Bertrand Garbinti, Jonathan Goupille-Lebret, Mathilde Muñoz, Stefanie Stantcheva, Gabriel Zucman · NBER WP 31333 (2023), revised April 2026; R&R Review of Economic Studies

Tax Design, Information, and Elasticities: Evidence From the French Wealth Tax

18 problems found: 10 moderate · 8 minor

What the paper claims

Bunching is sharp at information-disclosure thresholds (simplification thresholds at EUR 3M in 2011-12 and EUR 2.57M from 2013; the exemption threshold) but absent at pure tax-rate kinks; elasticities to tax rates are 'very small and insignificant'.
Lowering the simplified-return threshold from EUR 3M to EUR 2.57M (2013) reduced reported wealth growth of affected taxpayers: 'annual wealth growth rates are on average 20% lower among affected taxpayers'.
The response is driven by a minority of compliers (bunchers) who cut reported growth by 3pp or more.
The decline 'appears due to increased evasion facilitated by the lower disclosure requirements' rather than real saving changes; hassle-cost or privacy motives are unlikely to be central.
Responses are persistent and cumulative, grow for later cohorts, and are not reversed when detailed disclosure is restored (EUR 3M episode).
Responses to disclosure requirements are ten times larger than responses to kinks in tax rates; the disclosure effect equals raising the marginal wealth-tax rate from 0.7% to 2.84%.
Fiscal cost: by 2017, 19% of counterfactual taxpayers in the affected bracket are missing; bunchers evade 18.4% of their wealth tax (EUR 2,435/yr, 2% of taxable income); offsetting the revenue loss requires raising bunchers' effective rate by 22.5%.

Every problem found

1moderateconfirmed · newly identified here · methodology

When France raised the wealth-tax entry point to EUR 1.3 million in 2011, anyone just above it suddenly owed EUR 1,250-2,750 while anyone just below owed nothing. That jump alone is a strong reason to report wealth just under the line, so the evidence at this threshold cannot show that paperwork rather than tax drove the response. The paper's main evidence, at EUR 2.57 million, is not affected.

Technical detail and evidence

Why it matters, in detail. The 2010-to-2011 change at EUR 1.3M turned a 0.2pp MTR kink into a EUR 2,750 liability notch plus a filing/disclosure discontinuity. At the paper's own dynamic kink elasticity (0.13), the notch alone implies a bunching region of ~EUR 24-31K (about 70-95 times the kink's) and 15-20% missing mass in the paper's window, matching Table B.4 for 2011-13; the contrast cannot apportion the response between tax and information (the later rise to 41% may still contain a disclosure component).

Evidence. DGFiP notice 2725-NOT (July 2011) p.17: 'le calcul de l'impot s'effectue en appliquant le bareme progressif y compris a la tranche ... comprise entre 800 000 et 1,3 million EUR'. BOFiP BOI-PAT-ISF-40-10 (12/09/2012): tax reduced to EUR 1,500 at EUR 1.3M, decote 24,500 - 1.75%P to EUR 1.4M (worked example EUR 2,980 reproduced). BOI-PAT-ISF-40-10 (14/06/2013): decote 17,500 - 1.25%P, EUR 1,250 at EUR 1.3M (worked example EUR 2,693 reproduced). Paper's Table B.4 p.61: average tax of missing taxpayers EUR 0.47-0.58K (2006-10) vs EUR 2.16-3.30K (2011-17). Quadratic misreporting-cost model with the paper's e=0.13: bunching range EUR 335 for the 2010 kink vs EUR 31.4K (2011 notch) and EUR 23.9K (2013 notch); under Pareto(2) a pure notch removes 19.5% (2011) and 15.0% (2013) of the [threshold, EUR 1.49M) window vs Table B.4's 10.0%, 16.7%, 20.5% (2011-13). Londono-Velez & Avila-Mahecha (2024, NBER WP 32134, Sec. 4) find bunching at Colombian non-exemption (pure tax) notches. Scripts: final/scripts/adjudicator_calcs.py.

Why this severity. Removes the exemption-threshold leg of C1 and the basis for re-interpreting other countries' exemption-threshold elasticities as disclosure responses; the main EUR 2.57M simplification evidence (only a 0.3pp kink) and the pre-2011 exemption evidence (a kink) are unaffected.

2moderateconfirmed · newly identified here · overclaiming

In the first year, reported wealth growth was about a fifth lower for households just under the new cut-off. Across all affected households it was about an eighth lower, and over five years the gap was smaller than the abstract's wording suggests.

Technical detail and evidence

Why it matters, in detail. ITT/control-growth ratios in 2013: 21.4% (Just Below), 22.7% (Far Below), 20.5% (All Below), 12.7% (all treated), 5.9-6.4% (above groups). Five-year cumulative: 5.4-6.8% (windowed DB), ~7-12% (whole-range proxies), ~20-30%/yr (DiD, Just Below only). The headline conflates the first-year below-threshold ratio with an average annual effect on all affected taxpayers.

Evidence. Abstract; Intro p.4 ('equivalent to 20% of the control group's wealth growth rate in 2012'); Fig. 9 p.41 (ITTs -0.47, -0.50, -0.14, -0.45, -0.13, -0.28pp; control 2.2%); Sec. 5.2 p.28 ('0.28 (.03) p.p, which is a 15% reduction'; 0.28/2.2 = 12.73%); Fig. 10 p.42; App. C, Table B.5 p.68. Script: final/scripts/adjudicator_calcs.py.

Why this severity. The first-year below-threshold estimate is reproduced and corroborated by the DiD; the overstatement is in the abstract's generalisation to all affected taxpayers and to an annual rate (about 1.6x for all treated and ~2x for the five-year average, estimator-dependent), not in the existence or sign of the effect.

The authors' response. The introduction specifies that the 0.5pp/20% refers to growth from 2012 to 2013 (p.4), and five-year ITTs are reported in Sec. 4.3.1.

3moderateconfirmed · newly identified here · internal inconsistency

The paper measures how long the under-reporting lasted with two methods, and they disagree: one says the effect kept adding up every year, the other that it grew only slowly. The second method also leaves out part of the data where the groups visibly differ. The paper's long-run numbers, including its revenue-loss table, are therefore less precise than presented, and may be too low rather than too high.

Technical detail and evidence

Why it matters, in detail. Cumulative 2013-17 effect for Just Below: DB 0.89pp (window [-0.07,0.21]) vs DiD 2.0-3.4pp; whole-range DB proxy ~1.5-1.8pp. Window-free Delta P(g<0) exceeds the windowed B by 2.4pp (Just Below) and 1.2pp (all groups) at five years, so Table 1's 2016-17 evaded wealth and tax could be understated by roughly 15-50%. The above-group 2013 ITTs (-0.13/-0.14pp) and the claim that groups above the threshold are 'significantly affected' are fragile.

Evidence. App. C pp.66-68 (Table B.5, Table B.6, fn 24, fn 40); Sec. 4.2.3 pp.19-20; Figs. 9-10 pp.41-42. Adjudicator digitisation of the vector figures (final/scripts/digitize.py, bunching_stats.py, inline_checks.py; final/derived/inline_checks.json). Proxies use bin centres of normalised growth and the plotted range [-0.4,0.4] (~87% of five-year mass).

Why this severity. First-year results and qualitative persistence survive, but five-year magnitudes and the 2014-17 trajectory of Table 1 are uncertain by a factor of roughly 1.5-4, most likely in the direction of understating cumulative effects.

The authors' response. Footnote 24 asserts that DiD and DB ITTs are consistent (shown for 2013 only); footnote 40 attributes the DB's precision to focusing on the excluded range.

4moderateconfirmed · newly identified here · overclaiming

The '22.5%' means that the households who gamed the threshold had, by 2017, avoided about a fifth of their own wealth tax. But there were only about a thousand such households in the group studied, and the lost revenue was around EUR 1-3 million a year against a tax raising EUR 4-5 billion. So the paper's talk of 'sizable fiscal costs' is not backed by its own numbers.

Technical detail and evidence

Why it matters, in detail. The offset metric s/(1-s) rises mechanically with years of stacking (s = 8.7% to 18.4%) and with the counting rule (cohort-based 18.4% vs cross-sectional 9.5%). The policy-relevant aggregate is ~EUR 1.3-2.9M per year under both methods (~0.05% of ISF revenue); a uniform ~0.05% rise in ISF collections, or ~1% on the cohort's tax, would restore neutrality. Bunchers cannot be targeted ex ante.

Evidence. Abstract; Intro pp.5-6; Sec. 5.2 pp.27-28 and fn 29; Table 1 p.45; WIL 2024/17 pp.5, 33-34, Table 4 p.58, Table B.6 p.99; Senate report n.42 (2019-2020), table 'Evolution du rendement brut et du rendement net de l'ISF' (gross EUR 4.3-5.5bn, net EUR 3.5-4.2bn, 2013-17). Arithmetic: final/scripts/adjudicator_calcs.py (1,241 x 1,053 = EUR 1.307M; 1,087 x 2,435 = EUR 2.647M).

Why this severity. The arithmetic is correct, but the abstract and Sec. 5.2 convey a fiscal importance that the paper's own estimates do not show; the behavioural estimates are unaffected. The quantification is local and does not measure possible evasion by simplified filers far below the threshold, which the paper neither estimates nor rules out.

The authors' response. Footnote 29 notes the estimates are upper bounds because no audit recovery is assumed; the 2026 version gives no aggregate figure.

5moderateconfirmed · newly identified here · methodology

The paper uses a second episode, a EUR 3 million cut-off in 2012, to confirm that paperwork rather than tax rates drove the response. But in 2012 that cut-off also came with a sharp jump in the tax rate, and the paper's own charts show people reacting to it. That episode is therefore not a clean confirmation, though the main 2013 evidence stands.

Technical detail and evidence

Why it matters, in detail. The 2012 spike at the kink (~80 excess taxpayers in the EUR 10K bin) implies a static elasticity of about 0.02, so the kink probably explains a small share of the 2012 response; but the 2011-to-2012 'confirmation' cannot rule out tax-rate confounds, and fn 15's late-announcement explanation of the larger 2012 bunching ignores a fourfold stronger tax incentive at EUR 3M in 2012.

Evidence. BOFiP BOI-PAT-ISF-40-10 (12/09/2012) Sec. II-III (worked example EUR 13,620 for EUR 3.144M reproduced); NBER 2023 appendix Sec. B.5 p.86; paper fn 15 p.12, Sec. 4.3.1-C pp.23-25, Fig. 3 p.38, Fig. 11 p.43, Fig. A.1B p.46. Adjudicator digitisation: final/derived/inline_checks.json (fig3B, fig11B).

Why this severity. An undisclosed tax discontinuity at the threshold used as confirmation and for the hysteresis analysis; the 2011 EUR 3M (no kink) and 2013 EUR 2.57M episodes still show disclosure responses, and the visible spike implies a small elasticity (~0.02), so the main estimates are unaffected.

The authors' response. Footnote 15 attributes the larger 2012 response to the late (May 2011) announcement of the reform.

6moderateconfirmed · newly identified here · methodology

The paper argues people wanted the short form in order to hide wealth, not to save effort, because the short form did not draw more people into filing. But its comparison pits different years, thresholds and tax rules against each other, measured over windows of very different width. Measured comparably, the numbers could point the other way.

Technical detail and evidence

Why it matters, in detail. Missing share = missing / counterfactual within [threshold, top). For 2017 it is 41.3% in a +15% window vs 30.4% in a +31% window; extrapolated to the +53% width used for 2010 it is plausibly ~20-25%, against 40% in 2010, despite a notch that should increase missing mass. The test cannot reject a fall in the fixed filing cost gamma.

Evidence. Sec. 5.3 pp.30-31; Table B.4 and notes p.61; NBER 2023 text p.32 and appendix Table B.5 p.93; WIL 2024/17 Table B.5 p.99 and p.36. Window arithmetic: final/scripts/adjudicator_calcs.py (hassle_test_windows).

Why this severity. The only empirical support for the claim that hassle or privacy motives are not central (which supports the evasion interpretation) does not discriminate between hypotheses; a like-for-like comparison would, if anything, point the other way. Behavioural estimates are unaffected.

The authors' response. The paper also argues that records must be kept regardless of the form and that the administration already holds much of the information (p.30).

7moderateconfirmed · newly identified here · overclaiming

People filling in a two-box form tend to write round numbers, while totals added up from long itemised forms end in random digits. That, rather than cheating, explains most of the pattern the paper presents as evidence of manipulation.

Technical detail and evidence

Why it matters, in detail. Excess zeros are a form effect (~0.045 among all simplified filers, including the 2010-11 placebo), with a residual ~0.012 concentrated just below the threshold; that residual is consistent with bunchers choosing a number below the cut-off, which bunching already implies, and adds little independent evidence of underreporting.

Evidence. Fig. A.17 p.57; App. B.2 pp.65-66; Sec. 5.1 pp.26-27; Intro p.5. Adjudicator digitisation (final/scripts/lastdigit.py; final/derived/figA17.json) matches Auditor A's (claude/derived/figA17_lastdigit.json).

Why this severity. Removes most of the independent weight of a piece of mechanism evidence highlighted in the introduction; the evasion interpretation still rests on other evidence (sharp bunching under asset-price noise, persistence), and the behavioural estimates are unaffected.

The authors' response. Sec. 5.1 describes the pattern as 'indicative of rounding or deliberate manipulation'.

8moderateconfirmed · newly identified here · internal inconsistency

The later groups were chosen after the rule change, so they are full of people who had already gamed the threshold; finding more gaming among them shows that it persisted, not that it spread. Some numbers reported for these groups, such as negative shares of 'bunchers', show that the method's assumptions do not hold there.

Technical detail and evidence

Why it matters, in detail. Conditioning on post-reform wealth (e.g., W_2013 in [2500K, 2570K)) selects stackers; negative first stages (B < 0) for above groups indicate selection or defiers; signed Wald ratios have the opposite sign to the labels. Later-cohort comparisons are descriptive, not LATEs.

Evidence. Fig. A.11 p.53; Fig. 11B p.43; Sec. 4.3.1-B p.23 and fn 25; App. E p.72; Intro p.5. Adjudicator digitisation: final/derived/inline_checks.json (A11 panels).

Why this severity. Affects a secondary claim within C5 (growth and spread of responses over time); persistence within the fixed 2012 cohort is unaffected, and the authors flag selection in a footnote.

The authors' response. Footnote 25: cohorts defined in 2013 and 2016 'are constructed after the reform was implemented, and may therefore be affected by selection'.

9moderatelikely · previously known · overclaiming

The paper says the paperwork change mattered ten times more than tax rates. But it measures the tax-rate effect only at tiny steps in the tax schedule, where people barely react even when they do respond to taxes over longer periods. Using other well-known estimates of how wealth responds to tax rates, the gap could be much smaller.

Technical detail and evidence

Why it matters, in detail. tau' = 1 - (1 - tau0)(1 - ITT/e) with tau0 = 0.7% and ITT = 0.28pp gives tau' = 2.84% at e=0.13 but ~0.75-1.3% for e in [0.5, 6]. Long-run DiD elasticities in comparable settings are one to two orders of magnitude above the French kink estimates; at such elasticities the per-year response to a 0.2pp rate change (~0.1-0.25pp/yr) would be of the same order as the one-year disclosure ITT.

Evidence. Abstract; Intro p.6; Sec. 3.1 pp.10-11; Sec. 5.2 p.28; Fig. 1 p.36. JJKZ (2020) QJE 135(1): fn 15 and Table II. Saez & Zucman (2019) BPEA p.472. Kopczuk (2019) BPEA comment p.516 (corpus us-wealth-taxes-18 / optimal-tax-behavior-16). Brulhart, Gruber, Krapf & Schmidheiny (2022) AEJ:EP 14(4) (optimal-tax-behavior-19). Advani & Tarrant (2021) Fiscal Studies 42(3-4) (optimal-tax-behavior-20). MTR equivalence: final/scripts/adjudicator_calcs.py.

Why this severity. The abstract sentence is literally about kinks, and the order-of-magnitude contrast in sharp local bunching is real; but the broader message that disclosure matters far more than tax rates depends on treating tiny-kink bunching as the tax-rate response, which the authors' own related work warns against.

The authors' response. Sec. 3.1 (p.11) acknowledges that 'behavioral responses may still be prevalent but not visible at the kinks', and fn 3 cites JJKZ's view that static bunching may capture short-term responses.

10moderateplausible · previously known · speculative assumption

People may have reported less wealth by cheating, but also by legal moves such as giving money to children before the valuation date or valuing their homes conservatively. The paper's tests cannot tell these apart, so 'evasion' is a reasonable guess rather than a demonstrated fact.

Technical detail and evidence

Why it matters, in detail. Misreporting is inferred from (i) the sharpness of bunching under asset-price noise, (ii) null income responses with low power and (iii) housing correlates that are not robust to controls; none of these rules out gifts, debt-financed exempt assets or valuation choices within legal latitude, which would also be invisible on the simplified return.

Evidence. Abstract ('appears due to increased evasion'); Intro p.5; Sec. 5.1 pp.25-27; App. B pp.62-66 and fns 35-36; Table B.3 p.60; NBER 2023 version p.29 ('We do not detect any such differences between the treated and control groups'). Kopczuk (2019) BPEA comment pp.516-517 on gifting below thresholds.

Why this severity. The behavioural response to disclosure stands regardless of mechanism; its classification as evasion, which drives the policy and welfare interpretation, is suggestive rather than established. The abstract hedges ('appears').

The authors' response. The paper acknowledges that the income test is underpowered (pp.26, 65) and that exempt assets cannot be tracked (fn 35); the abstract says the decline 'appears' due to evasion.

11minorconfirmed · newly identified here · internal inconsistency

The paper says the tax-rate effects could not be told apart from zero, but one of its own estimates clearly can. The effects are still small, so little changes in substance.

Technical detail and evidence

Why it matters, in detail. Normal-approximation z: dynamic e 3.25, ITT 3.0, third-kink B 3.0, static b 2.0; static elasticities 0.08 (0.06) and 0.14 (0.11) are insignificant. The correct statement is 'small, and in one of four estimates statistically significant'.

Evidence. Abstract; Intro pp.3-4; Sec. 3.1 pp.10-11; Fig. 1 p.36; Conclusion p.32. z-statistics: final/scripts/adjudicator_calcs.py (kink_significance).

Why this severity. Statistical-description errors; the economic magnitudes (elasticities 0.02-0.14) are small whatever their significance, so the substantive conclusion that kink responses are small is unchanged.

12minorconfirmed · newly identified here · methodology

A formula in the paper's theory appendix is derived incorrectly, but the intuition it illustrates still holds, and none of the empirical results depend on it.

Technical detail and evidence

Why it matters, in detail. At the corner w_{t+1} = S, FOC_{t+1} = lambda >= 0, so v'_t + beta*v'_{t+1} + h'_t - beta^2*h'(0) = tau(1+beta) + beta*lambda. Current reports depend on S through -beta*h'(w_t - S), not on future true wealth.

Evidence. App. D pp.69-70; Codex numerical counterexample (codex/scripts/audit_calculations.py, model_KKT_counterexample).

Why this severity. An error in an illustrative model that generates no estimate; the qualitative prediction (anticipatory misreporting) survives a correct derivation.

The authors' response. The model is presented as an illustrative rationalisation of the findings.

13minorconfirmed · newly identified here · misrepresentation of source

The paper gets some dates and form details of the French reforms wrong. This does not change its results.

Technical detail and evidence

Why it matters, in detail. Mis-dated enactment and a time-invariant description of a reporting regime that changed in 2012 and 2013; no identification consequence beyond F6.

Evidence. BOFiP ACTU-2013-00151; BOI-PAT-ISF-50 (12/09/2012) para. 30; BOI-PAT-ISF-40-10 (12/09/2012); DGFiP notice 2725-NOT (2011) pp.1-5; paper pp.2, 9, 12, 37-38, 46, 58.

Why this severity. Descriptive errors; no estimate depends on the month of enactment or on these labels (item (c) is related to F6).

14minorconfirmed · newly identified here · arithmetic or transcription

Some numbers in the text are described loosely, for example a 2017 value presented as if it held every year. The tables themselves are correct.

Technical detail and evidence

Why it matters, in detail. Denominator confusion (19% of the counterfactual excluded range vs 7.7% of the cohort), year-specific values presented as annual, and an income-concept mismatch in the compliance-cost benchmark.

Evidence. Intro pp.5-6; Sec. 5.3 p.31; fn 16 p.13; Table 1 p.45; Fig. 10D p.42; Table B.2 p.59. Arithmetic: final/scripts/adjudicator_calcs.py (fiscal_mean_gain_2013_17, benzarti).

Why this severity. Wording and denominator slips that make magnitudes sound larger or more uniform than the tables show; no effect on the estimates.

15minorconfirmed · newly identified here · documentation gap

Some key choices are not spelled out and the data are confidential, so outsiders cannot fully re-run the analysis.

Technical detail and evidence

Why it matters, in detail. Exact replication requires per-panel windows, control definitions, bin-level growth and the bootstrap scheme; window choice matters at five years (F3).

Evidence. Sec. 4.1 p.14; eq. (2) p.17; fn 26 p.24; fn 28 p.27; Fig. 8 p.40; Sec. 4.2.3 p.19; window positions digitised (final/derived/*.json); no replication package located (Dataverse search by Codex; NBER appendix directory).

Why this severity. Limits external verification; no computational error follows from these inconsistencies (the pooled and balance checks pass).

16minorlikely · newly identified here · data error

One of the traits used to describe who gamed the system was measured years after the events, so it may be a result of the rule rather than a cause.

Technical detail and evidence

Why it matters, in detail. A post-treatment covariate is used as a 2010 control; the 'No Accountants x Treated' coefficient (0.09***) and the attenuation of the housing interactions cannot be read as pre-determined heterogeneity.

Evidence. Fig. A.6G p.49 (axis label text extracted from the PDF); Table B.3 p.60; App. B.1.1 pp.62-64; Sec. 5.1 p.26.

Why this severity. Weakens one supporting mechanism correlation and the housing-share conclusion conditional on it; no effect on the main estimates.

17minorplausible · newly identified here · speculative assumption

The paper says a small minority made big cuts in reported wealth. That reading assumes everyone else did not change behaviour at all, which the paper's own theory suggests is not quite true. In the first year, though, the data look consistent with the 'small minority' story.

Technical detail and evidence

Why it matters, in detail. ITT = p_c*Delta_c + p_at*Delta_at; with Delta_at < 0, ITT/p_c overstates |Delta_c|. The 2013 distributions show a local response (excess mass in [aL,0) matched by missing mass in [0,aU), little change elsewhere), so the illustrative 20-30% of always-takers responding by 0.5pp is not supported; the bias may matter at five years.

Evidence. App. D pp.69-71; App. E pp.71-73; Intro pp.4, 6; Fig. 9 p.41. Adjudicator: final/derived/inline_checks.json. Codex illustration (codex/calculations.json).

Why this severity. An internal inconsistency between the illustrative model and the identifying assumption, with little demonstrated impact on the headline 2013 LATEs.

The authors' response. The identifying assumptions are stated explicitly in Appendix E.

18minorplausible · newly identified here · overclaiming

The paper suggests its French results apply broadly, including to income taxes, but countries where banks report directly to the tax office are quite different.

Technical detail and evidence

Why it matters, in detail. Disclosure effects are expected to scale inversely with third-party coverage; transporting the French magnitude to third-party-reported bases is unsupported.

Evidence. Sec. 5.3 pp.31-32; JJKZ (2020) QJE pp.332-333; Saez & Zucman (2019) BPEA pp.440, 472.

Why this severity. Interpretive extrapolation; it does not affect the estimates and holds for some countries (France, Spain, Switzerland, Colombia).

Claims examined and rejected

Problems one auditor raised that did not survive checking.

I9: the rise in later-cohort pooled buncher shares largely reflects wider bunching windows (with 2012 windows, All Groups B is 6.6% and 8.5% rather than 9.1% and 10.6%). — The window-free complier share P(g<0)_T - P(g<0)_C, which needs no window, also rises across cohorts (all groups 7.35 -> 9.59 -> 11.03pp; all below 10.15 -> 14.31 -> 14.89pp), so the wider windows track where the distributions diverge. The selection concern is kept in F10.
I12: pooled 2013 B 'falls 19% with the benchmark aL', showing that pooled estimates (inputs to 'ten times' and Table 1) are fragile. — The -0.04 benchmark is the Just Below window. The pooled panels include groups whose bunching extends further down, and the drawn pooled window gives 7.27%, against a window-free complier share of 7.35pp. The window concern is kept for the five-year panels (F3), where truncation runs the other way.
I2: read as an average annual effect over 2013-17, the headline overstates by roughly 4x (20% vs ~5-7%). — The 5-7% relies on windowed five-year dynamic-bunching estimates that omit visible treated-control differences. Whole-range proxies give ~10-12% for below-threshold groups and the paper's DiD >=20%, so the overstatement is ~2x and estimator-dependent (kept in F2 and F3).
I4: headline quantification and results changed across versions without reconciliation (stand-alone 'version instability', moderate). — The 2024-to-2026 fiscal change reflects a different estimator and population (static cross-section vs the 2012 cohort), not a silent revision of the same estimate. Its substantive parts are kept elsewhere: selective adoption of the larger per-buncher figure (F4), the verdict flip of the exemption test (F7) and the asset-composition reversal (F9). The remaining items (intro elasticity range, Far Above B 1.4% -> 3.1%, non-resident share) are ordinary revisions with no bearing on conclusions.
Initial lead (withdrawn by Codex): the pooled ITT is inconsistent with the group ITTs (implied pooling weights 0.469 vs 0.661 from buncher shares). — The plotted pooled distributions are an exact 0.651/0.349 mix of Figs. 9D and 9E for both treated and control (max residual 6e-6, adjudicator and both auditors). The ITTs use different windows and within-bin raw growth, so the naive comparison is invalid.
I3: illustrative sensitivity in which 20-30% of always-below taxpayers respond by -0.5pp, making complier effects 21-32% smaller. — The 2013 distributions show a local response (windowed B close to the window-free complier share; small differences outside the windows), so the illustrative magnitudes are not supported for the headline year. The logical concern is kept as minor (F11).
I15: Table B.4 lists EUR 1,310K as the 2011-12 exemption threshold, whereas the legal threshold was EUR 1.3M. — Immaterial: EUR 1.31M was the upper bound of the 2011 first bracket, and a EUR 10K difference has no bearing on any estimate or conclusion.

Audit notes

What reproduced. No microdata or code exist (confidential DGFiP data in CASD). Reproduced from published material by an independent digitiser of the Stata vector figures (final/scripts/digitize.py, bunching_stats.py): all printed buncher shares in Figs. 9, 10, 11A-B and A.11 within 0.07pp (e.g. Fig. 9: 14.35/8.77/3.62/9.48/3.19/7.27 vs 14.3/8.7/3.6/9.4/3.2/7.3); kink panels 0.18/0.84 vs 0.17/0.78; the excess = missing mass rule in every simplification panel; pooling weights (9F = 0.651*9D + 0.349*9E); LATE = ITT/B; and the Table 1 arithmetic against the statutory 2013-17 schedule (within 1-2%), with BOFiP's worked examples reproduced exactly. Headline arithmetic reproduces (22.5%, 2.84%, 9.3x, 1.5%) except the '15%' on p.28, which should be 12.7%. ITTs were only approximated with bin centres of normalised growth (2013 Just Below -0.56 vs -0.47; all groups -0.36 vs -0.28; 2012-17 all groups -0.80 vs -0.77). Not reproducible: exact ITTs, bootstrap SEs, the DiD, the Table B.3 regressions, the income and portfolio tests, and the Table B.4 Pareto counterfactuals. New adjudicator results: whole-range vs windowed comparisons at five years (F3), the 2012 EUR 3M kink spike (F6) and the relative window widths in the hassle test (F7).

Limits of this audit. No microdata or code: all quantitative checks rest on published figures and tables. ITT proxies use bin centres of normalised growth, and the five-year whole-range proxies cover only the plotted range [-0.4, 0.4] (~87% of mass), so they indicate direction and rough size only. Legifrance was inaccessible, so schedules come from BOFiP (2012, 2013), the DGFiP 2011 notice and Senate reports, cross-checked against their worked examples. Not verified: the Benzarti 0.6-0.8% figure, exact percentile positions, and whether the '2021' label on Fig. A.6G is a typo. No published critique of or author reply to this paper was found (web search; OpenAlex citing works reviewed by title only); the authors' VoxEU column was not reviewed and the authors were not contacted.