Local Randomization Near A Threshold

Why Treat a Neighborhood of the Cutoff as a Design?

Regression discontinuity can be analyzed as a local comparison near a threshold. A local-randomization analysis makes a stronger, finite-sample claim: within a specified neighborhood of the cutoff, assignment to the two sides behaves as if randomized under a stated assignment mechanism. This can make the analysis and its target especially transparent, but it does not follow automatically from being close to a cutoff. The window and the claim that assignment is as-if random there both require justification.

Let $R_i$ be unit $i$'s running variable, $c$ the cutoff, and $Z_i=1(R_i\ge c)$ the cutoff-based assignment indicator. Let $D_i$ denote actual treatment receipt, which can differ from $Z_i$ in a fuzzy design. For a proposed half-width $h>0$, the window contains the units whose running-variable values are sufficiently close to the cutoff.

Definition: The cutoff-centered window with half-width $h$ is $W_h=\{i:c-h\le R_i\le c+h\}$. Write $N_h$ for the number of units in this window. A local-randomization analysis treats assignment $Z_i$ among the units in $W_h$ as governed by a specified randomization mechanism, conditional on the window membership and any features of the assignment mechanism held fixed, such as the number assigned to each side.

The definition identifies a group to analyze; it does not establish that assignment is random in that group. In an ordinary threshold rule, $Z_i$ is mechanically determined by $R_i$. Local randomization is therefore an approximation about how units came to have scores on either side: within the chosen window, the assignment pattern is taken to be sufficiently like a random allocation for the proposed mechanism to be credible. It is not a claim that the cutoff literally randomized anyone.

Assumptions and the Target Effect

The assumptions should be stated for the chosen window, not vaguely for “units near the cutoff.” First, the treatment and outcome must be well defined for each unit, with no interference: one unit's assignment does not change another unit's outcome. Second, the assignment mechanism within the window must be specified. For example, a complete-randomization model holds the number assigned to each side fixed and treats every allocation with those counts as equally likely. A different mechanism, such as independent assignment with known probabilities, would require a different specification.

Most importantly, the proposed mechanism must be plausible: assignment within the window must not systematically select units with different potential outcomes. This is an as-if-random assumption, not something demonstrated by a balance table. Each unit must also have a positive chance of each assignment under the stated mechanism if both potential outcomes are to be represented by the design. Under complete randomization with at least one unit assigned to each side, this condition holds for every unit.

Let $Y_i(1)$ and $Y_i(0)$ denote unit $i$'s potential outcomes under assignment and non-assignment. For a sharp design, assignment determines treatment receipt, so the assignment effect is also the treatment effect. The natural target is then the average treatment effect among the units in the specified window—not an effect for everyone in the study or population.

\tau_{W_h}=\frac{1}{N_h}\sum_{i\in W_h}\left[Y_i(1)-Y_i(0)\right].

Under the specified assignment mechanism, the difference in observed mean outcomes estimates this finite-window average. If $n_1$ and $n_0$ are the numbers assigned and $Y_i$ is the observed outcome, the estimator is

\hat{\tau}_{W_h}= \frac{1}{n_1}\sum_{i\in W_h:Z_i=1}Y_i - \frac{1}{n_0}\sum_{i\in W_h:Z_i=0}Y_i.

This target is deliberately local: changing $h$ changes the set of units and therefore changes the estimand. If treatment receipt is imperfect, the same difference in outcomes targets the effect of assignment in the window. Interpreting a ratio of the assignment effect on outcomes to the assignment effect on treatment receipt as a treatment effect for local compliers requires additional instrumental-variable assumptions, including exclusion and monotonicity. Assignment and receipt effects should not be conflated.

Why the Difference in Means Targets the Window Effect

Under complete randomization with $n_1$ assigned units fixed, each unit has probability $n_1/N_h$ of assignment. The treated mean is unbiased for the window mean of $Y_i(1)$. To see this, let $I_i=1$ when unit $i$ is assigned. Then $E(I_i)=n_1/N_h$, and the treated mean is $n_1^{-1}\sum I_iY_i(1)$. Taking its expectation gives

E\left[\frac{1}{n_1}\sum_{i\in W_h}I_iY_i(1)\right] = \frac{1}{n_1}\sum_{i\in W_h}\frac{n_1}{N_h}Y_i(1) = \frac{1}{N_h}\sum_{i\in W_h}Y_i(1).

The same argument shows that the control mean is unbiased for $N_h^{-1}\sum_{i\in W_h}Y_i(0)$. Subtracting the two expectations gives $E(\hat{\tau}_{W_h})=\tau_{W_h}$. This justification depends on the assignment mechanism being credible; it cannot rescue an implausible window or an incorrect model of assignment.

Choosing and Defending the Window

A defensible window balances two aims. A narrower window may make the as-if-random claim more plausible because units are more alike in running-variable value, but it can leave few units and little support for comparison. A wider window can improve precision and include more units, yet increase differences between the two sides or include regions where assignment is less plausibly random. There is no universal half-width that resolves this tradeoff.

Use design information rather than choosing a window because it produces a preferred outcome estimate. Before examining outcome contrasts, specify candidate windows using substantive knowledge and inspect:

Sorting and manipulation: Are there signs that units could precisely control or manipulate their running-variable values around the cutoff? Earlier material on testing for sorting and heaping helps frame this concern.
Predetermined covariates: Do characteristics measured before assignment look similar on either side? Large or systematic differences weaken the local-randomization argument. Balance is supporting evidence, not proof, and a nonsignificant test does not establish random assignment.
Support and composition: Are there observations on both sides across the proposed window? Are particular score values, groups, or periods represented on only one side? Sparse or uneven support can make the proposed comparison fragile.
Window sensitivity: Does the substantive rationale for the window survive nearby alternatives? If a small change in $h$ radically changes which units are included or the diagnostic picture, the design claim needs qualification.

A difference in the running variable across assignment groups is not, by itself, surprising: the cutoff rule assigns units according to that variable. In a discrete-score setting, for example, the score may have only a few possible values on each side. The relevant question is whether the chosen assignment model is plausible for the observed units and whether the associated diagnostics reveal serious incompatibilities—not whether every covariate has exactly identical sample means.

Worked Example: Defining a Sharp-Design Target

Hypothetical data. A program assigns a scholarship offer to applicants with a score of at least $70$. Consider the pre-specified window $68\le R_i\le72$. There are 30 applicants in it: 16 are offered the scholarship and 14 are not. Mean follow-up earnings are \$28,400 among those offered and \$26,900 among those not offered. Assume for this example that receiving the offer determines scholarship receipt.

The assignment contrast is $28{,}400-26{,}900=\$1{,}500$ in mean earnings. Because this is a sharp design, assignment and treatment coincide, so the corresponding target is the average scholarship effect for applicants in this 68-to-72-point window.

The numerical contrast alone does not establish that the window is randomized. Suppose, in addition, that predetermined baseline earnings average \$24,100 and \$23,900 in the two assignment groups, and age averages 18.6 and 18.7 years. These small differences are compatible with the as-if-random account, but do not prove it. Investigators would also need to consider score manipulation, how the window was chosen, and whether the score support in this range permits the proposed comparison.

The conclusion is limited to the applicants in this specified window. It is not automatically the scholarship effect for applicants with much lower scores or for all eligible students. If the offer does not guarantee receipt, the \$1,500 contrast is instead an assignment effect.

Worked Example: Comparing Candidate Windows

Hypothetical diagnostics. Investigators consider three windows around a cutoff. The following table summarizes their sizes and the largest absolute standardized difference across four predetermined covariates; larger absolute differences indicate more imbalance on at least one measured covariate.

Half-width $h$	Units in window	Largest absolute standardized difference	Support note
1	18	0.12	Both sides represented, but few units
2	42	0.18	Both sides represented across the window
3	70	0.46	One score value is unusually concentrated on one side

The $h=3$ window raises a concern: its largest covariate difference is $0.46$, and the score concentration is consistent with a possible composition or sorting problem. The $h=1$ window has the smallest reported imbalance, but only 18 units, so it may provide limited information. If substantive knowledge supports $h=2$, it offers a plausible compromise: 42 units, usable support on both sides, and no comparably large measured imbalance.

These diagnostics do not calculate a uniquely correct window. The choice of $h=2$ would need to be justified by the design context and preferably set without selecting on the outcome contrast. If the $h=2$ window also showed manipulation or important unmeasured differences, its larger size would not make the randomization claim credible.

Worked Example: Assignment Effect Versus Treatment Effect

Hypothetical data. In a local window with 40 applicants, 20 are assigned an offer and 20 are not. Of those offered, 18 enroll in the program; of those not offered, 5 enroll through another route. Mean outcome scores are 8.4 points for the offer group and 4.8 points for the no-offer group.

The assignment effect estimate is $8.4-4.8=3.6$ outcome points. The difference in enrollment proportions is $18/20-5/20=0.90-0.25=0.65$. The ratio of these two contrasts is $3.6/0.65\approx5.538$ outcome points per enrollment.

The first contrast describes the effect of assignment in the window. The ratio can be interpreted as a local complier treatment effect only if the assignment is as-if random in the window and the additional instrumental-variable assumptions—especially exclusion and monotonicity—are credible. The arithmetic does not establish those assumptions. Without them, reporting 5.538 points as the causal effect of enrollment would overstate what these summaries identify.

Common Pitfalls and Alternatives

A frequent mistake is to say, “The covariate differences are small, so treatment was randomized.” The reasoning is incomplete: measured balance can support an as-if-random argument, but unmeasured differences and manipulation may remain. The correction is to state the proposed assignment mechanism and window, present diagnostics as evidence rather than proof, and explain the substantive basis for the design claim.

Local randomization differs from a continuity-based regression-discontinuity analysis. The latter identifies a limiting contrast at the cutoff under continuity assumptions on potential-outcome relationships; local randomization instead makes an as-if-random assignment claim for the finite set in a chosen window. The approaches can be complementary, but their assumptions and targets are not interchangeable. Matching or regression adjustment may describe observed similarities or account for measured covariates, but neither makes an implausible assignment mechanism random. Likewise, narrowing the window does not guarantee validity if units can manipulate their scores or if the remaining units differ systematically.

The main limitation is external scope: the window effect may not apply away from the cutoff. A second limitation is that the as-if-random assumption cannot be verified from observed outcomes and covariates alone. Sensitivity to the window, weak support, and evidence of sorting should be reported as substantive limitations, not hidden by a single preferred estimate.

Key takeaway: A local-randomization analysis requires a clearly specified cutoff-centered window, a credible assignment mechanism within it, and an estimand tied to the units in that window. Diagnostics can challenge or support the claim; they cannot prove it.

Check Your Understanding

Answer each question, then compare your reasoning with the solution immediately below it.

A cutoff is $c=50$, and the selected half-width is $h=3$. State the window and explain what changes if $h$ is increased. Solution: The window is $47\le R_i\le53$. Increasing $h$ changes the included units and therefore generally changes the finite-window target as well as the plausibility of the assignment assumption.
Why does a lack of statistically significant covariate differences fail to prove local randomization? Solution: A test may have limited power, only measured covariates are examined, and balance does not rule out manipulation or unmeasured differences. It is diagnostic evidence, not proof of the assignment mechanism.
In a sharp design, mean outcomes are 12.6 units in the assigned group and 10.1 in the comparison group. What is the estimated contrast, and what is its target? Solution: $12.6-10.1=2.5$ outcome units. Under the local-randomization assumptions, it estimates the average treatment effect among units in the specified window.
In a fuzzy design, why is the difference in outcome means not automatically the treatment effect? Solution: Assignment and treatment receipt differ, so the outcome contrast is the effect of assignment. A treatment effect for compliers requires additional instrumental-variable assumptions and a suitable ratio estimand.
What is a concern if a wider window contains a score value heavily concentrated on one side of the cutoff? Solution: The sides may differ in composition or support, making the as-if-random claim less plausible. Investigators should investigate sorting and justify the window rather than assuming that a larger sample resolves the problem.