-score theory (Definition 10.1, Theorem 10.1, Theorem 10.2) that lets the scalar \(e(X)\) stand in for the full covariate vector \(X\). What the present theorem supplies is the identification all of them implement.

Remark. It is worth dwelling on a subtlety the proof exposes. It used only mean ignorability for each arm, the weakest form in Definition 9.7, together with positivity and SUTVA. Yet the assumption we usually state is strong ignorability. Why assume more than we use? Two reasons, and they are not merely stylistic. First, strong ignorability is the natural output of randomization: a trial that assigns treatment by a coin flip makes \(T\) independent of the entire joint law of \((Y(0),Y(1))\), not just of its conditional means, so in a trial the strong form is available at no extra cost. Second, the balancing-score and propensity-score theory of the next chapter genuinely requires the full conditional independence, not equal conditional means alone; the result that conditioning on the scalar \(e(X)\) can replace conditioning on \(X\) (Theorem 10.1) fails under mean ignorability. So the stronger assumption is doing real work elsewhere in the book, even though this single identification theorem does not need it. \(\blacktriangleleft\)

9.7 The naive contrast and selection bias

Why not simply compare the average outcome among the treated with the average among the controls? That naive contrast is what an unadjusted analysis reports, and it is in general not the ATE. Here is the picture before the algebra: in the running example, clinicians give the new drug preferentially to favorable-baseline patients, so the treated arm is stacked with high scorers and the control arm with low scorers. Even if the drug did nothing, the treated would out-score the controls simply because they were healthier to begin with. That built-in head start is selection bias, and the next theorem locates it exactly: the naive contrast equals the effect on the treated plus a term measuring how treated and control groups would have differed even under no treatment.

Theorem 9.4 (The naive contrast equals ATT plus selection bias) Under SUTVA, define the naive contrast \(\Delta_{\mathrm{naive}}=\mathbb{E}[Y\mid T=1]-\mathbb{E}[Y\mid T=0]\). Then \[ \Delta_{\mathrm{naive}} = \underbrace{\tau_{\mathrm{T}}}_{\text{ATT}} + \underbrace{\bigl(\mathbb{E}[Y(0)\mid T=1]-\mathbb{E}[Y(0)\mid T=0]\bigr)}_{\text{selection bias}} . \tag{9.13}\]

[machine-checked: theories/PotentialOutcomes.v, Lemma selection_bias_decomposition]

Proof. By the consistency identity Theorem 9.2, \(Y=Y(1)\) on \(\{T=1\}\) and \(Y=Y(0)\) on \(\{T=0\}\), so the observed group means are potential-outcome means: \[ \mathbb{E}[Y\mid T=1]=\mathbb{E}[Y(1)\mid T=1], \qquad \mathbb{E}[Y\mid T=0]=\mathbb{E}[Y(0)\mid T=0]. \] Therefore \[ \Delta_{\mathrm{naive}}=\mathbb{E}[Y(1)\mid T=1]-\mathbb{E}[Y(0)\mid T=0]. \] Add and subtract the counterfactual control mean among the treated, \(\mathbb{E}[Y(0)\mid T=1]\). We choose precisely this quantity because it is the one bridge between the two observed means: it shares the conditioning event \(\{T=1\}\) with the first term (so the pair combines into an effect among the treated) and it shares the potential outcome \(Y(0)\) with the second term (so that pair compares the same counterfactual across the two groups). Concretely, \[ \Delta_{\mathrm{naive}} =\bigl(\mathbb{E}[Y(1)\mid T=1]-\mathbb{E}[Y(0)\mid T=1]\bigr) +\bigl(\mathbb{E}[Y(0)\mid T=1]-\mathbb{E}[Y(0)\mid T=0]\bigr). \] The first bracket is \(\mathbb{E}[Y(1)-Y(0)\mid T=1]=\tau_{\mathrm{T}}\) by linearity of conditional expectation and Equation 9.5; the second is the selection-bias term. This is Equation 9.13. \(\square\)

Why this matters. This decomposition is the precise reason an indirect comparison cannot simply pool raw arm means across trials. The selection-bias term compares the untreated potential outcome \(Y(0)\) between the group that took treatment and the group that did not; it is nonzero exactly when the two groups would have differed even absent treatment, which is precisely confounding. It is an identity, not an approximation: it holds under SUTVA alone, with no ignorability. Population adjustment exists to remove this term. The next corollary shows it vanishes under the strongest form of ignorability, marginal independence, which is what a randomized trial provides, and that this is what makes the naive contrast valid there.

Corollary 9.2 (When the naive contrast is the ATE) Suppose SUTVA holds and treatment is marginally ignorable, \(\bigl(Y(0),Y(1)\bigr)\perp T\) (no conditioning on \(X\)), as in a marginally randomized experiment. Then the selection-bias term in Equation 9.13 is zero and \[ \Delta_{\mathrm{naive}}=\tau_{\mathrm{T}}=\tau. \]

Proof. Marginal independence gives \(\mathbb{E}[Y(0)\mid T=1]=\mathbb{E}[Y(0)]=\mathbb{E}[Y(0)\mid T=0]\), so the selection-bias term in Equation 9.13 is \(0\) and \(\Delta_{\mathrm{naive}}=\tau_{\mathrm{T}}\). Independence also gives \(\mathbb{E}[Y(1)-Y(0)\mid T=1]=\mathbb{E}[Y(1)-Y(0)]\), so \(\tau_{\mathrm{T}}=\tau\). \(\square\)

Here “marginally randomized experiment” means the simplest randomized design: treatment is decided by one coin flip for every patient, the same flip probability for all, with no conditioning on covariates. This is the plain randomized controlled trial a health researcher already knows; the word “marginally” only signals that the coin ignores \(X\) entirely, which is why the independence in the corollary holds without any conditioning. (A stratified trial, which flips a differently biased coin within each stratum of \(X\), delivers only the conditional independence of Definition 9.7, and there one must still adjust.) When ignorability holds only conditionally on \(X\), as in an observational study or in two trials with different case mixes, the selection-bias term is generally nonzero and the naive contrast is biased; the remedy is to condition on \(X\) and average, which is exactly the adjustment formula Equation 9.12. This is the formal reason indirect comparisons cannot simply pool raw arm means across studies, and it motivates every population-adjustment method in Parts IV and V.

9.8 A worked example: confounding, the g-formula, and selection bias

We now put concrete numbers to the whole machinery in a single population, verifying the adjustment formula and the selection-bias decomposition by hand. This is the population Alice and Bob live in: the two covariate strata are their favorable (\(X=1\)) and poor (\(X=0\)) baselines, and the stratum means are exactly their potential scores. The example is deliberately built on the identity scale with a constant conditional effect, so that the only thing separating the naive contrast from the ATE is confounding, not the non-collapsibility studied in Example 7.5; that lets us see selection bias in isolation.

Example 9.2 (Standardization undoes confounding in a two-stratum population) Let \(X\in\{0,1\}\) be a binary prognostic covariate with \(P(X=0)=P(X=1)=\tfrac12\). Treatment is confounded by \(X\) through the propensity score \[ e(0)=P(T=1\mid X=0)=0.25,\qquad e(1)=P(T=1\mid X=1)=0.75, \] so that the favorable-baseline stratum \(X=1\) is three times as likely to be treated (clinicians steer the new drug toward the patients who were already doing better). Assume SUTVA, strong ignorability, and positivity (both \(e\) values lie strictly in \((0,1)\)). The conditional mean potential outcomes are \[ \mu_0(0)=10,\quad \mu_1(0)=14,\qquad \mu_0(1)=20,\quad \mu_1(1)=24, \] so the conditional average treatment effect is constant, \(\tau(0)=\tau(1)=4\). Under ignorability the observable regressions equal these conditional means, \(\mu_t^{\mathrm{obs}}(x)=\mu_t(x)\).

True ATE by the adjustment formula (Equation 9.12). Averaging the constant stratum effect, \[ \tau=\mathbb{E}_X[\mu_1(X)-\mu_0(X)] = \tfrac12(14-10)+\tfrac12(24-20) = \tfrac12\cdot 4+\tfrac12\cdot 4 = 4. \] Equivalently \(\mathbb{E}[Y(1)]=\tfrac12(14)+\tfrac12(24)=19\) and \(\mathbb{E}[Y(0)]=\tfrac12(10)+\tfrac12(20)=15\), giving \(\tau=19-15=4\).

The naive contrast. Treatment selection skews the covariate mix within each arm. The joint cell probabilities are \(P(X=x,T=t)=P(X=x)\,e(x)^{t}(1-e(x))^{1-t}\): \[ \begin{aligned} &P(X{=}0,T{=}1)=\tfrac12(0.25)=0.125,\quad P(X{=}1,T{=}1)=\tfrac12(0.75)=0.375,\\ &P(X{=}0,T{=}0)=\tfrac12(0.75)=0.375,\quad P(X{=}1,T{=}0)=\tfrac12(0.25)=0.125. \end{aligned} \] Hence \(P(T=1)=P(T=0)=0.5\), and the within-arm covariate distributions are \[ P(X=1\mid T=1)=\frac{0.375}{0.5}=0.75,\qquad P(X=1\mid T=0)=\frac{0.125}{0.5}=0.25. \] The treated arm is covariate-shifted toward the high-risk stratum, the control arm toward the low-risk stratum. Using consistency, \(\mathbb{E}[Y\mid T=1]=\mathbb{E}[Y(1)\mid T=1]\) and \(\mathbb{E}[Y\mid T=0]=\mathbb{E}[Y(0)\mid T=0]\): \[ \begin{aligned} \mathbb{E}[Y\mid T=1]&=0.25(14)+0.75(24)=3.5+18=21.5,\\ \mathbb{E}[Y\mid T=0]&=0.75(10)+0.25(20)=7.5+5=12.5, \end{aligned} \] so the naive contrast is \[ \Delta_{\mathrm{naive}}=21.5-12.5=9.0. \] The unadjusted analysis overstates the effect by more than a factor of two, reporting \(9\) against the truth of \(4\).

Selection-bias decomposition (Equation 9.13). Because the conditional effect is the constant \(4\), the effect on the treated is \(\tau_{\mathrm{T}}=\mathbb{E}[\tau(X)\mid T=1]=4\). The counterfactual control mean among the treated and the factual control mean among the controls are \[ \begin{aligned} \mathbb{E}[Y(0)\mid T=1]&=0.25(10)+0.75(20)=2.5+15=17.5,\\ \mathbb{E}[Y(0)\mid T=0]&=0.75(10)+0.25(20)=7.5+5=12.5, \end{aligned} \] so the selection bias is \(17.5-12.5=5.0\). The decomposition checks out: \[ \Delta_{\mathrm{naive}}=\tau_{\mathrm{T}}+\text{selection bias}=4+5=9.0 . \] The entire discrepancy between the naive contrast and the ATE is the \(5.0\) of selection bias, created because the treated would have had worse untreated outcomes (mean \(17.5\)) than the controls did (mean \(12.5\)), purely through the covariate imbalance the propensity score induces.

Standardization recovers the truth. The adjustment formula reweights the stratum-specific contrasts by the population covariate distribution rather than the arm-specific one: \[ \tau=\mathbb{E}_X\bigl[\mu_1^{\mathrm{obs}}(X)-\mu_0^{\mathrm{obs}}(X)\bigr] =\tfrac12(14-10)+\tfrac12(24-20)=4 , \] matching the true ATE and removing the bias entirely. \(\blacktriangleleft\)

The example exhibits the chapter in miniature. The same observed data \((X,T,Y)\) produce a biased number (\(9\)) when contrasted naively and the correct number (\(4\)) when standardized, and the gap is exactly the selection-bias term the decomposition isolates. Notice that ATE, ATT, and CATE all equal \(4\) here, because the effect is constant on the collapsible identity scale; had we measured the effect as an odds ratio the marginal and conditional effects would have parted ways even with no confounding, which is the separate phenomenon of Definition 7.7 and the subject of Definition 11.6 in the next chapter. It is worth separating two things this example might otherwise blur. The covariate \(X\) here is a prognostic variable (it predicts the outcome) that is also a confounder (it steers treatment), and that is why the within-study effect is biased. In an indirect comparison the usual villain is different: it is an effect modifier, a covariate that changes the size of the treatment effect across its levels, distributed differently in two study populations. A baseline imbalance that involves only prognosis, with no effect modification, biases the naive within-study contrast (as here) but need not obstruct the cross-study transport of a conditional effect on a suitable scale. The distinction between prognostic variables, confounders, and effect modifiers is the theme of Chapter 11 (Definition 11.5, Definition 11.3); keep it in view, because the whole logic of population adjustment turns on it.

9.9 Why identification is the foundation of indirect comparison

Everything so far concerned a single population. This closing section connects that single-population identification to the multi-study problem the book exists to solve, in three steps: what carries over within a study, what is needed to move across studies, and what therefore becomes central in later chapters.

Within a study, identification is settled. One population has one covariate law \(P_X\), one propensity score \(e(x)\), one pair of observed regressions \(\mu_t^{\mathrm{obs}}(x)\). The adjustment formula Equation 9.12 identifies the ATE in that population, and the selection-bias decomposition Equation 9.13 explains what goes wrong if we ignore the covariates. A randomized trial of \(A\) versus \(B\) identifies the \(A\)-versus-\(B\) effect in the trial’s own population; a trial of \(A\) versus \(C\) identifies the \(A\)-versus-\(C\) effect in its own population. Nothing in this chapter compares \(B\) with \(C\).

Across studies, indirect comparison is the same logic applied between populations. To compare \(B\) with \(C\) we exploit a shared anchor: the common treatment \(A\). The structure is small enough to tabulate.

Study	Arms	Within-study effect it identifies	Role
\(AB\)	\(A\) vs \(B\)	\(d_{AB}\), the effect of \(B\) vs \(A\) in study \(AB\)’s population	supplies the \(A\)-vs-\(B\) contrast
\(AC\)	\(A\) vs \(C\)	\(d_{AC}\), the effect of \(C\) vs \(A\) in study \(AC\)’s population	supplies the \(A\)-vs-\(C\) contrast
target	\(B\) vs \(C\)	\(d_{BC}=d_{AB}-d_{AC}\), valid only if both refer to a common population	the quantity we actually want

The subtraction \(d_{BC}=d_{AB}-d_{AC}\) is the indirect (Bucher) comparison of Chapter 14. It is honest only when the two within-study effects live in, or can be transported to, a common population; otherwise we are subtracting effects defined in two different worlds. Transport across populations is governed by the very two assumptions of this chapter, now read between studies rather than within one. Positivity becomes covariate overlap: the studies’ covariate ranges must intersect, or no reweighting can bridge them (the elderly-only versus young-only picture of Section 9.5 is exactly this failure). Ignorability becomes the requirement that the covariates explaining between-study differences are measured and adjusted for, formalized as the transportability conditions of Definition 12.3 and as the absence of the ecological bias of Definition 16.2.

What therefore becomes central later. Three things that were benign or invisible in one population move to the foreground across populations. First, the estimand: population-adjustment methods target a marginal effect in a stated target population, so naming that population is now unavoidable. Second, effect modification: a covariate whose distribution differs between studies and that modifies the effect will make a within-study effect fail to transport, which is why the CATE, not just the ATE, is the object that must be carried across. Third, the effect scale: benign here on the identity scale, it becomes decisive once nonlinear links and the non-collapsibility of Definition 11.6 enter, because then even a correctly transported conditional effect need not average to the marginal effect a decision maker wants. The next chapter develops the estimators that implement the adjustment formula within a study; Chapters 11 and 12 extend identification to effect modification and transport; and Parts III to V build these into the Bucher comparison, network meta-analysis, MAIC, STC, and ML-NMR that indirect comparison actually requires.

9.10 Notes and references

The potential-outcomes model is due to Hernán and Robins (2020)’s lineage of Neyman, in the 1923 randomization analysis of agricultural experiments, and Rubin, who in 1974 extended it to observational studies and named the counterfactual framework; Holland’s 1986 article crystallized the “fundamental problem of causal inference” used in Theorem 9.1. Our treatment follows Hernán and Robins (2020) throughout, with the strong-ignorability formulation and the central role of the propensity score from Rosenbaum and Rubin (1983). The adjustment formula Equation 9.12 is the simplest instance of Robins’s g-formula (Robins (1986)); the letter “g” stands for generalized, since the same construction generalizes to sequences of treatments given over time, where it becomes the g-computation algorithm. This chapter corresponds to items B.1 through B.5 of the companion proof catalogue: potential outcomes and SUTVA (B.1, Definition 9.1, Definition 9.3), the consistency identity (B.2, Theorem 9.2), ignorability in its three forms (B.3, Definition 9.7), positivity (B.4, Definition 9.8), and the identification of the ATE (B.5, Theorem 9.3). The estimators that the adjustment formula underwrites, namely inverse-probability weighting, G-computation, and the doubly robust augmented estimator, are catalogue items B.6 through B.12 and are developed in the next chapter as Theorem 10.3, Theorem 10.4, Theorem 10.5, and Theorem 10.6, together with the balancing-score and propensity-score theory Definition 10.1, Theorem 10.1, and Theorem 10.2.

Several results carry machine-checked tags pointing to the companion Coq development; a reader auditing the formalization can follow them via Appendix G, and every other reader may ignore them. The fundamental problem is ITE_unobservable in theories/PotentialOutcomes.v; the consistency identity and its masked and swapped forms are Definition consistency, Lemma consistency_equiv, Lemma consistency_expectation, Lemma consistency_treated_mean, and Lemma consistency_control_mean in the same file; the estimands and their decomposition are Definition ATE, Definition ATT, Definition ATC, Lemma ATE_split, and Lemma ATE_decomposition; and the selection-bias decomposition is Lemma selection_bias_decomposition. The assumptions and the ATE identification live in theories/CausalAssumptions.v: SUTVA and the no-interference reduction are Definition SUTVA and Lemma no_interference_unit_level; ignorability is Definition weak_unconfoundedness and Definition strong_unconfoundedness with the ordering Lemma strong_implies_weak_unconf; positivity is Definition weak_positivity and Definition strong_positivity with Lemma strong_implies_weak; and the identification theorem is Theorem ATE_identification. The Coq development states the probabilistic content (the tower property, the locality of conditional expectation, and the conditional-independence consequences) as named hypotheses on abstract expectation operators, exactly as the pen-and-paper proofs here invoke Theorem 4.4, Corollary 4.1, Theorem 4.5, and Definition 4.6 from Chapter 4; the proofs in this chapter supply the measure-theoretic justifications the Coq statements take as inputs.

The attributions to Neyman (1923, translated 1990), Rubin (1974), and Holland (1986) rely on sources not yet in the bibliography; they are listed with full bibliographic data in the work log for the orchestrator to merge. The worked example Example 9.2 is original to this text.

9.11 Exercises

A starred exercise (\(\star\)) has a full worked solution in Appendix F; the unstarred ones are for practice. The first two are gentle warm-ups; the later ones build to short proofs.

Exercise 9.1 (Warm-up: reading potential outcomes) (Warm-up.) Recall Alice from Section 9.1: her potential function scores are \(Y(1)=24\) under the new drug and \(Y(0)=20\) under standard care. (a) State her individual treatment effect \(\tau(\omega)\). (b) If Alice is assigned the new drug, write down her observed outcome \(Y\) and her counterfactual (hidden) outcome, and do the same if she is assigned standard care. (c) In one sentence, explain why, no matter which treatment she receives, we can never compute her ITE from her data alone, citing Theorem 9.1.

Exercise 9.2 (Interpretation: which estimand answers the question?) (Interpretation.) For each question below, name which of the ATE, ATT, ATC, or CATE it asks for, and say (one clause) which population the average is over. (a) “Across all eligible patients, how much would average function improve if everyone switched from standard care to the new drug?” (b) “Among the patients who actually received the new drug, how much did it help on average?” (c) “For favorable-baseline patients specifically, what is the average benefit?” (d) A regulator asks what the drug did for the people who took it. Which estimand, and why does the answer differ from (a) when treatment was not randomized?

Exercise 9.3 (Recomputing the worked example) (Computation.) Repeat Example 9.2 with the propensities changed to \(e(0)=0.1\) and \(e(1)=0.9\), keeping the covariate law and all four conditional means \(\mu_t(x)\) unchanged. (a) Recompute the within-arm covariate distributions \(P(X=1\mid T=1)\) and \(P(X=1\mid T=0)\). (b) Recompute the naive contrast \(\Delta_{\mathrm{naive}}\). (c) Verify the selection-bias decomposition Equation 9.13 numerically, and confirm that the standardized contrast Equation 9.12 still equals \(4\). (d) Explain in one sentence why sharper confounding (more extreme propensities) enlarges the bias while leaving the ATE untouched.

Exercise 9.4 (The masked-outcome identities) (Computation and proof.) Using only \(T\in\{0,1\}\) and the consistency identity Equation 9.1, prove the two masked identities Equation 9.2, \(TY=TY(1)\) and \((1-T)Y=(1-T)Y(0)\), and deduce that \(\mathbb{E}[TY]=\mathbb{E}[TY(1)]\) and \(\mathbb{E}[(1-T)Y]=\mathbb{E}[(1-T)Y(0)]\) for any population. Explain why these identities require no ignorability assumption.

Exercise 9.5 (ATE, ATT, and ATC in the worked example) (Computation.) In the population of Example 9.2, compute the ATT \(\tau_{\mathrm{T}}\) and the ATC \(\tau_{\mathrm{C}}\) directly from their definitions, and verify the decomposition \(\tau=p\,\tau_{\mathrm{T}}+(1-p)\,\tau_{\mathrm{C}}\) of Proposition 9.1 with \(p=P(T=1)\). Then modify a single conditional mean so that the CATE is no longer constant, and show that ATT and ATC now differ while the decomposition still holds.

Exercise 9.6 (Mean ignorability is strictly weaker) (Proof.) Construct a joint law for \((Y(1),T,X)\) in which mean ignorability \(\mathbb{E}[Y(1)\mid T,X]=\mathbb{E}[Y(1)\mid X]\) holds but weak ignorability \(Y(1)\perp T\mid X\) fails. (Hint: use the two-row template of Section 9.5; fix a single stratum \(X=x\) and give \(Y(1)\) the same conditional mean but different conditional variances across \(T=0\) and \(T=1\), for instance the values \(\{9,11\}\) among the treated and \(\{5,15\}\) among the untreated.) Prove carefully that the conditional means are equal (so mean ignorability holds) yet the conditional laws differ (so weak ignorability fails). Confirm that the identification of \(\mathbb{E}[Y(1)]\) in Lemma 9.2 still goes through, illustrating that the proof uses only the first moment.

Exercise 9.7 (Positivity failure breaks identification (\(\star\))) (Proof.) Let \(X\in\{0,1\}\) with \(P(X=1)=\tfrac12\), and suppose treatment is deterministic in one stratum: \(e(0)=P(T=1\mid X=0)=0\) while \(e(1)=0.5\). Keep SUTVA and strong ignorability. As a preliminary, draw the \(2\times 2\) table of the four cells \(\{X=x,T=t\}\) and mark which cell is empty (has probability zero); this empty cell is the whole source of the failure. Then: (a) Show that \(\mathbb{E}[Y\mid T=1,X=0]\) is undefined, so the right-hand side of the adjustment formula Equation 9.12 cannot be evaluated. (b) Exhibit two values of \(\mu_1(0)=\mathbb{E}[Y(1)\mid X=0]\), consistent with the same observed-data law, that yield different ATEs, thereby proving the ATE is not identified when positivity fails. (c) Relate this to the covariate-overlap requirement for indirect comparisons discussed in Section 9.9. (Solution in Appendix F.)

Exercise 9.8 (A symmetric selection-bias decomposition (\(\star\))) (Challenge.) Prove the control-side analogue of Theorem 9.4: \[ \Delta_{\mathrm{naive}}=\tau_{\mathrm{C}}+\bigl(\mathbb{E}[Y(1)\mid T=1]-\mathbb{E}[Y(1)\mid T=0]\bigr), \] by adding and subtracting \(\mathbb{E}[Y(1)\mid T=0]\) instead of \(\mathbb{E}[Y(0)\mid T=1]\) in the proof. Then average the two decompositions (the ATT-side of Equation 9.13 and this ATC-side) to express \(\Delta_{\mathrm{naive}}\) as a half-and-half combination, and interpret the resulting symmetric bias term. Show that under marginal ignorability both bias terms vanish, recovering Corollary 9.2. (Solution in Appendix F.)

Hernán, Miguel A., and James M. Robins. 2020. Causal Inference: What If. Chapman & Hall/CRC.

Robins, James. 1986. “A New Approach to Causal Inference in Mortality Studies with a Sustained Exposure Period.” Mathematical Modelling 7 (9-12): 1393–512.

Rosenbaum, Paul R., and Donald B. Rubin. 1983. “The Central Role of the Propensity Score in Observational Studies for Causal Effects.” Biometrika 70 (1): 41–55.