Rdd

Regression discontinuity

An opinionated RD workflow grounded in a read canon (references/canon.md, current as of 2026-07-28): the Cattaneo-Titiunik Annual Review of Economics survey and its applied companion, the Cattaneo-Keele-Titiunik guide, which includes a real failed design this skill uses as its refusal template. Deliverable: the recommendation with its citation, the R estimation and diagnostics code, and a methods paragraph.

Refresh path: run litreview on the method since the canon date, then propose additions to references/canon.md as flagged addenda.

Design shapes and the case that anchors each

Each canonical case is a precedent a methods section can cite; details.md says what each teaches.

The design gate: is this an RD at all?

An RD requires a score, a known cutoff, and a treatment rule that existed ex ante and is verifiable. Before any estimation, write the qualitative account: who computes the score, was the cutoff public, can agents precisely control their score near it. Precise manipulation is the most important threat. Lab-measured or third-party-computed scores resist it; self-influenced scores (customer spend near a tier threshold, follower counts near a monetization bar) invite exactly the sorting the density test detects, so the falsification battery carries more weight in marketing settings than in the medical originals.

One more gate question, and the one sharp designs skip: list every rule, benefit, message, and flag that changes at this exact threshold, and say which of them is the treatment. Medicare starts at 65 and so does retirement, so Card, Dobkin, and Maestas (2008) went to a third dataset on the same running variable (the March CPS 1996-2004) and showed employment does not jump. When the confounder is not in your data, find a dataset on the same score where it is.

Two red flags, the first disqualifying on its own (from the failed Oncotype-DX application in Cattaneo-Keele-Titiunik 2023):

1. Treatment take-up jumps at score values away from the official cutoff (the rule was soft: reps contact leads below the threshold, managers grant status matches early). Plot take-up against the score before anything else.
2. Covariate imbalance already in the smallest window around the cutoff: disqualifying when the imbalanced covariate plausibly drives the outcome (the balance battery's standard, below), otherwise a serious flag that demands an explanation before proceeding.

When a design fails, say so and decline to report an effect; the guide's own verdict on its failed application ("the evidence does not support an RD analysis") is the template. Route the question back to causal-design for another identification strategy.

Triage: two frameworks, and which one leads

Sharp vs fuzzy is a fact of the institution, not a choice: sharp when the rule binds mechanically (a trial expires, a discount ends at an anniversary), fuzzy whenever anyone can cross their assignment (overrides, opt-ins). Under fuzziness always report both ITT effects (on take-up and on the outcome) alongside the fuzzy ratio.

Continuity vs local randomization is decided by the score:

• Continuous score, many observations near the cutoff: continuity framework with local polynomials leads; local randomization is the robustness complement.
• Discrete score (rule of thumb: roughly 30 or fewer distinct values) or very few observations near the cutoff: local randomization leads. Continuity methods there extrapolate from the nearest mass points and their effective sample size is the number of mass points, not the number of observations. Discrete running variables (weeks of tenure, order counts, months since signup) are the norm in marketing data, which makes this branch more common than the econ literature suggests.
• Local randomization needs a strictly stronger assumption (potential outcomes unrelated to the score inside the window), which must be argued, not assumed.

When both frameworks apply, run both; agreement is a robustness result, and the local randomization CIs covering the continuity point estimate counts as consistency. Expect the window to be far narrower than the bandwidth (in the guide's HIV application, 121 patients vs 2,593), so a local-randomization null alongside a significant continuity estimate can be a power difference, not a contradiction.

The consensus recipe (continuity framework)

Local linear regression, triangular kernel, MSE-optimal bandwidth, robust bias-corrected confidence intervals (Calonico-Cattaneo-Titiunik). Report both the conventional and the robust interval. The one-line justification: conventional 95 percent intervals at the MSE-optimal bandwidth cover only about 80 percent, and bias correction with the matching variance adjustment restores coverage at the same bandwidth. Two things get called robust: the Mixtape (Cunningham, Causal Inference: The Remix, ch. 6) moves between heteroskedasticity-robust OLS standard errors and rdrobust's Robust row without flagging the difference, and this skill keeps them apart because HC-robust errors leave the point estimate alone while rdrobust's Robust row recenters on the bias-corrected estimate and widens the interval by the variance of the bias estimate.

Hard rules from the review, stated as prohibitions because that is how it states them:

• Bandwidths must be data-driven and criterion-optimal; choosing one by hand "is discouraged." MSE-optimal for the point estimate, CE-optimal when the interval is the object. Distinct left/right bandwidths are available when curvature differs by side. The Mixtape (ch. 6) replicates Hansen 2015 with hand-picked bandwidths and a rectangular kernel, which is how RD was done before 2014; this skill refuses that as a primary specification and keeps it only for reproducing a paper that predates the criterion-optimal machinery.
• Never cluster standard errors on the running variable. The Mixtape (ch. 6) reports the practice as history, recommended by Lee 2008 and Lee and Card 2008 and then discouraged; this skill states it as a prohibition because Kolesar and Rothe 2018 show it inflates Type I error. Use heteroskedasticity-robust variance, honest intervals for a discrete score, and cluster only on a real assignment unit that is not the score. Replicating or refereeing an older RD, expect to find this and fix it.
• Global polynomial fits are visualization only, never estimation (Gelman-Imbens): boundary behavior, counterintuitive weighting, overfitting.
• Polynomial order: p = 1 default, p = 2 as the robustness check, never high order. Underfitting biases in the other direction, and the Mixtape's cubic simulation with a true zero effect makes it vivid: -176,368.30 from a linear fit and 61,866.33 from a quadratic against 1.14 from the cubic. Curvature is handled by narrowing the window, since the MSE-optimal bandwidth shrinks as curvature rises. h_MSE also grows with p, so the p = 2 check runs on a wider window and a different effective sample. In the Mixtape's Table 6.8 the left bandwidth goes 0.020, 0.033, 0.038 and the effective N 13,794, 16,774, 17,545 as the fit goes from no polynomial term to BAC to BAC and BAC-squared. When p = 2 moves the estimate, check the window.
• Covariates are for precision only; they cannot restore identification of the canonical RD parameter, and adjusting an invalid design changes the parameter rather than rescuing it. The point estimate should barely move when covariates enter; a large move signals imbalance.

The local-randomization recipe

Select the window by nested covariate-balance tests, then difference in means inside it, with Fisherian randomization inference when the window holds few observations (exact under the sharp null) and Neyman or super-population inference when it is well populated. Window-selection mechanics, thresholds, and what a narrow window does to power: references/details.md.

Fuzzy designs: the IV discipline applies

The fuzzy estimand is a complier average effect at the cutoff under relevance, exclusion, and monotonicity, so the iv skill's habits transfer:

• Test the first stage inside the bandwidth or window, never on the full sample; the full-sample F overstates strength. The guide's contrast is the anchor: F around 698 in the valid design against F = 1.51 in the failed one, where the first-stage effect is 0.15 with a Fisherian p-value of 0.32. An in-bandwidth first-stage F that is neither the strong nor the hopeless extreme goes to the iv skill's ladder: read it against the F targets there and report Anderson-Rubin/CLR intervals rather than the 2SLS t.
• Argue exclusion qualitatively and concretely: it fails if crossing the cutoff changes behavior through anything other than treatment (a low churn score triggering a retention call AND a flag another team acts on).
• Monotonicity: safe when crossing the threshold moves treatment in one direction only; suspect when overrides run in both directions (the failed-design pattern above, reps contacting below-threshold leads while managers grant early crossings, is exactly the defiers case); one-sided noncompliance buys it for free.
• Run fuzzy-ratio balance tests: instrument strength amplifies covariate bias, so imbalance invisible to ITT balance can surface in the ratio.
• Use one MSE-optimal bandwidth for the ratio, not separate ones for numerator and denominator.

Falsification battery

Run them in this order. Each check's bandwidth convention and what its failure means are in references/details.md.

1. Qualitative manipulation account, written before estimation (who computes the score, who knows the cutoff).
2. Density continuity test (rddensity, robust bias-corrected) plus the exact binomial count test in small windows. A discontinuous density demands an explanation, and the sorting behind it can be administrative rather than strategic.
3. Heaping: plot the raw histogram of the score at its finest granularity before any formal test. The density test can pass while heaping biases the estimate, so run the donut whatever the density test says (Almond et al. 2010; Barreca et al. 2011, 2016).
4. Covariate and placebo-outcome balance: the full RD machinery with each predetermined covariate as the outcome, a fresh MSE-optimal bandwidth per covariate, robust p-values. A failure on a covariate that plausibly drives the outcome invalidates the design, and the verdict is to walk away rather than to adjust.
5. Placebo cutoffs, one side of the true cutoff at a time so treatment effects do not contaminate the placebo.
6. Donut hole: drop the observations at and immediately adjacent to the cutoff, keep the original bandwidth, re-estimate. The donut estimate is a different parameter, local to a wider neighborhood, and the write-up should describe it as one.
7. Bandwidth and window sensitivity: instability at or below the chosen bandwidth is the warning sign, failure far above it is expected by construction.

When a null matters, report minimum detectable effects (rdpower), never ex-post power from the observed effect.

The live dispute, carried honestly

Robust bias correction (this canon's school) vs honest uniform-in-bias inference (Armstrong-Kolesar, Imbens-Wager; R package RDHonest). The honest school bounds the second derivative by a constant M and gets uniformly valid intervals; the canon's objection is that a data-driven M destroys the uniformity that motivates the method, and a manual M is equivalent to choosing the bandwidth by hand. Default here: RBC. When a referee or coauthor asks for honest intervals, report RDHonest alongside with the M choice justified in text, and cite both sides.

Extensions, briefly

• Kink designs: same machinery on first derivatives; identification is more delicate.
• Multiple cutoffs or scores (tiered loyalty programs; geographic borders such as DMA boundaries): cutoff-specific effects or normalize-and-pool (rdmulti), with the pooled estimand's interpretation checked.
• RD in time: hard to justify as standard RD; the local-randomization framework is the adaptation when it works at all. Prefer did or synthetic-control for policy-date designs.
• Extrapolation beyond the cutoff LATE needs added assumptions, and the menu is in references/details.md. Say which one when claiming anything away from the cutoff. Absent one, the methods paragraph says the estimate is local to the cutoff, full stop.

R implementation

The complete runnable pipeline is scripts/rdd_template.R (estimation in both frameworks, fuzzy diagnostics, the full falsification battery, power/MDE), with every call verified against the rdpackages suite. The core:

library(rdrobust); library(rddensity); library(rdlocrand)
rdplot(y, x, c = cutoff)                      # anatomy first
summary(rdrobust(y, x, c = cutoff))           # sharp: local linear, triangular, MSE-h, RBC
summary(rdrobust(d, x, c = cutoff))           # first stage / ITT on take-up
summary(rdrobust(y, x, c = cutoff, fuzzy = d))# fuzzy ratio
summary(rddensity(x, c = cutoff))             # manipulation
w <- rdwinselect(x, Z, c = cutoff)            # local-randomization window
rdrandinf(y, x, cutoff = cutoff, wl = w$w_left, wr = w$w_right)

Four figures carry a credible RD: the density of the score, take-up against the score, covariate balance, and the outcome in bin means. If you cannot see the effect in the bin means you are underpowered or it is not there. Report the estimate against the mean of the dependent variable, so a small coefficient on a large base reads as a precise null (0.6 points on an 84.6 percent base, in the Mixtape's balance table).

Package index with versions and links in references/details.md. Stata and Python mirrors of the whole suite live at rdpackages.github.io; the guide ships full replication code in all three.

Methods paragraph template

Treatment assignment changes discontinuously at [cutoff] in [score], a rule set by [institution] before the outcomes we study, and units [cannot / can only imprecisely] control their score near it. We estimate the RD effect with local linear regression, a triangular kernel, and an MSE-optimal bandwidth, and report robust bias-corrected confidence intervals (Calonico, Cattaneo, and Titiunik 2014; Cattaneo and Titiunik 2022). We validate the design with the Cattaneo-Jansson-Ma density test and an exact binomial test, covariate balance at the cutoff with per-covariate bandwidths, placebo cutoffs, donut-hole estimates, and bandwidth sensitivity [and, for the fuzzy design, verify first-stage strength within the estimation bandwidth and report intention-to-treat effects alongside the complier estimate]. The estimate is local to the cutoff; a limitation of this design is that it does not identify effects for [units far from the threshold], and I extrapolate only [not at all / under the stated assumption], which costs [generalizability across the score distribution].

Every claim traces to references/canon.md; keys live in ../causal-design/references/causal.bib.

Handoffs

• causal-design: whether an RD exists at all; where to go when the design gate fails.
• iv: the fuzzy branch's in-bandwidth first stage and exclusion argument live here; weak-instrument inference (the F ladder, AR/CLR intervals) lives in iv, along with many-instrument and shift-share logic.
• did / synthetic-control: policy-date designs masquerading as RD in time.
• preregister: pre-specifying an RD on an upcoming threshold change.