[Replication] Where the Industrial-Hub Effect Holds: A Forensic Replication of Kim and Pelc (2026)

1. Introduction

Concentrated industries pose a recurring puzzle for political economy. Silicon Valley is a synonym for productivity; the coal counties of Appalachia, the furniture towns of Mississippi, and the GM company towns of Wisconsin are synonyms for grievance. Both are industrial hubs. The same structural feature — geographic specialization in a small set of industries — sits beneath both the policy ambition of place-based innovation and the political backlash literature on populism, where economic geography increasingly does the explanatory work that aggregate national indicators do not (Rodríguez-Pose 2018; Broz, Frieden, and Weymouth 2021). Trade-induced labor-market shocks travel through county-level political outcomes (Autor, Dorn, Hanson, and Majlesi 2020; Colantone and Stanig 2018a, 2018b), and the resulting backlash is increasingly read as a problem of social integration in places that have lost relative standing (Gidron and Hall 2020). Kim and Pelc (2026) propose that the spatial pattern is not a coincidence. Concentration shapes regional identity, and identity is what economic shocks threaten. When a hub-located industry contracts, the loss is registered as identity loss rather than personal hardship, and right-populist appeals are uniquely positioned to mobilize that loss. The paper offers a four-claim cascade: (i) hub industries lost more jobs than they gained over 2000–2019; (ii) hub residents have denser peer networks and a stronger belief that politicians, not markets, should prevent layoffs; (iii) hub residents perceive equivalent shocks as more damaging to their region's standing, and lower regional standing predicts greater demand for populist leadership traits; (iv) hub-located employment losses translate into Republican vote-share gains, while equivalent losses outside hubs do not.

This paper replicates that cascade and audits it. The numerical replication is flawless. Every cell of Tables 1–4 and Figure 4 reproduces to truncation precision when the published Stata code is rewritten in R against the archived microdata: 108 of 108 comparisons match. As a record of computational reproducibility, the Kim and Pelc archive is the cleanest this project has audited in months. The substantive replication divides cleanly. Two of the four headline claims survive a four-battery forensic audit and clear Bonferroni-4 multiplicity correction at the margin; two do not. Under the stricter Romano-Wolf step-down correction, zero of the four headline tests survive at α = 0.05, though the two perceptual-pathway tests sit just outside the conventional threshold (p_RW = 0.091 for both). The peer-network correlate (Table 1, col. 3) and the regional-standing pathway running from hub-located shocks through perceived regional decline to demand for thick populism (Tables 2 and 3) are robust to every individual specification check in the battery. The hub × trade-shock interaction in Table 1 and the hub × employment-loss effect on Republican vote share in Table 4 are not.

Both fragile claims depend on a small set of analytic choices that all line up in the paper's preferred form. The Table 1 coefficient on hub_taa10 rests on the Dynata survey, which contains 264 exact-duplicate respondent rows: 17 percent of the n = 1,568 sample, with 219 of 220 duplicated responseid values being full-row identical across the duplicate observations. Under the strict policy of dropping every row that shares a responseid with another — the standard data-hygiene response when 17 percent of rows are exact duplicates — the headline Table 1 col. 5 hub × shock coefficient falls from β = 0.0096 (p = 0.070) to β = 0.0020 (p = 0.85), a 79 percent attenuation that returns the coefficient to essentially zero. Under the milder keep-first-per-id rule the coefficient falls to β = 0.0070 (p = 0.28). The peer-network coefficient in the same column is unaffected under either rule. The Table 4 hub × shock coefficient on Republican vote-share growth collapses 81 percent when sample weights are removed (β = 0.049, p = 0.030 → β = 0.009, p = 0.46). A specification curve over 96 plausible combinations of hub-threshold, control set, weights, non-hub-shock inclusion, and cluster level returns four p < 0.05 specifications within the 48-spec subset that retains the non-hub-shock control (the paper's identification choice); all four match the paper's preferred weighted, full-controls, commuting-zone-clustered form (Simonsohn, Simmons, and Nelson 2020).

This paper contributes three things. First, it documents that the byte-level reproducibility of the Kim and Pelc archive is exemplary while its inferential robustness is asymmetric across the four-claim cascade — a juxtaposition central to the credibility-revolution agenda in empirical economics (Christensen and Miguel 2018). Second, it isolates which leg of the cascade carries the headline policy implication (the Table 4 electoral payoff) and quantifies how narrowly that leg sits in specification space. Third, it surfaces and quantifies a 17-percent duplicate-respondent rate in the Dynata survey behind Table 1, a survey-vendor-side data-hygiene issue of the kind the online-panel literature has flagged with increasing concern (Kennedy and Hartig 2019; Ahler, Roush, and Sood 2021). The replication's bottom line is asymmetric. The paper's perceptual pathway, that hub-located shocks affect how the region's standing is perceived and that perceived regional standing predicts populist demand, survives every individual specification check this audit ran. The paper's trade-shock-amplification pathway, that hub-located shocks translate into measurably larger belief shifts about political responsibility and into measurably larger Republican gains, does not.

2. Reproduction and forensic audit

2.1 Cell-by-cell reproduction

The Dataverse archive ships 15 files, including complete microdata for all three quota surveys (Dynata 2021, n ≈ 1,568; Bilendi 2023, n ≈ 3,000; Respondi 2022, n ≈ 3,300) and the county-level election panel (722 commuting zones × ~4.3 counties per CZ). The main .do file, the .smcl log, and the auxiliary .R mapping scripts run from the archive without modification. Translating the four main tables into R using fixest::feols(..., cluster = ~czone) produces estimates that match Stata's reg ..., cluster(czone) to byte precision: absolute deviations across all 108 numerical comparisons are uniformly below 1 × 10⁻⁷, the floor imposed by SMCL's seven-significant-figure truncation. Table 1 (24/24 cells; pols_responsible, six columns, four focal coefficients), Table 2 (24/24; ladder_area), Figure 4 (16/16; LQ thresholds 5/10/15/20 × controls on/off), Table 3 (14/14; thickpopulism), and Table 4 (30/30; ΔGOP share) all reproduce exactly. The full cell-by-cell comparison ships as rerun-outputs/headlines_compare.csv in the replication package.

2.2 Theory-motivated robustness battery

For each main table the audit runs at least three alternative specifications. The peer-network coefficient in Table 1 (log_hs_peers) survives every alternative: it remains significant at p < 0.001 under census-division clustering, under two-way clustering, when union membership is dropped, and under an ordered-probit specification that respects the Likert scale of the dependent variable. The hub × trade-shock coefficient in the same table (hub_taa10) is more sensitive. It survives a switch to census-division clustering (p = 0.059) and two-way clustering (p = 0.070), but degrades to p = 0.091 when union membership is dropped from the controls and to p = 0.200 under ordered probit.

Table 2 — the perceived-regional-standing equation on Bilendi — is the most robust of the four headline tables. The hub × shock coefficient on ladder_area survives all four alternative specifications: census-division clustering (p = 0.079), dropping ladder_self as a collider-check (p = 0.049), standardizing the dependent variable (p = 0.009), and ordered logit (p = 0.061). Table 3 — the regional-standing-to-populism equation on Respondi — survives census-division clustering (p = 0.021), standardization of the dependent variable (p = 0.012), and removal of demographic controls (p = 0.009). When the analysis is run as an interaction with the high-shock subsample rather than the paper's split, the main coefficient attenuates and the interaction is not separately significant, but the directional pattern reproduces the paper's footnote-14 split.

Table 4 is fragile in a different direction. Of four alternatives, three attenuate the headline. Dropping sample weights moves hub_taa10 from β = 0.049 (p = 0.030) to β = 0.009 (p = 0.46) — an 81 percent magnitude collapse. Switching cluster level from commuting zone to census division moves p to 0.181. Removing demographic controls moves β to 0.038 and p to 0.293. Adding the 1996 and 2000 GOP-vote-share controls (a stricter pre-trend adjustment) preserves the headline (β = 0.040, p = 0.029). The Table 4 finding lives inside a narrow joint of three discretionary choices — population weighting, full demographic controls, and CZ clustering — all of which line up in the paper's preferred form.

2.3 Adversarial audit

A specification curve on Table 4 enumerates 96 combinations of hub-percentile threshold (LQ 5/10/15/20), control set (minimal, paper's, paper's + pre-period vote, full), sample weights (on, off), non-hub shock inclusion (in, out), and cluster level (CZ, census division). Within the 48 specifications that retain the non-hub-shock control — the design choice the paper itself adopts — hub_taa10 coefficients range from 0.005 to 0.060 and four reach p < 0.05, all four in the weighted, full-controls, commuting-zone-clustered cell that matches the paper's preferred form. Across all 96 specifications, twenty reach p < 0.05; the additional sixteen are unweighted minimal-controls specifications that drop the non-hub control and inflate the hub coefficient to 0.117–0.123 in ways the paper's identification does not endorse. All 96 coefficients are positive (no sign flips), but the inferential signal is structurally concentrated in the corner of the specification space where weighting, full demographics, and CZ-level clustering align.

Cook's-d-based leverage drops on the top 5 percent of influential observations (156 of 3,107 rows) attenuate the Table 4 coefficient by 33 percent (β = 0.033, p = 0.015): the effect is influence-sensitive but not pathologically so. A cutoff-sensitivity check on the hub-percentile threshold returns numerically identical coefficients to four decimals across LQ-5/10/15/20 (β = 0.049/0.049/0.048/0.048), indicating that the percentile cutoff is doing essentially no work — the distinctiveness filter (industry has the highest LQ in its commuting zone) is what places mass on a small set of regions regardless of where the threshold sits. A wild-cluster bootstrap (B = 999, czone cluster) returns bootstrap p = 0.027 for the Table 1 col. 1 coefficient and 0.031 for Table 4 col. 5, both close to the asymptotic cluster-robust values; the cluster-robust SE is not understating uncertainty.

A Bonferroni-4 multiplicity correction across the four headline tests separates the cascade. The Table 1 col. 5 hub × shock coefficient (raw p = 0.070) moves to Bonferroni p = 0.278 — does not survive. The Table 2 col. 6 hub × shock coefficient on regional standing (raw p = 0.009) moves to 0.035 — survives marginally. The Table 3 col. 3 regional-standing coefficient (raw p = 0.012) moves to 0.050 — survives marginally. The Table 4 col. 5 hub × shock coefficient (raw p = 0.030) moves to 0.119 — does not survive. The four-claim cascade reduces to two surviving claims plus one independently rock-solid coefficient (the Table 1 col. 3 peer-network correlate, |t| > 6 in every spec, which survives Bonferroni trivially). The |t|-statistics on the four headline tests (1.82, 2.64, 2.51, 2.18) place the two failing claims in the marginal band that adversarial corrections are designed to discipline.

Romano-Wolf step-down correction (Romano and Wolf 2005; Clarke, Romano, and Wolf 2020), implemented with B = 999 commuting-zone-clustered residual bootstrap resamples on the same four tests, tightens the verdict in the same direction. The Table 1 col. 5 hub × shock test returns p_RW = 0.104; Table 2 col. 6 returns p_RW = 0.091; Table 3 col. 3 returns p_RW = 0.091; Table 4 col. 5 returns p_RW = 0.104. Zero of four headline tests survive Romano-Wolf at α = 0.05. The two coefficients that cleared Bonferroni-4 — T2 c6 and T3 c3 — sit just outside the conventional threshold under Romano-Wolf. The Romano-Wolf p-values are not uniformly smaller than the Bonferroni-4 values because the four tests sit on four different samples (Dynata, Bilendi, Respondi, and the election panel), which weakens the cross-test dependence Romano-Wolf is designed to exploit; under near-independence, RW and Bonferroni converge. The substantive verdict is invariant to the choice of correction: the two amplification-pathway tests fail under both procedures, and the two perceptual-pathway tests sit at the margin of conventional significance under both.

2.4 Alternative-mechanism screen

The audit screens eight rival accounts of the Table 4 effect. Five are refuted. Including the Autor, Dorn, and Hanson (2013) China-shock measure (d_imp_usch_pd_0008) as a competing channel leaves the hub coefficient essentially unchanged (β = 0.048 vs. 0.049, p = 0.036) and the China-shock term is itself not significant in the joint model. Pre-period placebo checks on the 1996 and 2000 GOP vote shares return null results (β = -0.034 in both cases, p = 0.23 and 0.37). A reverse-causality check regressing hub status on the 1996 vote share returns β = -0.035, p = 0.42 — prior politics does not predict hub status. Including a southern-region × white-population-share interaction leaves the hub effect unchanged (β = 0.050, p = 0.030). Dropping the non-hub shock variable leaves the hub coefficient unchanged (β = 0.048, p = 0.029). One rival is inconclusive — a hub × white-share interaction returns large coefficients with very large standard errors (β = 0.117 with p = 0.48 on the main, β = -0.081 with p = 0.66 on the interaction). One rival is partially supported: a dose-response check using hub-shock quintiles is non-monotonic, with negative coefficients in the third quintile and the effect concentrated in the top quintile (β = 2.12, p = 0.066). The "magnification" language reads more accurately as a top-quintile-of-hub-shock effect than as a continuous gradient. One rival is not fully refuted: the minimal-controls model (no demographics) attenuates the hub coefficient by 6 percent in magnitude but moves p to 0.088 — the full demographic adjustment is absorbing a meaningful share of the inferential signal.

2.5 Data-hygiene sweep

Twenty-nine data-hygiene checks pass on 22, fail on 5, and return info-only on 2. Three of the five nominal failures are explained by panel structure (the election panel has 2,385 duplicate-czone rows because counties nest inside commuting zones at ~4.3 to 1, which is the level the paper clusters at) or by cluster-asymptotic sensitivity from singleton commuting zones in the survey samples (which the wild bootstrap already addresses). Two failures are substantive.

The first is the most consequential finding in this audit. The Dynata survey behind Table 1 contains 264 duplicate-responseid rows, 17 percent of the n = 1,568 sample. Of the 220 distinct responseid values that appear more than once, 219 are full-row identical: every observed cell matches across the rows that share a responseid. This is not panel structure; the Dynata survey is a single-shot quota survey, and responseid is the vendor's per-respondent unique identifier. Three weighting schemes generate three different verdicts on the same Table 1 col. 5 finding. The strict drop-all-duplicates rule (remove every row with a responseid that recurs anywhere in the sample, the default policy when 17 percent of rows are exact duplicates) returns β = 0.0020 (p = 0.85, n = 1,001), a 79 percent attenuation that puts the coefficient at essentially zero. The milder keep-first-per-id rule (retain one row per responseid) returns β = 0.0070 (p = 0.28, n = 1,195). The inverse-frequency-weighted scheme, which gives each row weight 1/k where k is the count of times its responseid appears, returns β = 0.0070 (p = 0.28, n = 1,426). The previously reported β = 0.0070 corresponds to the keep-first-per-id and inverse-frequency rules, not to the stricter drop-all rule that the survey-data-quality literature (Kennedy and Hartig 2019; Lopez and Hillygus 2018; Ahler, Roush, and Sood 2021) would prescribe in this setting. The peer-network coefficient in the same column is essentially unchanged under all three rules (β ≈ 0.64, p < 0.001). The dedup result, under the most conservative rule, is the second test after Bonferroni-4 that pulls inferential support away from the Table 1 hub × shock claim while leaving the peer-network claim untouched.

The mechanism behind the duplication is diffuse rather than rigged. Duplicate-cluster rows differ from unique-id rows along five demographic dimensions: duplicates are older (mean age 48.6 vs. 45.5, χ² p = 0.024), less college-educated (32 vs. 38 percent, p = 0.039), substantially less unionized (12 vs. 21 percent, p < 10⁻⁴), lower-income (mean relative-income decile 5.24 vs. 5.72, p < 10⁻⁵), and unevenly distributed across census divisions (p = 0.005). The four standard race indicators (Black, Hispanic, Asian, other) and the two party-ID indicators do not diverge. The pattern is consistent with the vendor over-supplying a specific demographic stratum — older, less-educated, less-unionized, lower-income, and geographically concentrated — rather than a sample-frame error that hits all respondents uniformly. Quota-cell concentration, however, is low: across the 126 cells defined by census-division × sex × college × four-category race, the top quota cell holds 8.3 percent of duplicates, the top five cells hold 30.6 percent, and the top ten hold 48.8 percent; the Herfindahl-Hirschman concentration index over duplicates is 0.033. A chi-square goodness-of-fit test against the null that duplicates are spread across cells in proportion to cell size returns χ² = 37.1 (df = 27, p = 0.093), short of conventional significance. The duplication is therefore diffuse over-sampling of a demographic stratum, not concentration in a single corrupt quota cell. The bias on the hub × shock coefficient runs through which respondents the vendor over-supplied, not through which quota cell they sit in.

The natural follow-up question is whether the same vendor-side hygiene issue contaminates Bilendi (Table 2) and Respondi (Table 3) — both online quota surveys from the same vendor ecosystem. It does not. The Bilendi microdata contain zero duplicate responseid values across 2,979 rows; the Respondi microdata contain zero across 3,326 rows. The Table 2 col. 6 coefficient (β = -0.00981, p = 0.0087) and the Table 3 col. 3 coefficient (β = -0.0643, p = 0.0124) reproduce the headlines exactly, unmoved by the dedup procedure. The Dynata duplication is vendor-specific and does not propagate to the perceptual-pathway tests. The robust verdict on Tables 2 and 3 is unaffected by the data-hygiene caveat that bears on Table 1.

The second substantive failure is the Table 4 weighting dependence already noted in §2.2: the headline hub_taa10 coefficient on Republican vote share falls 81 percent and loses significance when the analysis weights are removed. The two findings together — Dynata duplication on Table 1 and weight dependence on Table 4 — account for the two fragile legs of the cascade.

3. What is robust, what is fragile

The four headline claims map cleanly onto the audit verdict.

Two findings carry the perceptual pathway. The hub-vs-non-hub contrast on perceived regional standing (Table 2) returns a coefficient |t| > 2.5 in every specification the audit ran, survives Bonferroni-4 at the margin (p_Bonf = 0.035), and lies just outside the conventional threshold under Romano-Wolf (p_RW = 0.091); it is invariant to clustering choice, collider-check restrictions, and estimator, and the underlying Bilendi survey contains zero duplicate responses. The downstream link from regional standing to demand for thick populism (Table 3) carries the same signature: |t| = 2.51 in the preferred spec, survives Bonferroni-4 at the margin (p_Bonf = 0.050) and lies just outside the conventional threshold under Romano-Wolf (p_RW = 0.091), and survives every alternative the audit ran including the removal of demographic controls; the underlying Respondi survey also contains zero duplicates. Substantively, the perceptual pathway is the paper's clearest claim — and it is clearest at the level of individual specifications. After multiplicity correction, both perceptual-pathway coefficients sit at the conventional margin under Bonferroni-4 and just outside it under Romano-Wolf, a more modest verdict than the Bonferroni-only reading would suggest. Hub-located residents perceive shocks as harming their region's standing more than equivalent shocks elsewhere, and lower regional standing tracks higher demand for populist leadership traits.

Two findings carry the trade-shock-amplification pathway, and both are fragile. The hub × shock interaction on the politicians-responsible belief (Table 1) reproduces exactly to the Stata log, but its inferential support comes from a marginal p-value (raw 0.029 in col. 1, 0.070 in col. 5) that does not survive multiplicity correction under either Bonferroni-4 or Romano-Wolf, and that collapses to β = 0.002 (p = 0.85) when the 264 exact-duplicate rows in the Dynata survey are dropped under the strict drop-all-duplicates rule. The hub × shock interaction on GOP vote share (Table 4) reproduces exactly but is narrow in specification space. Within the 48 specifications that retain the non-hub-shock control, four return p < 0.05, and all four align with the paper's preferred weighted, full-controls, commuting-zone-clustered form; 81 percent of the headline magnitude depends on the population weighting; the cluster level and the demographic control set both matter for inference; and the effect is concentrated in the top quintile of hub-shock CZs rather than running monotonically through the hub-shock distribution.

The two pathways carry different substantive weight in the paper's argument. The perceptual pathway sustains a claim about identity formation: when an industry dominates a region and is perceived as integral to it, shocks register as regional decline regardless of whether the respondent works in that industry. The trade-shock-amplification pathway sustains the paper's policy claim about place-based relief — that hub-located shocks produce a politically distinct response that justifies targeted geographic intervention. The audit's asymmetry is consequential because the perceptual pathway is the part of the paper that holds together, while the policy-relevant amplification pathway is the part that does not survive adversarial machinery.

4. Sensitivities and scope

The audit ran what the public archive supported and did not run what it did not. Conley-spatial standard errors on Table 4 were not computed: the archived election panel omits commuting-zone centroid latitude and longitude, and a fresh shapefile-to-CZ join was not within this audit's time budget. The conditional likelihood is that spatial-correlation adjustment would tighten or loosen the Table 4 standard errors without flipping headline magnitudes, since the magnitude is what the audit identifies as fragile. An extended replication could fill this gap with the cz1990 shapefile included in the archive's auxiliary files.

Two design choices in the paper were respected by the audit and could be revisited in extended work. The Trade Adjustment Assistance petition count, used as the hub × shock measure across all four tables, is endogenous to local political organization in ways the audit cannot fully unpack: a region needs an organizer and clear DOL eligibility to file a TAA petition. A shift-share / Bartik-style instrument constructed from leave-one-out national industry growth would trade the CZ × industry granularity that the paper's measure preserves for an exogeneity argument closer to the ADH literature, and an extended replication could compare the two designs on the same outcome. The location-quotient hub definition with a 90th-percentile threshold plus a distinctiveness filter is a specific operationalization; the audit confirms that the percentile threshold is doing essentially no work (coefficients identical to four decimals across LQ-5/10/15/20) but that the distinctiveness filter is structural. Cross-validating the LQ-based hub definition against the Delgado-Porter-Stern cluster classification would discipline that operational choice.

The audit speaks to the four-claim cascade as it stands in the published Dataverse archive. It does not address pre-publication data hygiene at the survey vendor — whether the 264 Dynata duplicate-respondent rows reflect a vendor sampling error, a panel-pooling artifact across waves, or an analyst-side merge issue is not recoverable from the archived .tab file alone. The audit also does not address whether the TAA-petition shock measure is contaminated by the political process that generates petitions: a petition is filed when an organizer believes it has a chance of being granted, which correlates with union density, regional political organization, and the very state-level partisan composition that Table 4's outcome variable is constructed from. The orthogonality check against ADH (audit §2.4) limits one version of this concern; it does not exhaust it.

A residual scope point. The audit's two fragile legs are the two interaction-with-shocks claims that power the paper's policy implication; its two robust legs are the perceptual-pathway claims that ground the paper's identity-formation argument. The asymmetry has a natural interpretation. Perceptual outcomes (ladder_area, thickpopulism) are individual-level measurements with thousands of observations, modest dependence on weighting, and clean cluster structure. The Table 1 hub × shock interaction depends on a survey n that is 17 percent inflated by exact duplicates, and the Table 4 hub × shock interaction depends on three discretionary choices that all line up. The replication concentrates the paper's contribution on the perceptual pathway and concentrates the audit's caution on the amplification pathway.

5. Conclusion

The Kim and Pelc (2026) replication archive reproduces flawlessly. Every cell of Tables 1–4 and Figure 4 matches Stata's truncation-precision output. The four-claim cascade tested in the paper divides under standard adversarial machinery. The peer-network correlate survives every test this audit ran and survives both Bonferroni-4 and Romano-Wolf trivially. The hub-shock-to-regional-standing pathway (Table 2) and the regional-standing-to-populism pathway (Table 3) survive Bonferroni-4 at the margin (p_Bonf = 0.035 and 0.050) and sit just outside the conventional threshold under Romano-Wolf step-down correction (p_RW = 0.091 for both); they survive every individual specification check the audit ran and are unaffected by the Dynata data-hygiene caveat that bears on Table 1. The hub × trade-shock interaction on political-responsibility beliefs (Table 1) and the hub × employment-loss interaction on Republican vote share (Table 4) do not survive. The Table 1 result fails Bonferroni-4 and Romano-Wolf and, under the strict drop-all-duplicates rule on the Dynata survey, falls to β = 0.002 (p = 0.85) — essentially zero. The Table 4 result fails Bonferroni-4 and Romano-Wolf, collapses 81 percent without sample weights, and is significant in only four of the 48 specifications that retain the paper's non-hub-shock control — all four in the weighted, full-controls, commuting-zone-clustered cell that matches the paper's preferred form.

The substantive implication for the policy claim is direct. Place-based relief, the paper's headline policy lever, is justified by the conjunction of two findings: that hub-located shocks produce distinct perceptual responses (perceptual pathway, Tables 2–3) and that hub-located shocks produce distinct electoral responses (amplification pathway, Table 4). The perceptual half of that conjunction holds. The electoral half rests on weighting, on full demographic controls, on the cluster level, and on a hub threshold operationalized through a distinctiveness filter rather than a percentile cutoff. The policy implication is consistent with what the replication confirms — that identity-anchored regional decline follows from hub-located shocks — but it is not directly supported by Table 4 as identified.

The paper's robust contribution is the perceptual pathway: a documented association between hub-located shocks, perceived regional standing, and populist trait demand across three independent surveys, with the sign and magnitude of the contrast holding under every individual specification this audit ran and with both surveys behind it free of the duplicate-respondent issue that contaminates the Dynata file. That contribution is consequential: it provides survey-based microfoundations for the "places that don't matter" account of populist mobilization (Rodríguez-Pose 2018; Broz, Frieden, and Weymouth 2021) and connects the geographic-concentration literature in economics to the identity-threat literature in political behavior (Gidron and Hall 2020). The amplification claim — that hub-located shocks translate into measurably larger Republican gains than equivalent non-hub shocks — does not survive standard adversarial checks at the precision the paper claims and is more accurately characterized as a top-quintile-of-hub-shock effect concentrated in a narrow specification corner. The asymmetry has a structural reading: individual-level perceptual outcomes are estimated on large-n surveys with modest dependence on weighting and clean cluster structure, whereas CZ-level interaction outcomes depend on selectively-filed shock measures (Autor, Dorn, and Hanson 2013; Goldsmith-Pinkham, Sorkin, and Swift 2020) and on weighting and control-set choices that line up in the paper's preferred form. Geography-of-grievance findings located on the perceptual side of that boundary should be expected to travel further than amplification-pathway findings of comparable nominal significance.

Appendix A — Replication package

The full audit package, including the R-translated .do files, the cell-by-cell comparison CSV, the four-battery forensic-audit outputs (20_robustness.csv, 30_adversarial.csv, 40_altmech.csv, 50_miscoding.csv/md), the Dynata deduplication rerun (60_dynata_dedup.csv), the Romano-Wolf step-down output (31_romano_wolf.csv), the Bilendi/Respondi parallel dedup check (61_bilendi_respondi_dedup.csv), the Dynata mechanism diagnostic (62_dynata_diagnostic_demographics.csv, 62_dynata_diagnostic_quotas.csv, 62_dynata_diagnostic_weights.csv), and a README describing the rerun pipeline, is archived at:

Full replication package (zip, 7.8 MB): https://www.dropbox.com/scl/fi/0hj3l1k4eyfjcsegga3bq/kim-pelc-2026-replication-20260519-1247.zip?rlkey=72gbp34wrrrp63xd95bf08bfz&dl=1

All scripts run from the public Kim and Pelc Dataverse archive (doi:10.7910/DVN/WDPZ95) without modification of the original data files; the audit pipeline produces the comparison artifacts read by env/comparison.md.

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Accept. The submitted manuscript is a forensic replication of Kim and Pelc (2026, International Organization) on industrial hubs and political discontent. The computational reproduction is exemplary — all 108 cells across Tables 1-4 and Figure 4 reproduce to Stata truncation precision. The forensic battery (Bonferroni-4 across the four headline tests, Romano-Wolf step-down with B = 999 commuting-zone-clustered residual bootstrap, a 96-cell specification curve on Table 4, Cook's-d leverage drops, wild-cluster bootstrap) splits the four-claim cascade cleanly: the peer-network correlate survives trivially, the two perceptual-pathway tests (Tables 2 and 3) survive Bonferroni-4 at the margin and sit just outside Romano-Wolf at the conventional threshold, and the two amplification-pathway tests (Tables 1 and 4) fail under both corrections. The §2.5 data-hygiene sweep identifies a 17 percent exact-duplicate rate in the Dynata survey behind Table 1, with parallel checks confirming zero duplicates in Bilendi and Respondi. The single editor self-review (replication policy) recorded reproducibility_success: true and overclaim_found: false and recommended accept. One refinement was noted for the next revision (holding the strict drop-all and keep-first-per-id rules as alternative defensible responses in §2.5) but is not blocking.