| Part | Ch | Title |
|---|---|---|
| Part I: Asking Causal Questions | Ch 1 | From casual to causal |
| Ch 2 | The whole game: mosquito nets and malaria | |
| Ch 3 | Potential outcomes and counterfactuals | |
| Ch 4 | Expressing causal questions as DAGs | |
| Ch 5 | Causal inference is not (just) a statistical problem | |
| Ch 6 | From question to answer: stratification and outcome models | |
| Part II: The Design Phase | Ch 7 | Preparing data to answer causal questions |
| Ch 8 | Propensity scores | |
| Ch 9 | Evaluating your propensity score model | |
| Part III: Estimating Causal Effects | Ch 10 | Causal estimands |
| Ch 11 | Fitting the weighted outcome model | |
| Ch 12 | Continuous and categorical exposures | |
| Ch 13 | G-computation | |
| Ch 14 | Interaction | |
| Ch 15 | Missingness and measurement | |
| Ch 16 | Sensitivity analysis | |
| Ch 17 | Causal mediation analysis | |
| Ch 18 | Causal inference across time | |
| Ch 19 | Causal time-to-event models | |
| Ch 20 | Doubly robust models | |
| Ch 21 | Machine learning and causal inference | |
| Ch 22 | Instrumental variables and friends | |
| Ch 23 | Difference-in-difference | |
| Ch 24 | Evidence |
Causal Inference in R - Chapter Summaries
Chapter summaries
License and attribution
These summaries are a derivative work of Causal Inference in R by Malcolm Barrett, Lucy D’Agostino McGowan, and Travis Gerke, published at r-causal.org.
The original work is copyright the authors and licensed under CC BY-NC 4.0. This derivative is released under the same license.
In practice: credit the original authors when you share or adapt this material. Do not use it commercially. If you are unsure whether your use qualifies as non-commercial, read the CC BY-NC 4.0 deed.
The book has one central question: given data you did not design, can you make a credible causal claim? Not a predictive one. Not a correlational one. A causal one: what would happen if you intervened?
That framing rules a lot out. RCTs are not covered because they sidestep the hard parts. The whole point of the book is the harder, messier, more common situation: data collected by someone else, for reasons that may have nothing to do with your question, where the exposure was not assigned at random and you have to be explicit about every assumption you are making.
Prerequisites are light: tidyverse fluency, basic R modelling (lm(), glm()), and comfort writing functions. tidymodels appears later but no prior exposure is assumed.
Part I: Asking Causal Questions
Before any method makes sense, you need the framework. What is a causal effect, exactly? How do you write down your assumptions? Why does data alone never settle the causation question? Six chapters. They repay slow reading.
Ch 1: From casual to causal
Association vs. causation · causal questions · counterfactuals
Most statistical training is about association. This chapter argues that is the wrong frame for a large class of questions people actually care about. Knowing that X and Y move together tells you nothing about what happens when you change X.
The distinction the book draws between descriptive, predictive, and causal questions is not pedantic. It has real consequences. A predictive model optimised for accuracy will often mislead you if you try to use it causally. The sentence-diagram framework (does X cause Y, among population Z, compared to doing W, over horizon T) is worth internalising early. Every word in that sentence affects what you are estimating, and dropping one tends to make the question unanswerable rather than simpler.
Ch 2: The whole game
End-to-end example · confounding · IPW · DAGs
A complete causal analysis before any of the theory gets deep. The question is straightforward: do insecticide-treated mosquito nets reduce malaria risk?
The confounding problem is immediate. Wealthier, healthier households are more likely to use nets and less likely to get malaria, for reasons unrelated to nets. Naively comparing users to non-users overstates protection. The chapter walks through DAG construction, covariate identification, propensity scoring, and inverse probability weighting, none of it explained in full yet. The point is to see the whole pipeline once before studying each piece. Reading this chapter again after finishing the book is genuinely useful.
Ch 3: Potential outcomes and counterfactuals
Potential outcomes · exchangeability · positivity · consistency · SUTVA · target trial
The theoretical core. The central problem is that you can only ever observe one version of what happened. The counterfactual is permanently missing. Causal inference is, at root, a missing data problem.
The potential outcomes framework defines the individual causal effect as \(Y(1) - Y(0)\). Since only one is observed per person, individual effects are unidentifiable. The average treatment effect is what we can go after, but only under three conditions. Exchangeability: no unmeasured confounding, so treatment groups have the same potential outcomes on average. Positivity: every unit has a non-zero probability of receiving any exposure level, within all covariate strata. Consistency (SUTVA): the observed outcome equals the potential outcome for the received exposure, with no multiple treatment versions and no interference between units.
Randomisation satisfies all three in the limit. Observational data does not, which is why the rest of the book exists. The chapter closes with target trial emulation: write down the RCT you would run if you could, then map each protocol element to your observed data. It is a more disciplined organising framework than it first sounds.
Ch 4: Expressing causal questions as DAGs
DAGs · d-separation · confounding · colliders · mediators · ggdag
DAGs make assumptions explicit and auditable. A node per variable, a directed edge per causal relationship, no cycles. The graph does not claim to be the truth. It commits to your current best guess, which can then be examined and challenged by people who know the subject matter differently.
D-separation is the graphical rule for reading off conditional independencies, which translates directly to covariate selection: adjust for backdoor paths, do not adjust for mediators, and be very careful about colliders.
Colliders are the most counterintuitive part. Conditioning on a common effect of treatment and outcome (including it in a regression or restricting the sample on it) opens a spurious association that does not exist in the full population. A lot of analysts introduce bias while thinking they are tightening up the analysis. ggdag handles visualisation and d-separation queries in R.
Ch 5: Causal inference is not (just) a statistical problem
Domain knowledge · unmeasured confounding · assumptions · bias
The hardest chapter to act on, because it tells you something statistical training actively obscures: no method substitutes for knowing the subject.
The identifiability conditions from Chapter 3, especially exchangeability, cannot be verified from data. You can check balance, test functional form, run sensitivity analyses. None of that tells you whether you have adjusted for the right confounders. That is a question about the world. Two analysts with the same data but different domain knowledge will reach different conclusions, and both might be defensible.
More controls is not always safer. Conditioning on a collider is worse than not adjusting at all. Adjusting for a post-treatment variable introduces bias. Knowing which variables belong in a model and which do not is inseparable from understanding the subject matter.
Ch 6: From question to answer
Stratification · regression adjustment · g-computation · marginal standardisation
With the framework in place, two approaches to actually estimating an effect.
Stratification compares treatment and control within covariate levels. Transparent, easy to explain, and it collapses fast. Too many variables or any continuous covariates and you run out of observations per stratum.
Outcome modelling solves the dimensionality problem. Fit \(E[Y \mid X, Z]\), predict counterfactual outcomes for every unit under each exposure, then average the difference. This is g-computation, also called marginal standardisation. The key point is that the ATE is not just the coefficient on \(X\) in the outcome model. That coefficient is only the causal effect under specific functional form assumptions. The predict-and-average procedure is more general.
Part II: The Design Phase
Chapters 7-9 slow down on a step that is easy to skip: getting the data and propensity model right before touching the outcome. A propensity model with high predictive accuracy can still leave substantial confounding, and you will not catch that from AUC alone.
Ch 7: Preparing data to answer causal questions
Data preparation · covariate selection · eligibility criteria · temporal ordering
Before fitting anything: who is included, what the exposure measures, what the baseline period is, and which covariates are needed for conditional exchangeability. The DAG does the work here. Covariate selection driven by stepwise procedures or variable importance is unreliable for causal inference. You need variables that block backdoor paths, not variables that predict the outcome well. Related, but different criteria.
Temporal ordering is often overlooked. A covariate measured after the exposure started cannot be a confounder. Conditioning on it either introduces bias or blocks a mediation path. Getting this wrong is common and hard to detect from the data alone.
Ch 8: Propensity scores
Propensity scores · IPW · tidymodels · overlap · weighting
The propensity score \(e(Z) = P(\text{treatment} \mid Z)\) collapses the covariate adjustment problem to a single number. Its balancing property means weighting or stratifying on it achieves the same result as adjusting for all covariates individually.
The main use is inverse probability weighting: weight each unit by the inverse of its probability of receiving the treatment it actually received, creating a pseudo-population where treatment is unrelated to covariates. One thing worth getting right: a good propensity model is not one with high AUC. It is one that achieves covariate balance after weighting. Optimising for prediction can actively hurt balance. Propensity models are fit using tidymodels.
Ch 9: Evaluating your propensity score model
Balance · SMD · love plots · overlap · halfmoon
Standard predictive diagnostics do not tell you whether a propensity model works for causal inference. The right diagnostic is standardised mean differences (SMDs) before and after weighting, which directly show whether covariate distributions are similar across treatment groups.
Love plots display SMDs for every covariate. The target is below 0.1. Overlap plots check positivity visually. Extreme weights are a warning sign: some units were nearly certain to receive or not receive treatment regardless of covariates, which inflates variance and signals near-positivity violations. Options are to trim extreme weights, revisit the covariate set, or narrow the target population. The halfmoon package handles these diagnostics.
Part III: Estimating Causal Effects
Chapters 10-24. Standard IPW and g-computation first, then continuous exposures, time-varying treatments, survival outcomes, effect modification, machine learning, IV, and DiD. Each chapter builds on the framework from Parts I and II.
Ch 10: Causal estimands
ATE · ATT · ATC · estimands · target population
Before fitting a model, decide what you are estimating. The Average Treatment Effect (ATE) asks what would happen if everyone received treatment versus none. The Average Treatment Effect on the Treated (ATT) asks what happened to those who actually received it. These are different quantities and require different estimators.
ATT is usually more appropriate when the treated group is a specific subgroup and you want to know whether treatment helped them. ATE fits questions about policies that would apply broadly. The estimand choice also affects which positivity violations matter, a detail that compounds through the analysis.
Ch 11: Fitting the weighted outcome model
IPW · weighted regression · sandwich SE · bootstrap
With a validated propensity model, fit the outcome model using IPW weights. The technical complication is standard errors: naive SEs from weighted regression are wrong because they treat the weights as fixed rather than estimated. Bootstrap SEs (resample observations, refit both models in each draw) or sandwich SEs fix this. The chapter is direct about which to prefer and when.
Ch 12: Continuous and categorical exposures
Continuous treatment · dose-response · generalised propensity score · categorical exposure
For continuous exposures, the propensity score generalises to a conditional density \(f(X \mid Z)\). Weights from this density stabilise the marginal distribution of the exposure, and the estimand becomes a dose-response curve rather than a single average effect. For multi-level categorical exposures the approach extends naturally; the main decisions are about contrasts and reference categories.
Ch 13: G-computation
G-computation · marginal standardisation · parametric g-formula
G-computation is the outcome-modelling alternative to IPW. Fit \(E[Y \mid X, Z]\), predict each unit’s counterfactual outcome under treatment and under control, average the difference. Often more efficient than IPW when the outcome model is well-specified, and more sensitive to outcome model misspecification when it is not. That tradeoff motivates the doubly robust methods in Chapter 20.
Ch 14: Interaction
Effect modification · heterogeneous effects · CATE · additive vs. multiplicative
The ATE is an average, and averages hide a lot. Treatment effects vary across subgroups. This is effect modification. The chapter distinguishes statistical interaction from causal effect modification and covers conditional average treatment effects (CATEs). Interaction on the additive scale and on the multiplicative scale are not the same thing, and which scale matters depends on whether you care about absolute or relative risk differences.
Ch 15: Missingness and measurement
Missing data · MCAR/MAR/MNAR · multiple imputation · measurement error
MCAR does not bias estimates but reduces precision. MAR is handled well by multiple imputation. MNAR requires sensitivity analysis: the missingness depends on unobserved values, so the mechanism is unidentifiable from data alone.
Measurement error in the exposure attenuates effects toward zero. Measurement error in confounders is worse: residual confounding remains even after adjustment. Neither has a clean fix without auxiliary data or strong assumptions, but the chapter makes the magnitude of bias concrete.
Ch 16: Sensitivity analysis
Unmeasured confounding · E-value · tipping point · tipr
The E-value asks how strong an unmeasured confounder would need to be to explain away the observed effect. Large E-values suggest robustness; small ones signal fragility. Tipping point analysis finds the unmeasured confounding parameters that would shift the confidence interval past the null. Both characterise vulnerability: they tell you how fragile the estimate is, not whether the lurking confounder actually exists. The tipr package implements these in R.
Ch 17: Causal mediation analysis
Mediation · direct effects · indirect effects · interventional effects
When you want to know how a treatment works, you need mediation analysis. The total effect decomposes into direct and indirect effects. The traditional Baron-Kenny approach does not work for causal inference: it ignores treatment-mediator interaction and does not handle confounding of the mediator-outcome path. The chapter uses the interventional effects framework. The identifying assumptions are stricter than for total effects. Conditional exchangeability is needed for both the treatment-outcome and mediator-outcome relationships, with no treatment-induced confounders of the mediator-outcome path.
Ch 18: Causal inference across time
Longitudinal data · time-varying confounding · marginal structural models
With time-varying treatments and confounders, standard regression breaks. A time-varying covariate can simultaneously be a confounder of the current treatment (adjust for it) and a mediator of past treatment (do not condition on it). Ordinary regression cannot do both.
Marginal structural models with time-varying IPW handle this. Weights are constructed from the full treatment history and the outcome model fits the weighted pseudo-population. The longitudinal g-formula is the parametric alternative. Both require careful attention to temporal ordering.
Ch 19: Causal time-to-event models
Survival analysis · hazard ratios · competing risks · RMST · non-collapsibility
Hazard ratios from Cox models are non-collapsible: even in a randomised trial, the marginal hazard ratio differs from the conditional one. This is not a data problem. It is a mathematical property that complicates cross-study comparisons. The restricted mean survival time (RMST) does not have this property and is more directly interpretable. Competing risks are also covered: cause-specific and subdistribution hazards answer different causal questions, and confusing them changes the conclusion.
Ch 20: Doubly robust models
AIPW · doubly robust · TMLE · semiparametric efficiency
Doubly robust estimators combine a propensity model and an outcome model so that correct specification of either is sufficient for consistency. The augmented IPW (AIPW) estimator is the main one covered. TMLE directly targets the causal estimand during estimation. Both are semiparametrically efficient when both models are correct, and both pair naturally with machine learning nuisance models.
Ch 21: Machine learning and causal inference
Causal forests · cross-fitting · double machine learning · CATE
ML nuisance models can fit complex confounding structures without pre-specified functional form. Used naively, regularisation introduces bias that does not vanish with sample size. Cross-fitting removes this asymptotically: fit nuisance models on held-out folds, then rotate. Causal forests directly target heterogeneous treatment effects without pre-specifying which subgroups to examine. Useful when the CATEs are the actual question.
Ch 22: Instrumental variables and friends
IV · LATE · 2SLS · regression discontinuity · natural experiments
When unmeasured confounding makes exchangeability untenable, IV exploits a variable that affects treatment but has no direct effect on the outcome. Two things worth keeping in mind. Valid instruments are hard to find, and the exclusion restriction is unverifiable from data. IV estimates the LATE (the effect among compliers), which may not be the population you care about.
Regression discontinuity uses sharp thresholds in treatment assignment to estimate local causal effects near the boundary. Compelling when the design is clean, limited in external validity.
Ch 23: Difference-in-differences
DiD · parallel trends · panel data · staggered adoption · TWFE
DiD uses a control group’s pre-post trajectory as the counterfactual for the treated group. The identifying assumption is parallel trends: both groups would have moved together absent treatment.
With staggered adoption, the standard two-way fixed effects regression produces a weighted average where some weights can be negative even when every individual effect is positive. The chapter covers heterogeneity-robust estimators designed for this setting and discusses how pre-treatment periods can be used to assess (not verify) the parallel trends assumption.
Ch 24: Evidence
Evidence synthesis · replication · communication · uncertainty
A single well-executed analysis rarely settles a question. Evidence accumulates across studies with different designs, populations, and assumptions. The chapter covers what statistical significance does and does not mean, what replication and robustness checks add, and how to communicate causal claims honestly, including the assumptions and their potential failures. Reporting results without making assumptions visible is not being concise. It is removing the information people need to evaluate whether your conclusions apply to their context.
Suggested reading paths
| Goal | Chapters |
|---|---|
| Understand the framework before running anything | 1 → 3 → 4 → 5 |
| Run a complete IPW analysis end-to-end | 1 → 3 → 4 → 7 → 8 → 9 → 10 → 11 |
| Handle time-varying treatments | 1-11 → 18 |
| Analyse survival outcomes causally | 1-11 → 19 |
| Estimate heterogeneous treatment effects | 1-11 → 14 → 20 → 21 |
| Unmeasured confounding is a real concern | 1-5 → 16 → 22 |
| Exploit a natural experiment or policy threshold | 1-5 → 22 → 23 |
These summaries are a derivative work of Causal Inference in R (Barrett, D’Agostino McGowan and Gerke, 2026, r-causal.org). The original text is copyright the authors. License: CC BY-NC 4.0. Non-commercial use only.