Temporal Regression Discontinuity Designs

Why a Policy Date Can Be a Cutoff

A policy that begins on a known date creates a possible discontinuity in treatment: observations just before the date are untreated, while those just after it are exposed. Comparing outcomes close to that date can be informative because nearby times may share similar background conditions. But calendar time is not automatically as-if random. Seasons change, other events may coincide with the policy, and people may respond to an announcement before the effective date. Temporal regression discontinuity therefore depends on a credible local comparison, not merely on knowing when a policy started.

The design is especially natural for an outcome observed repeatedly over time, such as a daily rate or weekly count. It can also use individual observations collected at different dates, provided the target population and the composition of observations are comparable on either side of the cutoff. The key question is whether, absent the policy, the expected outcome would have evolved smoothly through the policy date.

Definition: Let $t$ denote calendar time and $c$ the known policy date. The cutoff indicator is $Z_t=1(t\geq c)$. In a sharp temporal regression discontinuity, treatment status is $D_t=Z_t$: the policy applies from date $c$ onward and not before. The running time centered at the cutoff is $x=t-c$, so the cutoff is $x=0$. A temporal discontinuity is the right-hand limit of the expected outcome at $c$ minus its left-hand limit.

For a policy that changes treatment for everyone at the date, define $Y_t(0)$ and $Y_t(1)$ as the potential outcomes at time $t$ without and with the policy, respectively. These may be individual outcomes or an expected outcome for the population observed at time $t$. The causal effect at the cutoff is the difference in potential outcomes at $c$. In a sharp design, the observed outcome is $Y_t(0)$ before $c$ and $Y_t(1)$ from $c$ onward.

Identification: What Must Be Continuous?

The basic identifying argument is a limit comparison. On the left of the cutoff, observed outcomes reveal the untreated outcome trajectory. On the right, they reveal the treated trajectory. To interpret the difference between those limits as the effect at $c$, both potential-outcome means must be continuous there. Continuity of the untreated mean alone is not enough: the right-hand observed limit must also equal the treated mean at the cutoff.

Identification condition: For a sharp temporal design, suppose $E[Y_t(0)]$ and $E[Y_t(1)]$ are continuous at $c$, and the policy is the only cause of a discontinuous change in the observed outcome at $c$. Also suppose there is no anticipation that changes outcomes before $c$, and the population and outcome measurement are comparable across the date. Then $$ \lim_{t\to c^+}E[Y_t\mid t] - \lim_{t\to c^-}E[Y_t\mid t] = E[Y_c(1)]-E[Y_c(0)]. $$ The right-hand side is the average causal effect at the policy date for the population represented at that cutoff.

The justification follows directly from the treatment assignment rule. For $t<c$, $E[Y_t\mid t]=E[Y_t(0)]$; for $t\geq c$, $E[Y_t\mid t]=E[Y_t(1)]$. Taking the two limits and using continuity of each potential-outcome mean gives

\begin{aligned} \lim_{t\to c^+}E[Y_t\mid t] -\lim_{t\to c^-}E[Y_t\mid t] &=E[Y_c(1)]-E[Y_c(0)]. \end{aligned}

This argument makes the central threat explicit. A second event that also changes the outcome at $c$ can create a jump even if the policy has no effect. Likewise, if the treated potential-outcome mean is discontinuous at $c$ for a reason other than the policy, the observed right-hand limit need not equal $E[Y_c(1)]$. The causal interpretation is thus local and conditional on the design assumptions; it does not follow from a before-and-after difference alone.

Worked Example: Estimating a Local Jump From Two Trends

Suppose a hypothetical service policy begins on day $c$. The outcome is the number of completed services per 1,000 eligible residents per day, and $x=t-c$ is measured in days. For illustration, the observations at $x=-3,-2,-1$ are $44,46,48$; at $x=1,2,3$ they are $58,60,62$. Fit a separate straight-line trend on each side and compare its predicted value at $x=0$.

The three pre-policy observations lie exactly on $Y=50+2x$: for example, at $x=-2$, the fitted value is $50+2(-2)=46$. The pre-policy line therefore predicts 50 services per 1,000 residents per day at the cutoff.

The post-policy observations lie exactly on $Y=56+2x$: at $x=2$, the fitted value is $56+2(2)=60$. The post-policy line predicts 56 services per 1,000 residents per day at the cutoff. The estimated discontinuity is $$ \widehat{\tau}=56-50=6 $$ services per 1,000 residents per day.

This is a point estimate, not by itself evidence that the policy caused the increase. Its causal interpretation requires smooth potential-outcome means on both sides, no anticipatory response before day $c$, and no other change at that date. In this constructed example the trends have equal slopes, but equal slopes are not required for a discontinuity design: the fitted lines are used to estimate each side's limiting value, not to assert that the full trajectories are parallel.

Fitting Local Trends and Handling Calendar Patterns

A practical analysis often fits separate local regressions on either side of $c$, using only dates within a selected bandwidth. A simple linear specification for a sharp design is

Y_t=\beta_0+\tau Z_t+\beta_1x+\beta_2(Z_tx)+\varepsilon_t,\qquad x=t-c.

Here $\beta_0$ is the fitted left-hand value at the cutoff, $\beta_0+\tau$ is the fitted right-hand value, and $\tau$ is their difference. The interaction permits different local slopes. A bandwidth that is too wide can make the local linear approximation poor; one that is too narrow can leave too few time points and make the estimate unstable. Use observations on both sides and inspect how the estimate changes over reasonable bandwidths. Bandwidth sensitivity is a diagnostic, not a way to select the result that looks most favorable.

Seasonality needs particular care. A smooth seasonal pattern at the cutoff may be approximated locally by a trend when the window is short enough, but abrupt calendar features—such as a holiday closure, a reporting-cycle boundary, or a weekday-composition change—can look like a treatment jump. Depending on the data and timing, analysts may include weekday, month, or other calendar indicators, or compare like calendar periods across years as a sensitivity analysis. Such adjustments can address modeled calendar structure; they cannot prove that the remaining discontinuity is causal. If the policy date coincides with a calendar feature whose effect is itself discontinuous, the two changes may be inseparable.

Worked Example: A Weekday-Composition Adjustment

Suppose a hypothetical policy starts on a Monday. Daily data near the date produce an estimated raw jump of 8 completed cases per 1,000 people. A local model that also adjusts for weekday indicators estimates that the change in weekday composition around the cutoff contributes 3 cases per 1,000 to the raw difference. The adjusted jump is $$ \widehat{\tau}_{\text{adjusted}}=8-3=5 $$ completed cases per 1,000 people.

The adjusted estimate is 5 cases per 1,000, not 8. This interpretation is appropriate only if the weekday adjustment is specified adequately, there is support on both sides for the relevant weekdays, and no other abrupt change remains at the Monday cutoff. The subtraction illustrates a model-based adjustment; it does not establish those assumptions. If the policy began on the same Monday as a separate service redesign that also raised cases by 5 per 1,000, the adjusted jump could not distinguish the two changes.

Anticipation, Concurrent Events, and Diagnostics

The effective date may not be the date treatment first affects behavior. If a policy is announced in advance, providers may prepare, and individuals may alter their choices before implementation. Such anticipation violates the idea that the pre-cutoff trajectory represents outcomes under no policy response. Investigate the announcement and implementation timeline, plot the outcome over a sufficiently broad period, and examine whether changes begin before the nominal cutoff. A visible pre-policy shift is a warning, not a complete test: subtle anticipation may be difficult to detect, especially with noisy or sparse observations.

List other events at or near the cutoff, including concurrent policies, changes in eligibility, data systems, staffing, and outcome definitions. Check whether the number and composition of observations, missingness, and measurement procedures change. Predetermined covariates and placebo dates or outcomes can reveal some irregularities; a detected discontinuity weakens the design, while no detected discontinuity does not prove validity. The earlier material on placebo cutoffs and outcomes and predetermined covariate continuity checks provides relevant diagnostic principles.

Temporal observations are often serially correlated: nearby days or weeks may share shocks. Treating every date as independent can understate uncertainty and overstate precision. Inference should reflect the time structure, including the observation frequency, dependence, and number of effectively informative time points. With only a short sequence of dates, a large count of individual records per date does not necessarily supply many independent time observations. Report the bandwidth, model, uncertainty method, and sensitivity of the estimate; do not rely on a small standard error from an independence assumption that the data do not support.

Worked Example: A Coincident Event Prevents Attribution

Suppose a hypothetical policy starts on day $c$, and a separate outreach campaign also begins that day. The outcome is monthly enrollment per 10,000 residents. Local trend fits estimate a left limit of 40 and a right limit of 47, so the observed discontinuity is $$ 47-40=7 $$ additional enrollments per 10,000 residents.

The seven-unit jump is the combined observed change. If the outreach campaign independently adds 3 enrollments per 10,000 at the cutoff, then the policy contribution would be $7-3=4$, but the data described do not establish that the campaign effect is 3. Without additional credible information or variation separating the two events, the policy effect is not identified: many allocations of the seven-unit jump between the policy and campaign fit the same observed discontinuity.

The appropriate conclusion is that enrollment rose by an estimated 7 per 10,000 at the coincident changes, not that the policy caused an increase of 7. A different comparison, external information about the campaign, or another design may help, but merely adding a time trend does not separate two changes that occur at the same cutoff.

What the Design Can and Cannot Establish

Temporal regression discontinuity is related to interrupted time series, which also studies outcome trajectories before and after an intervention. The distinction is one of emphasis: a temporal RD targets the limiting jump at a known date under local continuity conditions, whereas an interrupted time-series analysis commonly models changes in level and slope over a broader span. A short local window can reduce reliance on a long-run trend model but may be vulnerable to sparse data and date-specific shocks. A broader series can show longer patterns but requires stronger modeling of trends and seasonality.

A geographic regression discontinuity uses proximity to a spatial boundary; a temporal design uses proximity in calendar time. Both rely on continuity of expected potential outcomes at a cutoff, but time has distinctive threats: seasonality, serial dependence, anticipation, and concurrent events. Neither design makes treatment randomly assigned merely because observations are close to a boundary or date. Matching, covariate adjustment, or a more elaborate trend specification can improve comparability only under their own assumptions; they do not repair an unmeasured discontinuity at the cutoff.

The effect is local to the policy date and the population represented by observations near that date. It need not equal the policy's long-run effect, its effect in other locations, or its effect under a different implementation. If treatment uptake is not deterministic at the policy date, a simple sharp-design jump is not the treatment effect; the fuzzy regression discontinuity framework is needed to interpret the change in outcomes relative to the change in treatment uptake.

Common Mistakes

Using an inconsistent time coordinate. With calendar time $t$, the cutoff is $c$ and $Z_t=1(t\geq c)$. With centered running time $x=t-c$, the cutoff is zero and the indicator is $1(x\geq0)$.
Assuming untreated continuity is sufficient. Identification also requires the treated potential-outcome mean to have the appropriate right limit at $c$, as well as no competing discontinuity.
Calling any before-and-after change a policy effect. A concurrent event or measurement change can generate the same jump. Establishing timing alone does not separate causes.
Assuming a calendar adjustment proves validity. Weekday or seasonal controls address modeled patterns, not unmeasured events that coincide with the cutoff.
Ignoring anticipation or serial dependence. Responses before the effective date compromise the untreated comparison; correlated observations can make ordinary independent-observation uncertainty estimates too small.

Key takeaway: A temporal discontinuity identifies a policy effect at the cutoff only when both potential-outcome means evolve continuously there, the policy is the only discontinuous cause, and pre-cutoff outcomes are not already affected by anticipation. Calendar controls and diagnostics can probe these conditions but cannot guarantee them.

Check Your Understanding

Answer each question, then compare with the solutions below.

If $t$ is calendar time and the policy starts at $c$, write the treatment indicator and the centered running time.
A fitted left limit is 22 and a fitted right limit is 27 cases per 1,000 residents. What is the estimated discontinuity, and what does it mean before causal assumptions are assessed?
Why must continuity be required for both expected potential outcomes, not only the untreated outcome?
A policy is announced three weeks before its effective date, and the outcome begins changing after the announcement. Name the central threat and explain why a clean jump at the effective date may not capture the policy's full effect.
A second intervention starts on the policy date. Can the observed jump alone identify the first policy's effect? Explain.

Solutions. (1) $Z_t=1(t\geq c)$ and $x=t-c$. (2) The estimate is $27-22=5$ cases per 1,000 residents; it is the fitted right-minus-left change at the cutoff, not necessarily a causal effect. (3) The right-hand observed limit must equal the treated potential-outcome mean at $c$, while the left-hand limit equals the untreated mean there. Continuity of both is needed for their difference to equal the effect at $c$. (4) Anticipation may affect outcomes before the effective date, so the pre-cutoff observations may no longer represent a no-policy trajectory; the date of announcement may be the first relevant exposure. A jump at implementation can omit earlier effects. (5) No. The observed jump combines the effects of both interventions and any other coincident discontinuities, so the first policy's contribution is not separately identified from that jump alone.