Causal analysis (causal inference) is the set of methods researchers use to move from “these two variables are associated” to “changing this variable would change that outcome.” It is a different, harder question than the one most statistical tests answer. A correlation coefficient or a regression p-value describes a pattern in the data you have; a causal claim is a statement about data you do not have — what would have happened to the same units under a different exposure. That gap is why correlation and causation are not interchangeable, and why the methods on this page exist: they are the disciplined ways researchers try to close that gap, or at least state honestly how far they got.
This guide assumes you already know why correlation alone does not establish causation — see Correlation vs. Causation for that argument, and Correlation Coefficient for how association is actually measured (Pearson vs. Spearman). What follows is the applied layer above that: the frameworks, designs, and reporting discipline that let a study support — or fail to support — a causal claim.
The counterfactual question
Causal inference reframes every research question as a comparison between two possible worlds for the same units: the world where they received the exposure or intervention, and the world where they did not. The causal effect is the difference between those two worlds. This is the counterfactual framing, and it is what separates “is X associated with Y” from “does X cause Y”: association asks whether two things move together across the units you observed; causation asks what would have happened to those same units had their exposure been different.
The practical difficulty is immediate: for any single unit — a patient, a lab, a grant applicant — you can only ever observe one of the two worlds. A patient either receives the drug or does not; you never see the same patient, at the same moment, both treated and untreated. Every method described below is a strategy for approximating the missing world, either by comparing different units who plausibly stand in for each other (a control group), or by using a design or statistical adjustment that makes the comparison defensible despite that missing data.
The potential outcomes framework (the Rubin causal model)
The formal language for the counterfactual comparison is the potential outcomes framework, associated with Donald Rubin’s work on causal inference. Each unit is assigned two potential outcomes: Y(1), the outcome that would occur if the unit received the treatment, and Y(0), the outcome that would occur if it did not. The individual causal effect for that unit is Y(1) − Y(0).
The framework gives a name to the difficulty just described: the fundamental problem of causal inference is that for any given unit, only one of Y(1) or Y(0) is ever observed — the other is, by definition, counterfactual. Causal inference is therefore never a matter of measuring an individual effect directly; it is a matter of estimating an average effect across a population, using groups that are comparable enough that the unobserved potential outcome of one group can stand in for the unobserved potential outcome of the other.
Two population-level quantities come up constantly in causal-inference reporting, and they are not interchangeable:
- ATE (Average Treatment Effect) — the average of Y(1) − Y(0) across the entire population of interest, including units that were never actually treated. This is the effect a randomized trial with full compliance and no dropout estimates.
- ATT (Average Treatment Effect on the Treated) — the average effect specifically among units that actually received the treatment. In observational data, where treatment is not randomly assigned, ATT is often the quantity that is actually identifiable, and it can differ meaningfully from the ATE if the people who select into treatment would have benefited differently from it than the population at large.
A results section that reports “the effect of X” without specifying which estimand it means — ATE, ATT, or something else (ATC, local average treatment effect, etc.) — is under-specified. Naming the estimand is part of pre-specifying the causal question, discussed further below.
The Bradford Hill viewpoints
Before potential outcomes and DAGs were formalized, epidemiologist Austin Bradford Hill proposed a widely used framework for judging whether an observed association is plausibly causal, in his 1965 address to the Royal Society of Medicine, “The Environment and Disease: Association or Causation?” The nine viewpoints are: strength of association, consistency across studies and populations, specificity of the association, temporality (cause must precede effect), biological gradient (a dose-response relationship), plausibility (a credible mechanism), coherence with existing knowledge, experiment (does intervening change the outcome), and analogy to established causal relationships.
The important caveat, and one Hill himself was explicit about: he presented these as viewpoints to structure judgment, not as a checklist where satisfying a threshold number confirms causation. Several of them are neither necessary nor sufficient on their own — specificity fails for exposures with multiple effects (smoking causes several diseases, not one), and temporality is the only one of the nine that is genuinely non-negotiable. Treating the Bradford Hill viewpoints as a scorecard to tally is a common misuse; treating them as a structured prompt for weighing an observational association — alongside the design-based and DAG-based tools below — is the use Hill intended.
DAGs: making causal assumptions explicit
A directed acyclic graph (DAG) is a diagram of assumed causal relationships between variables, drawn as arrows from cause to effect, with no cycles (a variable cannot cause itself through a chain of arrows). DAGs, formalized in the causal-inference literature associated with Judea Pearl, are a tool for making explicit — and therefore checkable — the causal assumptions that any analysis is implicitly relying on. Once a DAG is drawn, it tells you which variables belong in an adjustment set and which do not. Getting this wrong in either direction is one of the most common, and most consequential, errors in applied causal analysis. There are three variable roles to distinguish:
- Confounders — a variable that causally influences both the exposure and the outcome, creating a spurious or distorted association between them if left unadjusted. Example: in an observational study of exercise and heart disease, age influences both how much someone exercises and their baseline cardiovascular risk. Age is a confounder. A DAG shows it as a variable with arrows pointing into both exposure and outcome. Confounders should be adjusted for (via study design, matching, or statistical control) — failing to do so leaves the association biased.
- Colliders — a variable that is causally influenced by both the exposure and the outcome (or by two variables of interest), rather than influencing them. A DAG shows a collider as a variable with two arrows pointing into it. The critical, counter-intuitive rule: conditioning on (adjusting for, stratifying by, or selecting a sample based on) a collider creates a spurious association between the two variables that cause it, even if no real relationship exists. A classic illustrative example: if hospitalization is caused independently by both a genetic risk factor and an unrelated environmental exposure, restricting a study sample to hospitalized patients only (conditioning on hospitalization, a collider) can produce an apparent association between the risk factor and the exposure among that sample, even though the two are unrelated in the general population. This pattern is sometimes called selection bias or collider-stratification bias, and it is a direct consequence of conditioning on the wrong node in the causal structure.
- Mediators — a variable that lies on the causal pathway between the exposure and the outcome, causally downstream of the exposure and causally upstream of the outcome. Example: in a study of a smoking-cessation program’s effect on lung function, smoking status itself is a mediator between program participation and the outcome. Adjusting for a mediator blocks part or all of the very causal pathway the study is trying to estimate, biasing the effect estimate toward zero (or, if the mediator is also a confounder of a downstream step, in a less predictable direction). Mediators should generally be left out of the adjustment set for a total-effect estimate, and analyzed separately (via formal mediation analysis) only if the question is specifically about the mechanism.
The practical discipline a DAG enforces is this: draw the assumed causal structure before choosing an adjustment set, using subject-matter knowledge, not statistical significance, to decide which arrows exist. A variable’s p-value or its correlation with the outcome says nothing about whether it is a confounder, a collider, or a mediator — only the assumed causal structure does, which is exactly why that structure needs to be stated, not left implicit.
Study designs, ordered by causal strength
Different study designs support causal claims to very different degrees, largely because of how much of the counterfactual problem they solve through design rather than after-the-fact adjustment.
Randomized controlled trials (RCTs)
Random assignment to a control group or treatment group is the strongest available design for causal inference, because randomization makes treatment assignment independent of both measured and unmeasured characteristics of the units, on average. With a large enough sample, randomization balances confounders — known and unknown — across arms, which is precisely what observational designs cannot guarantee. This is why an RCT can estimate the ATE directly from the difference in observed group means, without needing to enumerate every confounder in advance.
Quasi-experimental designs
When randomization is not possible or ethical, quasi-experimental designs try to approximate it by exploiting some naturally occurring source of as-if-random variation in exposure:
- Difference-in-differences (DiD) compares the change over time in an outcome between a group exposed to an intervention and a group that was not, under the assumption that both groups would have followed parallel trends absent the intervention. Widely used to evaluate policy changes that affect one jurisdiction or population but not a comparable other one.
- Regression discontinuity (RD) exploits a sharp, arbitrary threshold that determines treatment assignment (an eligibility cutoff, a funding-score threshold). Units just above and just below the cutoff are assumed comparable in every other respect, so the discontinuity in outcomes right at the threshold is attributed to the treatment.
- Instrumental variables (IV) use a third variable (the instrument) that affects the exposure but has no direct effect on the outcome except through the exposure, to isolate variation in the exposure that is plausibly free of confounding. Finding a genuinely valid instrument — one with no direct pathway to the outcome — is the hard part and the usual point of methodological attack.
- Interrupted time series (ITS) analyzes a single population’s outcome trend before and after an intervention, testing for a change in level or slope at the intervention point, against the counterfactual of the pre-existing trend continuing unchanged.
- Synthetic control constructs a weighted composite of untreated units that closely tracks the treated unit’s pre-intervention trajectory, then uses that synthetic composite as the counterfactual for the post-intervention period. Common in policy evaluation with a single treated unit (one state, one country) and many potential comparators.
Observational designs with statistical adjustment
Where neither randomization nor a natural quasi-experimental source of variation is available, researchers adjust for measured confounders directly:
- Matching pairs treated and untreated units with similar values on measured confounders, so the comparison approximates a randomized one on those measured characteristics.
- Propensity scores collapse a set of measured confounders into a single estimated probability of receiving treatment, then match, stratify, or weight on that score — useful when there are too many confounders to match on directly.
- Standardization (direct or indirect) reweights outcome rates to a common reference population’s confounder distribution, so treated and untreated groups are compared as if they had the same confounder mix.
- Inverse probability weighting (IPW) weights each unit by the inverse of its estimated probability of receiving the exposure it actually received, creating a pseudo-population in which exposure is no longer associated with the measured confounders.
All four of these methods share the same hard limitation: they can only adjust for confounders that were actually measured. None of them can address unmeasured confounding, which is why sensitivity analysis (below) exists as a separate, necessary step.
Why regression adjustment alone is not causal inference
It is common to see a regression model with several covariates presented as if the coefficient on the exposure of interest is automatically a causal effect once “everything else is controlled for.” This is not automatically true, for two separable reasons already covered above: the model can omit a real confounder (leaving the exposure coefficient biased), or it can include a collider or mediator in the adjustment set (introducing bias that would not otherwise exist). A regression coefficient is only a causal effect if the model’s adjustment set matches what a correctly specified DAG says it should be — regression is a computational tool for estimating an effect once the identification strategy is sound, not a substitute for having one.
A related and well-documented reporting error is the Table 2 fallacy, a term from Westreich and Greenland’s 2013 paper in the American Journal of Epidemiology. It describes the practice of presenting every adjusted coefficient in a multivariable regression table — the exposure of interest alongside age, sex, and every other covariate — and implicitly inviting readers to interpret all of them as causal effects. In most models, the covariates were included specifically to adjust for confounding of the exposure-outcome relationship; their own coefficients are not estimates of their causal effect on the outcome, because the adjustment set appropriate for the exposure of interest is generally not the correct adjustment set for each covariate’s own effect. A single regression table can produce a valid causal estimate for one variable in it and a biased, non-causal number for every other variable in the same row.
Sensitivity analysis for unmeasured confounding
Because adjustment-based methods can only control for confounders that were measured, a responsible causal analysis reports how sensitive its conclusion is to a confounder that was not measured. The most widely used current tool for this is the E-value, introduced by VanderWeele and Ding (2017, Annals of Internal Medicine). The E-value is the minimum strength of association, on the risk-ratio scale, that an unmeasured confounder would need to have with both the exposure and the outcome — after accounting for the measured covariates — to fully explain away the observed association. A large E-value means an unmeasured confounder would have to be implausibly strongly associated with both exposure and outcome to overturn the result; a small E-value means a fairly weak, plausible unmeasured confounder could do so. Reporting an E-value alongside an adjusted effect estimate is increasingly expected practice in epidemiology and health-services research specifically because it quantifies, rather than merely gestures at, the “there could be unmeasured confounding” caveat.
Mendelian randomization
Mendelian randomization is a specific application of the instrumental-variable approach that uses genetic variants as the instrument. Because genetic variants are assigned at conception, effectively at random with respect to most confounders that plague adult observational studies (as long as population stratification and other genetic-specific assumptions hold), a genetic variant reliably associated with an exposure of interest — and with no direct pathway to the outcome other than through that exposure — can be used to estimate the exposure’s causal effect on an outcome without needing to measure and adjust for the usual set of confounders. It is widely used in epidemiology to probe causal questions (for example, the causal role of a biomarker in disease risk) that would otherwise require an infeasible RCT, but it inherits the same core vulnerability as any instrumental-variable design: the result is only as valid as the assumption that the genetic instrument affects the outcome solely through the exposure being studied (no pleiotropy), which is a substantive, checkable-but-not-provable assumption rather than a guarantee.
Reporting and integrity: pre-specification and causal-language discipline
Two practices separate a credible causal analysis from an overreaching one, and both are squarely within CASRAI’s research-integrity remit:
- Pre-specify the causal question and the adjustment set before seeing the results. The causal question (which estimand — ATE, ATT, or another), the assumed DAG, and the resulting adjustment set should be decided from subject-matter knowledge and stated before the analysis is run, ideally in a pre-registration or analysis plan. Choosing which covariates to adjust for after seeing which combination produces the preferred result is a form of the same specification-searching problem that p-value and multiple-comparison misuse describes in other contexts — the causal-inference version of p-hacking.
- Do not let causal language drift into the discussion section when the design does not support it. A very common and avoidable integrity lapse: a paper’s methods and results sections are appropriately careful (“X was associated with Y after adjustment for confounders”), and then the discussion or abstract slides into causal phrasing (“X reduces Y,” “X improves outcomes”) that the observational design never earned. Readers, reviewers, and downstream evidence users (including systematic reviewers and guideline panels) reasonably rely on a paper’s own language to signal what its design supports. Matching the strength of the claim to the strength of the design — consistently, across the abstract, results, and discussion, not just in one careful sentence buried in limitations — is a baseline expectation, not an optional courtesy.
Frequently asked questions
What is causal analysis in research?
Causal analysis is the set of methods used to determine whether, and by how much, changing one variable (an exposure or intervention) changes an outcome, as distinct from simply describing that the two are associated. It relies on the counterfactual comparison of what happened under the exposure versus what would have happened without it.
What is the difference between causal analysis and correlation?
Correlation measures whether two variables move together across the units observed; it says nothing about direction or mechanism, and can arise from confounding, reverse causation, or chance. Causal analysis asks the counterfactual question — would the outcome have differed had the exposure differed — and requires a design or set of assumptions strong enough to rule out those alternative explanations. See Correlation vs. Causation for the full comparison.
Can regression analysis prove causation?
Not on its own. A regression coefficient is a causal effect only if its adjustment set correctly reflects the causal structure of the problem — every real confounder included, and no colliders or mediators mistakenly included. Regression is a computational tool for estimating an effect once a valid identification strategy (a DAG, a natural experiment, randomization) is in place; it does not supply that strategy by itself.
What is the difference between ATE and ATT?
ATE (average treatment effect) is the average causal effect across the entire population of interest, including units never actually treated. ATT (average treatment effect on the treated) is the average effect specifically among units that received the treatment, which can differ from the ATE if treatment uptake is related to how much a unit would benefit.
Are the Bradford Hill criteria a checklist for proving causation?
No. Austin Bradford Hill presented his nine viewpoints (strength, consistency, specificity, temporality, biological gradient, plausibility, coherence, experiment, analogy) explicitly as considerations to structure judgment about an observed association, not as a scorecard where meeting a threshold number proves causation. Temporality is the only one that is strictly necessary; several others (specificity in particular) do not hold for exposures with multiple effects.
Why is conditioning on a collider a problem?
A collider is a variable causally influenced by both the exposure and the outcome of interest. Conditioning on it — by adjusting for it in a model, or by restricting a sample based on it — opens a spurious statistical association between the exposure and outcome that did not exist in the unconditioned population, even when there is no real causal relationship between them. This is the opposite of what adjusting for a genuine confounder does, which is why distinguishing the two using a DAG matters before choosing an adjustment set.
What is Mendelian randomization used for?
Mendelian randomization uses genetic variants as instrumental variables to estimate the causal effect of an exposure (often a biomarker or modifiable risk factor) on an outcome, exploiting the fact that genetic variants are assigned effectively at random with respect to most adult confounders. It is used when a randomized trial of the exposure would be infeasible or unethical, though its validity depends on the genetic instrument having no pathway to the outcome other than through the exposure being studied.
