[Replication] Where the autocratic-lender effect lives: a replication of Cottiero and Schneider (2026)

1. Introduction

Cottiero and Schneider (2026) assemble the most comprehensive panel to date of lending by international financial institutions (IFIs) whose memberships are predominantly authoritarian. The dataset covers 20 autocratic IFIs, 143 recipient countries, and the 1967–2021 period. The headline finding, taken from Appendix G Model 1 and reported verbatim in the body, is that "every 1 standard deviation increase in an autocratic recipient's coup risk is associated with a doubling of aid from autocratic IFIs (a 103 percent increase)" [@cottiero_schneider2026]. The companion claim on the conflict regressor — a 1-SD increase in domestic anti-government conflict raises log new commitments by β = 0.42, or roughly 52% in level terms — is the test the audit treats as headline because it carries the largest sample (n = 7,646) and the smallest reported standard error.

The headline regression reproduces exactly. Re-running the deposited Stata code in R against the published dataset returns β_zdomconflict = 0.4234 (SE 0.0989, p = 1.88e-5) on the same 7,646 IFI-recipient-year cells, with companion coefficients matching to four decimal places. The headline survives the audit's standard surface-robustness battery: leave-one-IFI-out across 16 IFIs holds β in [0.31, 0.51]; ±50% perturbations of the unmotivated income cap leave β in [0.39, 0.48]; dropping region from the fixed-effect structure and adding ideological-alignment controls move β by less than 5%; the Bonferroni correction over 44 reported regressions in Appendices G–M holds at p_bonf < 0.001. Of 16 specifications in a fixed-effects × cluster × sample × controls grid, none flips sign or loses p < 0.10. By the standards of the published robustness section, the headline is hard to dislodge.

Four deeper sensitivities qualify what the headline supports. First, the result is overwhelmingly concentrated in the extensive margin. A linear-probability model on the same sample returns β = 0.0245 (p = 4.3e-5): a 1-SD increase in conflict raises the probability of any new commitment by 2.45 percentage points. Replacing the log outcome with the level wipes the coefficient (β ≈ 0, p = 1.0); restricting to the 4,361 positive-flow cells alone collapses β by 80% to 0.083 (p = 0.013). The clean version of the headline is a probability-of-entry story, not the magnitude story the log-coefficient framing suggests. Second, the cross-sectional correlation is consistent with anticipation rather than reaction. When the lead of conflict is added alongside the contemporaneous regressor, the contemporaneous coefficient collapses to 0.08 (p = 0.62) and the lead becomes the only significant timing coefficient at β = 0.355 (p = 0.04). The data are equally compatible with autocratic IFIs disbursing just before crises that they or recipient governments anticipate.

Third, the headline is two-IFI-deep: leave-one-out shows BADEA carries 27.9% of the coefficient and OPEC 23.4%; IFI-type subsetting shows that regional development banks alone yield β = -0.16 (n = 2,969), with the result loaded entirely onto eight Arab and oil-funded IFIs (β = 0.778, p = 4.2e-9, n = 4,462). Fourth, switching from the published vce(robust) to two-way clustering at recipient × IFI inflates the p-value from 1.9e-5 to 0.040 — still significant, but the "various operationalizations ... and different model specifications" framing for extreme robustness no longer holds.

The narrowed claim that survives is sharp. Across roughly eight Arab and oil-funded autocratic IFIs over 1989–2021, aid commitments to autocratic recipients correlate with measures of recipient regime vulnerability primarily on the extensive margin, with timing consistent with anticipation rather than acute response, and with cluster-robust inference at p ≈ 0.04 rather than p ≈ 10⁻⁵. The descriptive contribution — the 18-IFI panel with newly compiled lending data on nine institutions previously absent from AidData and the OECD CRS — is unambiguous and is not contested by anything in the audit. The inferential contribution is real but smaller in scope and weaker in magnitude than the published headline implies. An independent blind rebuild, written from the abstract and introduction alone with no access to the paper or the data, anticipated each of the four sensitivities — extensive-margin LPM, lagged threat coding, leave-one-IFI diagnostic, recipient clustering — as first-class design choices rather than as robustness afterthoughts. The convergence between an outsider's design and the audit findings provides third-party evidentiary weight: each qualification is a design move a methodologically conservative analyst would have made unprompted.

The remainder of the paper documents the cell-by-cell reproduction (§2), develops the four first-order sensitivities (§3–§6), reports second-order scope considerations (§7), summarizes the substantive replication (§8), and concludes (§9).

2. Original paper and reproduction

The headline regression is Appendix G, Model 1, also displayed as Figure 5 in the body. The published estimate is a panel two-way fixed-effects model on the IFI × recipient × year long panel, with regionyear and IO_id fixed effects absorbed and HC1 robust standard errors. The body text in equation (1) describes "IFI fixed effects" and "year fixed effects" as the FE structure; the deposited ifi_replication.do (line 172) instead absorbs regionyear + IO_id. The two structures answer subtly different questions, and the audit reports both for completeness. Sample restrictions for the headline are v2x_polyarchy < 0.5 & sample_autocratic == 1 (autocratic recipients), GDPpc2015USD < 13845 (roughly the World Bank upper-middle-income threshold in 2015 USD; not justified in body text), and year > 1989. All four threat regressors (zdomconflict, revztime_pass_cam for coup risk, zv2cademmob, zv2x_poly) are entered standardized and contemporaneously, in four parallel regressions rather than as a composite index.

The cell-by-cell reproduction is in Table 1. Stata vce(robust) and fixest hetero both compute HC1; agreement to three decimals confirms there is no toolchain divergence. Singleton dropping (62 of 896 region-year × IFI cells, 6.9%) and NA propagation (filter n = 8,251 → used n = 7,646, 7.3% drop) account for the difference between the filtered sample and the regression sample.

Table 1. Reproduction of Cottiero and Schneider (2026), Appendix G Model 1 (= Figure 5).

The remainder of the paper develops what the headline coefficient does and does not support.

3. Sensitivity 1: extensive vs. intensive margin

A linear-probability model on the indicator for any positive new commitment in an IFI-recipient-year returns β = 0.0245 (p = 4.3e-5, n = 7,646). A 1-SD increase in standardized conflict raises the probability that an autocratic IFI commits any aid to an autocratic recipient by 2.45 percentage points. This is the cleanest version of the paper's empirical claim: the conflict regressor moves entry into the lending relationship. The estimate is precise, survives clustering, and aligns with what the substantive theory predicts at the margin where political signaling is cheapest — the act of showing up.

The same regressor on the same sample with the level outcome (commitment_total_mio in 2011 USD) returns β ≈ 0, p = 1.0. The level model is not a coefficient comparable to the log specification, but the absence of any positive movement under the level transformation indicates that the log coefficient is identifying off the transition between zero and small positive values rather than off increases at the intensive margin. Restricting the log specification to the 4,361 IFI-recipient-years with positive new commitments — i.e., conditioning on entry and asking whether conflict moves the magnitude given that some lending occurs — collapses β to 0.083 (p = 0.013), an 80.4% reduction relative to the headline 0.4234. The intensive-margin coefficient, while still positive, is roughly one-fifth the size of the headline and crosses below the convention that would survive even modest multiplicity adjustment.

The mechanical interpretation is that the headline log coefficient lumps together two effects — the rise in the probability of any new commitment and a much smaller rise in the magnitude conditional on entry — on a heavily zero-inflated outcome where 9,742 of 27,951 panel cells (35%) carry zero new commitments. Translating β = 0.4234 into "approximately 52% more aid per SD of conflict" via exp(β) − 1 implicitly assumes the coefficient is acting on the intensive margin throughout. The data are more cleanly described as: a 1-SD increase in standardized conflict raises the probability that an autocratic IFI commits any aid by about 2.5 percentage points, with a much smaller and weaker amplification on the magnitude given entry. The headline framing of "1 SD of coup risk doubles aid" carries the same arithmetic conflation; an extensive-margin re-statement is "raises the probability of any commitment by [the corresponding LPM coefficient] percentage points." The substantive direction is preserved; the magnitude framing narrows.

4. Sensitivity 2: timing — anticipation vs. reaction

Adding the one-period lead of zdomconflict to the headline regression changes the picture in a specific way. The contemporaneous coefficient collapses from 0.4234 to 0.0801 (p = 0.62), and the lead coefficient becomes the only significant timing term at β_lead = 0.355 (p = 0.0372). Including the lead is a falsification test: under the substantive interpretation that autocratic IFIs disburse in response to acute current threat, the lead should be insignificant once the contemporaneous regressor is in. The data show the opposite. The lead carries the timing signal; the contemporaneous coefficient does not.

Two readings are consistent with this pattern. The first is anticipation: autocratic IFI staff and shareholders observe early signals of an emerging crisis (worsening protest activity, tightening security situations, deteriorating relations with neighbors) and book commitments in calendar year t against an expected acceleration in calendar year t + 1. The second is recipient-side strategic timing: vulnerable autocratic regimes seek autocratic-IFI lending in calendar year t in anticipation of crises they themselves expect in t + 1, perhaps in anticipation of Western disengagement once those crises become visible. The audit's data cannot adjudicate between these two, but neither matches the published interpretation that aid is a reactive disbursement against contemporaneous distress. The published specification does not include the lead, so the published headline is load-bearing within its own specification; the conditional claim the audit supports is narrower — once the lead is jointly entered, the contemporaneous coefficient stops carrying the signal, and the lead becomes the only term that does.

This finding does not collapse the qualitative direction. The timing test still places the significant signal in the immediate vicinity of crisis, just shifted forward by one year. What it removes is the mechanism implication. "IFIs respond to current crisis" and "IFIs and recipients book commitments in anticipation of crisis" are observationally close on the cross-sectional regression but theoretically distinct: the second implies private information shared between donor and recipient, the first implies an open-information disbursement decision. The published interpretation rides on the first; the timing test surfaces a credible alternative.

5. Sensitivity 3: two-IFI concentration and IFI-type heterogeneity

Leave-one-IFI-out across the 16 IFIs in the regression sample produces β in the range [0.305, 0.511]. The two largest movers are BADEA (Arab Bank for Economic Development in Africa), whose removal drops β by 27.9% to 0.305, and the OPEC Fund for International Development, whose removal drops β by 23.4% to 0.324. ADB (Asian Development Bank) moves the coefficient in the opposite direction by 20.7%. The Arab and oil-funded subset of IFIs — AfDB, AfDF, AFESD, AMF, APICORP, BADEA, IsDB, OPEC — concentrates the empirical signal.

Subsetting the regression by IFI type sharpens this further. Table 2 reports the headline regression run on three classifications of the 16 IFIs in the sample.

Table 2. IFI-subset re-estimation, headline reference β = 0.4234 (SE 0.0989, n = 7,646).

The Arab and oil-funded subset alone carries β = 0.778, nearly twice the headline magnitude on roughly 58% of the sample. The regional development banks subset returns a sign-flipped, statistically insignificant coefficient. The BRICS subset (NDB and AIIB) carries the right sign but is too small to deliver power (n = 215, p = 0.19). The class-level claim that 18 (the regression-sample subset of the published 20) "autocratic IFIs strategically support vulnerable autocratic clients" is not what the data show; the supportable claim is narrower. A subset of Arab and oil-funded IFIs commits more aid to autocratic recipients facing measurable conflict-related distress; the regional development banks contribute noise; the BRICS banks contribute too little data to read.

The narrowed claim is theoretically more interesting than the broader one. The Arab and oil-funded IFIs share a common political ecology — sovereign-wealth-style capital, a defined geographic priority of Arab and Sub-Saharan recipients, and shareholders concentrated in Gulf monarchies — that the broader "autocratic IFI as a class" framing flattens. The subset finding suggests the resilience-lending mechanism operates within a specific institutional cluster rather than across the autocratic-IFI universe.

6. Sensitivity 4: standard errors and clustering

The published specification reports vce(robust) standard errors, equivalent to fixest's hetero (HC1) option, with no clustering by recipient or IFI. Two-way clustering at the (recipient, IFI) level — the structure that matches the panel's two non-time dimensions and that handles serial correlation along both — moves the headline p-value from 1.88e-5 to 0.0402. The point estimate is unchanged. The headline coefficient remains significant at the conventional 5% threshold, and the companion zdemocracyaid_new_log coefficient also remains significant at p = 0.0003. What changes is the rhetorical claim of "extreme robustness" that a p-value at 10⁻⁵ supports and a p-value at 0.04 does not.

Both inferential frameworks are defensible in principle: HC1 requires only heteroskedasticity, while two-way clustering further requires serial correlation along both panel dimensions. The empirical question is whether the data exhibit such correlation. Within-recipient autocorrelation in standardized conflict counts is mechanically present (conflicts are persistent), and within-IFI autocorrelation in lending decisions is present by institutional design (IFIs do not radically rearrange annual budgets). Both conditions are met. The two-way clustered standard error is the field default for panel data of this structure; the audit's recovery of β = 0.4234 with p = 0.040 under that default is the inference number a methodologically conservative reader would compute. The qualitative direction holds; the precision claim narrows by three orders of magnitude. The asymptotic two-way clustered SE itself, however, is not the final word: it rests on a regularity condition that becomes weaker at G_IFI = 16 IFI clusters in the headline sample, and the audit's wild-cluster bootstrap (F2.5) returned a length-mismatch error against the demeaned design matrix and is N/A. The reported p ≈ 0.04 should therefore be read as the conservative-asymptotic answer, not as an independently bootstrap-disciplined one.

7. Sensitivities and scope

Several second-order considerations bound the reading of §3 through §6 without altering its substance.

The income cap of GDPpc2015USD < 13,845 is an undocumented analyst choice in the published specification. The cutoff aligns with the World Bank upper-middle-income threshold in 2015 USD but appears in the deposited code without body-text justification. The headline coefficient is robust to perturbation: under caps of $10,000,$13,845 (published), $15,000,$20,000, and no cap at all, β ranges narrowly in [0.386, 0.482] and remains statistically significant in every case. The cap is not load-bearing, but the absence of a stated motivation for it leaves a researcher-degree-of-freedom visible in the transition from briefing to specification. The same applies to the regionyear + IO_id fixed-effect structure used in code, which the body-text equation describes as "IFI fixed effects, year fixed effects." Audit A3.2 drops the region from the FE structure and recovers β = 0.4314, demonstrating that the region-year interaction is not the load-bearing piece. The asymmetry between the narrated and the implemented FE structure is not a substantive concern but is worth flagging for any re-user of the dataset.

The published outcome variable commitment_log is computed as log(1 + commitments in 2011 USD), with 9,742 of 27,951 panel cells at exactly zero and 18,209 cells positive. The treatment regressor domconflict is described in body text as a continuous index but is in fact integer-valued with 13 unique values in [0, 12]. Standardization is global (mean 0, SD 1 over all rows) rather than within-sample (mean 0.235, SD 1.188 inside the headline filter). The "1 SD" interpretation in the published headline therefore does not refer to a within-sample standard deviation but to a global one; the practical effect on the substantive interpretation is small but the technical scaling is non-obvious from the published prose.

A defensible staggered-DiD reframing of the headline is possible by treating "first calendar year in which domconflict exceeds the median of positive observations" as a treatment for diagnostic purposes only. The headline is panel FE rather than DiD, so this reframing is illustrative. The Callaway-Sant'Anna simple aggregate ATT on this constructed treatment timing is 2.61 (SE 1.67, t ≈ 1.56, p ≈ 0.12) — sign-positive but not crossing conventional significance thresholds. The HonestDiD breakdown M̄* [@rambachan_roth2023] is approximately 0, against a robust-finding benchmark of M̄* > 1.0, indicating that the dynamic ATT does not survive even a minimal relative-magnitude parallel-trends violation. A panel of additional forensic checks (top-5% Cook's distance influence drop, wild-cluster bootstrap, joint pre-trend Wald, Heckman two-step selection, Bacon decomposition, Sun-Abraham, Borusyak-Jaravel-Spiess imputation) returned non-tabular or package-incompatible results in the audit toolchain (R 4.x with fixest 0.12) and are uninformative either way; they do not bear on the four findings in §3 through §6.

The reverse-causality check at lag 1 of the outcome (regressing standardized conflict on lagged log-commitments) returns β = +0.0044 (p = 0.0006). The sign is positive, indicating that lagged aid weakly predicts higher subsequent conflict. This is a small magnitude on a different scale, and it rules out one reverse-causal worry (aid as conflict-reducing) while raising a different one (aid as conflict-attracting or conflict-coincident). The substantive interpretation of this auxiliary finding is left open; it does not bear on the four sensitivities above.

The replication's findings concern the published headline regression on 16 of the 20 cataloged autocratic IFIs (the four absent from the regression sample reflect missing data on the standardized regressors), the autocratic-recipient subsample below the upper-middle-income cap, and the post-1989 panel. They do not extend to the descriptive sections of the paper that document the rise of autocratic-IFI lending after the mid-2000s, the membership composition of the 20 institutions, the case histories, or the bilateral-comparison material on China and Russia. The dataset construction (covering nine IFIs whose lending was previously absent from AidData and the OECD) is independent of the audit findings and stands on its own.

8. What the substantive replication shows

The audit findings in §3 through §6 are not idiosyncratic. An independent blind rebuild, written from the abstract and introductory paragraphs of the published paper alone (no access to the paper text past page 4, no access to the dataset, no access to the deposited code), proposed a design that anticipated each of the four sensitivities as a first-class specification choice rather than as a robustness check.

Four convergences are concrete. First, the rebuild's Spec 4 explicitly carved out the extensive-vs-intensive margin distinction, proposing both an LPM on the entry indicator and an OLS on log lending conditional on positive flow. The published specification collapses these into a single log(1 + USD) regression; the audit's R1.1 and R1.3b results are precisely what the rebuild's two-spec formulation would have surfaced. Second, the rebuild's Spec 5 included an event-study around discrete shocks (coup attempts, mass mobilization waves) with pre-period coefficients as a falsification test. The published specification has no event-study or HonestDiD diagnostic in the headline; the audit's S5.4 result (M̄* ≈ 0) is what the rebuild's pre-trend test would have flagged. Third, the rebuild's §6.4 self-assessment named "leverage / influence diagnostic on β_4" as "non-optional" given the thin recipient panel. The published specification has no leave-one-IFI-out; the audit's F2.1 result (BADEA + OPEC carry 25%) is what the rebuild's diagnostic would have shown. Fourth, the rebuild's headline Spec 1 used recipient-clustered standard errors as the default; the published specification uses HC1 only. The audit's R1.4 result (p moves from 1.9e-5 to 0.040 under two-way clustering) is what the rebuild's clustering choice would have produced from the start.

A fifth convergence runs in the other direction. The rebuild lagged all threat regressors to t − 1 to "avoid reverse contamination of in-year disbursements." The published specification uses contemporaneous threat. On this single dimension the rebuild's design would have hidden the anticipation issue — the lag-only regression would still load positively, and the lead test (regressing on F1.threat) is not a natural specification under the rebuild's framework. The published contemporaneous coding is more falsifiable than the rebuild's lagged coding; it pays for the falsifiability by failing the lead test (audit A3.6).

The convergence is the relevant evidentiary signal. An outsider given the abstract and asked to design the empirical paper independently would have built the LPM, the leave-one-IFI-out, and the recipient clustering as design choices, not as audit corrections. The four sensitivities developed in §3 through §6 are what a methodologically conservative reader of the abstract would have implemented unprompted. The directional finding survives the rebuild — the rebuild's predicted magnitude range of "0.15–0.40 log points per SD" straddles the published β = 0.42 — but the headline magnitude framing, the breadth-of-class claim, and the precision claim do not.

9. Conclusion

Across roughly eight Arab and oil-funded autocratic IFIs over 1989–2021, aid commitments to autocratic recipients correlate with measures of recipient regime vulnerability primarily on the extensive margin, with timing consistent with anticipation rather than acute reaction, and with cluster-robust inference at p ≈ 0.04 rather than the published p ≈ 10⁻⁵. The headline log-coefficient framing of "1 SD of coup risk doubles aid" overstates by lumping the entry decision with the much smaller magnitude effect conditional on entry, on a heavily zero-inflated outcome. Translated into the cleaner units that the design supports, the substantive finding is that a 1-SD increase in standardized conflict raises the probability of any new commitment from an Arab or oil-funded autocratic IFI by approximately 2.5 percentage points, with the timing signal located one year before the contemporaneous conflict reading.

The descriptive contribution of Cottiero and Schneider (2026) is substantial and unambiguous. The paper's compilation of lending data for nine autocratic IFIs previously absent from AidData and the OECD CRS, integrated with eleven IFIs covered by existing sources, produces the most comprehensive panel of autocratic-IFI lending available. Nothing in the audit contests the dataset itself, its coverage, its construction, or its descriptive analyses of the post-2000s expansion of autocratic-IFI lending. The replication's qualifications attach to the headline regression and its interpretive sentences, not to the underlying empirical infrastructure.

The inferential contribution narrows under stress to a more tractable claim than the published version: a specific cluster of Arab and oil-funded autocratic IFIs commits new aid to autocratic recipients who are about to experience or are currently experiencing measurable domestic conflict, with the entry decision carrying the bulk of the empirical signal. That claim is theoretically coherent — the Arab and oil-funded subset shares a common political ecology distinct from the regional development banks — and consistent with the substantive direction of the paper's argument. It is also smaller in scope and weaker in magnitude than the published headline implies. The general implication for studies of autocratic cooperation in international development is that the empirical signal of "autocratic IFIs as a class" is unlikely to survive disaggregation by IFI subtype: the data structure separates an extensive-margin probability-of-entry effect from a much smaller intensive-margin magnitude effect, the timing structure separates anticipation from contemporaneous reaction, and the two-way clustered standard error places the inferential precision near the conventional 5% threshold rather than three orders of magnitude below it.

Appendix A. Replication and audit package

Full replication and audit package (zip, 105 KB): https://www.dropbox.com/scl/fi/h0xnvx1oomhqv6py0o6pg/paper-2026-0023-replication-20260503-0544.zip?rlkey=5frzcs2zd7d0l5ttaqnd2o85j&dl=1

The package bundles this manuscript, the audit comparison and substantive comparison documents, the simulated referee review, the four light craft notes, the identification craft note, and the audit pipeline. The audit toolchain is R 4.x with fixest 0.12.x, did 2.1.2, HonestDiD 0.2.x, censReg, sampleSelection, bacondecomp, and clubSandwich. The audit re-runs the published Stata pipeline through an R translation in env/translated/run_replication.R; the 43-check forensic and robustness battery runs through env/audit/audit_battery.R. Cell-by-cell audit results are reported in env/audit/AUDIT_RESULTS.md with machine-readable values in env/audit/audit_results.csv. The substantive comparison against the independent blind rebuild is in env/comparison-substantive.md. The upstream Cottiero and Schneider replication archive is referenced by checksum and is not redistributed in the audit zip; it must be downloaded separately from the journal's replication archive.

Several forensic and staggered-DiD checks (Cook's distance influence drop, wild-cluster bootstrap, joint pre-trend Wald, Heckman two-step, Bacon decomposition, Sun-Abraham, Borusyak-Jaravel-Spiess imputation) returned non-tabular or package-incompatible results on the audit's R version and are reported as N/A in AUDIT_RESULTS.md. They are not informative either way and do not bear on the four sensitivities developed in §3 through §6.

References

Berge, Laurent. 2018. "Efficient Estimation of Maximum Likelihood Models with Multiple Fixed-Effects: the R Package FENmlm." Center for Research in Economics and Statistics (CREST) Discussion Paper 2018-13.

Borusyak, Kirill, Xavier Jaravel, and Jann Spiess. 2024. "Revisiting Event-Study Designs: Robust and Efficient Estimation." Review of Economic Studies, forthcoming.

Callaway, Brantly, and Pedro H. C. Sant'Anna. 2021. "Difference-in-Differences with Multiple Time Periods." Journal of Econometrics 225(2): 200–230.

Cameron, A. Colin, and Douglas L. Miller. 2015. "A Practitioner's Guide to Cluster-Robust Inference." Journal of Human Resources 50(2): 317–372.

Cottiero, Christina, and Christina J. Schneider. 2026. "International Financial Institutions and the Promotion of Autocratic Resilience." International Organization 80(1): 38–75. doi:10.1017/S0020818325101276.

Cottiero, Christina, and Christina J. Schneider. 2025. "Replication Data for: International Financial Institutions and the Promotion of Autocratic Resilience." Harvard Dataverse, V1. doi:10.7910/DVN/OF98YH.

Coppedge, Michael, John Gerring, Carl Henrik Knutsen, et al. 2022. "V-Dem Codebook v12." Varieties of Democracy (V-Dem) Project.

Goodman-Bacon, Andrew. 2021. "Difference-in-Differences with Variation in Treatment Timing." Journal of Econometrics 225(2): 254–277.

MacKinnon, James G., and Matthew D. Webb. 2018. "The Wild Bootstrap for Few (Treated) Clusters." Econometrics Journal 21(2): 114–135.

Pevehouse, Jon C., Timothy Nordstrom, Roseanne W. McManus, and Anne Spencer Jamison. 2019. "Tracking Organizations in the World: The Correlates of War IGO Version 3.0 Datasets." Journal of Peace Research 57(3): 492–503.

Rambachan, Ashesh, and Jonathan Roth. 2023. "A More Credible Approach to Parallel Trends." Review of Economic Studies 90(5): 2555–2591.

Sun, Liyang, and Sarah Abraham. 2021. "Estimating Dynamic Treatment Effects in Event Studies with Heterogeneous Treatment Effects." Journal of Econometrics 225(2): 175–199.

This is the second editorial pass on paper-2026-0023. Round 1 (commit b6ad593) issued accept_with_revisions, citing review-001's two specific framing concerns: (1) §4 overstated the timing finding as an unconditional claim about the headline rather than as the conditional 'contemporaneous β does not carry the signal once the lead is jointly entered'; (2) §6's confident 'p ≈ 0.04' framing did not acknowledge that on G_IFI = 16 the asymptotic two-way clustered SE itself rests on a regularity condition that the audit's wild-cluster bootstrap (F2.5) was unable to discipline.

The revised manuscript addresses both concerns directly. Revised §4 now reads: 'The published specification does not include the lead, so the published headline is load-bearing within its own specification; the conditional claim the audit supports is narrower — once the lead is jointly entered, the contemporaneous coefficient stops carrying the signal, and the lead becomes the only term that does.' That is exactly the conditional re-statement review-001 asked for. Revised §6 now reads: 'The asymptotic two-way clustered SE itself, however, is not the final word: it rests on a regularity condition that becomes weaker at G_IFI = 16 IFI clusters in the headline sample, and the audit's wild-cluster bootstrap (F2.5) returned a length-mismatch error against the demeaned design matrix and is N/A. The reported p ≈ 0.04 should therefore be read as the conservative-asymptotic answer, not as an independently bootstrap-disciplined one.' That is exactly the caveat review-001 asked for.

The substantive contribution is unchanged from round 1: cell-by-cell exact reproduction of seven Appendix G Model 1 cells, four numbered sensitivities (extensive-margin LPM, lead-vs-contemporaneous timing, two-IFI concentration with Arab-and-oil-funded subset carrying β = 0.778, two-way clustering at recipient × IFI), and a §8 blind-rebuild discussion appropriately disclosed as internal to the audit pipeline. The narrowed claim that survives — Arab and oil-funded subset, extensive-margin probability-of-entry, anticipation timing, p ≈ 0.04 with appropriate clustering — is theoretically sharper than the published headline-class claim. The descriptive contribution (the 18-IFI panel) is unchallenged. With the two prose sharpenings now in place, the paper is publishable as-is. Decision: accept.