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The average treatment effect in a target population is $\mathbb{E}[Y(1)-Y(0)]$, the average additive contrast between two potential outcomes. It does not require every individual effect to be the same. If half the population has effect two and half effect minus one, the average treatment effect is $1/2$. Under consistency in causal inference, conditional exchangeability given pretreatment covariates $X$, and positivity, it is identified by ${\mathbb{E}}_X[\mathbb{E}(Y\mid A=1,X)-\mathbb{E}(Y\mid A=0,X)]$. The outer average uses the specified target population, not whichever group happens to be observed most often.

The average treatment effect on the treated is $\mathbb{E}[Y(1)-Y(0)\mid A=1]$, averaging over those who actually receive treatment. Their untreated potential outcomes are counterfactual. This can differ from the average treatment effect when effects vary and treatment uptake changes the population mix. Under conditional exchangeability, consistency in causal inference and adequate untreated overlap, it equals $\mathbb{E}[Y\mid A=1]-\mathbb{E}[\mathbb{E}(Y\mid A=0,X)\mid A=1]$. The second term standardizes untreated outcomes to the treated covariate distribution rather than using the crude untreated mean.

A causal effect compares potential outcomes under different specified interventions. For a binary treatment, a unit-level additive effect is $Y(1)-Y(0)$. Only one of those outcomes is observed for a given unit, so an observed treated-versus-untreated difference is not automatically the effect. For example, patients receiving treatment can differ in baseline severity from untreated patients. The average treatment effect averages the contrast over a target population; identifying it from data requires assumptions linking treatment assignment and the unobserved potential outcomes.

Causal inference uses data and explicit assumptions to learn effects of specified interventions. For binary treatment $A$, a target average treatment effect is $\mathbb{E}[Y(1)-Y(0)]$, comparing potential outcomes for the same population. Observing only $Y=Y(A)$ leaves one of each unit's potential outcomes unobserved.

An observed treated-minus-control difference can include confounding. For a concrete model, suppose half a population is in a low-baseline stratum with $(Y(0),Y(1))=(0,1)$ and half in a high-baseline stratum with $(2,3)$. Let treatment probabilities be $1/4$ and $3/4$ in the two strata. Every unit's causal effect is one. The treated mean is $\frac{1}{4}(1)+\frac{3}{4}(3)=2.5$, while the untreated mean is $\frac{3}{4}(0)+\frac{1}{4}(2)=0.5$. Their observed difference is two because their stratum compositions differ.

Under conditional exchangeability, positivity and consistency in causal inference, outcome standardization identifies the effect byIn the example, using the same half-and-half target weights for both strategies recovers one. The substantive assumptions, rather than the arithmetic alone, justify interpreting the standardized contrast as an intervention effect.^[ref]

A causal null hypothesis states that an intervention has no effect on a specified potential-outcome contrast. A sharp causal null sets every unit's treated and untreated potential outcomes equal; an average causal null sets their population mean difference to zero.

For binary potential outcomes, the causal risk ratio compares intervention risks:

In a binary-treatment potential outcomes model, conditional exchangeability given pretreatment covariates $X$ is $(Y(0),Y(1))\perp A\mid X$. Within each covariate stratum, treatment assignment then carries no information about the relevant potential outcomes. Together with consistency in causal inference and positivity, it permits outcome standardization to identify average causal contrasts. The assumption concerns unobserved counterfactual outcomes and cannot be established just by checking balance of the measured covariates. Including a large list of predictors is not by itself a guarantee that the assumption holds.

A confounder is a pretreatment variable relevant to removing confounding for a specified treatment-outcome question. A common cause $C$ with arrows $A\leftarrow C\to Y$ is a basic example: it creates a backdoor path between treatment $A$ and outcome $Y$.

Association with both variables is not a sufficient definition. In an appropriate causal directed acyclic graph, conditioning on a common effect can instead introduce collider bias. A confounder is a causal adjustment role, rather than any predictor with a small p-value.

One precise definition identifies a confounder as a member of some minimal sufficient adjustment set: there is a set containing $C$ that makes the relevant potential outcomes independent of treatment, and no proper subset of that set does so. The role can therefore depend on which other covariates are available and on the effect being estimated. A variable that merely reduces residual bias need not satisfy this definition.^[ref]

Confounding occurs when the compared treatment groups differ in relevant potential outcomes, so their observed outcome contrast mixes the causal effect with differences in baseline prognosis. In a binary-treatment model, absence of confounding is expressed through ignorability, $Y(a)\perp A$ for each compared $a$, or through conditional exchangeability after a sufficient pretreatment adjustment set is specified.

For a causal directed acyclic graph, $A\leftarrow U\to Y$ is the simplest backdoor path: the common cause changes both assignment and outcome. Confounding by indication is a practical example when baseline severity influences which treatment is received. Outcome standardization, matching and inverse probability weighting can address measured confounding under their identification assumptions.

A changed adjusted estimate does not, by itself, prove that confounding was removed. Noncollapsibility of the odds ratio can produce different marginal and conditional odds ratios even without confounding; adjustment for an inappropriate variable can introduce collider bias. Causal structure and the target effect must guide the adjustment choice.^[ref]

Consistency equates the observed outcome with the potential outcome under the treatment received.

Covariate balance means that the compared treatment groups have similar distributions of specified pretreatment covariates. Exact distributional balance in a weighted population isThis is a property of the represented covariates and chosen weights. Matching and inverse probability weighting can aim to approximate it.

Equal means are weaker than equal probability distributions. For example, a covariate taking values $-1,1$ equally often in one group and $-2,2$ equally often in the other has mean zero in both, but variances one and four. A zero standardized mean difference would miss that discrepancy. Inspect relevant spreads, tails, categories and combinations as well as means.

A nonsignificant difference test does not demonstrate covariate balance: small samples may have low statistical power, while large samples can detect negligible discrepancies. Covariate balance on measured pretreatment variables also cannot establish conditional exchangeability for unmeasured potential outcomes.

Doubly robust estimation combines two nuisance functions so that either one can be correctly estimated while the other is misspecified. For example, let $A\in \{0,1\}$ indicate treatment, $X$ covariates, $m_a(X)=\mathbb{E}[Y\mid A=a,X]$, and $e_a(X)=\mathbb{P}(A=a\mid X)$. Under conditional exchangeability, positivity and the usual consistency of observed and potential outcomes, ${\mu }_a=\mathbb{E}[m_a(X)]$ is the mean potential outcome under treatment $a$.

For candidate functions ${\tilde{m}}_a,{\tilde{e}}_a$ with denominators bounded away from zero, the augmented signal isConditioning on $X$ shows thatThe bias vanishes if either nuisance function is correct. This algebra explains Double robustness and the second-order product bias. It does not protect against both models being wrong, failed Causal identification, or nearly zero denominators. cross-fitting helps when flexible functions are estimated from the same sample; valid confidence intervals require further rate and moment assumptions. The average treatment effect is ${\mu }_1-{\mu }_0$.^[ref]

G-computation calculates the outcome distribution under a specified intervention from conditional laws identified under a causal model. For a single binary treatment, pretreatment covariates $X$, and outcome $Y$, the G-formula isIt follows by averaging over $X$, using conditional exchangeability to replace the conditional potential outcome mean by the mean among recipients of $a$, and using consistency in causal inference to replace $Y(a)$ by observed $Y$. Positivity ensures the required conditional outcome laws are represented in the target strata.^[ref]

For an illustrative binary outcome, suppose target weights are $0.8$ and $0.2$ in two baseline strata. Untreated risks $0.1,0.4$ give intervention risk $0.8(0.1)+0.2(0.4)=0.16$. Treated risks $0.05,0.2$ give $0.08$, so the standardized causal risk ratio is $0.5$ and the risk difference is $-0.08$. Both strategies use the same target weights.

With repeated treatments and time-varying covariates, the longitudinal G-formula integrates products of the covariate transition laws while setting each treatment according to the intervention strategy. This requires sequential exchangeability, longitudinal positivity and consistency in causal inference. Simply conditioning on every observed intermediate variable can block part of the intended effect; the sequential intervention calculation specifies which laws are averaged.

A treatment effect is homogeneous when the relevant contrast of potential outcomes is constant across units. For an additive treatment, this takes the form $Y(a)-Y(0)=\beta a$.

Ignorability is an assumption under which treatment assignment carries no information about relevant potential outcomes after conditioning on specified covariates.

Interference occurs when one unit's treatment changes another unit's potential outcome. It violates the usual assumption that each unit's potential outcomes depend only on that unit's own treatment.

Outcome standardization averages fitted conditional outcome risks over a specified target population's pretreatment covariate distribution. The same target distribution is used for each treatment strategy. Under conditional exchangeability, the positivity assumption and consistency, this average identifies the target mean of the corresponding potential outcomes. For a target consisting of treated subjects, average over their covariate distribution. A conditional odds ratio cannot generally be applied directly to an aggregate mean risk: the nonlinear odds-to-probability conversion must be performed before averaging. Outcome standardization supplies that individual-risk calculation.

As a rough rare-event calculation, divide the observed elective-group event count by the reported adjusted odds ratio:For a homogeneous illustrative risk, the exact odds conversion starts from $p_1=9/1515$ and givesThe corresponding baseline risk is about $0.22\%$, compared with $1.62\%$ in the observed reference group, roughly seven times lower. Thus taking the adjusted result literally implies exceptionally low background risk among the elective patients.

This is a diagnostic approximation, not an identified mean of potential outcomes obtainable from the aggregate table. A conditional odds ratio cannot generally be inverted at an aggregate mean: individual background risks are needed for outcome standardization. Interpreting the calculation causally also requires conditional exchangeability, the positivity assumption and a correctly specified outcome model. At very small risks the rare-event approximation makes the estimate of roughly three events useful for checking the plausibility of the adjustment.

Model deaths in disjoint equal-duration periods as independent observations with Poisson distributions with comparable population exposure and ascertainment. The expected before and after counts are ${\mu }_0=400$ and ${\mu }_1=320$. Their difference hasThe expected signal relative to its standard deviation is thereforeUnder the null of equal rates, condition on $N=D_0+D_1$: the first-period count has a binomial distribution with parameters $N$ and $1/2$. At a total near 720, the two-sided 5% rejection boundary for $D_0-D_1$ is approximately $1.96\sqrt{720}$. Under the proposed alternative, conditional on that total, its mean is $N/9$ and its variance is $80N/81$. Thus at $N=720$ the normal approximation gives power approximatelyThe lower-tail rejection probability is negligible at this alternative; allowing the Poisson total to fluctuate and using discrete rejection cutoffs changes the approximation slightly: an exact two-sided conditional test has about $83.8\%$ power under these Poisson means. Two years on each side should have adequate power for a 20% reduction under this model, though a particular realization can still fail to detect it.

This conclusion needs stable recording of drug-related deaths, comparable exposure denominators and no substantial overdispersion or temporal dependence. A change in population size, certification practice or other drug use can affect the comparison. Detecting a decline does not establish that mephedrone caused it: attributing displacement requires a credible comparison of potential outcomes, using an otherwise expected trend or other controls for changes occurring at the same time.

Let $Y(1)$ and $Y(0)$ be the potential outcomes for the same individual under well-defined interventions setting the binary exposure to 1 and 0. The average treatment effect, also called the average causal effect on the additive scale, isThe average is over the target population. This compares hypothetical outcomes under two interventions, rather than the observed difference $\mathbb{E}[Y\mid X=1]-\mathbb{E}[Y\mid X=0]$, which can be distorted by confounding. For binary $Y$, the displayed contrast is a causal risk difference. Consistency in causal inference and a well-defined intervention, including an appropriate no-interference in causal inference assumption, give these potential outcomes their meaning.