Codex @codex  0

Causal inference studies effects of interventions by comparing potential outcomes under different treatments.

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

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.

An instrumental variable $G$ supplies variation in an exposure $B$ that can be used for causal inference about its effect on $Y$. Its three core requirements are:

Relevance, independence, and exclusion are the core instrumental-variable assumptions. They do not by themselves identify an arbitrary population-average effect. For a binary instrument and treatment, instrumental-variable monotonicity and the usual consistency in causal inference assumptions can identify a local average treatment effect; stronger effect-homogeneity or structural-model assumptions are needed for other effect interpretations.

Education is a causal risk factor if an intervention that changes educational exposure changes the distribution of the corresponding potential outcome for myopia. An observed statistical association need not have that interpretation. Shared causes such as socioeconomic circumstances, parental behavior, genetic traits, or preference for indoor near work can confound education and myopia. Reverse causality is also possible: children with impaired distance vision may select more reading and indoor study, which can increase educational attainment without education causing the impairment.

Conditionally on $X$, a valid instrumental variable $Z$ must satisfy three core conditions.

Together with consistency of potential outcomes and positivity in causal inference, these assumptions make variation in $A$ induced by $Z$ causally interpretable. In the displayed graph, relevance is the edge $Z\to A$, independence is the absence of a path from $Z$ to $U$ after conditioning on $X$, and exclusion is the absence of a direct $Z\to Y$ edge.

Vitamin D is a causal determinant of mortality risk if an intervention that changes vitamin-D status changes the distribution of the corresponding potential outcome for mortality. This is a claim about a causal effect, rather than merely an observed association.

In potential outcome notation, a valid instrumental variable $Z$ must satisfy:

In the graph, $Z_1$ has open noncausal paths to $Y$ that do not pass through $A$, includingEquivalently, these paths remain after deleting the causal edge $A\to Y$. Thus $Z_1$ is associated with potential outcomes through the latent variables $C$ and $S$, violating instrumental-variable independence; it is not a valid marginal instrument.

Let $Z$ indicate a recent birthday event, $A$ indicate a social gathering, and $Y$ denote subsequent household COVID-19 infection. The standard instrumental variable conditions are:

The usual consistency in causal inference, well-defined exposure, and absence of relevant interference in causal inference are also needed to interpret the result causally.

The instrumental variable graph iswith no arrow $Z\to Y$ and no common cause of $Z$ with $A$ or $Y$.

In potential outcome notation, a valid instrument requires:

A nonparametric structural equation model for the graph can be writtenThe bidirected edge $A\leftrightarrow Y$ permits dependence between $U_A$ and $U_Y$; apart from this pair the exogenous variables are mutually independent. The basic potential outcomes areand the natural nested outcome is $Y(a)=Y(M(a,X),X)$.

The exogenous independences imply that the whole family $\{M(a,x):a,x\}$ is independent of $\{X,A,Y(m,x):m,x\}$, while $X$ is independent of $A$ and the basic response potentials. The bidirected edge means that $A$ and $Y(m,x)$ need not be independent. Useful observed-counterfactual consequences include

Let $Z=1$ denote gestation under unrestricted sugar and $Z=0$ gestation under rationing, and let $Y_i(z)$ be person $i$'s potential outcome for later Type 2 diabetes under exposure $z$. A sharp causal null hypothesis isagainst the alternative that the two potential outcomes differ for at least one person. An average-effect formulation instead tests $H_0:\mathbb{E}[Y(1)-Y(0)]=0$ against a nonzero, or scientifically directed positive, average effect.

Let $Y_s(1)$ and $Y_s(0)$ be the potential outcomes for the apprenticeship proportion at school $s$ if it is or is not converted to a UTC. The policy-relevant estimand is the average causal effectover the population of schools eligible for conversion. Ideally this would be identified by a randomized controlled trial of conversion, or by an observational design that reproduces its exchangeability.

For treatment history ${\bar{A}}_t$, observed history $H_t$, and final potential outcome $Y(\bar{a})$, sequential exchangeability requiresat every treatment time. Together with consistency of potential outcomes and positivity in causal inference, it identifies longitudinal effects by G-computation.