How Causal Inference Works | From Counterfactual Questions and Causal Assumptions to Randomisation, Adjustment, Target Trials, Sensitivity and Defensible Effects

Causal inference works by defining a counterfactual question about what would happen under different interventions, specifying the causal effect we want to estimate, designing or reconstructing a comparison that can identify that effect, declaring the assumptions that connect observed data to the unobserved counterfactuals, estimating the effect with methods appropriate to those assumptions, and testing how fragile the conclusion is to plausible bias, missingness, interference and model failure.

Two things can move together without one causing the other.

Students who attend more tuition may score higher.

People carrying umbrellas are more likely to be standing in rain.

Hospitals treating the sickest patients may have higher mortality.

A predictive algorithm can know who will struggle without telling us which intervention will help them.

Causal inference begins when the question changes from:

What is associated with the outcome?

to:

What would happen to the outcome if we intervened and changed something?

Quick Read

CAUSAL QUESTION → INTERVENTIONS → TARGET POPULATION → COUNTERFACTUAL OUTCOMES → CAUSAL ESTIMAND → DESIGN / TARGET TRIAL → IDENTIFICATION ASSUMPTIONS → EXCHANGEABILITY + POSITIVITY + CONSISTENCY → CONFOUNDING / SELECTION / MEASUREMENT CONTROL → ESTIMATION → UNCERTAINTY → SENSITIVITY → REPLICATION / TRIANGULATION → DECISION

Hernán and Robins make the central discipline explicit in Causal Inference: What If: causal questions and assumptions should be stated clearly, and causal inference cannot be reduced to a collection of statistical recipes. The 2025 TARGET reporting guideline extends this logic to observational studies emulating target trials, making the design, intervention, assignment, follow-up, outcome and analysis structure visible enough for readers to judge.

1. Causal Inference Begins With an Intervention Contrast

“Does tutoring cause higher scores?” is still vague.

What kind of tutoring?

How often?

Compared with what?

For which students?

Over what time?

A causal question needs sufficiently well-defined interventions and a comparison.

2. The Counterfactual Is the Outcome Under an Alternative Intervention

For one student, we observe the score under the teaching they actually received.

We do not simultaneously observe that same student’s score under the alternative teaching they did not receive.

The missing alternative is the counterfactual outcome.

See How Counterfactuals Work.

3. Individual Causal Effects Are Usually Fundamentally Unobservable

If one patient takes treatment, we see their treated outcome.

We cannot rewind the same world and observe the untreated outcome at the same moment.

Causal inference therefore moves from impossible individual comparisons to population contrasts identified through design and assumptions.

4. A Causal Estimand Defines the Population-Level Contrast

The average treatment effect compares average outcomes if everyone in the target population received treatment versus if everyone received the comparator.

Other estimands include:

• effect among the treated;
• effect among eligible participants;
• per-protocol effect;
• treatment-policy effect;
• controlled direct effect;
• effect under dynamic treatment strategies.

The estimand should be defined before choosing the regression model.

5. Association Is Not Causation Because Common Causes Can Create Both

Motivated students may be more likely to seek tutoring and more likely to study independently.

Motivation becomes a common cause of exposure and outcome.

The tutoring-score association therefore contains both treatment effect and background differences unless the design or adjustment separates them.

This is confounding.

6. Confounding Is a Causal Structure, Not Merely a Statistical Correlation

A variable is not a confounder merely because adding it changes a regression coefficient.

Its role depends on the causal relationships linking exposure, outcome and other variables.

See How Research Variables Work.

7. Randomisation Creates Exchangeability in Expectation

Random assignment makes treatment independent of baseline potential outcomes in expectation.

Treatment groups can therefore serve as counterfactual references for one another under the trial’s causal estimand and additional assumptions.

This is why randomised trials are such powerful causal designs.

8. Randomisation Does Not Solve Everything After Assignment

Participants can drop out.

Treatment adherence can differ.

Outcome measurement can be biased.

Post-randomisation variables can be conditioned on incorrectly.

Randomisation protects assignment; the rest of the causal route still needs design discipline.

9. Exchangeability Means the Comparison Groups Are Causally Comparable Conditional on the Design or Covariates

In observational data, treatment is not randomly assigned.

Conditional exchangeability assumes that after controlling a sufficient set of measured confounders, treatment assignment is independent of potential outcomes.

This is often called no unmeasured confounding.

It is powerful.

It is also generally untestable from the observed data alone.

10. Positivity Requires Relevant Treatment Options to Exist Across Covariate Strata

Suppose every extremely ill patient receives treatment and no extremely ill patient is untreated.

We have no untreated comparison in that region.

Positivity requires a non-zero probability of each intervention level for the covariate patterns where we want to estimate the effect.

Without overlap, causal estimation becomes extrapolation.

11. Consistency Connects Observed Outcomes to Well-Defined Interventions

If a student actually receives intervention A, consistency links their observed outcome to the counterfactual outcome under A.

This requires intervention versions to be sufficiently well specified.

“Tutoring” that ranges from one weekly worksheet session to intensive diagnostic teaching may violate a simple single-treatment interpretation.

Causal variables need operational identity.

12. Interference Challenges the Idea That One Person’s Treatment Affects Only Their Own Outcome

A vaccine changes transmission risk for other people.

A classroom intervention changes peer behaviour.

A traffic policy redirects congestion onto neighbouring roads.

When units interfere, ordinary potential-outcome notation needs extension.

The treatment of one unit can alter another unit’s counterfactual state.

13. Directed Acyclic Graphs Make Causal Assumptions Visible

A DAG represents assumed causal relationships as nodes and directed arrows.

The graph is not learned automatically from the data in ordinary applied use.

It encodes substantive assumptions about the data-generating process.

That explicitness is one of its greatest strengths.

14. DAGs Help Distinguish Confounders, Mediators and Colliders

Confounders may need adjustment.

Mediators may need to remain unadjusted when estimating total effects.

Colliders can create bias when conditioned upon.

These variables can all correlate with exposure and outcome.

The causal graph distinguishes their roles.

15. A Collider Is a Common Effect of Two Variables

Suppose ability and family support both influence admission to a selective programme.

Among admitted students, ability and family support can become negatively associated even if they were independent in the population.

Conditioning on the common effect opens a non-causal path.

Adjustment can create bias as well as remove it.

16. “Adjust for Everything” Is Not a Safe Causal Strategy

Adding every available variable to a regression can:

• adjust for mediators and block part of the causal effect;
• condition on colliders and open biasing paths;
• introduce measurement error;
• reduce precision;
• create positivity problems.

Covariate selection should follow causal structure, not availability alone.

17. The Backdoor Criterion Formalises Sufficient Adjustment in a DAG

A sufficient adjustment set blocks non-causal backdoor paths from exposure to outcome without blocking the causal path of interest or opening new biasing paths.

DAG software can help identify candidate adjustment sets once the causal graph is specified.

The software solves the graph.

It does not validate the graph’s scientific assumptions.

18. Regression Adjustment Can Estimate Causal Effects Under Identification Assumptions

If exchangeability holds conditional on measured covariates, positivity holds and the outcome model is correctly specified, regression can estimate adjusted causal contrasts.

The same regression equation can also be used purely descriptively or predictively.

Causal meaning comes from design and assumptions, not from the syntax of regression.

19. Standardisation Converts Conditional Predictions Into Population Effects

Fit an outcome model as a function of treatment and confounders.

Predict each person’s outcome under treatment A and treatment B.

Average the predicted outcomes across the target population.

The difference estimates a marginal causal contrast under the assumptions.

This is standardisation or the parametric g-formula in simple settings.

20. Inverse Probability Weighting Builds a Pseudo-Population

Estimate each participant’s probability of receiving their observed treatment given confounders.

Weight participants inversely by that probability.

The weighted pseudo-population aims to make treatment independent of measured baseline confounders.

The approach relies on correct treatment models, exchangeability and positivity.

21. Propensity Scores Compress Measured Treatment Predictors

The propensity score is the probability of treatment conditional on observed covariates.

It can be used for matching, stratification, weighting or covariate adjustment.

A good propensity model balances measured confounders.

It cannot balance confounders that were never measured.

22. Propensity Models Should Be Judged by Balance, Not Only Prediction Accuracy

A treatment model with excellent classification accuracy can produce poor overlap and inadequate covariate balance.

The causal job is not merely to predict who was treated.

It is to construct comparable treatment groups over measured causes.

23. Matching Trades Sample Coverage for Local Comparability

Matching pairs or groups treated and untreated units with similar covariate patterns or propensity scores.

Units without comparable counterparts may be discarded.

The resulting estimand can shift toward the region of common support.

Better local comparison may come with a narrower target population.

24. Doubly Robust Estimation Combines Outcome and Treatment Models

Augmented inverse-probability weighting and related estimators use both an outcome model and a treatment model.

Under suitable conditions, consistency can hold if one of those nuisance models is correctly specified.

The identification assumptions—especially exchangeability and positivity—still remain.

25. Targeted Learning Uses Flexible Prediction While Preserving a Causal Estimand

Methods such as targeted maximum likelihood estimation combine flexible nuisance-function estimation with a targeting step tied to a causal parameter.

Machine learning can help estimate complex relationships.

The causal estimand and identification assumptions still need to be specified first.

26. Cross-Fitting Reduces Overfitting Bias in Flexible Nuisance Estimation

Modern semiparametric causal estimators often split data, estimate nuisance functions on one part and evaluate estimating equations on another.

Cross-fitting rotates these roles across folds.

This helps combine machine learning with valid asymptotic inference under conditions.

27. Time-Varying Confounding Requires Special Care

A prior treatment can change a later health state.

That health state can influence the next treatment decision and future outcome.

Conventional regression adjustment for the time-varying confounder can block part of the treatment effect while also being needed to control confounding.

G-methods were developed for this structure.

28. Marginal Structural Models Use Time-Varying Weights

Inverse-probability weights can account for treatment histories and time-varying confounders affected by prior treatment.

The resulting marginal structural model estimates effects of treatment strategies under assumptions.

This is one example of why ordinary regression is not a universal causal adjustment recipe.

29. The Parametric G-Formula Can Simulate Longitudinal Interventions

Model the longitudinal outcome and covariate process.

Then simulate population trajectories under alternative treatment strategies.

The g-formula estimates the counterfactual outcome distribution under those interventions if the models and identification assumptions are adequate.

30. Instrumental Variables Use External Variation in Treatment

An instrument affects treatment but—under strong assumptions—affects the outcome only through treatment and is not confounded with the outcome.

Examples can include randomised encouragement, policy rules or natural variation.

Instrumental-variable estimates can identify a local causal effect for particular compliance types rather than a universal average effect.

31. Instrument Validity Is Usually Harder Than Instrument Strength

A strong association between instrument and treatment can be tested.

The exclusion restriction and absence of instrument-outcome confounding are largely causal assumptions.

A statistically strong instrument can still be causally invalid.

32. Regression Discontinuity Exploits a Treatment Threshold

A programme is assigned when a score crosses a cutoff.

Units just above and just below the threshold may be comparable except for treatment eligibility.

Under continuity and no-manipulation assumptions, the discontinuity in outcomes can identify a local causal effect near the threshold.

The effect is local by design.

33. Difference-in-Differences Uses Changes Over Time Between Groups

One region adopts a policy.

Another does not.

Difference-in-differences compares the before-after change in the treated group with the before-after change in the comparison group.

The key identifying assumption is a form of parallel counterfactual trends in the absence of treatment.

Modern staggered-adoption settings require care because simple two-way fixed-effects estimators can behave badly under heterogeneous effects.

34. Interrupted Time Series Uses the Pre-Intervention Trend as a Counterfactual Model

Repeated outcomes are observed before and after a policy or event.

The pre-intervention trajectory helps predict what might have happened without the intervention.

Concurrent shocks, seasonality and changing trends threaten causal interpretation.

Time itself is not a control group.

35. Synthetic Control Builds a Weighted Comparison Unit

When one country, city or organisation receives an intervention, a weighted combination of untreated units can be constructed to match the treated unit’s pre-intervention trajectory.

Post-intervention divergence is then interpreted causally under assumptions about unmeasured shocks and comparability.

The counterfactual is engineered from other units rather than directly observed.

36. Natural Experiments Are Not Automatically Random Experiments

A policy change, lottery, boundary or administrative rule can create treatment variation that resembles random assignment.

The causal credibility depends on why the assignment mechanism can reasonably be treated as exogenous.

“Natural experiment” is a design claim that requires evidence, not a prestige label.

37. Target Trial Emulation Starts by Writing the Trial You Wish You Had

When randomisation is impossible, observational causal studies can begin by specifying the hypothetical randomised trial that would answer the question.

Key elements include:

• eligibility criteria;
• treatment strategies;
• assignment procedures;
• time zero;
• follow-up;
• outcome;
• causal contrast;
• analysis plan.

The target trial makes design errors visible before modelling begins.

38. Time Zero Must Align Eligibility, Treatment Assignment and Follow-Up

A common observational error defines treatment using future information while starting follow-up earlier.

This can create immortal-time bias: participants must survive long enough to qualify as treated.

Target-trial thinking aligns eligibility, treatment classification and start of follow-up at a common time zero.

39. Immortal-Time Bias Can Create Treatment Benefit From Calendar Structure Alone

Suppose treated patients are defined as those who receive a drug within 30 days after diagnosis.

Anyone who dies on day 5 can never enter the treated group.

The treated group is guaranteed to survive long enough to receive treatment.

That guaranteed survival can masquerade as treatment effectiveness.

40. The 2025 TARGET Statement Makes Target-Trial Reporting Inspectable

The TARGET guideline was developed to improve reporting of observational studies explicitly emulating target trials.

Its purpose is not to certify causal validity.

It helps readers see the design and analysis choices needed to judge validity and usefulness.

Transparent design is a prerequisite for causal criticism.

41. Selection Bias Can Arise From Conditioning on Study Participation or Follow-Up

If participation is influenced by both exposure and causes of the outcome, conditioning on participants can open a collider path.

Loss to follow-up can create similar selection.

Causal inference must model not only treatment assignment but also who remains observable.

42. Missing Data Can Become Causal Selection Bias

Missing Data explains how unobserved values arise and how methods use assumptions to recover estimands.

In causal work, missing outcomes or confounders can destroy exchangeability or reduce identifiability.

Inverse-probability-of-censoring weighting and multiple imputation are two possible tools under different assumptions.

43. Measurement Error Can Bias Both Exposure and Outcome Effects

Misclassified treatment can mix intervention groups.

Noisy confounder measurement can leave residual confounding.

Outcome measurement influenced by treatment knowledge can create detection bias.

Causal inference requires a measurement model as much as a treatment model.

44. Blinding Protects Causal Evidence After Assignment

Blinding can prevent treatment knowledge from altering co-interventions, outcome assessment or analysis.

Randomisation controls baseline assignment bias.

Blinding controls post-assignment information pathways.

Causal validity is protected across stages.

45. Mediation Asks Through Which Path the Effect Operates

A tutoring programme may improve scores partly by increasing practice time.

Practice time becomes a mediator.

Estimating direct and indirect effects requires additional assumptions about mediator-outcome confounding and intervention definitions.

Mediation is more demanding than simply adding the mediator to a regression.

46. Conditioning on a Mediator Changes the Causal Estimand

If the goal is the total treatment effect, controlling for a mediator blocks part of the effect pathway.

The resulting coefficient does not estimate the same causal quantity.

Adjustment decisions should follow the estimand, not habit.

47. Effect Modification Is About Causal Heterogeneity, Not Merely Subgroup Significance

Treatment may help beginners more than experts.

The causal effect therefore varies by baseline skill.

Subgroup analysis should estimate differences in effects directly and manage multiplicity rather than comparing separate significance labels.

48. Transportability Asks Whether a Causal Effect Travels to a New Population

A trial in specialist schools estimates a valid local effect.

Will it work in ordinary schools?

If effect modifiers differ across populations, the average effect can change.

Generalisation and transport require assumptions about how causal response varies across settings.

49. Sensitivity Analysis Measures How Much Hidden Bias Would Be Needed to Change the Conclusion

No observational study can prove the absence of unmeasured confounding.

Sensitivity analysis asks what strength and structure of hidden confounding could explain away the observed effect.

This converts an unverifiable assumption into a robustness calculation.

50. Negative Controls Can Reveal Hidden Bias Pathways

A negative-control outcome should not plausibly be caused by the treatment.

A negative-control exposure should not plausibly cause the outcome.

If an association appears where no causal effect should exist, residual confounding, measurement or selection bias may be operating.

Negative controls diagnose pathways; they do not automatically quantify all bias.

51. Placebo Tests Are Design-Specific Negative Controls

A difference-in-differences study can examine pre-treatment periods where no effect should yet appear.

A regression discontinuity study can test for discontinuities in baseline covariates at the cutoff.

These tests probe identifying assumptions indirectly.

52. Falsification Tests Strengthen Causal Arguments by Looking for What Should Not Happen

A causal model makes implications beyond the main effect estimate.

If those implications fail, confidence in the causal story should fall.

Causal inference is stronger when it risks being wrong in multiple observable ways.

53. Triangulation Uses Different Bias Structures to Test the Same Causal Question

A randomised trial has one set of limitations.

An instrumental-variable study has another.

A natural experiment another.

If methods with different plausible biases converge on a similar causal effect, the combined case can be stronger than repetition of one design alone.

54. Replication Across Settings Tests Causal Stability

An effect observed in one country, school system or clinical setting may depend on local implementation and baseline risk.

Replication reveals whether the causal mechanism travels.

External validity is an empirical programme, not a footnote.

55. Prediction and Causation Answer Different Action Questions

Low attendance may predict low exam scores.

Forcing attendance may or may not improve scores if attendance is only a marker of motivation or illness.

Predictive importance does not imply intervention value.

Causal inference asks which variable changes outcomes when manipulated, not merely which variable forecasts them.

56. Machine Learning Can Estimate Nuisance Functions Without Identifying the Causal Effect

Flexible algorithms can model treatment probabilities and outcomes.

They can reduce model misspecification.

They cannot create exchangeability if important confounders were never measured.

Prediction power cannot replace causal identification.

57. Causal Discovery Algorithms Need Strong Assumptions

Algorithms can search for graph structures compatible with conditional independence patterns.

Their causal interpretation depends on assumptions such as causal sufficiency, faithfulness, acyclicity and measurement quality.

Data can constrain causal possibilities.

They rarely identify the entire causal world without assumptions.

58. Causal Inference in Education Requires Defining the Treatment as Teaching, Not a Label

“Tuition” is not one intervention.

Class size.

Teacher skill.

Diagnostic intensity.

Curriculum.

Practice design.

Feedback.

Duration.

All can vary.

Causal education research needs enough treatment identity to say what intervention is actually being estimated.

59. Causal Inference in Policy Must Respect Spillovers

A school policy changes student sorting.

A road toll changes nearby traffic.

A tax changes prices and substitution.

Interventions can alter the environment around untreated units.

Policy causal effects often require system-level outcomes, not isolated-unit assumptions.

60. The Hostile Test: Regression Coefficient Mistaken for Causation

Tutoring attendance predicts higher scores after adjusting for age and sex.

Prior attainment and motivation are unmeasured.

The coefficient is significant.

The causal effect is not identified merely because a multivariable model was fitted.

61. The Second Hostile Test: Adjusting for a Collider

Ability and family support both influence entry into a selective school.

The study restricts analysis to admitted students.

Within that selected group, ability and family support become associated.

Conditioning created a biasing path that did not exist in the population.

62. The Third Hostile Test: Immortal Time Creates a Miracle Treatment

Patients are classified as treated if they receive therapy within 60 days.

Those who die before day 60 can never enter the treated group.

The treatment group receives guaranteed survival time by definition.

A causal effect is manufactured by timeline misalignment.

63. The Fourth Hostile Test: No Positivity, Huge Weights

Very high-risk patients almost always receive treatment.

A few untreated high-risk patients receive enormous inverse-probability weights.

The estimate becomes unstable and highly model-dependent.

No statistical method can manufacture robust overlap where treatment options essentially never coexist.

64. The Fifth Hostile Test: Predictive Feature Treated as Intervention Target

An algorithm predicts poor grades from frequent help-seeking.

A school tries to reduce help-seeking to improve grades.

Help-seeking was a marker of difficulty, not its cause.

Prediction identified a signal.

Causal reasoning was needed before intervention.

65. Primary School: Causation Begins as “What Did We Change?”

Two plants differ in height.

One received more sunlight.

It also received more water and started taller.

Students learn that observing a difference is not enough to know what caused it.

To learn what caused the change, make the comparison fair enough that the changed factor can carry the explanation.

66. Secondary School: Separate Correlation, Confounding and Intervention

Students can ask three questions:

1. Do the variables move together?
2. Could another variable cause both?
3. What would happen if we actually intervened on the exposure?

This creates the bridge from association to causal thinking.

67. JC and University: Causal Inference Becomes Identification Before Estimation

At higher levels, learners should reconstruct:

• causal question;
• intervention strategies;
• target population;
• counterfactual outcomes;
• causal estimand;
• time zero;
• exchangeability;
• positivity;
• consistency;
• interference;
• DAG and adjustment set;
• selection and missingness;
• estimation method;
• sensitivity analysis;
• transportability.

The central discipline is simple:

identify first, estimate second.

68. Where Causal Inference Fits in the eduKateSG “How Works” Landscape

• How Counterfactuals Work — the missing alternative outcomes underneath causal effects.
• How Randomisation Works — experimental assignment that creates causal exchangeability.
• How Research Variables Work — confounders, mediators, moderators and colliders.
• How Research Bias Works — confounding, selection and measurement distortions.
• How Statistical Inference Works — the wider estimation and uncertainty machinery.
• How Missing Data Works — post-selection and unseen-value assumptions.
• How Research Validity Works — whether causal interpretation is internally and externally defensible.

Causal Inference owns one precise canonical job: explain how data, design and declared causal assumptions can identify and estimate the consequences of interventions rather than merely describe associations.

69. What This Article Does Not Claim

• Correlation or prediction does not automatically identify a causal effect.
• Regression adjustment is not a universal causal method.
• Randomisation protects treatment assignment but does not solve every post-assignment bias.
• No-unmeasured-confounding assumptions are generally not provable from observed data alone.
• Adjusting for every available variable can create collider bias or block mediating pathways.
• Propensity scores balance measured variables, not unmeasured confounders.
• Machine learning can improve nuisance estimation but cannot manufacture causal identification.
• Natural experiments require justification of their assignment mechanism.
• Target trial emulation improves design discipline but does not automatically make observational evidence equivalent to a randomised trial.
• Causal effects can vary across populations, treatment versions and interference structures.

70. A Compact Causal-Inference Audit

1. What intervention question is being asked?
2. What treatment strategies are sufficiently well defined?
3. What comparator is relevant?
4. What target population?
5. What outcome and time horizon?
6. What causal estimand?
7. What would the ideal target trial look like?
8. What is time zero?
9. How is treatment assigned?
10. Is exchangeability created by randomisation or assumed conditional on measured covariates?
11. What confounders are required for adjustment?
12. How were they selected?
13. Is a DAG available?
14. Could any adjusted variable be a mediator or collider?
15. Is positivity plausible?
16. Do treatment groups overlap across covariate patterns?
17. Is consistency plausible for the treatment definition?
18. Are multiple versions of treatment hidden inside one label?
19. Is interference plausible?
20. How are missing outcomes and censoring handled?
21. Could measurement error affect exposure, confounders or outcome?
22. What estimation method is used?
23. Does it match the identification strategy?
24. Are weights stable if weighting is used?
25. Are covariates balanced after matching or weighting?
26. Are time-varying confounders affected by prior treatment?
27. Is target-trial emulation needed?
28. What sensitivity analysis addresses unmeasured confounding?
29. Are negative controls or falsification tests available?
30. Does the effect transport to the intended population?
31. What independent design could triangulate the result?

71. Frequently Asked Questions

What is causal inference?

Causal inference is the process of estimating how outcomes would differ under alternative interventions or exposure strategies using study design, observed data and explicit assumptions that connect those data to unobserved counterfactual outcomes.

Why is correlation not causation?

Two variables can be associated because one causes the other, because the causal direction is reversed, because a common cause influences both, because selection creates an association, or because of measurement and chance. Causal interpretation requires design and assumptions that distinguish these possibilities.

What are the main assumptions for causal inference from observational data?

Common assumptions include conditional exchangeability or no unmeasured confounding, positivity or treatment overlap, consistency of well-defined interventions, appropriate handling of interference, valid measurement and correct treatment of selection and missing data.

What is a DAG?

A directed acyclic graph is a diagram of assumed causal relationships among variables. It can help identify confounding paths, mediators and colliders and therefore clarify which variables should or should not be adjusted for.

What is target trial emulation?

Target trial emulation begins by specifying the hypothetical randomised trial that would answer the causal question, then structures observational data to emulate its eligibility, treatment strategies, time zero, follow-up, outcomes, causal contrast and analysis as closely as possible.

72. Authoritative Research Corridor

• Hernán and Robins — Causal Inference: What If
• BMJ — Target Trial Emulation: Applying Principles of Randomised Trials to Observational Studies
• BMJ 2025 — TARGET Statement for Reporting Observational Studies Emulating a Target Trial
• International Journal of Epidemiology — Use of DAGs to Identify Confounders in Applied Health Research
• eduKateSG — How Counterfactuals Work

Final Thought: Causal Inference Is About the World We Did Not Get to Observe

Data show what happened.

Causal questions ask what would have happened otherwise.

That alternative world is missing.

Randomisation can make another group stand in for it.

Observational designs try to reconstruct it through covariates, timelines, natural variation and assumptions.

The methods can be mathematically sophisticated.

The governing discipline remains simple.

State the intervention.

State the counterfactual.

State the assumptions.

Design the comparison so those assumptions are as credible as possible.

Then test how much the answer changes when reality pushes back.

Causal inference does not make the unobserved world visible. It builds the most defensible bridge we can between the world we observed and the world our decision needs to imagine.