Thomas Tørsløv, Ludvig Wier, Gabriel Zucman · American Economic Journal: Economic Policy 15(2): 497-525

Externalities in International Tax Enforcement: Theory and Evidence

17 problems found: 1 major · 7 moderate · 9 minor

What the paper claims

Danish transfer-price (TP) corrections overwhelmingly involve other high-tax countries; corrections involving tax havens recover only a small fraction of estimated profit shifting to havens.
Danish enforcement targets high-tax counterparts beyond what the geography of Danish affiliate links predicts.
Danish TP enforcement slightly lowers the global tax bills of the targeted multinationals.
Firms are more likely to appeal corrections that raise their global tax bill ('fight back when it suits them').
The reduction in global tax payments is driven by multinationals headquartered in Denmark.
If Denmark maximised global rather than national tax revenue, global tax payments would rise and Danish revenue fall.
Cross-country data show that high-tax countries' TP enforcement mostly targets other high-tax countries.
Theory: a capacity-constrained, revenue-maximising tax authority corrects equal-rate 'mistakes' and thereby crowds out corrections of shifting to havens; tax planners invest in resistance; high-tax countries engage in an enforcement arms race; easier MAPs and country-by-country minimum taxes can increase shifting.
Context: a large resource asymmetry between private and public transfer-pricing staff.

Every problem found

1majorconfirmed · newly identified here · data error

The paper's eye-catching claim that Danish tax audits actually lower multinationals' total worldwide tax bills depends on valuing Denmark's extra revenue at a 22% tax rate, but Denmark's rate in the years studied was 23.5-25%. With the correct rate the effect is roughly zero or slightly positive, so the claim that enforcement lowers global taxes is not supported, although the broader point that most of what Denmark gains is simply taken from other high-tax countries still holds.

Technical detail and evidence

Why it matters, in detail. The net global effect is the difference of two large gross flows (Danish gain EUR 320-364m vs foreign loss EUR 333m), so d(net)/d(t_DK) = EUR 14.6m per percentage point. Holding the workbook's foreign side fixed, the net is -EUR 13.1m only at 22%; at the rates in force (23.5-25%) it is +EUR 9m to +EUR 31m. A fully consistent historical recomputation also needs the undocumented foreign-rate vintage: if the non-haven foreign rates were 2018 values about 2pp below contemporaneous ones (27.2% -> 29.2%), the net would return to about zero. The defensible statement is a net of approximately zero (within about +/-EUR 30m, +/-10% of gross flows) with undetermined sign. The Figure 4 lower bound consists entirely of eliminating the non-haven net (-EUR 61m at 22%, -EUR 31m at 24.5%), so it halves; the preferred estimate falls from 1.22% to about 0.8% of Danish CIT revenue. C5's subgroup signs survive (Danish-HQ net -EUR 8m at 24.54%).

Evidence. Workbook TWZ2020b.xlsx 'Table 1'!C14 = 320.279 = 0.2200 x C10 (1,455.81); D14/D10 = E14/E10 = 0.2200; implied foreign rates 27.16% (non-havens) and 3.82% (havens). Official rates: Skatteministeriet 'Centrale skattesatser i skattelovgivningen 2010-2017' (Selskabsskat 25, 25, 25, 25, 24.5, 23.5, 22, 22) and OECD Tax Database CIT_C (DNK 2009 25.0, 2014 24.5, 2015 23.5, 2016 22.0). NBER WP 26899 p. 11; TWZ (2017) slides ('Danish tax authority (tax rate 24.5%)'); SKAT TP-redegoerelse 2014 and 2015 (revenue 'all else equal' = the relevant year's nominal rate x the adjustment). Adjudicator recomputation (final/scripts/sensitivity.py, work/sensitivity.out): net -EUR 13.1m at 22%, +8.8m at 23.5%, +23.3m at 24.5%, +23.9m at the SKAT-amount-weighted 24.54%, +30.6m at 25%; Figure 4 preferred 1.22% -> 0.77-0.86%, lower bound 0.84% -> 0.38-0.42%, upper 2.48% -> 2.06-2.29%.

Why this severity. Correcting a documented factual error reverses the sign of a headline estimate that the introduction and abstract use to claim that enforcement reduces multinationals' global tax payments, and cuts the Figure 4 gains by roughly a third (preferred) to a half (lower bound); it does not affect the composition findings (C1-C2) or the theory.

2moderateconfirmed · newly identified here · methodology

The paper's model assumes that a tax-dodging firm always keeps its profit shifting just small enough to avoid an audit. In the model as written, though, a firm could shift far more, accept the audit and still come out ahead, because an audit only claws back part of the shifted profit. The model's conclusions can be rescued with a standard extra assumption, so this is a gap in the proof rather than a reason to reject the idea.

Technical detail and evidence

Why it matters, in detail. The firm's value is (t_H - t_L)[x 1{x <= x*} + (1 - gamma_L) x 1{x > x*}], unbounded for gamma_L < 1. With a profit bound X, the threshold equilibrium requires (1 - gamma_L)X <= x*; otherwise the firm chooses X, is audited, and haven corrections are not crowded out. Proposition 1's comparative statics (increasing in b and gamma_H, decreasing in gamma_L) hold only where that constraint holds; the welfare ranking in Proposition 2 is robust. Denmark's 10%-of-income TP penalty (EY 2014) would not by itself close the gap at these parameters.

Evidence. TWZ (2023) pp. 515-518, eqs. (1)-(6) and Propositions 1-2; adjudicator re-derivation; Auditor B scripts/reproduce.py (theory block). Eqs. (1)-(4) and the marginal-yield threshold itself are correct.

Why this severity. The formal derivation of the central propositions has a gap, but standard repairs (bounded mispricing with (1 - gamma_L)x_max <= x*, a large enough penalty, or treating gamma as a per-case resource cost so that a corrected firm loses its whole shift, close to the paper's informal story) restore them; the externality result (capacity spent on zero-global-value corrections lowers global revenue) holds regardless, and no empirical result depends on it.

3moderateconfirmed · newly identified here · misrepresentation of source

The paper uses European and OECD dispute statistics to show that tax havens rarely appear in tax disputes, but it misreads how these statistics are compiled: each dispute is counted once by each of the two countries involved, which makes havens look about half as common as they are, and one haven (Switzerland) was left out of the count. Corrected, about one dispute in five involves a haven rather than one in ten, and the data cannot show which country started the dispute.

Technical detail and evidence

Why it matters, in detail. With distinct pairs NN, NH and HH, reporter-based counts are 2NN + NH in non-haven rows and NH + 2HH in haven rows, so the row share NH/(2NN + NH) is about half the distinct share NH/(NN + NH). With 597/71/69/3 reports, NN = 298.5, NH = 70, HH = 1.5, giving 19.0-19.3%; the directional share f NH/(NN + f NH) is unidentified (f = share of mixed cases initiated by the high-tax side; 10.5% at f = 0.5). For the OECD data, 2018 TP starts summed over jurisdictions are 1.9 times OECD's own aggregate, so the haven share of distinct cases is up to about 20% (10.45% of reports including Switzerland).

Evidence. JTPF/013/2012/EN p. 3, parsed by final/scripts/parse_jtpf2011.py (non-haven reporters 597 non-haven/71 haven partners; haven reporters 69/3; all 27 row sums equal the printed totals; the source attributes discrepancies to cases 'reported by the initiating CA and the counterpart CA'); workbook 'TableE2' (595/71/71/3) and 'DataF5-6'!D10 = 74/740; 'Data F. A5'!J3 formula (final/scripts/check_oecd_map.py); OECD 2018 per-jurisdiction statistics (Switzerland 14 + 19 = 33, Germany 149 + 78 = 227, Ireland 6 + 2 = 8 closed TP cases); EY's summary of the OECD 2018 release gives 930 TP cases started in 2018, about half the 1,786 jurisdiction reports summed in the workbook.

Why this severity. Haven involvement in the cross-country MAP corroboration roughly doubles (about 19-21% rather than 8-10.7%) and the direction of enforcement is not identified; a non-haven majority of about 80% survives, and the paper itself notes that MAP data under-represent zero-tax havens.

The authors' response. In-paper caveat (pp. 513-514): firms may not request a MAP when profits are relocated from a zero-tax place, so MAP data under-represent havens. No response on the structure of the statistics.

4moderateconfirmed · newly identified here · internal inconsistency

The paper's description of an international survey says only two tax havens are ever named as targets, but its own chart shows six more havens being named and the two it mentions ranked third and fourth overall. Havens make up almost three in ten of the targets named, which still leaves a majority of non-havens but is a weaker result than the text suggests.

Technical detail and evidence

Why it matters, in detail. Top-three mentions: non-havens 55/77 (71.4%), havens 22/77 (28.6%); across all listed positions havens are about 36%. Without a volume benchmark (havens host a large share of multinational profits and intragroup transactions), a 71/29 split is weak evidence of under-targeting. The coding is otherwise faithful to EY (e.g., Germany's list: Switzerland, China, Hong Kong, Singapore, Cyprus).

Evidence. TWZ (2023) p. 511 and Figure 5 (p. 512, rendered); workbook 'TableE3b' and 'DataF5-6' (final/scripts/ey_recount.py); EY (2014) Global Transfer Pricing Tax Authority Survey, US, Germany, Austria, Denmark and Poland chapters; NBER WP 26899 Figure 4 (two panels).

Why this severity. The narrative overstates the absence of havens in one of the three cross-country sources (29% of mentions, with Switzerland and the Netherlands ranked third and fourth); the figure still shows a 71% non-haven majority, so the qualitative claim survives with less force.

5moderateconfirmed · newly identified here · internal inconsistency

The paper's appendix table splitting corrections between Danish-owned and foreign-owned multinationals has its two halves labelled the wrong way round in the journal's version, which reverses one of the paper's main findings; the authors corrected it by hand on their own website copy. Even with the labels fixed, the table's tax effects are estimated with averages rather than measured for each group.

Technical detail and evidence

Why it matters, in detail. With pooled rates each subgroup's net = (0.22 - 0.2716) NH + (0.22 - 0.0382) H, so the Danish-HQ net (-EUR 34m under the corrected labels) follows from its 92% non-haven value share, not from subgroup counterpart rates. The 'home bias' reading rests on Danish-HQ groups having 70% of correction value against 56-64% of income or sales, a mild over-representation.

Evidence. AEA appendix (aea-appendix.pdf, created 2021-08-05) vs author appendix TWZ2023Appendix.pdf (modified 2023-07-05), page 5 rendered; workbook 'Table A2' (B4/B12 labels; D9, E9, D17, E17 formulas; C21 = 372/(210+372), C22 = 5/9); TWZ (2023) pp. 508-510.

Why this severity. The journal's own appendix reverses a result the paper lists among its five main findings; the authors' informal correction resolves the labels in the text's favour but cannot be verified without the micro-data, and the revenue split is an imputation, so C5 reduces to 'corrections of Danish-headquartered groups are more non-haven-heavy'.

The authors' response. The appendix on the authors' website (gabriel-zucman.eu/files/TWZ2023Appendix.pdf) carries hand-drawn corrections swapping the panel labels to match the text; the AEA-hosted appendix and the replication workbook retain the original labels.

6moderatelikely · newly identified here · documentation gap

The paper says it studies all of Denmark's transfer-price corrections, but an earlier presentation of the same data shows that about a fifth of the money involved had no identified partner country, and these cases appear to have been left out without saying so. Most corrections still involve high-tax countries however those cases are counted, but the share involving tax havens could be anywhere between roughly 15% and 35% rather than the stated 18%.

Technical detail and evidence

Why it matters, in detail. If the unclassified EUR 374m/yr is distributed like the classified corrections, C1 is unchanged. At the extremes the non-haven share of the full universe is 65.0% (all unknowns havens) to 85.5% (all non-havens), the haven share 14.5-35.0%, and haven corrections relative to MPN shifted profits 10.0-24.0%. Gross corrections become EUR 1,830m (+26%) and the Danish gain at 22% EUR 403m. The C3 net ranges from -EUR 16m (unknowns with the classified rate mix) to +EUR 69m (no foreign relief because no counterpart is identified), adding to the sign uncertainty in F1 and F3.

Evidence. TWZ (2017) 'EUR 600 Billion and Counting' slides 43-44 (gabriel-zucman.eu copy; slides 44-45 of the KU research-portal copy), bar heights measured by final/scripts/measure_2017_bars.py (cases 64.75/26.96/8.29; value 65.02/14.52/20.46; slide note: '65% of the value ... concerns a high tax country'); workbook 'Table 1'!C10 = D10 + E10; SKAT TP-redegoerelse 2015 Tabel 1-2 and 2014 Tabel 1; final/scripts/sensitivity.py. With 2008 (the year given in the NBER version and the Nov-2020 slides) instead of 2009, the published total would be 93% of the official figure but the total including the unknown block 117%, which is impossible; the 2009 reading with exclusion fits.

Why this severity. The headline composition result survives any allocation of the unclassified block (non-havens at least 65% of value), but the haven share and the 'only 10%' ratio become bounded rather than point estimates, totals and Danish revenue are understated by about 26%, and the sample is misdescribed as the universe.

7moderatelikely · newly identified here · overclaiming

The EUR 320 million gain for Denmark and EUR 333 million loss abroad assume that every correction sticks and is fully offset by the other country, yet the paper's introduction presents them as what actually happened. Danish official records show that many corrections are reduced or still in dispute years later, so the real amounts are smaller and the sign of the tiny net effect cannot be pinned down.

Technical detail and evidence

Why it matters, in detail. A MAP outcome in which Denmark keeps a share alpha of its claim and the partner relieves the same amount scales both sides and preserves the sign. The sign therefore depends on value-weighted asymmetries the evidence does not pin down: incomplete relief on non-haven corrections (s < 0.96 at 22%) makes the net positive (+EUR 19m at s = 0.9, +EUR 52m at s = 0.8), while lower sustained shares for haven corrections (plausible given Figure 3 and SKAT's 25% haven-project hit rate) make it negative (-EUR 37m if half are sustained). Danish loss-making entities (31% of the 2014 amount) also mean the present-value Danish gain is below rate x amount. Realised Danish revenue is likely 15-25% below EUR 320m given MAP reductions of 14% so far, with a further 23% of amounts still in MAP.

Evidence. Danish State Auditors (Rigsrevisionen 2014) Table 6: 422 adjustment cases 2002-12, DKK 48,936m of DKK 65,912m (74%) still outstanding in MAP or appeal, success 'not possible to assess'. Skatteministeriet overview (Nov 2020, as summarised by Kromann Reumert, Dec 2020): 2010-19 increases DKK 114.7bn, reduced by DKK 16.1bn via MAP, DKK 26.4bn still in MAP, DKK 23.3bn before the tribunal or courts. SKAT TP-redegoerelse 2014-15: revenue cannot be computed as rate x amount (loss carryforwards, joint taxation); loss-making companies 43% of 2014 cases. EY (2014) Denmark chapter: about 20 TP competent-authority cases received a year (vs about 44 non-haven corrections a year), '<5% of the cases remain unresolved', 90% of disputes go to MAP with appeals on hold. EY summaries of the OECD 2017 and 2018 MAP statistics. NBER WP 26899 p. 12 and fn. 13. Adjudicator sensitivity (final/scripts/sensitivity.py): at 22% the net turns positive if non-haven relief covers less than 96% of value (+EUR 19m at 90%); symmetric 30% MAP cuts leave the sign unchanged (-EUR 9m); if only half of haven corrections are sustained the net is -EUR 37m (-EUR 4m at 24.54%).

Why this severity. The conditionality is disclosed in the table and symmetric MAP reductions leave the sign unchanged, but the unconditional introduction language overstates what is shown, the Danish gross gain is probably overstated by at least 15-25%, and plausible asymmetries move the small net in either direction, so the claim that enforcement lowers global taxes is not established.

The authors' response. In-paper only: the Table 1 note labels the calculation 'if fully realized', and p. 507 cites completed MAPs and practitioner interviews as support. No response to the specific evidence was found.

8moderatelikely · newly identified here · overclaiming

The data show what kinds of corrections Danish auditors ended up making, not how they spent their time or what firms intended. Cases involving tax havens are, by the paper's own argument, harder and costlier to pursue, so a small share of corrections could still mean a large share of effort, and many corrections between high-tax countries involve deliberate valuation choices rather than innocent mistakes. The claim that this enforcement is wasteful is therefore an interpretation rather than a finding.

Technical detail and evidence

Why it matters, in detail. With 132 non-haven and 53 haven corrections, the haven share of resources is 53c/(132 + 53c) for a relative cost c per case; it exceeds one half for c > 2.49 (54.6% at c = 3). SKAT's figures show haven-targeted auditing with a hit rate one-third that of the loss-making-company project, consistent with gamma_L < gamma_H (the model's assumption) but equally with a rational allocation given lower yields. Because Figure 4 redeploys effort one-for-one in cases, its upper and preferred estimates are optimistic if haven cases are costlier; the zero-return lower bound is unaffected.

Evidence. TWZ (2023) pp. 499, 504 fn. 7, 510, 522-523; Danish State Auditors (2014) Table 3 (2013 plan: haven project 7.5 FTE for an estimated tax gap of DKK 100m; loss-making-company project 37 FTE, DKK 2,500m) and Table 4 (2010-13: haven-transactions project hit rate 25%, 10 of 40 cases, DKK 620m; loss-making companies 78%, 83 of 107, DKK 8.6bn; intangible valuations DKK 30.4bn of DKK 39.7bn) and Bilag (intangibles 'used for tax optimisation'); SKAT TP-redegoerelse 2014 (intangibles 38% of the amount; loss-making companies 43% of cases, 31% of the amount); workbook 'Data F4' (mean EUR 23.6m vs median EUR 3.3m per case).

Why this severity. The measured composition is unaffected, but the paper's central interpretation (enforcement resources crowded away from havens and spent correcting random high-tax mistakes, at a welfare cost) is inferred from outputs that cannot separate it from the alternative that haven cases are simply harder or are handled by other instruments.

The authors' response. In-paper: the conclusion says the evidence 'suggests'; pp. 510-511 note that behavioural responses are not modelled; Section V.C discusses one alternative explanation (authorities tolerating shifting to attract investment).

9minorconfirmed · newly identified here · internal inconsistency

The paper's check on which corrections firms appeal says it looks only at cases involving EU countries, but the chart and the computer code say the opposite. The main result, that firms appeal more often when a correction raises their total tax bill, is unaffected, but this particular check cannot be relied on.

Technical detail and evidence

Why it matters, in detail. Whether the restricted sample keeps or drops intra-EU cases reverses the stated identification logic (neutralising 'safety-net' appeals filed while a near-certain EU MAP runs), so the shift to +3.7pp cannot be attributed to removing safety appeals. The do-file's unweighted mean regressions (reg court_diff) versus weighted CDFs cannot be checked without the data.

Evidence. TWZ (2023) p. 508 and Figure 3 (p. 509); Online Appendix Figure A3; replication 'Master online.do' lines 38, 40, 53, 64 and 73.

Why this severity. Only the robustness panel (+3.7pp) becomes uninterpretable; the main comparison (+2.0pp for appealed cases vs -4.1pp for corrections) is unaffected and its direction is consistent with SKAT's low haven hit rate and EY's description of appeals as safety nets.

10minorconfirmed · newly identified here · arithmetic or transcription

Several equations in the paper's theoretical extensions contain algebra mistakes and leave out conditions needed for the results to hold. Fixing them does not change what the theory predicts; one fix actually makes the paper's warning about minimum taxes stronger.

Technical detail and evidence

Why it matters, in detail. Correct revenue from the N-bar largest corrections is N t gamma b (n - n^2), increasing in n on (0, 1/2), which delivers 'the tax authority with the highest capacity will invest more'. The minimum-tax multiplier t_H/(t_H - t_min) exceeds the printed 1/(1 - t_min) for any t_H < 1, so Proposition A2's adverse enforcement channel is stronger than stated, while the paper's caveat that direct minimum-tax gains may dominate still applies.

Evidence. TWZ (2023) pp. 515-521; Online Appendix B, eq. (15); adjudicator re-derivation; Auditor B numerical examples (scripts/reproduce.py).

Why this severity. The qualitative propositions survive under standard interior-solution assumptions; the corrections either support the stated comparative statics (the printed n - 2n^2 would reverse Proposition 4's capacity result for n > 1/4, the correct n - n^2 supports it) or strengthen the paper's own mechanism (the minimum-tax effect is larger than printed).

11minorconfirmed · newly identified here · misrepresentation of source

To put the corrections in context, the paper borrows an estimate of profit shifting 'between high-tax countries' that in fact includes several European tax havens, and mixes estimates from different years and models. This affects only background comparisons, not the paper's main numbers.

Technical detail and evidence

Why it matters, in detail. Panel A is not a mutually exclusive geographic decomposition (EU havens appear in both sources), and its years differ (2012 vs 2015). Haven corrections relative to haven shifting: 266/2,670 = 10.0% (MPN) vs 266/1,349 = 19.7% (Alvarez-Martinez, whose haven channel excludes EU havens).

Evidence. Alvarez-Martinez et al. (2018) CESifo WP 6870, Table 2 (Denmark: gains 133.0, losses -19.3, net 113.8, havens -337.2); workbook 'Table 1'!D5 = -113.8 x 4 and 'Table A1'!F22 = 133 x 4; TWZ (2023) pp. 500 and 504-505.

Why this severity. Context only: the Danish inter-country flows are small (net inflow EUR 455m) and no measured correction share changes; using Alvarez-Martinez's haven estimate would raise the 'only 10%' ratio to about 20%, still a small fraction.

12minorconfirmed · newly identified here · version instability

Between the working paper and the journal article, the years covered by the data, some revenue figures and several cautionary statements changed without explanation. These changes do not alter the main finding but make the published numbers harder to trace.

Technical detail and evidence

Why it matters, in detail. The NBER Danish column implies different rates for haven and non-haven cases (19.2% vs 22.2%), the published one a flat 22%; neither matches the 23.5-25% in force. The removed 30% MAP-reduction statement bears directly on the realised-revenue claim (F3).

Evidence. NBER WP 26899 pp. 2, 9-13 and Table 1; TWZ2023bSlides.pdf ('Covers the years 2008 and 2014-15'); TWZ (2023) pp. 498 and 503-507; DataCite record for 10.3886/E146321V1 (temporal coverage 2009-2015).

Why this severity. The changes do not alter the composition result; their substantive consequences (rate choice, realisation caveats) are graded under F1 and F3.

13minorconfirmed · newly identified here · arithmetic or transcription

The paper contains a number of small errors: wrong signs, mislabelled columns, a broken data link and figures quoted for the wrong years. None changes the conclusions, but together they make the work harder to check.

Technical detail and evidence

Why it matters, in detail. Using actual 2015 Danish corporate tax revenue (about EUR 8.28bn) instead of the constructed EUR 7.34bn lowers the Figure 4 world gains to 2.19/1.08/0.74%. The haven-rate inconsistency between Tables 1 and A1 changes the haven foreign loss by EUR 2.2m.

Evidence. TWZ (2023) pp. 498, 502-506, 511-513 and 525; Online Appendix Table A1; workbook 'Table 1', 'Table A1', 'DataF1', 'DataF5-6' and 'Data F4'!V16; doi.org resolution test (404 vs 302 redirect); OECD Revenue Statistics (Denmark, tax 1200, 2015: $9.19bn); TWZ2022.xlsx Table 3; Danish State Auditors (2014) Table 4; SKAT TP-redegoerelse 2014-15; JTPF/013/2012/EN p. 2.

Why this severity. Individually small and none changes a conclusion; the Figure 4 denominator choice moves the percentages by about 11%.

14minorlikely · newly identified here · overclaiming

The appendix claims that recent reforms cut the time to settle tax disputes from 40 months to under 7, but this compares old, long-running cases with new cases that have only just begun, so it does not show that the reforms sped things up.

Technical detail and evidence

Why it matters, in detail. A cohort-truncated mean of completed new cases cannot identify a treatment effect; the claimed fall of more than 80% is not supported by the cited statistics.

Evidence. Online Appendix A p. 1 and fn. 20; NBER WP 26899 pp. 8-9; EY Global Tax News, 'OECD releases 2017 mutual agreement procedure statistics' (2018).

Why this severity. Peripheral motivation for Proposition A1 in the appendix, with the truncation caveat disclosed in a footnote; no core result depends on it.

The authors' response. Footnote 20 notes that 'the average time for cases after 2016 is under-estimated due to some cases being still ongoing'.

15minorplausible · previously known · external inconsistency

The claim that Denmark's corrections recover only a tenth of the profits shifted to tax havens depends on the authors' own estimate of how much is shifted, which other researchers think is too high. Even with lower estimates, the share recovered stays small.

Technical detail and evidence

Why it matters, in detail. Ratio = 266/S. For S scaled to MPN's lower bound (0.6 x 2,670) or halved (Blouin-Robinson-type adjustment), the ratio is 17-20%; combined with the unclassified block of F2 it could reach about 40% at the extreme. A narrower haven list (Hodge) would raise, not lower, the non-haven share of corrections.

Evidence. Workbook 'Table 1'!E5; TWZ2018.xlsx and TWZ2022.xlsx Denmark ($2.9617bn shifted; 5.73% of reported profits; 8.43% revenue loss); corpus offshore-havens-09 (Blouin & Robinson 2025, Journal of Public Economics 252: 105512; corpus entry marked unverified), -11 (Fuest, Hugger & Neumeier 2022, JEBO 194), -12 (Fuest, Greil, Hugger & Neumeier 2025, JEEA 23(5)), -13 (Forstater 2018, CGD note), -14 (Hodge 2018, Tax Foundation); TWZ (2023) fn. 9 (Jansky & Palansky 2019: 7% of the Danish base).

Why this severity. Even a benchmark 40-50% lower leaves haven corrections at roughly 17-20% of estimated haven shifting, still a small fraction; the composition result does not depend on the benchmark.

The authors' response. The authors respond to these critiques in the Missing Profits of Nations paper (REStud 2023), not here; this paper notes that its Danish estimate is consistent with Jansky & Palansky (2019).

16minorplausible · newly identified here · methodology

The paper compares the tax rates of the countries targeted by Danish auditors with those of all countries where Danish firms have affiliates, but appears to use tax rates from different years for the two groups and does not test whether the difference is statistically reliable. A cleaner version in the appendix shows the same pattern, so the conclusion probably holds.

Technical detail and evidence

Why it matters, in detail. Mixed vintages could move the ORBIS mean by roughly 1pp (US links at -5pp under 2018 rates vs about -15pp under 2009-15 rates), so the 1.8pp statutory-rate gap is imprecisely measured; with about 185 cases and a standard deviation near 7.3pp the naive t is about 3.3, which clustering of corrections within groups would lower.

Evidence. TWZ (2023) Figure 2 (p. 506), rendered at 200 dpi; replication 'Master online.do' lines 20, 32-34 and 69-70; Auditor A digitisation (TP-case mean -4.23, ORBIS -2.28).

Why this severity. The direction of C2 is supported by the same-vintage effective-rate version (Figure A1: -4.0 vs -2.4) and the FDI-weighted benchmark (-1.2); ORBIS under-coverage of haven affiliates and the zeroing of confidential haven cells in the FDI data bias the benchmarks against the paper.

17minorplausible · newly identified here · external inconsistency

The paper says only about 1 in 100 transfer-pricing specialists work for governments, based on a LinkedIn search, but the survey it cites as confirmation lists more government staff than that search found. The true share is probably somewhat higher, though still small.

Technical detail and evidence

Why it matters, in detail. If public TP staff number about 5,000-7,000 rather than 3,368, the public share is about 1.5-2% and the private-to-public ratio about 50-70 rather than 100; LinkedIn coverage biases both counts.

Evidence. TWZ (2023) Figure 1 and fn. 4-5; workbook 'DataF1'; EY (2014) chapters (e.g., China about 1,000 TP specialists; Denmark 100 FTEs).

Why this severity. A context figure only; the qualitative resource asymmetry between private advisers and tax administrations is not in doubt.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

With defensible corrections, the best estimate of the net global effect is small and positive; it is negative in only 3 of 120 sensitivity combinations. — The 120-cell grid varies only parameters that raise the net (higher Danish rate, incomplete foreign relief, MAP withdrawal, an unknown block without relief). It omits equally defensible adjustments that lower it: contemporaneous foreign rates if the workbook's are 2018 vintage (+2pp on non-haven foreign rates returns the net to about zero at 24.54%), lower sustained shares for haven corrections (half sustained gives -EUR 4m even at 24.54%), Danish loss positions (present-value gain below rate x amount), and statutory rather than effective rates for ordinary Belgian, Dutch or Luxembourg counterparts. The defensible conclusion, adopted in F1 and F3, is a net of about zero with undetermined sign.
The appendix's statement that initiated MAPs 'rose 59%' from 2016 to 2018 is not reproducible (the workbook data give +47.7%). — The 59% reproduces from OECD's all-case aggregates (1,496 cases started in 2016, 2,385 in 2018, +59.4%, as reported in EY's summaries of the OECD 2017 and 2018 releases); +47.7% is the sum of jurisdiction-reported TP cases in the workbook, a different series. Only the accompanying '87% non-haven' attribution mixes series (it uses TP-only per-jurisdiction changes); this is noted under F5.
The digitised Figure 2 contains an 'impossible' +27pp differential, above Denmark's maximum rate. — Not established: corrections initiated in 2009 can concern income years 2005-06, when Denmark's rate was 28% (30% before 2005), so +27/+28pp against a near-zero-rate counterpart is possible if income-year rates are used, and the value comes from digitising the tail of a CDF. It is not used in F13.
Denmark's 2018 OECD MAP outcomes (63% of closed TP cases fully eliminating double taxation) show that the paper's 'more than 90 percent of MAPs result in an agreement' is not borne out. — Partially rejected. The paper's statement is global, and Denmark's 65 closed TP cases include foreign-initiated cases; in Denmark's own breakdown only 3% ended with 'no agreement', EY (2014) reports fewer than 5% of Danish cases unresolved, and OECD TP-only statistics show about 85% fully resolved in 2019. OECD all-case statistics for 2017-18 (81-84% resolved, about 60% by agreement) do indicate that the paper's figure is high; the point is retained in weakened form in F3.
Danish MAP volumes (about 25 TP MAP cases closed a year against about 62 corrections) show that full foreign offsets cannot have occurred. — Not established. MAP counts include foreign-initiated cases and one correction can generate several MAP cases, while large cases (which dominate value) are the ones most likely to go to MAP; case counts do not translate into a value-weighted relief share. The volume evidence is consistent with incomplete relief for smaller cases, which F3 records as an uncertainty rather than a demonstrated shortfall.
Halving the EU MAP counts is not a valid correction of the haven proportion; the substantive point is not that the ratio has been doubled. — The correction is not uniform halving: de-duplicating the largely symmetric bilateral matrix counts non-haven pairs once instead of twice and shows that about 19% of distinct pending cases involve an EU haven, which is also the upper bound on the haven share of cases initiated by high-tax members. The reported 10.7% is therefore neither the distinct-case share nor an identified directional share; F5 adopts both points.
The 2017 deck's 'Counterpart unknown' category does not justify a sample-omission finding, because public annual summaries cannot be reconciled with the confidential sample. — Excluding the 'Counterpart unknown' block from the 2017 value distribution reproduces the published 81.74% to four digits, and the published total plus that block equals 98.5% of SKAT's official 2009/2014/2015 TP increases (78.4% without it). Case counts cannot be reconciled because SKAT changed its counting unit in 2015, but values can (F2).

Audit notes

What reproduced. Reproduced exactly: Table 1 panels B-C and Table A1 from the workbook's hard-coded aggregates (82/18% of value, 71.4/28.6% of cases, EUR 320.3m/333.3m/-13.05m, -EUR 49.3m), Figure 4 (2.48/1.22/0.84% and -1.58/-3.10/-3.56%), Figure 1 (1.03%; $24.0bn), the Figure 5 counts, Figure 7's 8.28% (10.45% with Switzerland), the Alvarez-Martinez and MPN inputs, and the OECD 2018 per-jurisdiction inputs; Figure 6's source matrix reproduces within two records (597/71/69/3 vs 595/71/71/3). Re-estimated: the net global effect at sample-year Danish rates (+EUR 8.8m to +EUR 30.6m; break-even 22.90%) and Figure 4 under corrected rates (preferred about 0.8%, lower bound about 0.4%); the de-duplicated EU MAP haven share (about 19%); the 2017 precursor shares (value split excluding 'unknown' = 81.74%, matching the paper) and the reconciliation with SKAT totals (98.5% including the unclassified block). Not reproducible: anything requiring the confidential Danish micro-data or ORBIS (Figures 2-3 and A1-A4, case-level rates and classification, the Table A2 split and its labels) and Figure A5's 13%. The workbook holds aggregates only, so reproduction verifies arithmetic, not data construction; the openICPSR deposit could not be accessed.

Limits of this audit. The confidential Danish micro-data (TP corrections, court cases, completed MAPs), the ORBIS links and the KPMG and effective-rate input files were unavailable, so the foreign-rate vintages, the unclassified-counterpart block and the Table A2 labels could not be verified at case level. The openICPSR deposit (10.3886/E146321V1) was blocked by Cloudflare; the author-site zip (December 2020) was used and may differ from it. The unclassified-block inference rests on bar heights measured on 2017 slides (about +/-0.2pp) plus value reconciliation with SKAT totals; SKAT's 2015 change of counting unit prevents a case-count reconciliation. Skatteministeriet's 2010-19 MAP and appeal figures were read via a law-firm summary (Kromann Reumert), and OECD global MAP outcomes and aggregate counts via EY summaries, not the OECD originals. Rate-vintage inferences from Figure 2 are visual. Only four OECD per-jurisdiction reports were inspected. LinkedIn and Glassdoor counts were not re-queried, and not every literature citation was audited.