Causal inference: identification, diagnostics and the limits of robustness

Start with the causal claim

These six papers distinguish identifying an effect, detecting it and quantifying uncertainty. Read them as a guide to different failure points, not competing answers to one question. A regression-discontinuity primer explains identification through treatment thresholds; conditional-independence tests seek outcome differences that averages can obscure. Better detection does not itself justify a causal comparison (RD primer; Debiased Conditional Independence Tests).

What makes a comparison credible?

The RD primer compares patients just above and below a known cutoff, relying on continuity of potential outcomes or local randomization. Manipulated scores or another policy changing at that threshold threaten interpretation. Breunig instead characterizes selection through a conditional mutual information restriction: potential outcomes, conditional on covariates, must not be more informative about treatment than latent outcome heterogeneity is. Under the maintained model and this restriction, sufficiently rich variation in treatment probabilities implies unconfoundedness—conditional independence between treatment and potential outcomes (RD primer; Unconfoundedness as an Information Constraint).

These are not interchangeable justifications. In Breunig’s binary-treatment result, a nonconstant propensity score suffices only within that framework; variation alone cannot establish absence of hidden confounding. Shared concern with selection is not agreement on an identification strategy (information constraint).

Whose effect is identified?

Read fuzzy RD alongside Pala’s externally instrumented panel vector autoregression. With imperfect compliance, RD distinguishes the threshold rule’s effect from the treatment effect for people whose receipt changes because of it. Pala’s μ-LATE likewise has an instrument-dependent interpretation. Identification requires independence, exclusion, monotonicity, linearity and instrument relevance. Without relevance, the estimand’s ratio does not exist; weak-instrument-robust confidence sets do not remove that identification requirement. Longer-horizon responses additionally require a serially uncorrelated policy shock and an instrument uncorrelated with other shocks at every date (RD primer; externally instrumented PVARs).

The medical example reports no evidence of long-term kidney harm from contrast-enhanced CTPA, assuming RD and fuzzy-RD conditions hold, specifically for patients near the D-dimer cutoff whose CTPA receipt changes because of the rule. The complier-effect confidence interval permits both decreases and increases in kidney function: harm remains compatible with the estimate even within this subgroup. It does not establish safety for all patients. Pala reports persistently higher nontradable payroll after a stock-wealth gain in US counties. Different outcomes, populations and identifying variation prevent treating these applications as corroboration or contradiction (RD application; PVAR application).

When diagnostics alter inference

Arora and Yanagi question reassuring preliminary evidence through different mechanisms. In covariate-adjusted difference-in-differences, Arora shows that controls measured after a placebo window starts can absorb outcome shocks, flatten pre-trends and narrow sensitivity bands. This distortion can occur separately from bias in the treatment estimate. Earlier measurements permit tests and estimation of the distortion; its importance differs across applications (When Covariates Mask Pre-Trends).

Yanagi instead accounts for selecting a hypothesis after testing for spillovers. The construction uses a randomized saturation design: disjoint clusters receive randomized saturation labels, then units receive randomized treatments conditional on those labels. Within this design and the branch-specific assumptions, second-stage tests condition on selection and control selective Type I error in finite samples. Non-rejection leads to direct-effect testing assuming no spillovers; rejection leads to exposure-contrast testing assuming a correct prespecified mapping based on own treatment and cluster saturation. Non-rejection does not establish no spillovers. This is neither a demonstrated guarantee for arbitrary observational pretests nor a remedy for Arora’s timing problem (Selective Randomization Inference for Interference).

Detection and remaining reading questions

The conditional-independence tests ask whether outcomes improve treatment prediction beyond covariates. Simulations favor them under complex heterogeneity, including effects averaging to zero, but also report small-sample, weak-effect settings with nonzero mean effects where comparators perform better. That is conditional testing-performance evidence, not a universal ranking (conditional-independence tests).

Across this selected coverage, ask which assignment assumption is credible, whose effect is identified and whether diagnostics change uncertainty. The papers do not settle those choices for every application or imply field-wide consensus.

All six records supply selected paper-text excerpts and abstracts, not complete papers. Abstract-only evidence cannot support unreported implementation details; omitted passages do not establish absence from a paper. Extraction visibly disrupts equations and tables, limiting numerical comparisons. These are arXiv-hosted versions requiring preprint-status caution, not assumed peer-reviewed findings. The RD excerpt separately reports online publication and forthcoming JAMA status; the supplied evidence does not establish peer-review status for the others (RD publication note).