Data, design, inference, and identification — in full

What this page documents — and how it cites

This is the full methodology behind the tri-state event study: a panel of U.S. publicly traded firms studied around the 2025 corporate-law reforms in Delaware (S.B. 21), Texas (S.B. 29), and Nevada (A.B. 239). The results themselves — Delaware's null controlled-firm reaction, Texas's power-limited null, and the underpowered Nevada estimate — are reported on the event-study page. This page documents how every number there was produced, so that a reader who reads only the methods can reconstruct the design.

One reference on this page is not a methods authority and is cited only as the object of replication: Kenneth Khoo (National University of Singapore) & Roberto Tallarita (Harvard Law School), The Price of Delaware Corporate Law Reform (2025), the working paper whose Delaware estimate §9 replicates. It is identified in text and is the single non-peer-reviewed link on the page; it is never treated as a source for a method.

The panel: returns, factors, fundamentals, and the incorporation crosswalk

1.1 Daily returns and delisting

Daily total returns are taken from the CRSP daily stock file (CIZ format) as the canonical source through 2025-12-31; from 2026-01-01 through the data end (2026-06-18) the live panel uses Compustat-derived daily total returns, validated against CRSP over the overlap window. Delisting returns are incorporated for the CRSP window so that firms that stop trading are not silently dropped at a return of zero — the bias that Shumway, The Delisting Bias in CRSP Data, 52 J. Fin. 327 (1997) JF showed inflates measured long-run returns when missing delisting returns are set to zero. For the post-CRSP Compustat-live window, delisting treatment is separately audited and the status is displayed next to every result.

The market-model and factor-model machinery in this study follows the daily-return event-study framework of Brown & Warner, Using Daily Stock Returns: The Case of Event Studies, 14 J. Fin. Econ. 3 (1985) JFE, which established that daily data, properly handled for non-normality and event-day clustering, deliver well-specified tests.

1.2 Winsorization

Returns and all continuous covariates are winsorized at the 1st and 99th percentiles of the cross-section on each event day — not of the pooled sample. Per-day winsorization removes day-level outliers without conflating within-day dispersion with the across-day variation that pooled trimming would absorb. This is the project's standing rule, consistent with the dispersion-preserving treatment surveyed in Adams, Hayunga, Mansi, Reeb & Verardi, Identifying and Treating Outliers in Finance, 48 Fin. Mgmt. 345 (2019) Fin. Mgmt. and with the long-tail return distribution documented by Bessembinder, Do Stocks Outperform Treasury Bills?, 129 J. Fin. Econ. 440 (2018) JFE. In the canonical panel, 2.06% of firm-days are clipped.

1.3 Risk factors

The benchmark return model is the five-factor model of Fama & French, A Five-Factor Asset Pricing Model, 116 J. Fin. Econ. 1 (2015) JFE — market, size (SMB), value (HML), profitability (RMW), and investment (CMA) — augmented with the momentum factor of Carhart, On Persistence in Mutual Fund Performance, 52 J. Fin. 57 (1997) JF. The three-factor model of Fama & French, Common Risk Factors in the Returns on Stocks and Bonds, 33 J. Fin. Econ. 3 (1993) JFE is reported as a robustness check. Daily factor returns are taken from the Kenneth R. French data library; the maximum available FF5 and UMD dates bound the factor-model long-horizon results (see §6), and the as-used factor vintage is reported next to every estimate.

1.4 Fundamentals

Firm-level controls are trailing fiscal-year-end Compustat values (total assets, book common equity, total debt, PP&E, market value of equity, net income), used to construct log(assets), book-to-market, leverage, tangibility, ROA, and Tobin's Q. Control definitions follow the conventions of Bates, Kahle & Stulz, Why Do U.S. Firms Hold So Much More Cash than They Used To?, 64 J. Fin. 1985 (2009) JF and Almeida, Campello & Weisbach, The Cash Flow Sensitivity of Cash, 59 J. Fin. 1777 (2004) JF.

1.5 As-of-event incorporation crosswalk

The treatment in every leg keys on a firm's state of incorporation as of the event date, not its current state. Because reincorporation is the very behavior under study, using a firm's current domicile would assign treatment using post-event information. The crosswalk is built from primary EDGAR cover-page disclosures. Conditioning the sample only on named structural grounds — never on outcomes, post-event survival, or disclosure quality — is the discipline that keeps the event-study identification intact, the point made in the survey by Kothari & Warner, Econometrics of Event Studies, in Handbook of Corporate Finance: Empirical Corporate Finance 3 (B. Espen Eckbo ed., 2007) Handbook.

Controller exposure, measured from voting power

Delaware S.B. 21 amends DGCL §144 with a statutory definition of "controlling stockholder." A person is a controller if, with affiliates, they (i) hold a majority of director-election voting power; or (ii) hold contractual rights to elect a board majority; or (iii) hold power functionally equivalent to majority control by virtue of both (a) at least one-third of the voting power and (b) managerial authority over the business. The 33⅓% bright line is a new statutory creation in amended §144 — it is not the MFW cleansing threshold. (Prior drafts described it backwards; In re Match Group, 315 A.3d 446 (Del. 2024), reaffirmed the strict MFW standard that S.B. 21 then displaced.)

The treatment variable is therefore controller exposure measured from voting power. Controlling-shareholder firms are those with a single holder controlling ≥ one-third of voting power, read from the firm's proxy statements (DEF 14A beneficial-ownership tables and Item 403 disclosures), combined where relevant with facts supporting functional managerial authority. Founder-influenced firms with 15%–33⅓% blocks are flagged separately and are not treated as controller-exposed.

The voting-power indicator is parsed from DEF 14A Item 403 tables firm-by-firm against EDGAR-direct filings. A five-firm hand-audit of the automated voting-block parser found a 3-of-5 binding-defect rate (Oracle, Berkshire, Rollins misclassified), so the dual-class indicator is used only as a directional control and is labeled provisional wherever it enters a causal estimator.

Seven firm-level controls

The same seven controls enter every conditional estimator, defined from trailing fiscal-year-end Compustat fields:

Definitions track Bates, Kahle & Stulz (2009) JF and Almeida, Campello & Weisbach (2004) JF. All seven are winsorized 1/99 cross-sectionally per day (§1.2).

Estimation window, abnormal returns, and the event-window grid

4.1 Abnormal and cumulative abnormal returns

For each firm \(i\) and trading day \(t\), the abnormal return is the realized return minus the FF5+UMD model prediction:

Factor loadings are estimated over the pre-event window \([-250,-20]\) (a firm needs ≥100 non-missing return days to be included — the power threshold of Brown & Warner (1985) JFE), so no event-window data leaks into the baseline. The estimation-window / event-window architecture follows the survey of MacKinlay, Event Studies in Economics and Finance, 35 J. Econ. Literature 13 (1997) JEL.

The cumulative abnormal return over a window \([\tau_1,\tau_2]\) is the sum of daily \(AR\):

4.2 Event windows, by leg

Windows are leg-specific and fixed in a locked analysis plan before the data re-run (a frozen internal plan, not an external pre-registration — we do not use the word "pre-registered"). The full window grid is reported so that any window-specific dependence is visible, the multiplicity discipline urged by Harvey, Presidential Address: The Scientific Outlook in Financial Economics, 72 J. Fin. 1399 (2017) JF and Harvey & Liu, Lucky Factors, 141 J. Fin. Econ. 413 (2021) JFE.

The window-robustness finding

For the Delaware leg we run a symmetric and asymmetric window grid on the locked K-T universe (≈989 DE vs ≈979 non-DE). The DE-minus-non-DE spread is small and statistically insignificant across every window — e.g., +0.29pp at [−1,+1] (Welch t≈1.45, p≈.15), +0.05pp at [−1,+3] (p≈.92), +0.05pp at [−1,+5] (p≈.89). This window-robustness is itself a result: the Delaware reaction does not appear at one window and vanish at another; it is absent throughout. (By contrast, K-T's own published estimate is not window-robust — its discount lives in the +2…+5 drift and reverses sign at [−1,+1].)

Five complementary statistics on the same CAARs

Because event-day returns are fat-tailed and firms sharing one event date are not independent, a naïve cross-sectional t-test over-rejects. We report five statistics, each guarding a different failure of the t-test:

5.1 Multiple-testing correction across windows

Because the window grid means several tests are run per leg, the family-wise error rate is controlled with the step-down procedure of Romano & Wolf, Stepwise Multiple Testing as Formalized Data Snooping, 73 Econometrica 1237 (2005) Econometrica, with Holm and Benjamini–Hochberg reported alongside as references. No Delaware controlled-firm window survives the Romano–Wolf max-t criterion, consistent with the null reported in §2.

Did the announcement reaction persist? Calendar-time and BHAR

A short-window CAAR captures the announcement reaction; it cannot tell us whether the market eventually repriced. We measure persistence two ways, deliberately, because the long-run literature warns they can disagree and the disagreement is informative — the bad-model and benchmark-contamination problems laid out by Fama, Market Efficiency, Long-Term Returns, and Behavioral Finance, 49 J. Fin. Econ. 283 (1998) JFE.

6.1 Calendar-time portfolio (CTP) alphas

We form a controlled-minus-dispersed long-short portfolio, hold it each calendar day, and regress its daily return on FF3 and FF5+UMD factors. The intercept \(\alpha\) is the abnormal return; standard errors are Newey–West to absorb heteroskedasticity and serial correlation:

The calendar-time approach is the method Lyon, Barber & Tsai, Improved Methods for Tests of Long-Run Abnormal Stock Returns, 54 J. Fin. 165 (1999) JF recommend precisely because it controls the cross-correlation of overlapping holding periods that biases BHAR test statistics; the HAC covariance is Newey & West, 55 Econometrica 703 (1987) Econometrica. For Delaware, the controlled-minus-dispersed hedge alpha is economically and statistically zero through the full window to 2026-06-18 (unconditional daily mean +0.0046%, NW t≈0.14, p≈.89; CAPM α p≈.93; FF5+UMD α p≈.82 to the factor-bounded 2026-04-30). Texas's CTP FF3 alpha is +0.45%/yr (p≈.96).

6.2 Buy-and-hold abnormal returns (BHAR)

BHAR compounds each firm's return against a matched benchmark over the holding horizon:

Because long-run BHARs are right-skewed, inference uses the skewness-adjusted bootstrapped t of Lyon, Barber & Tsai (1999) JF rather than a naïve t. The benchmark-portfolio construction and the empirical power of BHAR test statistics follow Barber & Lyon, Detecting Long-Run Abnormal Stock Returns, 43 J. Fin. Econ. 341 (1997) JFE, who documented the new-listing, rebalancing, and skewness biases that a reference portfolio must address. For Delaware, BHAR mean is +3.1% with a wide 95% CI of [−21.8, +34.8] and a median of −17.7% — consistent with the no-persistence reading. The CTP and BHAR readings agree in significance (both null), which is the cross-check Fama (1998) JFE recommends.

Six estimators, read jointly — five inferential, one diagnostic

Selection into Delaware domicile (or into controller exposure within Delaware) is non-random and correlated with size, growth options, and capital structure; the pre-match maximum standardized mean difference on log(assets) is large (≈0.65). No single estimator settles this. We run six side-by-side and read the result space rather than one coefficient — the multi-estimator discipline of Atanasov & Black, Shock-Based Causal Inference in Corporate Finance and Accounting Research, 6 Critical Fin. Rev. 207 (2016) CFR and Bertrand & Mullainathan, Enjoying the Quiet Life?, 111 J. Pol. Econ. 1043 (2003) JPE.

7.1 What the battery shows

The estimates diverge rather than converge: the two exact-balance estimators (entropy balancing, AIPW) reach significance (p≈.0015 and p≈.0098), while the two matching estimators that fail to balance size (PSM, CEM) shrink the coefficient toward zero and lose significance (p≈.30 and p≈.63). Post-match maximum SMD is 0.25 for PSM and CEM against the 0.10 target of Stuart, Matching Methods for Causal Inference, 25 Stat. Sci. 1 (2010) Stat. Sci.; only entropy balancing achieves SMD = 0. King & Nielsen, Why Propensity Scores Should Not Be Used for Matching, 27 Pol. Analysis 435 (2019) Pol. Anal. is why we do not retune the score to chase balance. Where balance fails, the matching estimates are descriptive stress tests, not credible ATTs — and the divergence is itself the finding: the identifying assumption (selection on observables) is not satisfied by the available covariates.

7.2 Synthetic control is diagnostic only

The donor panel lacks a complete daily pre-event return series for every donor, so the NNLS fit reaches a near-zero pre-RMSE that makes RMSPE-ratio placebo inference degenerate. The synthetic-control output is reported as a diagnostic and never used to build a confidence interval or support the headline. The placebo-inference and data requirements are those of Abadie, Diamond & Hainmueller (2010) JASA and Abadie, Using Synthetic Controls, 59 J. Econ. Literature 391 (2021) JEL.

7.3 Selection corrections and the Gelbach decomposition

Two further checks document the selection problem rather than solve it. The Heckman, Sample Selection Bias as a Specification Error, 47 Econometrica 153 (1979) Econometrica two-step has no valid exclusion restriction here (identified only off probit nonlinearity), so it is reported as a sensitivity, not a result — its inverse-Mills coefficient is itself insignificant (p≈.10) and the implied controlled coefficient collapses. A 2SLS attempt with a leave-one-out industry-share instrument is inadmissible (first-stage F≈0.09, far below the weak-instrument threshold, and the exclusion restriction is implausible). The Gelbach, When Do Covariates Matter? And Which Ones, and How Much?, 34 J. Lab. Econ. 509 (2016) JOLE decomposition attributes how much of the raw spread is explained by each covariate (size dominates), confirming that the apparent effect is a size/value factor tilt.

Naming the null: a power-limited null is not a zero

A failure to reject is not evidence of no effect unless the design could have detected a plausible one. For each leg we report the minimum detectable effect (MDE) at 80% power and 5% size, and — where warranted — a two one-sided tests (TOST) equivalence test against a pre-stated band.

• Texas (n=43). Clean-cut MDE ≈ 2%; clustered MDE ≈ 4–6%. The design cannot resolve effects smaller than ~2%, and TOST does not clear a ±50bp band (the MDE is roughly 4× the band). Texas is therefore labeled a power-limited null, explicitly not a bounded or decisive zero.
• Nevada (n≈80 with betas). Estimated but underpowered; reported with the same MDE discipline and flagged accordingly.
• Delaware (K-T universe, n≈989 vs 979). Well-powered for the K-T between-state comparison; here the null is a genuine precise zero, not a power artifact.

The multiplicity logic behind reporting power alongside p-values — that a literature of underpowered tests manufactures false positives — is the argument of Harvey (2017) JF. We never describe a power-limited null as a demonstrated absence of effect.

Replicating the published Delaware estimate

The Delaware leg is a direct replication of the working paper Kenneth Khoo & Roberto Tallarita, The Price of Delaware Corporate Law Reform (2025) — the only non-peer-reviewed reference on this page, cited as the object of replication, never as a methods authority. (Author is Kenneth Khoo, NUS — not any other name.) We reproduce their design as published:

• Universe: top-1000 Delaware-incorporated firms vs top-1000 non-Delaware firms (≈989 / ≈979 usable after the ≥100-day estimation filter).
• Event date: 2025-02-18, the first trading day after the S.B. 21 introduction signal.
• Estimation window: [−250, −20]; winsorization 1/99 cross-sectional per day; market proxy a value-weighted panel index.
• Headline window: [−1, +5], with the full [−1,+1]…[−1,+10] grid for window-robustness.
• Treatment: as-of-event incorporation (asof_state_clean == "DE").

Our replicated DE-minus-non-DE spread is small and insignificant at every window (e.g., [−1,+5] DE CAAR −0.80%, non-DE −0.85%, spread +0.05pp, Welch p≈.89; SIC3-clustered DE regression coefficient at [−1,+1] +0.25pp, p≈.37). The K-T published discount of roughly −1.4% (top-1000 DE vs non-DE, with deeper cuts for blockholder and dual-class subsets) is not window-robust in their own table — it concentrates in the +2…+5 drift and flips sign at the tight [−1,+1] window. We report both the replication and the original target side by side and draw no inference from a window that does not reproduce.

What this design cannot do

1. As-of-event treatment lock is owed. The within-Delaware controlled split and the diff-in-CAAR controls still use a current Compustat incorporation snapshot, not the EDGAR as-of-event lock. Every affected estimate carries the caveat.
2. Controller variable is provisional. The dual-class proxy has a measured binding-defect rate; the proper DEF 14A Item 403 voting-power rebuild is gated, and the proxy enters causal estimators only as a directional control.
3. Selection is not solved. The identification battery diverges, four of six estimators fail balance or are diagnostic/inadmissible, Heckman has no exclusion restriction, and the IV is weak. We document the selection problem; we do not claim a causal ATT for Delaware.
4. Texas and Nevada are underpowered. N=43 and N≈80; both are power-limited nulls, not demonstrated zeros, and the tariff confound (the April-2 oil-and-gas shock) drives the lone Texas E1 −2.48% — it vanishes ex-energy (−0.25%).
5. One event date per leg. Each legislative leg has a single information date, so the long-horizon results are descriptive of one episode, not a cross-section of events.
6. Factor-bounded long horizon. Factor-model CTP alphas end 2026-04-30 with factor availability; equal-weight market BHAR extends to 2026-06-18. Benchmark and end-date are reported on every long-horizon number.

Neutral, source-pinned, and deliberately conservative: where a result is fragile, the page labels it fragile. No causal or normative claim is placed on any null or on any estimate that fails its own balance or power test.

Method sources of record

Every method above links to the article in which it was published. Finance journals are marked JF / JFE / JEF; methods whose paper of record is a top non-finance journal are marked non-finance and listed separately below, as the honest exceptions to the finance-first rule.

Full bibliography → — the complete reference apparatus (statutes, bills, cases, data sources, and internal artifacts) with per-link audit status flags, in Bluebook and Chicago author–year form.

Finance journals (JF / JFE)

1. Brown & Warner, Using Daily Stock Returns: The Case of Event Studies, 14 J. Fin. Econ. 3 (1985). JFE doi:10.1016/0304-405X(85)90042-X
2. Fama & French, Common Risk Factors in the Returns on Stocks and Bonds, 33 J. Fin. Econ. 3 (1993). JFE doi:10.1016/0304-405X(93)90023-5
3. Fama & French, A Five-Factor Asset Pricing Model, 116 J. Fin. Econ. 1 (2015). JFE doi:10.1016/j.jfineco.2014.10.010
4. Carhart, On Persistence in Mutual Fund Performance, 52 J. Fin. 57 (1997). JF doi:10.1111/j.1540-6261.1997.tb03808.x
5. Boehmer, Musumeci & Poulsen, Event-Study Methodology under Conditions of Event-Induced Variance, 30 J. Fin. Econ. 253 (1991). JFE doi:10.1016/0304-405X(91)90032-F
6. Corrado, A Nonparametric Test for Abnormal Security-Price Performance in Event Studies, 23 J. Fin. Econ. 385 (1989). JFE doi:10.1016/0304-405X(89)90064-0
7. Barber & Lyon, Detecting Long-Run Abnormal Stock Returns: The Empirical Power and Specification of Test Statistics, 43 J. Fin. Econ. 341 (1997). JFE doi:10.1016/S0304-405X(96)00890-2
8. Lyon, Barber & Tsai, Improved Methods for Tests of Long-Run Abnormal Stock Returns, 54 J. Fin. 165 (1999). JF doi:10.1111/0022-1082.00101
9. Fama, Market Efficiency, Long-Term Returns, and Behavioral Finance, 49 J. Fin. Econ. 283 (1998). JFE doi:10.1016/S0304-405X(98)00026-9
10. Shumway, The Delisting Bias in CRSP Data, 52 J. Fin. 327 (1997). JF doi:10.1111/j.1540-6261.1997.tb03818.x
11. Bessembinder, Do Stocks Outperform Treasury Bills?, 129 J. Fin. Econ. 440 (2018). JFE doi:10.1016/j.jfineco.2018.06.004
12. Bates, Kahle & Stulz, Why Do U.S. Firms Hold So Much More Cash than They Used To?, 64 J. Fin. 1985 (2009). JF doi:10.1111/j.1540-6261.2009.01492.x
13. Almeida, Campello & Weisbach, The Cash Flow Sensitivity of Cash, 59 J. Fin. 1777 (2004). JF doi:10.1111/j.1540-6261.2004.00679.x
14. Harvey, Presidential Address: The Scientific Outlook in Financial Economics, 72 J. Fin. 1399 (2017). JF doi:10.1111/jofi.12530
15. Harvey & Liu, Lucky Factors, 141 J. Fin. Econ. 413 (2021). JFE doi:10.1016/j.jfineco.2021.04.014

Top non-finance journals — the honest exceptions to the finance-first rule

These methods originate in statistics or econometrics; finance inherited them. Each is cited to its peer-reviewed journal of record, not downgraded to force a finance link.

1. Heckman, Sample Selection Bias as a Specification Error, 47 Econometrica 153 (1979). Econometrica doi:10.2307/1912352
2. Newey & West, A Simple, Positive Semi-Definite, Heteroskedasticity and Autocorrelation Consistent Covariance Matrix, 55 Econometrica 703 (1987). Econometrica doi:10.2307/1913610
3. Romano & Wolf, Stepwise Multiple Testing as Formalized Data Snooping, 73 Econometrica 1237 (2005). Econometrica doi:10.1111/j.1468-0262.2005.00615.x
4. Rosenbaum & Rubin, The Central Role of the Propensity Score in Observational Studies for Causal Effects, 70 Biometrika 41 (1983). Biometrika doi:10.1093/biomet/70.1.41
5. Hainmueller, Entropy Balancing for Causal Effects, 20 Pol. Analysis 25 (2012). Pol. Anal. doi:10.1093/pan/mpr025
6. Iacus, King & Porro, Causal Inference Without Balance Checking: Coarsened Exact Matching, 20 Pol. Analysis 1 (2012). Pol. Anal. doi:10.1093/pan/mpr013
7. King & Nielsen, Why Propensity Scores Should Not Be Used for Matching, 27 Pol. Analysis 435 (2019). Pol. Anal. doi:10.1017/pan.2019.11
8. Robins, Rotnitzky & Zhao, Estimation of Regression Coefficients When Some Regressors Are Not Always Observed, 89 J. Am. Stat. Ass'n 846 (1994). JASA doi:10.2307/2290910
9. Abadie, Diamond & Hainmueller, Synthetic Control Methods for Comparative Case Studies, 105 J. Am. Stat. Ass'n 493 (2010). JASA doi:10.1198/jasa.2009.ap08746
10. Abadie, Using Synthetic Controls: Feasibility, Data Requirements, and Methodological Aspects, 59 J. Econ. Literature 391 (2021). JEL doi:10.1257/jel.20191450
11. Kolari & Pynnönen, Event Study Testing with Cross-Sectional Correlation of Abnormal Returns, 23 Rev. Fin. Stud. 3996 (2010). RFS doi:10.1093/rfs/hhq072
12. Petersen, Estimating Standard Errors in Finance Panel Data Sets: Comparing Approaches, 22 Rev. Fin. Stud. 435 (2009). RFS doi:10.1093/rfs/hhn053
13. Hou, Xue & Zhang, Replicating Anomalies, 33 Rev. Fin. Stud. 2019 (2020). RFS doi:10.1093/rfs/hhy131
14. Harvey, Liu, Saretto & Pontiff, An Evaluation of Alternative Multiple Testing Methods for Finance Applications, 10 Rev. Asset Pricing Stud. 199 (2020). RAPS doi:10.1093/rapstu/raaa003
15. Stuart, Matching Methods for Causal Inference: A Review and a Look Forward, 25 Stat. Sci. 1 (2010). Stat. Sci. doi:10.1214/09-STS313
16. Gelbach, When Do Covariates Matter? And Which Ones, and How Much?, 34 J. Lab. Econ. 509 (2016). JOLE doi:10.1086/683668
17. Patell, Corporate Forecasts of Earnings Per Share and Stock Price Behavior: Empirical Tests, 14 J. Acct. Res. 246 (1976). JAR doi:10.2307/2490543
18. MacKinlay, Event Studies in Economics and Finance, 35 J. Econ. Literature 13 (1997). JEL jstor:2729691
19. Bertrand & Mullainathan, Enjoying the Quiet Life? Corporate Governance and Managerial Preferences, 111 J. Pol. Econ. 1043 (2003). JPE doi:10.1086/376950
20. Atanasov & Black, Shock-Based Causal Inference in Corporate Finance and Accounting Research, 6 Critical Fin. Rev. 207 (2016). Crit. Fin. Rev. doi:10.1561/104.00000031
21. Kothari & Warner, Econometrics of Event Studies, in Handbook of Corporate Finance: Empirical Corporate Finance 3 (B. Espen Eckbo ed., 2007). Handbook doi:10.1016/B978-0-444-53265-7.50015-9
22. Adams, Hayunga, Mansi, Reeb & Verardi, Identifying and Treating Outliers in Finance, 48 Fin. Mgmt. 345 (2019). Fin. Mgmt. doi:10.1111/fima.12269
23. Rosenbaum, Observational Studies (2d ed. 2002). monograph Springer

Object of replication (not a methods authority)

38. Kenneth Khoo & Roberto Tallarita, The Price of Delaware Corporate Law Reform (2025) (working paper; the Delaware estimate replicated in §9; cited as object of replication only, not as a method source).

Methodology companion to the tri-state event study. Canonical results: tristate_results_canonical.json (build v3, 2026-06-21), BUILD_MANUAL §152.149–§152.164. ← Return to the event-study results.