DiD with Intertemporal Treatment Effects#

The didinter module implements the difference-in-differences methodology for settings where lagged treatments may affect current outcomes, based on the work of de Chaisemartin and D’Haultfœuille (2024). This approach addresses the challenges of estimating treatment effects when the treatment is potentially non-binary, non-absorbing, and when treatment history matters for current outcomes.

When Intertemporal Effects Matter#

Standard DiD methods typically assume that only contemporaneous treatment affects outcomes. However, many real-world treatments have effects that persist and accumulate over time. A policy implemented today may continue to affect outcomes for months or years afterward. When such dynamic effects are present, failing to account for them can lead to biased estimates of treatment effects.

Consider a panel of groups observed over multiple time periods where treatment can vary in intensity and can increase or decrease over time. Examples include state-level policy changes where intensity varies, dosage effects in medical treatments, or regulatory changes that can be strengthened or relaxed. In these settings, a group’s outcome at time \(t\) may depend not only on its current treatment but also on its entire treatment history.

This methodology is particularly valuable when the treatment is non-binary (taking on multiple values rather than just 0 or 1), non-absorbing (groups can leave treatment or have treatment intensity change in either direction), or when there is reason to believe that treatment effects accumulate or decay over time. The DID estimators developed in this framework are applicable to any design where some groups maintain their initial treatment level for at least a few periods, providing valid comparison units.

Setup and Notation#

We consider a panel of \(G\) groups observed at \(T\) time periods. Let \(D_{g,t}\) denote the treatment of group \(g\) at period \(t\), where \(D_{g,t} \geq 0\). Groups may represent states, counties, firms, or even individuals depending on the application. The treatment may be binary or take on multiple values, and may increase or decrease over time.

Using the dynamic potential outcome framework, let \(Y_{g,t}(d_1, \ldots, d_t)\) denote the potential outcome of group \(g\) at time \(t\) if its treatments from period 1 to \(t\) were equal to \((d_1, \ldots, d_t)\). This framework explicitly allows for the possibility that a group’s outcome at \(t\) depends on its entire treatment history, not just its current treatment. The observed outcome is

\[Y_{g,t} = Y_{g,t}(D_{g,1}, \ldots, D_{g,t}).\]

A key quantity is the first period at which a group’s treatment changes from its initial value. Let

\[F_g = \min\{t : t \geq 2, D_{g,t} \neq D_{g,t-1}\}\]

denote the first treatment change for group \(g\), with the convention that \(F_g = T + 1\) if the treatment never changes. The DID estimators use groups whose treatment has not yet changed as comparison groups for those whose treatment has changed.

Design Requirements#

Not every panel with a time-varying treatment fits this framework. Two restrictions on the treatment process are needed, both mild in practice. The first ensures that valid comparison groups exist; the second rules out treatment paths that cross in a way that would invalidate the comparisons.

Design Restriction 1 (Common Baseline Treatment)

There exist groups \(g\) and \(g'\) such that \(D_{g,1} = D_{g',1}\) and \(F_g \neq F_{g'}\).

This restriction has two parts. First, there must exist at least two groups with the same period-one treatment. Second, among groups with the same baseline treatment, there must be variation in when they first change treatment. The restriction rules out designs where treatment is extremely non-persistent (all groups change in period 2) or where there is a universal treatment change affecting all groups simultaneously.

Several common designs automatically satisfy this requirement.

  • Binary staggered (\(D_{g,t} = \mathbf{1}\{t \geq F_g\}\)) where all groups start untreated and some eventually receive treatment.

  • Binary with exit (\(D_{g,t} = \mathbf{1}\{E_g \geq t \geq F_g\}\)) where groups can join and then leave treatment. A special case is one-shot treatment where groups are treated for a single period.

  • Staggered with group-specific intensities (\(D_{g,t} = I_g \mathbf{1}\{t \geq F_g\}\)) where all groups start at zero but treatment doses vary.

  • Zero baseline (\(D_{g,1} = 0\) for all \(g\)) which nests the previous three as special cases.

  • Discrete baseline (\(D_{g,1} \in \{0, 1, \ldots, K\}\)) with unrestricted treatment paths. This allows non-zero initial treatment levels.

The estimators are inapplicable only when treatment is extremely non-persistent (all groups change in period 2) or when there is a universal treatment change affecting all groups at once.

A second design restriction rules out cases where groups cross their baseline treatment in both directions.

Design Restriction 2 (No Crossing)

For all groups \(g\), either \(D_{g,t} \geq D_{g,1}\) for all \(t\), or \(D_{g,t} \leq D_{g,1}\) for all \(t\).

This restriction ensures that treatment effects have a clear interpretation. If a group experiences both higher and lower treatments than its baseline, the resulting effect parameter can be written as a difference between effects of increasing and decreasing treatment, which may have opposite signs. This makes interpretation difficult and violates a “no sign reversal” property. When this restriction fails in the data, one can simply exclude the problematic observations and apply the DID estimators to the remaining sample.

Identifying Assumptions#

Identification relies on two key assumptions that generalize standard DiD assumptions to the dynamic setting.

Assumption 1 (No Anticipation)

A group’s current outcome does not depend on its future treatments. For all groups \(g\) and all treatment sequences \((d_1, \ldots, d_T)\),

\[Y_{g,t}(d_1, \ldots, d_T) = Y_{g,t}(d_1, \ldots, d_t).\]

This assumption rules out anticipatory behavior where units change their outcomes in response to expected future treatment changes. If treatment changes are announced in advance, the treatment timing should be redefined accordingly.

Assumption 2 (Parallel Trends for Same Baseline Treatment)

Groups with the same period-one treatment have the same expected evolution of their status-quo potential outcome. If \(D_{g,1} = D_{g',1}\), then for all \(t \geq 2\),

\[\begin{split}\begin{aligned} &\mathbb{E}[Y_{g,t}(D_{g,1}, \ldots, D_{g,1}) - Y_{g,t-1}(D_{g,1}, \ldots, D_{g,1}) \mid \boldsymbol{D}] \\ &= \mathbb{E}[Y_{g',t}(D_{g',1}, \ldots, D_{g',1}) - Y_{g',t-1}(D_{g',1}, \ldots, D_{g',1}) \mid \boldsymbol{D}]. \end{aligned}\end{split}\]

The status-quo outcome \(Y_{g,t}(D_{g,1}, \ldots, D_{g,1})\) is the counterfactual outcome that would have been observed if the group had maintained its period-one treatment throughout. The assumption requires that this counterfactual outcome evolves in parallel across groups with the same baseline treatment.

This assumption is weaker than requiring parallel trends across all groups regardless of their baseline treatment. To see why, consider groups with a binary treatment where some are initially treated (\(D_{g,1} = 1\)) and some are initially untreated (\(D_{g,1} = 0\)). Requiring parallel trends for the status-quo outcome across both types would imply that in initially-treated groups, the effect of being treated for \(t\) periods equals the effect of being treated for \(t-1\) periods. This rules out both dynamic and time-varying effects, which is rarely plausible.

By restricting comparisons to groups with the same baseline treatment, the identification strategy only requires that the incremental effect of one additional treatment period does not vary across groups with the same baseline. This is compatible with dynamic and time-varying effects.

Parameters of Interest#

The fundamental parameter is the actual-versus-status-quo (AVSQ) effect, which compares a group’s actual outcome to what it would have been under the status-quo counterfactual of maintaining the period-one treatment.

Actual-Versus-Status-Quo Effects#

The basic building block is the effect of a group’s actual treatment path relative to the counterfactual where treatment had stayed at its period-one level. For a group \(g\) whose treatment first changes at period \(F_g\), the AVSQ effect at \(\ell\) periods after \(F_g - 1\) is

\[\delta_{g,\ell} = \mathbb{E}[Y_{g,F_g-1+\ell} - Y_{g,F_g-1+\ell}(D_{g,1}, \ldots, D_{g,1}) \mid \boldsymbol{D}].\]

This parameter captures the expected difference between the group’s actual outcome and its status-quo outcome at period \(F_g - 1 + \ell\). When \(\ell = 1\), this is the effect one period after the first treatment change. When \(\ell = 2\), it is the effect two periods after, and so on.

The AVSQ effect captures the combined impact of all treatment changes from period \(F_g\) through period \(F_g - 1 + \ell\). In binary staggered designs, \(\delta_{g,\ell}\) is simply the effect of having been treated rather than untreated for \(\ell\) periods.

In more complex designs where treatment continues to change, \(\delta_{g,\ell}\) is harder to interpret because the magnitude and timing of increments may vary across groups. If one group receives treatment dose 4 at \(F_g\) and then returns to 0, while another receives dose 2 and then 3, their \(\delta_{g,2}\) values reflect very different trajectories. Still, under Design Restriction 2, \(\delta_{g,\ell}\) is always the effect of having been exposed to a weakly higher (or weakly lower) treatment for \(\ell\) periods.

When the number of distinct treatment trajectories is small relative to the number of groups, one can estimate trajectory-specific versions of the effects, yielding estimates for the average effect of each specific treatment path. This may produce more interpretable results than aggregating across all trajectories.

Event-Study Effects#

To summarize results across groups, we aggregate the group-specific effects into event-study parameters. Let \(S_g = 1\) if the treatment increases at the first change (\(D_{g,F_g} > D_{g,1}\)) and \(S_g = -1\) if it decreases (\(D_{g,F_g} < D_{g,1}\)). The event-study effect at event time \(\ell\) is

\[\delta_\ell = \frac{1}{N_\ell} \sum_{g: F_g - 1 + \ell \leq T_g} S_g \delta_{g,\ell},\]

where \(N_\ell\) is the number of groups for which \(\delta_{g,\ell}\) can be estimated, and \(T_g\) is the last period where valid comparison groups exist for group \(g\).

Multiplying by \(S_g\) ensures that \(\delta_\ell\) can be interpreted as an average effect of having been exposed to a weakly higher treatment dose for \(\ell\) periods. For groups whose treatment increased, their effect enters positively. For groups whose treatment decreased, their effect is negated so that the overall parameter still captures the effect of higher treatment.

Estimation#

The \(\text{DID}_{g,\ell}\) and \(\text{DID}_\ell\) estimators compare the outcome evolution of groups that change treatment to groups that have not yet changed and share the same baseline treatment.

Group-Specific Estimator#

For group \(g\) at event time \(\ell\), the DID estimator is

\[\text{DID}_{g,\ell} = Y_{g,F_g-1+\ell} - Y_{g,F_g-1} - \frac{1}{N_{F_g-1+\ell}^g} \sum_{g': D_{g',1} = D_{g,1}, F_{g'} > F_g-1+\ell} (Y_{g',F_g-1+\ell} - Y_{g',F_g-1}),\]

where \(N_{F_g-1+\ell}^g\) is the number of groups with the same baseline treatment as \(g\) that have not changed treatment by period \(F_g - 1 + \ell\).

This estimator compares the \((F_g - 1)\)-to-\((F_g - 1 + \ell)\) outcome change for group \(g\) against the average outcome change for groups with the same baseline treatment that have not yet experienced any treatment change. Under the identifying assumptions, this comparison identifies the causal effect \(\delta_{g,\ell}\).

Event-Study Estimator#

Individual group effects are often too numerous to interpret directly. Averaging the group-specific \(\text{DID}_{g,\ell}\) across all groups observed at horizon \(\ell\) gives the event-study estimator

\[\text{DID}_\ell = \frac{1}{N_\ell} \sum_{g: F_g - 1 + \ell \leq T_g} S_g \text{DID}_{g,\ell}.\]

Under assumptions 1 and 2, this estimator is unbiased for the event-study effect \(\delta_\ell\). The estimator can be computed for any \(\ell\) from 1 up to the maximum horizon where valid comparison groups exist.

Connection to Callaway and Sant’Anna (2021)#

When all groups have the same period-one treatment (Design 4, including all of Designs 1-3), \(\text{DID}_\ell\) is numerically equivalent to binarizing the treatment (defining it as an indicator for whether the group’s treatment has ever changed) and then computing the Callaway and Sant’Anna (2021) event-study estimator with this binarized treatment. When groups have different period-one treatments, the two estimators differ because Callaway and Sant’Anna compare switchers and non-switchers regardless of their baseline treatment, while \(\text{DID}_\ell\) restricts comparisons to groups with the same baseline. This restriction is what allows \(\text{DID}_\ell\) to remain valid when lagged treatments affect outcomes.

Normalized Effects#

While the event-study effects \(\delta_\ell\) provide reduced-form evidence on treatment effects, they can be difficult to interpret in complex designs where treatment trajectories vary across groups. The framework addresses this by defining normalized versions of these parameters.

Definition of Normalized Effects#

Let

\[\delta_{g,\ell}^D = \sum_{k=0}^{\ell-1} (D_{g,F_g+k} - D_{g,1})\]

denote the total treatment dose received by group \(g\) from \(F_g\) to \(F_g - 1 + \ell\) relative to the status-quo counterfactual. The normalized AVSQ effect is

\[\delta_{g,\ell}^n = \frac{\delta_{g,\ell}}{\delta_{g,\ell}^D}.\]

The normalized event-study effect is a weighted average across groups

\[\delta_\ell^n = \frac{\delta_\ell}{\delta_\ell^D},\]

where

\[\delta_\ell^D = \frac{1}{N_\ell} \sum_{g: F_g - 1 + \ell \leq T_g} |\delta_{g,\ell}^D|.\]

Interpretation as Average of Lag Effects#

The normalized effect has a structural interpretation as a weighted average of the effects of different treatment lags on the outcome. Specifically,

\[\delta_{g,\ell}^n = \sum_{k=0}^{\ell-1} w_{g,\ell,k} s_{g,\ell,k},\]

where \(s_{g,\ell,k}\) is the slope of the potential outcome function with respect to the \(k\)-th treatment lag, and

\[w_{g,\ell,k} = \frac{D_{g,F_g-1+\ell-k} - D_{g,1}}{\delta_{g,\ell}^D}\]

are weights that sum to one and are non-negative under Design Restriction 2.

In binary staggered designs, the normalized effect simplifies to the simple average of the effects of the current treatment and its \(\ell - 1\) first lags. In designs with group-specific treatment intensities, the normalized effect averages the effects of different lags, with each lag’s effect scaled by the treatment intensity. This interpretation makes \(\delta_\ell^n\) more comparable across different values of \(\ell\) than the non-normalized \(\delta_\ell\).

Testing for Constant Effects#

The normalized effects can be used to test whether the current and lagged treatments have the same effect on outcomes. If effects are constant across lags, then \(\ell \mapsto \delta_\ell^n\) should be constant. A test of this null hypothesis provides evidence on whether treatment effects are stable or dynamic over time.

Cost-Benefit Analysis#

Beyond event-study parameters, the framework defines a cost-benefit parameter useful for policy evaluation. Consider a planner comparing the actual treatment allocation to a counterfactual where all groups maintained their period-one treatment. This parameter is

\[\delta = \frac{\sum_{g: F_g \leq T_g} \sum_{\ell=1}^{T_g - F_g + 1} \delta_{g,\ell}}{\sum_{g: F_g \leq T_g} \sum_{\ell=1}^{T_g - F_g + 1} (D_{g,F_g-1+\ell} - D_{g,1})}.\]

This parameter represents the average benefit per unit of treatment administered relative to the status quo. If the treatment cost per unit is \(c\), then the treatment changes were beneficial in monetary terms if \(\delta > c\).

The parameter \(\delta\) has an interpretation as an average total effect per unit of treatment. Each treatment increment at period \(F_g + k\) produces effects not only at that period but also at all subsequent periods up to \(T_g\). The numerator of \(\delta\) sums these total effects across all increments and all groups. The denominator sums all the incremental treatment doses administered. The ratio gives the average total return per unit of treatment, accounting for both immediate and delayed effects. One can divide \(\delta\) by the average number of periods over which each dose’s effect is cumulated to obtain an average per-period, per-dose effect.

The cost-benefit parameter connects to the event-study effects through the relation

\[\delta = \sum_{\ell=1}^{L} w_\ell \delta_\ell,\]

where the weights \(w_\ell\) are non-negative. This shows that \(\delta\) is a weighted average of the event-study effects.

Pre-Treatment Testing#

The identifying assumptions have testable implications that can be assessed using placebo estimators. For a group \(g\) with \(F_g \geq 3\), we can compute

\[\text{DID}_{g,\ell}^{pl} = Y_{g,F_g-1-\ell} - Y_{g,F_g-1} - \frac{1}{N_{F_g-1+\ell}^g} \sum_{g': D_{g',1} = D_{g,1}, F_{g'} > F_g-1+\ell} (Y_{g',F_g-1-\ell} - Y_{g',F_g-1}).\]

This placebo estimator mimics the actual estimator but compares outcome changes in the pre-treatment period, from \(F_g - 1 - \ell\) to \(F_g - 1\), before group \(g\)’s treatment changes. Under the identifying assumptions, the expected value of this placebo is zero. Significant pre-treatment effects suggest potential violations of parallel trends.

The placebo estimators assess whether groups that will change treatment at different times have similar outcome trends before any treatment changes occur. This tests the same parallel trends assumption over the same time horizon that is required for \(\text{DID}_{g,\ell}\) and \(\text{DID}_\ell\) to be unbiased.

Why Standard Approaches Fail#

Beyond the well-known negative weighting problems of TWFE in binary staggered designs (see DiD with Multiple Time Periods), additional issues arise when treatment varies in intensity and past treatments affect current outcomes.

Two-Way Fixed Effects with Treatment Intensity#

In designs without variation in treatment timing, researchers often estimate TWFE regressions with treatment intensity interacted with period fixed effects. While intuitive, these regressions produce weights on individual group effects that depend on each group’s deviation from the mean intensity. The coefficient \(\hat{\beta}_{fe,\ell}\) from such regressions identifies

\[\mathbb{E}[\hat{\beta}_{fe,\ell} \mid \boldsymbol{D}] = \sum_{g: I_g \neq 0} w_g^{fe} \frac{\delta_{g,\ell}}{I_g},\]

where \(I_g\) is group \(g\)’s treatment intensity and the weights \(w_g^{fe}\) can be negative for groups with intensity below the mean. Groups below the mean intensity are effectively used as comparisons, and their effects enter with the opposite sign.

Local-Projection Panel Regressions#

Local-projection regressions of \(Y_{g,t-1+\ell}\) on \(D_{g,t}\) with group and period fixed effects suffer from three distinct problems. First, \(\hat{\beta}_{lp,\ell}\) is contaminated by effects of other exposure lengths. What is supposed to measure the effect of \(\ell\) periods of exposure is actually a mixture of effects from different durations, because some groups with \(D_{g,t} = 1\) started treatment before period \(t\) (so the regression captures more than \(\ell\) periods of exposure for them), while some groups with \(D_{g,t} = 0\) start treatment between \(t+1\) and \(t-1+\ell\) (so the regression captures less than \(\ell\) periods for those “controls”).

Second, for \(\ell \geq 2\) in binary staggered designs, some weights are always negative.

Third, the weights can sum to less than one or even to a negative number. In the banking deregulation application of Favara and Imbs (2015), the weights on \(\hat{\beta}_{lp,4}\) sum to \(-0.018\), meaning that even with perfectly constant treatment effects, the coefficient would have the wrong sign. This is a fundamental misspecification, not a finite-sample issue.

Distributed-Lag Regressions#

Distributed-lag regressions of \(Y_{g,t}\) on the current treatment and its first \(K\) lags with group and period fixed effects also face problems. The coefficient on the \(l\)-th lag estimates a weighted sum where weights may be negative. Even under the strong assumption that the functional form is correctly specified (only the first \(K\) lags matter and they enter additively), each coefficient is contaminated by effects of other lags whenever treatment effects are heterogeneous across groups or time periods.

Asymptotic Properties and Inference#

The DID estimators have well-behaved large-sample properties that support standard inference tools. This section covers the asymptotic distribution, variance estimation, and confidence interval construction.

Asymptotic Normality#

Under standard regularity conditions (independent groups, bounded moments, non-degenerate variances), the DID estimators are asymptotically normal. For each \(\ell\),

\[\sqrt{N_\ell}(\text{DID}_\ell - \delta_\ell) \xrightarrow{d} N(0, \sigma_\ell^2),\]

where the asymptotic variance \(\sigma_\ell^2\) can be consistently estimated using cohort-specific variance estimators.

Confidence Intervals#

Confidence intervals of the form

\[CI_{1-\alpha} = \left[\text{DID}_\ell \pm z_{1-\alpha/2} \frac{\hat{\sigma}_\ell}{\sqrt{N_\ell}}\right]\]

are asymptotically valid. In general, inference is conservative due to the heterogeneity across groups in the i.n.i.d. (independent but not identically distributed) setup. When groups are identically distributed and the treatment path is determined by the baseline treatment and switching behavior, the confidence intervals achieve their nominal coverage asymptotically.

Extensions#

Several extensions to the basic framework are available.

Covariates. The DID estimators accommodate time-varying covariates \(X_{g,t}\) by replacing the equality in Assumption 2 with a version requiring that the status-quo outcome evolution, after removing the component explained by covariate changes \((X_{g,t} - X_{g,t-1})'\theta_{D_{g,1}}\), be parallel across groups with the same baseline treatment. The coefficient \(\theta_d\) is estimated from the subsample of groups with baseline treatment \(d\) that have not yet changed treatment, and outcomes are adjusted before computing the DID comparisons. Time-invariant covariates \(X_g\) can be handled by defining \(X_{g,t} = X_g \times t\), which reduces the assumption to a conditional parallel trends with a linear functional form.

Group-Specific Trends. When units may have different underlying trends, the DID estimators can be extended to allow for group-specific linear trends, estimated from the pre-treatment period.

Heterogeneous Effects. Treatment effects can be estimated separately for subgroups defined by time-invariant covariates, allowing researchers to examine treatment effect heterogeneity across different types of units.

Fuzzy Designs. When treatment varies within groups (e.g., at the individual level within states), the DID estimators extend to fuzzy designs using appropriate aggregation.

Note

For complete theoretical details including proofs, regularity conditions, and additional extensions, see the original paper by de Chaisemartin and D’Haultfœuille (2024).