Facundo Alvaredo, Anthony B. Atkinson, Lucas Chancel, Thomas Piketty, Emmanuel Saez, Gabriel Zucman · WID.world Working Paper 2016/1 (per Zucman site; WID lists 2016/2), December 2016; revised 2020/2021 as 'Distributional National Accounts Guidelines: Methods and Concepts Used in the World Inequality Database'

Distributional National Accounts (DINA) Guidelines: Concepts and Methods used in WID.world

21 problems found: 6 moderate · 15 minor

What the paper claims

Income-concept framework: four concepts defined with SNA 2008 codes (pre-tax factor income, pre-tax national income, post-tax disposable income, post-tax national income); pre-tax factor, pre-tax national and post-tax national income each sum exactly to net national income, while post-tax disposable income is 'typically around 70% of national income' where in-kind transfers and public spending are about 30%.
Observation units and output format: benchmark unit is the adult aged 20+, with narrow equal-split (within couples) benchmark series and individualistic series; couples' capital income split 50/50; distributions delivered as 127 generalized percentiles and synthetic micro-files.
Basic imputation methods for countries with high-quality micro-data: fiscal income scaled to national-accounts totals by category (default: proportional); undistributed profits imputed from dividends and capital gains; production taxes proportional (property taxes by housing); corporate tax on all capital except housing; public health lump-sum and all other in-kind transfers and collective expenditure 'in proportion to post-tax disposable income', called 'the simplest (and distribution neutral) way'; pre-tax and post-tax disposable distributions 'can be estimated in a relatively precise manner' because variants show limited consequences.
Wealth concepts and reconciliation: SNA balance-sheet wealth (personal, private, public, national at market and book value); income capitalization with fixed returns by asset class supplemented by surveys ('mixed method'); reconciliation of capitalization and estate-multiplier estimates through differential returns r(k), mortality m(k) and evasion e(k), with Saez-Zucman (2016) cited as concluding that evasion explains the remaining gap; fiscal sources 'generally more reliable than surveys and billionaires list'.
Methods for countries/years with limited data: generalized Pareto interpolation (gpinter) giving 'errors typically less than 0.1%'; France before 1970 built with 'the same average ratios as those observed during the 1970-2014 period', alternatives 'very close'; China survey-tax merge (surveys reliable to 'say p=0.9', tax data above p=0.99/0.995; profile variants make 'limited difference'); non-fiscal income added with a Gumbel copula (theta ~3; 2.5-5 has 'relatively small impact'); donor Pareto coefficients and transplanted ratios where tax data are missing.
Continuity with WTID and precision: 'In most cases, the general trends in inequality depicted in the WTID series will not necessarily be very different in DINA series', while DINA 'will allow for more precise comparisons over time and across countries'.

Every problem found

1moderateconfirmed · previously known · selective presentation

To count public services like schools, police and defence in people's incomes, the guidelines share them out in proportion to income and call this 'neutral'. In fact it is the choice that shows the least redistribution. Giving everyone the same amount would cut the top 1%'s US share from about 15% to 12.5% and raise the poorer half's from 20% to 25%, and the 2016 text did not show this alternative.

Technical detail and evidence

Why it matters, in detail. US 2016: allocating collective consumption (16.6% of NI) per adult instead of in proportion to disposable income lowers the post-tax top-1% share from 15.0% to 12.5% and raises the bottom-50% share from 20.0% to 25.1%. The Guidelines' 'simplest' rule gives 16.4% and 17.1%. The 1980-2014 rise in the post-tax top-1% share ranges from 6.0 to 8.4 pp (benchmark 7.4). Calling proportionality 'neutral' understates redistribution through public goods relative to a central allocation; no trend reverses.

Evidence. June 2017 text pp. 36, 64-65; 2020 Guidelines p. 65. Adjudicator recomputation on PSZ external micro-file usdina2016.dta (equal-split adults; collective consumption 16.6% of NI, in-kind transfers 8.4%), script final/scripts/us_posttax_alloc.py. Post-tax national income shares (top 1 / top 10 / bottom 50): PSZ benchmark 15.0/38.0/20.0. Collective consumption per adult: 12.5/33.1/25.1. Half per adult (Auten-Splinter type): 13.7/35.6/22.6. Education lump-sum (PSZ variant colexp2): 14.2/36.6/20.6. Guidelines' all-proportional rule: 16.4/40.7/17.1. All in-kind and collective spending per adult: 12.5/33.2/24.9. Rise of the top-1% share 1980-2014 (PSZ 2022-vintage files): +6.0 pp per adult, +7.4 benchmark, +8.4 all-proportional. These reproduce auditor A's figures exactly.

Why this severity. The concept and its adding-up are unaffected, and the text calls the exercise 'approximate and exploratory'. But the level of post-tax inequality moves by -17% to +9% (top 1%) and -15% to +26% (bottom 50%) across defensible rules, and the trend by roughly 15-20%. Measuring that level is the purpose of the post-tax concept. The 2016 text shows only the low-redistribution side and calls it neutral. The qualitative trend survives every rule.

The authors' response. The 2020 revision (pp. 64-65) relabels proportional allocation as 'a realistic lower-bound on redistribution' and announces a lump-sum 'upper-bound' series alongside the benchmark. Saez & Zucman (2020) argue that per-capita rules have perverse implications, and PSZ describe their treatment as neutral (corpus us-income-13).

2moderateconfirmed · newly identified here · misrepresentation of source

For France before 1970, the guidelines describe one way of converting old tax statistics and say a second way gives nearly the same answer. The French study actually used the second way, and the two do not agree. Around 1915-1929 the richest 1%'s estimated share differs by about 3-5 percentage points out of roughly 20, though the story of falling inequality holds either way.

Technical detail and evidence

Why it matters, in detail. Applying constant 1970-2014 g-percentile pre-tax/fiscal ratios instead of a 1915-1970 phase-in raises French 1915-29 pre-tax top-1% shares by 2.8-4.7 pp (13-21%), 1930-44 shares by 0.4-2.0 pp and top-10% shares by up to 3.2 pp. It also raises the measured 1915-45 fall in the top-1% share from 11.3 to 15.0 pp. After 1945 the gap is between -0.3 and +1.2 pp. The choice is first-order for early-period levels and for the size of the wartime compression, and so for any WTID-to-DINA conversion of historical tabulations.

Evidence. Guidelines p. 78 (PDF 79); GGP Dec 2016 draft (piketty.pse.ens.fr/files/GGP2016DINA.pdf, Wayback 2020-11-29) and WID WP 2017/4 April 2017 file (wid.world/wp-content/uploads/2017/04/GGP2016DINA_2017_4_v2.pdf), p. 20. GGP Jan 2018 revision, pp. 23-24. Adjudicator counterfactual (final/scripts/france_pre1970.py; WID bulk FR sfiincj992/sptincj992, 2026-10-15). It averages 1970-2014 pre-tax/fiscal share ratios over 37 groups (p0p50, p50p90, nine percentiles p90-p99, 28 top-1% g-percentiles), applies them to pre-1970 fiscal shares and renormalises. Top-1% share, described rule vs WID: 23.7% vs 19.9% (1915, +3.8 pp); 27.6% vs 22.9% (1916, +4.7 pp, +21%); 23.6% vs 20.1% (1920); 23.8% vs 21.0% (1925); 19.2% vs 17.3% (1930). The gap is +2.8 to +4.7 pp (13-21%) in 1915-29, +0.4 to +2.0 pp in 1930-44, 0.1-0.5 pp in 1945-50 and -0.3 to +1.2 pp in 1951-69. Top-10% gap up to +3.2 pp. 1915-45 fall in the top-1% share: 15.0 pp vs 11.3 pp. Auditor A's top-share shortcut gave +3.2/+3.5 pp. The g-percentile calculation gives more because ratios rise steeply inside the top 1% (2.2 for the top 0.001%).

Why this severity. No published series changes (WID uses GGP's rule), and the long-run decline holds under either rule. But the Guidelines recommend the approach for other tabulation-only countries and periods. The robustness they assert fails by up to about 20% of the early top-1% level and about a third of the measured 1915-45 compression.

The authors' response. None located. GGP say of their own approximation that 'the impact on our long run patterns is likely to be limited (and in any case would tend to reinforce our main findings)' (GGP Dec 2016 / Apr 2017 drafts).

3moderateconfirmed · previously known · methodology

The guidelines produce very detailed numbers but give no way of saying how uncertain they are. The one accuracy figure they quote is for a minor technical step that is precise to a fraction of a percent. The big judgement calls can move results by 10-25% and are never measured, so readers may take fragile estimates as precise.

Technical detail and evidence

Why it matters, in detail. The only error metric offered (gpinter, about 0.1-1% relative) is dwarfed by convention uncertainty of ±10-25% in levels (F1, F2) and by unquantified merge and donor uncertainty in data-poor countries. Without bounds, the cross-country and over-time comparisons that DINA exists to support carry undisclosed error bands that can exceed the differences being compared.

Evidence. June 2017 text pp. 7, 63, 76, 85. A text search of the June 2017 and April 2018 versions finds no uncertainty framework ('standard errors' appears only for gpinter). Magnitudes from F1 (US 2016 post-tax top-1% 12.5-16.4%) and F2 (French 1915 pre-tax top-1% 19.9% vs 23.7%). The 2020 revision, Ch. 9 (pp. 159-160), adds a country transparency index and 0-5 quality grades per series, but no quantitative uncertainty.

Why this severity. No estimate changes, but users cannot tell robust from fragile series. The precision claims in C6 rest on no error analysis. The 2020 quality grades only partly fill the gap. This is a cross-cutting reporting gap; its magnitude is not additional to F1-F5.

The authors' response. The 2020 Guidelines (Ch. 9) introduce an inequality transparency index and 0-5 data-quality grades per series. They also announce three post-tax series to bracket the public-spending allocation (p. 65).

4moderatelikely · previously known · speculative assumption

Tax returns capture only about half to 60% of national income. By default the guidelines spread the rest in proportion to what people report. In the US, reasonable alternatives move the top 1%'s pre-tax share by up to about 2 points out of 20. The guidelines say such choices matter little, which is debated but not disproved.

Technical detail and evidence

Why it matters, in detail. With 40-55% of national income absent from tax returns, proportional scaling imposes the reported-income distribution on the missing part. Audit-based allocation with re-ranking lowers the US 2014 top-1% pre-tax share by up to 2.0 pp (AS). SZ argue a smaller difference when ranking by true income. Effects on the 1979-2019 trend are small by both sides' accounts. In developing countries the direction is unknown, because the gap mixes informal income with errors in the national-accounts aggregates.

Evidence. Guidelines pp. 17-20, 55-56, 63, 81. Fiscal income excluding capital gains is 59.8% of US national income (PSZ micro-file 2016, adjudicator) and 45-49% of French NNI per adult over 1970-2014 (WID). Auten & Splinter (2024) attribute 2.0 pp of the 6.0 pp gap in the 2014 US top-1% pre-tax share to the proportional allocation of underreported income (corpus us-income-10). Saez & Zucman dispute this. Iselin & Reck (2025) place PSZ's implied relative misreporting at the high end of plausible values and AS's implied decline as implausible (us-income-15). PSZ attribute about 5% of the 1979-2019 AS-PSZ trend gap to evasion (us-income-10). Not re-estimated here.

Why this severity. The best-documented alternative allocations move the US top-1% pre-tax level by up to about 2 pp of roughly 20 (≈10%), with small effects on the trend. The Guidelines' claim of limited sensitivity is contested rather than refuted, and the qualitative findings are unaffected.

The authors' response. Saez & Zucman (2020, NBER WP 27921, Sec. 3.1) and PSZ's comment on Auten-Splinter dispute the audit-based allocation and argue that random audits miss sophisticated evasion (corpus us-income-10). Gale, Sabelhaus & Thorpe (2023) side broadly with PSZ on this point (us-income-21).

5moderatelikely · previously known · methodology

The guidelines estimate wealth from the interest and dividends people report, assuming everyone earns the same return on each kind of asset. Wealthier people seem to earn higher returns, so this makes them look richer than they are. In US studies, fixing this lowers the top 1%'s wealth share by about 5-7 points out of about 40, and the guidelines give no such range.

Technical detail and evidence

Why it matters, in detail. Uniform within-class yields map the concentration of interest and dividends one-for-one into wealth concentration. If top yields exceed average yields, top shares are overstated. Low-rate years push capitalization factors toward 100 and amplify the error. Linked-data re-estimates lower the US top-1% share by 5-7 pp in 2011-2016.

Evidence. Guidelines pp. 41-43, 56-59, 69-73. Bricker, Henriques & Hansen (2018): US top-1% wealth share in 2011 falls from 40.5% (homogeneous returns) to 33.9% (heterogeneous interest returns) (us-wealth-taxes-03). Smith, Zidar & Zwick (2023): 2016 top 1% 38.9% with equal returns vs 33.7% (us-wealth-taxes-06). Fagereng et al. (2016, Norway) and Lundberg & Waldenström (2018, Sweden: up to ~15% overstatement) (us-wealth-taxes-04, -05). Not re-estimated here.

Why this severity. In the US, published re-estimates lower the top-1% wealth share by about 5-7 pp (≈15%) and part of its post-2000 rise. The bias is disclosed qualitatively and partly accepted by the authors, so it qualifies the wealth framework rather than overturning it.

The authors' response. Saez & Zucman (2016, Sec. IV.C) validate capitalization on foundation data. Saez & Zucman (2020) adopted higher top fixed-income yields but dispute SZZ's top yields (corpus us-wealth-taxes-06).

6moderateplausible · previously known · speculative assumption

For countries with poor data, the guidelines patch survey figures with tax data or borrow patterns from other countries. These patches rest on untested guesses, such as where surveys stop being reliable or that a correction measured in one period applies to decades of others. For China, a correction measured in 2006-2010 is applied to every other year without the guidelines saying so; how this affects trends is unknown.

Technical detail and evidence

Why it matters, in detail. In tabulation-only settings the corrected top share depends on the survey-trust percentile, the tax-data floor and the interpolated upgrade profile. With the 2006-2010 profile held fixed for 1978-2005, the pre-2006 correction is a rescaled image of the survey's shape and cannot detect changes in survey under-coverage. The direction of any resulting trend bias is ambiguous.

Evidence. Guidelines pp. 79-84. PYZ WP 2017/6 pp. 17-18 and fn 19 on p. 18 (read by adjudicator). Flachaire, Lustig & Vigorito (2023): corrected inequality 'may be significantly biased' if the merging threshold is misplaced (international-global-05; Codex read the 2021 conference version). Ravallion (2022) (international-global-01); Hlasny & Verme (2020) (international-global-12). Yonzan et al. (2022) find survey and tax data agree up to P99 in three rich countries. That supports p≈0.9 there but is silent on poorer countries (international-global-04).

Why this severity. These assumptions set corrected levels and trends for most WID countries outside the OECD. Their impact has not been quantified by the authors, the auditors or here, so this is a robustness concern with undemonstrated magnitude rather than a demonstrated bias.

The authors' response. The 2020 revision adopts the Blanchet-Flores-Morgan reweighting method with a data-driven merging point and labels donor parameters 'last resort'. Chancel & Piketty (2021, JEEA) concede corrections often rely on a limited set of countries (corpus international-global-01).

7minorconfirmed · newly identified here · misrepresentation of source

The guidelines say an earlier study by two of their own authors concluded that hidden wealth explains why two measurement methods disagree. That study actually left the question open. No numbers change, but the evidence is overstated.

Technical detail and evidence

Why it matters, in detail. The source offers an unresolved three-way attribution (mortality gradient, avoidance, approach-of-death effects), not a residual decomposition. Citing it as evidence for e(k) overstates support for the capitalization series against estate-based ones. Their decedent-income test points to an unrepresentative decedent sample.

Evidence. Guidelines p. 71 (PDF 72); 2020 Guidelines p. 129. Saez & Zucman (2016) QJE 131(2), pp. 524, 541-542, 570-572 (adjudicator read the QJE PDF).

Why this severity. No series is affected. The passage overstates the evidence for attributing the capitalization-estate gap to evasion, and hence for preferring capitalization-based wealth series.

8minorconfirmed · newly identified here · misrepresentation of source

Some numbers quoted for China do not match the study they come from. For example, income missing from tax data started at about 5% of national income, not 1%, and peaked in 2007 rather than rising steadily. The broad point still holds.

Technical detail and evidence

Why it matters, in detail. The 1978 level is understated by about 4 pp of NI; a hump-shaped profile is described as a monotone rise. Tax data covering ~0.5% of urban adults (fewer of all adults) are described as covering the top 0.5-1% of the whole distribution.

Evidence. Guidelines pp. 79, 81 (unchanged April 2018). PYZ WP 2017/6 pp. 17 and 19. PYZ data workbook PYZ2017DistributionalData.xlsx, sheet TB0: non-fiscal income 5.0% (1978), 14.8% (2007), 10.7% (2015); fiscal income 60.7-69.5% of NI (adjudicator).

Why this severity. The qualitative point (a large, rising non-fiscal component) stands. The starting level is misstated, the 2007 peak omitted, and the tax data's population coverage roughly doubled.

9minorconfirmed · newly identified here · version instability

A setting used to combine income sources changed from about 2 to about 3 between drafts, described both times as 'observed' in US and French data. The paper cited contains no such estimate. The setting seems to matter little, but its basis is unclear.

Technical detail and evidence

Why it matters, in detail. The same 'observed' US/France dependence is reported as 1.8-2.2 and then 2.5-3.5 without explanation, and the cited source contains no copula estimates. Theta governs how non-fiscal capital income is allocated across the income distribution in data-poor countries, but within 2-5 its effect is small according to PYZ.

Evidence. Guidelines June 2017 p. 82 and fn 36; January 2017 version pp. 80-81. BFP WID WP 2017/3 files (April and October 2017): zero hits for copula/Gumbel (adjudicator text search). PYZ WP 2017/6 p. 19 fn 23.

Why this severity. PYZ report small effects of theta on China's top shares. The problem is the evidential basis and the unexplained change, not a demonstrated effect on results.

10minorconfirmed · newly identified here · overclaiming

The guidelines say their interpolation tool is accurate to within 0.1%. The study they cite shows errors several times larger in some cases, up to about 1%. That is still small, but the claim is too strong.

Technical detail and evidence

Why it matters, in detail. For France and for quantiles the claim is off by a factor of 2-10. For the three-threshold configuration described, BFP give no estimate, and their optimal three-bracket case has a 2.35% maximum error.

Evidence. Guidelines p. 85; BFP WID WP 2017/3 (April 2017 file) Table I p. 18 and Table V p. 33 (adjudicator read).

Why this severity. Interpolation errors of 0.2-1% are small next to other uncertainties (see F6), but the stated precision is too high by a factor of 2-10 for several statistics.

11minorconfirmed · newly identified here · internal inconsistency

The pension accounting subtracts the same small income flow twice and then adds it back elsewhere. Totals still come out right, but the money could be credited to the wrong people. In the worked example it is half a percent of national income, and a table note also quotes wrong pension totals.

Technical detail and evidence

Why it matters, in detail. The double deduction removes D442 from pension-wealth holders (and D6141 from contributors via D61) and returns it as a surplus allocated by a different key. The distributional effect scales with D442/NI: 0.5% in the template, more in funded-pension countries. Its sign depends on the allocation keys, and it is not quantified for any country.

Evidence. Guidelines pp. 31-32 and Table 4 (PDF 99); 2020 Guidelines pp. 47, 61, 113. UN SNA 2008 Annex 2, secondary distribution of income account: D61 333; D611 181 (D6111 168); D612 19 (D6121 18); D613 129 (D6131 115); D614 10 (D6141 8); service charges 6; D621 53 (D6211 45); D622 279 (D6221 250). Adjudicator checked the UN SNA text; Codex recomputed the companion workbook cells.

Why this severity. Aggregate pre-tax income is restored by the compensating surplus, so all totals hold. The misallocated flow is 0.5% of NI in the example, and no effect on a published distribution has been shown. The 2020 recommended broad definition is correct. Codex rated this moderate; the adjudicator does not, because nothing published is shown to change.

12minorconfirmed · newly identified here · arithmetic or transcription

Several ratios in the worked-example tables were calculated with the wrong numbers, and one total does not match its parts. These tables only illustrate the method and feed no published figures.

Technical detail and evidence

Why it matters, in detail. Two indices are overstated by 75-125%, two capital-output ratios are misassigned, and proportional land splitting is not additive across sectors. None of this affects any distributional estimate.

Evidence. Tables 2, 6, 10, 12-14, 16 (PDF 97, 101, 105, 107-109, 111) in the January and June 2017 versions; dropped in April 2018. Arithmetic checked by adjudicator; consistent with both auditors.

Why this severity. These are illustrative tables built on the fictional SNA economy. The main identities hold, and no WID series uses these cells.

13minorconfirmed · newly identified here · internal inconsistency

In the worked example, spending by charities and other non-profits is mislabelled as a government deficit. The totals still add up, but the label is wrong and could lead to the wrong people being charged for it.

Technical detail and evidence

Why it matters, in detail. Implemented literally, the rule offsets NPISH-financed spending with a fictitious government 'deficit' allocated by the deficit key. The omission of capital taxes is small.

Evidence. Table 5 (PDF 100); pp. 36-37, 62-63. UN SNA 2008 Annex 2 use-of-income accounts: P32 168 (S13) + 1 (S15); D63 184 (S13) + 31 (S15) (adjudicator). 2020 Guidelines p. 64 and Table 2.8.

Why this severity. Aggregate post-tax income still equals NNI. The mislabelled item is 2% of NI in the template, and NPISH consumption is typically a few percent of GDP.

14minorconfirmed · newly identified here · documentation gap

In tables of returns on different savings, company profits that are kept rather than paid out are shared out in an odd, unexplained way. This produces implausible results, such as bank deposits earning more than shares, though the tables are only examples.

Technical detail and evidence

Why it matters, in detail. Allocating retained earnings to interest-bearing claims and pension funds in proportion to their distributed income produces return gaps that contradict asset pricing (equity below deposits). Capitalization with these yields would misallocate wealth across asset classes.

Evidence. Tables 8-9 (PDF 103-104); p. 42; 2020 Guidelines Table 3.4 (p. 75). Adjudicator reproduced the printed values under the flow key.

Why this severity. These are illustrative variants, and there is no evidence WID country series use them. But the text endorses the all-assets variant, and its implied yields would distort capitalization factors by factors of 2-3 if used.

15minorconfirmed · newly identified here · internal inconsistency

An appendix table labelled as national income per adult shows figures about 30% below national income per adult. It is only meant to show the format of the data.

Technical detail and evidence

Why it matters, in detail. The income column corresponds to a narrower concept (about 0.69 x NNI, close in magnitude to disposable income), and the population is probably not the 20+ population.

Evidence. Table A1 (PDF 120-122). WID FR anninci992 2010 = 44,216.1 x inyixxi999 2010 = 0.79449; npopuli992 = 49,152,864; ahwealj992 x price index (adjudicator).

Why this severity. The table is presented as a format template, not as estimates.

16minorconfirmed · previously known · speculative assumption

The guidelines assume an answer to who ultimately pays company taxes, and the later version switches to a different answer. For the US the choice moves the top 1%'s pre-tax share by less than one point, and after-tax figures not at all.

Technical detail and evidence

Why it matters, in detail. The choice moves the 2016 pre-tax top-1% level by -0.2 to +0.7 pp. Effects on long-run trends could be larger when corporate taxes were heavier (Kopczuk); not quantified here.

Evidence. Guidelines pp. 61-62; 2020 Guidelines pp. 57-58, 67. PSZ micro-file 2016 (adjudicator, final/scripts/us_deficit_corptax.py): corporate tax 2.9% of NI. Pre-tax top-1% share: 19.34% benchmark, 19.12% with 25% on labour, 20.07% with all on equity owners.

Why this severity. The effect is small for current US levels (-0.2 to +0.7 pp of a 19% share). Post-tax series are invariant by construction, as the Guidelines correctly note.

The authors' response. The 2020 revision recasts incidence as an accounting convention (pp. 57-58). Saez & Zucman defend current-incidence conventions ('Harberger meets Diamond-Mirrlees', 2023; corpus us-wealth-taxes-13).

17minorconfirmed · previously known · documentation gap

When a government spends more than it raises, the after-tax figures must charge someone for the gap. The 2016 guidelines promise to explain how and never do. The choice matters little in normal years but more in crises, when deficits are large.

Technical detail and evidence

Why it matters, in detail. The undocumented allocation concerns a balancing item worth -3% to more than -10% of NI in recent US deficit years. It moves the post-tax top-1% share by ±0.3-0.6 pp in 2014/2016, potentially several pp in crisis years. Different rules in the Guidelines and the flagship country series reduce cross-country comparability.

Evidence. Guidelines pp. 36-37, 63 fn 32; 2020 Guidelines pp. 60, 66. PSZ micro-files (adjudicator, final/scripts/us_deficit_corptax.py), post-tax top-1% share across rules (PSZ 50/50, factor-income, all to taxpayers, all to beneficiaries, per adult): 14.9-15.5% in 2016 (deficit 2.9% of NI) and 14.4-15.1% in 2014 (deficit 3.6%). Saez & Zucman note that Auten-Splinter's tax-proportional rule would cut the 2020 post-tax top-1% share by about 3.3 points (corpus us-income-13).

Why this severity. In normal years the choice moves the US post-tax top-1% share by up to about 0.5 pp. It is undocumented in 2016 and inconsistent between the 2020 Guidelines and the US series, and matters more in high-deficit years.

The authors' response. The 2020 revision (Sec. 2.2.5.2) specifies the factor-income rule.

18minorconfirmed · newly identified here · internal inconsistency

In the 2020 update, the step-by-step recipe for after-tax income does not add up: followed literally, the total comes out about 2% short of national income. The published data do add up, so the error is in the write-up, not the numbers.

Technical detail and evidence

Why it matters, in detail. Following the text, the bridge is short by 30 (1.8% of NI) because government property income and the social-insurance balance are double-counted. Published series are unaffected.

Evidence. 2020 Guidelines pp. 50-51 (Tables 2.7-2.8), 60-64 (adjudicator recomputation). WID post-tax national income averages equal NNI per adult exactly for the US, France and the UK, 1980-2022 (WID API), so production code does not follow the text literally.

Why this severity. This is a definitional error in a later version's write-up of a core concept. Published series add up, so no estimate is affected. Codex rated it moderate; the adjudicator does not, because the published data are unaffected.

19minorconfirmed · newly identified here · replication failure

The 2020 update tells researchers to use a default setting supplied in a data file. The file contains a different kind of number from the one the text describes, so following the instructions gives nonsense. This hampers outside replication, but published data are not shown to be affected.

Technical detail and evidence

Why it matters, in detail. Outside users cannot reproduce the recommended limited-data imputation from the published defaults. Whether WID's internal parameters follow the text or the file is unknown.

Evidence. 2020 Guidelines pp. 138-141. Official companion archive (sha256 8506ccf7...), file 'Chapter 7/Default Parameters/default-parameters-lambda.dta': min 0.88507, max 10, first seven = 10, p50 = 1.10, top bracket 0.97 (adjudicator read with pyreadstat). Codex's synthetic test not re-run.

Why this severity. This is a replication failure for a last-resort default in a later version's companion package. It is self-revealing and not shown to affect any published series. Codex rated it moderate; the adjudicator does not, because published series are unaffected.

20minorconfirmed · newly identified here · arithmetic or transcription

Several formulas in the technical chapters of the 2020 update have sign errors, wrong symbols or incorrect claims. Where the computer code is public, it uses the correct versions, so published numbers appear unaffected.

Technical detail and evidence

Why it matters, in detail. Literal implementation would fail visibly: negative reconciled aggregates, out-of-range Lorenz coordinates, a wrong AR(1) mean. The alpha claim matters only if beta is transplanted without its alpha. Remaining code issue: a small junction discontinuity in the Lorenz example.

Evidence. 2020 Guidelines pp. 90-95, 135-137, 145-148 (adjudicator read). WID public code read as text: wid-enforce.ado lines 833-847 uses +sign(x) on the right-hand side; impute-confc.do lines 183-194 include rho^t*e0 and the correct gap formula, and lines 437-443 split household CFC by gross operating surplus and 30% of gross mixed income. combining-lorenz-example.do line 106 computes q_svy from l_svy. Codex's numerical tests not re-run.

Why this severity. These are documentation errors. Where public code exists it implements the intended algebra, and no published series is shown to be affected.

21minorconfirmed · newly identified here · documentation gap

The document has many editing slips: wrong section references, unfinished notes, a broken link and a few small factual errors. They make it harder to use but change no results.

Technical detail and evidence

Why it matters, in detail. Several cross-references point to discussions that do not exist (notably the 70/30 split alternatives), making some conventions undocumented. Otherwise these are editorial errors.

Evidence. June 2017 pp. 2, 6, 8, 12, 29, 32, 41, 58, 66, 76, 92, Tables 16-17. April 2018 version PDF pp. 92-94 (Sec. 7.6 twice; note-form text). JO Sénat 22/01/2015 p. 157 (Ministry answer to question 08185). All checked by adjudicator.

Why this severity. These affect usability and citation accuracy only; no result changes.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

I15: the expectation (p. 7) that DINA trends resemble WTID trends is overclaiming, because it holds for direction but not magnitude. — The sentence is a hedged expectation ('will not necessarily be very different'), paired with a commitment to compare the series systematically (fn 1). The adjudicator's recomputation from WID (final/scripts/wtid_vs_dina_trends.py) finds the same sign in 24 of 26 country-window comparisons. Differences in magnitude (e.g. US top 10% 1980-2014: +11.7 pp DINA vs +17.6 pp fiscal) are what the DINA corrections are designed to produce. The facts are recorded in checks_passed; this is not a defect.
I4 (part): the Guidelines' survey-reliability threshold 'p=0.9' misstates PYZ's benchmark of p=0.8. — The Guidelines give 'say p=0.9' as an illustration of a generic method, not as PYZ's parameter. PYZ's own fn 19 uses p1 = 0.9 for the extrapolated profile, while its main text says 0.8. The rest of the claim, the undisclosed time-invariant upgrade profile, is retained in F5.
I16 (part): 'in Russia and Gulf countries the share of financial wealth held offshore seems to exceed 50%' is wrong because Zucman (2014) gives 50% for Russia. — Zucman (2014, JEP, Table 1) gives Russia 50% and Gulf countries 57%, and its own text says 'as much as 50 percent in Russia and Gulf countries'. The joint paraphrase is loose but not materially wrong.
I7: the Forbes-correction equations 6.1-6.2 fail dimensional and bracket-mass checks. — Verified as real typesetting/formula errors (2025 Guidelines, PDF p. 148, printed p. 146). They occur only in the October 2025 Guidelines' new global-wealth section. That is a separate later document, not among this work's versions (2016 WP; 2020 revision), and not attributable to the 2016 authors' work. Out of scope; flagged for the 2025 Guidelines' own audit.
I8 (part): the latest Table 3.3 labels the capital share of mixed income 40% while its numbers use 30%. — Present only in the 2025 Guidelines (printed p. 78). The 2020 Table 3.3 (p. 74) correctly says 30%. Out of scope.
I3 (part): the latest Guidelines start post-tax disposable income from pretax factor income, omitting pension replacement (worker/retiree example [100,0] instead of [80,20]). — 2025-only. The 2020 revision (p. 64) starts from pretax national income. Out of scope; the 2020 bridge error is retained as F18.
Severity: I1 (lambda defaults), I2 (pension duplication) and I3 (revised post-tax bridge) are moderate issues. — The defects are confirmed (F19, F11, F18), but the moderate grade is not accepted. None changes a published series: WID totals add up exactly, public code corrects the equations, and the lambda file is a last-resort default. None touches the original framework's results, so each is graded minor.

Audit notes

What reproduced. Reproduced: (i) the SNA-based template accounting (adjudicator spot checks of all SNA inputs to Tables 3-5 and of the Table 14/16 arithmetic; full reproductions by both auditors); (ii) WID's adding-up of pre-tax and post-tax national income; (iii) the quantitative asides on the US pension surplus, the FDI share of foreign equity, the offshore shares, disposable income at ~70% of NI and China's fiscal-income share; (iv) auditor A's US 2016 post-tax sensitivity (exact) and corporate-tax incidence results (to ±0.02 pp), extended to 1980/2014 trends and to deficit allocation; (v) auditor A's WTID-vs-DINA trend comparison. Not reproduced: the Table 4 note's pension totals (309/295, not 333/332); the Table 14 and 16 ratios; the Table 5 government balance (0, not -32); the French pre-1970 rule as described (it would put the 1915-29 top-1% share 2.8-4.7 pp above WID, against the claimed 'very close'); the China figures (5.0%, 14.8% peak, 10.7%, against '1% to 12%'); the gpinter precision claim (BFP report 0.2-1% for several statistics); a source for the Gumbel parameter (BFP 2017 contains none); the 2020 post-tax bridge (1,617, not 1,647); and the 2020 default lambda file (values 0.885-10, against a documented range of -0.5 to +0.5). No country DINA series was re-estimated from raw data; the Guidelines have no replication package.

Limits of this audit. The first version (12 December 2016) and the supplementary Excel workbook listed in the Appendix were not obtained; the audited text is the June 9, 2017 version, compared with the January 2017, April 2017 (capture), April 2018 and 2020 (served as 27 Feb 2024) versions. Country checks use the current WID vintage (October 2026) and PSZ's external-use micro-files (2016 from the 2019 vintage; 1980 and 2014 from the 2022 vintage), not the 2016-2018 vintages the Guidelines describe. The French pre-1970 counterfactual applies averaged share ratios over 37 groups to current WID fiscal series, approximating GGP's g-percentile income ratios. Limited-data country series (China, India, Middle East, Africa) and capitalization-based wealth series were not re-estimated, so the magnitudes for F3-F5 rest on the cited critics and are disputed. Codex's synthetic tests (lambda formula, Lorenz junction, consumption profile) and full workbook recalculation were inspected but not re-run. The WID code read is a current snapshot, not tied to historical releases. Contemporaneous incidence studies cited by auditor A (Suárez Serrato & Zidar 2016; Fuest, Peichl & Siegloch 2018) were not re-read. The October 2025 Guidelines are treated as out of scope except for version comparisons.