Building Gormley–Matsa (2016): Playing It Safe?

The Lecture 8 Part 1 corporate-finance DiD, assembled from scratch and checked number by number

How to use this document

Lecture 8’s Part 1 works through Gormley and Matsa’s Playing It Safe? Managerial Preferences, Risk, and Agency Conflicts (Journal of Financial Economics, 2016): the staggered state adoption of business-combination antitakeover laws, and what insulated managers do with the firm’s cash and risk. The slides show results and hide the code; this document does the opposite, rebuilding the whole replication in the order the lecture tells it and printing our reproduced number next to the paper’s for every claim.

Unlike the Olken replication that sits behind this course’s other Lecture 8 companion, this one cannot run end to end on your laptop. Gormley–Matsa rests on Compustat funda/fundq (and, for the risk legs, secd-derived daily returns): licensed instructor data that is gitignored and never redistributable. So the WRDS pulls and every regression that reads the built panel are shown but not executed (eval: false), and their outputs are quoted from the pipeline’s frozen ledgers in outputs/. Exactly one input is free and public — the 33 business-combination-law adoption years, hand-coded from Gormley–Matsa’s Appendix Table A.1 — so the treatment indicator, the cohort map, and a small piece of arithmetic do run, and the two robustness figures rebuild live from committed result ledgers.

Five code chunks in this document execute: the BC-dates spine (§1), the log-points arithmetic (§8), the leave-one-out figure (§13), the standard-error-versus-N figure (§16), and the session-info footer. Everything else is displayed for reading, with its result quoted from a named ledger cell. The pipeline map below says which script produces which number, and whether it runs here.

Two panel vintages appear throughout, and they are never silently mixed. The 1976–2006 baseline is Gormley–Matsa’s own window; the cash and bad-controls legs are quoted on it so they sit against the paper’s own N. The extended 1976–2026 vintage re-runs the same scripts with the sample end pushed to today; the volatility legs are quoted on it because that is where they reach the paper’s sample size. Every table below carries both, side by side, and names its window.

The pipeline at a glance

The build is a small directed graph of scripts. Only the first row and the three figure rows touch no licensed data; everything else reads a gitignored Compustat extract and is shown, not run, with its numbers quoted from the ledger it writes.

Script	Reads	Produces	Runs here?
`code/gm_bc_dates.py`	GM Appendix Table A.1 (printed)	`data/gm_bc_dates.csv` — 33 state→year pairs, treatment rule, cohort map	yes (free)
`pull_compustat_gm.py`	WRDS `comp.funda ⋈ comp.company`	`data/gm_compustat_raw.parquet` (gitignored)	no (`eval:false`)
`pull_compustat_gm_fundq.py`	WRDS `comp.fundq`	`data/gm_fundq_raw.parquet` (gitignored)	no (`eval:false`)
`code/gm_did.py`	built panel	`outputs/gm-pipeline-numbers.md` (G1–G9, B1–B3) + `gm_event_study_cash.png`	no (`eval:false`)
`code/gm_de_robustness.py`	built panel	`outputs/gm-de-robustness.md` (G12, G12b)	no (`eval:false`)
`code/gm_cashflow_vol.py`	panel + `fundq`	`outputs/gm-cashflow-vol.md` (G5)	no (`eval:false`)
`code/gm_stock_vol.py` (+ probe)	panel + BCWX/JKP daily	`outputs/gm-stock-vol.md` (G10, G11)	no (`eval:false`)
`gm_did_rcheck.R`, `gm_phase3_rcheck.R`	built panel	R `fixest` cross-checks	no (`eval:false`)
`code/gm_fig_adoption_timing.py`	`gm_bc_dates` + one quoted share	`figures/gm_adoption_timing.png`	figure (free)
`code/gm_fig_leaveoneout.py`	`outputs/gm-de-robustness.md`	`figures/gm_leaveoneout.png`	yes (parses ledger)
`code/gm_fig_se_vs_n.py`	`outputs/gm-cornerstone-findings.md`	`figures/gm_se_vs_n.png`	yes (ledger numbers)

The three “runnable” figures do not recompute any regression: two of them rebuild the picture from a frozen result ledger, and the adoption-timing figure draws only the printed dates. Read them as renders of committed results, not fresh estimation.

1. The one shareable input: BC-law adoption dates

Everything downstream keys off a single, entirely public fact: which state adopted a business-combination law in which year. Gormley–Matsa print these in Appendix Table A.1, so they carry no licence. code/gm_bc_dates.py transcribes that table into a state→year lookup and a treatment rule, and it is the one piece of this build a student can run.

import sys, os
import pandas as pd
sys.path.insert(0, "code")
import gm_bc_dates as bc

# 33 adopting states, keyed to state of INCORPORATION, sorted by adoption year.
dates = (
    pd.DataFrame(
        [(s, bc.STATE_NAMES[s], y,
          "Pinnell 2000" if s in bc.PINNELL_ADDITIONS else "Bertrand–Mullainathan 2003")
         for s, y in bc.BC_LAWS.items()],
        columns=["state", "name", "adopt_year", "source"],
    )
    .sort_values(["adopt_year", "state"])
    .reset_index(drop=True)
)
dates

	state	name	adopt_year	source
0	NY	New York	1985	Bertrand–Mullainathan 2003
1	IN	Indiana	1986	Bertrand–Mullainathan 2003
2	MO	Missouri	1986	Bertrand–Mullainathan 2003
3	NJ	New Jersey	1986	Bertrand–Mullainathan 2003
4	AZ	Arizona	1987	Bertrand–Mullainathan 2003
5	KY	Kentucky	1987	Bertrand–Mullainathan 2003
6	MN	Minnesota	1987	Bertrand–Mullainathan 2003
7	WA	Washington	1987	Bertrand–Mullainathan 2003
8	WI	Wisconsin	1987	Bertrand–Mullainathan 2003
9	DE	Delaware	1988	Bertrand–Mullainathan 2003
10	GA	Georgia	1988	Bertrand–Mullainathan 2003
11	ID	Idaho	1988	Bertrand–Mullainathan 2003
12	ME	Maine	1988	Bertrand–Mullainathan 2003
13	NE	Nebraska	1988	Bertrand–Mullainathan 2003
14	SC	South Carolina	1988	Bertrand–Mullainathan 2003
15	TN	Tennessee	1988	Bertrand–Mullainathan 2003
16	VA	Virginia	1988	Bertrand–Mullainathan 2003
17	CT	Connecticut	1989	Bertrand–Mullainathan 2003
18	IL	Illinois	1989	Bertrand–Mullainathan 2003
19	KS	Kansas	1989	Bertrand–Mullainathan 2003
20	MA	Massachusetts	1989	Bertrand–Mullainathan 2003
21	MD	Maryland	1989	Bertrand–Mullainathan 2003
22	MI	Michigan	1989	Bertrand–Mullainathan 2003
23	PA	Pennsylvania	1989	Bertrand–Mullainathan 2003
24	WY	Wyoming	1989	Bertrand–Mullainathan 2003
25	OH	Ohio	1990	Bertrand–Mullainathan 2003
26	RI	Rhode Island	1990	Bertrand–Mullainathan 2003
27	SD	South Dakota	1990	Bertrand–Mullainathan 2003
28	NV	Nevada	1991	Bertrand–Mullainathan 2003
29	OK	Oklahoma	1991	Bertrand–Mullainathan 2003
30	OR	Oregon	1991	Pinnell 2000
31	IA	Iowa	1997	Pinnell 2000
32	TX	Texas	1997	Pinnell 2000

The roster runs from New York in 1985 to Iowa and Texas in 1997 — 33 states in all. Thirty of them are the Bertrand–Mullainathan (2003) set that adopted between 1985 and 1991; Gormley–Matsa add three more from Pinnell (2000) — Oregon (1991), Iowa and Texas (both 1997). The absorbing treatment dummy switches on in a firm’s adoption year and stays on, and firms incorporated in a never-adopting state (Florida, California) are never treated:

checks = {
    "DE treated in 1987 (before its 1988 law)": bc.is_treated("DE", 1987),
    "DE treated in 1988 (adoption year)":       bc.is_treated("DE", 1988),
    "FL treated in 2000 (never adopts)":        bc.is_treated("FL", 2000),
    "states in the full set":                   len(bc.BC_LAWS),
    "states in the BM-only 30-state subset":    len(bc.bm_only()),
}
checks

{'DE treated in 1987 (before its 1988 law)': 0,
 'DE treated in 1988 (adoption year)': 1,
 'FL treated in 2000 (never adopts)': 0,
 'states in the full set': 33,
 'states in the BM-only 30-state subset': 30}

The bm_only() subset drops the three Pinnell additions to recover the core 30-state Bertrand–Mullainathan design the literature standardised on — a robustness leg we return to in §7. The treatment is assigned on the firm’s state of incorporation, which is the whole design and the subject of the next section. In the paper’s own words on what the laws reach:

These state laws applied only to target firms incorporated in the state.

and, from footnote 1,

the BC laws make only hostile takeovers of target firms incorporated in that state more difficult. Friendly mergers are unaffected by the law, as are hostile takeovers of firms incorporated elsewhere, even when the acquirer is incorporated in the affected state.

The timing is easiest to read as a strip. Delaware — the dot to watch, because it carries 53.4% of firm-year observations in the baseline panel (gm-pipeline-numbers.md §G1) — adopts in 1988. The figure below is drawn by gm_fig_adoption_timing.py, which needs only the dates above plus that one quoted share; it is committed and regenerable, shown here as a static image.

Adoption timing: 33 states, 1985–1997, keyed to state of incorporation. Delaware (1988) is the dominant cohort at 53.4% of baseline firm-year observations.

2. Incorporation versus location: where identification comes from

Treatment follows the state a firm is incorporated in, not the state where it operates — and those come apart. More than 60% of firms incorporate and locate in different states, and that gap is the entire identification argument. Because incorporation and location are distinct, the regression can absorb everything that hits a location in a given year (local business cycles) and everything that hits an industry in a given year, and still have treatment variation left to read. In the authors’ words:

Using a difference-in-differences estimator, we compare changes among firms located in states that pass a BC law with changes among firms incorporated elsewhere. The underlying identification assumption is that, but for the law, the two sets of firms would follow parallel trends; that is, the change in outcome $y$ for firms incorporated in the states that pass a BC law would have been the same as for firms incorporated in states that did not pass a BC law.

and the sentence that licenses the state-by-year fixed effects:

We are able to obtain estimates for the BC laws’ effects even after including state-by-year fixed effects because more than 60% of our firms are incorporated and located in different states. Our estimates are identified by comparing the differential response of two firms that operate in the same state, $l$, but when only one of these firms is incorporated in a state, $s$, that passes a BC law. Thus, any unobserved, time-varying state-level factors, such as local business cycles, that could coincide with a BC law’s adoption and affect our outcomes of interest do not bias our findings.

The 2×2, and why location does not confound it

Two firms in the same building in Palo Alto, selling to the same customers, in the same industry:

Firm	Incorporated in	Operates in	Treated from
A	Delaware	California	1988, when Delaware adopts
B	California	California	never — California does not adopt

A California-by-year shock hits both identically and is swept out by the location-by-year fixed effect. What remains is that one of them was treated in 1988 because of a filing cabinet in Wilmington. That is the variation the design uses.

The >60% figure is Gormley–Matsa’s own (gm-cornerstone-expectations.md, “What we reproduce”); we do not recompute it here, because doing so needs the Compustat header that carries incorporation and location state.

3. Recall the week-6 machinery

Nothing in the estimand is new this week. The target is the average treatment effect on the treated,

\[ \text{ATT} = E\!\left[\,Y_{it}(1) - Y_{it}(0)\;\middle|\;W_{it}=1\,\right], \]

with $Y_{it}(1)$ and $Y_{it}(0)$ the two potential outcomes for firm $i$ in year $t$ and $W_{it}$ the treatment indicator. It is identified under the four week-6 assumptions — consistency, no anticipation, no interference, and parallel trends — the last of which Gormley–Matsa state exactly as the “but for the law … the two sets of firms would follow parallel trends” sentence quoted above. The one genuinely new object is that $W_{it}$ switches on at a different date for different firms: staggered adoption. A single before-after 2×2 becomes a stack of them, one per adoption cohort, and that stack is where the staggered-DiD problems of §12 come from. Everything from §4 onward is week-6 machinery run on real data.

4. Assembling the panel from Compustat

The panel is a WRDS pull followed by a handful of sample screens. The pull joins comp.funda to the comp.company header for the incorporation and location states, and — crucially — applies no common-stock or size screen. That absence is deliberate: it is the whole reason this cornerstone reproduces where a CRSP-screened one attenuates (§18 returns to that contrast). The complete, runnable pull is pull_compustat_gm.py; its core query, shown but not executed here:

# pull_compustat_gm.py — WRDS Compustat annual pull (INSTRUCTOR-DATA, gitignored).
# No CRSP, no common-stock screen. Treatment/cluster key is c.incorp; the
# location-by-year FE uses c.state (HQ). Runnable with WRDS access:
#   (the pull script lives in the private working repo; not shipped here)
import wrds
conn = wrds.Connection(wrds_username=os.environ["WRDS_USER"])
df = conn.raw_sql("""
    select f.gvkey, f.fyear, f.datadate, f.sich,
           f.at, f.sale, f.ni, f.ch, f.che,
           f.dltt, f.dlc, f.lt, f.re, f.wcap, f.oiadp,
           f.csho, f.prcc_f, f.dvc, f.prstkc, f.act, f.lct, f.dp,
           c.incorp as inc_state,   -- TREATMENT: state of incorporation
           c.state  as hq_state,    -- location, for the location-by-year FE
           c.loc    as hq_loc, c.sic as header_sic
    from comp.funda f
    left join comp.company c on f.gvkey = c.gvkey
    where f.indfmt='INDL' and f.datafmt='STD' and f.popsrc='D' and f.consol='C'
      and f.fyear between 1974 and 2026 and f.at is not null and f.at > 0
""")

The screens Gormley–Matsa describe are applied downstream in gm_did.py, so the drop counts stay visible. In the paper’s own statement of them:

We obtain firms’ financial data from Compustat, excluding regulated utility firms (SIC codes 4900–4999), firms located or incorporated outside the US, and firm-year observations with either missing or negative assets or sales. Financial ratios are winsorized at the 1% level. To include at least ten years of data before and after each law’s adoption, our sample period is 1976–2006.

and, on the endogeneity of incorporation itself:

To avoid endogenous changes in whether a firm is subject to a BC law, we exclude firms that reincorporate from a state without a BC law to a state with a BC law or vice versa.

Our build uses the current Compustat incorporation header rather than Gormley–Matsa’s historical (Cohen 2012) coding. Their footnote 6 settles that this is immaterial:

Relative to the most recent version of Compustat, our historical data change the state of incorporation for about 6% of observations and change treatment status for only 2% of observations.

so the current-header build is Gormley–Matsa’s own stated robustness variant. The build code, shown but not executed:

# gm_did.py — build_panel(): screens, outcomes, treatment (INSTRUCTOR-DATA).
df = df[df["hq_loc"] == "USA"]
df = df[df["inc_state"].isin(US_STATES) & df["hq_state"].isin(US_STATES)]
df["sic4"] = pd.to_numeric(df["sich"].fillna(df["header_sic"]), errors="coerce")
df = df[~df["sic4"].between(4900, 4999)]           # utilities only (GM keeps financials)
df = df[(df["at"] > 0) & (df["sale"] > 0)]
df["ln_cash"] = np.log(df["ch"].where(df["ch"] > 0))   # ln(ch); ch>0 only
df["cash_at"] = df["che"] / df["at"]
for c in ["cash_at", "ch_at", "roa", "debt_at", "payout_at"]:
    df[c] = winsorize(df[c], 0.01, 0.99)               # ratios winsorized 1/99
df["bc"] = [is_treated(s, int(y)) for s, y in zip(df["inc_state"], df["fyear"])]
df["bc_cohort"] = df["inc_state"].map(adoption_year)   # cohort = adoption year

The resulting sample is quoted below on both vintages (gm-pipeline-numbers.md §G1 and gm-pipeline-numbers-2026.md §G1). A student who checks GM’s location assignment will find it is the headquarters — “We assign a firm’s location based on the location of its headquarters, which is typically also where major plants and operations are located.”

	1976–2006 baseline	Extended to 2026
Ln(cash) firm-years	174,627 (GM 172,739; within 1.1%)	262,641
Unique firms	17,837	22,266
Treated incorporation-states	33	33
Never-treated firm-years	18,639	24,522
Delaware share of observations	53.4%	55.8%

The extension adds only post-treatment and never-treated mass — every adoption is 1985–1997 — so it introduces no new staggered-timing comparisons, only more data of the kinds already present.

5. From the 2×2 to the regression we run

The design maps onto two specifications, worth seeing side by side because the contrast between them is the identification lesson. The teaching baseline is the week-4/week-5 two-way fixed-effects model,

\[ Y_{it} = \alpha_i + \lambda_t + \delta\,W_{it} + u_{it}, \]

firm and year fixed effects with one treatment dummy. Gormley–Matsa’s own specification replaces the year effect with location-state-by-year and four-digit-industry-by-year effects (their Eq. 4):

\[ y_{ijlst} = \beta_1\,BC_{st} + f_i + \omega_{lt} + \lambda_{jt} + \eta_{ijlst}, \]

which the authors read out as:

$f_i$ are firm fixed effects; $\omega_{lt}$ are state-by-year fixed effects; and $\lambda_{jt}$ are four-digit SIC industry-by-year fixed effects. … Finally, we adjust the standard errors for clustering at the state-of-incorporation level.

The extra structure is exactly what the incorporation-versus-location gap pays for, and it is what makes the heavy-FE estimate defensible:

The inclusion of state-by-year and industry-by-year fixed effects ensures that our difference-in-differences estimates are robust to many types of unobservable omitted variables that could otherwise confound our analysis.

Two choices carry the weeks-1-through-5 material into this design. First, the standard errors cluster on state of incorporation — the level treatment is assigned at, the clustering lesson from lecture4.qmd used in anger, and the number that comes back to bite us in §16. Second, there are no firm controls in the headline: no size, no leverage, no profitability on the right-hand side. That is deliberate, and §14 is its defence. In pyfixest, the headline is one line:

# gm_did.py:143 — paper FE spec, clustered on incorporation state (INSTRUCTOR-DATA).
import pyfixest as pf
FE_PAPER = "gvkey + hq_state^fyear + sic4^fyear"     # firm + loc-state×year + sic4×year
m = pf.feols("ln_cash ~ bc | " + FE_PAPER, data=d_cash, vcov={"CRV1": "inc_state"})

6. Threats, named before results

Four ways this could be wrong, named before a single estimate appears — a commitment device that stops the diagnostics from being chosen after the fact to flatter the result. Three of the four are omitted-variable stories in the weeks-1-2 sense: something left out that correlates with both treatment and cash. The fourth is the mirror image, and the one students most often get wrong: a variable wrongly put in, one the treatment itself moves.

#	Threat	The story	Answered in
i	Pre-existing drift	cash was already trending up in treated states before adoption	§10 (event study), §11 (placebo)
ii	Staggered contamination	already-treated firms used as controls for later cohorts (Goodman-Bacon)	§12 (Sun–Abraham)
iii	A dominant cohort	Delaware alone is 53% of the file and adopts in 1988	§13 (drop DE, leave one out)
iv	Bad controls	conditioning on size/leverage/ROA, which the law itself moves	§14

Gormley–Matsa’s own defence against threat (i)/(iii)-style legislative endogeneity leans on the political economy of the laws:

Romano (1987) and Bertrand and Mullainathan (2003) find that the passage of these laws typically did not result from the pressure of a large coalition of economic players in the state and conclude that an omitted economic variable is unlikely to explain measured effects of the law.

and on a five-part run of evidence they summarise as:

First, we find no measureable differences in the ex ante characteristics of firms incorporated in states adopting the laws. Second, no preexisting trends exist … before the laws come into effect. … All five of these results suggest that our findings are not explained by legislative endogeneity.

Each threat gets its own section, in the order above, and each answer is reported whether or not it is comfortable.

7. The headline: what the paper found, and what the rebuild found

Same law, same window, an independently assembled Compustat extract. The sample lands within 1.1% of the paper’s, the coefficient at 89% of theirs, and — the detail worth dwelling on — estimated more precisely than the paper’s own (t 2.89 against 2.47). Numbers from gm-pipeline-numbers.md §G1/§G2/§G3/§G8 and gm-cornerstone-findings.md, headline verdict; extended column from gm-pipeline-numbers-2026.md.

	GM (2016), Table 2	Rebuild, 1976–2006	Rebuild, extended 2026
Ln(cash), N	172,739	174,627 (within 1.1%)	262,641
Ln(cash)	+0.121 (t 2.47)	+0.1081 (SE 0.0374, t 2.89, p .006)	+0.1057 (SE 0.0408, t 2.59, p .013)
Cash ratio, che/at	+0.0023, ns	−0.0024 (SE 0.0027, t −0.90)	−0.0018 (t −0.68)
BM-only 30-state	≈ +0.121	+0.1225 (t 2.77)	+0.1194 (t 2.44)
Alternative timing (first full year)	—	+0.0624 (t 1.68)	+0.0614 (t 1.52)

The closest apples-to-apples row is the last-but-one: dropping the three Pinnell late-adopters (Iowa, Oregon, Texas) to recover Gormley–Matsa’s core 30-state Bertrand–Mullainathan design gives +0.1225 (t 2.77), a whisker from the paper’s +0.121. A replication that lands within one percent on sample size has the same firms in it, which is what licenses reading the coefficient comparison at all.

The estimate is identical in R. gm_did_rcheck.R re-runs the same built panel through fixest::feols and reproduces pyfixest to the reported precision:

m = pf.feols("ln_cash ~ bc | gvkey + hq_state^fyear + sic4^fyear",
             data=d_cash, vcov={"CRV1": "inc_state"})
# -> bc = +0.1081, t 2.89, N 174,627   (gm-pipeline-numbers.md §G2)

# gm_did_rcheck.R — reads the identical built panel Python used.
library(fixest); library(arrow)
d <- as.data.frame(read_parquet("data/gm_panel_built.parquet"))
d <- d[!is.na(d$ln_cash), ]
m_paper <- feols(ln_cash ~ bc | gvkey + hq_state^fyear + sic4^fyear,
                 data = d, cluster = ~inc_state)
# -> beta +0.1081, t 2.89, N 174,627   (matches pyfixest exactly)

One sentence on why this paper: Gormley–Matsa’s cash sample is Compustat-native with no common-stock screen, so it structurally escapes the CRSP-screen attenuation that hit the runner-up cornerstone (Serfling 2016) on the same install (gm-cornerstone-findings.md, Serfling comparison) — the reason it was chosen over an otherwise-similar staggered-law design.

8. Reading the coefficient

The headline is on log cash, so exponentiating turns it into a percentage. This is pure arithmetic on printed coefficients — no data — so it runs:

import numpy as np
import pandas as pd

pd.DataFrame({
    "source":        ["Rebuild (1976–2006)", "GM (2016) printed"],
    "beta_ln_cash":  [0.1081, 0.121],
    "pct_change":    [np.exp(0.1081) - 1, np.exp(0.121) - 1],
}).assign(pct_change=lambda d: (d["pct_change"] * 100).round(1))

	source	beta_ln_cash	pct_change
0	Rebuild (1976–2006)	0.1081	11.4
1	GM (2016) printed	0.1210	12.9

So $\exp(0.1081)-1 \approx 11.4\%$ more cash, against Gormley–Matsa’s own 12.1 log points, “or about 13%.” Insulated managers hold more cash — precautionary hoarding, or a quiet life; this lecture does not adjudicate between those stories and should not pretend to. The caveat arrives immediately, in the next section: the cash ratio does not move.

9. Log-level versus ratio: the same data, two answers

Cash grew. So did assets. Which normalisation gets used is a modelling choice with a real answer attached, not a formatting detail — and here the two choices disagree. Numbers from gm-pipeline-numbers.md §G3 (extended column §G3 of the 2026 file).

Outcome	Rebuild, 1976–2006	Rebuild, extended 2026	GM (2016), printed
Ln(cash)	+0.1081 (t 2.89), N 174,627	+0.1057 (t 2.59)	+0.121 (t 2.47)
Cash ratio che/at	−0.0024 (SE 0.0027, t −0.90), N 193,261	−0.0018 (t −0.68), N 283,331	+0.0023 (SE 0.0034), ns
Cash ratio ch/at	+0.0013 (t 0.51)	+0.0015 (t 0.54)	—

The disagreement is not a replication failure: Gormley–Matsa’s own printed ratio result is null too. In their words,

Average total cash holdings increase by 12.1 log points, or about 13%, after a BC law is adopted (Column 5), but the increase in the ratio of cash to book assets is smaller and not significant (coefficient = 0.0023, standard error = 0.0034).

So both builds say the same thing — the level of cash moves and the share of the balance sheet held as cash does not — which means assets grew roughly in step with cash. Whether that is the interesting fact or a nuisance depends entirely on the question. A student who reports only the specification that moved has not made a coding error; they have made a write-up error.

Why the sample sizes differ

The three cash rows run on different N: Ln(cash) needs ch > 0 (193,261 firm-years have a defined cash ratio, but only 174,627 have positive cash to log), and the ratio uses the full defined sample. This is the same reason the §11 placebo (56,006) and the headline (174,627) differ — different rows are eligible for different questions. Naming the estimation sample is part of naming the estimate.

10. Pre-trends: the event study GM never drew

Gormley–Matsa plot acquisitions, not cash — their Figure 2 is the acquisition event study, and nobody draws the cash pre-trend. So we did. The figure below (from gm_did.py, static; its source needs the licensed panel and is not regenerated here) puts the reference year at $k=-1$ and reads the leads. Numbers from gm-pipeline-numbers.md §G6/§G7.

Ln(cash) event study, reference year k = −1, firm + location-state×year + industry×year fixed effects, SEs clustered on state of incorporation. 1976–2006 baseline panel, N 174,627.

The leads all clear the bar — $t$ of $\{-5:-1.64,\ -4:-1.45,\ -3:-1.00,\ -2:-1.26\}$, every $|t|<1.65$ — which is the parallel-trends evidence the paper never shows for cash. But the honest beat is that every lead sits mildly negative, and $k=-5$ is a whisker from the line at $-1.64$: a faint hint of an upward cash drift into adoption. Not a violation; the “is this pre-trend real?” moment. After adoption the effect is immediate and sustained — $k=0$ at +0.0696 (t 3.2), holding to $k=5$ at +0.1002 — but it dips at $k=2$ (+0.0225) rather than phasing in monotonically.

Logged honestly as CHECK, not PASS

The dynamics are an immediate, persistent, growing increase, but not a strict monotone phase-in. The pipeline records G7 as CHECK, and this document does not launder it to PASS. Gormley–Matsa’s own timing claim is the qualitative one this supports: “the law’s adoption precedes the effects we assign to it instead of the other way around.”

11. The placebo, reported honestly

Move every adoption three years earlier and estimate on the pre-period alone. Nothing happened in those years, so the coefficient should be zero. It is insignificant — +0.0591 (t 1.68), N 56,006 (gm-pipeline-numbers.md §G9; extended: +0.0603, t 1.65, N 61,889) — but it leans positive, in exactly the direction the mild leads of §10 hinted at.

A placebo that “passes” at 1.96 and a pre-trend that “passes” at 1.65 can be telling you the same soft thing. “The placebo is insignificant” is a true sentence and an incomplete one; the reader is owed the coefficient, the $t$, and the direction it leans. This is the same report-don’t-launder discipline the pre-testing literature (week 6) asks for.

12. Staggered timing is not one experiment

With 33 treated cohorts and a thin never-treated group, the static two-way fixed-effects coefficient is exposed to the Goodman-Bacon problem: some of its identifying 2×2s use already-treated firms as controls for later-adopting ones, a comparison nobody intended. The structure is visible from the shares alone (gm-pipeline-numbers.md §B1): 33 treated incorporation-states versus 18 never-treated; treated-state firm-years 89% against 11% never-treated; and Delaware alone is 53% of observations, adopting in 1988, so the DE-1988 cohort’s 2×2s carry heavy weight while the clean control group is small. Exact Goodman-Bacon weights need a balanced panel, so this is kept qualitative; the quantitative answer is the heterogeneity-robust estimator, whose natural tool here is Sun–Abraham (fixest::sunab).

# gm_did_rcheck.R — Sun-Abraham event study, never-treated as control.
d$cohort <- ifelse(is.na(d$bc_cohort), 10000, d$bc_cohort)
m_sa <- feols(ln_cash ~ sunab(cohort, fyear) | gvkey + fyear,
              data = d, cluster = ~inc_state)
aggregate(m_sa, agg = "att")
# -> ATT +0.169 (SE 0.0507, t 3.33, p .0016); path k0..k5 +0.093 → +0.088

# gm_did.py — cohort × relative-time saturated design, never-treated control.
# Overall post ATT (cohort-share weighted) = +0.1012
# path k0..k5: +0.0999, +0.0820, +0.0674, +0.0883, +0.1326, +0.1369

Both implementations survive: the aggregate ATT is positive and significant, and the event-time path is positive and roughly flat under each (gm-pipeline-numbers.md §B2, R cross-check). The two aggregates differ — Python’s +0.1012 against R’s +0.169 (t 3.33, p .0016) — because of aggregation weighting and endpoint binning, not because one is wrong.

Report the sign and the path, never one SA number

A heterogeneity-robust estimate is a family of estimates; quoting one of them to three decimal places as “the answer” overstates what the method delivers. The teachable fact is that the sign and the path survive the correction — the static coefficient was not an artefact of forbidden comparisons.

This is the one diagnostic with no Gormley–Matsa quote: the paper predates the staggered-DiD critique, so the estimator is attributed to Sun & Abraham (2021) and this companion, not to the original.

13. Kill the dominant cohort: drop Delaware, then leave one state out

Delaware is 53% of the sample and adopts in 1988, so the single most direct robustness check is to remove it entirely and see if the result dies. It does not (gm-de-robustness.md §G12): dropping Delaware takes N from 174,627 to 81,345 and gives paper-FE Ln(cash) +0.1429 (SE 0.0667, t 2.14, p .037) — positive, still significant, and in fact larger than the full-panel +0.1081, because the heavy fixed-effect structure no longer competes with the dominant cohort for the same variation (the firm+year baseline on the DE-excluded sample is +0.1470, t 2.94). This matches Gormley–Matsa’s own §6.4, and their summary of the whole robustness family:

Finally, our findings are robust to alternative samples, time periods, and empirical specifications, including excluding firms incorporated in Delaware (50% of observations) or any of the 32 other states that adopted a BC law.

That last clause — any of the 32 other states — is the leave-one-out sweep, which the pipeline runs and which this document rebuilds live. gm_fig_leaveoneout.py parses the 33-row table straight out of the committed ledger (it asserts exactly 33 rows, so a drifted ledger fails loudly) and plots the firm+year-FE coefficient with each treated state dropped in turn:

import contextlib, io
sys.path.insert(0, "code")
import gm_fig_leaveoneout
with contextlib.redirect_stdout(io.StringIO()):
    gm_fig_leaveoneout.main()   # rebuilds the figure from outputs/gm-de-robustness.md
from IPython.display import Image
Image("outputs/figures/gm_leaveoneout.png")

Across all 33 states the coefficient stays in [+0.1394, +0.1678] and never changes sign — minimum when Minnesota is dropped (+0.1394, t 3.94), maximum when New York is dropped (+0.1678, t 4.56), against a full-panel firm+year baseline of +0.1472 (gm-de-robustness.md §G12b). The punchline is a sentence students can reuse in any staggered design: identification does not rest on any single treated unit, and if it does, that is a finding about the paper, not about the world.

14. Bad controls versus AvgE: two ways to break a clean estimate

The absence of firm controls in the headline (§5) was deliberate, and this is its defence. Size, leverage and profitability are all things a business-combination law can move, so conditioning on them shuts down part of the very channel being measured. Gormley–Matsa’s literal demonstration of this (their Table 7) is on the number of acquisitions — an SDC-gated outcome we cannot build — so the lesson is run here on Ln(cash) instead, where both directions of bias show up on a single outcome (gm-pipeline-numbers.md §B3, extended §B3).

Specification	1976–2006	Extended 2026
Proper FE, no controls	+0.1081 (t 2.89, N 174,627)	+0.1057 (t 2.59)
+ endogenous “bad controls” (log assets, leverage, ROA)	+0.0795 (t 3.18, N 174,624)	+0.0698 (t 2.60)
AvgE “common error” (group-mean DV in place of FE)	+0.1942 (t 6.68, N 174,627)	+0.2357 (t 9.56)

Post-treatment mediators attenuate the estimate by about 26%; the “AvgE” substitution documented in Gormley & Matsa’s (2014) Common Errors — replacing the fixed effects with a group average of the dependent variable, which looks like a control and is not — inflates it by about 80%. Bias runs in both directions from one clean estimate.

The detail that lands hardest

Read the $t$ column top to bottom: 2.89, then 3.18, then 6.68. Both mistakes make the result look better — tighter, more publishable. A rising t-statistic is not evidence that a specification improved. The exam-shaped rule: a control that the treatment itself moves is not a control; it is part of the effect being measured (Angrist–Pischke on bad controls; Gormley & Matsa 2014).

15. Did they actually get safer? Three risk measures

Gormley–Matsa’s substantive claim is that insulated managers take less risk. Three measures test it, and they return three different verdicts. Two of the three are built from Compustat-secd-derived daily returns with no CRSP anywhere in the pipeline — the deliberate stress test, since Gormley–Matsa build their volatility from CRSP. Quoting GM’s own “from CRSP” beside our no-CRSP build is what makes the stress explicit.

Both vintages, from gm-cashflow-vol{,-2026}.md and gm-stock-vol{,-2026}.md:

Measure	Rebuild, baseline	Rebuild, extended 2026	GM (2016)	Verdict
Cash-flow volatility	−0.0015 (t −0.92), N 102,153	−0.0024 (t −1.05), N 159,268	−0.0028, ns	null reproduced — PASS
Stock volatility	−0.0172 (t −2.26), N 81,936	−0.0232 (SE 0.0081, t −2.88, p .006), N 132,446	−0.023 (SE 0.008), N 132,494	holds — PASS
Operating-asset volatility	−0.0131 (t −1.69), N 75,919	−0.0152 (SE 0.0090, t −1.69, p .097), N 125,131	−0.015 (SE 0.006), N 120,401	directional only — CHECK

Reproducing a null is a pass, and students rarely believe that until it is said. Cash-flow volatility comes in at −0.0015 (t −0.92) against Gormley–Matsa’s own −0.0028, ns; more data on the extended panel keeps it null. Stock volatility is the stress test and it passes: −0.0232 (t −2.88) on the extended daily panel, essentially on GM’s N and magnitude. Operating-asset volatility lands right on GM’s −0.015 but stops just short of the bar at t −1.69 — recorded as CHECK, not laundered to PASS.

The three constructions, in Gormley–Matsa’s own words and our faithful code. Stock volatility:

we calculate a firm’s stock volatility using the square root of the sum of squared daily stock returns over the year.

and Table A.2: “Calculated from Center for Research in Security Prices (CRSP) … the raw sum is multiplied by 252 and divided by the number of trading days.” Our leg does exactly this, from secd-derived daily returns rather than CRSP:

# gm_stock_vol.py — GM's raw (non-demeaned) sum-of-squares, annualized inside the root.
m["r2"] = m["ret"] ** 2
g = m.groupby(["gvkey", "fyear"]).agg(n_days=("ret", "size"), ssr=("r2", "sum"))
g["stockvol"] = np.sqrt(252 / g["n_days"] * g["ssr"])   # NOT a demeaned SD × √252

Operating-asset volatility unlevers that:

we approximate the volatility of a firm’s returns on operating assets using the product of a firm’s stock volatility and its market value ratio of equity to operating assets. This approximation holds exactly if both debt and cash are risk-free.

with Table A.2’s formula Stock volatility × [E/(V−C)], E/(V−C) = (csho × prcc_f) / [lt + (csho × prcc_f) − ch]. Cash-flow volatility is “the annual standard deviation of a firm’s quarterly ratio of cash flow to assets,” from a quarterly fundq pull:

# gm_cashflow_vol.py — quarterly Sloan-accruals CF/assets, within-year SD.
accruals_q = q["d_actq"] - q["d_cheq"] - q["d_lctq"] + q["d_dlcq"] - q["dpq"]
q["cf_at"] = (q["oiadpq"] - accruals_q) / q["atq_lag"]
cfvol = q.groupby(["gvkey", "fyearq"])["cf_at"].std()   # SD across the year's 4 quarters

Two caveats that govern how this table is read

The quarterly item mapping is our inference. Gormley–Matsa print the annual Sloan-accruals formula and the verbal “quarterly ratio,” but no quarterly item mapping (gm-cornerstone-expectations.md, Phase-3 build note). The specific quarterly items above are ours, not GM-verbatim.

Our volatility levels run 18–26% below GM’s, so read percent-of-mean, not absolute agreement. On the extended panel the stock-vol mean is 0.500 against GM’s Table A.3 value of 0.611 (~18% below), operating-asset 0.296 against 0.400 (~26% below), cash-flow vol 0.0645 against 0.084 (gm-stock-vol-2026.md, sample block). So our −0.0232 is 4.6% of our own mean against GM’s −0.023/0.539 = 4.3% of pre-law — matching, if anything slightly larger, proportionally. An earlier “proportional down-scaling” reading was RETRACTED in Phase 3.5 (the level gap widened while the coefficient rose to GM’s), and this document does not revive it.

Why operating-asset volatility is the leg that matters and the softer one: it is Gormley–Matsa’s tool for isolating business risk from the mechanical financial-risk channel folded into equity volatility — and §7’s cash result confirms that channel is active (firms raise cash, which mechanically lowers equity volatility even with unchanged business risk). So stock volatility’s significance does not by itself confirm the business-risk story; G11 is the construct-specific test, and it is under the bar. A probe (gm_stockvol_opsample_probe.py) shows why: the 6,017 firm-years dropped for undefined E/(V−C) carry a disproportionate −0.0403 (t −3.06) stock-vol effect under firm+year FE, so the sub-2 $t$ is sample composition on the truncated 1984–2006 daily span, not a construction failure.

16. Why more data didn’t help: standard errors versus N

The obvious diagnosis of the operating-asset leg’s soft $t$ is power, so the panel was extended to 2026, reaching essentially GM’s own sample size (125,131 against GM’s 120,401) and landing on GM’s own −0.015. The $t$ stayed −1.69. That is the segment’s sharpest inference lesson, and it is worth teaching rather than burying (gm-cornerstone-findings.md, Phase 3.5).

The reason is the clustering choice from §5. Standard errors cluster on state of incorporation — roughly 51 clusters, a count fixed by law-adoption geography that added years do not grow. More within-cluster observations do not shrink a clustered SE the way iid N would. The figure below (gm_fig_se_vs_n.py, hard-coding the Phase-3.5 SEs from the findings ledger) compares the SE an iid model predicts at the extended N against the actual clustered SE:

import contextlib, io
sys.path.insert(0, "code")
import gm_fig_se_vs_n
with contextlib.redirect_stdout(io.StringIO()):
    gm_fig_se_vs_n.main()   # numbers from gm-cornerstone-findings.md, Phase 3.5
from IPython.display import Image
Image("outputs/figures/gm_se_vs_n.png")

For operating-asset volatility the SE rose from 0.0078 to 0.0090 on +65% N; an iid model predicts ≈0.0061 at the extended N, so the actual clustered SE is +48% above iid. Stock volatility shows the same pattern (predicted ≈0.0060, actual 0.0081, +35% above iid), but its larger effect clears the bar anyway. The lesson for students: more observations do not buy precision when the thing you cluster on is fixed. This is an inference-precision limit, not small-N, and it ties straight back to §5’s clustering decision.

17. The card we wrote before we ran anything

Every expectation in the scorecard below was frozen before the first line of estimation code ran (gm-cornerstone-expectations.md); the verdicts were filled in afterwards. The previous sections are this card being scored. Two rows are verdicts on the replication process itself, not on the paper — and they are kept red, not laundered.

Leg	Written before the code	Found	Verdict
Ln(cash) headline	≈ +0.121, t ≥ 2	+0.108, t 2.89	PASS
Cash ratio che/at	≈ +0.0023, ns	−0.0024, t −0.90	PASS (null)
Event-study leads	flat, all \|t\| < 1.65	−1.64, −1.45, −1.00, −1.26	PASS
Dynamic phase-in	rises and stabilises	immediate + persistent, dip at k2	CHECK
Placebo, three years early	insignificant	+0.0591, t 1.68	PASS (borderline)
Sun–Abraham ATT	sign preserved	+0.101 Python / +0.169 R, both sig.	PASS
Delaware excluded	positive, ideally significant	+0.1429, t 2.14	PASS
Cash-flow volatility	≈ −0.0028, ns	−0.0015, t −0.92	PASS (null)
Stock volatility	≈ −0.023, t ≤ −2	−0.0232, t −2.88	PASS
Operating-asset volatility	≈ −0.015, t ≤ −2	−0.0152, t −1.69	CHECK
Phase-3 reading: vol coefficients scale down with the lower vol levels	(written after Phase 3, not before)	level gap widened while the coefficient rose to GM’s	RETRACTED
Conjecture: the soft leg just needs more N	iid scaling put t ≈ −2.1 at GM’s N	N reached, t stayed −1.69, SE 48% above iid	REFUTED

The reason the green rows mean anything is that the middle column was frozen before any code ran: a PASS you could not have failed is not a pass. The two red rows are the honest part — a reading withdrawn (§15’s level caveat) and a conjecture the data refuted (§16’s clustering finding). Card: gm-cornerstone-expectations.md; the two red rows: gm-cornerstone-findings.md, Phase 3.5.

18. What to believe, and how much

The deliverable of the whole segment is not any single coefficient; it is an ordering of the claims by how much weight each carries.

Insulated managers hold more cash — solid. The headline (+0.108, t 2.89) survived four attempted breakages: the event study, the placebo, the Sun–Abraham re-estimation, and the drop-Delaware-plus-leave-one-out sweep. Nothing moved the sign, and little moved the magnitude.
Equity risk falls — reproduces. Stock volatility declines at t −2.88 on a daily panel assembled from Compustat with no CRSP — the harder road, and the one students can imagine walking.
Business risk falls — directional only. Operating-asset volatility lands on GM’s magnitude but at t −1.69, and §16 explained why more data will not fix it. This is the honest weak point of the risk story.
Cash-flow volatility is unchanged — a null, and GM’s own. Reported as a result because reproducing the paper’s null is the result.

Then the hand-off to Part 2: today the danger was a variable wrongly included or wrongly omitted in a causal design. Next it is the same disease in an asset-pricing model — where what gets left out of the specification prices what stays in.

19. Skeptic’s appendix

Four objections a careful reader would raise, each already measured, plus two things genuinely out of reach.

Parallel trends holds by the bar, not pristinely. The event-study leads are all mildly negative and $k=-5$ sits at t −1.64; the three-years-early placebo is +0.0591 (t 1.68). Both clear their thresholds and both lean the same soft way (gm-cornerstone-findings.md, caveat 2). Reported, not hidden.
Delaware dominance. 53% of observations on the baseline panel, 55.8% extended, adopting in 1988, with the never-treated share only 11% (9% extended). Answered by §13’s drop-DE and leave-one-out sweeps, but the caveat stays live.
Our volatility levels run below GM’s. Stock-vol mean 0.500 against 0.611, op-asset 0.296 against 0.400, cash-flow vol 0.0645 against 0.084 — so the numbers in §15 are read percent-of-mean, where −0.0232 is 4.6% of our mean against GM’s 4.3% of pre-law (gm-stock-vol-2026.md, sample block). The “proportional down-scaling” reading was retracted.
Incorporation is the current Compustat header, not Cohen (2012) historical coding. Gormley–Matsa footnote 6 settles it: historical coding changes treatment status for about 2% of observations, conclusions unchanged, so this build is their stated robustness variant.

Genuinely out of reach, and worth one honest sentence each if asked: performance-related exit (Gormley–Matsa build it from CRSP delisting codes 400–500, 550, 552, 560, 561, 572, 574, 580, 584 — “we use CRSP delisting codes to construct an indicator variable that equals one when firms exit our sample because of bankruptcy, liquidation, or other performance-related reasons” — which we do not have), and the literal Table-7 acquisitions outcome (Table A.2: “Number of acquisitions Calculated using the Securities Data Company (SDC) …”, which is licence-gated).

Two further conjectures are flagged and deliberately not asserted, because neither was measured here: that the extended window spans more volatility-regime heterogeneity (2008, 2020), and that Compustat-secd daily returns are noisier than CRSP (untestable — CRSP is not on disk). Neither belongs on a slide as an explanation.

Sources

Gormley, T. A., & Matsa, D. A. (2016). Playing it safe? Managerial preferences, risk, and agency conflicts. Journal of Financial Economics 122(3), 431–455. All GM quotes above are verbatim from the paper’s Sections 3–4 and Appendix Table A.2.
Bertrand, M., & Mullainathan, S. (2003). Enjoying the quiet life? Corporate governance and managerial preferences. Journal of Political Economy 111(5) — the 30-state BC-law dating GM builds on.
Pinnell, C. (2000). State Takeover Laws — the source for GM’s three additional states (Iowa, Oregon, Texas).
Gormley, T. A., & Matsa, D. A. (2014). Common errors: How to (and not to) control for unobserved heterogeneity. Review of Financial Studies 27(2), 617–661 — the AvgE “common error” doctrine behind §14.
Sun, L., & Abraham, S. (2021). Estimating dynamic treatment effects in event studies with heterogeneous treatment effects. Journal of Econometrics — the §12 estimator.
Angrist, J. D., & Pischke, J.-S. Mostly Harmless Econometrics — the bad-controls warning of §14.
Build provenance: the committed scripts code/gm_*.py, gm_did_rcheck.R, gm_phase3_rcheck.R, and the frozen result ledgers outputs/gm-*.md.

Session info

The free spine of this document ran under the versions below; the quoted econometrics ran under pyfixest, cross-checked in R fixest per gm_did_rcheck.R / gm_phase3_rcheck.R.

import sys, platform, pandas, matplotlib
sys.path.insert(0, "code")
import gm_bc_dates as bc

print("Python     :", platform.python_version())
print("pandas     :", pandas.__version__)
print("matplotlib :", matplotlib.__version__)
print("gm_bc_dates:", len(bc.BC_LAWS), "states,",
      len(bc.bm_only()), "in the BM-only subset")
print("econometrics quoted from ledgers; ran under pyfixest, cross-checked in R fixest")

Python     : 3.13.13
pandas     : 2.3.3
matplotlib : 3.10.7
gm_bc_dates: 33 states, 30 in the BM-only subset
econometrics quoted from ledgers; ran under pyfixest, cross-checked in R fixest

--- title: "Building Gormley–Matsa (2016): Playing It Safe?" subtitle: "The Lecture 8 Part 1 corporate-finance DiD, assembled from scratch and checked number by number" format: html: toc: true toc-depth: 2 code-tools: true code-overflow: wrap df-print: kable execute: warning: false message: false eval: false # global default OFF: most chunks read licensed data. # the five free-data chunks flip eval:true locally. freeze: true jupyter: python3 # pipeline is pyfixest/pandas; R cross-checks shown eval:false --- ## How to use this document Lecture 8's Part 1 works through Gormley and Matsa's *Playing It Safe? Managerial Preferences, Risk, and Agency Conflicts* (*Journal of Financial Economics*, 2016): the staggered state adoption of business-combination antitakeover laws, and what insulated managers do with the firm's cash and risk. The slides show results and hide the code; this document does the opposite, rebuilding the whole replication in the order the lecture tells it and printing our reproduced number next to the paper's for every claim. Unlike the Olken replication that sits behind this course's other Lecture 8 companion, this one cannot run end to end on your laptop. Gormley–Matsa rests on Compustat `funda`/`fundq` (and, for the risk legs, `secd`-derived daily returns): licensed instructor data that is gitignored and never redistributable. So the WRDS pulls and every regression that reads the built panel are shown but not executed (`eval: false`), and their outputs are quoted from the pipeline's frozen ledgers in `outputs/`. Exactly one input is free and public — the 33 business-combination-law adoption years, hand-coded from Gormley–Matsa's Appendix Table A.1 — so the treatment indicator, the cohort map, and a small piece of arithmetic *do* run, and the two robustness figures rebuild live from committed result ledgers. Five code chunks in this document execute: the BC-dates spine (§1), the log-points arithmetic (§8), the leave-one-out figure (§13), the standard-error-versus-N figure (§16), and the session-info footer. Everything else is displayed for reading, with its result quoted from a named ledger cell. The [pipeline map](#the-pipeline-at-a-glance) below says which script produces which number, and whether it runs here. Two panel vintages appear throughout, and they are never silently mixed. The **1976–2006 baseline** is Gormley–Matsa's own window; the cash and bad-controls legs are quoted on it so they sit against the paper's own N. The **extended 1976–2026 vintage** re-runs the same scripts with the sample end pushed to today; the volatility legs are quoted on it because that is where they reach the paper's sample size. Every table below carries both, side by side, and names its window. ## The pipeline at a glance {#the-pipeline-at-a-glance} The build is a small directed graph of scripts. Only the first row and the three figure rows touch no licensed data; everything else reads a gitignored Compustat extract and is shown, not run, with its numbers quoted from the ledger it writes. | Script | Reads | Produces | Runs here? | |---|---|---|---| | `code/gm_bc_dates.py` | GM Appendix Table A.1 (printed) | `data/gm_bc_dates.csv` — 33 state→year pairs, treatment rule, cohort map | **yes** (free) | | `pull_compustat_gm.py` | WRDS `comp.funda ⋈ comp.company` | `data/gm_compustat_raw.parquet` (gitignored) | no (`eval:false`) | | `pull_compustat_gm_fundq.py` | WRDS `comp.fundq` | `data/gm_fundq_raw.parquet` (gitignored) | no (`eval:false`) | | `code/gm_did.py` | built panel | `outputs/gm-pipeline-numbers.md` (G1–G9, B1–B3) + `gm_event_study_cash.png` | no (`eval:false`) | | `code/gm_de_robustness.py` | built panel | `outputs/gm-de-robustness.md` (G12, G12b) | no (`eval:false`) | | `code/gm_cashflow_vol.py` | panel + `fundq` | `outputs/gm-cashflow-vol.md` (G5) | no (`eval:false`) | | `code/gm_stock_vol.py` (+ probe) | panel + BCWX/JKP daily | `outputs/gm-stock-vol.md` (G10, G11) | no (`eval:false`) | | `gm_did_rcheck.R`, `gm_phase3_rcheck.R` | built panel | R `fixest` cross-checks | no (`eval:false`) | | `code/gm_fig_adoption_timing.py` | `gm_bc_dates` + one quoted share | `figures/gm_adoption_timing.png` | figure (free) | | `code/gm_fig_leaveoneout.py` | `outputs/gm-de-robustness.md` | `figures/gm_leaveoneout.png` | **yes** (parses ledger) | | `code/gm_fig_se_vs_n.py` | `outputs/gm-cornerstone-findings.md` | `figures/gm_se_vs_n.png` | **yes** (ledger numbers) | The three "runnable" figures do not recompute any regression: two of them rebuild the picture from a frozen result ledger, and the adoption-timing figure draws only the printed dates. Read them as *renders of committed results*, not fresh estimation. ## 1. The one shareable input: BC-law adoption dates Everything downstream keys off a single, entirely public fact: which state adopted a business-combination law in which year. Gormley–Matsa print these in Appendix Table A.1, so they carry no licence. `code/gm_bc_dates.py` transcribes that table into a state→year lookup and a treatment rule, and it is the one piece of this build a student can run. ```{python} #| eval: true #| echo: true import sys, os import pandas as pd sys.path.insert(0, "code") import gm_bc_dates as bc # 33 adopting states, keyed to state of INCORPORATION, sorted by adoption year. dates = ( pd.DataFrame( [(s, bc.STATE_NAMES[s], y, "Pinnell 2000" if s in bc.PINNELL_ADDITIONS else "Bertrand–Mullainathan 2003") for s, y in bc.BC_LAWS.items()], columns=["state", "name", "adopt_year", "source"], ) .sort_values(["adopt_year", "state"]) .reset_index(drop=True) ) dates ``` The roster runs from New York in 1985 to Iowa and Texas in 1997 — 33 states in all. Thirty of them are the Bertrand–Mullainathan (2003) set that adopted between 1985 and 1991; Gormley–Matsa add three more from Pinnell (2000) — Oregon (1991), Iowa and Texas (both 1997). The absorbing treatment dummy switches on in a firm's adoption year and stays on, and firms incorporated in a never-adopting state (Florida, California) are never treated: ```{python} #| eval: true #| echo: true checks = { "DE treated in 1987 (before its 1988 law)": bc.is_treated("DE", 1987), "DE treated in 1988 (adoption year)": bc.is_treated("DE", 1988), "FL treated in 2000 (never adopts)": bc.is_treated("FL", 2000), "states in the full set": len(bc.BC_LAWS), "states in the BM-only 30-state subset": len(bc.bm_only()), } checks ``` The `bm_only()` subset drops the three Pinnell additions to recover the core 30-state Bertrand–Mullainathan design the literature standardised on — a robustness leg we return to in §7. The treatment is assigned on the firm's **state of incorporation**, which is the whole design and the subject of the next section. In the paper's own words on what the laws reach: > These state laws applied only to target firms incorporated in the state. and, from footnote 1, > the BC laws make only hostile takeovers of target firms incorporated in that state more > difficult. Friendly mergers are unaffected by the law, as are hostile takeovers of firms > incorporated elsewhere, even when the acquirer is incorporated in the affected state. The timing is easiest to read as a strip. Delaware — the dot to watch, because it carries **53.4% of firm-year observations** in the baseline panel (`gm-pipeline-numbers.md` §G1) — adopts in 1988. The figure below is drawn by `gm_fig_adoption_timing.py`, which needs only the dates above plus that one quoted share; it is committed and regenerable, shown here as a static image. ![Adoption timing: 33 states, 1985–1997, keyed to state of incorporation. Delaware (1988) is the dominant cohort at 53.4% of baseline firm-year observations.](outputs/figures/gm_adoption_timing.png){fig-align="center" width="70%"} ## 2. Incorporation versus location: where identification comes from Treatment follows the state a firm is *incorporated* in, not the state where it operates — and those come apart. More than 60% of firms incorporate and locate in different states, and that gap is the entire identification argument. Because incorporation and location are distinct, the regression can absorb everything that hits a *location* in a given year (local business cycles) and everything that hits an *industry* in a given year, and still have treatment variation left to read. In the authors' words: > Using a difference-in-differences estimator, we compare changes among firms located in > states that pass a BC law with changes among firms incorporated elsewhere. The underlying > identification assumption is that, but for the law, the two sets of firms would follow > parallel trends; that is, the change in outcome $y$ for firms incorporated in the states > that pass a BC law would have been the same as for firms incorporated in states that did > not pass a BC law. and the sentence that licenses the state-by-year fixed effects: > We are able to obtain estimates for the BC laws' effects even after including > state-by-year fixed effects because more than 60% of our firms are incorporated and > located in different states. Our estimates are identified by comparing the differential > response of two firms that operate in the same state, $l$, but when only one of these > firms is incorporated in a state, $s$, that passes a BC law. Thus, any unobserved, > time-varying state-level factors, such as local business cycles, that could coincide with > a BC law's adoption and affect our outcomes of interest do not bias our findings. ::: {.callout-note title="The 2×2, and why location does not confound it"} Two firms in the same building in Palo Alto, selling to the same customers, in the same industry: | Firm | Incorporated in | Operates in | Treated from | |---|---|---|---| | A | Delaware | California | 1988, when Delaware adopts | | B | California | California | never — California does not adopt | A California-by-year shock hits both identically and is swept out by the location-by-year fixed effect. What remains is that one of them was treated in 1988 because of a filing cabinet in Wilmington. That is the variation the design uses. ::: The >60% figure is Gormley–Matsa's own (`gm-cornerstone-expectations.md`, "What we reproduce"); we do not recompute it here, because doing so needs the Compustat header that carries incorporation and location state. ## 3. Recall the week-6 machinery Nothing in the estimand is new this week. The target is the average treatment effect on the treated, $$ \text{ATT} = E\!\left[\,Y_{it}(1) - Y_{it}(0)\;\middle|\;W_{it}=1\,\right], $$ with $Y_{it}(1)$ and $Y_{it}(0)$ the two potential outcomes for firm $i$ in year $t$ and $W_{it}$ the treatment indicator. It is identified under the four week-6 assumptions — consistency, no anticipation, no interference, and parallel trends — the last of which Gormley–Matsa state exactly as the "but for the law … the two sets of firms would follow parallel trends" sentence quoted above. The one genuinely new object is that $W_{it}$ switches on at a *different date for different firms*: **staggered** adoption. A single before-after 2×2 becomes a stack of them, one per adoption cohort, and that stack is where the staggered-DiD problems of §12 come from. Everything from §4 onward is week-6 machinery run on real data. ## 4. Assembling the panel from Compustat The panel is a WRDS pull followed by a handful of sample screens. The pull joins `comp.funda` to the `comp.company` header for the incorporation and location states, and — crucially — applies **no common-stock or size screen**. That absence is deliberate: it is the whole reason this cornerstone reproduces where a CRSP-screened one attenuates (§18 returns to that contrast). The complete, runnable pull is `pull_compustat_gm.py`; its core query, shown but not executed here: ```{python} #| eval: false #| echo: true # pull_compustat_gm.py — WRDS Compustat annual pull (INSTRUCTOR-DATA, gitignored). # No CRSP, no common-stock screen. Treatment/cluster key is c.incorp; the # location-by-year FE uses c.state (HQ). Runnable with WRDS access: # (the pull script lives in the private working repo; not shipped here) import wrds conn = wrds.Connection(wrds_username=os.environ["WRDS_USER"]) df = conn.raw_sql(""" select f.gvkey, f.fyear, f.datadate, f.sich, f.at, f.sale, f.ni, f.ch, f.che, f.dltt, f.dlc, f.lt, f.re, f.wcap, f.oiadp, f.csho, f.prcc_f, f.dvc, f.prstkc, f.act, f.lct, f.dp, c.incorp as inc_state, -- TREATMENT: state of incorporation c.state as hq_state, -- location, for the location-by-year FE c.loc as hq_loc, c.sic as header_sic from comp.funda f left join comp.company c on f.gvkey = c.gvkey where f.indfmt='INDL' and f.datafmt='STD' and f.popsrc='D' and f.consol='C' and f.fyear between 1974 and 2026 and f.at is not null and f.at > 0 """) ``` The screens Gormley–Matsa describe are applied downstream in `gm_did.py`, so the drop counts stay visible. In the paper's own statement of them: > We obtain firms' financial data from Compustat, excluding regulated utility firms (SIC > codes 4900–4999), firms located or incorporated outside the US, and firm-year observations > with either missing or negative assets or sales. Financial ratios are winsorized at the 1% > level. To include at least ten years of data before and after each law's adoption, our > sample period is 1976–2006. and, on the endogeneity of incorporation itself: > To avoid endogenous changes in whether a firm is subject to a BC law, we exclude firms > that reincorporate from a state without a BC law to a state with a BC law or vice versa. Our build uses the *current* Compustat incorporation header rather than Gormley–Matsa's historical (Cohen 2012) coding. Their footnote 6 settles that this is immaterial: > Relative to the most recent version of Compustat, our historical data change the state of > incorporation for about 6% of observations and change treatment status for only 2% of > observations. so the current-header build is Gormley–Matsa's own stated robustness variant. The build code, shown but not executed: ```{python} #| eval: false #| echo: true # gm_did.py — build_panel(): screens, outcomes, treatment (INSTRUCTOR-DATA). df = df[df["hq_loc"] == "USA"] df = df[df["inc_state"].isin(US_STATES) & df["hq_state"].isin(US_STATES)] df["sic4"] = pd.to_numeric(df["sich"].fillna(df["header_sic"]), errors="coerce") df = df[~df["sic4"].between(4900, 4999)] # utilities only (GM keeps financials) df = df[(df["at"] > 0) & (df["sale"] > 0)] df["ln_cash"] = np.log(df["ch"].where(df["ch"] > 0)) # ln(ch); ch>0 only df["cash_at"] = df["che"] / df["at"] for c in ["cash_at", "ch_at", "roa", "debt_at", "payout_at"]: df[c] = winsorize(df[c], 0.01, 0.99) # ratios winsorized 1/99 df["bc"] = [is_treated(s, int(y)) for s, y in zip(df["inc_state"], df["fyear"])] df["bc_cohort"] = df["inc_state"].map(adoption_year) # cohort = adoption year ``` The resulting sample is quoted below on both vintages (`gm-pipeline-numbers.md` §G1 and `gm-pipeline-numbers-2026.md` §G1). A student who checks GM's location assignment will find it is the headquarters — "We assign a firm's location based on the location of its headquarters, which is typically also where major plants and operations are located." | | 1976–2006 baseline | Extended to 2026 | |---|---|---| | Ln(cash) firm-years | **174,627** (GM 172,739; within 1.1%) | 262,641 | | Unique firms | 17,837 | 22,266 | | Treated incorporation-states | 33 | 33 | | Never-treated firm-years | 18,639 | 24,522 | | Delaware share of observations | 53.4% | 55.8% | The extension adds only post-treatment and never-treated mass — every adoption is 1985–1997 — so it introduces no new staggered-timing comparisons, only more data of the kinds already present. ## 5. From the 2×2 to the regression we run The design maps onto two specifications, worth seeing side by side because the contrast between them *is* the identification lesson. The teaching baseline is the week-4/week-5 two-way fixed-effects model, $$ Y_{it} = \alpha_i + \lambda_t + \delta\,W_{it} + u_{it}, $$ firm and year fixed effects with one treatment dummy. Gormley–Matsa's own specification replaces the year effect with location-state-by-year and four-digit-industry-by-year effects (their Eq. 4): $$ y_{ijlst} = \beta_1\,BC_{st} + f_i + \omega_{lt} + \lambda_{jt} + \eta_{ijlst}, $$ which the authors read out as: > $f_i$ are firm fixed effects; $\omega_{lt}$ are state-by-year fixed effects; and > $\lambda_{jt}$ are four-digit SIC industry-by-year fixed effects. … Finally, we adjust the > standard errors for clustering at the state-of-incorporation level. The extra structure is exactly what the incorporation-versus-location gap pays for, and it is what makes the heavy-FE estimate defensible: > The inclusion of state-by-year and industry-by-year fixed effects ensures that our > difference-in-differences estimates are robust to many types of unobservable omitted > variables that could otherwise confound our analysis. Two choices carry the weeks-1-through-5 material into this design. First, the standard errors cluster on **state of incorporation** — the level treatment is assigned at, the clustering lesson from `lecture4.qmd` used in anger, and the number that comes back to bite us in §16. Second, there are **no firm controls** in the headline: no size, no leverage, no profitability on the right-hand side. That is deliberate, and §14 is its defence. In `pyfixest`, the headline is one line: ```{python} #| eval: false #| echo: true # gm_did.py:143 — paper FE spec, clustered on incorporation state (INSTRUCTOR-DATA). import pyfixest as pf FE_PAPER = "gvkey + hq_state^fyear + sic4^fyear" # firm + loc-state×year + sic4×year m = pf.feols("ln_cash ~ bc | " + FE_PAPER, data=d_cash, vcov={"CRV1": "inc_state"}) ``` ## 6. Threats, named before results Four ways this could be wrong, named before a single estimate appears — a commitment device that stops the diagnostics from being chosen after the fact to flatter the result. Three of the four are omitted-variable stories in the weeks-1-2 sense: something left out that correlates with both treatment and cash. The fourth is the mirror image, and the one students most often get wrong: a variable wrongly *put in*, one the treatment itself moves. | # | Threat | The story | Answered in | |---|---|---|---| | i | Pre-existing drift | cash was already trending up in treated states before adoption | §10 (event study), §11 (placebo) | | ii | Staggered contamination | already-treated firms used as controls for later cohorts (Goodman-Bacon) | §12 (Sun–Abraham) | | iii | A dominant cohort | Delaware alone is 53% of the file and adopts in 1988 | §13 (drop DE, leave one out) | | iv | Bad controls | conditioning on size/leverage/ROA, which the law itself moves | §14 | Gormley–Matsa's own defence against threat (i)/(iii)-style legislative endogeneity leans on the political economy of the laws: > Romano (1987) and Bertrand and Mullainathan (2003) find that the passage of these laws > typically did not result from the pressure of a large coalition of economic players in the > state and conclude that an omitted economic variable is unlikely to explain measured > effects of the law. and on a five-part run of evidence they summarise as: > First, we find no measureable differences in the ex ante characteristics of firms > incorporated in states adopting the laws. Second, no preexisting trends exist … before the > laws come into effect. … All five of these results suggest that our findings are not > explained by legislative endogeneity. Each threat gets its own section, in the order above, and each answer is reported whether or not it is comfortable. ## 7. The headline: what the paper found, and what the rebuild found Same law, same window, an independently assembled Compustat extract. The sample lands within 1.1% of the paper's, the coefficient at 89% of theirs, and — the detail worth dwelling on — estimated *more precisely than the paper's own* (t 2.89 against 2.47). Numbers from `gm-pipeline-numbers.md` §G1/§G2/§G3/§G8 and `gm-cornerstone-findings.md`, headline verdict; extended column from `gm-pipeline-numbers-2026.md`. | | GM (2016), Table 2 | Rebuild, 1976–2006 | Rebuild, extended 2026 | |---|---|---|---| | Ln(cash), N | 172,739 | **174,627** (within 1.1%) | 262,641 | | **Ln(cash)** | **+0.121 (t 2.47)** | **+0.1081** (SE 0.0374, t **2.89**, p .006) | +0.1057 (SE 0.0408, t 2.59, p .013) | | Cash ratio, che/at | +0.0023, ns | −0.0024 (SE 0.0027, t −0.90) | −0.0018 (t −0.68) | | BM-only 30-state | ≈ +0.121 | **+0.1225** (t 2.77) | +0.1194 (t 2.44) | | Alternative timing (first full year) | — | +0.0624 (t 1.68) | +0.0614 (t 1.52) | The closest apples-to-apples row is the last-but-one: dropping the three Pinnell late-adopters (Iowa, Oregon, Texas) to recover Gormley–Matsa's core 30-state Bertrand–Mullainathan design gives **+0.1225 (t 2.77)**, a whisker from the paper's +0.121. A replication that lands within one percent on sample size has the same firms in it, which is what licenses reading the coefficient comparison at all. The estimate is identical in R. `gm_did_rcheck.R` re-runs the same built panel through `fixest::feols` and reproduces `pyfixest` to the reported precision: ::: {.panel-tabset} ## Python (`pyfixest`) ```{python} #| eval: false #| echo: true m = pf.feols("ln_cash ~ bc | gvkey + hq_state^fyear + sic4^fyear", data=d_cash, vcov={"CRV1": "inc_state"}) # -> bc = +0.1081, t 2.89, N 174,627 (gm-pipeline-numbers.md §G2) ``` ## R (`fixest`) ```r # gm_did_rcheck.R — reads the identical built panel Python used. library(fixest); library(arrow) d <- as.data.frame(read_parquet("data/gm_panel_built.parquet")) d <- d[!is.na(d$ln_cash), ] m_paper <- feols(ln_cash ~ bc | gvkey + hq_state^fyear + sic4^fyear, data = d, cluster = ~inc_state) # -> beta +0.1081, t 2.89, N 174,627 (matches pyfixest exactly) ``` ::: One sentence on *why this paper*: Gormley–Matsa's cash sample is Compustat-native with no common-stock screen, so it structurally escapes the CRSP-screen attenuation that hit the runner-up cornerstone (Serfling 2016) on the same install (`gm-cornerstone-findings.md`, Serfling comparison) — the reason it was chosen over an otherwise-similar staggered-law design. ## 8. Reading the coefficient The headline is on log cash, so exponentiating turns it into a percentage. This is pure arithmetic on printed coefficients — no data — so it runs: ```{python} #| eval: true #| echo: true import numpy as np import pandas as pd pd.DataFrame({ "source": ["Rebuild (1976–2006)", "GM (2016) printed"], "beta_ln_cash": [0.1081, 0.121], "pct_change": [np.exp(0.1081) - 1, np.exp(0.121) - 1], }).assign(pct_change=lambda d: (d["pct_change"] * 100).round(1)) ``` So $\exp(0.1081)-1 \approx 11.4\%$ more cash, against Gormley–Matsa's own 12.1 log points, "or about 13%." Insulated managers hold more cash — precautionary hoarding, or a quiet life; this lecture does not adjudicate between those stories and should not pretend to. The caveat arrives immediately, in the next section: the cash *ratio* does not move. ## 9. Log-level versus ratio: the same data, two answers Cash grew. So did assets. Which normalisation gets used is a modelling choice with a real answer attached, not a formatting detail — and here the two choices disagree. Numbers from `gm-pipeline-numbers.md` §G3 (extended column §G3 of the 2026 file). | Outcome | Rebuild, 1976–2006 | Rebuild, extended 2026 | GM (2016), printed | |---|---|---|---| | **Ln(cash)** | **+0.1081** (t 2.89), N 174,627 | +0.1057 (t 2.59) | +0.121 (t 2.47) | | Cash ratio che/at | −0.0024 (SE 0.0027, t −0.90), N 193,261 | −0.0018 (t −0.68), N 283,331 | +0.0023 (SE 0.0034), ns | | Cash ratio ch/at | +0.0013 (t 0.51) | +0.0015 (t 0.54) | — | The disagreement is not a replication failure: Gormley–Matsa's own printed ratio result is null too. In their words, > Average total cash holdings increase by 12.1 log points, or about 13%, after a BC law is > adopted (Column 5), but the increase in the ratio of cash to book assets is smaller and not > significant (coefficient = 0.0023, standard error = 0.0034). So both builds say the same thing — the *level* of cash moves and the *share* of the balance sheet held as cash does not — which means assets grew roughly in step with cash. Whether that is the interesting fact or a nuisance depends entirely on the question. A student who reports only the specification that moved has not made a coding error; they have made a write-up error. ::: {.callout-note title="Why the sample sizes differ"} The three cash rows run on different N: Ln(cash) needs `ch > 0` (193,261 firm-years have a defined cash ratio, but only 174,627 have positive cash to log), and the ratio uses the full defined sample. This is the same reason the §11 placebo (56,006) and the headline (174,627) differ — different rows are eligible for different questions. Naming the estimation sample is part of naming the estimate. ::: ## 10. Pre-trends: the event study GM never drew Gormley–Matsa plot acquisitions, not cash — their Figure 2 is the acquisition event study, and nobody draws the cash pre-trend. So we did. The figure below (from `gm_did.py`, static; its source needs the licensed panel and is not regenerated here) puts the reference year at $k=-1$ and reads the leads. Numbers from `gm-pipeline-numbers.md` §G6/§G7. ![Ln(cash) event study, reference year k = −1, firm + location-state×year + industry×year fixed effects, SEs clustered on state of incorporation. 1976–2006 baseline panel, N 174,627.](outputs/figures/gm_event_study_cash.png){fig-align="center" width="72%"} The leads all clear the bar — $t$ of $\{-5:-1.64,\ -4:-1.45,\ -3:-1.00,\ -2:-1.26\}$, every $|t|<1.65$ — which is the parallel-trends evidence the paper never shows for cash. But the honest beat is that every lead sits *mildly negative*, and $k=-5$ is a whisker from the line at $-1.64$: a faint hint of an upward cash drift into adoption. Not a violation; the "is this pre-trend real?" moment. After adoption the effect is immediate and sustained — $k=0$ at **+0.0696 (t 3.2)**, holding to $k=5$ at **+0.1002** — but it dips at $k=2$ (+0.0225) rather than phasing in monotonically. ::: {.callout-warning title="Logged honestly as CHECK, not PASS"} The dynamics are an immediate, persistent, growing increase, but *not* a strict monotone phase-in. The pipeline records G7 as **CHECK**, and this document does not launder it to PASS. Gormley–Matsa's own timing claim is the qualitative one this supports: "the law's adoption precedes the effects we assign to it instead of the other way around." ::: ## 11. The placebo, reported honestly Move every adoption three years earlier and estimate on the pre-period alone. Nothing happened in those years, so the coefficient should be zero. It is insignificant — **+0.0591 (t 1.68), N 56,006** (`gm-pipeline-numbers.md` §G9; extended: +0.0603, t 1.65, N 61,889) — but it leans positive, in exactly the direction the mild leads of §10 hinted at. A placebo that "passes" at 1.96 and a pre-trend that "passes" at 1.65 can be telling you the same soft thing. "The placebo is insignificant" is a true sentence and an incomplete one; the reader is owed the coefficient, the $t$, and the direction it leans. This is the same report-don't-launder discipline the pre-testing literature (week 6) asks for. ## 12. Staggered timing is not one experiment With 33 treated cohorts and a thin never-treated group, the static two-way fixed-effects coefficient is exposed to the Goodman-Bacon problem: some of its identifying 2×2s use already-treated firms as controls for later-adopting ones, a comparison nobody intended. The structure is visible from the shares alone (`gm-pipeline-numbers.md` §B1): **33 treated incorporation-states versus 18 never-treated**; treated-state firm-years **89%** against **11%** never-treated; and Delaware alone is **53% of observations, adopting in 1988**, so the DE-1988 cohort's 2×2s carry heavy weight while the clean control group is small. Exact Goodman-Bacon weights need a balanced panel, so this is kept qualitative; the quantitative answer is the heterogeneity-robust estimator, whose natural tool here is Sun–Abraham (`fixest::sunab`). ::: {.panel-tabset} ## R (`fixest::sunab`) ```r # gm_did_rcheck.R — Sun-Abraham event study, never-treated as control. d$cohort <- ifelse(is.na(d$bc_cohort), 10000, d$bc_cohort) m_sa <- feols(ln_cash ~ sunab(cohort, fyear) | gvkey + fyear, data = d, cluster = ~inc_state) aggregate(m_sa, agg = "att") # -> ATT +0.169 (SE 0.0507, t 3.33, p .0016); path k0..k5 +0.093 → +0.088 ``` ## Python (hand-rolled) ```{python} #| eval: false #| echo: true # gm_did.py — cohort × relative-time saturated design, never-treated control. # Overall post ATT (cohort-share weighted) = +0.1012 # path k0..k5: +0.0999, +0.0820, +0.0674, +0.0883, +0.1326, +0.1369 ``` ::: Both implementations survive: the aggregate ATT is positive and significant, and the event-time path is positive and roughly flat under each (`gm-pipeline-numbers.md` §B2, R cross-check). The two aggregates differ — Python's **+0.1012** against R's **+0.169 (t 3.33, p .0016)** — because of aggregation weighting and endpoint binning, not because one is wrong. ::: {.callout-important title="Report the sign and the path, never one SA number"} A heterogeneity-robust estimate is a *family* of estimates; quoting one of them to three decimal places as "the answer" overstates what the method delivers. The teachable fact is that the sign and the path survive the correction — the static coefficient was not an artefact of forbidden comparisons. ::: This is the one diagnostic with no Gormley–Matsa quote: the paper predates the staggered-DiD critique, so the estimator is attributed to Sun & Abraham (2021) and this companion, not to the original. ## 13. Kill the dominant cohort: drop Delaware, then leave one state out Delaware is 53% of the sample and adopts in 1988, so the single most direct robustness check is to remove it entirely and see if the result dies. It does not (`gm-de-robustness.md` §G12): dropping Delaware takes N from 174,627 to **81,345** and gives paper-FE Ln(cash) **+0.1429 (SE 0.0667, t 2.14, p .037)** — positive, still significant, and in fact *larger* than the full-panel +0.1081, because the heavy fixed-effect structure no longer competes with the dominant cohort for the same variation (the firm+year baseline on the DE-excluded sample is +0.1470, t 2.94). This matches Gormley–Matsa's own §6.4, and their summary of the whole robustness family: > Finally, our findings are robust to alternative samples, time periods, and empirical > specifications, including excluding firms incorporated in Delaware (50% of observations) or > any of the 32 other states that adopted a BC law. That last clause — *any of the 32 other states* — is the leave-one-out sweep, which the pipeline runs and which this document rebuilds live. `gm_fig_leaveoneout.py` parses the 33-row table straight out of the committed ledger (it asserts exactly 33 rows, so a drifted ledger fails loudly) and plots the firm+year-FE coefficient with each treated state dropped in turn: ```{python} #| eval: true #| echo: true import contextlib, io sys.path.insert(0, "code") import gm_fig_leaveoneout with contextlib.redirect_stdout(io.StringIO()): gm_fig_leaveoneout.main() # rebuilds the figure from outputs/gm-de-robustness.md from IPython.display import Image Image("outputs/figures/gm_leaveoneout.png") ``` Across all 33 states the coefficient stays in **[+0.1394, +0.1678]** and never changes sign — minimum when Minnesota is dropped (+0.1394, t 3.94), maximum when New York is dropped (+0.1678, t 4.56), against a full-panel firm+year baseline of +0.1472 (`gm-de-robustness.md` §G12b). The punchline is a sentence students can reuse in any staggered design: identification does not rest on any single treated unit, and if it does, that is a finding about the paper, not about the world. ## 14. Bad controls versus AvgE: two ways to break a clean estimate The absence of firm controls in the headline (§5) was deliberate, and this is its defence. Size, leverage and profitability are all things a business-combination law can move, so conditioning on them shuts down part of the very channel being measured. Gormley–Matsa's literal demonstration of this (their Table 7) is on the number of acquisitions — an SDC-gated outcome we cannot build — so the lesson is run here on Ln(cash) instead, where *both* directions of bias show up on a single outcome (`gm-pipeline-numbers.md` §B3, extended §B3). | Specification | 1976–2006 | Extended 2026 | |---|---|---| | Proper FE, no controls | **+0.1081** (t 2.89, N 174,627) | +0.1057 (t 2.59) | | + endogenous "bad controls" (log assets, leverage, ROA) | **+0.0795** (t 3.18, N 174,624) | +0.0698 (t 2.60) | | AvgE "common error" (group-mean DV in place of FE) | **+0.1942** (t 6.68, N 174,627) | +0.2357 (t 9.56) | Post-treatment mediators attenuate the estimate by about 26%; the "AvgE" substitution documented in Gormley & Matsa's (2014) *Common Errors* — replacing the fixed effects with a group average of the dependent variable, which looks like a control and is not — inflates it by about 80%. Bias runs in both directions from one clean estimate. ::: {.callout-important title="The detail that lands hardest"} Read the $t$ column top to bottom: 2.89, then 3.18, then 6.68. Both mistakes make the result look *better* — tighter, more publishable. A rising t-statistic is not evidence that a specification improved. The exam-shaped rule: a control that the treatment itself moves is not a control; it is part of the effect being measured (Angrist–Pischke on bad controls; Gormley & Matsa 2014). ::: ## 15. Did they actually get safer? Three risk measures Gormley–Matsa's substantive claim is that insulated managers take less risk. Three measures test it, and they return three different verdicts. Two of the three are built from Compustat-`secd`-derived daily returns with **no CRSP anywhere in the pipeline** — the deliberate stress test, since Gormley–Matsa build their volatility from CRSP. Quoting GM's own "from CRSP" beside our no-CRSP build is what makes the stress explicit. Both vintages, from `gm-cashflow-vol{,-2026}.md` and `gm-stock-vol{,-2026}.md`: | Measure | Rebuild, baseline | Rebuild, extended 2026 | GM (2016) | Verdict | |---|---|---|---|---| | Cash-flow volatility | −0.0015 (t −0.92), N 102,153 | −0.0024 (t −1.05), N 159,268 | −0.0028, ns | null reproduced — **PASS** | | Stock volatility | −0.0172 (t −2.26), N 81,936 | **−0.0232** (SE 0.0081, t **−2.88**, p .006), N 132,446 | −0.023 (SE 0.008), N 132,494 | holds — **PASS** | | Operating-asset volatility | −0.0131 (t −1.69), N 75,919 | **−0.0152** (SE 0.0090, t **−1.69**, p .097), N 125,131 | −0.015 (SE 0.006), N 120,401 | directional only — **CHECK** | Reproducing a *null* is a pass, and students rarely believe that until it is said. Cash-flow volatility comes in at −0.0015 (t −0.92) against Gormley–Matsa's own −0.0028, ns; more data on the extended panel keeps it null. Stock volatility is the stress test and it passes: −0.0232 (t −2.88) on the extended daily panel, essentially on GM's N and magnitude. Operating-asset volatility lands right on GM's −0.015 but stops just short of the bar at t −1.69 — recorded as **CHECK**, not laundered to PASS. The three constructions, in Gormley–Matsa's own words and our faithful code. Stock volatility: > we calculate a firm's stock volatility using the square root of the sum of squared daily > stock returns over the year. and Table A.2: "Calculated from Center for Research in Security Prices (CRSP) … the raw sum is multiplied by 252 and divided by the number of trading days." Our leg does exactly this, from `secd`-derived daily returns rather than CRSP: ```{python} #| eval: false #| echo: true # gm_stock_vol.py — GM's raw (non-demeaned) sum-of-squares, annualized inside the root. m["r2"] = m["ret"] ** 2 g = m.groupby(["gvkey", "fyear"]).agg(n_days=("ret", "size"), ssr=("r2", "sum")) g["stockvol"] = np.sqrt(252 / g["n_days"] * g["ssr"]) # NOT a demeaned SD × √252 ``` Operating-asset volatility unlevers that: > we approximate the volatility of a firm's returns on operating assets using the product of a > firm's stock volatility and its market value ratio of equity to operating assets. This > approximation holds exactly if both debt and cash are risk-free. with Table A.2's formula `Stock volatility × [E/(V−C)]`, `E/(V−C) = (csho × prcc_f) / [lt + (csho × prcc_f) − ch]`. Cash-flow volatility is "the annual standard deviation of a firm's quarterly ratio of cash flow to assets," from a quarterly `fundq` pull: ```{python} #| eval: false #| echo: true # gm_cashflow_vol.py — quarterly Sloan-accruals CF/assets, within-year SD. accruals_q = q["d_actq"] - q["d_cheq"] - q["d_lctq"] + q["d_dlcq"] - q["dpq"] q["cf_at"] = (q["oiadpq"] - accruals_q) / q["atq_lag"] cfvol = q.groupby(["gvkey", "fyearq"])["cf_at"].std() # SD across the year's 4 quarters ``` ::: {.callout-warning title="Two caveats that govern how this table is read"} **The quarterly item mapping is our inference.** Gormley–Matsa print the *annual* Sloan-accruals formula and the verbal "quarterly ratio," but no quarterly item mapping (`gm-cornerstone-expectations.md`, Phase-3 build note). The specific quarterly items above are ours, not GM-verbatim. **Our volatility levels run 18–26% below GM's, so read percent-of-mean, not absolute agreement.** On the extended panel the stock-vol mean is 0.500 against GM's Table A.3 value of 0.611 (~18% below), operating-asset 0.296 against 0.400 (~26% below), cash-flow vol 0.0645 against 0.084 (`gm-stock-vol-2026.md`, sample block). So our −0.0232 is 4.6% of our own mean against GM's −0.023/0.539 = 4.3% of pre-law — matching, if anything slightly larger, proportionally. An earlier "proportional down-scaling" reading was **RETRACTED** in Phase 3.5 (the level gap *widened* while the coefficient rose to GM's), and this document does not revive it. ::: Why operating-asset volatility is the leg that matters and the softer one: it is Gormley–Matsa's tool for isolating *business* risk from the mechanical financial-risk channel folded into equity volatility — and §7's cash result confirms that channel is active (firms raise cash, which mechanically lowers equity volatility even with unchanged business risk). So stock volatility's significance does not by itself confirm the business-risk story; G11 is the construct-specific test, and it is under the bar. A probe (`gm_stockvol_opsample_probe.py`) shows *why*: the 6,017 firm-years dropped for undefined E/(V−C) carry a disproportionate −0.0403 (t −3.06) stock-vol effect under firm+year FE, so the sub-2 $t$ is sample composition on the truncated 1984–2006 daily span, not a construction failure. ## 16. Why more data didn't help: standard errors versus N The obvious diagnosis of the operating-asset leg's soft $t$ is power, so the panel was extended to 2026, reaching essentially GM's own sample size (125,131 against GM's 120,401) and landing on GM's own −0.015. The $t$ stayed **−1.69**. That is the segment's sharpest inference lesson, and it is worth teaching rather than burying (`gm-cornerstone-findings.md`, Phase 3.5). The reason is the clustering choice from §5. Standard errors cluster on state of incorporation — roughly **51 clusters**, a count fixed by law-adoption geography that added *years* do not grow. More within-cluster observations do not shrink a clustered SE the way iid N would. The figure below (`gm_fig_se_vs_n.py`, hard-coding the Phase-3.5 SEs from the findings ledger) compares the SE an iid model predicts at the extended N against the actual clustered SE: ```{python} #| eval: true #| echo: true import contextlib, io sys.path.insert(0, "code") import gm_fig_se_vs_n with contextlib.redirect_stdout(io.StringIO()): gm_fig_se_vs_n.main() # numbers from gm-cornerstone-findings.md, Phase 3.5 from IPython.display import Image Image("outputs/figures/gm_se_vs_n.png") ``` For operating-asset volatility the SE *rose* from 0.0078 to 0.0090 on +65% N; an iid model predicts ≈0.0061 at the extended N, so the actual clustered SE is **+48% above iid**. Stock volatility shows the same pattern (predicted ≈0.0060, actual 0.0081, **+35% above iid**), but its larger effect clears the bar anyway. The lesson for students: **more observations do not buy precision when the thing you cluster on is fixed.** This is an inference-precision limit, not small-N, and it ties straight back to §5's clustering decision. ## 17. The card we wrote before we ran anything Every expectation in the scorecard below was frozen *before the first line of estimation code ran* (`gm-cornerstone-expectations.md`); the verdicts were filled in afterwards. The previous sections are this card being scored. Two rows are verdicts on the replication process itself, not on the paper — and they are kept red, not laundered. | Leg | Written before the code | Found | Verdict | |---|---|---|---| | Ln(cash) headline | ≈ +0.121, t ≥ 2 | +0.108, t 2.89 | PASS | | Cash ratio che/at | ≈ +0.0023, ns | −0.0024, t −0.90 | PASS (null) | | Event-study leads | flat, all \|t\| < 1.65 | −1.64, −1.45, −1.00, −1.26 | PASS | | Dynamic phase-in | rises and stabilises | immediate + persistent, dip at k2 | **CHECK** | | Placebo, three years early | insignificant | +0.0591, t 1.68 | PASS (borderline) | | Sun–Abraham ATT | sign preserved | +0.101 Python / +0.169 R, both sig. | PASS | | Delaware excluded | positive, ideally significant | +0.1429, t 2.14 | PASS | | Cash-flow volatility | ≈ −0.0028, ns | −0.0015, t −0.92 | PASS (null) | | Stock volatility | ≈ −0.023, t ≤ −2 | −0.0232, t −2.88 | PASS | | Operating-asset volatility | ≈ −0.015, t ≤ −2 | −0.0152, t −1.69 | **CHECK** | | *Phase-3 reading:* vol coefficients scale down with the lower vol levels | (written after Phase 3, not before) | level gap widened while the coefficient rose to GM's | **RETRACTED** | | *Conjecture:* the soft leg just needs more N | iid scaling put t ≈ −2.1 at GM's N | N reached, t stayed −1.69, SE 48% above iid | **REFUTED** | The reason the green rows mean anything is that the middle column was frozen before any code ran: a PASS you could not have failed is not a pass. The two red rows are the honest part — a reading withdrawn (§15's level caveat) and a conjecture the data refuted (§16's clustering finding). Card: `gm-cornerstone-expectations.md`; the two red rows: `gm-cornerstone-findings.md`, Phase 3.5. ## 18. What to believe, and how much The deliverable of the whole segment is not any single coefficient; it is an ordering of the claims by how much weight each carries. 1. **Insulated managers hold more cash — solid.** The headline (+0.108, t 2.89) survived four attempted breakages: the event study, the placebo, the Sun–Abraham re-estimation, and the drop-Delaware-plus-leave-one-out sweep. Nothing moved the sign, and little moved the magnitude. 2. **Equity risk falls — reproduces.** Stock volatility declines at t −2.88 on a daily panel assembled from Compustat with no CRSP — the harder road, and the one students can imagine walking. 3. **Business risk falls — directional only.** Operating-asset volatility lands on GM's magnitude but at t −1.69, and §16 explained why more data will not fix it. This is the honest weak point of the risk story. 4. **Cash-flow volatility is unchanged — a null, and GM's own.** Reported as a result because reproducing the paper's null *is* the result. Then the hand-off to Part 2: today the danger was a variable wrongly included or wrongly omitted in a *causal* design. Next it is the same disease in an *asset-pricing* model — where what gets left out of the specification prices what stays in. ## 19. Skeptic's appendix Four objections a careful reader would raise, each already measured, plus two things genuinely out of reach. 1. **Parallel trends holds by the bar, not pristinely.** The event-study leads are all mildly negative and $k=-5$ sits at t −1.64; the three-years-early placebo is +0.0591 (t 1.68). Both clear their thresholds and both lean the same soft way (`gm-cornerstone-findings.md`, caveat 2). Reported, not hidden. 2. **Delaware dominance.** 53% of observations on the baseline panel, 55.8% extended, adopting in 1988, with the never-treated share only 11% (9% extended). Answered by §13's drop-DE and leave-one-out sweeps, but the caveat stays live. 3. **Our volatility levels run below GM's.** Stock-vol mean 0.500 against 0.611, op-asset 0.296 against 0.400, cash-flow vol 0.0645 against 0.084 — so the numbers in §15 are read percent-of-mean, where −0.0232 is 4.6% of our mean against GM's 4.3% of pre-law (`gm-stock-vol-2026.md`, sample block). The "proportional down-scaling" reading was retracted. 4. **Incorporation is the current Compustat header**, not Cohen (2012) historical coding. Gormley–Matsa footnote 6 settles it: historical coding changes treatment status for about 2% of observations, conclusions unchanged, so this build is their stated robustness variant. Genuinely out of reach, and worth one honest sentence each if asked: **performance-related exit** (Gormley–Matsa build it from CRSP delisting codes 400–500, 550, 552, 560, 561, 572, 574, 580, 584 — "we use CRSP delisting codes to construct an indicator variable that equals one when firms exit our sample because of bankruptcy, liquidation, or other performance-related reasons" — which we do not have), and the **literal Table-7 acquisitions outcome** (Table A.2: "Number of acquisitions Calculated using the Securities Data Company (SDC) …", which is licence-gated). Two further conjectures are flagged and deliberately *not* asserted, because neither was measured here: that the extended window spans more volatility-regime heterogeneity (2008, 2020), and that Compustat-`secd` daily returns are noisier than CRSP (untestable — CRSP is not on disk). Neither belongs on a slide as an explanation. ## Sources - Gormley, T. A., & Matsa, D. A. (2016). *Playing it safe? Managerial preferences, risk, and agency conflicts.* Journal of Financial Economics 122(3), 431–455. All GM quotes above are verbatim from the paper's Sections 3–4 and Appendix Table A.2. - Bertrand, M., & Mullainathan, S. (2003). *Enjoying the quiet life? Corporate governance and managerial preferences.* Journal of Political Economy 111(5) — the 30-state BC-law dating GM builds on. - Pinnell, C. (2000). *State Takeover Laws* — the source for GM's three additional states (Iowa, Oregon, Texas). - Gormley, T. A., & Matsa, D. A. (2014). *Common errors: How to (and not to) control for unobserved heterogeneity.* Review of Financial Studies 27(2), 617–661 — the AvgE "common error" doctrine behind §14. - Sun, L., & Abraham, S. (2021). *Estimating dynamic treatment effects in event studies with heterogeneous treatment effects.* Journal of Econometrics — the §12 estimator. - Angrist, J. D., & Pischke, J.-S. *Mostly Harmless Econometrics* — the bad-controls warning of §14. - Build provenance: the committed scripts `code/gm_*.py`, `gm_did_rcheck.R`, `gm_phase3_rcheck.R`, and the frozen result ledgers `outputs/gm-*.md`. ## Session info The free spine of this document ran under the versions below; the quoted econometrics ran under `pyfixest`, cross-checked in R `fixest` per `gm_did_rcheck.R` / `gm_phase3_rcheck.R`. ```{python} #| eval: true #| echo: true import sys, platform, pandas, matplotlib sys.path.insert(0, "code") import gm_bc_dates as bc print("Python :", platform.python_version()) print("pandas :", pandas.__version__) print("matplotlib :", matplotlib.__version__) print("gm_bc_dates:", len(bc.BC_LAWS), "states,", len(bc.bm_only()), "in the BM-only subset") print("econometrics quoted from ledgers; ran under pyfixest, cross-checked in R fixest") ```