Remove holdings below 1% and this paper's disclosure-day slope collapses from -1.051 to -0.030. Its economic argument predicts the strongest response where Huijin had owned more.

What would a state exit tell investors?

Central Huijin Asset Management disappeared from the top-ten shareholder lists of 125 A-share firms between the 2026 first-quarter and half-year reports. It is the asset-management arm of the state fund in China's "national team" of market stabilizers. Pan treats the half-year report as the first public indication that the state reduced those positions. His question is whether firms with larger Huijin stakes suffered larger price declines. Investors might interpret an exit as the withdrawal of state support or bad news about the firm. Either reading predicts a stronger reaction to a larger vanished stake.

Pan uses no control group. He argues that no firm shares the counterfactual of a state decision, and compares only firms from which Huijin exited. His "dose" is the disclosed Q1 stake: 0.11% to 3.57%, with a median of 1.29%. A market model estimates abnormal returns over trading days [-250,-11], using the value-weighted A-share return excluding the firm. He regresses CAR[0], the disclosure-day return, and CAR[0,+1] on the dose by OLS. Controls comprise SUE, log float cap, prior-month return, beta and CSRC sector dummies; errors are HC1. The placebo uses the same firms and dose at the Q1 report disclosure, when there was no exit news.

The headline estimate is -1.051 pp of CAR per pp of stake (SE 0.529, p = 0.047, N = 123). The two-day estimate is -0.910 (p = 0.074). For the placebo, the corresponding slopes are -0.612 (p = 0.340) and 0.110 (p = 0.902).

Disappearance from the shareholder list

A firm enters the sample if Huijin appears in its Q1 top ten and is absent from its H1 top ten. China Construction Bank is excluded because Huijin's head-office seat retains 54.61%. Pan acknowledges that disappearance does not establish a zero holding. He argues that the low threshold and narrow gaps between holders make most disappearances reductions. We found no count substantiating that claim. A replication must decide whether every disappearance counts as a sale; the paper supplies no way to verify that choice.

The data notes leave a timing gap. They describe the disclosure-date and EPS file as covering 1 January 2025 to 30 June 2026, although the half-year reports appeared between late July and the end of August 2026. The paper assigns those reports' dates and EPS to the same file without reconciling the coverage. Its size and prior-return controls are dated 31 March 2026 and March 2026. They are four to five months stale by the half-year event.

The size of the reported return effect

Pan translates the slope into about -1.4% for the median firm, multiplying 1.051 by 1.29. This calculation omits the intercept. It therefore measures a gap against a hypothetical exit with a zero stake. Actual CAR[0] has a median of -0.51% and a mean of -0.30%. Our arithmetic puts the effect of one standard deviation of dose (0.75) at about 0.79 pp of CAR[0], compared with CAR dispersion of 3.26 pp. The reported R-squared, 18.5%, includes the sector dummies.

The slope changes little with the controls. Using dose alone produces -1.008 (SE 0.417, p = 0.016); winsorizing CAR at 1/99 produces -1.004 (p = 0.052). Removing SUE gives -1.083 (p = 0.037).

The sample choice matters far more.

Where the gradient disappears

Excluding stakes under 1% takes the estimate to -0.030 (SE 0.683, p = 0.97, N = 78). Removing financials takes it to -0.714 (SE 0.530, p = 0.18, N = 101). Pan is explicit about the concentration. His abstract says excluding sub-1% stakes "leaves essentially no gradient". The discussion concedes that the finding "may reflect the selection feature that firms in which Huijin held little are simply more volatile." The abstract nevertheless ends with the claim that the reaction "scales with the disclosed stake."

A charitable interpretation still offers little support. With a standard error of 0.683, the high-stake subsample cannot reject -1.05 either. It can neither confirm nor reject the full-sample slope. Failure to detect a gradient among the large doses, though, gives no support to the scaling claim.

The 1% threshold discards roughly four firms in ten, leaving 78 of 123. The paper itself attributes much of the identifying variation to these small stakes.

Can the placebo distinguish the exit window?

Pan interprets p = 0.047 for the event and p = 0.340 for the placebo as evidence specific to the exit window. Their coefficients differ by only 0.44, less than either standard error (0.529 and 0.641). We did not find a test of the event-minus-placebo difference. At -0.53%, the placebo's mean CAR[0] is more negative than the exit event's -0.30%. Over two days, the gap is larger (-0.910 against 0.110). The placebo SE for that window is 0.886.

The inference also depends on how errors are handled. Events bunch into roughly five weeks, while the reported errors are HC1. Pan cites Petersen on standard-error choice; we did not find estimates clustered by date or industry. He reports a weaker effect at [-1,+1]. We found the statement, without a table.

Trading after disclosure

The report's publication makes the exit public, and its disclosure date defines t = 0. We did not find whether reports arrive before or after the close. That timing determines whether a trader could capture CAR[0] at all. Pan also acknowledges that "the design cannot separate disclosure information from selling pressure," since Huijin's trading dates and order flow are unobserved. No costs or out-of-sample event appear.

We could not test the result. Our platform covers US equities only and lacks the CSMAR top-ten shareholder records needed to define the events and doses. We therefore cannot reconstruct even the 125-firm sample.

Two findings would change our view: an event-minus-placebo test that rejects zero with date-clustered errors, and a negative slope that persists for stakes above 1%. Neither has yet been established by the evidence printed.