Why Staggered DiD Can Fail Even When Parallel Trends Holds
July 2026 | Applied Economics | Causal Inference | ← Back to Blog
A staggered rollout can make a standard Difference-in-Differences estimate wrong, even when parallel trends holds perfectly. This post explains why, using the Goodman-Bacon decomposition, and walks through the cohort-based fix proposed by Callaway and Sant'Anna.
Treatment Rarely Happens to Everyone at Once
Treatment does not always happen to everyone at once. A platform update might roll out to different markets over several months. A merger closes on one date for one deal and a different date for another. So might a policy change, introduced region by region rather than everywhere simultaneously. This is staggered treatment timing, and it is closer to the norm in applied work than the clean, single-period treatment assumed in a textbook DiD example.
The temptation is to run standard TWFE anyway. In practice this usually means estimating a two-way fixed effects model, TWFE, with unit and time fixed effects, plus a treatment indicator. The regression runs without complaint and produces a coefficient. The question is whether that coefficient identifies the treatment effect you think it does.
What Goodman-Bacon Showed
Goodman-Bacon (2021) provided the key decomposition. He showed that the standard TWFE estimator in a staggered setting is mathematically equivalent to a weighted average of every possible pairwise 2x2 DiD comparison across all treatment timing groups in the data.
"The standard estimator implicitly compares already-treated units against each other, using earlier-treated units as controls for later-treated ones."
Some of those pairwise comparisons are exactly what you would want: an early-treated group compared against a never-treated group, or a later-treated group compared against units that have not yet been treated. But other comparisons in the decomposition use an already-treated group as the control for a group that is treated even later. In that comparison, the "control" group is not actually untreated. Its own treatment effect may still be evolving, and whatever change is happening in that group gets absorbed into what should have been a clean counterfactual.
Why This Produces Bias, Not Just Noise
De Chaisemartin and D'Haultfœuille (2020) showed why the already-treated-as-control problem is not a minor technical footnote. When treatment effects are heterogeneous, meaning they vary across units or change over time as a treatment matures, the weights attached to these problematic comparisons in the TWFE aggregation can become negative.
A negative weight means that a comparison is subtracted from the overall estimate rather than added to it. If enough of these negative-weight comparisons accumulate, and if the true treatment effects being compared are large enough, the final aggregate TWFE coefficient can end up with the opposite sign from every individual unit's true effect. In the most extreme case, every single unit in the data could have experienced a genuinely positive treatment effect, and the standard TWFE regression could still report a negative overall coefficient. This is not sampling noise. It is a structural property of how the estimator aggregates contaminated comparisons.
The Fix: Cohort-Based Estimation
Callaway and Sant'Anna (2021) proposed a solution that avoids the contamination directly rather than trying to correct for it after the fact. Instead of running one pooled regression across every unit and time period, their approach defines cohorts, groups of units that were all first treated in the same period, and estimates a separate treatment effect for each cohort.
Critically, each cohort-specific estimate is constructed using only never-treated units or not-yet-treated units as the comparison group. Already-treated units are never used as controls for anyone. This eliminates the exact source of contamination that Goodman-Bacon identified, since the comparisons that produced negative weights simply are not permitted in the estimation.
Once each cohort has a clean, credible estimate, the cohort-specific estimates are aggregated using weights appropriate for the question being asked, for example equal cohort weights, population weights, or event-study averages, rather than forcing every observation into a single regression.
Parallel Trends Is Not the End of the Checklist
This is the point that is easy to miss. Even if parallel trends holds, the identification problem is not over in a staggered setting. An already-treated unit can satisfy parallel trends perfectly in its own pre-treatment period. That assumption is about the trajectory before treatment begins. It says nothing about whether that same unit, now already treated, is a valid control for a different unit that has not yet been treated.
If that already-treated unit is serving as a control, its own treatment effect is still unfolding during the period being used as the "control" trend. That is not a clean counterfactual, no matter how well the pre-trends line up. The two questions, does parallel trends hold, and is my control group actually untreated, are separate questions, and a staggered setting is exactly where they can come apart.
The lesson is simple: satisfying parallel trends does not guarantee valid identification under staggered adoption. When treatment timing varies, the choice of comparison group becomes part of the identification strategy itself.
Further Reading
Goodman-Bacon, A. (2021). Difference-in-Differences with Variation in Treatment Timing. Journal of Econometrics, 225(2), 254-277.
de Chaisemartin, C. and D'Haultfœuille, X. (2020). Two-Way Fixed Effects Estimators with Heterogeneous Treatment Effects. American Economic Review, 110(9), 2964-2996.
Callaway, B. and Sant'Anna, P. (2021). Difference-in-Differences with Multiple Time Periods. Journal of Econometrics, 225(2), 200-230.
