7 Event Studies
The canonical DiD design compares treated and control units before and after treatment, in its simplest form using two groups and two periods. But many real policy settings are richer. Units may be treated at different times, treatment effects may evolve gradually, and researchers may want to know not only whether a policy had an effect, but also when the effect appeared and how it changed over time.
This is the main motivation for event-study designs. In this chapter, the term event study refers to modern DiD-based approaches that estimate treatment effects relative to the timing of an event, such as the adoption of a reform, the introduction of a policy, or the occurrence of a shock.1
1 The term event study is also used differently in other fields. In finance, for example, traditional event studies typically measure abnormal stock returns around a specific event by comparing observed returns with the returns predicted by a model of normal market performance. This differs from the DiD-based event-study designs discussed here, which compare outcome dynamics across groups relative to the timing of treatment.
Event studies organize estimates in event time: periods before and after the treatment starts.
Event studies are especially useful when treatment adoption is staggered. Some units receive treatment early, others later, and some may never be treated. Instead of estimating a single average treatment effect, event-study methods estimate dynamic effects at different horizons relative to treatment.
Recent econometric work has shown that standard TWFE event-study regressions can be misleading when treatment effects are heterogeneous across groups or over time. This chapter focuses on the logic of modern DiD event-study estimators, drawing on recent guides to the literature (Baker et al. 2026; Chaisemartin and D’Haultfœuille 2026; Roth et al. 2023).
7.1 The Evaluation Problem
Suppose we observe units \(i=1,\ldots,N\) over periods \(t=1,\ldots,T\). Some units become treated at different times. Once treated, they remain treated in all later periods. This is the common case of staggered adoption.
Let \(G_i\) denote the first period in which unit \(i\) is treated. For never-treated units, let \(G_i=\infty\). Let \(t\) denote calendar time. The treatment indicator is
\[ D_{it}=\mathbb{1}\{t\geq G_i\}. \]
Let \(\mathcal{G}\) denote the set of observed treatment cohorts, excluding never-treated units. Under consistency, the observed outcome is
\[ Y_{it}^{obs}=Y_{it}(G_i). \]
For brevity, the superscript \(obs\) is omitted below and the observed outcome is written simply as \(Y_{it}\).
The central object is often a group-time average treatment effect:
\[ ATT(g,t) = E\left[Y_{it}(g)-Y_{it}(\infty)\mid G_i=g\right], \qquad t\geq g. \]
Here, \(G_i=g\) means that unit \(i\) first receives the treatment in period \(g\). The term \(Y_{it}(g)\) is the potential outcome of unit \(i\) at time \(t\) if it first received the treatment in period \(g\), while \(Y_{it}(\infty)\) is the potential outcome at time \(t\) under the never-treated regime. The parameter \(ATT(g,t)\) therefore measures the average effect, at time \(t\), for the group of units first treated in period \(g\).
Once we have group-time effects, we can aggregate them in different ways:
- by treatment cohort;
- by calendar period;
- by event time;
- into an overall average treatment effect on the treated.
The key point is that the estimand must be explicit. A single coefficient can hide many different treatment effects.
7.2 Event Time
For an ever-treated unit, event time measures the distance from its treatment date:
\[ \ell_{it}=t-G_i. \]
For units belonging to cohort \(g\), this becomes
\[ \ell=t-g. \]
When \(\ell=0\), the unit is in its first treated period; when \(\ell=1\), it is one period after treatment onset; and when \(\ell=-1\), it is one period before treatment.
Event time is not defined for never-treated units because they do not have a treatment date. These units may nevertheless contribute as controls when cohort-specific effects are estimated.
Throughout this chapter, \(ATT^{ES}(\ell)\) denotes an aggregate post-treatment effect at event time \(\ell \geq 0\), where the superscript \(ES\) stands for event study. Pre-treatment diagnostic estimates are denoted separately by \(\pi_{\ell}\) for \(\ell < -1\), where \(\ell=-1\) is used as the reference period.2 The sample estimates are written as \(\widehat{ATT}^{ES}(\ell)\) and \(\widehat{\pi}_{\ell}\), respectively.
2 The reference period is the period against which all event-study estimates are compared. Its coefficient is normalized to zero, so each estimated coefficient measures the difference relative to that period. Using \(\ell=-1\) means that the period immediately before treatment serves as the baseline.
The pre-treatment estimates are useful diagnostics. Since treatment has not yet occurred, they should generally be close to zero, unless units anticipate the treatment or treated and control units were already following different trends.
The post-treatment estimates describe treatment dynamics. The effect may appear immediately, grow over time, fade out, or even change sign.
The right-hand graph of Figure 7.1 provides a typical example of an event-study plot, showing pre-treatment diagnostic estimates and post-treatment dynamic effects, usually with confidence intervals and a vertical line at the treatment date. This visual representation makes the results particularly immediate and easy to interpret, allowing researchers to assess both pre-treatment patterns and the evolution of treatment effects at a glance. This transparency has likely contributed to the widespread adoption of event-study designs in applied research.
7.3 Why Not Just Use TWFE?
A traditional event-study regression is often written as
\[ Y_{it} = \alpha_i+\lambda_t + \sum_{\substack{\ell\in\mathcal{L}\\ \ell\neq -1}} \beta_{\ell} \mathbb{1}\{G_i<\infty,\ t-G_i=\ell\} + u_{it}. \]
Here, \(\mathcal{L}\) is the set of event-time horizons included in the regression, \(\alpha_i\) are unit fixed effects, \(\lambda_t\) are time fixed effects, and the period just before treatment, \(\ell=-1\), is omitted as the reference period. The coefficients \(\beta_{\ell}\) describe outcome differences at each event-time horizon relative to the omitted period. They should not be confused with the modern event-time aggregates \(ATT^{ES}(\ell)\) defined below. Under staggered adoption and heterogeneous effects, \(\beta_{\ell}\) need not identify a clean weighted average of causal effects.
This specification is intuitive, but it can be problematic under staggered adoption as we have already seen at the end of Chapter 6. To avoid such identification issues, modern event-study methods construct comparisons more carefully as shown below.
7.4 Clean Comparisons
The safest comparisons are usually those between newly treated units and units that are still untreated at the same calendar time, either because they will be treated later or because they remain untreated throughout the analyzed period.
Suppose one group is first treated in period \(g\). To estimate its effect at time \(t\geq g\), we compare the change in outcomes for this group with the change in outcomes for units that are valid controls for cohort \(g\) at time \(t\).
The identifying assumption is a modified version of the parallel trends assumption:
\[ E\left[Y_{it}(\infty)-Y_{i,g-1}(\infty)\mid G_i=g\right] = E\left[Y_{it}(\infty)-Y_{i,g-1}(\infty)\mid C_i(g,t)=1\right], \]
where \(C_i(g,t)=1\) denotes units that form a valid comparison group for cohort \(g\) at time \(t\), such as never-treated units or not-yet-treated units.
In words, absent treatment, the treated cohort and its comparison units would have experienced the same outcome change between the baseline period and time \(t\).
When not-yet-treated units are used as controls, a no-anticipation assumption is also needed. It ensures that, before their own treatment begins, their observed outcomes coincide with the outcomes they would experience under the never-treated regime.
\[ Y_{it}(g)=Y_{it}(\infty) \qquad \text{for } t<g. \]
This logic underlies several modern DiD estimators.
7.5 Weighted Difference-in-Differences
Callaway and Sant’Anna propose a framework that estimates group-time treatment effects and then aggregates them (Callaway and Sant’Anna 2021). The first step is to estimate \(ATT(g,t)\) for each treatment cohort \(g\) and post-treatment period \(t\geq g\). The second step is to combine these effects using transparent weights.
This approach makes clear which treated group is being compared with which control group, and how the final estimate is constructed.
The comparison group can be defined in two main ways:
- never-treated units, namely units that are never exposed to the treatment during the observation period;
- not-yet-treated units, namely units that have not yet received the treatment at time \(t\), even if they will receive it later.
In staggered-adoption designs, not-yet-treated units can be attractive comparison units because they are scheduled to receive the treatment later. This often makes them more comparable to already-treated units than never-treated units, both in observed characteristics and in unobserved factors related to treatment adoption.
However, not-yet-treated units can serve as “clean” controls only up to the point at which they receive treatment. After that, their outcomes may reflect treatment effects, and using them as controls can bias ATT estimates in later periods by design.
There is therefore a trade-off between using not-yet-treated units and restricting the control group to never-treated units. Using not-yet-treated units enlarges the pool of available controls and may provide more comparable units, but each of these units can serve as a control only until it becomes treated. As treatment adoption progresses, the composition of the control group therefore changes over time. Restricting the analysis to never-treated units instead provides a stable group that remains unaffected by treatment throughout the analyzed period. However, this group may be smaller and systematically different from the treated units, making the parallel-trends assumption less plausible. Neither choice is inherently preferable: researchers should make clear which units serve as controls at each point in time and assess whether they provide a credible comparison for the treated units.
In both cases, the comparison can also be adjusted for observed covariates. This means that treated units in cohort \(g\) are compared with control units that are similar in terms of pre-treatment characteristics, rather than being compared mechanically with all available untreated units.
Once the group-time effects have been estimated, they can be aggregated into event-time effects. This produces the event-study plot, but without relying on TWFE comparisons that may be contaminated by already-treated units.
Estimate treatment effects separately by cohort and period, then aggregate them using explicit weights. In the Callaway and Sant’Anna framework, these weights are transparent and are typically linked to the number of treated units contributing to each group-time effect. This makes the final estimate easier to interpret than a single TWFE coefficient, because we can see which cohorts and time periods contribute to the aggregate effect, and how much they contribute.
7.6 Multiple Difference-in-Differences
de Chaisemartin and D’Haultfoeuille develop related estimators that also avoid problematic TWFE comparisons (Chaisemartin and D’Haultfœuille 2020, 2026).
The broad idea is to build treatment-effect estimates from clean DiD comparisons. Rather than allowing the regression to implicitly choose comparisons and weights, the method constructs comparisons between units whose treatment status changes and appropriate control units whose treatment status does not change over the relevant interval.
This family of estimators is useful because it emphasizes a practical lesson: with staggered adoption, the researcher should know which comparisons identify the effect.
In applications, these estimators often report dynamic effects, showing how the outcome changes in the periods following treatment.
Both approaches address the same problem: with staggered adoption and heterogeneous treatment effects, TWFE regressions may use problematic comparisons, especially comparisons involving already-treated units.
The Callaway and Sant’Anna approach is organized around group-time treatment effects, \(ATT(g,t)\). Units are grouped by the period in which they first receive treatment, and the effect is estimated for each cohort \(g\) and post-treatment period \(t\geq g\), using never-treated or not-yet-treated units as controls. These \(ATT(g,t)\) parameters can then be aggregated into overall effects or event-study effects using explicit weights.
The de Chaisemartin and D’Haultfoeuille approach is organized more directly around clean DiD comparisons. The key idea is to compare units whose treatment status changes, called switchers, with units whose treatment status does not change over the same interval. This perspective is especially useful for understanding which comparisons identify the effect and for extending DiD logic beyond the simplest staggered binary-treatment setting.
In short, Callaway and Sant’Anna start from cohort-time causal parameters and then aggregate them. de Chaisemartin and D’Haultfoeuille start from valid treatment-status changes and build the estimator from those clean comparisons.
7.7 Matching DiD for Panel Data
Another approach is to combine matching with DiD. The basic matching DiD estimator, already presented in Chapter 6, uses matching to account for observed differences between treated and control units and differencing to account for time-invariant unobserved differences (Heckman et al. 1997).
Imai, Kim, and Wang extend this logic to time-series cross-sectional (TSCS) data3 through PanelMatch (Imai et al. 2023), a non-parametric matching approach that provides an alternative way to estimate the dynamic treatment effects typically displayed in event-study analyses. The method constructs matched sets for treated observations using their pre-treatment histories.
3 TSCS data have essentially the same two-dimensional structure as panel data: multiple units are observed repeatedly over time. The term TSCS is especially common in political science, often for aggregate units such as countries, states, or municipalities observed over a relatively long time span. There is no sharp boundary between TSCS and panel data.
The procedure can be summarized in four steps:
- For each treated unit-period, construct an initial set of eligible controls observed at the same time through exact matching, requiring controls to have the same treatment history over a chosen number of pre-treatment periods and, when appropriate, the same values of selected covariates.4
- Refine this initial matched set by selecting or reweighting controls to improve balance in pre-treatment outcomes and covariate histories.
- Use the resulting matched controls to construct counterfactual outcomes for the treated observations.
- Estimate treatment effects over different post-treatment horizons.
4 Exact matching requires treated and control observations to have exactly the same values for the variables on which the restriction is imposed. For example, a treated municipality may be compared only with municipalities in the same region or population category. This differs from matching methods that allow controls to be similar, but not identical, on these characteristics.
This approach is attractive because it makes the construction of the control group transparent. It also allows researchers to inspect balance not only in baseline covariates, but also in lagged outcomes and covariate histories.
PanelMatch asks: for each unit at the moment it becomes treated, can we find units that are still untreated and have a similar recent history in terms of treatment status, pre-treatment outcomes, and covariates?
7.8 Dynamic Treatment Effects
Event studies are valuable because treatment effects may not be instantaneous.
For example, a reform allowing election-day registration may affect turnout immediately. A labor-market shock may reduce employment quickly but generate longer-run adjustment. A mass layoff may affect local employment for many years. A democratization episode may affect economic growth gradually.
For post-treatment horizons, dynamic treatment effects can be summarized by event-time effects:
\[ ATT^{ES}(\ell) = \sum_{g\in\mathcal{G}_{\ell}} \omega_{g\ell}ATT(g,g+\ell), \qquad \ell\geq0, \]
where \(\mathcal{G}_{\ell}\) is the set of cohorts for which calendar time \(g+\ell\) is observed and a valid comparison group is available. The aggregation weights satisfy
\[ \omega_{g\ell}\geq0 \quad\text{and}\quad \sum_{g\in\mathcal{G}_{\ell}}\omega_{g\ell}=1. \]
The weights determine how much each contributing cohort matters for the event-time effect. A natural, and generally preferable, choice is to weight cohorts in proportion to their size, so that the aggregate effect reflects the relative number of treated units represented by each cohort. The corresponding sample estimate is denoted by \(\widehat{ATT}^{ES}(\ell)\).
The event-study plot then becomes a compact visual summary of both pre-treatment diagnostics and post-treatment dynamics.
7.9 Pre-Trends and Anticipation
For pre-treatment periods before the reference period, \(\ell<-1\), let \(\pi_{\ell}\) denote an aggregated pre-treatment placebo contrast. Its exact construction depends on the estimator, but it compares the pre-treatment evolution of future-treated cohorts with that of their comparison units. These quantities are not ATT parameters because treatment has not yet begun.
Pre-treatment event-time estimates are often interpreted as tests of the parallel-trends assumption. This interpretation should be cautious.
If estimates before treatment are far from zero, this is a warning sign. Treated units may have been on different trends, or the policy may have been anticipated before formal implementation.
If pre-treatment estimates are close to zero, this supports the design, but it does not prove parallel trends. The counterfactual post-treatment trend remains unobserved.
Anticipation is especially important in event studies. If units change behavior before the treatment date because they expect the policy, then periods just before treatment are no longer untreated in a substantive sense.
Too much emphasis is often placed on whether pre-treatment event-study estimates are statistically significant. Failure to reject zero is not evidence that departures from parallel trends are negligible. Wide confidence intervals can include both zero and differences large enough to undermine the causal interpretation. This reflects low statistical power, not necessarily a credible comparison group.
For a stylized example, suppose an employment-rate pre-treatment contrast is estimated at zero, with a 95% confidence interval from -5 to +5 percentage points. It is not statistically significant, but it does not rule out substantial pre-treatment divergence. That uncertainty is particularly concerning if the estimated post-treatment effect is only two percentage points. The comparison is a diagnostic warning, not a direct calculation of post-treatment bias.
Bilinski and Hatfield (2026) propose a non-inferiority/equivalence approach: ask whether the data can rule out violations large enough to matter, using a substantively justified threshold. The practical lesson is to assess the magnitude and precision of pre-treatment estimates, not simply whether their intervals contain zero.
Even precise evidence of similar pre-treatment trends cannot establish that untreated trends would have remained parallel after treatment. Institutional reasoning and sensitivity analysis remain essential.
7.10 Choosing the Baseline Period
Regression-based event studies require a reference period. A common choice is the period just before treatment, \(\ell=-1\). In group-time DiD estimators, period \(g-1\) similarly often serves as the baseline from which outcome changes are measured, although it is not itself an event-time treatment effect. In regression-based event studies, this period is omitted from the specification and all coefficients are interpreted relative to it. In group-time DiD estimators, the same logic appears through the baseline period (g-1), which is used to construct the relevant outcome changes. The baseline period is therefore not an estimated treatment effect; it is either omitted from the plot or shown as a normalized zero.
7.11 Aggregation
Modern DiD event-study methods often begin with many building blocks: effects by cohort, calendar time, and event time. The final estimate depends on how these building blocks are aggregated.
Aggregation is not a purely technical detail. Different weights answer different questions.
For example:
- equal weights across cohorts answer a cohort-balanced question;
- weights proportional to cohort size answer a population-weighted question;
- event-time weights describe the average effect at a given horizon after treatment;
- calendar-time weights describe the average effect in a given period.
Baker et al. emphasize that applied researchers should be explicit about the target parameter and the weights used to construct it (Baker et al. 2026).
7.12 How event-study plots are computed
In staggered-adoption designs, event-study plots are not based on a single comparison between one treated group and one control group. They are built from many smaller cohort-time comparisons. Post-treatment comparisons identify causal effects under the assumptions discussed above; pre-treatment comparisons are diagnostic placebo checks.
The post-treatment building blocks are the group-time treatment effects, denoted by \(ATT(g,t)\). Each \(ATT(g,t)\) measures the average effect at calendar time \(t\geq g\) for the cohort of units first treated in period \(g\). Pre-treatment points are constructed from the corresponding placebo contrasts rather than from ATT parameters.
Once these effects are estimated, they can be reorganized in event time, where event time is defined as
\[ \ell = t-g. \]
For example, \(\ell=0\) is the first treated period, \(\ell=1\) is one period after treatment, and \(\ell=-1\) is one period before treatment. For \(\ell\geq0\), the event-study plot reports \(\widehat{ATT}^{ES}(\ell)\), obtained by aggregating the available \(ATT(g,g+\ell)\) values as defined above. For pre-treatment periods before the reference period, \(\ell<-1\), the plot reports the diagnostic estimate \(\widehat{\pi}_{\ell}\). The reference period, \(\ell=-1\), is normalized to zero and is not estimated separately.
This construction is useful because it summarizes many cohort-specific comparisons in a single graph. Instead of reporting a separate estimate for every cohort and calendar period, the event-study plot shows pre-treatment diagnostics and how treatment effects evolve after treatment.
However, this convenience comes with an important caveat: the set of cohorts contributing to the plot may change across event-time horizons. Early pre-treatment periods are observed only for cohorts treated sufficiently late, while long post-treatment horizons are observed only for cohorts treated sufficiently early.
For example, suppose the panel begins in period 1, one cohort is first treated in period 3, and another is first treated in period 4. At event time \(\ell=-3\), the cohort treated in period 3 cannot contribute because this would require an observation in period 0. The cohort treated in period 4 can contribute because \(4-3=1\), which is observed. Similarly, long-run post-treatment effects may be based only on early-treated cohorts.
This changing composition matters. If cohorts differ systematically, changes in the event-study profile may reflect not only dynamic treatment effects, but also changes in which cohorts are included at each horizon. A rising or falling event-study line can therefore partly reflect treatment dynamics and partly reflect sample-composition changes.
For this reason, event-study plots should be interpreted with care. Researchers should report which cohorts contribute to each event-time estimate, whether the sample changes across horizons, and whether results are robust to using a balanced event window. A balanced event window restricts the analysis to cohorts observed for the same set of pre- and post-treatment periods. This improves comparability across event time, but it may discard many cohorts and reduce precision.
A classic application of event-study methods is Wolfers’ analysis of unilateral divorce laws in the United States (Wolfers 2006). We already introduced this application in Chapter 6 to illustrate the logic of DiD. Here, we return to the same setting from an event-study perspective, focusing on how the effects evolve relative to the timing of policy adoption.
The setting is well suited to an event-study design because U.S. states adopted unilateral divorce laws in different years. This staggered timing makes it possible to compare the evolution of divorce rates before and after adoption across different groups of states. The event-study framework is especially useful because the effect of the reform need not be immediate or constant over time. Divorce rates may respond gradually after the law changes, and the effect may increase, decline, or disappear several years after adoption.
The application also illustrates why modern DiD methods are needed in staggered-adoption settings. If treatment effects vary across cohorts or over time, a simple TWFE event-study regression may combine comparisons that are difficult to interpret, including comparisons between newly treated states and states that were already treated. Modern estimators instead make the comparison more explicit: they compare states adopting the reform at a given time with states that are not yet treated or never treated, and then aggregate the resulting cohort-time effects using transparent weights.
7.13 Diagnostics and Validity Checks
A credible event-study analysis should report:
- the timing of treatment adoption across units;
- which units are used as controls at each horizon;
- whether treatment is absorbing or can turn on and off;5
- whether never-treated and/or not-yet-treated units are used;
- event-time plots with confidence intervals;
- whether anticipation or carryover effects are plausible;6
- how group-time effects are aggregated.
5 An absorbing treatment is one that, once adopted, remains in place in all subsequent periods. By contrast, a non-absorbing treatment can switch on and off over time, so the same unit may move between treated and untreated states.
6 Carryover effects occur when treatment continues to affect outcomes even after it has ended. In this case, a unit that is currently untreated may still be influenced by its past treatment exposure, complicating the definition of a clean control period.
The treatment variation plot is often useful. It shows when units become treated and whether enough untreated or not-yet-treated units remain available as controls at each point in time.
7.14 Worked Example
Suppose some regions introduce a new active labor-market policy in different years. Once introduced, the policy remains in place. We observe employment rates for all regions over time.
A simple TWFE regression would compare all treated and untreated observations while absorbing region and year fixed effects. But if early-treated regions are later used as controls for late-treated regions, and if the policy effect evolves over time, the estimate may be misleading.
A modern event-study approach would instead proceed as follows:
- Group regions by the year in which they first adopt the policy.
- For each treated cohort and each post-treatment year, compare the cohort with regions not yet treated or never treated.
- Estimate cohort-time effects.
- Aggregate these effects by event time.
- Plot pre-treatment diagnostics and post-treatment dynamic effects.
If the pre-treatment estimates are close to zero and the post-treatment estimates increase gradually, the evidence would be consistent with a positive employment effect that emerges over time. By contrast, if the estimates are already increasing before treatment begins, the credibility of the design would be weakened.
In a 2025 LinkedIn post titled Event Studies Madness, I construct a deliberately implausible event study. The performance of eight Italian Serie A teams qualifying for European competitions is compared with that of eight successful Serie B teams. The two groups display remarkably similar pre-treatment trends in points, while their outcomes diverge after European competitions begin. Taken mechanically, the resulting event-study plot would suggest that participation in European competitions increases domestic-league performance.
The conclusion is clearly not credible. Serie A and Serie B teams differ substantially in budgets, player quality, competitive environment, and many other characteristics. Similar outcome trends over a short pre-treatment period do not make these teams valid counterfactuals for one another.
The example illustrates an important limitation of event-study diagnostics: pre-treatment estimates close to zero do not prove that the parallel-trends assumption is valid. They show only that treated and control units followed similar trends before treatment, whereas the key assumption concerns the counterfactual post-treatment period, namely how treated outcomes would have evolved relative to control outcomes after treatment, in the absence of treatment. Pre-treatment estimates are therefore useful diagnostic evidence, but they cannot replace a substantive justification of the comparison group. Researchers should always explain why treated and control units are likely to be exposed to comparable underlying dynamics, examine differences in relevant pre-treatment characteristics, and discuss institutional reasons why their outcomes would have evolved similarly in the absence of treatment.
7.15 Summary
Event studies extend DiD by organizing effects around the timing of treatment. They are especially useful for staggered adoption and dynamic treatment effects.
The lesson of recent years is that event-study estimates should not be produced mechanically using TWFE regressions. In particular, when treatment adoption is staggered and treatment effects are heterogeneous, TWFE estimators may rely on problematic comparisons and assign implicit weights that complicate the interpretation of the estimated effects.
Modern event-study estimators instead build effects from clearer comparisons, such as treated cohorts versus not-yet-treated or never-treated units, and then aggregate group-time effects transparently. The central questions are: what is the comparison group, what is the target estimand, and how are the dynamic effects aggregated?
Several software packages can be used to implement DiD and event study designs.
- R
did: implementation of Callaway and Sant’Anna-type DiD estimators for multiple periods and staggered treatment adoption.DIDmultiplegtDYN: implementation of de Chaisemartin and D’Haultfoeuille-type DiD estimators for dynamic and potentially complex treatment designs.HonestDiD: sensitivity analysis for violations of parallel trends.PanelMatch: tools for non-parametric DiD with comparison groups constructed on the basis of treatment histories and pre-treatment outcomes (Imai et al. 2023).
- Python
pyfixest: Python implementation inspired byfixest, useful for fixed-effects and event-study specifications.differences: Python package implementing DiD estimators for multiple periods and staggered treatment adoption.diff-diff: Python library for difference-in-differences, event-study, and related DiD designs.
- Stata
csdid: Stata command implementing Callaway and Sant’Anna-type DiD estimators for multiple periods.did_multiplegt_dyn: Stata command implementing de Chaisemartin and D’Haultfoeuille-type dynamic DiD estimators.eventstudyinteract: implements interaction-weighted event-study estimators.
For a more detailed overview of available DiD software packages, see Asjad Naqvi’s online guide.