Introduction to Causal Inference: Why Correlation Is Not Enough and What Actually Establishes Causation

Everyone knows "correlation doesn't imply causation." Far fewer people can explain precisely why. There are exactly three mechanisms that generate a statistical association between X and Y without X actually causing Y. Understanding all three is the foundation of causal inference. First, confounding. A third variable Z causes both X and Y, creating a spurious association between them. Classic example: ice cream sales and drowning deaths are positively correlated. Ice cream doesn't cause drowning. Hot weather (the confounder) increases both ice cream consumption and swimming, which increases drowning risk. In the data, X and Y move together — but only because Z is pulling both strings. Roughly 70-80% of causal inference problems you'll encounter in coursework involve confounding. Second, reverse causation. Y actually causes X, not the other way around. Countries with more hospitals have higher death rates. Do hospitals cause death? No — countries build more hospitals because they have sicker populations. The arrow points the other direction. Cross-sectional data (one snapshot in time) often can't distinguish X→Y from Y→X. Longitudinal data (repeated measurements over time) helps, but even temporal ordering isn't definitive proof of causation. Third, collider bias (also called Berkson's paradox or selection bias). This one's more subtle. A collider is a variable that is caused by both X and Y. If you condition on (control for, stratify by, or select based on) the collider, you create a spurious association between X and Y even when none exists. Example: among hospitalized patients, there appears to be a negative association between flu and broken legs. Not because flu protects against fractures — but because a patient had to have one or the other (or both) to be hospitalized. Hospitalization is the collider. By restricting to hospitalized patients, you've induced an artificial relationship. Collider bias trips up even experienced researchers because controlling for more variables feels like it should always make results more accurate — but controlling for a collider makes things worse. These three mechanisms are exhaustive. If X and Y are correlated but X doesn't cause Y, one (or more) of these three things is happening. Causal inference methods exist to rule out or account for all three.

To reason rigorously about causation, you need a formal definition. The potential outcomes framework (also called the Rubin causal model, after Donald Rubin) provides one. The idea: for any individual, there are two potential outcomes. Y(1) is the outcome if they receive the treatment. Y(0) is the outcome if they don't. The individual causal effect is Y(1) - Y(0). For a patient considering surgery: Y(1) is their health if they get surgery, Y(0) is their health if they don't. The causal effect of surgery for that patient is the difference. Here's the fundamental problem of causal inference: you can never observe both potential outcomes for the same individual. A patient either gets surgery or doesn't. You see Y(1) or Y(0), never both. The unobserved potential outcome is called the counterfactual — what would have happened under the alternative scenario. Causal inference is fundamentally about estimating something you cannot directly observe. Since individual causal effects are unobservable, we focus on the Average Treatment Effect (ATE): E[Y(1) - Y(0)] across the population. In a randomized experiment, random assignment ensures that the treatment and control groups are comparable on average — so the difference in group means estimates the ATE. This works because randomization makes treatment assignment independent of the potential outcomes. The treated group's average Y(1) is a valid estimate of what the whole population's Y(1) would be, and similarly for control. In observational data, treatment isn't randomly assigned. People who choose surgery may be healthier (or sicker) than those who don't. The treatment and control groups differ in ways that affect the outcome, so the simple difference in means conflates the treatment effect with pre-existing differences. Every observational causal inference method is trying to recreate the conditions of a randomized experiment — making treated and untreated groups comparable — using assumptions and statistical adjustments instead of actual randomization. A key assumption for most methods: the Stable Unit Treatment Value Assumption (SUTVA). This requires that one person's treatment doesn't affect another person's outcome (no interference) and that there's only one version of each treatment level. Vaccination studies violate SUTVA because your vaccination affects your neighbor's health through herd immunity. When SUTVA fails, the potential outcomes framework needs extension.

Directed Acyclic Graphs (DAGs) are the visual language of causal inference. A DAG is a diagram where nodes represent variables and arrows represent direct causal effects. "Directed" means the arrows point in one direction (from cause to effect). "Acyclic" means there are no loops — you can't follow the arrows in a circle back to where you started. DAGs aren't just pretty pictures. They encode testable assumptions about the causal structure, and they tell you exactly which variables to control for (and which to leave alone) to identify a causal effect. This matters because thoughtlessly throwing every available variable into a regression model — something researchers do constantly — can introduce bias rather than remove it. Three building blocks of DAGs. A fork: Z → X and Z → Y. Z is a common cause (confounder). X and Y are correlated because of Z. Controlling for Z removes the confounding and isolates the causal path from X to Y (if one exists). A chain: X → M → Y. M is a mediator. X causes M, which causes Y. Controlling for M blocks the causal path from X to Y. If you want the total effect of X on Y, do NOT control for M. If you want the direct effect (not through M), then control for M. A collider: X → C ← Y. C is caused by both X and Y. X and Y are NOT associated unless you condition on C. If you do condition on C, you create a spurious association. Do NOT control for colliders. The practical rule: control for confounders (forks), don't control for mediators (unless you want direct effects), and never control for colliders. DAGs make these decisions visual and systematic. Example: You want to estimate the effect of education (X) on income (Y). Parents' socioeconomic status (Z) affects both education and income — it's a confounder (fork). You should control for it. Job type (M) is caused by education and causes income — it's a mediator (chain). If you want the total effect of education on income, don't control for it. If you control for job type, you only see the effect of education that operates through channels other than job placement. College selectivity (C) is caused by both education effort and family wealth (which also affects income) — depending on the DAG structure, controlling for it might open a collider path. Drawing the DAG forces you to state your assumptions explicitly. Two researchers can disagree about the DAG (is Z a confounder or a mediator?) and have a productive argument about the causal structure rather than blindly running regressions.

When randomization isn't possible (which is most of the time outside clinical trials), four quasi-experimental methods let researchers make credible causal claims from observational data. Each exploits a different source of variation to approximate random assignment. Randomized Controlled Trials (RCTs) remain the gold standard. Randomly assign subjects to treatment vs. control, measure outcomes, compare. Randomization ensures that all confounders — measured and unmeasured — are balanced on average across groups. The simple difference in means is an unbiased estimate of the causal effect. RCTs aren't always feasible (you can't randomly assign smoking, poverty, or education), ethical (you can't withhold a known effective treatment), or practical (they're expensive and time-consuming). That's where the next three methods come in. Difference-in-Differences (DiD) compares the change in outcomes over time between a group that received treatment and a group that didn't. The key assumption is "parallel trends": absent the treatment, both groups would have followed the same trajectory. Example: a state raises the minimum wage on January 1. You compare the employment change in that state (before vs. after) to the employment change in a neighboring state that didn't raise the wage. If both states were trending similarly before the policy, the difference in their changes estimates the causal effect. DiD is powerful because it controls for all time-invariant confounders (geography, culture, demographics that don't change) and all common time trends (national economic shifts). It fails when the parallel trends assumption is violated — if the treatment state was already on a different trajectory before the policy. Instrumental Variables (IV) use a third variable (the instrument) that affects the treatment but has no direct effect on the outcome except through the treatment. Example: distance to the nearest college affects whether someone attends college (the treatment) but arguably doesn't directly affect future earnings (the outcome) except through its effect on college attendance. If the instrument is valid, comparing outcomes across values of the instrument reveals the causal effect of the treatment. IV requires two assumptions: relevance (the instrument actually affects treatment — testable) and exclusion (the instrument only affects the outcome through the treatment — not directly testable and often debatable). Weak instruments (small effect on treatment) produce unreliable estimates with enormous standard errors. Regression Discontinuity (RD) exploits a threshold rule. If treatment is assigned based on whether a continuous variable crosses a cutoff — students scoring above 70 get a scholarship, patients with blood pressure above 140 get medication — then individuals just above and just below the cutoff are nearly identical except for their treatment status. Comparing outcomes in this narrow band around the cutoff estimates the causal effect of treatment at the cutoff. RD is one of the most credible quasi-experimental designs because the assumption (people just above and below the threshold are comparable) is often very plausible. The limitation: it only estimates the effect at the cutoff, not for the entire population. StatsIQ helps you build intuition for these methods with practice problems that present research scenarios and ask you to identify which causal inference method applies, state the required assumptions, and evaluate whether the assumptions are plausible.