Thomas Piketty, Emmanuel Saez, Stefanie Stantcheva · American Economic Journal: Economic Policy 6(1): 230-271

Optimal Taxation of Top Labor Incomes: A Tale of Three Elasticities

18 problems found: 1 major · 8 moderate · 9 minor

What the paper claims

Theory: with zero welfare weight on top earners, the revenue-maximising top rate is tau* = (1 + t*a*e2 + a*e3)/(1 + a*e); it rises with the zero-sum bargaining elasticity e3 and tends to 100% as the real elasticity e1 tends to 0.
Top-rate cuts are associated with rising top-1% pre-tax income shares; the long-run total elasticity of top incomes to the net-of-tax rate is 'large, around 0.5'.
Top-rate cuts are not associated with higher growth, so the real supply-side elasticity e1 is small: 'e1 is at most 40 percent of the total elasticity'.
Tax avoidance explains little of the long-run rise in top incomes (e2 < 0.1), because top shares including and excluding realised capital gains show the same elasticity.
US CEO 'pay for luck' is larger when top tax rates are low (1987-2010) than when they are high (1970-86), while industry workers' wages show no pay for luck.
Across 13 countries in 2006, CEO pay is negatively related to top tax rates even controlling for firm characteristics and performance, and more so in poorly governed firms.
Headline calibration: 'in our preferred estimates' e = 0.5 decomposes into e1 = 0.2 (at most), e2 = 0, e3 = 0.3 (at least), implying a 'socially optimal' top rate of 83% versus 57% in the pure supply-side case.

Every problem found

1majorconfirmed · previously known · overclaiming

The paper's famous 83% top tax rate depends on one number: how much top earners' extra income reflects real extra work and output rather than grabbing a bigger slice. The paper's own growth data are far too noisy to pin that number down. They are equally consistent with the conventional answer of about 57%, so the 83% is an illustration of what follows if the authors' guess is right, not a measured result.

Technical detail and evidence

Why it matters, in detail. tau* is driven almost entirely by e1 (tau* = 1 - a*e1/(1 + a*e)), and e1 is identified only through beta = pi*e1 in an 18-country growth panel whose correctly clustered SE (0.036) is about 0.7 times the beta implied by the full supply-side case (0.05). The test has roughly 25% power against e1 = 0.5, and the e1 point estimate moves between about -0.5 and 0.8 with window, specification (catch-up control vs plain FE), one country's tax coding (Spain, Norway) and the choice of pi (0.06-0.15). The defensible statement is conditional: if e1 is about 0.2 then tau* is about 83%. The evidence spans roughly 57-93% (or 100% for e1 <= 0), so 'e1 = 0.2 (at most)' is not an empirical upper bound.

Evidence. Adjudicator re-implementation of international.do (scripts/pss_intl.py; output/table2_cols1to3_adjudicator.csv, intl_extra_adjudicator.json) reproduces Table 2 exactly. Preferred beta = 0.0083: (a) paper's own HC1 SE 0.0173 -> 95% CI for e1 [-0.26, 0.42]; (b) country-clustered SE 0.0364 (G = 18), t(17) CI for e1 [-0.69, 0.85]; (c) wild-cluster restricted bootstrap (Webb weights, 999 draws): p(beta = 0) = 0.82, CI for beta [-0.052, 0.116], i.e. e1 [-0.52, 1.16]. Power of the test to detect the pure supply-side case (e1 = 0.5, beta = 0.05): 0.82 with HC1 SEs but 0.23-0.28 with clustered SEs; P(e1-hat <= 0.2 | e1 = 0.5) = 0.21. Specification and window: the 2011 version's own specification (country FE + trend, 1975-2008) on the published data gives beta = 0.047 (HC1 0.014; clustered 0.047), i.e. e1 = 0.47 and tau* = 60%; for 1975-2010 it gives 0.061 (tau* = 48%). Across start years 1960-1990 and end years 2007/2010, e1 ranges from -0.52 to 0.40 (preferred specification) and from -0.84 to 0.82 (FE specification) (output/growth_window_sensitivity.csv). Single-country coding: using Spain's statutory top rates (Alvaredo & Saez 2008) moves the preferred beta to 0.016-0.021, and using the package's own XLS Norway rates moves it to 0.015 (e1 roughly doubles). Pi mapping: fn 33 calls pi = 10% a lower bound, but at the start of the preferred window (1981) the top-1% share averaged 6.3% across the 18 countries; pi in [0.063, 0.15] puts the e1 point estimate at 0.06-0.13 and its HC1 upper bound at 0.28-0.67. Of the 15 Table 2B point estimates, 11 imply e1 < 0 and the largest implies 0.37 (FE, 1981-2010). Version history: Nov 2011 NBER WP p. 31 justified e1 <= 0.2 by 'an absolute upper bound b = 0.2 (accounting for the standard errors)' on a FE estimate of 0.012 (0.013), whose own 95% upper bound is 0.037; the 2014 text keeps 'at most 40 percent' with new estimates. Mapping tau* = 1 - a*e1/(1 + a*e), a = 1.5, e = 0.5: e1 = 0.08 -> 93%; 0.2 -> 83%; 0.3 -> 74%; 0.37 -> 68%; 0.42 -> 64%; 0.5 -> 57%.

Why this severity. The 83% vs 57% contrast is the paper's best-known result. Within its own formula, moving e1 from 0.2 to the paper's own 95% upper bound (0.42) gives 64% (-19 pp, about 23% of the level), and to e1 = 0.5 (not rejected under clustered inference) gives 57% (-26 pp, about 31%). That materially changes the headline magnitude. It is not critical because the theory and the conditional calibration remain valid, the point estimates mostly lie below 0.2, and the authors state that the estimates are 'not sharply identified'.

The authors' response. In the paper itself: 'Note that the standard error around this estimate is large as the growth regressions are not precisely estimated' (p. 257); 'those regressions rely on a very strong identifying assumption' (p. 258); 'Naturally, these estimates are not sharply identified but they illustrate the critical importance of the decomposition' (p. 268). No published reply to Reynolds (2019) or Mertens & Montiel Olea (2018) located.

2moderateconfirmed · newly identified here · methodology

The paper's error bars for its cross-country regressions are two to four times too narrow, because each country's year-to-year data are treated as if they were independent pieces of evidence. With correct error bars the link between tax cuts and rising top incomes still holds. The growth results, however, become too uncertain to say much either way.

Technical detail and evidence

Why it matters, in detail. With persistent regressors and residuals, HC1 understates sampling variance by a factor of 4-15 in variance terms. Clustered (CR1) and wild-cluster bootstrap inference with G = 18 should be used. The descriptive tax/top-share elasticities survive, while all growth coefficients become statistically indistinguishable from zero and from pi*e1 = 0.05.

Evidence. international.do (all regressions ', robust'). Adjudicator output/table2_cols1to3_adjudicator.csv: SE ratio CR1/HC1 2.01-3.90. Top-share FE 1960-2010: 0.314, HC1 0.025 vs clustered 0.055; wild-cluster CI [0.22, 0.46] (p < 0.002); 1981-2010: 0.626, CI [0.38, 1.01]. Full-period growth coefficients with clustered SEs: -0.064 (0.106), -0.029 (0.045), -0.095 (0.060), -0.088 (0.066), -0.018 (0.033); none significant (|t| <= 1.6, t(17) critical value 2.11).

Why this severity. This is an inference problem in a core table. It removes the statistical basis for the 'detrimental to growth' reading and is the mechanism behind F1's wide e1 interval, but it leaves the top-share/top-rate association significant. Its consequences overlap with F1.

The authors' response. null in the paper's SE choice; the US time-series analysis (Table 1) uses Newey-West SEs, and Table 2 columns 4-6 report the spread of estimates across 500 random country/period subsamples.

3moderateconfirmed · previously known · overclaiming

Part of the jump in top incomes reported on US tax returns after 1986 came from business owners moving profits from company accounts onto their personal returns, not from earning more. The paper's check for this kind of tax-driven relabelling misses the main way it happens. So the claim that relabelling plays 'no role' is too strong, and some of what the paper calls bargaining could be relabelling.

Technical detail and evidence

Why it matters, in detail. A smaller real-income elasticity under a comprehensive income concept (0.29 vs 0.54 within the same unit) is what PSS's own test (p. 248) predicts under avoidance. The concept gap also includes items unrelated to top-end avoidance (non-taxable fringe benefits of the bottom 99%, imputed rent), so it bounds e2 only loosely, plausibly 0-0.25. The TRA86 break (4 pt in two years) shows that a large part of the measured fiscal-income response is a change in reporting base. Because e3 is computed as e - e1 - e2, any unmeasured e2 is booked as bargaining.

Evidence. usdata.dta (scripts/pss_us.py): excl.-KG top-1% share 8.23% (1960-64) -> 17.66% (2004-08); 1986 -> 1988 jump +4.04 pt = 42.8% of the rise; elasticity 0.52 -> 0.34 if the jump is treated as reclassification. Incl.-KG: 12.66% (1987) -> 15.49% (1988), +2.83 pt (24% of its rise), elasticity 0.52 -> 0.42. PSZ (2018) DINA, equal-split adults (scripts/dina_check.py): fiscal-income top-1% share 9.47% -> 20.79%, elasticity 0.54; pre-tax national income share 12.75% -> 19.44%, elasticity 0.29. Table 1C re-run with DINA pre-tax national income (scripts/table1c_dina.py): top-1% coefficient 0.082 (NW 0.047) vs 0.265 (0.047) with fiscal income.

Why this severity. With e1 held at 0.2, moving 0.1-0.2 of e from bargaining to avoidance changes tau* only to 69-76% under the current base (t = 20%) or 79-81% after base broadening. However, the 'e3 = 0.3 (at least)' claim and the zero-sum reading of the top-share rise lose much of their support. Not major because the headline rate is driven by e1, and the main text (pp. 248-249) is more careful than the table note.

The authors' response. The main text acknowledges other avoidance channels (offshore accounts, perquisites) and argues that they have, if anything, grown since the 1960s (pp. 248-249). Setting e2 = 0 is framed as the post-base-broadening scenario (pp. 237-238). Piketty & Saez's 2006 reply to Reynolds (https://eml.berkeley.edu/~saez/answer-WSJreynolds.pdf) stresses the rise in top wage income. The authors' later DINA series (PSZ 2018) still shows a large long-run rise.

4moderateconfirmed · newly identified here · methodology

To measure how much CEOs are paid for pure luck, the authors compare each firm with the rest of its industry. A coding mistake means the 'rest of the industry' figure still partly depends on the firm itself, and firms with no industry peers get a meaningless value of zero. We cannot tell how much this changes the results, because the underlying data are proprietary.

Technical detail and evidence

Why it matters, in detail. Z_code = (1 - s_it)*Z_LOO, so within-firm variation in Z_code includes -Z_LOO*Delta s_it. With Z in log levels (about 4-10) and s_it changing with firm growth, industry entry and exit, and the 1992 Forbes-to-ExecuComp switch, this term can be comparable to genuine industry shocks (about 0.1-0.3). It is mechanically correlated with own-firm size, which affects pay directly. The direction of bias is unknown, so the published pay-for-luck coefficients are unverified.

Evidence. US CEO analysis/BM_tables.do lines 363-400: 'egen industry_at_roe = total(at_roe), by(sic2 fyear)' (own assets included); only industry_at is reduced by own assets (line 378) and it is unused; the numerator removes the own firm (lines 390-392); 'gen roe_industry = roe_industry_temp2/industry_at_roe' under the comment '* Divide by denominator excluding firm:' (lines 393-396); singleton test on own-inclusive totals (lines 398-400). Logs: lines 115, 126-127. BM_tables_800.do lines 455-457 divide by the own-excluded total. BM_wages.do collapses the same mis-scaled variable to the industry level for the worker regressions (lines 266-306).

Why this severity. Table 3 is one of the three empirical pillars of the bargaining interpretation, and the defect could materially change its IV estimates (0.34/0.70/0.22/0.95) and their period difference. The proprietary data needed to quantify it are unavailable, and the macro results and the 83% are unaffected.

The authors' response. null. The paper (fn 48) reports a Forbes-firm-only robustness check as 'qualitatively consistent'; that program (BM_tables_800.do) uses a different, own-excluded denominator.

5moderateconfirmed · newly identified here · internal inconsistency

The table on CEO pay across countries says it adjusts for company performance and CEO characteristics in all of its main columns, but the program does so only partly in one column and not at all in the others. The headline number is unaffected. The extra results the authors use to argue that CEOs bargain for pay, however, are not as well controlled as described.

Technical detail and evidence

Why it matters, in detail. Mechanism tests (heterogeneity by governance; bonus vs salary) are estimated without performance controls, so they cannot separate rent extraction from performance pay along exactly the dimension the paper says identifies bargaining. The log-zero coding makes column 6's 4.68 potentially scale-dependent: shifting units changes the coefficient by -log(c) times the coefficient on a zero indicator.

Evidence. International CEO analysis/explore_tables.do lines 59-64 (macros), 163-193 (col. 1-6 regressions use firmcontrols in col. 2 and firmcontrols2 = 'lsales industry2 - industry12' in cols. 3-6; ceocontrols unused), 87-88 (zero coding), 47-49 (South Africa); explore_ceo graphs.do lines 90-117 (control-only regression, subtraction of continuous controls only, ttext '1.90 (.29)'), 44-45; Table 4 notes p. 265; text p. 263; Fig. 5 notes p. 264 (13 countries) vs Table 4 note ('14 OECD countries').

Why this severity. The abstract's 'even controlling for firms' characteristics and performance' rests on column 2, which does include performance controls, so the headline CEO elasticity survives as reported. The governance and pay-composition results, offered as mechanism evidence for bargaining, lack the controls claimed. The impact cannot be quantified without the confidential data.

The authors' response. null. Footnote 52 and appendix A.2.4 say that governance results with other index definitions are 'usually in the right direction, but not always significant'.

6moderateconfirmed · newly identified here · internal inconsistency

The cross-country CEO comparison quietly uses a broader measure of taxes, adding payroll and sales taxes, than the one the paper describes and uses elsewhere. With the measure the paper describes, the pattern across countries is much less clear-cut.

Technical detail and evidence

Why it matters, in detail. Payroll and VAT components vary strongly across the 13 countries (Sweden +17 pp, UK +15 pp, US +5 pp relative to income tax), so the regressor mixes income-tax variation with welfare-state size and social-contribution design, which can proxy egalitarian pay norms. The firm-level 1.97/1.90 should be reported under both concepts.

Evidence. taxes.dta: mtr labelled 'Total Top Marginal Tax Rate' (US 0.431, UK 0.552, Norway 0.608, France 0.633, Sweden 0.738) vs inctax (0.35, 0.40, 0.40, 0.428, 0.566); explore_tables.do lines 39-45 and explore_ceo graphs.do lines 38-42. Adjudicator extraction of Figure 5A marker x-positions from the PDF (p. 264): 0.431, 0.523, 0.532, 0.534, 0.552, 0.553, 0.561, 0.575, 0.596, 0.607, 0.632, 0.736, 0.738, matching the total-wedge values. Auditor A's country-level re-estimate from the recovered points (unweighted, 13 points, not the firm-level estimand): 1.55 (0.28) with the plotted wedge; 1.93 (0.98) with income tax only; 1.44 (1.03) income tax only excluding the US. Values match 2006, not the 1996 stated in the readme (e.g. US 35%, Norway 40%, Germany 0.481 = 42% x 1.145).

Why this severity. The total wedge is economically defensible for wage income, so the concept itself is not wrong. But the result is presented as a relationship with income tax rates and is inconsistent with the macro analysis; under the described concept it is far less precise at the country level; and the wedge also proxies welfare-state size.

The authors' response. null

7moderatelikely · previously known · methodology

The paper compares CEO pay before and after 1987 and credits the 1980s tax cuts for the change. Many other things changed at the same time: how CEOs were paid (far more stock options), which data source covers them, and accounting and tax rules on options. So the comparison cannot show that tax rates caused the change.

Technical detail and evidence

Why it matters, in detail. With one break and period-specific firm effects, beta_IV(post) - beta_IV(pre) is identified only up to any coincident change in contract form (option intensity, realised vs granted valuation), data source and sample composition. A realised-pay measure raises measured pay-for-luck in high-option eras whatever drives option use. The worker-wage placebo does not address CEO-specific contract changes.

Evidence. pp. 260-263 and Table 3 notes; BM_tables.do lines 179-218 ('This do file will use totalpay = tdc2 from execucomp'); appendix A.2.3 (TDC1 robustness 'almost unaffected'); Rose & Wolfram (2002), Journal of Labor Economics 20(S2): S138-S175, doi:10.1086/338677 (Section 162(m)); Reynolds (2019) point (4) on option timing.

Why this severity. This limits the causal reading of the secondary US CEO evidence: any secular change in pay practice is loaded onto the tax variable. The size and sign of any bias are unknown, and the authors concede that the test 'is not definitive'.

The authors' response. Workers' wages show no pay for luck in either period, and better-governed firms show less pay for luck (citing Bertrand & Mullainathan 2001). 'Naturally, this test is not definitive' (p. 263).

8moderatelikely · previously known · external inconsistency

The CEO evidence mostly shows that American CEOs are paid more and face lower taxes than CEOs elsewhere. The researchers who built the data explain that gap by American shareholders demanding performance-linked pay, not by tax-driven bargaining. And CEOs of listed companies are only a small part of the top 1%.

Technical detail and evidence

Why it matters, in detail. A country-level regressor with 13 clusters and one dominant cluster (the US) leaves the tax coefficient confounded with every US-specific feature of pay setting (ownership structure, equity-pay norms, market size). FFMM's controls for ownership and board structure attribute much of the premium to performance pay. Even a clean CEO estimate would cover a small fraction of top-1% income.

Evidence. FFMM (2013) RFS 26(2): 323-367; accepted Sept 2012 draft (eml.berkeley.edu/~saez/course131/CEO13.pdf) abstract and p. 10: final sample 1,532 US and 1,480 non-US CEOs. explore_tables.do lines 69-70, 105-110. Bakija, Cole & Heim (2012) Table 1 (2004, top 0.1% incl. KG): top non-financial executives of publicly traded firms 3.8% (Kaplan-Rauh estimate column), vs tax-data shares of 15.0% salaried and 13.6% closely held non-finance executives and 18.4% finance. Mertens & Montiel Olea (2018) QJE 133(4): 1803-1884.

Why this severity. This weakens the micro support for the bargaining share (e3 >= 0.3) that makes 83% rather than 57%, without quantifying an alternative. The paper presents the CEO results as 'suggestive', and bargaining could operate outside public firms.

The authors' response. The paper argues that controlling for performance leaves the tax coefficient unchanged (fn 51) and that the stronger effect in poorly governed firms supports bargaining. It concedes that governance measures are 'bound to be imperfect' (appendix A.2.4). No reply to Kaplan & Rauh or Mertens & Montiel Olea located.

9moderateplausible · previously known · speculative assumption

Even if the key number were right, the 83% would rest on simplifying assumptions: who loses when executives bargain for more pay, whether today's very unequal pay pattern would persist at much higher tax rates, and no knock-on benefits from top earners' work such as innovation. Reasonable changes to these assumptions trim the rate a little; other published models can lower it much more.

Technical detail and evidence

Why it matters, in detail. tau* = (1 + a*e3)/(1 + a*e) is a sufficient-statistics result valid when the income tax can undo the distributional effects of rent-seeking. When it cannot, the corrective term departs from s = e3/e in either direction (Rothschild-Scheuer). a is endogenous to tau, and revenue maximisation ignores spillovers from top effort. The 83% is local to these assumptions.

Evidence. Within PSS's formula (scripts/pss_intl_sensitivity.py): a = 2.0 -> 80% (bargaining) vs 50% (supply side); a = 2.4 (US P99 tails in the 1960s) -> 78% vs 45%; welfare weight g = 0.25/0.5/0.75 -> 80/76/70%. Rothschild & Scheuer (2016) REStud 83(3) calibration: correction 15.9% vs a 25% Pigouvian wedge when externalities fall within the rent-seeking sector (corpus optimal-tax-behavior-07). Badel-Huggett-Luo (2020, EJ 130(629)): about 49% vs 73% revenue-maximising rate in the Diamond-Saez setting; Jones (2022, JPE 130(9)): worker-welfare top rate far below the revenue maximum.

Why this severity. Inside the paper's framework the plausible alternatives lower the bargaining-scenario rate modestly (to 76-80%). Outside it, other models can lower it a lot but rest on their own unverified parameters. The assumptions are disclosed, and the qualitative result (bargaining raises the rate) survives.

The authors' response. PSS call uniform incidence 'a strong assumption' and show the formula carries over to a discrete-occupation model where the tax can undo spillovers (Appendix A.1). They state that in Rothschild-Scheuer the correction 'can be either smaller or larger' than the Pigouvian term (pp. 243-244), and present zero top welfare weight as yielding an upper bound (p. 234, p. 269).

10minorconfirmed · newly identified here · methodology

The program behind the US CEO table has several bookkeeping errors in how it runs its tests. Rough checks using the published numbers suggest these errors do not change the table's conclusions.

Technical detail and evidence

Why it matters, in detail. Mis-ordered demeaning induces an omitted firm-period constant when missingness differs across variables. Unclustered SUEST understates SEs of the OLS differences. The stacked IV is not the union of the two displayed models. None of these is likely to overturn the reported period differences, conditional on the displayed coefficients (which F4 calls into question).

Evidence. BM_tables.do lines 269-282 (demeaning), 289-305 and 311/319 (unclustered regressions feeding suest), 332-345 (clustered re-estimation for display), 437-438 (ceocontrols1 defined twice), 448/461 (stacked xtivreg2), 141-154 and 204-211 (trimming). Back-of-envelope period-difference tests from the displayed clustered coefficients and SEs, treating periods as independent: p = 0.024 (OLS NI), 0.029 (IV NI), 0.003 (OLS MV), 0.028 (IV MV), against published 0.01/0.06/0.00/0.05. Published differences (0.36; 0.72) equal the separately estimated coefficients to rounding.

Why this severity. These are implementation inconsistencies whose likely effect on the reported conclusions is small. Tests built from the displayed coefficients give similar or stronger significance, and the IV columns use xtivreg2 with proper fixed effects. Downgraded from the 'moderate' assigned by Auditor B.

The authors' response. null

11minorconfirmed · newly identified here · data error

The check that ordinary workers are not also 'paid for luck' uses a wage file in which, from 2001 on, most industries' wages were attached to the wrong industry. This weakens one comparison in the table but probably not its main point.

Technical detail and evidence

Why it matters, in detail. Industry FE regressions over 1987-2010 combine correctly matched wages (1987-2000) with mismatched wages (2001-2010). This adds a level break and noise unrelated to own-industry performance, biasing the panel-B slope (-0.02) and the panel-C test toward zero.

Evidence. US CEO analysis/NIPA_all wages_clean.dta (scripts/nipa_wage_check.py): cross-industry correlation of log wages between consecutive years is >= 0.990 in every year except 2000->2001 (0.543); 38 of 71 industries change by more than 0.25 log points in 2001 (maximum 1.04; no more than 2 industries in any other year). Examples: SIC 62 security brokers $162,102 -> $57,466; SIC 70 hotels $26,380 -> $70,216; SIC 36 electronic equipment $60,276 -> $34,041. BM_wages.do merges on sic2 and fyear (line 240).

Why this severity. Panel A (1970-86) is unaffected and also shows no worker pay for luck, so the CEO-worker contrast probably survives. Only the claim that workers' pay for luck did not change across periods is compromised.

The authors' response. null

12minorconfirmed · newly identified here · version instability

Several of the paper's underlying estimates changed between the 2011 draft and the 2014 article, yet the headline numbers stayed exactly the same, and one table still carries a heading from the old draft. That suggests the headline numbers are a chosen illustration rather than a direct product of the estimates.

Technical detail and evidence

Why it matters, in detail. The constancy of (e, e1, e3) = (0.5, 0.2, 0.3) across vintages in which the US endpoint elasticity halved and the growth estimates changed sign and specification shows that the calibration is not mapped from the estimates. A 1975-79 base would have implied e of about 1 and tau* of about 88% at e1 = 0.2.

Evidence. Nov 2011 NBER WP (Wayback copy of elsa.berkeley.edu/~saez/piketty-saez-stantchevaNBER11thirdelasticity.pdf): Table 1A 70% -> 35%, elasticity 1.03/1.12, 'very large around one'; Table 2B FE 0.012 (0.013), 1975-2008; text p. 31 'absolute upper bound b = 0.2'. AEJ Table 1 p. 247 header vs rows. Adjudicator reproduction: 1960-64 base 0.521/0.517; 1975-79 base 1.031/1.124 (scripts/pss_us.py).

Why this severity. This is documentation. The switch to a 1960-64 base is defensible (more countries, conservative for the headline), but the unchanged calibration through changing estimates supports F1's reading that 83% is an illustration.

The authors' response. null

13minorconfirmed · newly identified here · arithmetic or transcription

One number in the US results table was copied wrongly. The fix does not change the conclusion, but it shows the US evidence is less precise than printed.

Technical detail and evidence

Why it matters, in detail. Corrected beta = -0.036 (0.035) implies e1 = beta/pi with a 95% interval of about [-1.05, 0.33] for pi = 0.1, so the US time series also cannot exclude e1 = 0.2-0.33.

Evidence. scripts/pss_us.py (Newey-West, 8 lags, Stata small-sample scaling): all other Table 1B/1C cells reproduce: 0.254 (0.069), 0.262 (0.057), 0.301 (0.057), 0.289 (0.050); 0.265 (0.047), -0.080 (0.040); 0.261 (0.041), -0.077 (0.039), -0.027 (0.034).

Why this severity. The qualitative reading (average income not significantly related to the top rate) is unchanged. The corrected SE widens the US-based e1 interval to [-1.05, 0.33].

The authors' response. null

14minorconfirmed · newly identified here · data error

A few countries' tax-rate and income-share series were assembled in slightly inconsistent ways. These choices barely affect the main link between tax cuts and top incomes, but they noticeably move the growth-based estimate that the 83% rests on.

Technical detail and evidence

Why it matters, in detail. Top-share elasticities are robust to these codings (changes of 0.05 or less), whereas the preferred growth coefficient moves from 0.008 to 0.015-0.021. Interpolation inflates the effective N in the levels panels and is a further reason for clustered inference (F2).

Evidence. AllCountries_update_pre75.dta and .xls; appendix A.2.1-A.2.2; Alvaredo & Saez (2008 long version) App. A.1-A.2 and Table B4. Effects (adjudicator re-runs): Spain statutory -> Fig. 3 0.49-0.51, preferred growth beta 0.016-0.021; Norway XLS -> Fig. 3 0.475, recent FE 0.640, preferred beta 0.015; US 91% -> Table 1A 0.447; earned-income maximum tax -> Table 1B 0.195/0.250 (vs 0.254/0.301).

Why this severity. Each choice is defensible or immaterial for the top-share correlation (Fig. 3 stays at 0.47-0.51; panel FE unchanged). Their main relevance is that single-country coding roughly doubles the e1 point estimate (F1).

The authors' response. null. The appendix invites corrections ('We naturally welcome input on any remaining typos to further improve data quality').

15minorconfirmed · newly identified here · internal inconsistency

A robustness check described as covering 1960-2010 actually stops at 2006, and some of its reported figures are mislabelled. This does not change the results.

Technical detail and evidence

Why it matters, in detail. Excluding 2007-10 removes the post-crisis years from all subsample draws. The percentile reporting of SEs is mislabelled. Neither affects the full-sample columns.

Evidence. international.do bootstrap block ('replace year2 = 1959 + i' for i = 1/47; '-_se[lnmtr]'); regressions.log percentiles match the printed table. Auditor B's re-draws: preferred growth median -0.016 (coded support) vs -0.010 (through 2010); top-share FE median 0.27 vs 0.33.

Why this severity. The exercise is a robustness display. Correcting the support does not change its qualitative message.

The authors' response. null

16minorconfirmed · newly identified here · arithmetic or transcription

There are a number of small typos, mislabelled references and loose approximations. None of them changes the findings.

Technical detail and evidence

Why it matters, in detail. No effect on estimates. The TDC2 description matters only for interpreting Table 3 (see F5).

Evidence. AEJ pp. 241, 250, 252, 254, 257, 260, 264-265, 267; web appendix pp. 52, 58-60, 62; international.do line 'gen span=year_final-year_initial-5'; BM_tables.do lines 179-218; explore_tables.do lines 73-75, 126.

Why this severity. Presentation only. None changes a result.

The authors' response. null

17minorconfirmed · newly identified here · documentation gap

The 83% refers to all taxes combined on an extra dollar earned, not to the income tax alone. The paper never says what income-tax rate that would mean in practice, which would be somewhat lower.

Technical detail and evidence

Why it matters, in detail. Policy readings of '83%' as an income-tax rate overstate the implied statutory rate by several points where payroll and consumption taxes apply at the margin.

Evidence. AEJ p. 252 (excludes payroll and consumption taxes); Table 5; p. 267. Example: with 10% uncapped payroll tax and 20% VAT, a total wedge of 83% corresponds to an income-tax rate of 1 - 0.17 x 1.2/0.9, about 77%.

Why this severity. This is a matter of interpretation and documentation. Country fixed effects absorb constant other taxes in the elasticity estimates.

The authors' response. null

18minorlikely · newly identified here · overclaiming

The paper says some countries respond strongly to tax cuts and others hardly at all, but its own data do not show that particular pattern.

Technical detail and evidence

Why it matters, in detail. Under levels or long-difference specifications the UK elasticity is 0.2-0.3 and Italy's about 0.4, so the claimed contrast between English-speaking countries and others is not visible country by country. Pooled evidence with an English-speaking dummy still gives 0.36 (0.12).

Evidence. Adjudicator output/country_elasticities_adjudicator.csv (levels 1960-2010 / long difference): US 0.49/0.52; UK 0.21/0.32; Japan 0.08/0.05; Sweden 0.30/0.12; Italy 0.37/0.40 (matching Auditor A's figures).

Why this severity. This is a descriptive aside used to motivate institution-dependent elasticities. It does not enter the calibration.

The authors' response. null

Claims examined and rejected

Problems one auditor raised that did not survive checking.

Later evidence agrees with PSS's null: 'Hope & Limberg (2022) and Milasi & Waldmann (2018)' find no significant growth effect of top-rate cuts (counter-argument offered under its I1 and in its checks). — Partly wrong. Hope & Limberg (2022, Socio-Economic Review 20(2): 539-559) do find no significant growth effect of major tax cuts for the rich. Milasi & Waldmann (2018, Applied Economics 50(19): 2156-2170) instead report a significant hump-shaped relation, with a growth-maximising top rate 'in the order of 60%' and negative marginal effects above it (abstract via OpenAlex). That is evidence against, not for, a costless move to 83%.
Because DINA (with retained earnings) gives a long-run elasticity of 0.29 vs 0.52, the paper's own test implies an avoidance component e2 of roughly 0.2. — Rejected as a measurement, kept as qualitative support (F3). In a same-unit comparison (equal-split adults) the gap (0.54 vs 0.29) comes from the change of income concept. Pre-tax national income adds items unrelated to top-end avoidance (non-taxable fringe benefits and pension contributions mostly accruing below the top, imputed rent), so the gap does not identify e2.
Eleven of the 15 Table 2B point estimates imply e1 < 0, which the model rules out; this 'points to confounding rather than a small e1'. — Not established. With country-clustered SEs none of the negative estimates is significantly below zero (|t| <= 1.6), so they are consistent with noise around a small non-negative e1. Confounding remains possible but is not shown by the signs. The valid point, the wide interval, is retained in F1.
Fig. 5's elasticity labels are wrong because the unweighted country-level slope of panel B is 1.09, not 1.90. — A firm-level coefficient (US firms are about half the observations) need not equal an unweighted 13-country slope, so the mismatch is not itself an error. The valid part, that panel B plots a different specification from Table 4 col. 2 under a hard-coded label, is kept in F8.
The international CEO tax vector may be ten years out of date, since the readme describes taxes.dta as 1996 rates. — Auditor B itself rejected this, and the adjudicator agrees: taxes.dta matches 2006 rates (US 35%, Norway 40% after the 2006 reform, Germany 42% x 1.145 = 0.481), not 1996 (US 39.6%, Germany 53%). Only the readme is stale.
Auditor B rated the Table 3 implementation flaws (pre-restriction demeaning, unclustered SUEST, omitted period-1 CEO controls) 'moderate'. — Retained as an issue (F6) but downgraded to minor. Tests built from the displayed clustered coefficients give p = 0.003-0.029 for all four period differences, at least as strong as the published 0.00-0.06, and the published differences equal the separately estimated coefficients to rounding. The flaws do not appear to drive the conclusions.
Corpus critique optimal-tax-behavior-10 (Reynolds 2019): PSS's growth evidence rests on comparisons of changes between distant endpoints (Fig. 4). — Applies only to Figure 4. Table 2B uses full annual panels with country fixed effects, trends and catch-up controls, which reproduce exactly. The real weakness of the growth evidence is its imprecision (F1, F2), not endpoint selection.

Audit notes

What reproduced. Reproduced independently from the AEA replication package (sha256 5570f849..., macro files identical to Saez's Files_nberwp.zip). All 24 Table 2 cols. 1-3 coefficients and SEs, Figures 2-3 elasticities, Figure 4's null, Table 1A and 9 of 10 Table 1B/1C cells, and every Table 5 rate all match. Not reproduced: Table 1C 'average real income, excl. KG' (-0.036 (0.035) vs printed -0.027 (0.018)), and the paper's country-specific elasticity statements. Table 2 cols. 4-6 reproduce in distribution only, because the original uses Stata random draws and a 1960-2006 support. Not reproducible: Tables 3-4 and Figure 5 (proprietary Compustat/ExecuComp/Forbes 800 data and confidential Fernandes et al. data); only code and auxiliary files were audited, and Figure 5's plotted tax rates were recovered from the PDF vector graphics. Additional adjudicator computations: clustered and wild-cluster bootstrap inference, a power calculation, window/specification/pi/single-country-coding sensitivity of e1, the 2011 specification on the published data (e1 = 0.47), DINA same-unit elasticities, and a DINA re-run of Table 1C.

Limits of this audit. No access to the proprietary or confidential CEO microdata, so the numerical impact of F4, F6, F8 and F9 on Tables 3-4 is unknown; the conclusions about them are code-level. International top tax rates were checked against primary sources only for Spain, plus partly Germany, Norway and the US. WTID top-share inputs were not compared with current WID vintages. Moffitt & Wilhelm (2000) on hours of the affluent and some other supporting citations were not re-read. The DINA comparisons change the income concept in several ways at once and are indicative. The wild-cluster bootstrap uses 999 Webb-weight draws (p-value resolution about 0.001). The original Stata random-subsample draws cannot be replicated exactly. CEPR DP 8675 was not obtained (the auditors used the NBER versions). Critique assessments rely on the corpus entries plus spot checks of FFMM (2013), Bakija-Cole-Heim (2012), Hope & Limberg (2022), Milasi & Waldmann (2018) and Rose & Wolfram (2002).