Annette Alstadsæter, Niels Johannesen, Ségal Le Guern Herry, Gabriel Zucman · NBER Working Paper 35505, July 2026

Global Financial Transparency and Offshore Wealth Accumulation

13 problems found: 3 major · 6 moderate · 4 minor

What the paper claims

Taxpayers who become wealthy are much less likely to shift wealth to offshore (haven) banks after the 2013 G20 commitment to automatic exchange of information (AEOI) than before.
When wealth flows to havens, it is much less likely to reduce domestic tax payments or reported financial wealth after 2013. The paper reads this as 'financial transparency has largely eliminated wealth flows to tax havens motivated by tax evasion'.
There is no increase in the use of complex ownership structures for offshore wealth flows. Holding-company ownership rises more steeply with wealth after 2013, but haven transfers routed through holding companies do not.
Overall interpretation: automatic exchange of bank information is 'a significant deterrent of offshore tax evasion'. Descriptively, aggregate household flows to havens 'decreased significantly over the period where financial transparency improved and appear to have stabilized at a relatively low level'.

Every problem found

1majorconfirmed · newly identified here · methodology

The paper's first finding is that, after 2013, getting rich stopped being linked to sending money to tax havens. But the paper never checks whether the before/after gap is bigger than chance alone could produce, and its own numbers show it is not. The pattern points the same way in every version of the analysis, but the evidence is too noisy to say how large the change was, or even to be sure there was one.

Technical detail and evidence

Why it matters, in detail. C1 is identified by a difference of household-FE coefficients across two regressions. Every testable specification in Table A.1 yields |z| <= 1.1; the headline gives z = 0.55 printed or 0.81 digitized, with a 95% CI for the change of about [-0.004, +0.010] against a low-regime coefficient of 0.0035. Significance would need an implausible cross-regime correlation of at least 0.7. The most powerful delineation (top 1%) cannot be tested from the published rounding. The paper reports no pooled interaction test and no covariance matrix. The magnitude of the decline varies from about 0% to 85% across outcomes (about 40% for amounts). The direction is consistent across all 12 nested specifications, but these are not independent confirmations.

Evidence. Table A.1 Panel A (p. 22), hand-transcribed (scripts/period_tests_adj.py, data/period_tests_adj.txt). The two regimes are separate regressions on disjoint years with regime-specific household FE, so the estimates are treated as independent. - Headline (top 0.1%, >NOK 100k): 0.003 (0.002) vs 0.001 (0.003), z = 0.55. With the digitized point estimates 0.00348 vs 0.00054, z = 0.81 and the 95% CI of the change is [-0.004, +0.010]. - All nine testable low-minus-high differences have |z| <= 1.09, and at most 1.41 under any rounding of the printed figures. - Reaching |z| = 1.96 would need cross-regime correlations of 0.70-1.00. - The three top-1% indicator rows cannot be tested: SEs printed as 0.000/0.001 leave |z| anywhere between 0 and about 4. - The size of the decline depends on the outcome: about -85% for the >100k indicator (digitized), -37% to -44% for transfer amounts, and none for the top-1% >500k row (0.001** vs 0.001**). - Narrowing the top group from 0.1% to 0.05% multiplies the estimates 2-7x (e.g. 0.003 -> 0.011). Table 1 implies only about 42 top-0.1% households per year make large haven transfers (5.12% x 823). Both point to thin identifying variation. - Auditor A's period_difference_tests.py gives the same z-values.

Why this severity. C1 is one of the three abstract results, and it rests entirely on a between-regime change that the paper's own standard errors cannot tell apart from zero, nor from complete elimination. The point estimates go the same way in every specification, so the finding is not reversed. But neither its existence nor its size is established.

The authors' response. In the paper: 'Across the 12 specifications, we consistently find a larger effect ... in the low-transparency period ... In most of the specifications, the former effect is statistically significant while the latter is not' (p. 8). No test of the difference is offered. No published response to this point was found (paper circulated July 2026; search of 25 Oct 2026). The authors' ProMarket op-ed (29 Sep 2026) restates the findings without addressing it.

2majorconfirmed · newly identified here · internal inconsistency

To show the change is specific to tax havens, the paper compares haven transfers with transfers to ordinary countries and says the latter did not change. In fact, the tax effect of ordinary transfers also nearly disappeared after 2013. About half of the tax improvement the paper credits to transparency for havens therefore also happened where transparency was not the issue. The evidence that haven transfers specifically stopped hiding wealth comes from the reported-wealth and capital-income results, which do hold up, not from the tax-payment headline.

Technical detail and evidence

Why it matters, in detail. Using the non-haven change as a benchmark cuts the haven-specific attenuation of the tax response from 6.1 to 3.3 pp (-46%; the proportional attenuation stays about 87-89%). The triple difference is insignificant (p = 0.32) under both the static and the t-1 normalisation. A common factor is the natural reading: lower tax rates mean a smaller tax response per krone of reported wealth (see F7), consistent with the non-haven financial-wealth response barely changing relative to t-1 (-13.6% -> -11.7%) while its tax response halves. The haven-specific evidence for C2 therefore rests on financial wealth (p ~ 0.05) and capital income (p ~ 0.01). Because compliant cross-border transfers also lower reported financial wealth (by 7-14%), the raw -19% low-period haven effect overstates the evasion component, which is about 6-12 pp.

Evidence. Table A.2, cols 7-8 (p. 23), and Figure A.1 (p. 21); computations in data/period_tests_adj.txt and data/event_alt_adj.txt. - Non-haven taxes: -0.033*** (0.005) -> -0.005 (0.005); change z = 3.96, p < 0.001; -85%, against -87% for havens. - Other non-haven outcomes also change: capital income -0.071*** -> +0.073*** (z = 4.4); debts +0.048*** -> +0.114***; financial wealth -0.067*** -> -0.033**. - Haven-specific (triple-difference) change in the tax response: +0.033, SE 0.033, p = 0.32. The non-haven change equals 46% of the haven change (0.028/0.061). Relative to t-1 the triple difference is +0.034, so the conclusion does not depend on normalisation; the non-haven tax collapse itself is 85% static but 51% relative to t-1, because of pre-trends. - Haven-specific changes that survive: financial wealth +0.150 (SE 0.075, p = 0.046; +0.124 relative to t-1) and capital income +0.337 (SE 0.137, p = 0.014). - Reported financial wealth after non-haven transfers falls 6.7%/3.3% (static) or 13.6%/11.7% relative to t-1 (low/high). The non-haven pre-period coefficients are significantly negative (e.g. -0.138, -0.119, -0.105 in the low regime). - So the low-period haven 'evasion signature' in excess of the benchmark is 6-12 pp of financial wealth, not 19 pp. - Codex computes the same 6.1 -> 3.3 pp benchmark adjustment.

Why this severity. The benchmark the paper relies on moved almost as much as the haven estimates for tax payments, the abstract's headline outcome. That halves the haven-specific attenuation and leaves it statistically insignificant. The haven-specific changes in reported financial wealth and capital income survive, so C2 is weakened in magnitude and attribution, not reversed.

The authors' response. In the paper: transfers and tax payments 'are joint decisions ... our estimates should not be interpreted as the causal effect of one on the other' (p. 9). No published response to this point was found (paper circulated July 2026; search of 25 Oct 2026). The authors' ProMarket op-ed (29 Sep 2026) restates the findings without addressing it.

3majorplausible · newly identified here · methodology

Before 2013, when someone hid money abroad, their officially reported wealth fell afterwards. The method compares each household's richer and poorer years, so this alone makes it look as if people sent money abroad when they were richest, even if their behaviour never changed. After 2013, transfers no longer reduced reported wealth, so the distortion disappears. Simulations suggest this could explain anything from a small part to most of the measured drop.

Technical detail and evidence

Why it matters, in detail. Feedback from Y_it to later regressors D_i,t+k makes the within estimator inconsistent at fixed T = 7 (a Nickell-type bias). The bias scales with the raw transfer rate at the top, which is several times the FE gradient (about 2%/yr vs 0.35 pp), and with the per-transfer wealth fall relative to wealth volatility. Two independent simulations put the spurious low-minus-high difference at 9-51% of the observed 0.0029 decline for 0.5-1% falls, and at 30-104% for 2%. C1 and C2 are therefore not independent pieces of evidence. The fix is cheap and not reported: rank households on wealth before any large transfer, model the hazard of a first transfer, or drop post-transfer years.

Evidence. Paper: Eq. (1) and p. 7 (lagged groups, household FE); Fig. 3c-d (digitized post-event financial wealth -0.148, -0.187, -0.249, -0.232 in 2006-12 vs -0.060, -0.015, -0.082, -0.067 in 2013-19). - Auditor A's Monte Carlo (claude/scripts/sim_fe_feedback_bias.py) has identical behaviour in both regimes and feedback only before 2013. A 1% fall in reported net wealth per transfer creates a spurious low-minus-high difference of 0.0006-0.0011 (17-31% of the low-period coefficient); 2% gives 0.0012-0.0021; 5% gives 0.0031-0.0062. - The adjudicator re-implemented the model independently (scripts/sim_feedback_adj.py; N = 1,000,000, T = 7, 4 replications, common random numbers; data/sim_feedback_adj.csv). Bias as % of the observed decline (0.0029), at wealth-shock SD 0.12 / 0.20 and a raw top-0.1% transfer rate of about 2% (close to the ~2% implied by Table 1): - 0.5% fall per transfer: 33% / 13%; - 1%: 51% / 25%; - 2%: 104% / 55%; - 4%: 252% / 103%. With a raw rate of about 1.2% the shares are roughly 55-80% of these. - The key parameter, the fall in log reported net wealth per evasive transfer for households near the top-0.1% boundary, is unobserved. In 2006 the Scandinavian top-0.1% threshold was about $9m (AJZ 2019, fn. 22), so a NOK 0.25-1m transfer is roughly 0.5-2%. The Table A.1 ratio of the amount coefficient to the indicator coefficient (898 NOK / 0.0035) suggests small induced transfers, but amounts may be capped and are imprecise (SE 475).

Why this severity. Within a defensible range of the unobserved parameter (a 0.5-2% fall in reported net wealth per evasive transfer), the mechanism accounts for roughly 10% to 100% of the measured C1 decline: a central share of about a quarter to a half. Changing an unvalidated assumption (strict exogeneity of lagged wealth ranks) within that range would therefore substantially weaken C1. Confidence is only 'plausible' because the magnitude in the real data is unknown.

The authors' response. In the paper: lagged rather than contemporaneous wealth is used 'so that a household's position in the wealth groups is not mechanically related to the year's wealth transfers' (p. 7). Dynamic feedback is not discussed. No published response to this point was found (paper circulated July 2026; search of 25 Oct 2026). The authors' ProMarket op-ed (29 Sep 2026) restates the findings without addressing it.

4moderateconfirmed · newly identified here · overclaiming

After 2013, the estimated effect of haven transfers on taxes and reported wealth is close to zero, but it is measured so imprecisely that sizeable remaining effects cannot be ruled out. Saying evasion through new transfers was 'largely eliminated' treats 'too small to detect' as 'zero'. The change between the two periods in reported wealth is solid; the claim that nothing is left is not.

Technical detail and evidence

Why it matters, in detail. The high-regime nulls are low-powered. CIs reach 59-74% of the low-regime effects, the >500k high-regime financial-wealth estimate is 69% of the low one, and the baseline tax difference has p = 0.06. Relative to the event-study reference year, the high-regime financial-wealth response is -5%. That is still smaller than the non-haven benchmark (-12%), so it does not itself signal evasion. The defensible statement is that the haven-specific wealth-hiding signature fell substantially (financial-wealth change p = 0.012), not that it was eliminated. Equivalence bounds are not reported.

Evidence. Table A.2 (p. 23); data/period_tests_adj.txt and data/event_alt_adj.txt. - High-regime 95% CIs: taxes [-5.2%, +3.4%], i.e. up to 74% of the pre-2013 -7.0%; financial wealth [-11.3%, +9.9%], i.e. up to 59% of -19.1%. - Events above NOK 500k: high-regime financial wealth -0.134 (0.135), 69% of the low-regime -0.195; low-high difference p = 0.69. The paper calls this 'qualitatively robust' (p. 10). - Baseline tax difference: z = 1.87 (p = 0.061); z = 2.35 without controls. The financial-wealth difference is significant (z = 2.52) and robust to normalisation (relative to t-1: -19.5% vs -5.2%). - Fig. 3d high-regime pre-period financial wealth: -0.111, -0.089, -0.050, 0. Relative to t-1, financial wealth falls 5.2% and taxes 1.8%. - The authors' op-ed says the transfers 'no longer leave any trace on the tax return'. - Not used for grading: Auditor A's linear pre-trend extrapolations (-16% to -18% financial wealth); see rejected claims.

Why this severity. This does not overturn the significant change in the financial-wealth response. It limits how much of the pre-2013 evasion can be said to have disappeared, so it bears on the strength of C2's interpretation ('largely eliminated') rather than its direction.

The authors' response. No published response to this point was found (paper circulated July 2026; search of 25 Oct 2026). The authors' ProMarket op-ed (29 Sep 2026) restates the findings without addressing it.

5moderateconfirmed · newly identified here · overclaiming

The paper says rich people did not start routing money to tax havens through their companies instead of their personal accounts. But at the very top, where the drop in direct transfers is concentrated, the numbers are too imprecise to rule out exactly that kind of switch. Only one route, through Norwegian holding companies, is examined.

Technical detail and evidence

Why it matters, in detail. For the top 0.05-0.1%, the 95% CI for the change in holding-company haven transfers includes increases of 90-139% of the fall in direct transfers, so full substitution cannot be excluded where it matters. The claim holds only for the top-1% delineation, which rules out increases above about 65% of that group's direct-transfer decline. The ownership gradient rises robustly, and a tax-incentive change (dividend gross-up 1.15 -> 1.44) offers an alternative to the 'legal avoidance substitutes for evasion' reading.

Evidence. Table A.1 Panels C-D (p. 22); data/period_tests_adj.txt. - Panel D has no significant coefficient. - Top 0.1%, >100k: change -0.0016, 95% CI [-0.0059, +0.0027]. The upper bound is about 90% of the digitized fall in direct transfers (0.0029). - Top 0.05%: CI upper bounds of 117-139% of the direct-transfer fall (>50k/100k/500k). Some point estimates rise (top 0.05% >100k 0.0006 -> 0.0012; top 0.1% amount 1,216 -> 2,977). - Only the top-1% delineation is precise: it rules out an increase above about 0.0006, about 65% of the top-1% direct-transfer fall. - Ownership change: z = 2.1-5.7. - Dividend gross-up factor ('faktortall') was 1.15 (2016), 1.24 (2017), 1.33 (2018) and 1.44 (2019) (Skatteetaten page on 'oppjustering av utbytte', verified by the adjudicator). - The Introduction itself calls the holding-company evidence 'mixed' (p. 3).

Why this severity. C3's 'no increase' cannot be sustained at the top of the distribution, where the C1 decline is located, and the channel tested is narrow. There is no positive evidence of substitution into holding companies, so this qualifies one of three abstract results rather than overturning it.

The authors' response. In the paper: 'The evidence is mixed' (p. 3); the ownership rise 'may reflect substitution from illegal tax evasion to legal tax avoidance strategies, including the tax deferral offered by holding companies' (p. 11). No published response to this point was found (paper circulated July 2026; search of 25 Oct 2026). The authors' ProMarket op-ed (29 Sep 2026) restates the findings without addressing it.

6moderateconfirmed · previously known · overclaiming

The paper counts money sent to a fixed list of tax havens but leaves out the United States, Britain, the UAE and the Netherlands entirely. Those were natural alternatives after 2013 for people trying to stay hidden. The paper even cites London property as a shift its method handles, yet transfers to Britain are not counted. Some of the decline could be money going elsewhere.

Technical detail and evidence

Why it matters, in detail. C1's outcome is first-hop transfers to a 2009-vintage list of havens. Displacement to non-CRS or weakly reporting destinations (notably the US, outside the CRS; the UAE, exchanging from 2018), or to UK property, would lower the measured gradient without lowering offshore evasion, so the observed decline bounds the true decline from above. The paper's robustness claim about London real estate contradicts its own exclusion of the UK. The fix is simple: report the four excluded centres separately or in an inclusive specification.

Evidence. Paper: Introduction p. 2; Sec. 3 p. 5; Sec. 4.1 p. 8; Table 1 note (p. 19). - The 52-jurisdiction list was verified against Johannesen and Zucman (2014) Appendix Table A1. - Casi, Spengel and Stage (ZEW DP 18-036, 2019 version of the JPubE 2020 paper), abstract: after the CRS 'the United States, which so far did not commit to the CRS, seems to emerge as a potentially attractive location for cross-border tax evasion'. - OECD AEOI Implementation Report 2018, Table 1 note: the US exchanges under FATCA IGAs, not the CRS. - Bomare and Le Guern Herry (2022) document CRS-related UK property purchases by offshore companies. - Corpus offshore-havens-07 (TJN, State of Tax Justice 2024) argues that CRS induced shifts into non-reportable assets and locations. - Not adopted as evidence of substitution: the significant rise in large non-haven transfers at the top (rejected claims).

Why this severity. Unmeasured re-routing could make the decline in observed haven flows an overstatement of the decline in offshore flows, but nothing in the published material quantifies it. It narrows rather than overturns C1 and C3.

The authors' response. In the paper: holding structures and look-through rules are discussed (pp. 3, 5), but the excluded centres are not. No published response to this point was found (paper circulated July 2026; search of 25 Oct 2026). The authors' ProMarket op-ed (29 Sep 2026) restates the findings without addressing it.

7moderateconfirmed · newly identified here · internal inconsistency

The paper's only chart of total money sent to tax havens shows that flows fell before the 2013 transparency pledge and rose somewhat after it. The text describes this as a decline linked to greater transparency, which is not what the chart shows at the date the paper uses.

Technical detail and evidence

Why it matters, in detail. The descriptive support for a 2013 break is absent: the series falls 57% between 2006 and 2012 and rises 32% after the commitment. The authors' caveat that aggregates cannot show whether evasion by the wealthy fell is fair. A post-2013 rise in total flows is compatible with C2 (more compliant transfers), but it is hard to square with 'Norwegian households are shifting much less wealth to their offshore accounts than they used to' as an AEOI effect.

Evidence. Adjudicator digitization (scripts/digitize_fig1_adj.py, y-axis calibrated on tick marks; data/fig1_adj.csv), matching Auditor A's values. - 0.0346% of GDP at the first plotted semester (2006) -> 0.0148% (2012), -57%; already -37% by 2008. - 0.0159% (late 2013) -> 0.0210% (2015), +32%; then 0.018-0.020% to 2020. - The 2016-20 mean is 22% above the 2012-13 mean. - Period means: 0.0233% (2006-12) vs 0.0188% (2013-20), -19%, with no break at the treatment date. - The paper calls the 2009 measures 'largely unsuccessful' (p. 4). - Codex digitized the same series but judged that it 'does not contradict the longer-period decline'.

Why this severity. The aggregate series is the paper's only direct evidence on timing, and it shows no decline at the treatment date. The micro results do not depend on it, so the effect on the core findings is indirect.

The authors' response. In the paper: 'it is not clear from the aggregate trends alone whether this reflects a drop in offshore tax evasion by the wealthy' (p. 6). No published response to this point was found (paper circulated July 2026; search of 25 Oct 2026). The authors' ProMarket op-ed (29 Sep 2026) restates the findings without addressing it.

8moderatelikely · newly identified here · methodology

The paper compares 2006-12 with 2013-19 and credits the difference to the 2013 pledge to share bank information, although information did not actually start flowing until 2017-18. Over the same years Norway cut its wealth and capital-income taxes and interest rates fell, making hidden money less rewarding anyway. The paper does not check whether behaviour changed when information sharing actually began, nor rule out these other changes.

Technical detail and evidence

Why it matters, in detail. With only a pooled before/after contrast, the 'treatment' is every change between 2006-12 and 2013-19. The design cannot separate an announcement effect (2013-16) from implementation (2017-19) or from contemporaneous changes. The 34% fall in the annual tax gain from hidden deposits plausibly explains part of the C1 decline and mechanically lowers the C2 tax-payment response (not the financial-wealth response), which ties in with F2. Year-by-year interaction estimates or a 2017-18 break would be the natural test.

Evidence. Paper: Sec. 4.1 p. 7 (regime definitions); Fig. 1 note. - OECD (2018) AEOI Implementation Report, Table 1: lists of first exchanges in 2017 and by 2018 (verified). - Boas et al. (2024, NBER w32714, co-authored by Johannesen and Zucman) place AEOI in 'the second half of the 2010s' and call 2016 'the very first year of the CRS' (verified in text). - Storting note 'Endringer i formuesskatten fra 2000 til 2024' (verified): wealth-tax rate 1.1% -> 1.0% (2014) -> 0.85% (2015-); threshold NOK 870k (2013) -> 1.0m (2014) -> 1.2m (2015) -> 1.4m (2016) -> 1.48m (2017); share valuation discount 10% (2017), 20% (2018), 25% (2019). - SSB table 08175 deposit rates: 2.0-5.0% (2006-12) vs 0.8-2.3% (2013-19). - Annual tax saved per NOK hidden in deposits: 1.89% (2006-12) -> 1.25% (2013-19), -34% (Auditor A's computation; inputs checked). - Non-haven tax response relative to t-1 halves while the non-haven financial-wealth response barely changes (data/event_alt_adj.txt), consistent with lower tax sensitivity. - Codex noted the 2017/18 exchange dates in its assumptions table but did not count an issue.

Why this severity. Attributing the before/after changes to AEOI rather than to other changes between two seven-year windows is assumed rather than shown. Plausible confounders exist, but they are unlikely to explain all of C1: the non-haven gradient is unchanged, and a 34% fall in the gain from evasion would need an elasticity above 2 to explain an ~85% fall in the gradient.

9moderatelikely · previously known · overclaiming

The tax-payment result comes from roughly one in ten of the large transfers to havens, made by younger, Norwegian-born, one-time senders without foreign ties. Older people, repeat senders and people with property abroad, who may hold much of the hidden wealth, are left out. The result may not describe how the richest households behave.

Technical detail and evidence

Why it matters, in detail. The C2 estimand is the average change in taxes and wealth around a single large haven transfer by low-mobility, mostly sub-top-1% households. Repeat transferors, older households and the foreign-linked are excluded. The restrictions guard against migration and retirement confounding, which is reasonable, but they make C2 silent on the households whose behaviour C1 describes. Possible conditioning on post-event status (never emigrated, no foreign property) would be selection on outcomes; its direction is unknown.

Evidence. Fns. 5-7 (p. 9); Table 1 (p. 19); Table A.2 N treated (p. 23). - 823 x 7 = about 5,760 large-transfer household-years per regime, so treated N is about 10% of them. The share of distinct households is higher, because repeat transferors count several times. - 85% of large haven transferors are below the top 1% (Table 1: 14.8% in the top 1%). C2 therefore mainly describes upper-middle-wealth one-off transferors, not the top-0.1% households that drive C1. - Corpus offshore-havens-04 (Leenders et al. 2023, JPubE 217) shows that offshore-evasion patterns are context-dependent.

Why this severity. This limits the generality of C2 as stated in the abstract, but there is no evidence that the excluded groups behave differently, so the size of any bias is unknown.

The authors' response. In the paper: the restrictions are imposed 'to address potential confounders related to international mobility' (p. 9). No published response to this point was found (paper circulated July 2026; search of 25 Oct 2026). The authors' ProMarket op-ed (29 Sep 2026) restates the findings without addressing it.

10minorconfirmed · newly identified here · documentation gap

The official register of cross-border payments was not fully complete in 2006-07, two of the seven 'before' years, and the paper does not say so. If anything, this probably makes the before/after contrast look smaller rather than bigger, so it is a minor caveat.

Technical detail and evidence

Why it matters, in detail. Partial reporting in 2006-07 adds noise to, and probably downward bias in, the pre-2013 transfer outcome. With household FE and year FE, a missing-at-random undercount scales down the low-regime gradient (a conservative bias for C1). Bank-specific gaps that correlate with wealth could have either sign. A 2008-12 re-estimate would settle it.

Evidence. SSB, 'Cash flows between Norway and abroad', Sources of error and uncertainty (read in the cached page, updated 14 Aug 2026), says: 'In the year 2005, several reporting entities did not give full reports ... The data for 2006 and 2007 are also somewhat incomplete ... From year 2008, we consider that the data is complete'. The same page says the register was established on 1 Jan 2005 and that its owner changed in January 2016. - Undercounting at random would attenuate the low-period C1 gradient, which works against the finding, and would understate Figure 1's early levels, which makes the pre-2009 decline steeper. - It could also misclassify a few event-study treatments or repeat transferors.

Why this severity. Limited to two early years, probably works against rather than for the paper's C1 contrast, and SSB judged the 2006-07 data fit for research release. This is an undisclosed caveat, not a threat to the findings.

11minorconfirmed · newly identified here · selective presentation

A few side results are described more favourably than the tables show. For example, a statistically significant rise in debts after post-2013 haven transfers is called 'no clear pattern'. These are small points, but they all lean the same way.

Technical detail and evidence

Why it matters, in detail. Debt +12.2% (p < 0.05) and real capital +6.4% (p < 0.10) around high-regime haven transfers are tax-relevant: a debt-financed real-asset purchase lowers net taxable wealth through valuation discounts. They deserve discussion rather than dismissal. The wage figure is mis-transcribed (-1.5% vs '1%').

Evidence. Table A.2 Panels A-B and Fig. 3f/3h against the text on pp. 10-11. - The paper itself signs small estimates elsewhere ('-1%', '-0%'), so an unsigned '1%' reads as positive (Codex I6).

Why this severity. These are descriptive slips in secondary outcomes. C2's financial-wealth result is unaffected.

12minorconfirmed · newly identified here · arithmetic or transcription

There are several typos, mislabelled references and small rounding exaggerations. None of them changes the results.

Technical detail and evidence

Why it matters, in detail. The rounding slips modestly flatter the contrasts ('almost 0.4' for 0.35 pp; '30-fold' for 36-fold weakens the holding-company contrast). The mis-references and the caption error impede checking. None changes any estimate or inference.

Evidence. - Text vs digitized figures: data/figs_adj.csv (top 0.1% low 0.003475; holding-company high 0.051336 / baseline 0.00141). - Version diff of the 3 Jul 2026 draft (nielsjohannesen.net) against NBER w35505. - References list (pp. 13-14). - ProMarket, 29 Sep 2026. - The clustering inconsistency is likely immaterial for SEs: about 580 treated vs about 190,000 controls per regime, and each treated household appears in a single cohort (fn. 5).

Why this severity. Presentation errors with no effect on conclusions.

13minorconfirmed · newly identified here · documentation gap

Relying on confidential data is normal in this field, but the paper also leaves out details of how its estimates were built. Even a researcher with data access could not rebuild them exactly, and outsiders cannot run the before/after tests the conclusions depend on.

Technical detail and evidence

Why it matters, in detail. Even with authorised SSB access, the specifications cannot be rebuilt exactly. The missing covariance matrices are the substantive gap: they prevent the joint tests that F1, F2 and F5 show to be decisive. The other omissions (outcome scaling, controls) have small demonstrated effects.

Evidence. Secs. 3-4, Eq. (2), fns. 5-8; SSB register documentation. - Codex I5 (cohort-support enumeration: full 11-year windows exist only for cohorts 2009-15); Auditor A I12. - The no-controls results (Table A.2 cols 1-2) are close to baseline. - A log reading would change -0.070 to -6.8% (Codex).

Why this severity. This impedes verification, especially of the between-regime tests, but no estimate demonstrably depends on the unstated details.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

I6: with a linear pre-trend adjustment, the post-2013 haven financial-wealth effect is -16% to -18%, 'comparable to the pre-2013 effect under the same adjustment'. This is part of the basis for grading the high-regime null as a major problem. — Linear extrapolation of the pre-event rise is not a credible counterfactual here. The same adjustment implies financial-wealth falls of -24% to -35% around presumably ordinary non-haven transfers (data/event_alt_adj.txt). Their pre-period coefficients rise significantly into t-1 and then fall back, a hump characteristic of large transfer events. The defensible alternative normalisation (relative to t-1) gives -5.2% after 2013 vs -19.5% before, smaller than the non-haven benchmark (-11.7%). The imprecision part of the claim is retained in F4 at moderate severity.
I5: large non-haven transfers by the very wealthy rose significantly between regimes (top 0.1%, >NOK 500k: 0.019 -> 0.035, z = 2.26), with increases 'several times the fall in haven transfers', as evidence consistent with re-routing. — The non-haven group excludes the US, UK, UAE and Netherlands and consists largely of CRS-participating countries, so higher flows there do not provide evasion opportunities. If anything, this supports the paper's point that cross-border activity did not contract. The >100k row (the specification behind the paper's 'essentially unchanged' wording) rises 37% with z = 1.31. The coverage concern about the four excluded centres is retained as F6.
Checks passed, item 6: the rise in the median baseline probability (0.00012 -> 0.00016), like the fixed nominal NOK threshold, biases against the paper's C1 finding. — The C1 gradient is measured in absolute percentage points, which the baseline does not affect. In the paper's fold-change framing ('30-fold' vs '3-fold'), a higher post-2013 baseline makes the contrast look larger, not smaller (3.4x vs 4.5x on the pre-2013 baseline). The nominal-threshold and exchange-rate point is verified (NOK 100k = EUR 12,436 vs 11,079; CHF 17,805 vs 12,568) and kept as a check passed.
I11 (sub-point): in a stacked design that reuses controls, the household×cohort clustering stated in the text 'can understate SEs'. — The text/caption inconsistency is retained (F12), but the claimed consequence is immaterial here. Each treated household belongs to one cohort (fn. 5), and with about 580 treated vs about 190,000 controls per regime the variance of the DiD is dominated by the treated side, so how reused controls are clustered barely moves the SEs.
I4 graded moderate: the incomplete 2006-07 Currency Register coverage is a moderate threat to C1-C3. — The fact is confirmed (SSB documentation), but the severity is downgraded to minor (F10). Undercounting at random attenuates the pre-2013 gradient, working against C1. Only two of seven early years are affected, SSB itself releases 2006-07 for research, and Figure 1's early levels would if anything be higher.
I5 graded moderate: missing estimator and variable definitions are a moderate issue. — The gaps are confirmed and retained (F13), but downgraded to minor. No estimate demonstrably depends on them: no-controls estimates are close to baseline, and a log reading changes -7.0% to -6.8%. The substantive consequence, untestable between-regime differences, is graded under F1, F2 and F5.

Audit notes

What reproduced. No re-estimation was possible. The Norwegian tax, population, Currency Register and shareholder microdata are confidential, and no code, intermediate data or covariance matrices are published. Public SSB tables (07478) are regional and mix firms with persons, so they cannot rebuild Figure 1. Reproduced from the published PDF, all with the adjudicator's own scripts: (i) vector digitization of Figs. 1-4 and A.1, matching Table A.1/A.2 after rounding and both auditors' values; Figure 1 calibrated on tick marks gives -57% (2006-2012), +32% after the 2013 commitment, and -19% in period means; (ii) between-regime z-tests with rounding bounds: C1 |z| <= 1.09 testable, top-1% rows indeterminate; C2 taxes p = 0.061, financial wealth p = 0.012; non-haven tax change z = 3.96; triple differences taxes p = 0.32, financial wealth p = 0.046, capital income p = 0.014; (iii) alternative event-study normalisations; (iv) an independent Monte Carlo of the FE feedback bias, which confirms Auditor A's order of magnitude (9-51% of the C1 decline for 0.5-1% wealth falls per transfer; 30-104% for 2%); (v) exchange-rate and tax-parameter checks from Norges Bank, the Storting note and SSB. The headline coefficients themselves could not be reproduced.

Limits of this audit. No access to microdata, code or covariance matrices, so no headline estimate could be re-estimated. Between-regime tests assume independence of the two regime estimates; sensitivity to correlation and to the published three-decimal rounding is reported. Digitized values come from PDF vector paths (precision about 1e-5 for Figs. 1, 2 and 4; about 1e-3 for event-study coefficients and CIs). The feedback-bias simulations are stylised: their key parameter (the fall in reported net wealth per evasive transfer near the top-0.1% threshold) and the wealth volatility at the top are unobserved, so F3's magnitude is a range, not an estimate. Casi, Spengel & Stage was read in its 2019 ZEW discussion-paper version, not the JPubE text. Bomare & Le Guern Herry (2022) was taken from the auditors' readings (abstract and introduction) and not re-read; the dividend gross-up factors and Norwegian wealth-tax parameters were checked against the cached Skatteetaten page and Storting note. No author was contacted, and no published critique of or reply to this July 2026 paper was found (searches of 25 Oct 2026).