WorksEconomics, Econometrics and Finance
How Different are Different Differences-in-Differences? A Large-Scale Meta-Analysis
Abstract
I use AI-assisted replication to assess the empirical importance of negative weights in two-way fixed effects (TWFE) estimation, drawing on 1,346 staggered-adoption specifications from 108 economics papers. TWFE estimates are highly correlated with estimates from modern difference-in-differences methods, with observed sign reversals in 10.8-14.5% of comparisons and greater precision for TWFE. Hierarchical models that account for estimation noise imply a 91-98% correlation between estimands and a 0.6-2.1% probability of obtaining a statistically significant TWFE estimate with the opposite sign from the modern estimand. These findings suggest negative weights may be a less serious problem in practice, and illustrate how AI can support large-scale empirical assessments of new econometric methods.
Introduction
Difference-in-differences (DiD)—one of the most widely used empirical strategies in applied microeconomics [12]—has recently undergone a crisis of faith. In staggered adoption settings, where a binary treatment is received at different calendar dates, the workhorse two-way fixed effects (TWFE) regression estimator is now understood to carry a “negative weights” concern. The concern is that TWFE can implicitly apply non-convex weights to heterogeneous treatment effects when aggregating over event times, potentially leading to sign reversals. Even when all treatment effects are positive, the TWFE estimand can wind up negative—bringing into question the general reliability of the estimator.
This important theoretical development notwithstanding, the actual prevalence and impact of negative weights are ultimately empirical questions. In many staggered adoption settings, TWFE weights may in fact be convex or nearly so. And even given a large share of negative weights, TWFE bias may be minimal when treatment effect variation is small or idiosyncratic. Switching from TWFE to a modern DiD estimator, which targets an unweighted average treatment effect, may then sacrifice the relative precision of regression estimates for robustness to a minor threat of sign reversals or other biases.
This paper studies the empirical importance of negative weights in TWFE estimation, using a large sample of replicated specifications from ten general-interest journals in economics. I first use agentic artificial intelligence (AI) to search 16,094 papers in 2000-2026 for eligible staggered-adoption DiD specifications with public replication archives. This search results in 1,346 replicated specifications from 108 papers, to which I then apply TWFE and a modern estimator. I consider both DiD-averaging (as in Callaway and Sant’Anna [6]), which combines clean event-time DiDs with prespecified convex weights, and imputation (as in Borusyak et al. [4]), which constructs counterfactual outcomes for individual treated units. Comparisons between conventional TWFE estimates and these modern DiD estimators give an indirect test of how much negative weights affect the empirical conclusions.2
Overall, the findings suggest negative weights may be a less serious problem in practice than in theory. TWFE and modern DiD estimates are highly correlated, around 90%, and sign reversals are fairly uncommon. Around 14.5% of TWFE estimates change sign when switching to DiD-averaging; for imputation, this share is 10.8%. Some of this represents noise: shares of sign flips with a statistically significant difference in estimates are a lower 3.5% for DiD-averaging and 2.2% for imputation. DiD-averaging and imputation yield standard errors that are, on average, 47% and 14% larger than TWFE’s. I also find that negative weights are relatively infrequent and tend to make up a small share of the total absolute weight that TWFE applies to treatment effects.
There is, nevertheless, predictable variation in sign reversals. Later publication years (especially 2021 and after) and a paper’s reporting of both TWFE and modern DiD estimators are associated with lower rates of sign reversals. Consistent with econometric theory, specifications with larger always-treated shares exhibit significantly more sign reversals for DiD-averaging while larger never-treated shares predict significantly fewer reversals for imputation. In contrast, journal rank, paper citation counts, and the prominence of specifications show no statistically significant association with sign reversals.
Finally, I use a hierarchical model to estimate the distribution of TWFE and modern DiD estimands while accounting for typically nontrivial estimation error. Model estimates confirm high (91–98%) correlation across estimands and low (5.6–11.5%) prior probabilities of sign reversals. I further use the model to estimate the probability of a “significant” sign reversal: the probability that a true positive (or negative) modern DiD estimand produces a statistically significantly negative (or positive) TWFE estimate. These rates are 2.1% for DiD-averaging and 0.6% for imputation. I obtain similar findings in the baseline Gaussian model and a nonparametric model, both allowing for precision dependence [7].
This paper builds on a recent and impactful econometrics literature studying negative weights and related issues in popular regression estimators. Examples include Goodman-Bacon [13], de Chaisemartin and D’Haultfœuille [10], Sun and Abraham [17], Callaway and Sant’Anna [6], Borusyak et al. [4], Goldsmith-Pinkham et al. (2024), Borusyak and Hull [4], Arkhangelsky et al. [2], Wooldridge [19], and Gardner et al. [11]; see Roth et al. (2023) and Baker et al. [3] for recent reviews. These papers establish important concerns and illustrate their empirical relevance in selected applications. The current paper complements that work with a systematic empirical assessment of the negative weight concern across a large sample of economics papers.3
An important precedent for this paper is Chiu et al. [9], who reanalyze 49 papers published in three leading political science journals during 2017–2023 using heterogeneity-robust estimators, parallel-trends diagnostics, and sensitivity analyses. My analysis covers more papers, journals, and specifications while focusing on staggered adoption settings (which characterize only 13 studies in Chiu et al. [9]). Beyond comparing estimates, I directly measure the prevalence and mass of negative TWFE weights and examine how sign reversals vary with publication timing, treatment composition, and specification characteristics. The estimated model allows us to distinguish between latent estimand reversals and reversals from estimation noise, and to quantify the empirically relevant probability of obtaining a statistically significant wrong-signed TWFE estimate.
Methodologically, this paper shows how modern AI tools can be used to conduct large-scale meta-analyses and explore the empirical content of econometric theory. While recent meta-analyses in economics—such as Meager [14] or Andrews and Kasy [1]—demonstrate the value of synthesizing evidence across studies, many such analyses use relatively small samples of papers that are painstakingly collected and harmonized. I assembled a replication sample of around 100 papers in roughly two weeks on a personal laptop. Human prompting, judgment, and oversight remained essential, but agents performed the bulk of work in reading articles, identifying qualifying specifications, and running and debugging replication code. Similar protocols could make systematic empirical assessments of new econometric methods a more routine complement to theoretical advances, with further advances in AI technology expanding the scale and range of such assessments.4
The rest of this paper is organized as follows. § 2 describes the construction of the replication sample, while § 3 describes the TWFE and modern DiD estimation procedures. § 4 then presents the findings. § 5 concludes.
Sample Construction
Using agentic AI, I searched 16,094 bibliographic records from ten general-interest economics journals since 2000; this count includes nonresearch materials dropped during screening.5 The journals are: the American Economic Review (AER), Econometrica (ECMA), the Journal of Political Economy (JPE), the Quarterly Journal of Economics (QJE), the Review of Economic Studies (REStud), the Review of Economics and Statistics (REStat), the Journal of the European Economic Association (JEEA), the Economic Journal (EJ), the American Economic Journal: Economic Policy (AEJ: Policy), and the American Economic Journal: Applied Economics (AEJ: Applied). Years were dropped prior to a journal’s stated start of a public replication archive; Figure 1 illustrates journal-specific sampling frames.6
Figure 1. Papers in the Replication Sample. Notes: This figure counts papers in the replication sample. The final year includes papers that were published or forthcoming by October 10, 2026. White areas without cell outlines precede the journal search window.
An initial screening dropped nonresearch materials such as journal frontmatter. We (I and the AI agents) used abstracts, keywords, and available article text and replication materials to identify potentially qualifying staggered-adoption specifications. Candidates then received further review of main-text tables, figures, equations, and numerical prose, with qualifying results linked to the corresponding code and data. The agents downloaded any publicly available copies of the article, keeping published versions where available; I manually downloaded the published version of any article or replication code/data requested by the agents for further screening, using valid credentials.
Papers were retained if they satisfied two requirements. First, the paper must report an estimate from an eligible DiD specification in the main text, including tables, figures, and text discussions. Eligible specifications include TWFE, the Callaway and Sant’Anna [6] DiD-averaging estimator, or the Borusyak et al. [4] imputation estimator, used either statically or in an event study, with staggered adoption (i.e. multiple treatment adoption periods).7 To ease comparison across methods, I excluded specifications with time-varying controls, unit trends, or other complications (see Appendix § 7). The second requirement is replicability of an eligible specification. Our replication primarily used public code/data; in some cases, authors provided additional materials from private correspondence. In the vast majority of cases replication was exact; deviations in other specifications are generally small (see again Appendix § 7). We included all eligible and replicable specifications in a paper.
The search concluded with 1,346 specifications across 108 papers, with each journal and almost all years after 2004 represented. Figure 1 shows journal-year paper counts and Appendix Table A1 lists the papers themselves. Column 1 of Table 1 summarizes this sample. Around half of all specifications come from a paper published in the so-called “Top Five” journals (AER, ECMA, JPE, QJE, and REStud), with 51% published in 2021 or later. The average number of citations to a retained paper is 154 (specification-weighted). Around 23% of specifications are event studies; around 24% come from papers that report both TWFE and either a DiD-averaging or imputation estimator.8
| All specifications (1) | DiD-Averaging comparisons (2) | Imputation comparisons (3) | |
| Publication year | 2019.9 | 2020.3 | 2019.9 |
| Published in 2021 or later | 0.507 | 0.555 | 0.519 |
| Reports both TWFE and CSA/BJS | 0.238 | 0.256 | 0.250 |
| Journal rank | 5.448 | 5.535 | 5.360 |
| Top-five journal | 0.498 | 0.461 | 0.494 |
| Paper citations | 154.0 | 158.1 | 167.0 |
| Abstract/intro. prominence | 0.682 | 0.718 | 0.720 |
| Preferred specification | 0.551 | 0.574 | 0.560 |
| Event study | 0.230 | 0.252 | 0.260 |
| Always-treated share | 0.069 | 0.065 | 0.067 |
| Never-treated share | 0.415 | 0.404 | 0.412 |
| Specifications | 1,346 | 925 | 987 |
| Comparisons | – | 1,069 | 1,116 |
| Papers | 108 | 82 | 89 |
Table 1. Replication Sample Summary. Notes: This table summarizes specifications in the replication sample. Column 1 covers all specifications, while columns 2 and 3 cover specifications contributing at least one retained DiD-averaging or imputation comparison, respectively. An event study is counted once even when it contributes both pre- and post-treatment comparisons. Entries other than publication year, journal rank, and citations are proportions. Journal ranks are 1–10 in RePEc order, with 1 denoting the highest standing. The top-five journals are AER, ECMA, QJE, JPE, and REStud. Citations are published-paper OpenAlex counts retrieved October 19, 2026. Reports-both indicates the paper reported both TWFE and either a DiD-averaged or imputation estimator in the main text or appendix. Abstract/introduction prominence indicates that a result is mentioned in either section. In columns 1–3, the preferred specification indicator is nonmissing for 1083, 737, and 786 specifications; the never-treated measure is nonmissing for 1,340, 925, and 987 specifications.
Four other measures were constructed to assess specifications and the potential for sign reversals. The first is an indicator for whether a finding is mentioned in the paper abstract or introduction; Table 1 shows 68% have such prominence. The second is an indicator for whether the specification is “preferred”: either explicitly described in the paper as a baseline, main, or benchmark specification or implicitly judged as one by the AI agents’ full-text review. Among the 1,083 specifications able to be classified in this way, the table shows 55% are preferred. Finally, we construct measures of the share of units in the specification which are always-treated or never-treated. As reviewed below, these shares are expected to drive differences between TWFE and the modern DiD estimators.
Columns 2 and 3 of Table 1 summarize these variables in the subsamples for which direct comparisons between TWFE and one of the two modern DiD estimators can be made. These exclude specifications that yield extremely high-leverage estimates: those with fewer than 10 effective clusters or a maximum cluster share of more than 25%. Such specifications are likely to suffer from unstable estimates and unreliable inference, complicating the analysis. Reassuringly, all specification characteristics are similar in both subsets, which represent large majorities of papers (76% and 82%, respectively). For event studies, we average post-event and pre-event estimates to obtain up to two comparisons per specification.
In total, we obtain 1,069 comparisons between TWFE and DiD-averaging and 1,116 comparisons between TWFE and imputation; see Appendix Table A1 for paper-specific counts. For comparability across specifications, I normalize all outcomes to have unit standard deviation. I next review the estimators and the leading negative-weight concern in TWFE which the modern DiD estimators are designed to address.
TWFE and Modern DiD
For each specification, the TWFE estimate comes from a regression of the form:
Here is the outcome for observation , indexes a stable unit or group, indexes calendar time, is a treatment vector discussed below and contains fixed unit characteristics or subgroup indicators (and may be empty). The and notation accommodates both panels and repeated cross-sections; for a panel indexed by unit and time , we have , , and .9
In static TWFE specifications, is a single indicator that switches on at treatment adoption. For example, Martinez-Bravo et al. (2022) study the effect of introducing village elections in China on outcomes such as public-goods expenditure and exemptions from the one-child policy. Here contains province indicators, allowing for province-specific year effects. In event-study specifications, is a vector of (possibly binned) relative event-time indicators with a reference period omitted. For example, Bailey and Goodman-Bacon (2015) estimate the dynamic effects of establishing community health centers on age-adjusted mortality, using post-establishment coefficients to estimate treatment effects and pre-establishment coefficients to assess pretreatment trends. As noted above, I separately average the available pre- and post-treatment coefficient estimates over common supported windows for the comparisons with modern estimators.
A recent concern with TWFE is the potential for sign reversals: the regression estimand can be negative even when every individual treatment effect is positive, because it can attach negative weights to some treated observations [13, 10]. Formally, under the usual no-anticipation and parallel-trends assumptions (here given ), the static TWFE estimand can be written:
Here is the residual from projecting on all fixed effects and controls while is the causal effect of treatment for observation . Borusyak and Hull [4] call the ex post weights because they depend on realized treatment assignments.10 These weights can be negative because residualized treatment can be negative among treated observations, where . With sufficient treatment-effect heterogeneity, negative weights can place outside the convex hull of the effects. Event-study coefficients can likewise place negative weights on effects at the target relative time and can be contaminated by effects at other relative times [17] (Goldsmith-Pinkham et al. 2024); see Roth et al. (2023) and Baker et al. [3] for more discussion.
The first modern estimator addresses these issues by separately estimating and averaging together conditional DiD contrasts with nonnegative weights, rather than relying on the implicit regression-weighting of TWFE. This DiD-averaging estimator follows Callaway and Sant’Anna [6] while also being close to approaches in de Chaisemartin and D’Haultfœuille [10] and Sun and Abraham [17]. For static specifications, the estimates take the form:
where the are convex weights, proportional to the number of treated observations in adoption cohort and post-treatment period , and are sample-average outcomes for cohort in period and the last observed period before adoption, , and is an estimated counterfactual change in average outcomes without treatment.11 This counterfactual uses units that remain untreated through , including never-treated units, adjusting linearly for the fixed characteristics . Under the no-anticipation and parallel-trends assumptions, the term in parentheses identifies the average treatment effect on the treated (ATT) in period for the cohort first treated in period and identifies the overall average. Event study estimates follow similarly, with cohort-average effects at different horizons first averaged with treated-count weights then averaged together over pre- or post-treatment periods.
The second modern estimator follows the imputation approach of Borusyak, Jaravel and Spiess [4] (see also Gardner et al. [11]). The approach first estimates an untreated-outcome regression model by fitting equation (1) via OLS without any treatment indicators and only on observations before treatment adoption, including any never-treated units. This returns fitted values for all supported treated observations. The estimator is then:
where is the set of supported treated observations. Again, under the no-anticipation and parallel-trends assumptions, this estimates the ATT for supported observations. Post-treatment event-study summaries average the imputed effects at each horizon and then average bin coefficients equally.12
Alongside bias concerns from the potentially-negative weights in TWFE, one may also worry about the relatively higher variance of modern DiD estimators. Indeed, under constant treatment effects and the common identifying assumptions, the three treatment-effect estimands coincide; they can remain close when heterogeneity is small or weakly related to differences in their weights. But TWFE, by using more realized variation in the treatment, will tend to be more precise in these scenarios. I next probe these concerns empirically: first by comparing the , , and estimates themselves, and then via a hierarchical model that can separate estimation noise from true variation in the estimands.
Results
Comparisons
TWFE estimates are highly correlated with modern DiD estimates in this sample. The sample correlation is 0.88 for DiD-averaging and 0.93 for imputation. Correspondingly, sign reversals are relatively infrequent—and especially so with statistically significant estimator differences. Around 14.5% of TWFE estimates change sign with DiD averaging while 3.5% do so with a significant difference. These shares are lower with imputation, at 10.8% and 2.2%. Figure 2 plots the full distribution of estimates.13

Figure 2. Modern Difference-in-Differences vs. Two-Way Fixed Effects. Notes: This figure compares DiD-averaging estimates (as in [6] and imputation estimates (as in [4]) with two-way fixed-effects (TWFE) estimates. Each point is a scalar estimate (circle) or an event-study average (square), including separate pre- and post-treatment averages when available. The samples are described in Table 1. Both coordinates are divided by the TWFE standard error, and the diagonal denotes equal estimates. Filled circles and squares indicate that the estimate difference is statistically significant at the 5% level. Coordinates are capped at ; uncapped values, without standardizing by TWFE standard errors, are used for statistics. “Sign flips” reports the share of pairs with opposite signs; “Significant flips” reports the share with a sign flip and a significant difference.
One likely reason for the infrequency of sign reversals is the relatively small footprint of negative ex post weights. Among static TWFE specifications, the median fraction of treated observation rows with negative ex post weights is approximately 8%, while the median share of absolute effect weight carried by negative weights is only 1.4% (Appendix Figure A3 shows full distributions).14 Hence, while negative weights are theoretically important, their mass is limited in the typical specification.15
The Figure 2 scatterplots also show substantially more dispersion in the DiD-averaging estimates than in the imputation estimates, which are themselves more dispersed than the TWFE estimates. These suggest increased noise, assuming similar estimands, and indeed DiD-averaging and imputation standard errors are on average 47% and 14% larger than corresponding TWFE standard errors. The findings thus illustrate the tradeoff between robustness to the potential bias from TWFE weighting and the relative precision of OLS. The relative precision of imputation vs. DiD-averaging also helps explain its lower rate of sign reversals in Figure 2.
Correlates
TWFE sign reversals have declined over time, particularly after the publication of influential econometrics papers establishing the concern. Figure 3 plots coefficients from regressing sign flip indicators on various specification and paper characteristics; we weight inversely by the TWFE estimate variance (standard error squared), normalized by paper such that each paper receives equal weight. The first two rows show that later publication years are associated with a statistically significantly lower rate of a sign reversal: when moving from TWFE to a DiD-averaging specification, there is a decline of around 13 percentage points per decade and an overall average decline of 14 percentage points for papers published in 2021 and later.16 Trends for imputation are similarly negative, but not statistically significant.17
Figure 3. Correlates of Sign Reversals. Notes: Points are coefficients from separate weighted regressions of sign reversal on each predictor. The first two rows include journal fixed effects; the citation row includes publication-year fixed effects. All other rows have no additional controls. Whiskers are 95% intervals using paper-clustered standard errors. Inverse-squared TWFE standard-error weights sum to one within paper and estimator after each restriction. The sample is as in Figure 2: 1,069 DiD-averaging observations from 82 papers and 1,116 imputation observations from 89 papers. The preferred specification regression instead uses 833 observations from 65 papers in panel A and 867 from 71 in panel B. Journal ranks follow RePEc order, 1–10 from highest to lowest standing. Always-treated and never-treated share coefficients represent associations per 10 percentage points. See Table 1 for other variable definitions.
Over-time declines are consistent with increased awareness of—and endogenous responses to—the TWFE negative weight concern. Another finding consistent with this hypothesis is shown in the third row of Figure 3: papers that report both TWFE and a modern DiD estimator (either from Callaway and Sant’Anna [6] or Borusyak et al. [4]) see a significant 16 percentage point lower probability of sign reversals from DiD-averaging. Again, for imputation this correlation is also negative but insignificant. Of course we cannot rule out the possibility that sign reversals decline for some other reason, such as the increased number of other robustness checks (e.g. pre-trend or subsample analyses).
Cross-sectionally, while sign reversal rates vary across journals, there is no statistically significant association with journal rank. The next two rows of Figure 3 show statistically insignificant coefficients from regression on RePEc journal rankings and an indicator for top-five status. Similarly, the relationship with paper citations is insignificant.18
Furthermore, there is no statistically significant association between sign reversals and whether specifications appear to be more prominent or preferred. The next two rows of Figure 3 show statistically insignificant coefficients on both the indicator for a result being mentioned in the paper’s abstract or introduction and our constructed indicator for a preferred specification. The following row shows that event studies are somewhat less likely to exhibit sign reversals for DiD-averaging, though this coefficient is statistically insignificant.
The final two rows of Figure 3 establish two strong predictors of TWFE sign reversals which are consistent with the econometric theory and easily computed in a specification: the shares of units which are always treated or never treated. Always-treated units generally increase TWFE’s exposure to “forbidden comparisons,” in which already-treated units serve as controls for units newly adopting treatment ([13, 4]). Empirically, I find that a ten percentage point increase in a specification’s always-treated share predicts a statistically significant 6.7 percentage point increase in the rate of sign reversals for DiD-averaging; for imputation, this coefficient is a similar (though not significant) 4.9 percentage points. Never treated units provide “clean controls,” so a larger share of them can reduce exposure to forbidden comparisons. Here for imputation I find a statistically significant reduction of 2.1 percentage points in sign reversals per 10 percentage point increase in the never-treated share; for DiD averaging, this coefficient is also negative but insignificant.
Hierarchical Model
The final set of analyses uses a hierarchical model to characterize the distribution of TWFE and modern DiD estimands, separating variation in estimands from sampling error. The model builds on ones proposed in Chen [7] and Walters [18] in allowing the first and second moments of estimands to depend on estimator precision; in the baseline model, residual variation is modeled as Gaussian.
Specifically, the model uses the usual asymptotic approximation to specify pairs of TWFE and modern DiD estimates for each comparison point as bivariate normal around those specifications’ estimands , with variances given by squared standard errors:
where denotes the estimated variance-covariance matrix for , including the covariance
Notes: This table reports estimates from the Gaussian hierarchical model described in the text. Estimates come from averaging priors over observed standard errors, giving equal weight to each retained comparison point. Standard deviations are in regression-sample outcome standard deviations. A sign reversal is . A significant wrong-signed TWFE estimate is and , where . Parentheses report delta-method standard errors clustered by paper, incorporating uncertainty in the fitted parameters and empirical precision mixture. The sample is the same as in Figure 2.
between the two estimators.19 The Gaussian baseline model then specifies:
where and for (TWFE or modern DiD) and where denotes the demeaned log standard error of specification with estimator . Thus each estimand’s marginal mean and standard deviation depend on its estimator precision. The model has a total of nine parameters, for each set of comparisons. I estimate these parameters by maximum likelihood, first profiling out the mean parameters by generalized least squares, with inference clustered by paper. This is a bivariate version of the Gaussian precision-dependent model in Walters [18]. I also check sensitivity to the analogous nonparametric-prior model as in Chen [7].20
Model estimates show that the high correlation between TWFE and modern DiD estimators in Figure 2 is not driven by correlated estimation error. Table 2 reports estimand correlations of 0.91 for DiD-averaging and 0.98 for imputation. TWFE and modern DiD estimands have similar standard deviations of around 0.2 (in units of observation-level outcome standard deviations) with modern estimands being somewhat more variable. This suggests that the ex post weights of TWFE may somewhat understate the dispersion of unconditional-average causal effects.
| DiD-Averaging | Imputation | |
| Standard deviation of TWFE estimands | 0.194<br>(0.017) | 0.185<br>(0.017) |
| Standard deviation of modern-DiD estimands | 0.216<br>(0.022) | 0.214<br>(0.023) |
| Correlation of TWFE and modern-DiD estimands | 0.913<br>(0.027) | 0.976<br>(0.005) |
| Prior probability of a sign reversal | 0.115<br>(0.021) | 0.056<br>(0.007) |
| Significant wrong-signed TWFE probability | 0.021<br>(0.007) | 0.006<br>(0.001) |
| Observations | 1,069 | 1,116 |
| Papers | 82 | 89 |
Table 2. Hierarchical Model Estimates
Estimand sign reversals are rarer than the estimate reversal rates in Figure 2 suggest. Table 2 reports that around 11.5% of TWFE and modern DiD estimand pairs have opposite signs, as opposed to 14.5% of estimate pairs. For imputation, these rates are 5.6% for estimands versus 10.8% for estimates. Naturally, some estimate sign flips reflect finite-sample noise which the model can account for. The model also allows us to infer how often TWFE would lead to an incorrect judgement on the modern DiD estimand’s sign: i.e., the probability of a researcher finding a significantly positive (or negative) TWFE estimate when the modern DiD estimand is negative (or positive). These rates are 2.1% for DiD averaging and 0.6% for imputation, reflecting the high correlation in estimands. In other words, in this sample, sign reversals do not tend to move the TWFE estimand far below (or above) zero relative to the estimator’s standard error.21
Importantly, these qualitative conclusions persist under the alternative nonparametric specification. Nonparametric estimates of estimand joint distributions, plotted in Figure A5, give latent sign-reversal rates of 11.3% for DiD-averaging and 5.5% for imputation, compared with 11.5% and 5.6% in the Gaussian model. Probabilities of significant sign errors are 2.4% and 1.6%, compared with 2.1% and 0.6% in the Gaussian model.
Figure A5. Estimand Distributions, Parametric vs. Nonparametric. Notes: This figure shows estimated joint distributions of TWFE and modern DiD estimands. Panels A and B use the baseline Gaussian model described in the text while panels C and D use a nonparametric model for the prior distribution, with separate precision-dependent means, scales, and mixing distributions for pretreatment and static/post-treatment comparisons. Distributions are averaged over empirical standard-error pairs. The nonparametric density is smoothed with an isotropic Gaussian kernel of standard deviation 0.025 per coordinate. Annotations report full-prior sign-flip and significant wrong-signed TWFE probabilities using the definitions in Table 2. Estimands are plotted in outcome-standard-deviation units. All panels share the logarithmic density scale; white denotes density below 0.001. The sample is the same as in Figure 2.
Conclusion
The empirical relevance of theoretical econometric concerns is rarely evaluated systematically. This paper shows how modern AI tools can be used to reanalyze a large number of published economic specifications and assess a recent concern that has reshaped how the profession thinks about and approaches staggered adoption designs. Findings suggest that negative weights, while potentially a serious problem for TWFE, are unlikely to dramatically affect empirical conclusions across the large number of replicated specifications. Future work could apply similar large-scale meta-analyses to other high-profile concerns, such as weak instruments, standard error clustering, or insufficiently flexible regression adjustment.
Importantly, this paper does not take a stance on whether the estimated sign reversal rates or estimand correlations are “low enough” to dismiss concerns over TWFE estimation. Modern DiD estimators are easily run in most circumstances, and checking their empirical relevance is likely useful for any given staggered-adoption application. Instead, this paper gives a systematic empirical foundation to ongoing discussions about relative tradeoffs between TWFE and alternative estimators, which can of course have their own drawbacks (such as imprecision). The findings may help shape further research and practical guidance for navigating the many potential pitfalls of TWFE-based causal inference—including parallel trend violations and standard error misspecification, alongside negative weights.
| DiD-Averaging | Imputation | |
| Standard deviation of TWFE estimands | 0.209<br>(0.018) | 0.202<br>(0.018) |
| Standard deviation of modern-DiD estimands | 0.232<br>(0.024) | 0.234<br>(0.026) |
| Correlation of TWFE and modern-DiD estimands | 0.912<br>(0.027) | 0.980<br>(0.004) |
| Prior probability of a sign reversal | 0.115<br>(0.021) | 0.052<br>(0.007) |
| Significant wrong-signed TWFE probability | 0.023<br>(0.008) | 0.006<br>(0.001) |
| Observations | 917 | 947 |
| Papers | 82 | 86 |
Table A2. Hierarchical Model Estimates, Excluding Pre-Treatment Comparisons. Notes: This table reports estimates from the Gaussian hierarchical model described in the text, refitted after excluding all pre-treatment comparisons. Estimates come from averaging priors over observed standard errors, giving equal weight to each retained comparison point. Standard deviations are in regression-sample outcome standard deviations. A sign reversal is . A significant wrong-signed TWFE estimate is and , where . Parentheses report delta-method standard errors clustered by paper, incorporating uncertainty in the fitted parameters and empirical precision mixture. The sample is the same as in Figure A1.

Figure A1. Modern Difference-in-Differences vs. Two-Way Fixed Effects, Excluding Pre-Treatment Comparisons. Notes: This figure compares DiD-averaging estimates (as in Callaway and Sant’Anna [6]) and imputation estimates (as in Borusyak, Jaravel and Spiess [4]) with two-way fixed-effects (TWFE) estimates. Each point is a scalar estimate (circle) or a post-treatment event-study average (square). The samples are those in Figure 2 after excluding all pre-treatment comparisons: 917 DiD-averaging observations from 82 papers and 947 imputation observations from 86 papers. Both coordinates are divided by the TWFE standard error, and the diagonal denotes equal estimates. Filled circles and squares indicate that the estimate difference is statistically significant at the 5% level. Coordinates are capped at ; uncapped values, without standardizing by TWFE standard errors, are used for statistics. “Sign flips” reports the share of pairs with opposite signs; “Significant flips” reports the share with a sign flip and a significant difference.
Additional Exhibits
Figure A2. DiD-Averaging vs. Imputation. The horizontal axis is CSA / SE(TWFE), and the vertical axis is BJS / SE(TWFE). Correlation: 0.917. Sign flips: 9.0%. Significant flips: 2.2%. The legend identifies AER, ECMA, JPE, QJE, REStud, REStat, JEEA, AEJ: Policy, AEJ: Applied. Scalar; Event average; Significant difference. Notes: This figure compares DiD-averaging and imputation estimates for the 1,001 common comparison points from 80 papers passing both estimators’ leverage screens. Each point is a scalar estimate (circle) or an event-study average (square), including separate pre- and post-treatment averages when available. Both coordinates are divided by the corresponding TWFE standard error, and the diagonal denotes equal estimates. Filled circles and squares indicate that the estimate difference is statistically significant at the 5% level. Coordinates are capped at ; uncapped values are used for statistics. “Sign flips” reports the share of pairs with opposite signs; “Significant flips” reports the share with a sign flip and a significant paired difference.
Figure A4. Negative Weights and Estimator Differences. A. DiD-Averaging. Opposite estimate signs (%). B. Imputation. Opposite estimate signs (%). C. DiD-Averaging. Mean noise-corrected squared gap. D. Imputation. Mean noise-corrected squared gap. Negative share of absolute TWFE effect weight. Zero; 0-1%; 1-3%; 3-10%; 10-25%; 25-50%. S: 202, P: 19; S: 144, P: 25; S: 21, P: 9; S: 82, P: 14; S: 207, P: 31; S: 36, P: 10. S: 204, P: 20; S: 151, P: 26; S: 20, P: 9; S: 114, P: 14; S: 214, P: 31; S: 27, P: 11. Notes: This figure relates negative TWFE weight shares to differences between TWFE and modern DiD estimates for static specifications. Panels A and B show the share of estimate pairs with opposite signs for DiD-averaging and imputation, respectively. Panels C and D show mean squared estimate differences after subtracting the estimated variance of each paired difference, including the covariance between estimators. Both estimates in a pair are normalized by the original regression-sample outcome standard deviation. Negative weight shares are defined as in Figure A3. Within each bin, papers receive equal weight and specifications receive equal weight within papers. Bars show 95% confidence intervals, clustered by paper. The S and P numbers report the specification and paper counts in each bin.
Figure A3. Negative Weights in Two-Way Fixed-Effects Estimates. Notes: This figure summarizes the distribution of negative ex post weights , as in Borusyak and Hull [4], across the 1,037 static TWFE specifications from 90 papers in the replication sample. Event-study contrasts are excluded. The sample includes 53 constructed static TWFE counterparts for specifications originally reporting modern DiD estimators. Panel A shows the cumulative distribution function for the fraction of treated observation rows with negative weights, including zero-weight rows in the denominator. Panel B shows the distribution for the share of absolute effect weight carried by negative weights, . Annotations report the equally weighted specification-level mean, median, standard deviation, and interquartile range (IQR).
| Paper | Specs. | CSA | BJS | Paper | Specs. | CSA | BJS |
| Abeberese et al. (REStat ’23) | 7 | 8 | 7 | Dippel and Heblich (AER ’21) | 2 | 2 | 2 |
| Acemoglu and Azar (ECMA ’20) | 3 | 3 | 3 | Donaldson (AER ’18) | 1 | 1 | 1 |
| Ager et al. (REStat ’20) | 1 | 2 | 2 | Egedesø et al. (EJ ’20) | 20 | 22 | 22 |
| Aghion et al. (AER ’08) | 2 | 2 | 2 | Esposito et al. (AER ’23) | 8 | 8 | 8 |
| Agrawal and Goldfarb (AER ’08) | 1 | 1 | 1 | Falcone (EJ ’26) | 7 | 12 | 12 |
| Akerlof et al. (JEEA ’26) | 2 | 2 | 1 | Fasani et al. (JEEA ’21) | 2 | 0 | 0 |
| Aman-Rana and Minaudier (AER ’26) | 14 | 16 | 16 | Fetzer (EJ ’22) | 3 | 1 | 1 |
| Andersson et al. (REStat ’23) | 39 | 39 | 39 | Fetzer et al. (REStat ’21) | 4 | 4 | 4 |
| Andrews (AEJ: Policy ’23) | 9 | 6 | 5 | Frakes (AER ’13) | 3 | 0 | 0 |
| Askarov et al. (JEEA ’23) | 4 | 0 | 0 | Funke et al. (AER ’23) | 2 | 0 | 0 |
| Avis et al. (JPE ’18) | 3 | 3 | 3 | Galiani et al. (JPE ’05) | 2 | 2 | 2 |
| Bahaj and Reis (REStud ’26) | 16 | 16 | 1 | Gibson and McKenzie (REStat ’14) | 60 | 60 | 60 |
| Bailey (AEJ: App ’12) | 11 | 11 | 12 | Gibson (REStat ’19) | 44 | 15 | 13 |
| Bailey and Goodman-Bacon (AER ’15) | 2 | 4 | 4 | Giorcelli and Moser (JPE ’20) | 4 | 0 | 4 |
| Bancalari (REStat ’26) | 32 | 52 | 52 | Gokmen et al. (EJ ’21) | 36 | 36 | 25 |
| Banerjee et al. (AEJ: App ’20) | 1 | 1 | 1 | Gonçalves et al. (AER ’26) | 15 | 0 | 0 |
| Baum-Snow and Lutz (AER ’11) | 55 | 21 | 25 | González et al. (EJ ’24) | 12 | 12 | 12 |
| Bazzi et al. (REStud ’26) | 18 | 24 | 24 | Hamory et al. (JEEA ’21) | 14 | 11 | 14 |
| Becker et al. (JEEA ’25) | 3 | 0 | 1 | Hansman et al. (JPE ’20) | 7 | 0 | 5 |
| Bellégo and Drouard (AEJ: Policy ’24) | 21 | 42 | 21 | He and Wang (AEJ: App ’17) | 12 | 12 | 15 |
| Benzell and Cooke (AEJ: App ’21) | 2 | 2 | 0 | Hjort and Poulsen (AER ’19) | 3 | 2 | 2 |
| Bertrand et al. (QJE ’21) | 1 | 1 | 1 | Hodler and Raschky (QJE ’14) | 12 | 14 | 14 |
| Bhalotra et al. (JEEA ’23) | 25 | 21 | 21 | Hollingsworth et al. (AER ’24) | 81 | 96 | 96 |
| Bindler and Hjalmarsson (AEJ: Policy ’18) | 10 | 0 | 0 | Iyer et al. (AEJ: App ’12) | 9 | 0 | 0 |
| Boomhower (AER ’19) | 1 | 1 | 1 | Janssen and Zhang (AER ’23) | 2 | 2 | 2 |
| Borcan et al. (AEJ: Policy ’17) | 5 | 5 | 5 | Jensen and Miller (AER ’18) | 7 | 7 | 7 |
| Bostwick et al. (AEJ: Policy ’22) | 2 | 0 | 1 | Jia et al. (JEEA ’15) | 10 | 0 | 10 |
| Braga and Malkova (JEEA ’24) | 6 | 0 | 0 | Johnson et al. (REStat ’24) | 4 | 0 | 0 |
| Braguinsky et al. (AER ’15) | 8 | 0 | 13 | Johnson and Noguera (REStat ’17) | 6 | 6 | 6 |
| Buchmueller and Carey (AEJ: Policy ’18) | 38 | 0 | 0 | Kreindler et al. (AER ’26) | 25 | 26 | 24 |
| Calamunci and Lonsky (EJ ’25) | 3 | 3 | 3 | La Ferrara et al. (AEJ: App ’12) | 3 | 3 | 3 |
| Cantoni et al. (JPE ’17) | 103 | 103 | 103 | Lafortune et al. (AEJ: App ’18) | 46 | 43 | 41 |
| Cantoni et al. (ECMA ’24) | 14 | 10 | 14 | Le Barbanchon and Sauvagnat (JEEA ’22) | 2 | 2 | 2 |
| Cantoni and Pons (QJE ’21) | 14 | 0 | 0 | Lewis-Faupel et al. (AEJ: Policy ’16) | 2 | 0 | 0 |
| Carrillo et al. (AEJ: Policy ’23) | 1 | 2 | 2 | Martinez-Bravo (AEJ: App ’17) | 4 | 4 | 4 |
| Cervellati et al. (EJ ’17) | 2 | 2 | 2 | Martinez-Bravo et al. (AER ’22) | 5 | 4 | 4 |
| Chen and Lan (AEJ: App ’17) | 1 | 1 | 1 | Mastrocco and Teso (REStud ’26) | 1 | 1 | 1 |
| Chen et al. (EJ ’22) | 1 | 1 | 1 | Moser et al. (AER ’14) | 5 | 5 | 5 |
| Chiovelli et al. (ECMA ’25) | 11 | 11 | 11 | Muñoz (QJE ’24) | 3 | 4 | 4 |
| Chu et al. (AEJ: App ’21) | 2 | 1 | 1 | Nangengast and Yotovo (AEJ: App ’25) | 2 | 2 | 2 |
| Cicala (AER ’15) | 4 | 0 | 8 | Noack and Costello (JPE ’24) | 1 | 2 | 2 |
| Cohen et al. (JPE ’11) | 1 | 0 | 1 | Norris and Xiong (EJ ’23) | 9 | 9 | 9 |
| Cohen et al. (JPE ’17) | 16 | 0 | 0 | Priks (EJ ’15) | 15 | 1 | 0 |
| Colonnelli and Prem (REStud ’22) | 5 | 5 | 5 | Rexer (AER ’25) | 90 | 37 | 61 |
| Conley and Taber (REStat ’11) | 1 | 0 | 0 | Sánchez de la Sierra et al. (AER ’24) | 32 | 0 | 0 |
| Cook and Shah (REStat ’22) | 4 | 4 | 4 | Shin (REStat ’25) | 1 | 2 | 2 |
| Coube et al. (QJE ’26) | 12 | 18 | 18 | Snyder and Welch (JPE ’17) | 21 | 0 | 16 |
| Couttenier et al. (JEEA ’17) | 1 | 0 | 0 | Spenkuch et al. (ECMA ’23) | 3 | 3 | 3 |
| Cunningham and Goodman-Bacon (AEJ: App ’25) | 36 | 47 | 44 | Stevenson and Wolfers (QJE ’06) | 8 | 8 | 8 |
| Dahis and Szerman (AEJ: App ’26) | 5 | 0 | 0 | Sun and Yannelis (REStat ’16) | 2 | 2 | 2 |
| Dal Bó et al. (REStud ’09) | 2 | 1 | 2 | Wolfers (AER ’06) | 12 | 2 | 11 |
| Davis and Wolfram (AEJ: App ’12) | 37 | 35 | 36 | Yang et al. (AEJ: Policy ’24) | 1 | 1 | 1 |
| de Janvry et al. (AER ’15) | 9 | 9 | 9 | Yousaf (JEEA ’21) | 1 | 1 | 1 |
| Deryugina (AEJ: Policy ’17) | 28 | 41 | 41 | Zussman (AEJ: App ’23) | 5 | 5 | 5 |
| Total (108 papers) | 1,346 | 1,069 | 1,116 |
Table A1. Notes: This table lists the 108 papers with replicated specifications. Specs. counts all 1,346 specifications, including those that contribute no comparison plotted in Figure 2; CSA and BJS count retained DiD-averaging and imputation comparison points plotted in that figure, respectively.
Replication Protocol
Search frame and review. The 16,094-record search frame used for this analysis covers the following ten journals and publication windows: the Quarterly Journal of Economics from 2000; the American Economic Review and Econometrica from 2004; the Journal of Political Economy from 2005; the Review of Economic Studies from 2006; the Review of Economics and Statistics, the Journal of the European Economic Association, and the American Economic Journals in Applied Economics and Economic Policy from 2009; and the Economic Journal from 2012. AEJ: Microeconomics and AER: Insights are excluded from this record count and do not contribute papers to the replication sample. Starting years were determined by official journal policy on the posting of replication packages except for the QJE, for which no policy record was found. Papers and Proceedings articles from the American Economic Review were excluded. All search windows ended on October 10, 2026, inclusive; forthcoming papers required evidence that both the accepted, intended-publication manuscript and its corresponding replication package were available by this date.
Bibliographic records were initially screened using abstracts, keywords, and any publicly available main text, appendices, and replication code. For papers with promising-sounding abstracts but no publicly available drafts, the drafts were manually downloaded with the author’s credentials. Screens use frozen, reproducibly randomized cross-journal queues. Keywords such as “difference-in-differences,” “event study,” and “staggered adoption,” and corresponding software commands were used. Screened-in papers were subjected to further review of main-text tables, figures, equations, and numerical prose and potentially qualifying results were linked to relevant code and data. Most of this review was automated; human oversight and spot-checking were used at various points to ensure fidelity.
Unit of analysis. The collection rule was to retain every qualifying main-text specification, including ancillary and diagnostic results and regardless of sign, magnitude, significance, or the authors’ causal interpretation. Different outcomes, outcome transformations, samples, treatment definitions, event windows or bins, weights, fixed effects, or controls define distinct specifications. A jointly estimated event-study path counts as one specification.
Eligible designs. Both panels and repeated cross sections qualified, provided treatment is assigned to stable units or groups. The typical eligible specification is either a linear regression with unit/group and calendar-time fixed effects and a single binary treatment or an unstacked event study. Time-invariant characteristics interacted with calendar-time fixed effects were allowed, including fixed subgroup-by-time fixed effects. Other time-varying controls, lagged outcomes, unit/group-specific trends, additional treatments, treatment-intensity regressors, subgroup-treatment interactions, and other nonredundant additive fixed effects were excluded. Explicitly identified Callaway and Sant’Anna [6] and Borusyak, Jaravel and Spiess [4] estimators provided additional specifications under the same design restrictions. Interacted event studies, as in Sun and Abraham, were also permitted when they coincided with Callaway and Sant’Anna [6] estimation. Stacked DiD specifications, instrumental variables, nonlinear models, and other estimators were excluded.
Treatment timing and support. Adoption dates were established from the original treatment-assignment history. A specification needed to contain at least two distinct first-adoption dates among cohorts with observed untreated and treated outcome observations and an untreated comparison unit in at least one treated period. For a small share of treatments that switch off, we drop periods after adoption in which the original treatment equals zero. The eligibility of a TWFE specification did not require every treated cell to be usable by every modern estimator; estimator-specific support was allowed and incorporated into the leverage screen (detailed below).
Documentation and author outreach. Each retained record identified the draft version and exact page, table or figure, panel, row, and column; the outcome, treatment, sample restrictions, weights, fixed effects, and clustering; and the observation, assignment, and calendar-time units. Event studies additionally record bins, omitted periods, and aggregation conventions. These records were randomly spot-checked by the author.
In the minority of cases where exact replication failed or ambiguities remained about a specification’s eligibility, study authors were contacted over email. In some of these cases additional private data or corrected code was shared. A few inexact replications, where the estimated coefficients were qualitatively similar to published figures, were admitted. See below for an accounting of implementation exceptions.
Leverage screen. Each TWFE or modern DiD estimate, constructed as described in the main text, was evaluated for high leverage. To characterize this screen, note first that any such estimate can be written as for some . For a clustering partition , define
with , and . A TWFE and modern DiD pair was retained (in, e.g., Figure 2) if both estimators have and . For two-way clustering, these calculations are made in each clustering dimension.
Implementation Exceptions
Source bin boundaries and a treated reference ((Bailey, 2012)). The replication code’s event-year bins are retained where the printed text describes different boundaries: annual tails at years and , and Table 3 post-treatment bins 1–5, 6–10, 11–14, and . Event year 0 is the omitted treated reference.
Fixed propensity-score donor weights and source county counts ((Cunningham and Goodman-Bacon, 2025)). Estimated propensity scores are treated as fixed weights. Four Table 6 scalar summaries use post-treatment event-window comparisons over years 0–5.
Exact absorbed nuisance columns ((Davis and Wolfram, 2012)). The age regressor equals a calendar-time component minus a fixed unit-specific operation date, so it is absorbed by unit and calendar-time fixed effects and is dropped.
Bartlett spatial–temporal covariance (Deryugina, 2017). The source code uses different weights for the spatial-temporal clustering of standard errors than documented in the paper, and results in a variance-covariance matrix that is not positive semidefinite. All 28 specifications use the documented weighting formula.
Fixed-effect specification (Giorcelli and Moser, 2020). The source code omits an intercept and one indicator from each fixed-effect set, imposing an additional restriction at the omitted-category intersection. The TWFE comparator uses the full unrestricted additive fixed-effect span.
Recovered OLS first stages (Benzell and Cooke, 2021). The two retained specifications are ordinary least squares (OLS) first stages recovered from the original instrumental variable estimation procedure, using its original estimation samples.
Event windows and mixed references (Cantoni, Mohr and Weigand, 2024; Muñoz, 2024). Muñoz (2024) has an adjusted event-study comparison whose post-treatment average uses years 0–6 in the baseline sample and 0–2 in the aligned sample; its separate pretreatment average uses years −3 and −2. Cantoni, Mohr and Weigand (2024) retain the published reference bin (−10, 0], which includes the adoption year, and subtract its estimated treatment effect in modern contrasts and each bootstrap draw. Unsupported horizons remain unavailable rather than being replaced with zero.
Imputation Event Studies
For imputation estimation of standard event studies, I follow Borusyak et al. (2024) in regressing outcomes on the allowed fixed effects, controls, and lead-bin indicators using untreated observations, then average the identified lead coefficients over the bins. In settings with an explicit reference period, I instead average within each supported bin, average the bins equally, and subtract the weighted residual mean in the source reference observations. This includes wholly untreated reference sets. The latter pretreatment summaries are in-sample residual contrasts, not standard Borusyak et al. (2024) pretrend coefficients; see Roth (2026) for discussion of these issues.
Replicated Papers
Abeberese, Ama Baafra, Prabhat Barnwal, Ritam Chaurey, and Priya Mukherjee, “Democracy and Firm Productivity: Evidence from Indonesia,” The Review of Economics and Statistics, 2023, 105 (3), 713–722.
Acemoglu, Daron and Pablo D. Azar, “Endogenous Production Networks,” Econometrica, 2020, 88 (1), 33–82.
Ager, Philipp, Benedikt Herz, and Markus Brueckner, “Structural Change and the Fertility Transition,” The Review of Economics and Statistics, 2020, 102 (4), 806–822.
References
- [1]Andrews, Isaiah and Maximilian Kasy, “Identification of and Correction for Publication Bias,” American Economic Review, 2019, 109 (8), 2766–2794.
- [2]Arkhangelsky, Dmitry, Guido W. Imbens, Lihua Lei, and Xiaoman Luo, “Design-Robust Two-Way-Fixed-Effects Regression for Panel Data,” Quantitative Economics, 2024, 15 (4), 999–1034.arxiv.org/abs/2107.13737
- [3]Baker, Andrew, Brantley Callaway, Scott Cunningham, Andrew Goodman-Bacon, and Pedro H. C. Sant’Anna, “Difference-in-Differences Designs: A Practitioner’s Guide,” Journal of Economic Literature, 2026, 64 (2), 498–557.
- [4]Borusyak, Kirill and Peter Hull, “Negative Weights Are No Concern in Design-Based Specifications,” AEA Papers and Proceedings, 2024, 114, 597–600.
- [6]Callaway, Brantley and Pedro H. C. Sant’Anna, “Difference-in-Differences with Multiple Time Periods,” Journal of Econometrics, 2021, 225 (2), 200–230.
- [7]Chen, Jiafeng, “Empirical Bayes When Estimation Precision Predicts Parameters,” Econometrica, 2026, 94 (2), 305–340.arxiv.org/abs/2212.14444
- [9]Chiu, Albert, Xingchen Lan, Ziyi Liu, and Yiqing Xu, “Causal Panel Analysis under Parallel Trends: Lessons from a Large Reanalysis Study,” American Political Science Review, 2026, 120 (1), 245–266.
- [10]de Chaisemartin, Clément and Xavier D’Haultfœuille, “Two-Way Fixed Effects Estimators with Heterogeneous Treatment Effects,” American Economic Review, 2020, 110 (9), 2964–2996.
- [11]Gardner, John, Neil Thakral, Linh T. Tô, and Luther Yap, “Two-Stage Differences in Differences,” 2026. Working paper, June.
- [12]Goldsmith-Pinkham, Paul, “Tracking the Credibility Revolution across Fields,” NBER Working Paper 35051, National Bureau of Economic Research 2026. — , Peter Hull, and Michal Kolesár, “Contamination Bias in Linear Regressions,” American Economic Review, 2024, 114 (12), 4015–4051.
- [13]Goodman-Bacon, Andrew, “Difference-in-Differences with Variation in Treatment Timing,” Journal of Econometrics, 2021, 225 (2), 254–277.
- [14]Meager, Rachael, “Understanding the Average Impact of Microcredit Expansions: A Bayesian Hierarchical Analysis of Seven Randomized Experiments,” American Economic Journal: Applied Economics, 2019, 11 (1), 57–91.DOI
- [17]Sun, Liyang and Sarah Abraham, “Estimating Dynamic Treatment Effects in Event Studies with Heterogeneous Treatment Effects,” Journal of Econometrics, 2021, 225 (2), 175–199.
- [18]Walters, Christopher, “Empirical Bayes Methods in Labor Economics,” in Christian Dustmann and Thomas Lemieux, eds., Handbook of Labor Economics, Vol. 5, Elsevier, 2024, pp. 183–260.
- [19]Wooldridge, Jeffrey M., “Two-Way Fixed Effects, the Two-Way Mundlak Regression, and Difference-in-Differences Estimators,” Empirical Economics, 2025, 69 (5), 2545–2587.





