Causal Capybara

When one unit's treatment affects another's outcome, estimate the direct and spillover effects separately instead of pretending neither exists.

Not everyone offered a programme takes it. Report what the offer did, and separately what taking it up did for the people it moved.

When whole schools, clinics or villages were assigned, the number of clusters is the sample size that matters.

Compare the two arms as they were randomised, and let covariates sharpen the comparison without letting them change the question.

Re-run the randomisation thousands of times with the outcomes held fixed, and see how unusual what actually happened really is.

Estimate inside the blocks the randomisation was run in, then average them the way your estimand says to.

Take an effect estimated in one population and ask what it would be in another with a different mix of characteristics.

Report the range the effect must lie in given only what the data can support, without assuming away the missing counterfactual.

Search for a graph consistent with the data. It does not recover the true causal structure from observational data without extra assumptions.

Grow trees that look for units whose effect differs, keeping the rows that chose each split away from the rows that estimate it.

A separate outcome model for each arm plus a treatment model, combined in a doubly robust score: right if either side is right.

Predict the outcome and the treatment from the confounders, then regress what is left of one on what is left of the other.

Build the per-unit effect out of ordinary prediction models, four different ways, on the same cross-fitting.

Learn a short, readable rule for who to treat, then value that rule on data it never saw.

Use a treatment model and an outcome model together; it is right if either one is.

Bin the covariates, then compare only inside bins that contain both arms.

Search over distance-metric weights until balance is as good as it can get, instead of trusting one metric.

Pair each treated unit with the most similar untreated unit, then compare within pairs.

Choose the whole set of matches at once to minimise total distance, rather than greedily one treated unit at a time.

Impute the missing values several times, run the analysis in each, and combine -- instead of dropping every row with a gap.

Model the outcome, then ask what would have happened if everyone had been treated, and if nobody had.

Combine several candidate learners by cross-validated weights instead of betting on one.

Fit the outcome model, then nudge it once in the direction the treatment model says it is wrong.

Fit the treatment model so that it balances covariates, rather than fitting it to predict treatment and hoping balance follows.

Find the weights closest to equal that make the covariate means match exactly.

Reweight the sample so the treated and untreated groups look alike on the measured confounders.

Grow a boosted model for the propensity score, stopping at the iteration that balances covariates best.

Learn what untreated life looks like from untreated cells only, then ask how far each treated cell landed from it.

Estimate one clean before-and-after for every adoption cohort, then say out loud how you averaged them.

An estimator built for panels where treatment switches on and off, which the imputation and cohort estimators assume never happens.

One before-and-after with covariates, using an outcome model and a comparison-group model together so either one can carry it.

Plot the effect period by period around adoption, so you can see whether the gap opened when the policy arrived or long before it.

Strip out unit and period effects using untreated cells only, then regress what is left on the policy.

Open up a two-way fixed effects estimate and show every two-group comparison inside it, with the weight each one carries -- including the ones that use already-treated units as controls.

Match treated to comparison units on pre-period characteristics first, then difference.

Give every cohort its own event-study path, then average the paths by cohort size instead of letting the regression choose the weights.

Weight both units and periods, then take a difference-in-differences -- halfway between synthetic control and DiD.

Compare the treated-versus-comparison difference for the group the policy could reach with the same difference for a group inside the same units that it could not.

One regression with unit and period fixed effects. Familiar, fast, and not an average treatment effect when units adopt at different dates.

Two groups, two periods: compare how much the treated group changed with how much the comparison group changed over the same window.

Run the same estimator on variables the programme cannot have changed; they should not step at the threshold.

Compare how many units sit just below the threshold with how many sit just above.

Divide the jump in the outcome by the jump in take-up: the effect for the people the cutoff actually moved.

Where a formula changes slope rather than switching on, measure the change in slope of the outcome.

Fit a line either side of the threshold and measure the step between them.

Treat a narrow window around the cutoff as a small randomised experiment rather than fitting a curve through it.

Several thresholds, or a boundary on a map, pooled into one design.

Use only the part of the treatment that the instrument moved, and see what happened to the outcome.

Weight the instruments by how informative each one actually is, using a weight matrix estimated from the data.

The maximum-likelihood cousin of two-stage least squares, which stays much better behaved when the instruments are weak.

Trace the effect as a function of how reluctant a unit is to be treated, instead of reporting one local average.

Combine national shocks with local exposure shares to build an instrument for local changes.

Report the set of effects the data cannot reject, which stays honest however weak the instrument is.

Build a weighted copy of the treated place out of untreated places that looked like it beforehand, then watch the two lines separate.

When no weighted average of the donors can match the treated place, correct the leftover bias with a ridge model and show the size of the correction.

Treat the missing treated-period outcomes as holes in a panel and fill them in with a low-rank model of what the panel would have done.

Synthetic control when the treated unit is a neighbourhood or a small area and there are many of them.

Confidence intervals for a synthetic control that come from a model of the prediction error rather than from permutation.

Weight the comparison units and the pre-treatment periods, then run a difference in differences on the result - a level gap is allowed, a trend gap is not.

Model the memory in the series itself, then ask how big a step, pulse or ramp the data need at the intervention date.

Model the counterfactual series with a structural time-series model and control series, and report a posterior rather than an interval.

The same interruption, measured against a series the intervention did not touch, so a shock that hit everybody is not booked as your effect.

Fit the trend before the interruption, project it forward, and measure the jump and the change of direction after it.

What the treatment would still do if the mediator were fixed at one value for everybody.

Shift the mediator to the distribution it would have in the population, rather than to each person's own unobservable counterfactual.

Split the total effect into the part that travelled through the mediator and the part that did not.

Estimate the effect of a treatment regime by finding the parameter that removes the association between treatment and the blipped-down outcome.

Model each period in turn, then simulate the world where everyone followed the strategy you name.

Estimate the effect of shifting a continuous or multi-valued treatment, rather than of setting everyone to one value.

Regress backwards from the final outcome, then correct with the treatment probabilities: right if either set of models is right.

Time-to-event outcomes with time-varying treatment and censoring, targeted at each time.

Reweight each person-period so the treated and untreated histories look alike, then fit one simple model to the reweighted data.

Fit a right-censored log-normal/Weibull AFT model; standardize survival/RMST over baseline covariates under explicit causal assumptions, or report a conditional time factor.

Compare observed group event-free probabilities at an explicit common horizon; this is an unadjusted association.

Compare areas under observed Kaplan–Meier curves through a common horizon in time units; this is an unadjusted association.

Logistic interactions plus separate standardized risk-difference, risk-ratio or marginal odds-ratio heterogeneity tests.

Multinomial treatment interactions and a joint test of category-probability contrasts; preserves categories without assigning numeric scores.

OLS treatment-by-baseline-modifier interactions with HC3 or cluster sandwich inference, direct mean-difference tests and Holm pairwise comparisons.

Poisson conditional-mean interactions with robust sandwich inference; compare standardized count or fixed-exposure rate contrasts.

Simulate a common cause of a stated strength and watch the estimate move; read off how strong one would have to be to explain the result away.

Run the grid of defensible specifications and sort the answers. The curve is the result, not the one you happened to run.

How strong would an unmeasured confounder have to be -- compared with the covariates you already have -- to explain the estimate away?

The smallest confounder-treatment and confounder-outcome association that could explain the result away.

What survives when parallel trends is allowed to fail by a stated amount.

Drop one cluster, cohort or donor at a time and see whether any single one is carrying the result.

Estimate something that shares the confounding but not the causal path. A non-zero answer is bias you can see.

How important would unobserved variables have to be, relative to the controls you already have, to drive the coefficient to zero?

Run the same analysis on something the treatment could not have changed. It should find nothing.

Move the policy date earlier, reshuffle who was treated, or swap in a variable that cannot cause the outcome.

Add a variable that causes nothing to the adjustment set. The estimate should barely move.

How unequal could the odds of treatment be inside a matched pair before the conclusion stopped being clear?

Re-estimate on random subsets. The answer should move about as much as losing that much data costs, and no more.

Re-estimate across a grid of propensity-score trimming thresholds instead of picking one and hoping.