Emmanuel Saez · In H. Boushey, J. B. DeLong and M. Steinbaum (eds.), After Piketty: The Agenda for Economics and Inequality, Cambridge MA: Harvard University Press, ch. 13, pp. 304-321

The Research Agenda after Capital in the Twenty-First Century

17 problems found: 1 major · 4 moderate · 12 minor

What the paper claims

Research agenda (the chapter's main contribution): build Distributional National Accounts (DINA) consistent with national income; improve US wealth and saving data through administrative sources (year-end balances on information returns, IRA/401(k) balances, asset-purchase reporting); measure inherited vs self-made wealth; link business and individual tax data to learn the industrial composition of top business income; evaluate taxation and regulation as remedies.
Preliminary DINA estimates (PSZ 2016) show growth became far less equally shared after 1980.
Post-tax inequality is lower than pre-tax inequality, but 'the time trends in inequality pretax and post-tax are very similar': growing transfers and declining tax progressivity 'roughly cancel each other out'.
US wealth data are weak and contradictory: estate data show low, stable concentration; the SCF shows high and rising concentration; Saez-Zucman capitalization shows a very large rise, stronger than the SCF since 1989, raising 'the real possibility that U.S. wealth inequality is actually exploding'; better administrative wealth data are urgently needed.
Mechanisms and fairness: the US inherited-wealth share is poorly measured; saving rates rise with wealth and middle-class saving has plummeted (SZ synthetic saving rates), so saving inequality magnifies wealth inequality; executives, managers, supervisors and financial professionals account for about two-thirds of the rise in top-0.1% income; the surge in top business income is even larger than in wages, and whether it reflects value creation or rents (e.g., tech quasi-monopolies) is a key open question.
Policy shapes inequality: inequality rose most where policy reversed (US, UK), which 'strongly suggests that policy plays a key role'; top-1% shares correlate with top tax rates 'with no visible effects on growth', suggesting rent extraction (PSS 2014); tight financial regulation in 1933-80 coincided with stronger growth; a progressive wealth tax is the most direct instrument; estate-tax unpopularity is largely due to misinformation.

Every problem found

1majorplausible · previously known · external inconsistency

The chapter says that since 1980 the bottom 90% of Americans got only about a third of the growth in average income. That figure is computed correctly from the authors' data, but other credible ways of counting put it between about 36% and 50%. Every method agrees the bottom 90% fell behind after 1980; how far behind is less certain than the chapter suggests.

Technical detail and evidence

Why it matters, in detail. The statistic is 0.9 x change in bottom-90% mean / change in overall mean income per adult; with the bottom-90% pre-tax share falling from 65.8% to 53.0% (PSZ Dec 2016) it equals 32.0%. It is sensitive to (i) the unit: 44.1% of aggregate growth; 40-46% for persons in households ranked by size-adjusted income (CBO); (ii) allocations of income missing from returns (underreported business income, retirement income), where Auten-Splinter obtain a top-10% rise of 7.3 pp instead of 12.8 pp and a capture of about 50%; (iii) vintage (36.2% in WID 2026). Against a stable 1946-80 benchmark of about 69%, the drop in the bottom-90% share of growth ranges from about 37 pp (PSZ 2016) to about 19-33 pp in other series. The PSZ-Auten-Splinter dispute is unresolved (Gale, Sabelhaus & Thorpe 2023 side with PSZ on underreporting, with Auten-Splinter on retirement income).

Evidence. Adjudicator, PSZ Dec-2016 appendix TB3 (the vintage behind the printed numbers): 1980-2014 all adults 1.41%/yr, bottom 90% 0.77%/yr (ratio 0.54), bottom-90% capture 32.0% of per-adult growth, but 44.1% of aggregate real income growth (adults x1.51, PSZ TA0). Authors' current series (WID 2026, aptincj992): 0.89% vs 1.47%/yr (ratio 0.61), capture 36.2%. Auten-Splinter (2024) workbook, pre-tax national income of individuals: 1.35% vs 1.70%/yr (ratio 0.80), capture 50.5% (51.2% with PCE deflator); their top-10% share rises 32.8% to 40.1% vs PSZ 34.2% to 47.0%. CBO 2019 household data per person (Auditor A's computation, market-income case re-checked by hand): market income 40%, income before transfers and taxes 46%. The 1946-80 benchmark is about 69% in every PSZ/WID vintage. Print PT217.

Why this severity. If the alternative units and allocations are closer to the truth, the headline magnitude moves by a quarter to a half (32% to 40-50%; growth ratio 0.54 to 0.65-0.80), which meets the rubric's threshold for this core empirical claim; the direction survives in every series and the authors' own like-for-like revision is smaller (32% to 36%). It does not touch the agenda (C1).

The authors' response. PSZ defend their allocations (Piketty, Saez & Zucman 2024 comment on Auten-Splinter) while revising several of them (PSZ update log: retirement income, interest); the chapter labels the estimates 'preliminary'.

2moderateconfirmed · newly identified here · internal inconsistency

The chapter says government taxes and transfers did essentially nothing to slow the rise in inequality since 1980, because bigger transfers and less progressive taxes cancelled out. The authors' own detailed numbers, released at the same time, show that taxes and transfers did offset about a quarter to a third of the rise. Inequality after taxes still rose a lot, so the broad picture holds, but this specific claim goes too far.

Technical detail and evidence

Why it matters, in detail. The post/pre ratio of share changes is 0.74 for the top 10% and top 1% (PSZ Dec 2016), 0.79-0.80 in WID 2026 and about 0.72 in CBO; growth in transfers (mainly Medicare and Medicaid) outweighed the mild decline in PSZ-measured progressivity (top-1% average tax rate 38.5% to 36.4%, Auditor A). Under alternative conventions the offset is larger: Auten-Splinter's allocation of government consumption and deficits, and CBO-based measures in which federal progressivity rose (Splinter 2020). So 'roughly cancel' is the extreme-end reading under every convention; 'very similar' holds only in proportional terms (top 10% +37% pre-tax vs +32% post-tax).

Evidence. Adjudicator, PSZ Dec-2016 TB1/TC1, 1980 to 2014: top 10% pre-tax 34.2% to 47.0% (+12.8 pp) vs post-tax 29.5% to 39.0% (+9.5 pp); top 1% +9.5 vs +7.1 pp; top 0.1% +5.8 vs +4.1 pp; bottom 50% -7.4 vs -6.3 pp. Bottom-90% income grew 0.77%/yr pre-tax but 0.98%/yr post-tax and captured 32% of pre-tax but 45% of post-tax per-adult growth (TC3). PSZ NBER WP 22945 (Dec 2016) p. 19: 'it has risen less than pre-tax inequality. Between 1980 and 2014, the top 10% income share rose by about 10 points post-tax and 13 points pre-tax'; note 58: redistribution 'has only offset about one third of the growth gap between the bottom 90% and the average'. WID 2026: top 10% +11.7 vs +9.3 pp. CBO (Auditor A): top 10% +10.0 vs +7.2 pp. Print PT217 confirmed: 'In net, these two factors roughly cancel each other out.'

Why this severity. The broad message (post-tax inequality also rose sharply; redistribution offset only part of it) survives, but the specific claim that the two policy forces net out is not supported: in the authors' own data they offset about a quarter of the rise in top shares and a third of the bottom-90% growth gap.

The authors' response. The co-authored PSZ papers (2016 WP; 2018 QJE) describe the offset as 'only a small fraction'; no response specific to the chapter.

3moderateconfirmed · previously known · overclaiming

The chapter notes that countries that cut top tax rates the most did not grow faster, and concludes that the rich responded to tax cuts by grabbing a bigger slice of the pie rather than by working harder. With only 18 countries the data cannot tell a zero effect on growth apart from a sizeable positive or negative one, and the rich may simply have reported their income differently. The pattern is real; the explanation is not established by it.

Technical detail and evidence

Why it matters, in detail. Under PSS's mapping beta = pi x e1 (pi about 0.1), the clustered interval corresponds to e1 between about -0.7 and 0.85. The data are thus consistent both with no real supply response and with one large enough to deliver the supply-side case. Separating e3 (bargaining) from e2 (avoidance and income shifting, e.g., C-to-S conversions after TRA86) needs micro evidence. Eighteen country observations with country-specific confounders (post-war catch-up in Germany and Japan; Reynolds 2019) give little power. The bias runs toward overstating the evidence for the zero-sum interpretation.

Evidence. Adjudicator re-run of PSS Figure 4A (international.do translated to Python; AllCountries_update_pre75.dta): N=18 countries, 1960-64 to 2006-10; slope of annual GDP-per-capita growth on the change in the top marginal rate 0.0008 per pp (HC1 s.e. 0.0094), R2 = 0.000; a 40-pp cut (US -47.3 pp, UK -46.8 pp) implies -0.03 pp/yr with 95% CI [-0.77, +0.70] pp/yr, against mean growth of 2.44%/yr (sd 0.62). Auditor B: preferred 1981-2010 panel coefficient 0.0083, robust s.e. 0.0173, country-clustered s.e. 0.0364. This project's PSS adjudication: e1 interval about [-0.7, 0.85], power about 25% against the pure supply-side case. The top-share/top-rate elasticity itself reproduces (0.47, s.e. 0.11; both auditors). Contrary evidence: Mertens & Montiel Olea (2018, QJE); Kaplan & Rauh (2013, JEP). Print PT223-PT224.

Why this severity. The descriptive facts behind C6 hold; what fails is the mechanism drawn from them. This weakens one of the chapter's two main arguments for policy remedies (rate cuts raised top shares without growth gains because of rent extraction) but not its broader claim that policy matters.

The authors' response. PSS (2014, pp. 255-257) themselves acknowledge reverse causality, period sensitivity and imprecision; the chapter says 'suggests'.

4moderateconfirmed · newly identified here · overclaiming

The chapter says the US grew faster when finance was tightly regulated (1933-1980), so regulating finance does not hurt growth. But 1933 was the bottom of the Great Depression, which makes the regulated era look much better; measured from 1946 it grew about as fast as 1980-2007. Many other things also changed between the two periods, so the comparison cannot show that regulation was harmless.

Technical detail and evidence

Why it matters, in detail. Starting at the 1933 trough adds about 1.2 pp/yr of recovery growth to the regulated period (3.28% vs 2.12% from 1946). Post-war catch-up, demographics and the post-1973 productivity slowdown confound any regulatory effect: growth was 1.45%/yr in 1973-80, while regulation was still tight. A single time series with two regimes provides no counterfactual.

Evidence. Adjudicator, BEA NIPA series A939RX (real GDP per capita): 1933-80 3.28%/yr; 1929-80 2.34%; 1946-80 2.12%; 1950-80 2.28%; 1973-80 1.45%; versus 1980-2007 2.08% and 1980-2014 1.73%. The regulated era's advantage is +1.55 pp/yr with the 1933 start vs 1980-2014, +0.39 pp with a 1946 start, and +0.04 pp against 1980-2007 (matches Auditor A). Print wording confirmed by Auditor A's full-text hit ('1933 to 1980 is actually associated with stronger economic growth'); draft p. 16.

Why this severity. The descriptive association survives only weakly with a non-trough start (2.1% vs 1.7% a year against 1980-2014; none against 1980-2007), and the causal 'shows' is unsupported; this undercuts a supporting argument for regulation as a remedy, not the agenda.

5moderatelikely · previously known · external inconsistency

The chapter cited new estimates showing the richest 1% going from 23% to 42% of US wealth between 1978 and 2012, and raised the possibility that wealth inequality was 'exploding'. That method assumed the rich earn the same interest rate on their savings as everyone else; when the authors later allowed for higher returns at the top, the 2012 figure fell to about 37%, and other researchers find lower numbers still. Wealth concentration still rose substantially, but by less than the chapter reported.

Technical detail and evidence

Why it matters, in detail. Capitalization sets wealth = capital income / class yield with one yield per asset class. At the low fixed-income yields of 2008-13, capitalization factors approach about 100 per dollar of interest (BHKS 2016), so top shares hinge on that yield. A 1.4x top interest premium plus refined allocations lowers the 2012 top-1% share from 41.8% to 36.6% and the post-1989 rise from 14.0 to 7.8 pp (SCF +5.6 pp). Return-heterogeneous estimates (SZZ 2023) are lower again. The rise since 1978 remains +13 to +15 pp. The SZ synthetic saving rates in C5 are computed from the same capitalized series and inherit the revision.

Evidence. SZ (2016) Table B1: 22.94% (1978), 27.81% (1989), 41.82% (2012) (adjudicator). SZ's own alternative interest capitalization (Table B41b/c, 2012): top 1% 39.97% (-1.85 pp), top 0.1% 18.70% (-3.31 pp). Authors' current series (WID 2026, shwealj992): 21.8% (1978), 28.8% (1989), 36.6% (2012): the 1978-2012 rise is 14.8 pp rather than 18.9 pp (-22%), the 2012 level is 5.2 pp lower, and the 1989-2012 rise (7.8 pp) barely exceeds the SCF's (+5.6 to +5.7 pp) instead of 14.0 pp. PSZ update log section 2.1.1 now capitalizes top-1% interest at 1.15x (2003-07) and 1.4x (from 2008) the average rate. Heterogeneous-return estimates: Bricker, Henriques & Hansen (2018), 2011 top 1% 40.5% to 33.9%; Smith, Zidar & Zwick (2023), 2016 top 1% 33.7% vs 38.9% with equal returns; Fed DFA about 31% in 2014 (Batty et al. 2019). Print PT218-PT219.

Why this severity. Rising concentration since the late 1970s survives in every series, and the chapter's recommendation (better administrative wealth data 'to settle the debate') is strengthened by the later disagreement; but the magnitude behind 'exploding' has been cut by about a fifth by the authors and by more in heterogeneous-return estimates, and the 'stronger than the SCF' comparison largely disappears.

The authors' response. Saez and Zucman added a top interest-rate premium in later series (PSZ update log section 2.1.1; Saez & Zucman 2020) and argue that Smith-Zidar-Zwick understate top wealth and its post-2001 rise (corpus us-wealth-taxes-06).

6minorconfirmed · newly identified here · arithmetic or transcription

Two numbers about 1946-1980 are slightly wrong in the published chapter: the bottom 90% actually grew a bit faster than average and got about 69% of the growth, not 62%. The mistake makes the later decline look smaller than it was, so it does not help the author's argument.

Technical detail and evidence

Why it matters, in detail. The correct per-adult contrast is 69% to 32% rather than 62% to 32%. The all-adult 1946-80 growth rate is overstated by 0.1 pp/yr, and 'the same' hides a 7% faster bottom-90% growth rate (2.12% vs 1.98%).

Evidence. Adjudicator, PSZ Dec-2016 TB3: all adults 1.98%/yr, bottom 90% 2.12%/yr, capture 68.9% per adult (67.1% of aggregate growth; 68.2% on factor income); WID 2026: 69.5%; Auditor A: 68.9-69.6% in all PSZ vintages. PSZ WP Table 2: 1946-80 full population +95%, bottom 50% +102%, middle 40% +105%. Print PT217: 'were the same, at 2.1 percent per year ... captured 62 percent of overall economic growth from 1946 to 1980'. Draft p. 5: 2.0% and 62% (and 27% for 1980-2012, where the data give 30.3%).

Why this severity. The error understates the pre-1980 benchmark and therefore understates, rather than inflates, the post-1980 deterioration; no conclusion depends on it.

7minorconfirmed · newly identified here · misrepresentation of source

The chapter slightly understates what its own cited source says the richest 1% owned according to estate-tax records: about 21-22%, not just under 20%. The point that this source shows much less concentration than the others still holds.

Technical detail and evidence

Why it matters, in detail. Estate-multiplier top-1% shares were 20.8-22.7% through 2000. The gap with capitalization is therefore about 1-2 pp smaller than stated, and the estate series is 'stable' at roughly 21-22% rather than below 20%.

Evidence. Kopczuk & Saez (2004) Table 3, column 2 (adjudicator check of the text): 19.06 (1982), 21.07 (1983), 22.35 (1985), 22.66 (1986), 21.96 (1989), 21.18 (1992), 21.54 (1995), 21.24 (1997), 21.70 (1998), 21.68 (1999), 20.79 (2000); p. 453 describes shares 'around 21-22 percent'. SZ (2016) extension for 2001-08: 19.4-23.5% (Auditor A). Print PT218.

Why this severity. It understates the estate-based level by about 1-2.7 pp; the contrast with the SCF (36%) and SZ (42%) is unaffected.

8minorconfirmed · newly identified here · external inconsistency

To illustrate who earns big business profits at the top, the chapter says start-ups like Uber and Facebook are a kind of company (LLC) whose profits show up on owners' personal tax returns. They were not: both were ordinary corporations. The research question the chapter raises is still a good one, but its examples were wrong.

Technical detail and evidence

Why it matters, in detail. C-corporation profits reach individuals as dividends and capital gains, not as pass-through business income. The tech quasi-monopoly framing therefore does not describe the income category whose growth the chapter is interpreting. When the recommended linked-data research was done (SYZZ 2019), it pointed to professional and mid-market private firms.

Evidence. Facebook S-1 (1 Feb 2012), Corporate Information: 'We were incorporated in Delaware in July 2004.' Uber S-1 (2019): 'incorporated as Ubercab, Inc., a Delaware corporation, in July 2010. In February 2011, we changed our name to Uber Technologies, Inc.' Polsky (2019, Hastings L.J. 70:409): start-up lawyers 'prefer C corporations'; LLCs are used in 'relatively rare cases'. Smith, Yagan, Zidar & Zwick (2019, QJE) find top pass-through profit accrues mainly to owners of closely held mid-market firms in skill-intensive industries. Print PT222.

Why this severity. No number or recommendation depends on it. It misdirects the illustrative interpretation of top pass-through income toward tech start-ups, while the recommended research (linking business and individual tax data) is unaffected.

9minorconfirmed · newly identified here · external inconsistency

The chapter says only one US survey records both what people earn and what they spend. A second major survey does too, and the study the chapter praises used it. This does not change the point that no survey captures the very rich well.

Technical detail and evidence

Why it matters, in detail. PSID offers panel income, wealth and near-complete CE-category expenditure, permitting saving measured both as income minus consumption and as the change in wealth. Neither PSID nor CEX covers the extreme top, which is the chapter's real constraint.

Evidence. Andreski, Li, Samancioglu & Schoeni (2014, AER P&P 104(5): 132-135): 'The Panel Study of Income Dynamics (PSID) expanded its expenditure data collection in 1999 and 2005'. Dynan-Skinner-Zeldes NBER w7906 abstract: 'using ... the Panel Study on Income Dynamics, the Survey of Consumer Finances, and the Consumer Expenditure Survey'. Print PT221.

Why this severity. A factual misstatement about data availability; the underlying point (no US survey measures saving at the top well) and the call for administrative data are unaffected.

10minorconfirmed · newly identified here · selective presentation

The chapter says that telling people only the very rich pay the estate tax doubles support for it. In the study cited, plain facts raised support by about half; the doubling happened only when the facts came with a persuasive picture and argument. And the question was about raising the tax, not about having it at all.

Technical detail and evidence

Why it matters, in detail. Information alone moves support for an increase from 21% to 32%. The extra 18 pp under the 'emotional' slide reflects framing and advocacy, so the evidence speaks to persuadability rather than to misinformation as the main cause of the tax's unpopularity. It also measures demand for an increase, not for keeping the tax.

Evidence. KNSS (2015, AER 105(4)) Table 7, column 4 (N=1,777): control mean 0.210; 'emotional' estate-tax slide +0.289 (+138%); 'neutral' factual version +0.109 (+52%); test of equality p=0.000. KNSS p. 1491: 'a purely clinical information treatment with no emotional component increases support by 50 percent instead of more than doubling it'; p. 1490: the omnibus treatment 'triples the share of respondents supporting an increase in the estate tax'. Auditor B re-estimated the same contrasts from the survey microdata (20.99%, +28.90, +10.87 pp). Print PT422.

Why this severity. A footnote supporting a secondary claim; the qualitative point (learning how few estates pay raises support markedly) survives, but the information effect is about half what is stated.

The authors' response. KNSS (2015, pp. 1491, 1496-1497), co-authored by Saez, report the neutral-treatment result themselves.

11minorconfirmed · newly identified here · external inconsistency

The chapter says about 1 in 1,000 people who die pay the estate tax; the real figure was about 2 in 1,000. Either way, very few estates pay it.

Technical detail and evidence

Why it matters, in detail. The taxable share of decedents was about 0.18-0.20% in 2013-16 at a $5.25-5.45m exemption; using filed returns it was about 0.44%.

Evidence. Adjudicator: IRS SOI 13es01yd (estate returns for 2013 decedents) 4,699 returns with net estate tax / 2,596,993 US deaths in 2013 = 1.81 per 1,000 (all 11,309 filed returns: 4.35 per 1,000); Auditor B obtained the same figure. Auditor A: 1.87-1.99 per 1,000 for returns filed in 2014-16. KNSS told survey respondents '1 decedent out of 1,000' (KNSS 2015, fn 32). Print PT422.

Why this severity. A factor-of-two slip in a footnote statistic; the point that the tax reaches very few estates is unaffected.

12minorconfirmed · newly identified here · misrepresentation of source

The chapter says the Census Bureau's official income measure subtracts some taxes; it subtracts none. It does include some government payments but not others, so the chapter's wider point about mixed definitions stands.

Technical detail and evidence

Why it matters, in detail. Census money income includes cash transfers (Social Security, UI, SSI, public assistance) and excludes in-kind benefits and all taxes and tax credits. It blurs the concepts on the transfer side only.

Evidence. DeNavas-Walt & Proctor (2015), Census P60-252, p. 4: estimates 'based solely on money income before taxes and do not include the value of noncash benefits'. Print PT421/PT583.

Why this severity. A footnote misdescription with no effect on any DINA number; the broader point (official money income is neither pre-tax nor post-tax national income) is valid.

13minorconfirmed · newly identified here · overclaiming

The chapter says nearly everyone agrees that ultra-fast trading firms add nothing of value. In fact economists were and are divided, and several major studies found such trading makes markets work better.

Technical detail and evidence

Why it matters, in detail. Both sides of the HFT literature were present when the chapter was written: liquidity and price-discovery benefits on one side, arms-race and adverse-selection costs on the other. A consensus claim is therefore not supported, whatever the net welfare effect.

Evidence. Print PT222: 'almost everybody agrees that hedge funds specializing in high-frequency trading do not add value but instead skim off gains at the expense of other, slower traders'. Brogaard, Hendershott & Riordan (2014, RFS 27(8): 2267-2306): 'Overall HFTs facilitate price efficiency'. Jones (2013 survey): 'Virtually every time a market structure change results in more HFT, liquidity and market quality have improved'. SEC staff literature review (2014): passive HFT strategies 'appear to have beneficial effects on market quality'. The opposing view: Budish, Cramton & Shim (2015, QJE) on a wasteful latency arms race.

Why this severity. An illustrative example; no estimate or recommendation depends on it.

14minorconfirmed · newly identified here · misrepresentation of source

The chapter contains a handful of small citation and wording mistakes, such as misnaming a co-author and giving the wrong reason for Kuznets's Nobel Prize. None of them changes any number or argument.

Technical detail and evidence

Why it matters, in detail. Readers may misattribute the JEL survey and misread the income concept: PSZ pre-tax income is after the operation of social insurance, so 'before any transfers' is inaccurate, but switching to factor income changes the bottom-90% growth statistics by at most 0.2 pp of capture.

Evidence. Nobel citation: 'for his empirically founded interpretation of economic growth which has led to new and deepened insight into the economic and social structure and process of development'; Nobel facts page: 'His prize was awarded for his earlier work with growth and the economy's size'. Print PT216 (Kuznets curve). Auditor A's full-text hits confirm in print the JEL attribution, 'Measuring Economic Stability', 'Berkhauser', 'Torre Olsen' and 'Explorations in Economic History 51 (2013)'. PSZ NBER WP 22945 pp. 9-10 define pre-tax income after pensions, DI and UI. Print PT217 ('before any taxes or government transfers'). The label is numerically immaterial: bottom-90% growth 1980-2014 is 0.76%/yr on factor income vs 0.77%/yr on pre-tax income (capture 31.8% vs 32.0%; adjudicator).

Why this severity. Documentation and attribution errors that affect no number or conclusion.

15minorconfirmed · newly identified here · version instability

The version of the chapter that anyone can download from the author's website is an earlier draft with different key numbers and an unedited placeholder, and it does not say so.

Technical detail and evidence

Why it matters, in detail. The two versions differ by 0.1 pp/yr in bottom-90% growth and by 5 pp in the captured share. The draft's 27% (1980-2012) is itself 3.3 pp below the Dec-2016 data.

Evidence. https://eml.berkeley.edu/~saez/saez_pikettyvolume.pdf (md5 96da7d71c34702f87fa4e19db7a17a15; identical across the three cached copies); draft pp. 5-7 vs print PT217-PT219 (Google Books snippets; Auditor A's Open Library hits). The draft's 27% does not match any public PSZ vintage either (30.3% in Dec 2016).

Why this severity. The published chapter is not affected, but readers of the free version see different headline statistics.

16minorplausible · previously known · methodology

The chapter says middle-class Americans stopped saving and that this helps explain growing wealth gaps. The saving numbers were not measured directly; they were worked backward from the same wealth estimates they are used to explain. Other data do show falling household saving, but how much is uncertain.

Technical detail and evidence

Why it matters, in detail. Writing W(t+1) = (1+q)(W(t)+S) with S as the residual, any error in capitalized wealth shares (e.g., the uniform-yield assumption) loads one-for-one onto group saving. The 'explanation' by saving inequality is thus an identity-based decomposition, not independent evidence. Re-estimation on the revised wealth series was not done.

Evidence. Print PT221 ('synthetic savings rate ... defined as the savings rate needed to explain the dynamics of top wealth shares'; 'savings inequality magnifies ...'); policy section 'saving rates for the U.S. middle class have plummeted since the 1980s' (print, Auditor A's full-text hit; draft p. 17). Bottom-90% synthetic saving reproduces (Auditor B: 5.6% 1970s, 6.9% 1980s, 2.0% 1990s, -3.8% 2000s; Auditor A: SZ Table B33). The authors' later revision raises the bottom-90% 2012 wealth share from 22.8% to 25.7% (WID 2026, adjudicator), which mechanically implies a smaller residual decline. Independent support for the direction: NIPA personal saving rate 11.1% (1980) to 2.2% (2005) (Auditor A).

Why this severity. The construction is disclosed and the direction has independent support; the issue is that an accounting residual is presented as an explanation, and its magnitude inherits the capitalization errors in F3.

17minorplausible · previously known · selective presentation

The chapter says almost nothing is known about whether America's rich mostly inherited their wealth. There was some evidence, and it suggested the richest Americans had become more self-made, not less. That evidence has limits, but the chapter does not mention it.

Technical detail and evidence

Why it matters, in detail. Survey inheritances are underreported (perhaps 20-30% of macro flows; Alvaredo, Garbinti & Piketty 2017), and the Forbes 400 is a narrow group. Still, the omitted evidence leans against a rising inherited share at the US top, which the chapter's framing leaves unacknowledged.

Evidence. Print PT220 ('little progress has been made on this question in the United States since this debate due to the lack of systematic administrative data'). Kaplan & Rauh (2013, JEP 27(3)): the share of the Forbes 400 who 'grew up wealthy fell from 60 to 32 percent' (1982-2011), while first-generation founders rose from 40% to 69% (adjudicator check of the text). Wolff & Gittleman (2014, JOEI): transfers fell from 29% to 19% of net worth (1989-2007) (corpus capital21-23).

Why this severity. Framing only; both omitted sources have known weaknesses (narrow Forbes sample; self-reported inheritances), so the call for administrative inheritance data is justified.

The authors' response. Alvaredo, Garbinti & Piketty (2017, Economica) argue that survey-reported inheritances are implausibly low and that US trends are highly uncertain (corpus capital21-23); no response specific to the chapter.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

The printed 1946-80 '62 percent' (and the draft's '27 percent') should not be counted as errors because the exact preliminary DINA vintage could not be located; they are unresolved discrepancies. — The print updated the other growth figures to the Dec-2016 vintage, which reproduces them exactly. That vintage, every later vintage (68.9-69.6%) and the co-authored PSZ working paper (Table 2; 1946-80 growth 'slightly equalizing') all contradict 'the same' growth and 62%. 62% equals the bottom 90%'s 1946 income share (62.8%), i.e., what equal growth would imply. Counted as a confirmed minor error (F6), minor because it understates the post-1980 contrast.
The chapter's pre-tax/post-tax claim is supported: post-tax inequality is lower and trends are broadly parallel; the exact cancellation of tax and transfer changes is merely not separately identified. — The authors' own Dec-2016 data and working paper show post-tax inequality rising less (top-10% share +9.5 vs +12.8 pp; PSZ WP p. 19) and redistribution offsetting about one third of the bottom-90% growth gap (WP note 58), which contradicts 'roughly cancel each other out' (F2).
The 'almost everybody agrees' HFT passage is not an issue because Brogaard-Hendershott-Riordan study proprietary traders and do not establish net welfare gains. — The chapter asserts a consensus. A substantial peer-reviewed and regulatory literature finding beneficial effects on liquidity and price efficiency (Brogaard et al. 2014; Jones 2013 survey; SEC staff 2014 review) refutes a consensus claim regardless of the net welfare verdict. Counted as minor (F13).
Synthetic saving rates raise no issue because the chapter labels them synthetic and states their definition. — Partly rejected. Nothing is concealed, but the chapter then uses the residual as an explanation of the wealth explosion and, in the policy section, as an established fact; kept as a minor, plausible methodology issue (F14).
The KNSS citation ('support for the estate tax doubles when people are informed') matches the source (recorded as a check passed). — It matches the KNSS abstract only. KNSS's own Table 7 and p. 1491 show that purely factual information raises support for increasing the tax by about 52%; doubling requires the emotional, argumentative slide (F10, from Auditor B).
'Scandinavian countries collect comprehensive wealth information across many asset classes' is outdated (Sweden stopped in 2007, Finland in 2006). — Norway retains a wealth tax with third-party wealth reporting, and Denmark continued to collect third-party wealth data after abolishing its wealth tax in 1997 (Jakobsen, Jakobsen, Kleven & Zucman 2020, QJE). The Danish research the chapter cites (Chetty et al. 2014) uses those data. The generalization is loose for Sweden and Finland but is not an error.
'Almost entirely repealed during the Bush administrations' overstates the estate tax's history. — EGTRRA (2001) legislated a phase-down and a full repeal for 2010 during the Bush administration. The phrase is a loose but defensible description and immaterial to any claim.
The chapter does not mention that roughly half of national income must be imputed to individuals (part of Auditor A's I2). — Partly rejected. The chapter does describe the main imputations (fringe benefits, retained earnings, pension returns, imputed rents) and says that defining pre-tax income 'requires a conceptual framework' and is 'not just a pure accounting and measurement exercise' (draft pp. 5-6; print PT217). What is missing is quantification and an uncertainty range, which F1 retains.

Audit notes

What reproduced. Adjudicator scripts are in final/scripts (run_all.sh) with outputs in final/outputs. Reproduced exactly: the printed 1980-2014 DINA figures from PSZ's Dec-2016 appendix TB3 (1.407% vs 0.765%/yr; capture 31.99%); the draft's 1980-2012 growth rates; SZ (2016) Table B1 top-1% wealth shares (22.94% in 1978, 41.82% in 2012) and SZ's alternative-capitalization values (39.97%, 18.70%); Kopczuk-Saez (2004) Table 3; Bakija-Cole-Heim's 67-70%; the PSS cross-country growth null (slope 0.0008 per pp, HC1 s.e. 0.0094; 40-pp cut 95% CI [-0.77, +0.70] pp/yr); BEA growth windows; IRS/NCHS estate-tax incidence (1.81 per 1,000); KNSS Table 7 (published table; Auditor B re-estimated it from the microdata). Not reproduced: the printed 1946-80 '62 percent' and 'the same, at 2.1 percent' (data: capture 68.9%; 1.98% vs 2.12%/yr); the draft's '27 percent' (data 30.3%); the 'roughly cancel' claim (data: post-tax top-10% rise 9.5 pp vs 12.8 pp pre-tax). Adjudicator sensitivities: capture of aggregate rather than per-adult growth 44.1% (1980-2014) and 67.1% (1946-80); factor-income capture 31.8%; WID 2026 capture 36.2% and top-1% wealth 36.6% in 2012; Auten-Splinter (2024) bottom-90% capture about 50% (individuals, 1980-2014).

Limits of this audit. The complete published chapter was not obtainable (JSTOR challenge page; Internet Archive scan print-disabled). Every printed passage relied on was confirmed through Google Books snippets (book 4H-7DgAAQBAJ; electronic page ids, not printed page numbers) or Auditor A's Open Library full-text hits; the author draft was read in full. The spring-2016 preliminary PSZ vintage behind the draft is not public. DINA and capitalization numbers were reproduced from released output tables, not confidential microdata. The Auten-Splinter and CBO comparisons use different units (individuals or households, size-adjusted ranking) and concepts; no alternative was re-estimated on PSZ's equal-split-adult concept, so F1's range is indicative. The CBO pre/post comparison and SCF microdata shares rely on the auditors' computations (CBO market-income case re-checked). PSS panel and clustered results rely on Auditor B and this project's PSS adjudication; only the endpoint regression was re-run. Synthetic saving rates were not recomputed on revised wealth series. Not verified: that section 162(m) 'fueled' stock options (cited to Hall & Murphy 2003), WTID country coverage, and the cost and feasibility of the proposed information reporting. The claim that an annual wealth tax would be 'much more difficult to avoid' than inheritance taxation was examined and not counted: it is an unquantified conjecture, and the evidence then available was mixed. Locations: 'print PTnnn' = Google Books electronic page id in book 4H-7DgAAQBAJ (published HUP text; not a printed page number); 'draft p. n' = page of the author-posted PDF.