Real-Time Inequality

Why it matters, in detail. The backtest uses final-vintage NIPA/QCEW/CPS/SSA inputs, complete QCEW and full-sample calibrations, and it aggregates 49 mostly calm years. In 2020-21 the binding errors came from the assumption of fixed within-component capital-income distributions at the top, from 2-year-old base files, and from data revisions. Net of aggregate revisions, Dec19->Dec21 real-time errors in relative factor-income growth were +4 to +6 pp (B50), +2 to +3 pp (M40) and -8 to -9 pp (top 1%), against final relative changes of -4.3, -3.7 and +10.7 pp. Real-time top-1% share changes over 2019-21 were +0.24 pp against +1.42 pp final. Disposable-income tracking at the bottom erred by only ~0.6 pp, so the method is reliable for transfer-driven changes but not for market-income concentration in a turbulent episode.

Evidence. Adjudicator recomputation from the authors' own website data (scripts/vintage_compare.py, realtime_errors.py, vintage_placebo.py; logs/): top-1% factor-income share 2019->2021 (annual averages, equal-split adults) +0.24 pp (Aug-2022 vintage) and +0.25 pp (Nov-2022) vs +1.42 pp in the July-2026 capture (identical in the Sep-2026 release); top-0.1% factor share -0.05 vs +0.92 pp; top-1% pretax share -0.03 vs +1.01 pp; Dec-2021 top-1% factor share 19.55% (Nov-2022) vs 21.12%. Real factor income per adult Dec 2019->Dec 2021: B50 +6.5% vs -0.6%, M40 +3.9% vs +0.1%, top 1% +6.7% vs +15.1%; net of aggregate revisions the real-time errors are +5.8 (B50), +2.7 (M40), -9.0 (T1) pp in the Aug-2022 vintage and +4.1/+2.1/-7.9 pp in Nov-2022, vs 2-year backtest RMSEs of 2.1/1.2/4.7 pp (Table A2). Placebo: the same vintages differ by <=0.5 pp on 2011-15 relative growth and <=2.2 pp on 2015-19, so most of the 2019-21 gap is projection error rather than later method revisions. Aug-2022 vintage had every group back to its Feb-2020 factor income by Sep 2021 (final: B50 Jul 2022, M40 Jul 2023). Second-quartile labor income Feb 2020->Jun 2022 was revised from +4.9% (Aug-2022) to +0.95% (Nov-2022) within three months. Top-1% wealth share Dec19->Dec21 +1.57 pp (Aug-2022) vs +0.48 (final; DFA +0.5); middle-40% -1.00 vs +0.88 (DFA +1.2). B50 disposable income +10.9% vs +10.4% (good). Backtest (vector-digitized Figs. 4-5, Codex): 2021 top-1% error -4.6 pp at 1 year and -7.1 pp at 2 years; B50 +3.7 pp (2021) and -4.6 pp (2022). ALFRED vintages of BEA corporate profits (CPROFIT): 2019-21 growth +18.5% (2022-08-25 vintage) vs +25.4% (2026-07-01), showing input revisions that a final-data backtest cannot capture; a rough calculation attributes only ~0.3-0.4 pp of the 1.2 pp top-1% share gap to this revision.

Why this severity. Validated real-time accuracy is the paper's methodological core. In its own showcase recession, real-time errors in relative factor-income growth were about 2-2.8 times the backtest's 2-year RMSE for the bottom 50% (about 2 times for the middle 40%), and real time captured only about one-sixth of the rise in the top-1% share, getting the direction of the inequality change wrong. This materially changes the magnitude of the accuracy claim for turbulent periods, though not the final tax-anchored Covid statistics or the disposable-income tracking.

The authors' response. None located. The paper calls the system a 'prototype' (Secs. 1, 8) and acknowledges larger top-1% errors in tax-reform years (Sec. 5.3), but does not discuss real-time vintages or revisions.

Why it matters, in detail. Because the predicted t+1 wage distribution is the fitted value of a regression that includes t+1, any drift in the QCEW->tax relation is absorbed into the slope and never shows up as backtest bias. The paper's 'low bias' and 'near-perfect alignment' are partly mechanical. A share-level expanding-window analog raises the top-1% wage-share residual by about 13-20%, a modest effect. The effect on bottom-50% predictions via the employment regression and filters was not quantified.

Evidence. Code (github.com/leonmouillet/real-time-inequality, publication-era files identical): 02-create-monthly-wages.do l.9-22, 57-78, 119-138 (`reg flemp flemp_naics/sic/cps if p==` pooled over years; fitted values saved as monthly-tabulations-flemp.dta); 03-build-monthly-microfiles-backtest-1y.do l.58-62 (1976 base) and l.469 (uses the fitted file); 02-prepare-bls-employment.do l.47; 02-adjust-seasonality-qcew.do l.33, 44; CHANGELOG '2026-03-mouillet'; 02-update-qcew-backtest.do (windows from 01/2020 to 01/2023). Adjudicator magnitude check (scripts/digitize_fig2.py, fig2_oos.py), a share-level analog from vector-digitized Fig. 2: expanding-window out-of-sample RMS residual of the top-1% wage share is 0.34 pp vs 0.30 pp in-sample (NAICS years) and 0.59 vs 0.49 (SIC years).

Why this severity. The look-ahead is confirmed in the code. But a rough out-of-sample analog suggests it inflates the measured accuracy of the top-wage component by only ~10-20% in RMS terms, and the larger real-time failures (F1) came mainly from capital income and data revisions.

The authors' response. No direct response; the paper calls the exercise 'retrospective' and the correction 'constant over the period'; the CHANGELOG openly reports weaker recent extrapolation.

Why it matters, in detail. The method's genuine contribution is the relative-growth component, which it predicts with R2 of about 0.4-0.5 (B50, M40, T1). It does no better than a constant for the next 9%. The headline R2 of ~0.7-0.8 and the 'half the SD' statistic mostly reflect aggregate growth imposed from NIPA. Mislabelling totals as per-adult inflates the mean-growth benchmark by ~1.2 pp/yr, so the bias-to-growth ratio for the B50 is ~0.5-0.7, not below 0.1.

Evidence. 04-backtest.do l.63, 191 (`gcollapse (sum) ... [pw=weight]`), l.217/231 (renamed 'average'), l.258 comment 'average = total income'; dina-rescaled.dta keeps population weights (02-prepare-dina.do l.278-336). Per-adult vs total means: Codex digitized points 0.57/1.05/1.67/3.04 vs 1.81/2.30/2.93/4.31 (1977-2024); Claude WID replication per-adult factor means 0.41/1.14/1.73/3.05. Relative-growth skill: from Table 2 (1 - RMSE_RTI^2/SD_uniform^2) 0.45/0.56/-0.27/0.43; from digitized points (scripts/backtest_stats.py) 0.42/0.52/-0.41/0.44; Table A1 B50 -0.38. backtest-table-share-*.tex generated (04-backtest.do l.700-760), not in the paper.

Why this severity. RMSEs and the comparison with naive benchmarks are unaffected, but two of the paper's summary statements of accuracy are materially overstated for the distributional question the method exists to answer.

The authors' response. None; footnote 18 concedes no improvement over the uniform model for the next 9%.

Why it matters, in detail. Reported 2019-21 real wealth growth exceeds the public series by 4 pp (average), 6 pp (top 1%) and 7 pp (top 0.01%), and the top-0.1% share gain by 0.6 pp. The paper's own data agree with the DFA (+1.4 pp), not with its text (+2 pp). The cause (an unreleased vintage, a different unit or deflator, or a transcription error) could not be identified.

Evidence. scripts/wealth_claims.py (logs/wealth_claims_jul2026.log, wealth_claims.log): real wealth per equal-split adult end-2019->end-2021 +23.1% (paper +27%), top 1% +24.7% (+31%), top 0.01% +36.7% (+44%). Top-0.1% share 19.95%->21.32%, +1.37 pp (paper '+2 points ... reaching 21.9%'; households 22.31%, working-age 23.06%; DFA +1.4). Fn 28 RTI top-1% share 1989Q3->2025Q4: equal-split 28.6->37.3, households 30.4->39.3, working-age 30.3->40.1 (paper 30.4->40.2, i.e. endpoints from different units). Changes for next 9%/M40/B50 -3.5/-4.4/-0.8 (paper -3.9/-5.4/-0.5). Fig. 10 note '[more than] two thirds of these gains were erased in 2022' for the top 0.1%: 53% in the data (67% for the top 1%). DFA (2026Q2 release) numbers in fn 28 reproduce within 0.1 pp.

Why this severity. These are secondary descriptive results. The qualitative findings survive: strong growth and rising concentration to end-2021, a partial 2022 reversal, and a DFA-consistent long-run trend (RTI +8.8 vs DFA +9.0 pp). But the stated gains at the top are 4-7 pp too high and cannot be audited.

Why it matters, in detail. Intra-quarter movements are attenuated by 50-70% and partly shifted earlier, consistent with near-smooth interpolation between quarter-end benchmarks that gives the equity indicator little weight. Monthly wealth inequality therefore lags or leads asset-price shocks by 1-2 months and understates their depth (top 0.1% about -6% at the 2020 trough vs equity -13% to -20%). The cause was not identified without running Stata.

Evidence. scripts/wealth_timing.py, wealth_timing2.py (FRED SP500 and NASDAQCOM daily -> month-end): total nominal wealth -4.86% (Jan 2020), -2.35% (Feb), +0.05% (Mar) vs S&P month-end -0.2%, -8.4%, -12.5%; top 0.1% -5.96%, -2.79%, -0.60%. 2017-2026 regression of monthly log changes on S&P month-end changes: top-0.1% beta 0.14/0.28/0.17 (months 1/2/3 of quarter) vs 0.48 quarter-end to quarter-end (corr 0.94); total wealth 0.04/0.19/0.13 vs 0.39. Similar in 2008 (Oct 2008 total -2.8% vs NASDAQ -17.7%) and 2022 (Apr 2022: total +0.6%, top 0.1% -0.3% vs S&P 500 -8.8%). Code 02-prepare-fa.do l.203-224 (Denton 'stock' with Wilshire/Case-Shiller indicators). Fig. 10 inspected (p.17).

Why this severity. This undermines the monthly wealth product and Fig. 10's timing, and contradicts a stated capability. The quarterly and annual wealth statements (end-2019, end-2021, DFA comparisons) are unaffected.

Why it matters, in detail. With the paper's own deflator the Covid-cycle second-quartile growth (0.45%/yr) barely exceeds the 2007-17 rate (0.36%/yr). Results span 0.14-1.04%/yr across standard deflators and swing by ~4 pp with the endpoint (Jun vs Sep 2022) and the vintage. Only the cross-sectional compression within the bottom 99% (Q2 vs Q3/Q4) and fast top-1% growth are robust.

Evidence. scripts/labor_recovery_claims.py (Jul-2026 capture; Sep-2026 release in parentheses). Q2 Feb 2020->Jun 2022 +1.06% (+0.97%), paper +1.6%; annualized 0.45%/yr vs 0.36%/yr Dec 2007-Dec 2017 (paper 0.7 vs 0.4). Deflator alternatives (FRED PCEPI, CPIAUCSL): PCE 1.04 vs 0.47%/yr, CPI-U 0.14 vs 0.24%/yr (reversed). Sep-2022 endpoint gives +5.5%; real-time Aug-2022 vintage +4.9%. Top 1% +5.0% (paper 'around 6%'). Top 1% Dec 2007->Dec 2017 +8.1% (0.78%/yr) vs total +7.3%, contradicting 'stagnated'. Q2 > Q3 (-2.4%) and Q4 (-0.7%) under all deflators.

Why this severity. This is a secondary finding. Its relative pattern survives, but the quantitative claim of a break in low-wage growth relative to the previous cycle is not supported at the quartile level and reverses with CPI-U.

Why it matters, in detail. About 41% of the subsidy flow labelled PPP belongs to other programs. If they had the same incidence, the PPP-only bottom-50% effect would be ~$89/month rather than ~$150. The incidence of PRF, airline support or the ERC need not match Autor et al.'s 23-34% worker share for PPP.

Evidence. raw-data/covid-aid-data/covid-aid-data.xlsx, sheet 'COVID (quarterly)': 2020Q2-2022Q1 cumulated subsidies $1,090.2bn vs PPP $645.1bn (59%). 02-prepare-nipa.do l.804 (publication copy l.803) `nipa_covidsub = covid_subsidies_mthly // XX`. 03-build-monthly-microfiles.do l.745-788 apply PPP keys. A fixed-key rescaling gives ~$89 rather than $150 per month (Codex). Autor et al. (2022) title figure: '$800 billion'.

Why this severity. This misattributes and overstates a specific secondary result (the PPP effect) by roughly 40-70% and transplants PPP incidence to programs with different recipients. Disposable-income totals are unaffected, and the correction strengthens the paper's own point that PPP effects were limited.

Why it matters, in detail. The system was not operated in real time for roughly 37 months, including the paper's submission. This indicates substantial maintenance costs and fragility to upstream data changes that bear on the feasibility claim in C1.

Evidence. Wayback captures of the root page on 2025-10-04, 2025-12-05, 2026-01-14 and 2026-05-14 (adjudicator re-downloads in /mnt/zdata/downloads/bmsz2026-rti-adjudicator/) carry the same banner and __NEXT_DATA__ ending 2023m3; data archived 2023-05-15 and 2024-05-28 are identical; the new site with R2-hosted data appears from late May 2026 (July-2026 data end 2026m3; Sep-2026 release ends 2026m6). CHANGELOG 2026-03 entries.

Why this severity. This is an important undisclosed caveat about the claimed timeliness of the product, and it means no real-time record exists for 2023-25. It does not affect the validity of any published estimate or of the method itself.

The authors' response. None; the CHANGELOG documents the 2026 revival of the pipeline.

Why it matters, in detail. All 'observed' growth for 2020-24 and all post-2019 levels rest on an unreleased DINA vintage. One of 49 backtest observations (2024) compares a projection with a partly projected target, and the 2016-19 top-0.1% wealth shares moved ~2 pp between vintages without explanation.

Evidence. usdina page (cached 2026-10-25, dateModified 2022-03-26) and PSZUpdates.pdf ('Last update: February 2022'); README 'The DINA microdata needs to be included in the repository under raw-data/dina-data/microfiles'; paper p.19 'Data will be made available upon request'; 02-add-ssa-wages.R l.25-26, 85-117; raw-data/dina-data/DINA(Aggreg).xlsx sheet Index ('Last update: 2026-02-21') and TC1 rows 2024-2025; top-0.1% wealth share 2019: 17.6% in the Aug/Nov-2022 vintages and PSZ Feb-2022 vs 19.95% in 2026 (scripts/vintage_compare.py; WID shwealj992).

Why this severity. The backtest and the 2020-2024 annual anchors cannot be reproduced from public materials, contrary to the paper's statements, and a material level revision behind a headline 'record' claim is undocumented. The core qualitative results are not shown to be wrong.

Why it matters, in detail. Under Auten-Splinter-type allocations the 2019 top-1% pretax share is ~14% rather than ~19%, and under heterogeneous-return capitalization the top-0.1% wealth share is ~3 pp lower. Changes over 2019-21 are less sensitive than levels; the RTI-DFA agreement supports wealth trends but not SZ levels.

Evidence. Paper Sec. 3.3, fn 4, Appendix B. Corpus: us-income-08, -10, -11, -12, -13 (Auten & Splinter 2024/2026), -16 (Smith, Yagan, Zidar & Zwick 2019), -17 (Kopczuk & Zwick 2020), -21 (Gale, Sabelhaus & Thorpe 2023); us-wealth-taxes-01 to -06, -10 (capitalization method; e.g. Smith, Zidar & Zwick 2023: 2016 top-0.1% wealth share 15.7% vs 18.4% in SZ20), -08 (DFA), -11 (Forbes). Adjudicator: WID post-1946 maximum of the top-1% factor share before 2021 is 19.5% (2012), so the 'highest since WWII' claim holds within the PSZ framework; RTI vs DFA top-1% wealth share change 1989-2025 +8.8 vs +9.0 pp (equal-split).

Why this severity. The high-frequency method is largely orthogonal to these level debates, but the paper's 'record' and long-run statements depend on PSZ/SZ levels whose alternatives in the literature are substantially lower and flatter.

The authors' response. Saez & Zucman (2020b, 'Trends in US income and wealth inequality: revising after the revisionists', NBER WP 27921) and PSZ comments on Auten & Splinter (2024, 2026) dispute these critiques and accept some corrections (e.g. pension rollovers); see corpus entries us-income-10 to -13.

Why it matters, in detail. Correctly accounting for the MA(1) structure of overlapping 2-year errors roughly triples the top-1% p-value (0.021 -> 0.061 unweighted, 0.041 Bartlett); B50 and M40 remain significant at 5%, N9 remains insignificant.

Evidence. 04-backtest.do l.535-559 (dm_stat = mean/(sd/sqrt(n)), t(n-1)). Recomputation from vector-digitized Figs. 4-5/A6 (scripts/backtest_stats.py) reproduces the published p-values: 1-year 0.030/0.0025/0.416/0.020; 2-year 0.0014/0.0009/0.137/0.021. With the HLN h=2 correction: 0.016/0.003/0.258/0.061 (B50/M40/N9/T1); Codex's Bartlett variant gives 0.041 for T1.

Why this severity. Only the top-1% 2-year significance becomes marginal (p 0.02 -> 0.04-0.06); point estimates and all other conclusions are unchanged.

Why it matters, in detail. Recovery lags are 7 (T1), 29 (B50) and 41 (M40) months for all adults, so the M40, not the B50, recovered last; the aggregate Covid recovery took 13 months vs 49 after the GR.

Evidence. scripts/labor_recovery_claims.py and vintage_compare.py, real factor income per adult. 'By October 2021 all groups had recovered' (Fig. 6 note): B50 recovers Jul 2022, M40 Jul 2023 (the Aug-2022 vintage had all groups back by Sep 2021). Top 1% 'one year': 7 months (Sep 2020). B50 'two years': 29 months for all adults, 24 for working-age. 'Recovered last': the middle 40% recovered last. Aggregate Covid recovery '18 months': 13 months in the working-age series that gives the 4y1m Great Recession benchmark; 18 months matches the Nov-2022 vintage. The GR benchmarks (97 months for the WA B50, -11.4% when the average recovered) and the Covid comparison (-6.3%, ~1 year from recovery) reproduce.

Why this severity. These are stale or inaccurate statements; the corrected timings make the top-vs-bottom contrast, if anything, sharper, and the GR comparison reproduces.

Why it matters, in detail. This overallocation to ineligible families above the phase-out end is redistributed away from eligible recipients by the NIPA rescaling; the simulated effect on the B50 share is about 0.2-0.3 pp.

Evidence. 03-build-monthly-microfiles.do l.673-690; IRS third-payment FAQ (updated 25 Mar 2022) and 26 USC 6428B(b),(d),(g)(2)(A) (Codex). Adjudicator simulation on the 2014 DINA file (scripts/eip_filer_sim.py): switching to the statutory phase-out changes the B50 share of the payment total by only +0.2-0.3 pp.

Why this severity. It is a real coding error, but it affects only upper-middle-income families with children, and its effect on bottom-50% results is negligible after aggregate rescaling.

Why it matters, in detail. Per-unit levels in the XLSX are understated by the group's population share (B50 x0.5, quartiles x0.25, top 1% x0.01); totals, shares and the JSON 'wage' field are correct.

Evidence. site_full-online-database.xlsx (sheet income_wealth: population = 251.5m for every group, Dec 2021); labor JSON 1976m1 Q1 pop 7.47m vs ~30m; code 03-build-website-payload.py l.147-204, 03-build-online-database-labor.do l.31, 85-92 (Codex).

Why this severity. These are data-product errors only; the paper's figures, the totals and shares, and the website charts are unaffected.

Why it matters, in detail. The splice produces an artificial ~0.7 pp drop in the WID bottom-50% factor share in 2020. It also means WID is not an independent benchmark for RTI vintages (see rejected claims).

Evidence. WID sfaincj992: B50 11.43 (2019) -> 10.21/10.28/10.38 (2020-22) = RTI May-2023 vintage 10.233/10.282/10.383; top 1% 18.97 -> 18.60/20.20/20.87 = 18.624/20.212/20.866; within that RTI vintage the B50 2019->2020 change is -0.48 pp vs -1.22 pp in WID (scripts/vintage_compare.py).

Why this severity. This concerns the authors' related WID series, not statistics in the paper; it matters for downstream users of WID.

Why it matters, in detail. Bias estimates moved by up to ~1.6 pp/yr between versions, and Covid levels by 1.6-3.1 pp of share; 'post-WWII high' claims for the top 0.1% wealth share flip with the DINA vintage.

Evidence. BSZ2022 (Nov 2022) Table 2 and pp.24, 1277 of text extraction; WIL WP 2022/14 (Jul 2022); Nov-2022 website vintage: max top-0.1% wealth share before Dec 2021 = 19.08% (Mar 2013) vs 18.76% at Dec 2021; WID shwealj992 2012 = 19.02%.

Why this severity. The published version is internally consistent on these items. The problem is that working-paper readers were given claims later contradicted, and 'record' statements are vintage-dependent.

Why it matters, in detail. Nominal OLS with a constant implies time-varying real intercepts and weights the late, high-price years more; with common inflation trends it also inflates the apparent linearity of the relation.

Evidence. 02-tabulate-qcew.do l.7-11; 02-create-monthly-wages.do l.61-78, 152-156 (Codex; confirmed by adjudicator).

Why this severity. It is a description/implementation mismatch; a nominal affine mapping is defensible, and no material bias was demonstrated.

Why it matters, in detail. Readers implementing the printed formula would miss the aggregate employment target by (1-S)(z - xbar).

Evidence. Online Appendix C.1 p.5; 03-build-monthly-microfiles.do l.123-129. Example: two equal cells at 0.8/0.6, target 0.6: printed formula gives mean 0.68, code gives 0.60 (verified algebraically by adjudicator).

Why this severity. This is a documentation error only.

Why it matters, in detail. Inconsistent statements of the baseline year and sources complicate replication but do not alter any reported statistic materially.

Evidence. The latest DINA file is given as '(2021)' (Intro p.2), '2024' (Sec. 3.3) and 'y2 = 2019' (App. C.1-C.2). The Fig. A3 note says the BLS rate is 'based on the monthly CPS', while the text and code use CES payrolls. The 'official national income deflator' is the GDP implicit price deflator (A191RD) interpolated monthly with the PCE index (02-prepare-nipa.do l.169, 427, 970-973), with an unstated base month. SCF described as 'about 6500 families' (Sec. 4.1); the 2019 SCF has 5,777. Adult population given as 248.9m in May 2022 (App. D.4), 252.6m in current data. The README figure-to-program map is stale. Sec. 6 says it 'uses our real-time estimates' although 2020-24 are now tax-anchored. Tables use sqrt(bias^2 + sample SD^2) for RMSE. The 2018 TCJA is not flagged as a tax-reform year.

Why this severity. These are presentation and documentation slips that do not change any result.

Why it matters, in detail. Excluding non-filers lowers the B50 share of EIP totals by up to ~6 pp (up to ~12% of B50 EIP receipts for all adults, ~7% for the working-age population), shifting several billion dollars per wave up the distribution. This is an upper bound, since not all eligible non-filers were paid; receipt rates were not verified here. The March-2021 peak of B50 disposable income is likely understated by up to ~$100-200/month.

Evidence. 03-build-monthly-microfiles.do l.616-690. IRS COVID Tax Tip 2020-44 ('Payments will also be automatic for those who receive Social Security ... who don't normally file a tax return'; cached /mnt/zdata/downloads/bmsz2026-rti-adjudicator/irs_eip_questions.html). In the public PSZ 2014 DINA file (Feb-2022 release) 14% of adults are non-filers, 99.8% of them in the factor-income bottom 50% (28% of B50 adults). Simulating the third payment with the code's rule (scripts/eip_filer_sim.py) gives the B50 45.7% of the total (all adults; 49.4% ages 20-64), vs 52.0% (53.3%) if non-filers are paid under the same rule.

Why this severity. The bias runs against the paper's conclusion (it understates transfers to the bottom 50%), and its size is roughly 1 pp of bottom-50% disposable income in 2021.

Why it matters, in detail. Labor income accounts for roughly half or more of the 2019-25 decline in the pretax ratio, depending on the base year (more over 2023-25, less from a 2020 base). The decomposition by component is not published, so the 'mostly capital' claim cannot be verified.

Evidence. scripts/race_claims.py (demographics export): pretax ratio 49.2 (2019), 50.2 (2020), 48.5 (2023), 46.6 (2024), 45.1% (2025); WA labor ratio 63.0, 64.4 (2023), 59.3% (2025); wealth ratio 22.7% in 2019 and 2025; 2022Q4 vs 2019Q4: White +2.0%, Black -0.1%, Hispanic -1.7%; 1989 ratio 53.5%. The levels ($56.8k vs $126.0k; 45%; labor 59%; wealth 22.7%; GR 2011Q3 -3.9%) reproduce.

Why this severity. This is an interpretive overstatement in a secondary section; the level comparisons reproduce.

Why it matters, in detail. If the tabulation-based aging of the 2014 file shares the RTI's fixed within-component structure, the recent-decade backtest partly compares a model with a model at the top. Testing this requires the authors' DINA aging code.

Evidence. Vector-digitized Figs. 4-5/A6 (scripts/backtest_stats.py): top-1% 1-year RMSE 1.88 (2015-24) vs 2.74 (1976-2014 excluding tax-reform years), against uniform-model RMSE 3.48 vs 3.44 (ratio 0.54 vs 0.80); for the B50 the ratio is unchanged (0.72 vs 0.73).

Why this severity. This is a hypothesis with suggestive but statistically weak evidence (10 years); if true it would modestly flatter recent top-1% accuracy.