Pierre Bachas, Matthew Fisher-Post, Anders Jensen, Gabriel Zucman · American Economic Journal: Applied Economics 18(4): 509-549

Globalization, Capital Taxation, and Development: Evidence from a Macro-Historical Database

16 problems found: 1 major · 6 moderate · 9 minor

What the paper claims

A new macro-historical database of effective tax rates (ETRs) on capital and labor, the first with global coverage of developing countries.
Effective capital tax rates fell in high-income countries, driven by corporate taxation.
New stylized fact: effective capital tax rates rose in developing countries after 1990, more so in large economies.
Labor and capital ETRs converged globally, through a rise in labor taxation and a fall in capital taxation (headline of the 2022 versions).
Trade openness raised ETR_K (and, less, ETR_L) in developing countries and accounts for about a quarter of the rise.
Trade raised total tax revenue in developing countries, about half through CIT.
Mechanism: trade raised the share of output produced in corporations and, within the corporate sector, in larger firms, where effective capital taxation is higher (a tax-capacity channel that outweighs tax competition).

Every problem found

1majorlikely · newly identified here · methodology

The paper argues that trade raised taxes on capital by moving activity from small family businesses into corporations. But for most developing countries that split is not measured; it is estimated with a formula based on average income, so the data cannot show that trade, rather than ordinary economic growth, caused the shift. The separate finding that corporations paid higher effective tax rates holds up better.

Technical detail and evidence

Why it matters, in detail. The Table 3 coefficients on the corporate share (+0.176) and mixed income (-0.179) are identified mostly from imputed cells whose within-country movements follow log income per capita (imputed gradient -0.088, matching the observed -0.094). In the public data the instruments also move income strongly (IV 2.4 log points per unit of trade/NDP); conditioning on log income cuts the mixed-income effect from -0.29 to -0.08 and the corporate-share effect from +0.31 to +0.14 (both insignificant), while ETR_K (0.29 -> 0.25) and corporate ETR (0.26 -> 0.28) are stable. The 'corporations' channel is therefore observationally equivalent to a development effect built into the imputation; the within-corporate-sector (larger-firm) channel retains support. The income control is a bad control if trade raises income, so this is a diagnostic, and the AEJ's stronger instruments could not be tested.

Evidence. Authors' July 2022 data (master.dta): mixed income imputed in 89.5% and corporate surplus in 83.6% of LMIC country-years; 76.9% of non-'composite' cells still have imputed mixed income; imputed cells carry 99.7% (1989) and 81.2% (2018) of LMIC capital-income weight and 100% of treated observations in all seven event windows (scripts/a12_imputation.py, a21_misc_checks.py). Identity va_corp = ce_hh - ce_gov + os_corp holds in every non-missing row and the four shares sum to exactly 1 (a12). Within-country slope of the mixed-income share on log NNI per capita: imputed cells -0.088 (0.009), observed cells -0.094 (0.040) (a16). FE-2SLS with the public instruments (LMICs, N=3,552, first-stage F=6.4): mixed income -0.293 (0.121) -> -0.084 (0.069) when log NNI per capita is controlled; corporate share +0.306 (0.127) -> +0.140 (0.086); corporate surplus share +0.267 -> +0.110; ETR_K 0.291 (0.121) -> 0.249 (0.098) and corporate ETR 0.259 -> 0.279 (0.141) survive; observed-mixed-income cells alone give F=1.9 (a16, a18). Instrumented trade raises log NNI per capita by 2.4 (1.0) in the public data (a17). AEJ: Supp. App. B.1 p. 15; Table A3 col. 5; Table 3 p. 538; text p. 537.

Why this severity. Major for the abstract's mechanism claim ('by increasing the share of output produced in corporations'): that leg supplies most of the calibrated mechanism (channel A, about 9.8 of 11.3 pp) but rests on modeled splits; with observed data only the evidence is uninformative, and in the public data an income control removes 55-70% of the sector-share effects. The descriptive ETR trends and the trade effects on ETR_K and on the corporate ETR are not affected.

The authors' response. No published response. The paper states that 'our main results also hold without the imputed values (Table A3)' (Supp. App. B.1), but Table A3 covers ETR_K/ETR_L only; fn. 53 reports no effect of trade on statistical capacity.

2moderateconfirmed · newly identified here · data error

China's official statistics started counting the income taxes of private and foreign-owned firms only in 2001. The paper uses the series as if it were consistent, so China's company taxes look too low in the 1990s and seem to jump in 2001. This exaggerates how much China's capital taxation rose. It does not change the overall developing-country comparison between 1989 and 2018.

Technical detail and evidence

Why it matters, in detail. The NBS coverage change (SOE + collective -> all ownership types in 2001) is a level break of at least 44% in 2000 CIT on the domestic-EIT evidence alone. With foreign-invested firms' income tax and pre-2002 property/stamp duties (securities stamp tax alone was 47.8 bn yuan in 2000) the break is larger. Auditor A's 15.6-17.5 pp for China's corrected 1994-2018 rise is plausible against 22.6 pp in the 2022 data. It also biases the imputation-balanced robustness series (Fig. 3C), which backcasts China from its understated 1994 level, and makes the 1990s look flat.

Evidence. NBS, China Statistical Yearbook 2021, Table 7-4, note 1 (before 2001 EIT 'only includes state-owned and collective enterprise income tax'); CSY 2001 Table 8-4: 2000 EIT 999.63 = SOE 827.41 + collective 172.22 (100 m yuan). BFJZ's 2022 China CIT equals that row exactly for 1985-2001 (ratio 1.000) (scripts/a03_china_cit.py). State Administration of Taxation, 'Overview of the 2000 Tax Revenue' (china.org.cn, Jan 2001): domestic enterprise income tax 144.1 bn yuan, explicitly excluding foreign-invested enterprises, versus 99.96 bn in BFJZ. China's 'other taxes' are 2,725 (100 m yuan) in 2000, and its property taxes jump 195 -> 956 in 2002 as items are itemized (a03). State Council General Office urgent notice of 1 Jan 2002 (gov.cn): local EIT +139.4% y/y in Nov 2001 and +187.1% in early-mid Dec, with a warning against 'artificially raising the base'. The AEJ still shows the steps: Fig. 4A China about 7% (2000) -> 13% (2001) -> 17% (2002); Supp. Fig. A2(a) LMIC CIT about 2.3% -> 3.05% of NDP in 2001 and a property step in 2002. Sensitivity (a14): scaling 1994-2000 CIT by the SAT/NBS ratio (1.24 for 1999, 1.44 for 2000; domestic EIT only, a lower bound) raises China's 1994 ETR_K from 5.3% to 6.5-7.5% and cuts its 1994-2018 rise from 22.6 to 20.4-21.4 pp; China supplies 61% of the 2000->01 LMIC step (a04).

Why this severity. Overstates China's own rise (a headline example) by at least 1-2 pp and plausibly 5-7 pp, creates most of the 2001 aggregate step and inflates one of the two events that drive F2. It leaves the 1989-2018 LMIC benchmark change unchanged because China enters only in 1994 and its 2018 level is unaffected.

The authors' response. No published response. The paper discloses China's weight and reports an excluding-China series (Fig. 4B: 10% -> 15%); Supp. Table O1 says archival and OECD data for China 'match well in overlapping years', but the overlap (2007-08) is after the break.

3moderateconfirmed · newly identified here · methodology

The paper measures the rise from 1989, a low year when Brazil and Argentina had hyperinflation and when the data for many countries switch from old archives to modern statistics. Starting a year or a few years later makes the rise about 15-30% smaller, and the published series barely moves during the 1990s. The increase is real, but it is smaller and later than the 'after 1990' story suggests.

Technical detail and evidence

Why it matters, in detail. The splice and the base year coincide, so up to 1.4 pp of the AEJ's 8.4-8.7 pp (the 1989->90 step) is not clearly economic. The public data bound the artifact at about 0.3 pp (Brazil's CIT overlap gap only) to 2.0 pp (all switchers chain-linked). The 'post-1990 hyperglobalization' timing is not visible in the benchmark aggregate: the published series is 11.2% in 1990 and 11.3% in 2000. The ex-China series rises earlier, partly at the 1994 entry of ex-communist countries. A lower true rise would raise, not lower, the trade share computed in C5.

Evidence. AEJ Fig. 2 LMIC panel digitized at 400 dpi (scripts/a09_digitize_fig2.py): 9.8% (1989), 11.2% (1990), 12.2% (1994), 11.3% (2000), 13.3% (2001), 18.2% (2018), i.e. +8.4 pp from 1989 (stated 8.7), +7.0 from 1990, +6.0 from 1994; Auditor A's independent digitization agrees within 0.2 pp. 2022 data: 1989 9.41%, 1990 12.40%, 2000 11.08%, 2018 19.39% (a04). Between 1989 and 1990, 35 of 86 LMICs switch tax-data source, carrying 46% of 1989 LMIC capital income; their aggregate ETR_K goes 9.9% -> 16.8% while non-switchers go 9.0% -> 8.9% (a06). Brazil (18.5% of 1989 LMIC capital income): archival 7.3% (1989) -> CIAT/OECD 15.0% (1990); in 1990-96, when both exist, archival CIT is 28-45% below OECD CIT (median OECD/archival 1.62) (a06, a07). Bounds, 2022 data excluding Venezuela (absent from the AEJ): chain-linking all switchers at 1990 lowers the 1989-2018 rise from 10.0 to 8.0 pp, Brazil alone to 8.45, a 1990 base to 8.2 (a08). Fn. 24 calls 1989 'partly arbitrary' and reports changes from each series' lowest point (6.8-11.3 pp), which does not address a trough base. Earlier drafts used 1995 (Mar 2022) and 1994 (Jan 2024: '+7.6 ppt').

Why this severity. Reduces the headline 8.7 pp rise by about 15-30% depending on the base year (about 7 pp from 1990, 6 pp from 1994), and part of the 1989->90 step is plausibly a splice artifact. The qualitative rise survives every base year and every splice adjustment.

The authors' response. No published response. Fn. 24 acknowledges the base year is 'partly arbitrary'; p. 526 notes that excluding China 'a more significant part of the rise occurred earlier in the 1990s'.

4moderateconfirmed · newly identified here · misrepresentation of source

To show its explanation is believable, the paper borrows numbers from a published trade model and concludes the explanation accounts for about 75% of the estimated effect. But it counted only the rise in imports, while that model assumes exports rise just as much, so trade grows twice as fast as assumed. Corrected, the explanation accounts for about 37% of the effect, or less.

Technical detail and evidence

Why it matters, in detail. Channel A (formalization) falls from 9.8 to 4.8 pp and channel B (firm size) from 1.5 to 0.74 pp per 100 pp of openness, so the mechanism explains about 5.5 of the 14.9 pp IV effect (37%). The figure is about 33% in NDP units. DGMU's nonlinear large-shock results imply only about 10.7 pp of formalization per 100 pp of openness, against 71.4 pp assumed, which would bring the share to about 15%. Other inputs are transcribed correctly, apart from a trivial averaging slip (2.875 vs 2.8575).

Evidence. AEJ Supp. App. D.1 pp. 25-27; main text p. 539. Dix-Carneiro, Goldberg, Meghir & Ulyssea, 'Trade and Domestic Distortions: The Case of Informality', Cowles DP 2384 (Feb 2024): Table 8 p. 33 (informal employment -4.400% / -1.315%; TFP +1.637% / +1.502% for tau 2.4 -> 2.3); Sec. 5.1.2 p. 34 (imports/GDP 6.6% -> 15% -> 30%; informal share 51% -> 46% for tau 2.4 -> 1.6); Online App. H ('Trade balance implies that total imports must equal total exports'). Recomputation (scripts/a22_calibration.py): authors' method 74% (printed about 75-76%); balanced trade 37%; trade measured over NDP 33%; using DGMU's large-shock informality response about 15%. Auditors A and B obtained 37-38% independently.

Why this severity. Halves, or more, the quantitative plausibility check the paper offers for its size-based mechanism, but the calibration is a supporting exercise. The IV estimate, the 25% attribution and the descriptive trends do not depend on it.

The authors' response. No published response; the appendix describes the exercise as approximate and explicitly abstracts from exports.

5moderateconfirmed · newly identified here · selective presentation

The 2022 versions say capital taxes fell 5 points worldwide. That fall happens mostly because more of the world's capital income now comes from developing countries such as China that tax capital less, not because countries on average cut their tax rates on capital. Holding each country's weight fixed, the worldwide rate barely changes, though the rise in labor taxes is real.

Technical detail and evidence

Why it matters, in detail. Under time-varying factor-income weights, the 1965-2018 change in global ETR_K is -5.2 pp. Holding country weights fixed it is between -1.3 and +1.6 pp depending on the weight year, weight type and panel balancing. At least about 75% of the measured decline is therefore compositional, and on a balanced panel all of it. The HIC fall (about -4 to -6 pp) is offset by the LMIC rise; ETR_L rises 10-15 pp under every scheme, so labor-capital convergence survives only through the labor side.

Evidence. WB PRWP 9973 and NBER w29819 rev0 (Mar 2022) abstracts: rates 'converged globally since the 1960s, due to a 10 percentage-point increase in labor taxation and 5 percentage-point decrease' in capital taxation. 2022 data (scripts/a15_global_fixed.py): time-varying weights ETR_K 31.05% -> 25.83% (-5.2 pp); fixed 1994/2010/2018 capital-income weights +0.1/-0.7/-0.7 pp; fixed NDP weights -0.7/-0.9/-1.3 pp; balanced 72-country panel with fixed weights +0.2 to +1.6 pp. ETR_L +10 to +15 pp under every scheme. LMIC share of world capital income 15.8% (1965) -> 47.4% (2018); China 38% of LMIC capital income in 2018 (a04).

Why this severity. Essentially all of the capital side of the 2022 headline (-5 pp) reflects reweighting of world capital income rather than lower country tax rates, so the 'drop in capital taxation' part of C4 is mostly composition. The labor rise and the HIC decline (C2) are unaffected, and the published version defines the aggregate as dollar-weighted and notes the decline occurred only in HICs.

The authors' response. The AEJ defines the global rate as the 'average tax rate on a dollar of capital income' and states that 'the decline in capital taxation only occurred in HICs' (p. 522); no fixed-weight decomposition is reported.

6moderateconfirmed · newly identified here · overclaiming

In several places the text says results are 'robust' or 'significantly' larger, while the paper's own appendix tables show estimates that are not statistically distinguishable from zero. These are side results, but the wording makes the findings look more solid and more general than the tables support.

Technical detail and evidence

Why it matters, in detail. The conclusion that pro-tax impacts 'do not hinge on ... enforcement investments' (p. 543) rests on point estimates whose interactions are all insignificant. The mechanism results are robust to the gravity instrument but not to the oil-distance instrument (capital share flips sign). The total-tax result loses significance with NDP weights (t = 1.6). Each is a text-versus-table discrepancy rather than a computational error.

Evidence. (a) p. 534: total-tax effect 'robust to using NDP weights' vs Supp. Table A4 col. 1: 0.095 (0.061), not significant. (b) p. 543: trade's effect on corporate ETR 'significantly amplified when enforcement policies are in place' vs Table A5 col. 4 interactions 0.108 (0.122), 0.351 (0.428), 0.123 (0.126), 0.162 (0.152), none significant; the 'positive effect ... without these policies' on ETR_K is insignificant in two of four panels (0.113 (0.069), 0.109 (0.071)). (c) p. 544: trade 'raises ETR_L everywhere' vs Table A7 HIC implied 0.266 (0.189). (d) p. 538: mechanism 'robust to ... estimating IVs separately based on each instrument' vs Table A4 col. 6 (oil-distance only): mixed income -0.140 (0.138), capital share -0.021 (0.126). (e) Sec. VD presents the imports-vs-exports results without the weak first stage reported in the appendix (Kleibergen-Paap F = 3.69, Table D1).

Why this severity. Overstates the statistical support for secondary claims (enforcement heterogeneity, HIC labor effects, robustness of the total-tax and mechanism results) that bolster the paper's interpretation. The main ETR_K IV and the stylized facts are unaffected.

The authors' response. No published response; point estimates are of similar sign and size across specifications, and Supp. App. D.3 acknowledges the weak first stage for imports vs exports.

7moderatelikely · newly identified here · methodology

One of the paper's three main tests compares seven big trade-opening episodes with similar countries. Almost all of the tax increase in that test comes from China and Vietnam in 2001. China's jump that year coincides with a change in what its official statistics counted, not with more trade, so this test adds little independent proof that trade raised capital taxes. The paper's other tests are not affected.

Technical detail and evidence

Why it matters, in detail. Leave-one-out estimates (Supp. Fig. O7) cannot reveal the joint dependence, and no leave-two-out is reported. Without China and Vietnam the raw treated change is about +0.6 pp against +3.5, so the synthetic DiD of 0.041 would likely fall to around 0.01. The China leg is partly a statistical artifact: its e=0 jump coincides with the NBS coverage change while trade fell, and Vietnam's is plausibly oil-driven. Source switches at e+1/e+2 in three further windows threaten the 'sharp break from stable pre-trends' identification argument. The design's implied Wald ratio (0.041/0.055 = 0.75) is also five times the IV.

Evidence. Raw treated change, mean of e=0..7 minus e=-7..-1 (2022 data): China +11.0, Vietnam +10.9, Colombia +0.3, Mexico -3.0, Brazil +2.3, Argentina +2.7, India +0.6 pp; mean +3.5, +0.6 without China and Vietnam; China and Vietnam supply 92% of the e=0 jump (scripts/a10_event_raw.py; reproduces Auditor A exactly). China: ETR_K +5.5 pp and CIT 1.15% -> 2.74% of NDP in 2001 while trade/NDP fell 46.8% -> 45.6%. Vietnam: CIT 3.97% (1999) -> 7.57% (2001) -> 10.34% (2006) of NDP as oil and gas output rose from 4.2% to about 11% of NDP; Vietnam is not flagged oil-rich (5.9% average) (a10, a11). AEJ Fig. 6 levels (p. 530): treated ETR_K about 0.100 (e=-1) -> 0.118 (e=0) while treated trade about 0.395 -> 0.405 versus about 0.435 for the synthetic control; trade accelerates from e=2-3. Supp. Table A1 Panel A: Post x Treat on trade 0.0551 (0.0648) vs ETR_K 0.0413 (0.0147). Source switches inside the +/-7-year windows (Supp. Table O1): Argentina e+1, Brazil e+2, Vietnam e+2, Colombia e+5, China e+7 (plus the coverage break at e=0), Mexico e-5; only India has none. Brazil's ETR_K doubles at its switch (7.3% -> 15.0%, 1989-1990; a07); CSLL corporate levy created by Lei 7.689 of 15 Dec 1988 (law text checked).

Why this severity. Removes most of the independent support that one of the paper's three main designs gives to C5, and weakens the 'consistent across research designs' claim. The IV that quantifies C5, the within-country correlations and the 68-event Wacziarg-Welch design (which excludes the 2001 events and still gives +6.2 pp) are unaffected.

The authors' response. No published response. The paper reports leave-one-country-out results as similar (Supp. Fig. O7), notes that medium-run coefficients may reflect other reforms (pp. 529-530), and shows a 68-event alternative (Supp. Table C1).

8minorconfirmed · newly identified here · documentation gap

The evidence from Rwandan firms is described in contradictory ways (two different statistical methods and two different trimming rules), and the size of the effect changed tenfold between drafts. The direction of the result is consistent, but readers cannot tell how large it is.

Technical detail and evidence

Why it matters, in detail. Linear 2SLS on tax/(profit + 1) and a Poisson conditional mean imply different estimands. A coefficient of 1.5 on a share bounded in [0,1] is uninterpretable as a level effect on an ETR. The specification (instruments, sample, outcome) changed between May 2024 (0.133) and the AEJ (1.501), but the text still describes the PPML estimator.

Evidence. AEJ p. 540 (PPML; semi-elasticities; winsorize 1-95%), fn. 58 p. 541 ('As PPML is not compatible with IV, we estimate 2SLS'), Table 4 notes p. 542 (PPML and 2SLS; winsorized 1-99%); Supp. App. D.2 p. 29; fn. 57 (adds 1 to the denominator). May 2024 NBER version Table 4: linear IV 0.133 (0.060), N = 18,478, F = 18.17; AEJ Table 4: 1.501 (0.485) [bootstrap 0.677], N = 19,270, F = 129.34.

Why this severity. A documentation problem in supporting firm-level evidence. The sign is stable across versions and the paper uses the result only qualitatively, so the conclusions are unaffected, but the magnitude cannot be interpreted.

9minorconfirmed · newly identified here · version instability

The data that readers can download from the paper's website is an older 2022 version that gives different numbers from the published article, and several key figures changed noticeably between drafts. This makes the results harder to check or reuse, but it does not by itself mean the published numbers are wrong.

Technical detail and evidence

Why it matters, in detail. The trade-attribution share has ranged from 20% to 41% across versions as the preferred specification switched from NDP-weighted to unweighted. Country examples were re-based from 1995 to 1989, nearly doubling Brazil's reported rise. The public vintage's distinct features (Venezuela with misallocated oil income tax, larger China property taxes, a weaker instrument set) mean that results recomputed from the website will not match the paper.

Evidence. globaltaxation.world links (checked 25 Oct 2026) point to github.com/pierrebachas/Globalization_Factor_Taxation, last commit 11 Jul 2022. 2022 vintage vs AEJ: LMIC 1989-2018 rise +10.0 vs +8.7 pp; China 2018 ETR_K 27.9% vs 24%; mixed-income capital share 30% vs 25%; 155 vs 154 countries (Venezuela included). Benchmark unweighted IV: 0.250 (Mar 2022) -> 0.109 (Jun 2023, Jan 2024) -> 0.151 (May 2024) -> 0.150 (AEJ). Trade's share of the rise: 41% (Jun 2023, NDP-weighted 0.222) -> 33% (May 2024, 0.211) -> 25% (AEJ, unweighted). Base year: 1995 / 1989 / 1994 / 1989. China start 10% (1995, Mar 2022) -> 5% -> 6% (1994, AEJ); Brazil '18% to 28%' (1995-2018) -> '7% to 27%' (1989-2018). AEJ p. 526: ETR_K 'has only fallen in 1 country (Russia)' among the 19 largest LMICs; in the public data 7 of the 24 LMICs above 40 million people (4 of 18 non-oil) fell (scripts/a20_large_lmics.py).

Why this severity. Users of the advertised public database obtain numbers that differ from the article, and several headline quantities are version-sensitive. The deposited openICPSR package presumably holds the final data, and the revisions mostly moved estimates in a conservative direction.

10minorconfirmed · newly identified here · internal inconsistency

Kuwait is counted as one of the rich OECD-type countries even though it is not an OECD member, contrary to the paper's own rule. Moving it barely changes any result.

Technical detail and evidence

Why it matters, in detail. Moving Kuwait to the LMIC group shifts aggregates by hundredths to tenths of a point. Its prominence as a synthetic-control donor is neutralized by the LMIC-only donor robustness.

Evidence. AEJ p. 520 and Supp. Table O4 (Kuwait in Panel A); 2022 master.dta codes KWT rich = 1 (Auditor B). Reassignment changes the 2022-vintage LMIC 1989-2018 rise by +0.03 pp and HIC 2018 ETR_K by +0.23 pp (Auditor B). Kuwait is the largest ETR_K donor in several synthetic controls (Supp. Table O2: 83.6% for Colombia, 55.8% for Brazil), but LMIC-only donor pools give the same estimate (Supp. Table A1 Panel F).

Why this severity. A labeling inconsistency with negligible quantitative effect.

11minorconfirmed · newly identified here · internal inconsistency

The rule the paper states for labeling countries as oil-rich is not the rule actually used, and one country (Senegal) is labeled oil-rich because of an obvious data error. This only matters for side checks and changes almost nothing.

Technical detail and evidence

Why it matters, in detail. The flag is a long-run hydrocarbon-dependence indicator rather than the stated 2018 measure. Several flagged countries (Mexico, Indonesia, Malaysia, Egypt, Belize) are well below 7% of GDP in 2018, and Senegal's flag is a data error. The interaction-FE robustness (0.136) and the excluding-oil series are barely affected.

Evidence. AEJ Fig. 4 notes p. 526, Table 1 notes p. 533, Supp. Table O4 (Senegal, Mexico, Indonesia, Malaysia, Egypt, Belize flagged). oil_sample.dta: 'avg oil production > 6.5% of GDP since 1990'; Senegal 25.5%, Vietnam 5.9% (not flagged) (scripts/a11_oil.py). USGS 2017-18: Senegal crude output about 95,000 barrels in 2018, about 0.04% of GDP even at $100/bbl (Auditor B). Restoring Senegal to the non-oil sample changes its 1989-2018 rise by -0.01 pp (Auditor B).

Why this severity. Affects only the oil-rich robustness checks (Fig. 4C; Table 1 col. 6), with negligible measured impact.

12minorconfirmed · newly identified here · misrepresentation of source

The historical descriptions used to date two of the trade-opening episodes misstate their sources: the cited study says Brazil really opened up in 1990, not 1988, and Mexico joined the global trade body's predecessor in 1986, not 1985. The errors are small, but they matter for a method that depends on exact dates.

Technical detail and evidence

Why it matters, in detail. The selective quotation reverses the cited source's dating of Brazil's effective liberalization (1990 vs 1988). With a 1988 date, Brazil's 1990 data-source switch and ETR_K doubling fall at e=+2 of its event window (F2). The Mexico and Colombia 'WTO' references are factual slips (GATT 1986 and 1981 accessions).

Evidence. Supp. App. C.1 pp. 21-22 (lines on Brazil, Colombia, and 'Mexico's 1985 WTO accession'). Dix-Carneiro & Kovak (2017), AER 107(10), p. 2911: the 1988-89 cuts had 'no effect on the level of protection faced by Brazilian producers'; 'Liberalization effectively began in March 1990' (text checked). WTO Mexico page: GATT member since 24 Aug 1986, WTO member since 1 Jan 1995 (checked).

Why this severity. Narrative and dating errors in supporting text. A 1988 start can still be defended as the formal onset of reform, and the pooled results are robust to dropping single events; no re-dated estimate was run.

13minorconfirmed · newly identified here · data error

The public version of the data contains small coding errors, such as treating missing tax figures as zero, using a budget forecast instead of actual revenue for India, and mixing up company and personal taxes for Venezuela. None of them changes the main results much.

Technical detail and evidence

Why it matters, in detail. Zero-coding biases levels downward where a category is truly missing (China PIT effect on ETR_K about 0.1-0.3 pp). India's budget-estimate entry understates its 2018 ETR_K by about 0.5 pp. The NNI/NDP mismatch scales ETR_KC by NDP/NNI (median 1.017). Venezuela's misallocation inflated the public data's 1989->90 step but is moot for the AEJ.

Evidence. ETR_2_merge_factor_shares.do: 'replace `var' = 0 if `var'==.' for all pct_* ('true zeros were occasionally left coded as missing'); China PIT recorded as 0 in 1994 and 1996-98 although actual PIT was positive (a03). India: 2018 CIT = 538,744.97 crore = Budget Estimate 2017-18 (Union Budget, para. 31), vs CBDT provisional actual 571,202; 2017 value 493,924 vs audited 484,924 (CBDT Time Series p. 2); the AEJ rule is 'We only use actual amounts of taxes collected' (Supp. App. B.1); effect on India 2018 ETR_K +0.55 pp (Auditor B). ETR_cit = (CIT + 0.5 x 1300, % of NDP) / OS_corp (share of NNI): understatement median 1.7%, p90 about 7% (a21). Venezuela 1987-89 (ICTD): CIT 1.9-4.3% vs PIT 6.9-10.9% of NDP, then OECD 1990: CIT 14.6%, PIT 1.4%; Venezuela is absent from the AEJ (a07). ETR_4_construction.do: alpha_1300 = 0.50 default.

Why this severity. Each item is small for the aggregates and several concern only the public vintage. Persistence in the AEJ data could not be checked.

14minorconfirmed · newly identified here · arithmetic or transcription

There are a few small numerical and labeling slips, such as two magnitude figures that use inconsistent assumptions and a table note that contradicts the text. They do not affect the conclusions.

Technical detail and evidence

Why it matters, in detail. The total-tax interquartile-range effect is understated by about 0.3 pp (5.7 vs 6.0). The winsorization ambiguity concerns which of columns 2-3 is the benchmark, and both give about 0.15. The headline endpoints are internally inconsistent by about 0.5 pp.

Evidence. 8.5 pp for ETR_K (0.150, p. 532) and 5.7 pp for total taxes (0.105, p. 534) imply different interquartile ranges (0.567 vs 0.543); 5.7 equals the May 2024 coefficient 0.101 x 0.567, and the consistent value is about 6.0 (May 2024: 8.9 and 5.9 with 0.151 and 0.101). Table 1 notes say column 3 'the outcome is winsorized', while the text says 'nonwinsorized ETRs (column 3)' (p. 532). '10 percent in 1989 to 18 percent in 2018' does not square with '+8.7 pp' and '86 percent', which imply 10.1% -> 18.8%; Fig. 2 digitizes to 9.8% -> 18.2%. The World Bank threshold is described in 'GDP per capita' (the World Bank uses GNI per capita, Atlas method). App. D's '-2.875' average of -4.400 and -1.315 is -2.8575. Fig. A2 notes say 'national domestic product'.

Why this severity. Presentation and rounding slips with no effect on conclusions.

15minorconfirmed · newly identified here · misrepresentation of source

The paper slightly misquotes a source on how much US labor income is taxed. The difference is too small to matter for its results.

Technical detail and evidence

Why it matters, in detail. Using 70% or 80% instead of 75% changes the implied labor share of PIT from 84% to 83-85%. PIT capital contributes only -0.6 pp to the LMIC change in the public data.

Evidence. AEJ p. 517 and fn. 11; Piketty, Saez & Zucman, NBER WP 22945 (text checked): taxable labor income 'declined from 80%-85% in the post-World War II decades to just under 70% in 2014 ... only a third of total capital income is reported on tax returns'.

Why this severity. The implied capital share of PIT is 15-17% whichever PSZ figure is used, well inside the 0-30% robustness band.

16minorlikely · newly identified here · methodology

The paper counts all property taxes, including taxes on house sales, stock trades and bank transactions, as taxes on capital. That is a standard choice, but some of these taxes fall on everyday transactions, and in the publicly downloadable data they make up about half of the rise. The published data seem to have reduced this, so the effect on the paper's headline is probably small.

Technical detail and evidence

Why it matters, in detail. Allocating 4400 (bank-debit, deed and stamp taxes) to capital follows MRT (1994) but is economically debatable for LMICs. In the published data the property/wealth/transaction contribution is roughly 0.8 of about 2.8 pp of NDP in additional capital tax revenue (Supp. Fig. A2(a)). China's 4400 alone is about 0.8% of GDP with a 38% weight in LMIC capital income, so reclassification would plausibly lower the 8.7 pp rise by around 1 pp. The AEJ's 'driven by the corporate sector' holds better in the published than in the public data.

Evidence. 2022 data decomposition of the LMIC 1989-2018 rise (+10.0 pp): CIT +5.6, property/wealth +4.9, PIT -0.6; excluding China +4.7 = CIT +3.9, property +1.0 (scripts/a05_decomp.py). China's category 4000 in the public data is 1.3-2.2 times OECD Revenue Statistics 4000 for 2007-2018 (a13); OECD classes China's deed and stamp duties in 4400 (793 of 1,321 bn yuan of 4000 in 2018). AEJ Supp. Fig. A2(a): LMIC property/wealth taxes about 0.3% (1989) -> 1.1% (2018) of NDP vs 0.33% -> 1.72% in the 2022 data, against CIT about 2.4% -> 4.2%. Auditor A: excluding OECD 4400 cuts Argentina's 1990-2018 rise from +10.8 to +6.4 pp and Colombia's from +12.9 to +10.6 pp. AEJ p. 510: rise 'driven by the corporate sector'; fn. 21: property taxes are 'smaller contributions'.

Why this severity. In the published data property/transaction taxes appear to supply about 30% of the rise, under the standard Mendoza-Razin-Tesar convention disclosed in Table B2; treating transaction taxes differently would plausibly trim the rise by about 1 pp. The larger overcount is confined to the public 2022 database (see F10).

The authors' response. No published response; the allocation follows Mendoza, Razin and Tesar (1994) and is disclosed in Supp. Table B2.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

The statement that trade 'rises in the years post-event by close to 10 percentage points' (p. 529) overstates the event-study trade effect, since the DiD on trade is 0.055 (0.065) (I8(d)). — The sentence describes the dynamic path, not the post-period average. In AEJ Fig. 6 the trade coefficients at e=5-7 are about 0.09-0.11 and the treated-minus-synthetic gap widens by about 9.5 pp by e=7. The weak trade response at e=0 is retained in F2.
Illustrating magnitudes with the cross-country 25th-75th percentile range of trade (about 0.57) misleads, because identification is within-country (I8(g)). — This is a common and transparent illustration, and the paper's quantitative attribution (25%) uses the actual 1989-2018 change in trade (14.6 pp), not the interquartile range.
'22-31 percent' should read 23-31 (0.136 x 0.146/0.087 = 22.8%), and App. D's '14.9 percentage points' conflicts with Table 1's 0.150 (I9). — Both are within rounding of unrounded coefficients (e.g. 0.1355 or 0.149) and not genuine errors.
Fig. 1 notes use NDP in constant 2010 US dollars while Fig. 2 notes use constant 2019 US dollars (I9). — The figures use different weighting schemes (NDP vs factor income); each is internally consistent, so this is not an inconsistency.
Property and wealth taxes account for about half of the LMIC rise, contradicting the AEJ's description of them as 'smaller contributions' (I5). — Confirmed only for the public 2022 vintage (+4.9 of +10.0 pp). AEJ Supp. Fig. A2(a) shows a smaller rise in property taxes (about 0.3% -> 1.1% of NDP, about 30% of the increase in capital tax revenue), so the AEJ description is accurate for the published data. The convention and the public-data overcount are retained as minor issues (F8, F10).
Splitting unallocable income tax (OECD 1300) 50/50 contradicts the AEJ's statement that the split uses 'information from additional sources' (I11). — The 50/50 rule in ETR_4_construction.do is a default for residual amounts; the supplement (Table O1) documents country-specific reassignments of unallocable income taxes (e.g. Colombia, Guatemala, Iceland, Portugal, New Zealand). The two statements are compatible.
Because imputed mixed income is a function of income per capita, instrumented trade 'passes mechanically' into the mechanism variables, biasing them (I3, point 5). — Partly rejected: imputed and observed cells show the same within-country income gradient (-0.088 vs -0.094), so the imputation reproduces rather than invents the relationship and no bias is demonstrated. What survives (F1) is that the sector-share evidence cannot distinguish a trade-specific channel from income growth.
Moving the base year to 1989 in later versions raised the headline rise (I4). — Qualified: the June 2023 version already used 1989 (+10.2 pp) and only the January 2024 draft used 1994, so the base year flip-flopped rather than being switched once to 1989. The base-year sensitivity itself is retained in F4.
No critical or major issue affects the work (overall assessment). — Not accepted. The imputed mechanism data (F1, major) and the event-study, China-break, base-year/splice and global-composition issues (F2-F4, F6, moderate) were not examined by Auditor B and are confirmed here.

Audit notes

What reproduced. All computations use the authors' July 2022 GitHub vintage, because the AEJ package (openICPSR E235001) was inaccessible. Reproduced: LMIC ETR_K 9.41% (1989) -> 19.39% (2018), +9.97 pp (published +8.7); HIC about 36% (1965-69) -> 31.6%; global ETR_K 31.1% -> 25.8% and ETR_L 16.1% -> 24.9%; LMIC corporate ETR 11.3% -> 17.1% (published 12% -> 20%). These match both auditors to two decimals. AEJ Fig. 2 digitized gives +8.4 pp from 1989 and +7.0 from 1990. Decomposition (2022 data): CIT +5.6, property/wealth +4.9, capital PIT -0.6 pp. Seven-event raw paths reproduce Auditor A exactly (mean +3.5 pp; +0.6 without China and Vietnam). China's CIT equals the NBS state-plus-collective row (ratio 1.000), confirming the 2001 coverage break. The calibration recomputes to 74% (authors' method) and 37% with balanced trade. Not reproduced: the AEJ IV (0.150, F=23), since the public instruments give 0.291 (0.121), F=6.4, N=3,552; also the synthetic-control estimates, the 54-series envelope, Table 2-4 magnitudes and the Rwanda firm-level results (confidential).

Limits of this audit. The AEJ replication package (openICPSR E235001) was inaccessible (Cloudflare challenge via curl and WebFetch). All computations use the July 2022 GitHub vintage, which differs from the AEJ (+10.0 vs +8.7 pp; Venezuela included; older, weaker instruments). Published-version magnitudes were inferred from AEJ figures digitized at 400 dpi (about +/-0.3 pp). The China coverage correction is a lower bound: domestic EIT only, from the SAT 2000 overview; foreign-invested firms' income tax and pre-2002 property/stamp taxes were not quantified from a primary source. The IV diagnostics use the weak public instruments (F about 6) and an income control that is a 'bad control' if trade raises income, so they are diagnostic rather than corrective. The synthetic-control event study, the 54-combination envelope and the Rwanda results were not re-estimated. The hypothesis that Brazil's archival CIT omits the CSLL levy is plausible but unverified.