SMU Cox · Corporate Governance Initiative
Short-run event-study evidence and long-run market-performance tests — the two horizons of a single design.
Coming SoonIn active development — the full study publishes on this page.
When a company changes its state of incorporation, or a state rewrites its corporate law, does the stock market actually react? We are measuring it as a full empirical study across two horizons — the short-run reaction in the days around the change (an event study) and the long-run performance over the months that follow (calendar-time alpha and buy-and-hold returns) — isolating each firm's own response against carefully matched comparison firms.
What we're building
Each method below is paired with a plain-English explanation of what it does and why it matters — plain English first, academic detail on demand. The design is specified before the cohort results are computed, source-linked, and reproducible; it is neutral, and honest about what the data can and cannot tell us. Final results will publish here with a run manifest and replication package.
In plain English —We strip out what the whole market did on the same days, so we isolate each firm's own reaction to the legal change rather than crediting it for moves everyone made.
In plain English —Every firm is judged against look-alike peers — companies of similar size, industry, and profile — not against the market average, so the comparison is apples-to-apples.
In plain English —How an investor actually would have done holding the stock over months, not just the day or two around the announcement — the long game, not the headline.
In plain English —We test whether the firms that choose to move are already different in hidden ways — differences that could make a naive before-and-after comparison look like a reaction when it isn't.
In plain English —We report what we genuinely can and cannot detect, run the same tests on fake "events" to check for false signals, and don't cherry-pick the window that flatters a result.
Why we stress-test
Before any statistics, here is the whole problem in one sentence: when a company reincorporates and its stock moves, how do we know the legal change caused the move — and not something the firm already shared with the market, or some hidden reason it chose to move in the first place? Two everyday examples make the logic clear.
The cleanest way to know a new pill works is a randomized trial: for each patient, flip a coin — real pill or sugar pill — then compare recovery. Because the coin, not the patient, decides, the two groups are alike in every other way, so any difference in outcomes must be the pill.
The catch for corporate law: no one flips a coin. Firms choose to reincorporate. If the firms that move are already different — healthier, more troubled, differently governed — a naive before-and-after can credit the move for something that was there all along. Economists call this selection, or endogeneity.
A school district adopts a new teaching method and its test scores rise. Did the method do it? Maybe scores rose everywhere that year — an easier exam, a stronger economy, a kinder grading curve.
The fix is difference-in-differences: compare the change in the reform district to the change in a near-identical district that kept the old method, over the same window. Subtracting the two changes strips out both what is permanently special about the reform district and whatever lifted every district that year. What remains is the method’s own effect.
A worked precedent
The same toolkit was already run on a single firm — ExxonMobil’s 2026 New Jersey→Texas redomiciliation. It is the template for how the cohort study will treat every result: surface a candidate signal, then attack it from every angle a hostile referee would, and publish only what survives. The figures below are published and source-linked — they are not cohort results.
In plain English: the one-day reaction was statistically indistinguishable from zero. A second model controlling for an oil-price spike produced a borderline number — but it did not survive the checks for window-shopping (Romano-Wolf) or for the unusually volatile week (GARCH). The larger drop over the ten days before the announcement looked alarming until the peer comparison showed nearly every oil & gas firm moved the same way: the cause was a February 2026 oil shock, not advance knowledge of the Texas move. An equivalence test (TOST, ±2pp band, p = 0.011) then affirmatively bounded the effect near zero.
Read this before any result
In statistics, the null hypothesis is the starting assumption that the legal change had no effect on the stock. A null result means our test could not reject that assumption — it did not find a reaction standing out from ordinary noise. The single most misread word in this kind of work is that one: failing to reject “no effect” is not the same as proving “no effect.” We will always tell you which one we mean.
The test could not separate the result from day-to-day noise. That is not proof the effect is zero — it can equally happen when the sample is too small to see a real effect. Absence of evidence is not evidence of absence.
A harder, separate test (an equivalence test, TOST) shows the result falls inside a pre-set band around zero. Only then will we say the effect is, affirmatively, too small to matter.
This is why a null is not automatically good news or bad news. Whenever a test returns a null, we also report the smallest effect the study was actually powerful enough to detect (the minimum detectable effect). If that floor is large, a null mostly means “not enough data to tell” — and we say so plainly rather than dressing a weak null as a finding. The ExxonMobil result above clears this bar: it is null under the standard model and affirmatively bounded near zero by an equivalence test.
Two horizons
This is more than an event study; it is an empirical study with two horizons. A governance change can move a stock in the moment and also shape its value slowly over the months and years that follow — and a one- or two-day window cannot see the second part. So we measure both. The short-run leg is the event study described above: the abnormal return in the days around the legal change. The long-run leg uses the two standard tools below to ask whether the change still mattered a year later.
Picture running a fund that buys every company the month it reincorporates, holds each for a fixed window, and rebalances monthly. Did that fund earn more than its risk exposure alone would predict? The leftover return — the alpha — is the long-run effect of the move, after stripping out the market, company size, value, profitability, investment, and momentum.
Form a calendar-time portfolio of firms currently inside the post-event holding window; regress its monthly excess returns on the Fama-French five factors plus momentum. The intercept (α) is the risk-adjusted long-run abnormal performance; report equal- and value-weighted, with Newey-West (HAC) standard errors. Because it weights every calendar month equally and prices cross-firm return correlation directly, it is more conservative than averaging individual long-run abnormal returns — at the cost of lower statistical power.
The plain investor’s question: if you had bought the stock the day of the move and simply held it for six months or a year, how much better or worse did you do than holding a near-identical look-alike firm over the exact same stretch? That compounded gap is the buy-and-hold abnormal return.
For each firm, BHAR over a horizon (1, 3, 6, 12 months) is the compounded holding return minus the compounded return on a matched control firm or reference portfolio: Π(1+Rit) − Π(1+Rbench,t). Inference uses skewness-adjusted or bootstrapped t-statistics, because compounding makes the distribution right-skewed and a few extreme firms can dominate. All returns are winsorized at the 1st and 99th percentiles; the calendar-time portfolio above is the deliberate cross-check on BHAR’s sensitivity to outliers.
Both legs run against the same matched comparison firms and pass through the identification checks below, so the short-run and long-run readings are built on one consistent design.
The robustness toolkit
Each tool targets a specific threat to a clean causal read. Every card opens in two registers — a plain-English explanation with a worked example, and the formal method detail — so the same page serves a board member, a journalist, and a peer reviewer.
Firms are not assigned to reincorporate — they volunteer. The ones that volunteer may differ in ways we cannot directly see. Heckman’s method first models who chooses to move, then folds that into the outcome estimate so the result is not fooled by who selected in.
A two-step estimator. Stage 1 is a probit of the move / no-move decision on covariates plus an exclusion restriction — a variable that shifts the choice to move but not the stock reaction; from it we form the inverse Mills ratio (λ). Stage 2 adds λ to the outcome regression. A statistically significant λ is direct evidence of selection on unobservables; identification rests on the credibility of the exclusion restriction.
Instead of comparing a mover to the market average, we find the non-mover that looks most like it — same size, industry, profitability, and leverage — and compare those twins. Repeat for every mover, so the comparison is apples-to-apples rather than apples-to-orchard.
Estimate the propensity score P(treat | X) by logit, then match treated to controls on that score (nearest-neighbour or caliper) or reweight by it (inverse-probability weighting). Entropy balancing instead reweights controls so their covariate moments match the treated group exactly. This removes bias from observed confounders; post-match covariate balance must be verified. It does not address unobservables — that is the role of Heckman and IV.
When the decision to move is tangled up with the outcome, we look for a “nudge” that pushes firms toward moving but touches the stock only through the move — nothing else. We then use only the part of moving that the nudge explains, which is clean of the firm’s own choosing.
Two-stage least squares. Stage 1 regresses the endogenous treatment on an instrument Z plus controls; stage 2 regresses the outcome on the fitted treatment. Validity needs relevance (Z predicts treatment; first-stage F above ~10) and the exclusion restriction (Z affects the outcome only via treatment). It identifies a local average treatment effect for compliers; weak instruments bias estimates back toward OLS.
Compare the before→after change for movers to the before→after change for similar non-movers. Subtracting the two differences removes both what is permanently special about the movers and whatever moved everyone over the same period — leaving the move’s own effect.
A two-way fixed-effects regression: Y = α + δ(Treat×Post) + group FE + time FE + ε, where δ is the DiD estimate. The identifying assumption is parallel trends — absent treatment, treated and control would have evolved together. It is probed (not proven) with pre-period event-study leads: a flat pre-trend is supportive.
Add a third comparison to knock out a confounder that happens to hit the treated group for some unrelated reason at the same time. The extra difference cancels anything that affected the whole group, leaving only the part tied to the treatment itself.
Adds a third dimension (group × time × eligibility); the triple-interaction coefficient is the estimate. It relaxes DiD’s single parallel-trends requirement, absorbing group-specific or time×dimension-specific shocks that a lone DiD would misread as the treatment effect — at the cost of more demanding data and lower power.
Firms do not all move on the same day — they move in waves across many months. A naive fixed-effects design can mislead when the timing varies, because firms that already moved get quietly used as the “control” for later movers. Modern estimators line each firm up by its own start date and compare only clean, not-yet-moved firms.
Under heterogeneous treatment timing, two-way fixed-effects is a variance-weighted average of all 2×2 DiDs — including “forbidden” comparisons that use already-treated units as controls — and can even reverse sign when effects are heterogeneous. We instead use group-time ATT estimators with not-yet- or never-treated controls and aggregate to event-time dynamics.
Each tool answers one specific objection. A finding that survives the whole suite is one that cannot be waved away by any single alternative explanation.
| “But it was really…” — the objection | The check that answers it |
|---|---|
| …just the whole market moving that day | Market / six-factor (FF6) abnormal return |
| …an oil- or sector-price swing | Sector-augmented model (FF6 + oil) |
| …the one window you happened to pick | Romano-Wolf multiple-testing correction |
| …an unusually volatile week | GARCH(1,1) volatility-adjusted inference |
| …firms that were already different in visible ways | Propensity-score matching / entropy balancing |
| …firms different in ways you can’t see | Heckman two-step selection |
| …a hidden third cause driving both | Instrumental variables (IV / 2SLS) |
| …a market-wide trend over the whole period | Difference-in-differences |
| …a trend specific to those firms | Triple-difference |
| …an artifact of using already-moved firms as controls | Staggered DiD (Callaway-Sant’Anna) |
These run alongside the event-study core and honest-inference checks above. Full references appear on the References page; the estimated results, charts, and complete methodology publish here when the study goes live.
The analysis is in active development. When it is complete, the results, charts, and full methodology will appear on this page — presented in the same plain-English, source-linked style as the rest of the Reincorporation Index.
Bookmark this page — the results will be posted here when the study is complete.
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