John Guyton, Patrick Langetieg, Daniel Reck, Max Risch, Gabriel Zucman · NBER WP 28542 (2021); forthcoming, Journal of Public Economics (per author website, Oct 2026)

Tax Evasion at the Top of the Income Distribution: Theory and Evidence

11 problems found: 1 major · 4 moderate · 6 minor

What the paper claims

IRS National Research Program (NRP) individual random audits of tax years 2006-2013 failed to detect most sophisticated evasion (offshore accounts, entity-level pass-through misreporting), so detected under-reporting falls sharply within the top 0.1% and audit-only estimates understate evasion at the top.
Offshore evasion went almost entirely undetected in random audits and is highly concentrated at the top.
Entity-level pass-through evasion is under-detected in individual audits and substantial.
Headline (Dec 2025 abstract): accounting for sophisticated (offshore + pass-through) evasion raises the top-1% share of unreported income by 9 to 33 percentage points; aggregate unreported income rises by a factor of 1.11-1.29.
Accounting for evasion raises the top-1% fiscal income share (Nov 2023 abstract: '+50% unreported income of the top 1% and about +1 percentage point top-1% fiscal income share'; Dec 2025 Conclusion: 'Accounting for tax evasion increases the top 1% income share').
Theory: a fixed-cost concealment technology is adopted at high incomes; higher audit rates encourage concealment; with a fixed enforcement budget, costlier high-income audits can shift audits toward low-income taxpayers.

Every problem found

1majorlikely · previously known · overclaiming

When the paper's own most cautious assumptions are used together, counting hidden income slightly lowers the top 1%'s share of income (about 19.7% instead of 20.3%) rather than raising it. The paper shows its cautious assumptions only one at a time, so its flat statement that evasion makes measured inequality higher goes beyond its evidence. Its central estimate (about +1 point) is still a reasonable best guess.

Technical detail and evidence

Why it matters, in detail. With the additive macro allocation, the joint low case is s_LL = 20.7 + (20.3 - 21.3)(1.1377/1.1328) = 19.7%, i.e. -0.6 pp relative to the 20.3% reported share. q_LL = 16.2%, against 11.4% in raw NRP data and 16-17% in Auten-Splinter. The corners of the paper's own assumption space therefore span about 19.7-23.4% for the top-1% fiscal share (-0.6 to +3.1 pp; benchmark +1.0 pp) and about 16-45% for the top-1% share of unreported income, not the printed 20.3-22.4% and 21.9-39.4%. The lower corner is not an implausible extreme. The detected-share DCE allocation is close to the IRS DCE2019 microsimulation (top-1% share 18.1% vs 19.1% reported, 2008-13; DCE note Table 4a) and to Johns-Slemrod's no-change result.

Evidence. Dec 2025: Table A11 p.61 (DCE low alone 19.3%; DCE low + soph. bench 20.3%; DCE bench + soph. low 20.7%; benchmark 21.3%); Table A9 p.59 (no-DCE low 20.1%); Table A8 p.58; top-1% rates p.38 (12.4/14.1/17.1/21.8%); fn 62 p.39 (factor 1.016); range p.41; Conclusion p.43. Because DCE variants only redistribute a fixed dollar total, T_DL = T_B and s_LL = s_L + (s_DL - s_B) T_B/T_L = 20.7 - 1.0 x 1.004 = 19.70% (all-corner rounding box 19.54-19.85%); q_LL = 16.2% (15.9-16.5%); high-high 23.4% / 44.5% (scripts/reconstruct.py, out_reconstruct.txt section 4). The sign holds without any denominator: since T_L <= T_B, s_LL <= 20.7 + (20.3 - 21.3) = 19.7% (19.85% allowing rounding). Nov 2023: Appendix Tables A10-A13 (soph. lower bound 20.7%; detected-share DCE + soph. 20.4%), text pp.42-44 (additivity stated on p.38: 'We combine sophisticated and less-sophisticated evasion additively at the distributional level'). DCE companion note (2023) p.32: 'Inequality could be higher or lower due to undetected under-reporting'. Auditor values: Codex 19.70%; Claude 19.4% (biased low because it subtracts the DCE-benchmark-allocated double-count removal from DCE-low amounts).

Why this severity. The top-1% income-share revision is the paper's main implication for the inequality literature (Nov 2023 headline '+~1 pp'; Dec 2025 Conclusion). Its sign is not established within the paper's own stated lower bounds: -0.6 pp at the joint low end against +1.0 pp in the benchmark. The benchmark remains a defensible central estimate and the under-detection findings (C1-C3) are unaffected. This is a robustness failure of a core claim, not an error in the benchmark, so it is major rather than critical.

The authors' response. The Dec 2025 text concedes the level is 'uncertain, especially when we include DCE' (p.41). The DCE note calls the detected-share allocation 'too conservative' and 'an informative lower bound' (p.27). Reck, Risch & Zucman (Oct 2021 response to Auten-Splinter, p.23): 'We have difficulty rationalizing a decrease.' The Dec 2025 draft dropped the Nov 2023 robustness sentence and the '+1 pp' abstract claim but kept the Conclusion sentence. No response to the joint-case calculation was located.

2moderateconfirmed · newly identified here · selective presentation

The headline '9 to 33 points' compares the new estimates with what auditors directly found. It leaves out the standard IRS correction for evasion that auditors miss, which the paper itself uses for its main income estimates. Against that fuller starting point the rise is about 1 to 13 points (about 6.5 in the central case), so the headline makes the effect look roughly three times larger. The amount of extra hidden income found at the top is similar either way.

Technical detail and evidence

Why it matters, in detail. DCE adds about 6.9% of true income of mostly bottom-99% unreported income to the denominator, so the same top-end dollars move the top-1% share of unreported income much less: +21.6 pp without DCE vs +6.5 pp with benchmark DCE (range +9.3 to +32.8 vs +1.1 to +12.6). In levels the effect is similar (top-1% unreported income +1.6% vs +1.3% of aggregate reported income), and the top-1% under-reporting rate rises by +6.9 pp (2.3% -> 9.2%) vs +4.7 pp (12.4% -> 17.1%). The share-based headline depends on the baseline; the level effect does not.

Evidence. Abstract p.1; Introduction p.4 and fn 3; Table 2 p.32; Table A8 p.58; Section 5.3 pp.37-39 and fn 61. Aggregate factors reconstructed from the printed rates and shares are 1.11 / 1.14 / 1.29 with DCE (1.15 via the fn-62 factor) and 1.40 / 1.50 / 1.94 without DCE (out_reconstruct.txt sections 2-3). In levels, benchmark sophisticated evasion adds 1.57% (no DCE) vs 1.29% (with DCE) of aggregate reported income to top-1% unreported income. The Nov 2023 abstract instead used a DCE-inclusive metric (+50%; 1.19 x 30.9/23.8 = 1.55).

Why this severity. The number is arithmetically correct for its unstated baseline, and the DCE-inclusive results are disclosed in Section 5.3 and Table A8, so the qualitative claim survives. But read as the effect of sophisticated evasion within the paper's own complete framework, the headline is about three times too large (benchmark +21.6 pp vs +6.5 pp).

The authors' response. The introduction says DCE 'introduces a large amount of uncertainty about the distribution of unreported income' (p.4). Section 5.3 says the effect 'depends on the extent to which these shares also increase when we allocate DCE-identified under-reporting' (p.39). Footnote 61 notes that DCE-plus-sophisticated shares are 'significantly higher than the 11.4%'. No direct response.

3moderatelikely · previously known · speculative assumption

To spread the hidden business income the audits missed, the main scenario assumes the richest owners under-report at the same rate as everyone else. The only direct audit study of such businesses found they under-report at about a third of that rate. The authors give real reasons to think that study misses schemes used at the top, but one of them calls the equal-rate assumption the high end of what is plausible, so the central estimate probably leans high.

Technical detail and evidence

Why it matters, in detail. For the isolated no-DCE pass-through imputation, switching from the benchmark to the S-corporation profile cuts the top-1% share of unreported income from 26.3% to 16.9% (-9.4 pp, -63% of the increment) and the top-1% fiscal share from 20.4% to 19.9%. Page 34 and fn 50 attribute most of this to the distributional assumption. With RRM about 0.65, roughly half of these changes apply, and the DCE-inclusive benchmark top-1% share would fall from 21.3% to about 21.0-21.1%. This assumption is one of the two main drivers of the joint low-end reversal in F1.

Evidence. Dec 2025 pp.21-22, 28-31, 34 and fn 50; Figure 5a-b; Table 1; Table A6 p.56 (isolated pass-through: top-1% share of unreported 26.3% benchmark vs 16.9% low, i.e. +14.9 vs +5.5 pp over 11.4%); Table A10 p.60 (fiscal share 20.4% vs 19.9%); Iselin & Reck (5 Dec 2025, danreck.com/s/MisreportedIncomeDynamics.pdf) pp.5, 18, 23; out_reconstruct.txt section 7.

Why this severity. A mid-range RRM (about 0.65) would lower the benchmark no-DCE headline by roughly a sixth and the benchmark fiscal-share effect by about 0.2-0.3 pp. The S-corporation profile is already the paper's low end and lies inside the abstract's range, so the published range is not misstated, but the benchmark leans high.

The authors' response. The paper argues (pp.21-24, 29-31) that S-corporation audits by SBSE examiners likely miss sophisticated evasion in large, top-owned firms; that micro-captive participation is concentrated among top owners of large S-corporations; and that partnership complexity rises with income. Reck, Risch & Zucman's 2021 response (pp.14-18) distinguishes group-level allocation from proportional imputation and defends the 20% rate (net denominator). Iselin & Reck (2025) say values above 1 cannot be ruled out.

4moderatelikely · previously known · version instability

In the widely cited 2021 version, the IRS's standard correction on its own raised the top 1%'s income share by 0.6 points. The authors' own 2023 re-run of the same method on the same years shows a 0.6-point fall, with no explanation. The current version uses other methods, so this mainly matters for anyone relying on the 2021 numbers, much of whose headline effect rested on that step.

Technical detail and evidence

Why it matters, in detail. For the same method and years, the DCE-only effect on the top-1% fiscal share went from +0.6 pp (2021) to -0.6 pp (2023 note): a 1.2-pp swing against a headline of +1.5 pp. The identity reported income of the top group = s*T - q*U puts the 2021 value at the logical maximum (20.30%) of reported income for any 1% group, which implies zero re-ranking; the 2023 value implies 18.8%. Current versions use MA-DCE, whose DCE-only range is 19.3-21.4%, so even the sign of the DCE component is uncertain; the DCE note concedes that 'inequality could be higher or lower'.

Evidence. March 2021 draft (NBER w28542 rev0): Table 3 p.40, text p.39, Table 2 p.37, Section 2.2 p.9 (14.0% DCE aggregate). DCE note (Nov 2023): p.6, pp.31-32, Table 4b. Nov 2023 Appendix Table A13. Auten & Splinter (2021) Table 3 (a Johns-Slemrod-style replication gives -0.1 pp). out_reconstruct.txt section 6.

Why this severity. The current estimates no longer use DCE2001, so they are unaffected. But the change silently reverses a published robustness result and roughly 80% of the 2021 headline effect (+1.5 -> about +0.3 pp), and the 2021 version is the one most cited in policy discussion.

The authors' response. DCE note (2023, p.2): criticism of the DCE2001 distribution 'rightly identifies an important gap', and DCE2001 is no longer recommended because its profile 'seems unrealistic'. Reck, Risch & Zucman (2021) defended the 2021 DCE approach on conceptual grounds. No explanation of the numerical reversal was located.

5moderateplausible · previously known · speculative assumption

The estimate of income hidden offshore borrows the share of undeclared money from Swiss bank cases. Yet over 90% of the estimated US offshore money sat in other havens such as the Caribbean, where some deposits may belong to companies rather than families. It also treats the years after the 2008 crackdown as if nothing had changed. These choices probably push the offshore piece up somewhat, but the paper's cautious scenario covers much of this, and offshore income moves the top 1%'s income share by less than half a point.

Technical detail and evidence

Why it matters, in detail. On its own, offshore evasion moves the top-1% share of unreported income from 11.4% to 22.2% (benchmark) or 16.7% (low), and the top-1% fiscal share from 19.8% to 20.2% or 20.0% (Tables A6, A10). Plausible corrections would scale the benchmark flow down by roughly a quarter to a half: a smaller household share of Caribbean deposits, a concealment share falling toward about 85% after 2009 for the pooled window, and a return of about 5%. That is -2 to -5 pp on the no-DCE headline increment and -0.1 to -0.2 pp on the fiscal share. The distribution assumption mainly shifts income within the top 1% (p.34), and FATCA data support it for the US (33% to the top 0.01%).

Evidence. Dec 2025 Table 1 p.26; pp.24-28; fn 39-41. AJZ2017bData.xlsx sheet T.A3, US row: $1,058.2bn total, $85.1bn Switzerland, $440.1bn Caribbean; the US holds 69.5% of the Caribbean allocation. AJZ (2018), NBER w23805 pp.11-12. Senate PSI (2008) p.10: CHF 18.5bn undeclared vs 2.6bn declared = 87.7%. Johannesen et al. (2020) abstract. FATCA paper (9 Mar 2023 draft) Tables 2, 4, A5. Tables A6 and A10: offshore alone adds +10.8 pp to the top-1% share of unreported income and +0.4 pp to the top-1% fiscal share. out_source_checks.txt sections 1-5. Auditor B listed the concealment and 2007-base assumptions as unvalidated dependencies without grading them.

Why this severity. Each input plausibly biases the offshore component upward. But the paper's low end (flow 52% lower) brackets most of this, and offshore contributes only about 0.4 pp to the top-1% fiscal share. A 25-50% lower offshore flow would cut the no-DCE benchmark headline by a few points (out of 21.6) and the fiscal share by about 0.1-0.2 pp.

The authors' response. Reck, Risch & Zucman (2021): the offshore estimates 'reflect a time before the enforcement that began in 2008', and non-profits report directly, so they do not enter the asset-liability gap. The Dec 2025 draft (pp.27-28) uses FATCA data (about $2tn in havens in 2015-18, 5-6.5% returns, 33% to the top 0.01%) as validation and reports a low-end scenario. AJZ (2018) judged the Cayman bias 'likely to be limited' in aggregate.

6minorconfirmed · newly identified here · misrepresentation of source

The paper says its estimates of how much hidden income goes to the top exceed those of two critics because the critics ignore offshore and business-level evasion. About half the difference actually comes from the paper's own way of spreading the IRS's standard correction, and under the paper's most cautious combined assumptions the difference disappears.

Technical detail and evidence

Why it matters, in detail. The benchmark gap to AS is 30.3 - (16 to 18) = 12.3-14.3 pp. Of this, 23.8 - (16 to 18) = 5.8-7.8 pp is the DCE allocation and 6.5 pp is sophisticated evasion. Under DCE-low the whole excess (21.9% vs 16-18%) is sophisticated evasion; at the joint low end the excess disappears (about 16%).

Evidence. Dec 2025 p.41 and fn 63; Table A8; DCE note Table 3a; Auten & Splinter (Dec 2024), Reply to Iselin and Reck, fn 2 and p.3; out_reconstruct.txt section 4.

Why this severity. A hedged ('plausibly') interpretive sentence about another research team's series. It partly holds at the paper's low DCE end and does not affect the paper's own estimates.

7minorconfirmed · newly identified here · internal inconsistency

The mathematical appendix has several slips: a condition stated backwards in the main text, an inequality flipped in two places, a wrong formula, and proof steps that do not follow as written. The theory's conclusions still hold in standard cases, and the paper's data results do not depend on them.

Technical detail and evidence

Why it matters, in detail. The policy comparative static (a costlier high-income audit shifts a fixed budget toward low-income audits) holds when the curvature of the high-income revenue function is below 1, the opposite of the Appendix C restatement. The high-income concealment proposition survives for CRRA preferences, but the general proof needs a bounded rather than vanishing cost term and positive evasion on part of [p1, p0].

Evidence. Dec 2025 pp.42, 73-85. scripts/theory_checks.py: finite differences give dN_l/dc_h = +2.5 at curvature 0.5 and -1.25 at curvature 2; eq. (19) gives -1.36 / -2.14 where the correct values are -7.5 / -3.75; log-utility consumption gaps are 13.5 / 3 at y = 100 to 100,000; with p0 = 0.5 evasion is deterred yet adoption raises utility; the CARA evasion share falls from 1.0 to 0.017.

Why this severity. These are errors in statements and proofs of secondary theoretical results. The propositions hold in standard CRRA and log cases, and no empirical estimate depends on them.

8minorconfirmed · newly identified here · internal inconsistency

Several tables and figures carry wrong labels: the size of one low-income group, the top income group on a chart, the years on a table, and the two IRS designations of the tax schemes, which are swapped. These make the paper harder to check but do not change its conclusions.

Technical detail and evidence

Why it matters, in detail. The A3 inconsistency affects only the bottom decile. The Figure 5 label would imply a top bin ten times narrower. The A7/A1 period mismatch confounds the composition comparison on p.38: for example, dividends are 3.9% of income in 2006-13 but 2.2% in 2008-13 before any DCE adjustment. The notice designations slightly misstate the IRS's legal characterisation of the two scheme samples.

Evidence. Dec 2025 pp.21, 23, 25, 38, 51-57, 61; DCE note pp.27, 32 and Tables 1-2, 4b; IRS Notice 2016-66 and Notice 2017-10, p.1; out_reconstruct.txt section 9; page-25 image check.

Why this severity. Presentation and labelling errors that impede checking but do not change any headline estimate.

9minorconfirmed · newly identified here · arithmetic or transcription

There are a few small number slips, such as $28.7 billion where the stated inputs give $29.6 billion, and 'five times' where the ratio is about four. None of them changes any result.

Technical detail and evidence

Why it matters, in detail. Even if the whole $0.94bn low-end offshore discrepancy went to the top 1%, it would move the top-1% fiscal share by at most about 0.01 pp. The other items are labels and rounding.

Evidence. Dec 2025 pp.3, 14, 26-28, 34, 43 and fn 39, 41; Damodaran histretSP.xls (2006: price 13.62%, total 15.61%); FATCA paper Table A5; out_reconstruct.txt section 8; out_source_checks.txt sections 3-4.

Why this severity. Each slip is small, and none changes a reported result by more than a few hundredths of a point.

10minorconfirmed · previously known · documentation gap

Because the data are confidential IRS records and no code or intermediate totals are published, outsiders cannot re-run the estimates. Key combinations had to be reconstructed indirectly from rounded published numbers.

Technical detail and evidence

Why it matters, in detail. Publishing component totals by bin and the totals for each scenario would let outside researchers reproduce the joint-scenario envelope and the DCE-inclusive aggregate factors exactly, without disclosing taxpayer data.

Evidence. Dec 2025 Section 5 and Tables 2, A6, A8-A11; NBER supplementary materials list only an appendix PDF.

Why this severity. Understandable given IRS confidentiality, and the macro allocations are described well enough to reconstruct to about ±0.15 pp; no bias is demonstrated.

The authors' response. The data are confidential tax records; the paper publishes detailed share tables and an explicit list of assumptions (Table 1).

11minorplausible · previously known · methodology

The audit-based amounts count what examiners first proposed, before taxpayers' appeals, and at the very top more than half of proposed amounts are disputed. Some of what is called 'evasion' may be legally contested positions, which could overstate top-end evasion by an unknown amount. The main finding that audits miss top-end evasion survives large reversals.

Technical detail and evidence

Why it matters, in detail. The bias applies to levels at the top (NRP top-1% detections, DCE scaling and the 19.5% S-corporation rate). Its size is not identified, because appeal outcomes are not observed in the NRP and partly reflect taxpayers' resources to litigate.

Evidence. Dec 2025 fn 1 p.2, p.42, Figure A12 p.83; DCE note Section 5; Hemel, Holtzblatt & Rosenthal (2022); Auten & Splinter (2021).

Why this severity. This is a disclosed caveat shared by all tax-gap-based distributional work, including the critics' own. The operational-audit comparison in C1 survives even if two-thirds of top-end recommendations were reversed (a lower bound of about 0.4% vs <0.05% in the NRP).

The authors' response. Footnote 1 says the definition includes positions taxpayers would argue are legal; Section 6 and Figure A12 discuss gray areas; final outcomes are endogenous to taxpayers' resources to dispute (Appendix C.2).

Claims examined and rejected

Problems one auditor raised that did not survive checking.

The high-end 11% taxable return ('return on average equity for all U.S. banks, averaged over 2007') is mis-stated, because FDIC's 2007 ROE is 8.17%; the high-end offshore flow should therefore be $123bn, not $165bn. — FRED series USROE ('Return on Average Equity for all U.S. Banks'), which matches the paper's wording, averages 11.33% over the four 2007 quarters (12.10, 12.13, 11.75, 9.35). FDIC's full-year figure for all insured institutions is a different measure. The auditor could not reach FRED; it was reachable for this adjudication.
The 6% benchmark return leans high: with 2007 data the first-draft formula gives about 3.1%, and Johannesen et al. (2020) imply a 2-4% taxable yield. — Not upheld as a separate issue. Correcting footnote 39's mislabelled S&P figure (2006 total return 15.6%) raises the formula's result to 6.9%. The 3.1% comes from substituting 2007's crisis-depressed one-year return, an arbitrary choice. The 2-4% yields come from accounts disclosed in 2009-11, when interest rates were far lower than in 2007. FATCA haven yields are 5.0-6.5%. The return is kept only as a minor plausibility element in F4 and a citation slip in F9.
The Conclusion's 'at least 6 percentage points' of the top-1% under-reporting rate due to sophisticated evasion is not supported (net increment 4.7 pp with DCE). — The sentence explicitly describes the benchmark scenario. There the gross sophisticated component is about 6.4-7% of top-1% true income (both auditors' diagnostics), and the 12.4 -> 17.1 difference mixes denominators with the DCE double-count removal. It does not hold at the low end (about 1.7-3.3 pp), but the paper does not claim it does.
The joint low-low top-1% fiscal income share is about 19.4% (-0.9 pp). — The magnitude is corrected; the direction is upheld in F1. The construction subtracts the DCE-benchmark-allocated double-count removal (which is concentrated at the top) from DCE-low amounts. The exact additive identity gives 19.7% (rounding range 19.5-19.85%), i.e. -0.6 pp.
The headline framing on a no-DCE baseline (I1) is a major issue. — Regraded to moderate (F2). The figure is correct for its baseline, the DCE-inclusive results are disclosed in the body, and the level effect of sophisticated evasion is similar with and without DCE.
The pass-through benchmark issue is major, with confirmed confidence. — Regraded to moderate / likely (F3). The S-corporation profile is the paper's own low end and lies inside the abstract's range. A mid-range RRM changes the benchmark headline by about a sixth, and whether the benchmark is biased (rather than merely unvalidated) is not demonstrated.
The theory errors constitute two moderate issues (reversed comparative-static condition; invalid concealment proof). — Merged and regraded to minor (F7). The errors are real but lie in proofs and restatements of secondary results, which hold in standard cases; no empirical estimate depends on them.
Headline changes across versions accompany disclosed methodological revisions and are not undisclosed version instability. — Partly rejected. The change of DCE method is disclosed, but the reversal of the DCE2001-only result for the same method and years (+0.6 -> -0.6 pp) is not explained anywhere (F5).
Applying the Scandinavian (wealth-rank) HSBC distribution to income ranks makes the benchmark and high-end offshore distributions unreliable. — Not material. The paper's FATCA-era check (33% of individual and partnership haven wealth to the top 0.01% by income) is close to the benchmark's 35%, and the distributional assumption mainly reallocates within the top 1% (p.34). It is noted as a minor element of F4.
'1.7% of total U.S. household wealth' is wrong (1.5-1.6% in the current Z.1); the 1.2% operational-audit bound computes to 1.09% with SOI data. — Not errors. The first reflects the Financial Accounts vintage and the household vs household-plus-nonprofit concept. The second uses a different tax-liability concept (SOI income tax after credits vs corrected liability in the operational data); the difference does not affect the >20x gap with the NRP.
The S-corporation sample count differs (4,815 in Johns 2009 vs 4,515 in GLRRZ). — Not counted. It may reflect sample restrictions; the aggregate rate reproduces (19.51% vs 19.45%), and nothing indicates an effect on estimates. It is listed under limitations.

Audit notes

What reproduced. Reproduced from published material: the abstract's +9-33 pp, the Nov 2023 '+50%' and '+~1 pp', the top-1% rate identities, the DCE-inclusive 1.11-1.29 aggregate factor (and its no-DCE analogue of 1.40-1.94), the offshore flows (benchmark and high exact; low-end printed $28.7bn vs $29.6bn computed), the AJZ stock, and the FRED-based return parameters. The adjudicator reconstructed the joint scenarios the paper does not report, using an exact identity of the paper's additive macro allocation: low-low top-1% fiscal share 19.7% (19.5-19.85%), top-1% unreported share 16.2%; high-high 23.4% / 44.5%. The Nov 2023 joint low is also about 19.7%. Theory claims were checked numerically. Not reproducible: every microdata result (NRP 2006-13, operational audits, OVDP/FBAR lists, S-corporation study and owner links, Form 8886 filings, DCE simulations), because the data are confidential IRS records and no code is published. Scripts: final/scripts/reconstruct.py, source_checks.py, theory_checks.py (outputs out_*.txt).

Limits of this audit. No IRS microdata or code were available, so every distributional estimate is taken as published. The joint-scenario values rely on the additive macro-allocation method the paper describes and on rounded published shares and rates from slightly different periods (DCE totals are 2008-13 based), so they carry roughly ±0.15 pp of uncertainty; an exact IRS rerun could move them slightly but not their sign. The FATCA paper was checked in its 9 March 2023 draft, not the 2024 version GLRRZ cite. Auten-Splinter's online-appendix '18%' figure was not located (their December 2024 reply gives 16-17%). The Credit Suisse 85-95% figure was not re-checked (auditor A verified it). The 2020 CRIW conference version and the CEPR DP were not obtained, and no published JPubE version exists yet: Reck's site says revise-and-resubmit, Zucman's site says forthcoming. The Dec 2025 draft (identical text on danreck.com and irs.gov) is treated as the current version, and the Nov 2023 version (listed in the work record) was checked for its headline claims and sensitivity tables. Figures were checked only where they carry numbers used in the text.