Optimal Labor Income Taxation

Why it matters, in detail. In tau* = (1 + a e3)/(1 + a e) with a = 1.5 and e = 0.5, the split of e into a real part e1 and a bargaining part e3 = e - e1 is identified only through the growth coefficient beta = pi*e1. The preferred estimate (beta = 0.0083) has an HC1 standard error of 0.017 (0.036 clustered), so e1 is not distinguishable from 0 or from about 0.4, and the test's minimum detectable e1 (0.3-0.5) exceeds the 0.2 threshold separating 'above 80%' from lower rates. Treating 'no detectable effect' as e1 of about 0 mechanically assigns the whole total elasticity to e3. Within the interval, the optimum ranges from about 64% to 100% (point estimate 93%). Any upward bias in the total e from confounders inflates e3, and thus the rate, further. This is not a test that can discriminate the bargaining model from the standard model.

Evidence. Adjudicator's independent Python translation of PSS international.do (15 Nov 2012) on AllCountries_update_pre75.dta (scripts/pss_reproduce.py; output/pss_table2_reproduction.csv) reproduces PSS (2014) Table 2 to three decimals, as Auditor A also found. Preferred specification (country FE, trend, trend x initial GDP), 1981-2010: beta = 0.0083, HC1 s.e. 0.0173, country-clustered s.e. 0.0364, N = 540. PSS's conversion e1 = beta/pi with pi = 0.10 (PSS 2014, p. 257) gives e1 = 0.08 with a 95% CI of [-0.26, 0.42] (HC1) or about [-0.6, 0.8] (clustered, 18 clusters). Minimum detectable e1 at 80% power (HC1): 0.48 (1981-2010), 0.38 (1960-80), 0.30 (1960-2010). Implied tau* (a = 1.5, e = 0.5): 93% at e1 = 0.08, 83% at 0.2, 64% at 0.42, 57% at 0.5. Across PSS's five specifications for 1981-2010, beta runs from -0.098 to +0.037; the latter (country FE, no convergence term) has HC1 p = 0.049 (implying e1 of about 0.37 and tau* of 68%) but is insignificant with clustered s.e. (0.055). For 1960-2010 the preferred beta is -0.018 (p = 0.09). Even e1 = 0.2 implies only about 3% higher GDP from the US 1960-2009 cut (dlog(1 - tau) of about 1.5), below what such panels can detect. PSS themselves write that 'the standard error around this estimate is large', that the identifying assumption is 'very strong' and that the estimates are 'not fully robust to the choice of time period' (PSS 2014, pp. 257-258). Better-identified US time-series evidence (Mertens & Montiel Olea 2018, QJE 133(4)) finds that top-rate cuts raise real GDP and incomes below the top 1% and that 'explanations based on avoidance or rent-seeking alone cannot explain' this (their elasticities are short-run). Auditor B reproduced the same regressions with clustered intervals and judged that they 'do not pin down a zero real response or the rent component', but declined to count this as an issue because of the hedged wording.

Why this severity. The >80% figure is the chapter's main quantitative policy suggestion on top rates beyond the standard formula. It rests on an unvalidated parameter whose range in the authors' own data (e1 from about 0 to 0.42 even with optimistic standard errors) maps into optimal rates from about 64% to 100%, a range that includes the '50-60%' view the chapter says may be too low. Eq. (8) itself is correct and the sentence is hedged, so the finding is unestablished rather than refuted, which is why this is major rather than critical.

The authors' response. PSS (2014, pp. 257-258) concede the large standard error, the 'very strong' identifying assumption and sensitivity to the period, and present the result only as 'more consistent with' the bargaining model. The chapter itself adds that 'more compelling empirical identification would be very useful' (p. 434) and that 'little empirical evidence can bear on the issue' (p. 428). No reply to Mertens & Montiel Olea (2018) was located.

Why it matters, in detail. Omitting the 1/pi factor biases the top-bracket weight g toward zero and tau toward the revenue-maximising rate 1/(1 + a e). With pi = 0.5, Pr(low | top) = 0.17, a = 1.5 and e = 0.25, the chapter's method gives 68.9% instead of 63.8%. The p. 464 transition-probability proposal gives 72.6%. In the equal-opportunity limit it gives 57-73% instead of 0. The qualitative limiting result (g = 0 if nobody from a low background reaches the top) is unaffected.

Evidence. Algebra re-derived by the adjudicator (Auditor B's derivation confirmed). If earnings are independent of background (perfect equality of opportunity), the correct weight is 1 everywhere and tau = 0. The printed formula gives g = 0.5 and tau = 57% (a = 1.5, e = .25), and the p. 464 proposal with Pr(top 1% | low) = 0.01 gives 72.5%. With US mobility data, Pr(low | top 1%) = 0.170 (Saez & Stantcheva 2016, AER 106(1), Table 2, col. 1, from Chetty et al. 2014). The chapter's method then gives g = 0.17 and tau = 68.9% at e = .25 (52.5% at e = .5). The normalized weight 0.34 gives 63.8% (46.8%). The p. 464 transition-probability version (Pr(top 1% | low) of about 0.0034) gives 72.6%. Saez & Stantcheva (2016, pp. 39-41) define the weight as the 'representation index' (the low-background share relative to its population share) and report 47% at e = 0.5. In effect, the later paper co-authored by Saez normalizes correctly. The passage is identical in all three versions.

Why this severity. A substantive conceptual error, not a typo, in a secondary normative extension. It can prescribe a large positive top rate where the stated criterion implies none, and it inflates rates by about 5-9 percentage points with realistic mobility data. It does not touch the chapter's core formulas or calibrations.

The authors' response. No direct response. Saez & Stantcheva (2016, AER 106(1), Sec. IV.A and Table 2) use the normalized representation index, implicitly correcting the normalization.

Why it matters, in detail. Suppose about 0.25 of the 0.56 fiscal-income elasticity reflects top-1% income moving out of corporate retained earnings and into the personal base as individual top rates fell. In PSS's notation that is e2, not zero as the chapter infers. Then the comprehensive-income elasticity is about 0.31 (PSZ 2018), or about 0.23 in the 2022 vintage. With a = 1.5, e = 0.5, and e2 = 0.25 shifted to a base taxed at t = 0.35, PSS's formula tau = (1 + t a e2 + a e3)/(1 + a e) gives about 79% for e1 = 0.08 and about 65% for e1 = 0.25. If retained earnings could be taxed at tau, the relevant e would fall and tau would rise. Either way, the realized-gains comparison does not establish that shifting is not a main channel. The post-1960 US time-series evidence is not robust to a linear trend.

Evidence. Adjudicator's computation (scripts/us_concepts_check.py) uses PSZ (2018, QJE) Data sheet columns 102 (top-1% fiscal income, equal-split adults), 67 (pre-tax national income) and 253 (top-1% retained earnings, % of national income), with the US top statutory rate from PSS usdata.dta (83.7% in 1962-64, 35% in 2005-09). Long-run elasticity dlog(share)/dlog(1 - MTR), 1962-64 to 2005-09: fiscal income 9.47% to 20.47%, e = 0.56; pre-tax national income 12.75% to 19.48%, e = 0.31; pre-tax national income minus top-1% retained earnings 8.70% to 18.20%, e = 0.54 (0.51 if retained earnings are also removed from the denominator). The top 1%'s retained earnings fell from 4.05% to 1.28% of national income, which accounts for about 83-91% of the gap between the two elasticities. The 2022 PSZ vintage gives 0.23 (pre-tax, 1960-64 to 2005-09) against 0.53 (fiscal income incl. KG, tax units). US time series, Newey-West(8) (scripts/us_timeseries_check.py): 1913-2008 elasticities of 0.25-0.30 with or without a trend (reproducing PSS 2014 Table 1), but 1960-2008 elasticities of 0.45-0.47 without a trend turn to -0.12 with one, both including and excluding gains. Over 1962-2010 the DINA-based elasticities fall to between -0.10 and +0.03 once a trend is added. PSS (2014, note 26): 'the correlation disappears when additional polynomials in time are added as identification is based solely on time series variation.' Auditor A's figures are reproduced exactly; Auditor B made the conceptual point (realized gains do not make the measure comprehensive) without quantifying it.

Why this severity. The issue removes one link in the argument for high rates: that the long-run elasticity of about 0.5 is not avoidance. On a comprehensive income concept that elasticity is about 45% smaller. Its effect on the optimal rate is ambiguous: higher if the corporate-retention margin can be closed, roughly 65-79% rather than above 80% if it cannot. So it qualifies rather than overturns C3-C4.

The authors' response. The chapter's own note 72 describes the retained-earnings channel, and PSS (2014, note 26) acknowledge the time-series fragility. No direct response located. The interpretation depends on PSZ's allocation of retained earnings by equity ownership, itself an imputation.

Why it matters, in detail. Eq. (7) is exact given the total elasticity of top-bracket taxable income. The policy-relevant elasticity, however, includes long-run career and human-capital responses and assignment re-sorting, and revenue effects on lower brackets and other bases enter the first-order condition directly (tau = (1 - a2 e2 - a3 e3)/(1 + a1 e1) in BHL). Calibrated dynamic models move the revenue-maximising top rate from 73% to about 49% (BHL) or about 62% (SW), while a model with income risk gives about 79% (KK). The uncertainty is two-sided but large relative to the apparent precision of 1/(1 + a e).

Evidence. Badel, Huggett & Luo (2020, EJ 130(629)): revenue-maximising top rate about 49% against the 'established' 73%. Their decomposition (1 - 4.508*0.040 - 0.120*0.739)/(1 + 1.7*0.317) = 47.5% (65.0% without cross-base terms) was recomputed by Auditor B and the adjudicator. Scheuer & Werning (2017, QJE 132(1), Sec. 5.2): with Diamond-Saez parameters, the superstar adjustment raises e to 0.4 and the rate falls to 62%. Jones (2022, JPE 130(9)): worker-welfare-maximising top rate 9% in the benchmark against 91% for revenue maximisation ignoring innovation. Counter-evidence: Kindermann & Krueger (2022, AEJ:Macro 14(2)) find 79% in a life-cycle model with uninsurable earnings risk.

Why this severity. This is a robustness concern whose impact is model-dependent and contested: plausible alternatives move the illustrative 73% to anywhere between about 49% and 79%. The formula is exact for its stated sufficient statistics, and most of the critiques post-date the chapter.

The authors' response. The chapter acknowledges that long-run responses are hard to estimate (note 35) and that elastic education choices imply lower optimal rates (Sec. 6.6). No direct reply to Badel-Huggett-Luo, Scheuer-Werning or Jones located.

Why it matters, in detail. The long-difference cross-country elasticity (0.47, s.e. 0.11) reproduces. Only the verbal reading is wrong, and it hides two counterexamples: France and the Netherlands cut top rates by 17-19 points and saw falling top shares.

Evidence. Independent reproduction (scripts/pss_reproduce.py; output/fig5a_country_changes.csv). France cut its top rate by 17.2 points (comparable to the Netherlands' 18.5 and Australia's 18.6), with a top-1% share change of -0.93 points. Finland's top rate changed by -8.1 points and its top share by -1.82 points. The Netherlands' rate fell by 18.5 points and its share fell 2.81 points, a decrease. Portugal's rate fell 39.0 points and its share rose 3.65 points, as much as Canada's (+3.66). Six English-speaking countries are plotted, and New Zealand's +1.45 is below Italy's 'modest' +2.53. Elasticity 0.470 (s.e. 0.114), N = 18; leave-one-out range 0.42-0.54. The paragraph is nearly verbatim from PSS NBER WP 17616 rev0 (Nov 2011, pp. 28-29), which described a 1975-79 to 2004-08 comparison. PSS's March 2013 WP and the 2014 AEJ article corrected it ('Germany, Spain, Denmark or Switzerland'; 'Norway and Portugal'; modest 'Japan'; '0.47'). The text is the same in all three Handbook versions.

Why this severity. This is a description error. The regression and figure are correct and robust to dropping any country, but three of the four misclassifications (France, Finland, Netherlands) make the cut/increase pattern look cleaner than it is.

The authors' response. PSS (2014) corrected the corresponding prose in their own paper; the Handbook text was not corrected.

Why it matters, in detail. The sign flip reverses the direction of the income-effect adjustment: e = ē^u - η̄(a - 1)/a is at least ē^u, not at most. Plugging uncompensated elasticities and income effects into the footnote understates e and overstates tau by about 6-8 points for plausible parameters.

Evidence. Saez (2001, REStud 68(1), eq. 8): tau/(1 - tau) = (1 - ḡ)(zm/z̄ - 1)/(ζ̄^u zm/z̄ - η̄). With a = zm/(zm - z̄), this implies a e = a ζ̄^u - η̄(a - 1). Numerical checks: Auditor A (reform elasticity 0.193 against the footnote's -0.249) and Auditor B (log-utility example +0.25 against -0.25). The error is present in all three versions. Example: ē^u = 0.2, η̄ = -0.1, a = 1.5 gives a correct e = 0.233 and tau = 74%, against 0.167 and 80% from the footnote. Auditor B's example (ē^u = .3, η̄ = -.1, a = 2): 58.8% against 66.7%.

Why this severity. No calculation in the chapter uses the decomposition, and the text's qualitative statement (for a given compensated elasticity, income effects raise tau) is correct. A reader who used the footnote to convert Marshallian estimates would overstate the top rate by about 6-8 points.

Why it matters, in detail. Eq. (10) requires T(z)/(z - T(z)) = tau/(1 - tau) on (z - z*)-weighted average. With realistic schedules the weighted average wedge is below tau/(1 - tau), so the true optimum exceeds 1/(1 + a e + eta_m): about +3 to +7 points at a = 2, e = .25, eta_m = .5, and about +2 to +3 points at a = 1.5, e = .25, eta_m = .25. The gap is large only when migration is the sole margin.

Evidence. Adjudicator's computation (scripts/migration_check.py) uses the exact first-order condition with both margins, (1 - tau)[1 - eta_m W] = tau e a, where W is the (z - z*)-weighted mean of T/(z - T) over a Pareto tail. In the chapter's example (a = 2, e = .25, eta_m = .5), Eq. (10) gives 50% against an exact 53.4% (30% average tax at the threshold) or 56.8% (no tax at the threshold). In a US-like case (a = 1.5, e = .25, eta_m = .25), it gives 61.5% against 63.4-64.9%. Auditor B's counterexample has no intensive response and a tax-free threshold: Eq. (10) gives 66.7% against 90.9% by direct maximisation (reproduced), and 79.8-82.5% with a 30% threshold tax. Auditor A found the same restriction ('exact when the bracket's average rate equals tau; otherwise conservative'). The same expression appears in Brewer, Saez & Shephard (2010, online appendix).

Why this severity. The approximation errs toward overstating migration's effect, understating the optimal rate by about 2-7 points in the chapter's own parameterisations. So the chapter's conclusion that migration does not drastically change top rates is reinforced, not undermined. Auditor B's 24-point gap requires zero intensive elasticity and zero tax at the threshold.

Why it matters, in detail. For a US top rate that applies to ordinary income, the relevant tail index is about 1.6 (1.76 for wages) rather than 1.45, which lowers 1/(1 + a e) at e = .25 from 73% to 69-72%. Attributing the post-1970 thickening of the tail entirely to tax cuts would imply an even larger elasticity at the very top, not a fixed e = 0.25 with a variable a. That scenario is not established.

Evidence. Fig. 4 reproduced from IRS SOI 2005 Table 1.4: a = 1.49 ($200k), 1.43 ($500k), 1.42 ($1M), 1.43-1.45 ($1.5-2M). Caption thresholds match Piketty-Saez TabFig2010 nominal thresholds ($99,234; $350,501). Piketty-Saez (TabFig2010) a at P99 in 2005: 1.45 including gains, 1.59 excluding gains, 1.76 for wages (Table B3). The wage figure was 3.06 (1960), 3.10 (1970), 2.54 (1980), 1.99 (1990), 1.68 (2000) and 1.76 (2005). 1/(1 + 0.25a) is 73.4% with gains included, 71.6% for ordinary income and 69.4% for wages; the PSS 83% becomes 81% with the wage a.

Why this severity. The choice of income concept moves the revenue-maximising rate by about 1-4 points. The endogeneity concern is speculative: in the chapter's constant-elasticity model the tail index is invariant to tau, and Appendix A.1 describes calibrating the skill distribution and iterating to a fixed point.

The authors' response. Note 55 discloses that the figure uses total pre-tax family income including realized capital gains.

Why it matters, in detail. The cross-country CEO result is a level correlation conditional on performance, not a luck-sensitivity result. It is weaker evidence of tax-induced bargaining than the note implies.

Evidence. PSS (2013 WP; 2014 AEJ, abstract and Sec. III) show pay-for-luck only in US data for 1970-2010. Their international evidence (2006 CEO data from Fernandes et al. 2013) concerns pay levels: CEO pay is negatively correlated with top rates after controlling for firm performance, more so in poorly governed firms. It does not concern sensitivity to luck. The cited November 2011 WP contains no CEO regressions of its own (literature review only, pp. 31-32). The sentence is identical in all three versions.

Why this severity. This misdescribes supporting evidence for the bargaining interpretation, but the underlying US result exists. It overstates the breadth of the micro evidence without changing any number.

Why it matters, in detail. The Pigouvian term in Eq. (8) is valid only when the government can undo the externality with the demogrant. Otherwise the correction depends on who bears the rents. In Rothschild-Scheuer's calibration, a 25% Pigouvian wedge implies top-rate corrections between 15.9% and 31% depending on incidence.

Evidence. The PSS November 2011 WP (pp. 22-23, 'Non uniform external effects') shows nothing formal. It notes that if the externality falls on lower earners the optimal rate would be higher, that if it falls on upper earners it would be lower, and (note 20) that the government can then no longer undo it. PSS (2014, pp. 243-244) call the uniform case 'a strong assumption' and acknowledge that in Rothschild & Scheuer the correction 'can be either smaller or larger than the pure Pigouvian correction'. The chapter's own note 59 reports that in Rothschild-Scheuer high top rates are not optimal when rent-seekers take from other rent-seekers.

Why this severity. The text of the chapter elsewhere (note 59) discloses the qualification, so the misstatement is local; it does, however, understate the informational requirements of the >80% case.

The authors' response. PSS (2014, pp. 243-244) partially accept Rothschild & Scheuer's point.

Why it matters, in detail. A well-known TRA86 study finds a large real (participation-driven) response among high-income households. This weakens the categorical claim used to motivate small real elasticities at the top, although secondary earnings are a small share of top-1% income.

Evidence. Eissa (1995, NBER WP 5023) uses the 1986 Tax Reform Act as a natural experiment. It finds a labour-supply elasticity of about 0.8 for married women at or above the 99th percentile, at least half of it through participation (a second control group supports the participation response but is inconclusive on hours). The chapter cites Moffitt & Wilhelm (2000) on hours of top earners under the same reform (note 65) but not Eissa. The survey cited, Saez, Slemrod & Giertz (2012, p. 42), makes the weaker claim that there is no compelling evidence of real responses at the top.

Why this severity. The general reading of the taxable-income literature (most large short-run responses are avoidance or retiming) still largely holds, and secondary-earner elasticities are acknowledged in Sec. 6.4. The blanket 'none' is nonetheless false and supports the low-e1 premise behind C3.

Why it matters, in detail. Category-level entries differ from the cited source by up to 1.4 points of GDP, plausibly because of vintages or reclassification, but the construction is undocumented. The broad message (social spending is about 22-34% of GDP and dominated by education, health and pensions) is unaffected.

Evidence. Auditor B averaged the cited annual tables (Adema et al. 2011, Tables A.I.1.4a-d). Chapter value against source mean: US health 7.7 vs 7.16; France health 7.1 vs 7.50 (so the US/France ranking reverses); Germany pensions 10.1 vs 11.11; UK pensions 4.8 vs 5.42 (below every annual value, 5.3-5.6); Germany other social 4.4 vs 3.15; UK other social 5.7 vs 4.27. The entries also match no single column of Adema Table I.2, which the adjudicator checked: for example, UK pensions are 5.4/5.4/5.5 there. Component sums are internally consistent within 0.1 point. Totals excluding education are broadly in line with current SOCX (Auditor A).

Why this severity. This is a background table that plays no role in the formulas or calibrations, and note 12 warns that categories are not homogeneous across countries. It is a provenance gap, not evidence of fabricated numbers.

The authors' response. Note 12 says only 'broad orders of magnitude' are intended.

Why it matters, in detail. The figure mixes the earned-income schedule with the investment-income surcharge. The labour-income top rate was 83% (1974-78) and 60% (1979-88).

Evidence. Finance Act 1974, Part II, income-tax charge for 1974-75 (legislation.gov.uk copy in cache): higher rates up to 83% ('The remainder 83 per cent') on total income, plus an 'additional rate of 15 per cent' on investment income above GBP 2,000 only, so 98% applied only to investment income. The PSS data used for Fig. 5A code UK inctax as 0.83 (1974-78) and 0.60 (1979-87). Verified in AllCountries_update_pre75.dta.

Why this severity. Background figure. For a chapter on labour income it overstates the UK top rate on earnings by 15 points in 1974-83, and it is inconsistent with the authors' own regression data, but no result depends on it.

Why it matters, in detail. Several large advanced economies lie below the stated ranges. Since Panel B's tau = 35% is meant as a rate on the actual (narrower) base, the illustration is unaffected.

Evidence. OECD Revenue Statistics (current vintage, SDMX extract in cache), 2010 tax/GDP: 14 of the 38 current members were below 30%, including the US (23.4%), Japan (26.2%), Switzerland (25.8%) and Australia (25.1%); 10 of the 34 members as of 2012 were below 30%. The US ratio of tax to national income is roughly 27-31%.

Why this severity. This is an imprecise background statement. Note 39 explains that effective rates on actual tax bases exceed ratios of tax to national income, so the 35% used for the US in Table 2 Panel B remains defensible.

The authors' response. Note 39 notes that tax bases are narrower than national income.

Why it matters, in detail. Eq. (8), Eqs. (13)-(16) and Appendix A.2's Eq. (19) all reproduce once the local notation is corrected.

Evidence. Verified on rendered pages or extracted text of the published PDF. p. 427: '(y/z)e_b = (1 - s)e' should read (y/z)e_y. p. 438, Eq. (12): the sum uses T_n instead of T_m, so the printed behavioural term is identically zero because shares sum to one. p. 440, Fig. 7 graphic: dc1 is written for dc0, and the behavioural fiscal cost lacks its minus sign. p. 467: 'u_l(c, l = 0) > 0' should be < 0, and 'u(-c0, 0)' should be u(c0, 0). p. 468: the utility c - l^(1+e)/(1+e) is paired with labour [n(1 - T')]^e; the exponent should be 1 + 1/e. p. 432: 'Panel A also displays' should be Panel B. p. 424: '$400,000, approximately the top 1% threshold' is inconsistent with the caption's P99 of $350,500. Text window 2004-2009 vs caption 2005-2009. p. 451: Kleven, Kreiner and Saez '2009b' should be 2009a. p. 431: the citation years of the Kleven et al. papers are swapped. p. 464: the garbled 'those deem Roemer et al. (2003)'. Cross-references on pp. 405 and 414 to 'Section 6' for the limits of utilitarianism and welfare weights should point to Section 7. Table of contents page numbers are off by 1-2 pages from Sec. 4.2 onward (e.g., Sec. 6 is listed at p. 447 but starts at p. 445). Author-name errors in references ('Crépon, Esther, Marc, Roland and Philippe'; 'Stancheva').

Why this severity. None affects a conclusion; the neighbouring text or final formulas are correct in each case.

Why it matters, in detail. Including zero earners at c = R widens the dispersion of 1/c weights and lowers gbar. With intra-household pooling, gbar would rise and tau fall toward the earners-only bound (52% at e = .25). The printed utilitarian rates are therefore an upper end of the defensible range.

Evidence. Adjudicator's reconstruction (scripts/table2_check.py) from Census CPS ASEC 2011 PINC-05 (2010 earnings, ages 25-44 and 45-64; uniform within bins, Pareto top bin matched to the published mean). Including the 23.0% zero earners gives tau = 60.1/48.4/36.4% and gbar = 62.4/53.2/42.7%; earners only gives tau = 52.5/40.2/28.8%. Median/mean is 0.725 including zeros (0.765 earners only), against the '70%' used. Auditors A and B obtained the same results within 1 point using different grouped tables. The closed-form rows reproduce exactly.

Why this severity. The table is explicitly illustrative and its population definition is disclosed. Household sharing would lower the utilitarian rate by an unknown amount, bounded by roughly 9 points (the earners-only case). This is a modelling simplification, not an error.

The authors' response. Table 2 is described as 'simple illustrative calculations'.

Why it matters, in detail. Local (generalized-weight) optimality need not correspond to any coherent global ranking unless the weights are structurally utilitarian. Allocation-dependent weights can create multiple or self-fulfilling optima.

Evidence. Sher (2024, AER 114(11)) proves that generalized weights give consistent comparisons only if they are 'structurally utilitarian'. Weights that depend on taxes paid, as suggested on p. 463 ('weights depend positively on net taxes paid'), can generate intransitive rankings of tax reforms. Fleurbaey & Maniquet (2018, JEL 56(3), Sec. 10) show multiple equilibria, including a self-fulfilling 100% tax, in the Saez-Stantcheva luck/desert application.

Why this severity. This is programmatic language in the limitations section, not a quantitative result, and the main critiques post-date the chapter.

Why it matters, in detail. If extensive-margin elasticities at the bottom are small, Eq. (16) gives bottom rates near (1 - g1)/(1 - g1 + e1) with small e1, which pushes toward the intensive-margin prescription of Eq. (14) (high phase-outs) rather than in-work subsidies.

Evidence. Kleven (NBER WP 26405, 2019; revised 2024) re-examines every state and federal EITC reform. Apart from the 1993 federal reform, he finds EITC expansions 'are not associated with any clear and robust effects on employment', and the 1993 effects 'align more closely with confounding effects from welfare reform and the macroeconomy'. This reappraisal is itself debated; the chapter reflected the consensus of its time.

Why this severity. The transfer formulas are conditional on the elasticities and remain correct. Only the empirical support for the extensive-margin case is weaker than presented, and that support post-dates the chapter.