Annette Alstadsæter, Niels Johannesen, Ségal Le Guern Herry, Gabriel Zucman · Journal of Public Economics 206: 104587

Tax Evasion and Tax Avoidance

16 problems found: 6 moderate · 10 minor

What the paper claims

Taxes paid (tax liabilities 'claimed by the taxpayer') by amnesty participants rise about 30% at the time of disclosure.
The increases in reported wealth, income and taxes are sustained over the four years observed after disclosure.
After stopping to evade, taxpayers do not start avoiding more (low or zero substitution between evasion and avoidance); the conclusion states that significant substitution can be ruled out.
Before disclosure, disclosers paid less tax than equally wealthy non-disclosers (about -20%); after disclosure, slightly more (about +5%).
Disclosers repatriate most of the disclosed assets.
Policy: cracking down on evasion by the wealthy raises revenue, progressivity and equality; the annual tax increase is about 2% of disclosers' total net wealth, 'much more than the wealth tax at around 1% of reported net wealth', so enforcement 'can potentially raise more revenue than even large increases in nominal rates'.

Every problem found

1moderateconfirmed · newly identified here · overclaiming

The study shows convincingly that people did not simply swap illegal hiding for legal tax tricks one-for-one: their taxes went up and stayed up. But the paper goes further and says it can rule out any significant shift to legal tax avoidance. Its tests are not sharp enough for that. Some avoidance routes are measured imprecisely, moving abroad is barely measured at all, and the one clear response, setting up holding companies, is played down.

Technical detail and evidence

Why it matters, in detail. Observed tax growth equals G - A, where G is the mechanical gain at unchanged avoidance and A the offset. The paper estimates G - A (about 0.21-0.28 lp) but never G. With the compact CI of +16% to +32%, offsets of a quarter to a third of a mechanical gain of 0.30-0.40 lp cannot be rejected. The margin-specific tests rule out only large shifts on housing and holding companies. The unlisted-share test cannot rule out shifts of a size that would offset a quarter of the wealth tax on disclosed assets, and the emigration test has essentially no events. Low substitution is supported; zero or insignificant substitution is not established.

Evidence. Abstract; Intro p.2; Conclusion p.16; Table 2 p.12 (unlisted -0.132 (0.112), col. 5 -0.027 (0.112); holding +0.011 (0.004)); Fig. 4D p.10; Figs 6 and 8 pp.13, 15; Fig. A8 (Online Appendix p.47); Table 1 founding rate 0.69%. AvoidanceCLEAN.do: 'gen housing = a_housing_condo + a_housing_leisure + a_f_housing'. NBER WP 35505 (Alstadsaeter, Johannesen, Le Guern Herry & Zucman 2026) p.4: voluntary disclosure 'with limited success (Langenmayr, 2017; Johannesen et al., 2020; Alstadsaeter et al., 2022)'. scripts/adjudicator_checks.py section F.

Why this severity. The qualitative finding stands: there is no large offset and no detectable rise on the measured margins. What is overstated is the precision. Moderate partial substitution, or substitution on unmeasured margins, is not excluded.

The authors' response. No response to these specific points. The body text is more cautious ('we cannot exclude that unobserved margins change', p.2; 'suggestive that substitution ... is low or zero', p.10) and reports the aggressive-quintile evidence (p.13).

2moderateconfirmed · newly identified here · methodology

About half of the roughly 1,500 people who came forward did so after 2013, when the data stop, so the study never sees what they did afterwards. The finding that taxes stay higher for four years rests on only about 300 people who came forward in 2008-09. The finding may well hold for the later group, but the paper does not show it.

Technical detail and evidence

Why it matters, in detail. Treatment effects at k are averages over cohorts with disclosure year <= 2013 - k, weighted toward the 2009 cohort; there is no cohort-balanced or cohort-specific estimate. Heterogeneity between the information-on-request and CRS regimes (for example, more sophisticated evaders delaying until 2014-16, or different post-disclosure options) cannot be assessed. The four-year persistence is identified from 304 individuals.

Evidence. AJLZ 2022 fn 17 p.6, fn 30 p.12, Fig. 1 p.5 (scripts/fig1_counts2.py: 1, 15, 65, 223, 143, 89, 88, 142, 234, 286, 196 for 2006-2016; exact integers). Skatteetaten 7 Feb 2017 new-case table: 2013-2016 = 1,423 of 1,905. NBER WP 35505 Section 4.3 p.11. Corroboration of persistence in a CRS-era setting: Baselgia (2026, JPubE 258; SSRN 5109959 abstract), Swiss amnesty participants' reported wealth +50% with effects persisting in the medium run.

Why this severity. This scope limitation is disclosed only in a footnote. All effects concern the pre-CRS half of the sample, and persistence beyond two years concerns a fifth to a third of it. There is no direct evidence that later cohorts behave differently, and Swiss CRS-era evidence on reported wealth points to persistence, so the core finding is narrowed rather than overturned.

The authors' response. Disclosed in fn 17 (p.6) and fn 30 (p.12); no further discussion.

3moderatelikely · newly identified here · documentation gap

The paper's main number, taxes rising about 30%, compares taxes after people came forward with what they 'claimed' before. But Norwegian tax records do not store a 'claimed' tax, and the paper never says how it obtained one. The authors' earlier computer code estimated it with a fixed formula, so part of the 30% was built in by the researchers rather than observed. The formula looks reasonable, so the true figure is probably similar, but no reader can check it.

Technical detail and evidence

Why it matters, in detail. If the 2022 outcome is built like the 2017 one, pre-disclosure log claimed tax is log(A - 0.02276 D) and post-disclosure it is log(A'). So beta_k for k >= 0 equals the observed change in log A plus the imputed term [log A - log(A - 0.02276 D)]. Under zero substitution the observed change is about zero, and the 0.24-0.28 lp jump is the imputed term itself. Only the path of assessed taxes before and after disclosure tests substitution, and the paper does not report it. The persistence from k=0 to k=4 is observed, since D = 0 after disclosure. The average bias looks small (2.276% imputed vs 2.33% official per unit of disclosed wealth-year). Individual jumps can be biased either way by the zero floor, the uniform implied 4.2% return, wealth-tax thresholds and late-closed cases; the net effect cannot be quantified without microdata.

Evidence. AJLZ 2022 Section 2.1 p.3 and Section 4.1 p.8; no construction described in the paper, the Nov 2021 manuscript (gabriel-zucman.eu/files/AJLZ2021.pdf) or the Online Appendix. AJZ2017Programs.zip (gabriel-zucman.eu), norway/AvoidanceCLEAN.do, block '* Construct p_tax (claimed tax liabilities) *': 'gen p_tax4 = tax_all'; 'replace p_tax4 = max(0, tax_all - 0.02276 * da_wealth2)'; 'replace p_tax4 = max(0, tax_all - 0.01776 * da_wealth2) if avoid_80reduction == 1'. norway/makedata2_wealthCLEAN.do: tax_all labelled 'sum of all assessed taxes'; 'gen da_wealth = netwealth - p_netwealth'; late-closed cases update netwealth only. AJZ2017.xlsx sheet T4(raw) cell G6 = 0.2218 and G7 = (0.0317) for log_p_tax4. Calibration: Skatteetaten press release of 7 Feb 2017, NOK 1.5bn of increased tax on NOK 64.5bn of accumulated disclosed wealth-years = 2.33%, vs the 2.276% imputation. Online Appendix Fig. A7, p.46.

Why this severity. The direction and persistence of the tax rise come from observed post-disclosure assessed taxes and from observed jumps in wealth and income, and the imputation rate matches official aggregates (2.28% vs 2.33%), so the average bias is probably small. But the headline 30% is partly an imputed quantity whose construction is undisclosed, individual-level errors cannot be quantified, and the 'mechanical expectation' check offered as corroboration carries no information.

4moderatelikely · newly identified here · internal inconsistency

The paper says the crackdown raised each person's yearly taxes by about 2% of everything they own. It calls that much more than Norway's roughly 1% wealth tax, and uses it to argue that enforcement can beat raising tax rates. Using the paper's own figures and Norway's tax rates, the real gain is more like 0.4-0.9% of wealth. That is roughly what doubling the wealth tax would raise from these people, not much more. The main results are unaffected, but this policy comparison is overstated.

Technical detail and evidence

Why it matters, in detail. Fig. 3D is a winsorised mean of individual T/W ratios. Under the paper's stated mechanism each individual's change in T/W is at most about 0.02276 x h_i, so the mean is 0.7-0.9 pp for E[h] = 0.31-0.40. The dollar gain per discloser is about $19-39k a year (0.34-0.68% of mean market wealth). That is the same order as the mechanical yield of an extra 1% wealth tax on the same people's reported wealth ($30.8k, 0.54% of market wealth). The comparison is therefore not reversed, but 'much more than' is unsupported. Something other than taxes on the disclosed assets must drive the 2-3 pp: an artefact of the F1 construction, hidden non-capital income, cohort composition, or a denominator that differs from its description. Household-level hidden shares may understate individual-level shares for married disclosers, which narrows the gap without closing it.

Evidence. AJLZ 2022 Intro p.3; Section 4.1 p.8; Fig. 3D p.9 (scripts/fig3_digitize.py: 1.96, 1.72, 2.69, 3.02, 3.12 pp for k=0..4). AER 2019 (Alstadsaeter, Johannesen & Zucman, AER 109(6)) Table 1 col. 9 and p.2088. Table 1 means: claimed tax $80,948; market wealth $5,680,021; tax-value wealth $3,076,394. Skatteetaten 7 Feb 2017: NOK 1.5bn / NOK 64.5bn. scripts/adjudicator_checks.py section B.

Why this severity. The estimated tax response itself is unaffected. The paper's quantitative policy comparison (enforcement versus rate increases) rests on this number, which is overstated roughly 2-4 times.

5moderatelikely · previously known · overclaiming

The people studied chose to come forward. The paper's check that they are typical only compares how wealthy they are with leaked bank-client lists, and the two groups were already almost identical on that. The authors' own earlier work suggests the most aggressive evaders are less likely to come forward. So the finding that people did not switch to legal tax avoidance may not apply to the evaders who stayed hidden.

Technical detail and evidence

Why it matters, in detail. Reweighting on nine wealth bins with factors of 0.87-1.19 cannot move estimates appreciably whatever the true selection. Selection on evasion intensity or tax aggressiveness, which the authors' own AER evidence suggests, would make the complier substitution parameter a lower bound for the population of offshore evaders if aggressive evaders substitute more, as Fig. 8 hints. The policy-relevant population, evaders who do not come forward, is not covered.

Evidence. Intro p.3; Section 3 p.8; Table 2 col. (7); Online Appendix Table A1 p.50 (scripts/adjudicator_checks.py section E); AER 2019 p.2088 and Table 1 cols 3 and 9; AJLZ 2022 Fig. 8 p.15; Leenders, Lejour, Rabate & van 't Riet (2023), JPubE 217:104785.

Why this severity. The estimates are internally valid for compliers, as the paper notes (p.8). The generalisation in the abstract and conclusion depends on selection that the robustness check cannot address.

The authors' response. The paper acknowledges that estimates are 'local to this subsample' and that selection on unobservables is not addressed (pp.3, 8). AER (2019, p.2088) argues self-selection by wealth 'is not massive'. No reply to Leenders et al. was located.

6moderatelikely · newly identified here · methodology

One way rich people avoid tax is to move abroad, and the paper says disclosers did not do this. But its measure of moving abroad records only about one in ten to one in twenty-five of the departures that official Norwegian statistics show. Apparently this is because people who leave drop out of the data. So the paper cannot really tell whether disclosers moved abroad, because it does not see most moves.

Technical detail and evidence

Why it matters, in detail. Given an annual adult emigration hazard of about 0.2-0.5%, the indicator's 0.02% base rate implies it records only about 4-11% of emigration events. The precise null (|coefficient| <= 0.0002) is then an artefact of the risk set, not evidence of no response. Because emigrants exit the panel, the tax-liability effects are also estimated on stayers, a survivorship channel that would hide any revenue loss from post-disclosure emigration.

Evidence. AJLZ 2022 Table 1 p.6; Section 2.4 p.5 ('by contrast, they were less likely to migrate'); fn 17 p.6; Table 2 p.12; Fig. 4A p.10. SSB StatBank table 05756 queried 2026-10-25 (scripts/ssb_emigration.py; data /mnt/zdata/downloads/ajlz2022-final/ssb/emig_05756.json). AJZ2017Programs norway/AvoidanceCLEAN.do ('keep if livingresident == 1'; 'gen livingresident = 0; replace livingresident = 1 if ind_status==1'); AJZ2017.xlsx T4(raw): B6/B7 -0.0004 (0.0010), 8,316,826 obs, 'All'; H6/H7 -0.0000 (0.0001), 8,177,190 obs, 'Living resds'; NBER WP 23772 Table 4 col. 8 reports -0.0004 (0.0010). Draft of 8 Oct 2019 (nielsjohannesen.net Avoidance_FullPaper.pdf) p.12 and Table 1: 'Around 0.1% of non-disclosers emigrated ... almost by construction'; Emigrates 0.00% / 0.11% / 0.13%.

Why this severity. This removes one of the four measured avoidance margins, and the most direct way for the wealthy to escape Norwegian taxes, from the evidence. Few disclosers probably emigrated in 2008-13, so the effect on the tax estimates is likely small. But the paper's claim of no emigration response, and its statement that disclosers were less likely to migrate, rest on a test with almost no events.

7minorconfirmed · newly identified here · internal inconsistency

To argue that people disclosed all their hidden money, the paper compares two percentages measured in different ways, and uses a 40% figure from a leaked bank instead of its authors' own estimate of about one third for these same people. Done correctly, the numbers still fit full disclosure, and they imply that even more of the money came home than the paper says. So the paper's conclusions survive, but its reasoning here is flawed.

Technical detail and evidence

Why it matters, in detail. Writing B for reported tax-value wealth, M for reported market wealth and H for hidden wealth: H/(B+H) = 0.394 is not H/(M+H). With Table 1 means (B = $3.08m; market wealth including hidden assets, M+H = $5.68m), a 65% jump implies H of about $2.0m, i.e. about 35% of market wealth. That lies between the authors' own 31% and HSBC's 40%, closer to the former. Conversely, h = 0.31 predicts a jump of 0.457 lp, inside the estimate's CI. Neither benchmark discriminates sharply between full and substantial-but-incomplete disclosure.

Evidence. AJLZ 2022 p.8 ('65%/165 ~ 40%'; rendered page image) and p.14; AER 2019 Table 1 col. 9 and p.2088; NBER WP 23772 p.33 ('one third'); scripts/adjudicator_checks.py section C.

Why this severity. Both auditors rated this moderate; I downgrade it because the correction strengthens the paper's repatriation conclusion ('more than 60%' becomes about 74-79%), and full disclosure remains compatible with the estimates. The argument fails, not the conclusion.

8minorconfirmed · newly identified here · internal inconsistency

Different parts of the paper give somewhat different numbers for the same results, generally picking the larger ones for the summary. The tax increase is better described as roughly 24-32% than as a flat 30%. This does not change the story.

Technical detail and evidence

Why it matters, in detail. The abstract's '30%' corresponds to the dynamic coefficients for years 0 to 4 (0.243-0.313 lp, +27.5% to +36.7%), not to the paper's own summary estimate (0.212 lp, +23.6%, CI +16% to +32%). The introduction's income figure exceeds the paper's own point estimates by 5-8 pp.

Evidence. Abstract; Intro pp.2-3; Section 4.1 p.8; Section 4.5 p.14; Table 1 p.6; Table 2 p.12; Figs 3 and 5 (digitised); Online Appendix Fig. A9; scripts/adjudicator_checks.py sections A and H.

Why this severity. Each number is defensible as a rounding of some estimand, so conclusions are unaffected. But the abstract's 30% sits at the top of the paper's own range of about 24-32%.

9minorconfirmed · newly identified here · internal inconsistency

The paper says a small fall in housing investment was not statistically meaningful, but by its own main table it was. Since the fall points away from tax avoidance, this does not weaken the paper's conclusion.

Technical detail and evidence

Why it matters, in detail. Baseline housing: -10.9% (CI -20.1% to -0.5%); the 95% upper bound excludes any increase in the tax value of housing on the intensive margin.

Evidence. Section 4.2 p.10; Table 2 p.12; fn 28 p.11; scripts/adjudicator_checks.py section A.

Why this severity. The sign is the opposite of substitution, so the correction, if anything, favours the no-substitution reading, subject to the foreign-housing caveat in F3.

10minorconfirmed · newly identified here · arithmetic or transcription

A side comparison with the US programme uses US totals from a longer period than stated, which makes Norway's programme look about three times as large per person when, with those numbers, it is about twice as large. It does not affect the main results.

Technical detail and evidence

Why it matters, in detail. The footnote's period label is inconsistent with its figures. The '3x' holds only with the 2012 totals the footnote does not quote.

Evidence. AJLZ 2022 fn 6 p.4; NBER WP 24366 p.5 and reference 'IRS. 2014. IRS Offshore Voluntary Disclosure Efforts Produce $6.5 Billion; 45,000 Taxpayers Participate'; World Bank SP.POP.TOTL; scripts/adjudicator_checks.py section G.

Why this severity. An illustrative footnote with no bearing on the core findings.

11minorconfirmed · newly identified here · documentation gap

The paper says it left out 'a small number' of people whose cases were dropped. The authors' own earlier appendix shows that this was about one in four of everyone who came forward. Leaving them out makes sense, but the description is misleading.

Technical detail and evidence

Why it matters, in detail. The sample conditions on the authority's post-disclosure finding of non-negligible evasion, which removes about a quarter of participants. The estimates therefore describe confirmed, non-trivial evaders, a fact readers of 'a small number' would not infer.

Evidence. AJLZ 2022 Section 2.2 p.4; AJZ 2017/2019 Online Appendix Section G.1 (AJZ2017Appendix.pdf); Skatteetaten 7 Feb 2017; scripts/adjudicator_checks.py section H.

Why this severity. The exclusion is appropriate for the research question and does not bias estimates for evaders. The issue is an inaccurate description of the sample.

12minorconfirmed · newly identified here · version instability

Between the earlier and final versions, some statements were changed without explanation, for example from 'no sign' of people setting up holding companies to a clear increase. The main numbers barely moved, but readers are not told why the interpretation changed.

Technical detail and evidence

Why it matters, in detail. Revisions without comment of the benchmark used to validate full disclosure, and of the characterisation of ex-ante avoidance, reduce the evidentiary weight of these auxiliary arguments. The holding-company result in particular changed from a null to a significant response.

Evidence. NBER WP 23772 pp.33-34 and Table 4; AJZ 2017 Online Appendix Table G.7; drafts of 8 Oct 2019 and 28 Dec 2019 (Table 1, p.12); AJLZ 2022 Section 2.4 p.6, Fig. 2 p.7, Section 4.1 p.8, Table 2.

Why this severity. The core estimates are stable across versions (wealth 0.456 to 0.425, income 0.176 to 0.180, taxes 0.222 to 0.212); the changes concern framing and secondary benchmarks.

13minorconfirmed · newly identified here · documentation gap

The paper describes what kinds of assets people were hiding, but for most of the hidden money the type is unknown, so these descriptions rest on a small part of it. This has no effect on the main results.

Technical detail and evidence

Why it matters, in detail. Composition statements describe the classified minority of disclosed wealth; if the 72-85% that is unclassified differs in composition, the statements may not hold.

Evidence. Section 2.2 p.4; fn 9; Online Appendix Figs A2 (p.41) and A3 (p.42), read from rendered pages.

Why this severity. These are descriptive claims; the main analysis does not use the breakdown.

14minorconfirmed · newly identified here · misrepresentation of source

Some references point to the wrong paper or are missing, one sentence describes a result backwards, and one chart label is wrong. These are editing mistakes that do not change the findings.

Technical detail and evidence

Why it matters, in detail. These errors hinder tracing the HSBC benchmark (relevant to F7) and invert the verbal description of the emigration coefficient. No estimate is affected.

Evidence. AJLZ 2022 pp.1, 3, 8, 9, 15 and reference list p.16; Online Appendix Table A1; rendered page images of Fig. 4A and Fig. 8.

Why this severity. Typesetting and editorial errors; the intended meaning can be recovered.

15minorconfirmed · newly identified here · misrepresentation of source

The paper gives the wrong date, by about a year, for the international agreement on automatic sharing of bank information. It does not affect the results.

Technical detail and evidence

Why it matters, in detail. This is a chronology error in the institutional narrative. Anticipation of the CRS from 2013 is plausible, so the 2013 marker can be defended as a commitment date but not as a 'signature'.

Evidence. AJLZ 2022 p.4 and Fig. 1 note p.5; Spanish government release of 29 Oct 2014 ('54 countries and territories agree to automatic exchange of tax information as from 2017'); MCAA signatory list dated 29 Oct 2014; Norway's MCAA copy at regjeringen.no.

Why this severity. Treatment is defined by individual disclosure dates, not the treaty date, so no estimate is affected.

16minorlikely · newly identified here · internal inconsistency

Two parts of the paper that should show the same estimate of money brought home give noticeably different values, about 9% versus about 6% of wealth a year. It does not change the conclusion that most hidden money came home, but one of the two is likely mislabelled or computed differently.

Technical detail and evidence

Why it matters, in detail. An unbalanced panel can make the compact post-dummy differ from the simple mean of dynamic coefficients. But the gap is about 2 SE and appears only for the transfer outcomes, which suggests a different scaling or sample in Table 2 or in Figs 6-8.

Evidence. Table 2 p.12; Fig. 9A p.15 (visual reading: 0.072, 0.076, 0.050 at k=0-2; pre-period about 0.002-0.004); auditor A's digitisation of Figs 6-9; scripts/fig3_digitize.py for the tax comparison.

Why this severity. This is a discrepancy of about 45% in a secondary repatriation estimate. The cumulative 25% repatriation figure is computed from Fig. 9A itself and is unaffected.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

I1's framing that the headline is circular, and that the 30% 'is close to an assumption rather than a measurement'. — Only partly accepted. The imputation affects only the pre-disclosure level. The post-disclosure path of assessed taxes and the jumps in wealth and income are observed, and the 2.276% rate matches official aggregates (2.33%), so the conclusion is not assumed. The finding is retained as F1, recategorised from circularity to documentation_gap, with the near-tautological 'mechanical expectation' check noted.
I2's statement that, once corrected, the per-discloser gain (about 0.7-0.9% of total wealth) 'reverses the paper's comparison' with the wealth tax. — Overstated. The paper's benchmark is 1% of reported tax-value wealth, about 0.54% of disclosers' market wealth (Table 1). The corrected gain of 0.34-0.68% (up to 0.9% on statutory bounds) is of the same order, so 'much more' is unsupported but a reversal is not established. The rest of I2 is retained as F2.
I10: the small pre-trend dip at the reference year is a separate problem. — Not retained as a standalone issue. Only one of nine pre-period log coefficients (wealth k=-3: +0.047, CI 0.003-0.092) is marginally significant, which is consistent with chance; the log tax and income pre-trends are flat. The extensive-margin V-shape in Fig. A7 is plausibly produced by the zero-floor construction and is covered under F1.
I6(e): a ratio-of-means benchmark (+34-40%) above the +23.6% estimate indicates that a partial offset cannot be excluded. — This is not a like-for-like comparison. A ratio of means is dominated by the largest disclosers (Fig. 6 tax effects rise from 0.04 to 0.60 lp across disclosure-size quintiles), whereas the estimate is a mean of individual log changes. Only the narrower point, that no benchmark is computed, is retained in F3.
I9's explanation that the 1.45 ratio between Table 2 and Fig. 9A transfer estimates equals 1/(1-0.31), i.e. a denominator excluding disclosed wealth. — Speculative numerology. The discrepancy itself is retained (F9) without this explanation.
The year-by-year mismatch between Fig. 1 participant counts and Skatteetaten's official new-case counts (e.g. 446 individuals vs 236 cases in 2007-10) signals a data problem. — Not scored. The totals are largely reconciled by persons versus cases (joint spousal cases), dropped cases (about 25%, F12) and cases still in process: Fig. 1's 1,482 is 78% of the 1,905 official cases. The residual year-by-year pattern is unresolved and recorded under limitations.
Checks passed: the tax jump 'is not mechanically created' because original, pre-correction returns are used for all compliance outcomes. — Correct for wealth (claimed net wealth is observed) and for income (claimed income is assessed income minus the observed foreign-capital-income correction). For taxes, however, the authors' 2017 code imputes 'claimed' liabilities from assessed taxes; the claim rests on the paper's wording and auditor B did not examine the tax construction. See F1.
Comparing Fig. 3D's 2 pp with Table 1's ratio of mean taxes to mean wealth would be an 'invalid arithmetic objection', so the 2 pp figure passes. — The naive ratio-of-means comparison is indeed invalid, but the figure still fails another test. The mean of individual ratios is bounded by the tax rates times the mean individual hidden share, and the authors' own AER mean-of-ratios share (about 0.31) is the same statistic. That bound (0.6-0.9 pp) cannot produce 2-3 pp. F2 is retained.

Audit notes

What reproduced. The event-study regressions cannot be re-estimated: the Norwegian register microdata are confidential, and there is no 2022 code or replication package. Reproduced from published material: the Fig. 1 counts (exact), all Fig. 3 coefficients and confidence bands (matching both auditors), the Table 2 log-to-percent conversions and confidence intervals, the repatriation arithmetic (25%/40% gives 62%; the correct benchmark gives 74-79%), the back-tax conversion ($256m) and the Table A1 reweighting factors (0.87-1.19). Verified in the authors' public 2017 programs and workbook: the imputation of 'claimed' taxes (assessed tax minus 2.276% of the wealth correction) and the 'All' versus 'Living resds' samples behind the emigration estimates. Checked against external sources: official SSB emigration counts (9-25 times the paper's base rate), IRS totals via Johannesen et al. (2020 WP) with World Bank populations (per-capita ratios 2.1x and 2.4x, not 3x), the MCAA signing date (29 Oct 2014) and the AER (2019) hidden share for amnesty participants (about one third). Not reproduced or not reconcilable: the 2022 construction of claimed taxes (undocumented); Fig. 3D's 2-3 pp, which exceeds what taxes on disclosed assets can produce given the authors' own hidden shares; and Table 2's 'money transfers in' of 0.093 (Fig. 9A implies about 0.064).

Limits of this audit. Without the confidential microdata or the 2022 code, I inferred rather than verified that the 2022 paper used the 2017 imputation of claimed taxes: the wording is identical, the estimates are near-identical, and no claimed-tax variable exists among the paper's claimed/corrected pairs. Digitised coefficients are exact only up to rendering precision, and standard errors are inferred from symmetric bands. The F2 bound uses the AER's household-level mean hidden share; individual-level shares for married disclosers may be higher (up to about double), which narrows the gap but does not close it. SSB emigration comparisons are approximate (ages 16+ rather than 18+, population definitions, recent immigrants). Baselgia (2026) was read only as an SSRN abstract, and Leenders et al. (2023), Bomare & Le Guern Herry (2022) and Chan et al. (2023) through abstracts and auditor summaries. I could not examine whether some disclosers are heirs revealing inherited accounts, which would make part of the wealth jump an inheritance effect, because no Norwegian statistics were found. The year-by-year mismatch between Fig. 1 and Skatteetaten case counts is unresolved. No author was contacted, and no published critique of, or author reply about, this specific paper was located (OpenAlex citing works screened).