Sebastián Bustos, Dina Pomeranz, Juan Carlos Suárez Serrato, José Vila-Belda, Gabriel Zucman · NBER WP 30114 (2022); forthcoming, American Economic Journal: Economic Policy (per author website)

The Race Between Tax Enforcement and Tax Planning: Evidence From a Natural Experiment in Chile

19 problems found: 2 major · 9 moderate · 8 minor

What the paper claims

Before the reform, multinationals' intra-group payments (royalties, services, interest) were tax-motivated: payments to affiliates, relative to non-affiliates in the same country, rise as the destination tax rate falls.
The reform did not reduce the tax sensitivity of intra-group payments; 'estimates reject any substantial reduction in tax sensitivity post-reform'.
No reduction in the tax sensitivity of likely intra-group trade in goods (payments, quantities, unit prices).
The reform did not significantly raise multinationals' corporate income tax payments relative to internationally active domestic firms.
The reform triggered a drastic, transfer-pricing-specific boom in tax consulting.
Multinationals consolidated cost centres (a planning strategy described by interviewees): fewer countries receive intra-group payments, from non-havens.
Interpretation: the reform 'did not succeed at reducing profit shifting'; 'in the race between tax enforcement and tax planning, tax planning won'; enforcement circumvented by sophisticated planning 'can benefit tax consultants at the expense of tax authorities and taxpayers'; such reforms 'are generally vulnerable'.

Every problem found

1majorconfirmed · newly identified here · overclaiming

The study finds no clear rise in multinationals' tax payments, but its measurement is too imprecise to rule out a sizeable rise, perhaps enough to recover about half of the tax the paper says Chile was losing. 'We could not detect an effect' is not the same as 'there was no effect'.

Technical detail and evidence

Why it matters, in detail. With the paper's raw-unit normalization (coefficient/0.146) the SE is 4.8-5.6% of the mean; 95% upper bounds are 9.3-11.6% (12.3% with audit receipts), i.e. 46-58% (62%) of a 20% MNE-CIT gap (12%/0.60), or 54-68% if the MNE share is 70%. The MDE at alpha = 0.05 and 80% power (2.80 x SE) is 13.5-15.7%. If TWZ overstate Chile's loss (disputed in the corpus), the test is even less able to separate an effective from an ineffective reform. In dollars, 10% of sample MNE CIT (about $1.16bn in 2010 = 2,755 x $420k) is about $115m a year, far above the enforcement cost and the $13.6m a year of TP audit receipts.

Evidence. Table A.2 p. 49 (coefficients -0.00027/0.00084/0.00085, SE 0.00704/0.00738/0.00820, mean 0.146 printed on a shifted row); Table A.4 p. 51; pp. 3, 20, 27 and fn 3; June 2022 pp. 3-4, 25-26, Table 5 p. 49 and fn 39. Adjudicator recomputation (scripts/adjudicator_checks.py, section A): 95% CIs [-9.6%, +9.3%], [-9.3%, +10.5%], [-10.4%, +11.6%]; 90% upper bounds +7.8/+8.9/+9.8%; with audits up to +12.3%; common support on assets (B.39) up to +16.1%. Units check: Fig. A.4 estimate (1) has a 90% half-width of about 0.0385 SD, so Table A.2's SE of 0.00704 implies an outcome SD of about 0.30 (Table 1: 0.33-0.40), confirming the raw-unit reading used in the paper's own % conversion. 2022 statement: the correct 95% upper bounds with the printed mean of 0.15 are 9.0-11.3% (45-56% of the gap), not 7.5-8.9% (44%).

Why this severity. The literal claim (no statistically significant increase) is correct, but the stronger conclusions (reform ineffective, did not succeed, no revenue gain) are not shown: effects up to about half of the revenue loss the paper itself uses as a benchmark lie inside the 95% CI. This materially changes what the headline null rules out, without reversing its direction.

The authors' response. The June 2022 version (pp. 25-26) argued that the 95% CI 'rules out effects that closed more than 44%' of the gap, using mis-scaled bounds; the statement was removed from 2023 on. The current version relies on the consistency of near-zero point estimates across windows, subgroups (Fig. A.4) and robustness tables (A.4, B.38-B.40).

2majorconfirmed · newly identified here · overclaiming

The paper's strongest evidence that the reform did nothing compares how readily firms paid their related companies in low-tax countries before and after the reform, and it is precise only when it counts whether payments happen at all. When it weighs how much money moves, which is what matters for tax, the data cannot tell a reform that worked from one that did not. The paper also does not report whether the total amount paid to related companies abroad fell.

Technical detail and evidence

Why it matters, in detail. About 80% of firm-country-affiliation-year cells are zero (LPM mean 0.198), so the log(Y+1) estimates mainly measure the extensive margin; dollar amounts, which determine revenue, are tested only by PPML/levels, where the design has essentially no power (insignificant baseline, CIs spanning full elimination). B.20 absorbs firm-year-specific affiliate shocks, including the consolidation the paper documents, and there the point estimates move toward a reduction. The unreported beta6 (intra-group x post level) and the 36% fall in affiliate-payment destinations (Table 5) imply an extensive-margin change in intra-group payments that could be consolidation or reduced base erosion. The slope test cannot tell these apart.

Evidence. Table 3 p. 39; Tables B.20 p. 90, B.23 p. 93, B.24-B.26 pp. 94-96, B.27 p. 97, B.28 p. 98, B.29 p. 99; Appendix E pp. 131-132; Eq. 3 p. 16; Table 5 p. 41. May 2023 fn 37 (reductions to -0.033/-0.034 not rejected in Panels B/C) was removed in 2025-26. Adjudicator recomputation (scripts/adjudicator_checks.py, section B): largest reduction not rejected = (b3 + 1.96 se)/|b2| = baseline 13/29/21%; B.24 25-32%; B.26 35-53%; B.29 11-26%; B.23 31-54%; B.20 50-63%; B.27 115-154%; B.28 141-242%.

Why this severity. The qualitative 'no detectable reduction' survives everywhere (point estimates are at or below zero except small positives in B.20 and one panel of B.28). But the claimed precision, which is the paper's main evidence that the reform was ineffective rather than merely undetected, depends on the outcome transformation and fixed effects. Within defensible alternatives, the largest reduction that cannot be ruled out grows from about 13-29% to 50-63%, or to complete elimination.

The authors' response. Appendix E (pp. 131-132) reports these tables and summarises them as supporting no meaningful decrease. It describes PPML as showing 'if anything ... a - not statistically significant - increase in the sensitivity' and the sales-scaled estimates as 'attenuated towards zero'.

3moderateconfirmed · previously known · methodology

The paper's headline number for how strongly payments respond to tax rates shrinks by 60% simply by counting money in thousands of dollars instead of dollars, so it should not be read as 'payments are 5% higher'. The evidence that firms favour low-tax affiliates concerns mainly whether payments are made at all. And a check the paper relies on, that payments to unrelated firms do not respond to tax rates, fails for services.

Technical detail and evidence

Why it matters, in detail. beta_USD is approximately beta_kUSD + ln(1000) x beta_LPM. The robust, interpretable statement is that a 1 pp lower destination rate raises the probability of a positive affiliate payment by about 0.43 pp (2.2% of the 0.198 mean). Removing cross-pair variation roughly doubles the SE of the premise slope (0.011-0.013 to 0.023-0.026), so most precision comes from cross-country comparisons, which are more exposed to country-level confounding and to the clustering problem in F6.

Evidence. pp. 15-16; Table 2 p. 38; B.7 p. 77; B.8 p. 78; B.11-B.12 pp. 81-82; B.23 p. 93; B.24 and B.29. Adjudicator check of the Chen-Roth decomposition in the published numbers: -0.019 + ln(1000) x (-0.00433) = -0.0489, against the published USD coefficient of -0.049 (scripts/adjudicator_checks.py, section C).

Why this severity. The sign of the affiliate/non-affiliate differential is robust in log and extensive-margin specifications, so the premise survives qualitatively. But its quoted magnitude has no unit-free meaning, it is not established in dollar terms, and for services the placebo argument offered in its support is incorrect.

The authors' response. fn 33 and Appendix E cite Chen & Roth and report rescaled, calibrated, PPML, sales-scaled, LPM and IHS versions; fn 34 (2026) notes that both cross-sectional and temporal variation identify the coefficients.

4moderateconfirmed · newly identified here · overclaiming

The paper checks several routes firms could use to move profits, but some are not observed at all (money coming into Chile), and the goods check covers only about a tenth to a sixth of multinationals' trade, using affiliation defined from data collected after the reform.

Technical detail and evidence

Why it matters, in detail. Classifying pairs by post-treatment trade shares is valid only if affiliation is stable. Any reform-induced switching or exit is either misclassified in the pre-period or dropped from a positive-trade sample. Narrower bands (B.35-B.36) address measurement noise but not this selection, and inbound under-pricing is untested by design.

Evidence. pp. 1-3, 12 fn 24, 17-19, 117, 133 and fn 75; Table 4 p. 40 vs November 2025 Table 4 and May 2023 Table 4 p. 55; Appendix D quote on centralised sourcing (p. 128).

Why this severity. Goods is a secondary channel and the CIT regression in principle captures all channels, so this mainly limits the 'comprehensive' framing. No bias of known sign or size is shown.

The authors' response. The introduction calls the goods analysis 'a subset of transactions' (p. 2); fn 24 notes the missing inbound data; bandwidth, product-group and tax-source robustness checks are reported (Tables B.33-B.37).

5moderateconfirmed · previously known · external inconsistency

Several other careful studies find that rules like Chile's do reduce profit shifting and raise revenue. The paper's broad conclusion that such rules generally fail does not discuss them, and its own data cannot rule out effects as large as theirs.

Technical detail and evidence

Why it matters, in detail. Earlier quasi-experimental estimates imply roughly 50-60% reductions in shifting from documentation rules (Lohse & Riedel; Beer & Loeprick). This paper's CIs in dollar-weighted or saturated specifications do not exclude reductions of that size (F1-F2), so the divergence is plausibly about power and context rather than a contradiction.

Evidence. Conclusion p. 27; literature p. 4; June 2022 p. 4 and May 2023 p. 5 (Lohse & Riedel). Abstracts verified: Oxford CBT WP 13/07 page; WU/SSRN record of Beer & Loeprick; Muenster publication page of Knoll et al.; OpenAlex record of Laudage Teles et al. (OpenAlex also lists it as citing this paper).

Why this severity. This does not affect the Chilean estimates. But the paper's general policy conclusion conflicts with several published causal studies that it does not address, and the qualitative evidence offered for generality comes from one country.

6moderatelikely · newly identified here · overclaiming

The paper shows that consultants boomed and that taxes did not visibly rise, but it cannot show that the consultants are why taxes did not rise. Other explanations fit the same facts: the reform had little real bite, or it worked a little but too little to measure.

Technical detail and evidence

Why it matters, in detail. There is no mediation estimate, no variation in consultant exposure, and no fee or compliance-cost data. The model's comparative statics (dN^C/dF1 > 0, dN^C/dF2 < 0) fit the consultant boom but do not discriminate an offset from a reform without bite. A 1% undetectable CIT effect (about $12m a year on about $1.16bn of sample MNE CIT) is of the same order as total TP audit receipts ($13.6m a year in 2011-15).

Evidence. Abstract; pp. 1-2, 11 (model), 13 fn 26, 22 fn 49, 26-27; fn 23 p. 10; Appendix D pp. 120-128; Table C.1 p. 120; Table B.20 p. 90; June 2022 intro p. 2 ('decreased overall welfare', later removed); the May 2023 conclusion's 'shows that such reforms are generally vulnerable' became 'suggests' in 2026.

Why this severity. The descriptive findings (null point estimates, consultant boom) are unaffected. But the causal story behind the paper's title and policy message rests on interviews and a stylised model rather than identified evidence. This qualifies the central interpretation without overturning it.

The authors' response. fn 26 acknowledges that consultant use cannot be linked to tax records; the abstract frames the lesson as an illustration ('can benefit'). The 2022 claim that the reform 'decreased overall welfare' was removed, and the conclusion's 'shows' became 'suggests'.

7moderatelikely · newly identified here · overclaiming

After the reform, firms paid their foreign affiliates in fewer countries. The paper reads this as consultants helping firms route costs through tax-favourable places. But the change started before the consultants arrived, and it could equally mean that firms stopped dubious internal charges, which would be a sign the reform worked.

Technical detail and evidence

Why it matters, in detail. Up to 2013, before the DJ1912 switch, the decline is -0.292/1.050 = -28%; up to 2015 it is -36% (95% CI -50% to -22%). Without payment amounts or the tax rates of dropped destinations, a fall in counts fits (a) concentration in lower-tax hubs (planning), (b) dropping small, hard-to-document charges (compliance), or (c) less base erosion. The 2011 timing is easier to reconcile with anticipation or compliance reorganisation than with consultant up-selling.

Evidence. Table 5 p. 41; Fig. 6 p. 35 (adjudicator visual reading); Table C.1 p. 120; Appendix D pp. 125-128 (quotes, incl. 'such as the United States, Mexico, or the Netherlands' p. 128); SII DJ1907 instructions AT2013 (one record per operation type and related counterparty); SII Oficio 1599/2018 (Art. 41 F from 1 Jan 2015); SII Circular 65/2015 (from 30 Sep 2015); June 2022 Table 6 p. 50. scripts/adjudicator_checks.py section D.

Why this severity. The consolidation pattern is a robust feature of the data (services -47%). But its reading as consultant-driven tax planning, the paper's only quantitative link between the interviews and the tax data, is not supported over equally plausible alternatives, one of which (reduced intra-group charging) cuts against the paper's conclusion.

The authors' response. p. 21 notes that centralisation is 'optimal both from a tax efficiency and business perspective'; the concentration in services matches the interviews; the authors attribute the pattern to tax-planning advice (pp. 4, 24-25, 27).

8moderatelikely · newly identified here · methodology

The paper says the law was debated in 2011, but the official record shows the bill reached Congress in 2012 and took effect in late 2012, so some of the 'after' years are really 'before' years. Chile also raised its corporate tax rate in those years, which gave multinationals an extra reason to move profits abroad and could hide a modest effect of the reform.

Technical detail and evidence

Why it matters, in detail. Misdating Post dilutes the pooled beta3 and the CIT DiD roughly in proportion to the share of untreated post-reform years. The rate confound biases the MNE-vs-domestic CIT DiD downward by about 0.8 x the average rate change (2.4-3.0% of the mean across windows); corrected point estimates would be about +2% to +3.5%, still insignificant. The Law 20.780 measures would, if anything, raise 2015 enforcement, but they confound the 2015 consolidation path (F4).

Evidence. p. 7 and fn 15; Historia de la Ley No. 20.630, BCN, p. 4: 'Mensaje ... Fecha 02 de agosto, 2012' (downloaded to /mnt/zdata/downloads/bpsvz-adjudicator-src/bcn_hl20630.pdf); BioBioChile, 30 Apr 2012 (cached by Auditor A); SII Circular 29/2013 section III ('rigen a contar del 27 de septiembre de 2012'); SII Oficio 1599/2018 (Art. 41 F from 1 Jan 2015); SII Circular 65/2015 (from 30 Sep 2015); SII Oficio 3106/2016 (Art. 41 G from 1 Jan 2016); Tax Foundation rate series (scripts/tf_rates_check.py).

Why this severity. Year-by-year event studies (Figs. 1-3) show no effect in 2013-2015 either, which limits the damage from the misdating. The rate-change confound is a few percent of MNE CIT: within the CI, but large relative to the point estimates.

The authors' response. The timeline on p. 7 (2011 debate and new SII unit; 2012 law; 2013 first filing); fn 15 and Tables B.1/B.17 (rate differences) for Chilean rate changes in the intra-firm design; event-study figures.

9moderateplausible · newly identified here · methodology

The paper treats each firm as a separate piece of evidence, but the tax rates being compared differ only across countries, and many firms pay into the same few countries. The results probably look more precise than they are, which would make both the finding that firms shift profits and the finding that the reform did nothing less certain.

Technical detail and evidence

Why it matters, in detail. With a regressor constant within country-year and residuals positively correlated across firms within country x affiliation, firm-clustered SEs are biased downward by roughly the Moulton factor sqrt(1 + (m-1) rho_x rho_e). Wider SEs would lower the premise t-statistics (about 4.6 in Table 2) and widen the beta3 interval beyond +/-0.02. The magnitude cannot be computed without the data.

Evidence. Notes to Tables 2-5 and A.2 ('Standard errors clustered at the firm level'); p. 15; Tables B.7 and B.23 (SE of the premise slope 0.023-0.026 vs 0.011-0.013 in the baseline); fn 30 (tax changes in 60 of 91 countries). The adjudicator simulation (scripts/fe_identity_check.py) shows that absorbing common country-year shocks does not move the point estimates, which says nothing about error correlation across firms. Standard references: Moulton (1990, REStat); Cameron & Miller (2015, JHR); Abadie, Athey, Imbens & Wooldridge (2023, QJE).

Why this severity. Allowing for country-level dependence would most likely widen the confidence intervals. That would make the tax-motivated-payments premise less certain and the reform null even less informative. It would not create a positive reform effect.

10moderateplausible · newly identified here · methodology

The tax test gives a small firm the same weight as a giant one and trims the most extreme values, whereas government revenue depends mostly on a few very large companies. A change in what those big firms pay could be hidden in this average.

Technical detail and evidence

Why it matters, in detail. A mean-of-ratios estimand is not a ratio of means or an aggregate. With revenue skewed toward a few large payers (e.g. mining) and the outcome capped at p99, an effect concentrated among large payers could be diluted or missed. A revenue-weighted DiD, or PPML on tax levels with a payroll offset, would be needed to bridge to TWZ's aggregate benchmark (F1).

Evidence. Eq. 5 p. 19; Table 1 p. 37; Table A.2 p. 49; Table A.4 p. 51; Fig. A.4 p. 46 (primary-sector subgroup about -0.08 SD, 90% CI about -0.24 to +0.08); Appendix C pp. 117-118.

Why this severity. The direction is unknown and this does not show the null to be wrong. But the statement that the reform was 'ineffective at raising additional tax revenue' is not directly tested by an unweighted ratio regression.

The authors' response. Scaling by payroll with pre-period characteristics x year follows Yagan (2015); subgroup (Fig. A.4), common-support (B.38-B.39) and lagged-payroll (B.40) checks show no effect.

11moderatespeculative · newly identified here · speculative assumption

Chile taxed company profits less than most of the countries its firms pay, so the pattern the paper measures may partly reflect profits being kept in Chile rather than moved out, which Chile's tax authority would not try to stop. The paper does not check which of the two is happening.

Technical detail and evidence

Why it matters, in detail. Heterogeneity by the sign of (t_Chile - t_j) is untested. Tables B.1/B.17 replace the destination rate by the destination-minus-Chile difference, a shift common to all destinations in a year: B.17 is algebraically identical to Table 3 in the window ending 2013, and neither can detect asymmetry. Mismeasured effective rates (special regimes, withholding, integration) add attenuation of unknown size.

Evidence. p. 7; model p. 11; May 2023 fn 15; Tax Foundation 1980-2023 file (scripts/tf_rates_check.py: 24% of 179 jurisdictions strictly below 17% in 2010; partner rates as listed); SII DJ1850/DJ1912 instructions (Additional Tax withholding on outbound payments).

Why this severity. If most of the identifying variation came from destinations taxed above Chile, the reform test would measure a margin Chilean enforcement does not target, weakening the interpretation of C2. There is no direct evidence on this, and the 35% integrated rate makes outward shifting the more plausible reading for foreign-owned subsidiaries.

The authors' response. p. 7: 'Multinationals have incentives to shift profits out of Chile, even though it is not a high-tax country, because its corporate taxes are still higher than in many low-tax countries.' Tables B.1/B.17 use destination-minus-Chile rate differences.

12minorconfirmed · newly identified here · misrepresentation of source

A figure the paper credits to another study was in fact calculated by the authors, using a share they attribute to a government statistics page that does not contain it. The arithmetic is reasonable, but readers cannot check it.

Technical detail and evidence

Why it matters, in detail. The 60% denominator scales the share-of-gap reading in F1. With a 70% MNE share the gap is 17%, and the 95% upper bounds cover 54-68% of it rather than 46-58%.

Evidence. pp. 3, 7, 20; references p. 30; TWZ (2023) REStud 90(3), Table 3, Chile row 68/58/10/5/2.3/8/12 (read in /mnt/zdata/downloads/twz2023-replication/TWZ2023Restud-final.pdf); June 2022 pp. 3-4 and fn 39 p. 25.

Why this severity. The benchmark arithmetic is sensible if the 60% share is right; the problem is attribution and verifiability, not the estimates.

The authors' response. June 2022 fn 39 explained the 12%/60% derivation; it is not repeated in later versions.

13minorconfirmed · newly identified here · version instability

Several numbers changed between drafts without explanation. Most notably, the money recovered by transfer-pricing audits dropped by two-thirds, and the fall in the number of countries receiving payments grew from 23% to 36%. The main estimates did not change.

Technical detail and evidence

Why it matters, in detail. The audit-receipts revision (-67%) bears on the welfare claim. $204m over 2011-15 would be about $41m a year (about 3.5% of sample MNE CIT), against $13.6m a year after revision; with the revised figure, annual post-reform TP audit receipts are below the 2010 level ($17.2m). The consolidation effect rose by half (23% to 36%) after a sample redefinition.

Evidence. June 2022 Table 5 p. 49, pp. 25-26, Table 6 p. 50, Table A12 p. 72; May 2023 fn 37 p. 25, fn 40 p. 27, Table 4 p. 55, Table 6 p. 57; November 2025 Table 4 and p. 17; January 2026 Tables A.2, A.4, 4 and 5, p. 17, p. 118; Bustos, Pomeranz, Vila-Belda & Zucman (2019) AEA P&P 109: 500-505, p. 503. scripts/adjudicator_checks.py section A.

Why this severity. The current version's arithmetic is correct and the core coefficients are stable across versions. The changes affect secondary magnitudes (consolidation, audit receipts) and the paper's own statement of what the CIT null rules out.

The authors' response. From 2023 the audit statistics are described as covering 'firms in our sample', and Appendix C (p. 118) describes the 856-firm balanced consolidation sample; no reconciliation with earlier versions is given.

14minorconfirmed · newly identified here · internal inconsistency

Several tables have shifted or wrong labels, one appendix figure is a copy of another, and one table repeats another. Readers can work out the intended numbers, and none of these mistakes changes the results.

Technical detail and evidence

Why it matters, in detail. Taken literally, the SD-unit label would shrink the CIT CI to about +/-3-4% of the mean (1.96 x 0.0082 x SD of 0.30-0.40, divided by 0.146), so the mislabel matters to anyone re-deriving power (F1). The raw-unit reading is the one consistent with the paper's own % conversions and with Fig. A.4.

Evidence. Adjudicator renders of printed pp. 34-35, 46-49; Table C.1 p. 120; Tables B.8-B.17, B.29, B.32; Table 5 p. 41; scripts/measure_fig5.py (pixel reading of Fig. 5) and scripts/adjudicator_checks.py (section D).

Why this severity. These are presentation errors: the intended values can be reconstructed from neighbouring tables and text, and none changes an estimate.

15minorconfirmed · newly identified here · selective presentation

Some of the paper's checks could not have come out differently by construction, so they add no evidence. They are not wrong, just empty.

Technical detail and evidence

Why it matters, in detail. By Frisch-Waugh-Lovell: for the residualised T x G regressor x-tilde, the sum over g of x-tilde_ijgt is 0 for each (i,j,t). So Z'x-tilde = 0, and the within-cluster scores are unchanged, for any FE matrix Z that is symmetric in g.

Evidence. Tables 2, 3, B.1, B.5, B.6, B.17, B.21, B.22; fn 33; Appendix E p. 130. The adjudicator simulation (scripts/fe_identity_check.py) gives coefficients and CR0 firm-clustered SEs identical to six decimals with country x year or firm x country FE, and different ones with firm x year x group or firm x country x group FE, replicating Auditor A's simulation.

Why this severity. These checks are harmless but uninformative. They overstate the breadth of the robustness evidence without affecting any estimate; the informative FE variants (B.4/B.20, B.7/B.23) are discussed in F2 and F5.

16minorconfirmed · newly identified here · internal inconsistency

The 'seven-fold in three years' figure actually took four years; after three years the rise was closer to six-fold. The boom is real either way.

Technical detail and evidence

Why it matters, in detail. The 2015 multiple is 7.18x against 5.68x in 2014 (-21%); the interview ratio of 11.9x mixes 2014 and 2015 endpoints.

Evidence. pp. 3 and 21; Fig. 4 notes p. 34; Table C.1 p. 120; scripts/adjudicator_checks.py section E.

Why this severity. The boom is large under any dating (4.7x by 2013, 5.7x by 2014, 7.2x by 2015, against +30-47% for the comparison groups); only the headline speed is overstated. Auditor B rated this moderate; adjudicated minor.

The authors' response. The Figure 4 notes disclose the years actually used; the law entered into force in 2012, which would make 2015 'three years after' the law.

17minorconfirmed · newly identified here · documentation gap

In 2014 the tax form the study relies on changed how it records whether a payment goes to a related company, and the paper says it did not. The main results look the same using earlier years only, so this is mostly a problem for anyone trying to redo the work.

Technical detail and evidence

Why it matters, in detail. A mapping that treated the contractual codes as 'affiliate' before 2014 would mechanically reclassify some counterparties as non-affiliates from 2014, affecting the estimates for windows ending 2014/2015 and the 2014-15 consolidation path. No clean 2014 break is visible in Fig. 6.

Evidence. Appendix C pp. 112-117; SII DJ1850 instructions (AT2012, read by the adjudicator; AT2008-AT2013, read by Auditor A); DJ1912 instructions (Res. Ex. 25/2015, anexo 2, 'Codigo Tipo de Relacion'); DJ1907 instructions AT2013 (obligated filers a-c).

Why this severity. The windows ending 2013 precede DJ1912 and give the same results (Table 3 Panel A; Table 5 Panel A, -28%), so a coding break cannot drive the core nulls; the gap matters mainly for replication. Auditor A rated this moderate; adjudicated minor.

18minorconfirmed · newly identified here · arithmetic or transcription

Small wording and factual mistakes that a careful edit would fix; they do not change the findings.

Technical detail and evidence

Why it matters, in detail. Wording and labelling only; the one quantitative slip (26% vs about 10.5% of EBIT) overstates the scale of outbound payments in a descriptive statistic not used in the estimates.

Evidence. Pages as listed; TI CPI 2012 results PDF ('176 countries/territories'; Chile 20th, score 72); SII Oficio 3106/2016 (Art. 41 G 'vigente a partir del 1 de enero de 2016'); scripts/adjudicator_checks.py section F.

Why this severity. None of these affects an estimate or a conclusion.

19minorplausible · newly identified here · methodology

Which firms count as multinationals, and which firms are studied at all, was partly decided using information from after the reform, which can slightly distort before-and-after comparisons.

Technical detail and evidence

Why it matters, in detail. Conditioning on post-treatment survival or activity and on ever-observed payments can select on responses. Excluding payroll-less entities removes part of the population where TP adjustments may concentrate (compare the unexplained revision of audit receipts in F13).

Evidence. Sec. 3.2 p. 13; Appendix C pp. 115-118.

Why this severity. Subgroups by timing of MNE-status disclosure (Fig. A.4, estimates 10-12) give similar nulls; the plausible biases are small and of mixed sign.

The authors' response. Subgroup estimates by timing of MNE-status disclosure (Fig. A.4) show no differences.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

Rescaling payments to millions of USD would move the pooled semi-elasticity to about +0.008, i.e. to zero or past it (sub-claim in Auditor A's I6). — The linear Chen-Roth approximation behind it, log(1+Y) - log(1+Y/c) = ln(c), requires Y to be much larger than c. Typical positive payment cells are about $60-68k (exp(2.178/0.198) - 1, and the kUSD outcome), so with c = 10^6 the outcome is approximately Y/c, a scaled levels regression, whose behaviour resembles the imprecise levels/PPML results, not a coefficient of +0.008. The rest of the unit-dependence finding (USD to kUSD: -0.055 to -0.022) is upheld in F5.
The 'boom specific to transfer pricing' is a growth-rate artefact of a tiny base: in absolute terms, Big Four non-TP tax consultants grew more (+168) than TP consultants (+57) (sub-claim in Auditor A's I11). — The paper's specificity claim is about proportional growth relative to comparison groups, and Table C.1 supports it: Big Four TP +570% against Big Four tax +47%, non-Big-Four tax +34% and other professionals +30% (2010-2015), corroborated by the independent interview counts. Absolute headcounts of a much larger group do not refute specificity; the small-base caution is reflected in F16.
The CIT outcome omits the Additional Tax (66% of first-category revenue in 2010), so the revenue test misses part of the reform's effect (sub-point of Auditor A's I5). — Rejected as an explanation of the null. The direction is ambiguous: cutting deductible outbound payments raises first-category tax but lowers withholding on those payments, while higher retained profits raise later dividend taxes. It cannot be shown to bias the test toward zero. It is kept only as an estimand caveat in F7.
The 'All' column of the consolidation table counts dividend and financial payments, which are not cost-centre payments (point 4 of Auditor A's I3). — Not established. The Appendix C sentence (p. 118) describes which payment types determine inclusion in the 856-firm sample; whether dividends enter the column-(1) count of destination countries is not stated and could not be verified. It is not counted in F4.

Audit notes

What reproduced. No regression could be re-estimated: the SII tax and customs microdata, the Orbis/Dun & Bradstreet links, the Revelio extracts and the analysis code are not public, and no replication package was located (as of 2026-10-25). From the published tables the adjudicator re-computed the following. (i) CIT: the current-version % conversions, 95%/90% CIs, 80%-power MDEs and shares of the 20% benchmark gap ([-9.6%, +9.3%] to [-10.4%, +11.6%]; MDE 13.5-15.7%; upper bounds 46-58% of the gap, 62% with audits). (ii) Payments: the largest reduction not rejected in all 17 reform specifications (13-29% in the baseline; 50-63% in B.20; 115-242% in PPML/levels). (iii) Coherence of the published log(Y+1), kUSD and LPM coefficients with the Chen-Roth decomposition (-0.019 + ln(1000) x -0.00433 = -0.049). (iv) Observation counts, consolidation ratios (-36%, services -47%, haven CI -107% to +53%) and consultant multiples (11.9x; Revelio 4.7x/5.7x/7.2x for 2013/2014/2015). (v) The fixed-effect identities behind B.5/B.6/B.21/B.22, by simulation. (vi) The Fig. 5 series, by pixel measurement. (vii) The model algebra (reported-profit rule; psi = 1/2 sum K_j (t_j - t-tilde)^2). (viii) The TWZ benchmark (Chile 12% of CIT; 9% global). (ix) The legislative dates (BCN history of Law 20.630; SII circulars). The core current-version arithmetic (percentage conversions, CIs, sample sizes, ratios) reproduces. Not reproduced: the June 2022 % effects and CI statement; Fig. 5's non-Big-Four tax-consultant line (about 156% vs 134% in 2015) and Fig. 4b's 2014 sum (54 vs 53); the 'three years after' consultant multiples (7-fold is a 2015 figure); the 60% MNE share of CIT (not in the cited source); and the statement that the law was debated in Congress in 2011 (the official history starts with the 2 August 2012 message; an earlier bill was sent on 30 April 2012).

Limits of this audit. No microdata, code or replication package is available, so every judgement about estimates rests on published coefficients, standard errors and figures. Figure readings (Figs. 4-6, A.4) are approximate (+/- 1-3 pp or +/- 0.01 SD). The effect of country-level clustering (F6), of the DJ1912 code mapping (F17), and of revenue weighting or winsorisation (F7) cannot be computed. The CESifo 2026 and CEPR full texts were not accessible (assumed to match the NBER revisions); the BCN legislative history was read only for its opening pages (presidential message of 2 August 2012 and the TP section), so an earlier 2011 bill not part of Law 20.630's history cannot be ruled out with certainty. The 2011 creation of the SII TP unit, the audit counts and receipts, and the interview content could not be verified independently. The illustrative CIT-rate confound (F8) uses an external consensus semi-elasticity (0.8), not a Chilean estimate. The contrary studies in F10 were checked at the abstract level. No published critique of, or reply to, this specific paper was found, and the critique corpus contains no entry targeting it.