Raj Chetty, Nathaniel Hendren, Patrick Kline, Emmanuel Saez, Nicholas Turner · American Economic Review: Papers & Proceedings 104(5): 141-147

Is the United States Still a Land of Opportunity? Recent Trends in Intergenerational Mobility

13 problems found: 2 major · 3 moderate · 8 minor

What the paper claims

Rank-based intergenerational income mobility is 'extremely stable' for the 1971-1993 birth cohorts: the consolidated rank-rank series is 'virtually flat', and 'children entering the labor market today have the same chances of moving up in the income distribution (relative to their parents) as children born in the 1970s'.
Other rank-based measures also show little or no trend: transition probabilities into the top quintile and the college-attendance gradient (stable, or improving slightly, for the youngest cohorts).
Income inequality rose while the copula (joint distribution of ranks) did not change, so the consequences of the 'birth lottery' are larger than in the past; the rise in the bottom-99% Gini among parents 'almost exactly matches' the CPS.
Differences in mobility across US regions are large relative to the time trends and persist across cohorts.
Combined with Lee & Solon (2009), rank-based measures of social mobility 'have remained stable over the second half of the twentieth century in the United States'.
Krueger's (2012) Great-Gatsby-curve prediction of a 20% rise in intergenerational persistence 'was not borne out'; the CHKS cross-area relation between mobility and the bottom-99% Gini implies only a 7.5% rise (0.30 -> 0.323), so stable mobility is 'less surprising'.

Every problem found

1majorconfirmed · newly identified here · speculative assumption

For children born after 1982 the paper could not yet see adult incomes. For the youngest (born 1987-93) it predicted their future mobility from whether they enrolled in college at 19, assuming the link between college and later income never changes. The headline of 'no change, and at most a tiny one' depends on that prediction: the incomes actually measured are too noisy to rule out even the 20% worsening that some had predicted.

Technical detail and evidence

Why it matters, in detail. The 23-point OLS slope (-0.00057; UB 0.00080 = 0.27%/yr) is identified largely by the smooth 11-point forecast segment (own slope -0.0021/yr). That segment's decline comes entirely from the college gradient under a fixed s2 = 0.395. With measured income only, the 1971-82 slope is +0.0024/yr (CI -0.0026 to +0.0075), and the 1971-86 upper bound is +0.0034/yr, four times the published bound and compatible with Krueger's +0.0027/yr. Conversion drift of +14% by 1993 pushes the point estimate to 0.0008, and +20% yields a significantly positive trend. The calibration of s1 on three noisy bridge cohorts alone moves the trend from -0.0017 to +0.0004. Cross-sectional CZ correlations (0.84/0.96) do not identify temporal invariance, and WP fn 9 concedes the invariance failed for the 1960-80 cohorts.

Evidence. Rebuilt from the Dataverse app_tables.xls (doi:10.7910/DVN/HM91JN; md5 a66630bc..., identical to the author-site copy): s1 = 1.11778, s2 = 0.39479. Col. 13 is reproduced to 6.9e-8. Trend -0.000573 (SE 0.000658); t(21) upper bound 0.000796 (0.265%/yr) [scripts/reproduce_trends.py -> data/reproduction_results.json]. Measured income only: SOI 1971-82 gives +0.00244/yr (SE 0.00227; 95% CI -0.00261 to +0.00750), an interval that contains Krueger's +20% over 22 cohorts (about +0.0027/yr). The 1971-86 series without the college forecasts gives +0.00061 (95% CI -0.0022 to +0.0034). The 11 forecast points alone have slope -0.00205 (SE 0.00047), driven by the college gradient falling from 0.746 (1989) to 0.692 (1993). Stress tests: a +13.7% drift in the college-to-income conversion by 1993 moves the point trend to the published bound; +20% gives +0.00143 (95% CI +0.0001 to +0.0028). Dropping one 1980-82 bridge cohort moves s1 between 1.050 and 1.175 and the trend between -0.0017 and +0.0004. The cross-CZ correlation of the 1980-82 and 1983-85 cohort slopes is 0.84 unweighted and 0.96 population-weighted (CHKS Online Data Table V); this is a cross-sectional check only. Caveats: NBER WP pp.7-8 and fn 9 (January, March and May 2014 versions); absent from AER pp.144-145.

Why this severity. The headline's precision and its extension to the 1987-93 cohorts are forecasts, not measurements. Measured income alone cannot exclude Krueger's +20%. A drift of about 14-20% in the untested conversion factor, which is small next to the failure the authors themselves note for the 1960-80 cohorts, removes the bound or makes the trend significantly positive. The qualitative finding for the observed cohorts (no large change, 1971-86) survives.

The authors' response. The AER marks the 1983-93 points as forecasts and states the constant-multiple assumption (p.145); WP fn 9 notes it should be re-evaluated with later data. In later work (Chetty, Dobbie, Goldman, Porter & Yang, 'Changing Opportunity', Nov 2025, p.12), the lead author reports a modest upward trend that was 'not detectable' in the 2014 paper and attributes this to SOI sampling error (see F2).

2majorlikely · previously known · external inconsistency

The lead author and colleagues later measured the same generations with much larger and more complete data. They found that parents' income position had in fact become slightly more predictive of their children's, by roughly 5-9%, rather than staying flat. That is far from the 'collapse' some predicted, but it lies outside the narrow range the 2014 paper said it could rule out, and the 2014 prediction for the youngest children pointed the wrong way.

Technical detail and evidence

Why it matters, in detail. In CO, the age-27 rank-rank slope rises +0.0022/yr over 1978-92 and the age-29-30 slope +0.0034/yr over 1978-89, against -0.0024/yr for the 2014 consolidated series over 1978-92. Splicing CO's measurements into the paper's method yields +0.0020 to +0.0026/yr, 2.5-3.3x the published bound, with a lower 95% limit of about +0.0007. Allowing for CO's shorter parental-income windows in 1978-84, the robust core is the full-window age-27 rise of +0.0021/yr (2.6x the bound, 1985-92), during which the 2014 forecasts fell 5.1%. The age-29-30 series is flat over its five full-window cohorts, so the target-age evidence for 1985-89 matches the forecast's flatness but not its level. Best estimate: persistence rose roughly 5-9% over 1978-92, not the at most 3.7% the bound implies; the college-based forecast's decline for 1990-93 is not borne out.

Evidence. Values were extracted from the vector paths of CO App. Fig. A.3 (PDF p.101); the plotted 2014 SOI series reproduces App. Table 1 col. 5 exactly [scripts/extract_co_figA3.py -> data/co2025_figA3_extracted.csv]. Age 27: 0.286 (1978) -> 0.313 (1992), OLS +0.00219/yr (+9.4%). Ages 29-30: 0.326 (1978) -> 0.352 (1989), +0.00343/yr (+7.9%). The 2014 consolidated series over 1978-92: -0.00244/yr. For 1980-86, the 2014 population age-26 slope changes -3.2%, against +5.3% for CO age 27 and +11.0% for CO ages 29-30. Full-parental-window cohorts only: age 27, 1985-92, +0.00208/yr (SE 0.0002; +5.0%); ages 29-30, 1985-89, -0.0002/yr (flat). From 1986 to 1992 the 2014 forecasts fall 5.1% while CO age 27 rises 3.4%. Matched on the 1978-82 overlap, the 2014 forecasts sit 0.024 (1983) to 0.045 (1985) below CO's age-29-30 values. Replacing the 1983-92 forecasts with CO values in the paper's own splice (scaled on 1980-82) gives +0.00203/yr (95% CI +0.0007 to +0.0034) using age 27, and +0.00262/yr when chained via ages 29-30 [scripts/updated_headline_variants.py]. CHKS (QJE 2014, Sec. III.B): one year of parental income instead of five lowers the slope by 6.6% (0.320 vs 0.341). CO pp.6-8, 12, fn 11; App. Fig. A.3 notes.

Why this severity. Later population data from the same lead author contradict the headline's precision: the trend is about +0.002/yr, against a published upper bound of 0.0008. They also contradict its forward-looking claim, turning 'no change' into a modest rise in persistence of roughly 5-9% over 1978-92. That is material relative to the claimed bound (3.7% over those 14 cohorts), though far short of the feared +20% and consistent with 'no plunge'.

The authors' response. CO (2025) p.12 acknowledges the 'modest upward trend' and attributes the 2014 non-detection to SOI sampling error; p.6 still describes overall mobility as 'fairly stable in recent decades (Chetty et al., 2014b)'; fn 11 says trends at ages 27 and 29-30 are similar. The sampling-error explanation does not cover the population-based 1983-93 forecasts.

3moderateconfirmed · previously known · overclaiming

The paper extends its finding back to people born around 1950. To do so it leans on an older study that said it could not rule out modest changes and that measured something slightly different. Later research is split: one careful study finds mobility fell sharply for people born in the early 1960s compared with those born around 1950, while another finds little change.

Technical detail and evidence

Why it matters, in detail. Stability of ranks follows from stable IGEs only if the ratio of child to parent log-income SDs is constant. In the paper's population data the IGE (-21%) and rank slope (-3%) diverge over just six cohorts. Lee & Solon's PSID estimates (cohorts from 1952; daughters' equality test p = 0.04) cannot exclude modest trends. Davis & Mazumder's NLS estimates (+0.11 in the family-income rank-rank slope, SE 0.03, 95% CI 0.05-0.16; 'a 43 percent increase') imply a large rise for cohorts entering the labour market around 1980. They attribute it largely to changing marriage patterns by parental income: imputing spouse income for singles leaves no change in the rank-rank slope. Meanwhile Jacome et al.'s imputed-parental-income estimates show approximately flat rank correlations from the 1940s cohorts. The defensible statement is 'no robust evidence of a trend', not 'stable'.

Evidence. AER p.146; WP p.10 and fn 12. Lee & Solon (2009), REStat 91(4): 766-772: pp.769-771, Table 1 (tests of equal year effects: sons p = 0.18, daughters p = 0.04), fn 14. App. Table 1 cols 7 and 12: IGE 0.274 -> 0.217, rank slope 0.2735 -> 0.2648. Davis & Mazumder, Chicago Fed WP 2017-05 (rev. 14 Jan 2022), abstract, Sec. 4 and Sec. 6: rank-rank 0.25 -> 0.36 (difference 0.11, SE 0.03, 95% CI 0.05-0.16), IGE 0.28 -> 0.45; with spouse income imputed for singles, no change in the rank-rank slope (Table 7 col. 3); they call Hertz and Lee-Solon 'seemingly at odds' and their own results 'easily reconciled' with the 1971-82 tax-data trends; published as REStat 108(1): 1-15 (2026). Jacome, Kuziemko & Naidu (2025), JPE 133(1): 306-354, main results and fn 25 ('Between the 1940s and 1970s birth cohorts, the IGE measure drifts upward again, while there is little change in the rank-rank correlation'). Song et al. (2020), PNAS 117(1): 251-258, p.3.

Why this severity. A secondary, Discussion-level claim. The cited evidence cannot establish it, the paper's own data undercut the IGE-to-rank bridge, and the best-powered direct estimate contradicts it. Other evidence (Jacome et al.) is closer to the authors' view, so the claim is unestablished rather than refuted. It does not affect the measured 1971-86 results.

The authors' response. WP fn 12 discusses Aaronson & Mazumder (2008) and Justman & Krush (2013) and gives methodological reasons for preferring Hertz (2007) and Lee & Solon (2009). No response to Davis & Mazumder was located; they themselves reconcile their results with the 1971-82 tax-data trends, not with the 20th-century claim.

4moderateconfirmed · newly identified here · methodology

To explain why rising inequality did not reduce mobility, the paper says its companion study predicts only a 7.5% change, but that number moves from about 1% to 11% with reasonable choices about how to weight places and how to handle a break in the Census data. The paper's own margin of error would also rule it out. The general point, that inequality rising mainly at the very top need not reduce mobility much, survives.

Technical detail and evidence

Why it matters, in detail. The predicted rise is 0.548 x DeltaG99. The unweighted 709-CZ slope collapses under population weights (0.062, HC1 SE 0.138), so the national-aggregate prediction is not robustly different from zero. DeltaG ranges over 0.042-0.067 depending on how the 1993 CPS break is treated, because the paper subtracts the household-series jump (0.021) from the family series, whose jump is 0.025, and Census attributes at most about half to methods. The G-S definition is used consistently in the regressor and the tax-data change, so the G-S vs within-bottom-99-Gini distinction is numerically harmless. The paper's own UB (0.0008) rejects the 7.5% benchmark (0.00102/yr), and the later realized rise (F2) is close to it.

Evidence. CHKS Online Data Tables V and VIII (709 CZs): coefficient 0.5484 (SE 0.038), so 0.548 x 0.046/0.334 = 7.55%. Population-weighted: 0.062 (SE 0.039; HC1 0.138), giving 0.85%. Child-weighted: 0.114, giving 1.6%. The smallest half of CZs holds 6% of the population [scripts/chks_gatsby_coefficient.py]. CHKS QJE Table V notes (unweighted, 709 CZs). Census F-4: 0.369 (1981), 0.436 (2003), 0.404 -> 0.429 (1992 -> 93); H-4: 0.433 -> 0.454; P60-191 p.2 fn 3 (reporting-limit change about one-third; with CAPI possibly over one-half; 'a real increase in inequality between 1992 and 1993'). The adjusted 1981-2003 change is 0.042 (removing F-4's own jump), 0.054-0.059 (removing the methods share only) or 0.067 (no adjustment), giving predicted rises of 6.9%, 8.9-9.6% or 11.0%. The 1981 tax-data G-S of 0.3375 reproduces from the SOI public-use file (0.337 published) [scripts/soi1981_bottom99_gini.py]; the 2003 endpoint (0.382) is not verifiable from public files. Krueger (2012) p.4: IGE '.47 to .56'; 'until today's children have grown up and completed their careers'.

Why this severity. Affects a secondary, interpretive result. The 'expected' change spans roughly 1-11% under defensible choices, and the reconciliation is internally inconsistent with the paper's bound. The qualitative point that the CZ-based relation predicts far less than Krueger's 20% survives, and the core trend estimates are untouched.

The authors' response. WP fn 13 argues that Krueger's own logic implies a rise of more than 20% for the 1971-93 cohorts, strengthening the contrast; no response to the points above was located.

5moderatelikely · newly identified here · methodology

The paper's margin of error is too small. It treats predicted values as if they were separate measurements, and the small tax samples used for the earlier cohorts were noisier than reported. Done properly, the largest increase the data can rule out roughly doubles.

Technical detail and evidence

Why it matters, in detail. Under the actual error structure, Var(b) = sum of w_eff^2 sigma^2 over the 12 SOI points, where each bridge cohort's weight is inflated by 0.061/3 through s1 and s2. With sigma = 0.027 (empirical, and matching SOI-vs-population deviations), SE(b) = 0.0011 rather than 0.00066, and the upper bound rises from 0.0008 to 0.0017/yr. With Fig. 1-implied sigmas the OLS SE would be about right, but then Fig. 1 shows a z = 2.07 rise from 1975-78 to 1979-82. Either way, 'at most 0.27 percent per year' overstates precision, and it excludes model error from the conversion assumption.

Evidence. d(trend)/d(mean SOI 1980-82) = 0.061. The SOI residual SD around a linear trend is 0.0271, against per-cohort SDs of 0.014-0.021 implied by Fig. 1's SEs (0.009/0.007/0.008 for the four-cohort groups, scaled by cohort size): chi2(10) = 30.0, p = 0.0008 (28.7, p = 0.0014, with a common sigma of 0.016). Deviations of the SOI 1978-82 estimates from CO's population age-29-30 series have SD 0.027. SOI minus the rescaled population age-26 slope in 1980-82: -0.031, +0.037, -0.006. Propagating sigma = 0.027 through s1 and s2 gives SE = 0.00109 and a t(21) upper bound of 0.00168/yr (0.56%/yr), against 0.0008 (0.27%/yr). Fig. 1: (0.313 - 0.291)/sqrt(0.008^2 + 0.007^2) = 2.07, p about 0.04. CO (2025) p.12 says the SOI sample led to 'considerable sampling error' [scripts/reproduce_trends.py].

Why this severity. Roughly doubles the stated bound (0.27% -> about 0.56% a year) without moving the point estimate. The corrected interval still excludes Krueger's +20% under the forecast assumption but no longer excludes the paper's own +7.5% benchmark.

The authors' response. CO (2025) p.12 acknowledges that the SOI-based estimates were subject to 'considerable sampling error'.

6minorconfirmed · newly identified here · internal inconsistency

Some descriptive statements do not match the paper's own tables; for example, one mobility measure it calls 'stable or falling slightly' fell by about a fifth. None of this changes the main results based on income ranks.

Technical detail and evidence

Why it matters, in detail. Inconsistencies (1)-(2) show the IGE and rank slope moving very differently within the paper's own data, which contradicts fn 2/fn 12 and matters for any inference from IGE trends to rank trends. (3)-(4) mean the 'birth lottery' statement rests on the population sample and external CPS/SOI calculations rather than on every series shown. (5) is a significant decline in persistence that the text calls 'no trend'.

Evidence. AER pp.143, 146 and fn 2; WP p.10 and fn 6; App. Tables 1 (cols 7, 12) and 6; Census F-4 averages 0.429 (1996-2000) and 0.444 (2008-12) [scripts/reproduce_trends.py].

Why this severity. Descriptive inaccuracies that do not change the rank-based estimates. Items (1)-(2) do, however, weaken the IGE-to-rank bridge used for the 20th-century claim (F4).

7minorconfirmed · newly identified here · overclaiming

The paper says the whole pattern of who moves up or down stayed the same, but it checks only a few summary numbers. Those numbers can stay fixed while, for example, the chance of staying stuck at the very bottom changes.

Technical detail and evidence

Why it matters, in detail. Rank-rank slopes and P(child Q5 | parent q) are informative summaries but do not identify the copula; stability claims should be limited to the summaries examined (and, per F2, the slope itself later moved).

Evidence. AER pp.142, 145; Fig. 1; App. Table 4. Codex's construction, M = 0.3I + 0.14*ones(5,5) and M2 = M + 0.06aa' with a = (1,-2,1,0,0), verified [scripts/appendixB_and_copula_checks.py].

Why this severity. A wording overreach in the conceptual framing. There is no evidence that the copula changed along unmeasured dimensions, beyond the change in the slope itself documented in F2.

8minorconfirmed · newly identified here · documentation gap

The college records the paper uses miss some low-income students whose tuition is fully covered by grants, so 'records for all children' overstates things. This probably shifts the level of the measure more than its trend.

Technical detail and evidence

Why it matters, in detail. Under-recording of low-income attendance raises the measured attendance gradient by a roughly constant amount, which s2 absorbs. A bias in the 2003-12 trend requires a changing non-filing share. If anything, the 2009-11 Pell expansion would have raised the measured gradient, so this cannot explain the 1990-93 decline that drives the forecast segment.

Evidence. AER p.143; WP fn 4; CFSTY (2020) Online Appendix, data section and fn 7; IRS Instructions for Forms 1098-E and 1098-T (2003, 2009, 2012), 'Exceptions'.

Why this severity. Overstates data coverage. The effect is mainly an upward level bias in the college gradient, absorbed by the scaling factor; no trend effect is demonstrated. The most obvious channel, more Pell-funded students without forms, would push the measured gradient up, not down.

The authors' response. WP fn 4 discloses missing forms for 1999-2002 and restricts to post-2003 data; Chetty, Friedman, Saez, Turner & Yagan (2020) later supplement 1098-T records with Pell records for this reason.

9minorconfirmed · newly identified here · selective presentation

The paper's example comparing children born in 1971 and 1986 mixes two different data sets. The overall conclusion, that these chances barely changed, is still fair.

Technical detail and evidence

Why it matters, in detail. Sample-level differences (about 1.4 pp in the overlap) are as large as the illustrated change; within-sample trends are small (population sample -0.046 pp/yr).

Evidence. App. Table 4 [scripts/reproduce_trends.py, 'q1q5'].

Why this severity. Illustration only; 'little or no trend' remains a fair summary of the transition probabilities in the measured cohorts.

10minorconfirmed · newly identified here · version instability

One column of an appendix table was quietly replaced between versions, and both the old and the new versions are still distributed. It does not feed into any headline number.

Technical detail and evidence

Why it matters, in detail. No headline statistic uses col. 6; App. Table 4 and cols 5, 7 and 8 are unchanged. Users of the AEA package should take the 'updated' table.

Evidence. AEA supplement zip (members dated 2014-01-30 and 2014-03-19); text extraction of both PDFs; NBER WP vintages.

Why this severity. A documentation and versioning issue for a column not used in Figs. 1-2 or in the consolidated series.

The authors' response. An updated table (updatd_app_Table_1_USE.pdf) was added to the AEA package in March 2014, without a note explaining the change.

11minorconfirmed · newly identified here · arithmetic or transcription

In a side discussion, the paper uses the wrong formula to measure how persistent the Black-white earnings gap is. The corrected figure (0.94 instead of 0.99) leaves its point unchanged.

Technical detail and evidence

Why it matters, in detail. The corrected 0.94 still indicates very slow convergence across groups, consistent with Clark's estimates and with the paper's interpretation.

Evidence. NBER WP (May 2014) App. B pp.15-16 [scripts/appendixB_and_copula_checks.py]; the BLS inputs were not independently checked.

Why this severity. An arithmetic slip in a WP-only appendix; the qualitative reply to Clark (slow between-group convergence) survives.

12minorconfirmed · newly identified here · arithmetic or transcription

A few small typos and rounding slips; none affects the conclusions.

Technical detail and evidence

Why it matters, in detail. None of the slips changes a reported statistic; the factors used in col. 13 are the unrounded ones.

Evidence. AER pp.142, 144, 145; App. Table 1 cols 4, 8 [scripts/reproduce_trends.py].

Why this severity. Presentation only; no conclusion is affected.

13minorlikely · previously known · methodology

The paper probably understates how strongly parents' income predicts their children's, because it measures income over short periods and at fairly young ages. This matters less for its main point about change over time.

Technical detail and evidence

Why it matters, in detail. Persistence levels around 0.30 are likely understated by roughly 5-15% (single-year parental income; measurement at 29-30). The trend conclusions are robust to a constant level bias, but cohort-varying lifecycle or attenuation bias (e.g. CO's 29-30/27 ratio drifting from 1.11 to 1.19) adds to the forecast uncertainty in F1.

Evidence. AER p.143; CHKS QJE Sec. III.B; App. Table 1 cols 6-7; CO App. Fig. A.3 (age 29-30/age 27 ratio 1.11-1.19); Mazumder (2016), Research in Labor Economics 43: 83-129.

Why this severity. Mainly a level bias, absorbed by the scaling factors. It matters for trends only if it varies by cohort, which the CO age-ratio drift suggests to a limited extent.

The authors' response. CHKS (2014) and WP App. Figs. 1-3 argue that rank slopes stabilise by about age 30 and change little with multi-year parental averaging; CHKS's online appendix responds to an earlier Mitnik et al. draft.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

Appendix A's 'bottom-99% Gini' (Gini minus top-1% share, G-S) is not the within-bottom-99% Gini, so the calibration mixes non-equivalent concepts; re-expressed in true G99 terms the CZ coefficient falls from 0.548 to about 0.40 (part of Codex I3). — Correct as algebra but immaterial. The CHKS regressor and the paper's tax-data change (0.337 -> 0.382) are both defined as G-S, so the prediction is internally consistent (0.548 x 0.045 gives 7.4%). The analysis sample's own parents show a G-S change of +0.042 (1980 -> 1993 cohorts), which corroborates the magnitude, and Codex itself notes that no corrected prediction follows. The real CPS-side problems (pre-tax income mislabelled 'after-tax'; the size of the 1993 break) are kept in F5.
Incomplete 1098-T coverage of fully grant-funded low-income students may have biased the 2003-12 trend in the college gradient (2009-11 Pell expansion; American Opportunity Tax Credit) (part of Claude I7). — Not supported as an explanation of the forecast's decline. More Pell-covered students without forms would lower measured low-income attendance and raise the measured gradient, the opposite of the observed fall (0.746 -> 0.692); no AOTC effect is documented. The coverage misstatement itself is kept as minor (F8).
Using 'Southeast' for the East South Central Census division is a labelling slip (part of Claude I11). — An informal regional label for the ESC states (KY, TN, MS, AL), which lie in the US Southeast; Fig. 4 and App. Table 5 name the division correctly. Not an error.
The college-based forecast 'had the wrong sign' for the same cohorts (title of Claude I2). — Partly rejected (qualified). It holds against CO's age-27 series (2014 forecasts -5.1% vs CO +3.4% over 1986-92) and over 1978-92 as a whole. It does not hold against CO's age-29-30 series, the paper's target age, which is flat across the full-parental-window cohorts of 1985-89, as is the 2014 forecast; only the level differs. Kept in qualified form in F2.
Later re-measurement shows rank persistence rising about 8-9% for the same cohorts, 2.7-4.3x the stated upper bound (magnitude in Claude I2). — Partly rejected (magnitude). CO's 1978-84 cohorts have shorter parental-income windows (2-4 years on CO's stated data years; fewer than five for 1978-80 in any case), and CHKS show that one year instead of five lowers the slope by 6.6%. CO's age-29-30 series steps up as the window lengthens and is then flat. The robust full-window rise is about +5% (age 27, 1985-92; +0.0021/yr, 2.6x the bound), so F2 uses a range of roughly 5-9%.
The Gini coefficients in App. Table 6 contradict fn 2's statement that the marginals 'expanded at roughly similar rates' (part of Claude I6). — Partly rejected (evidence). Ginis do not directly test fn 2, which concerns proportional changes in the standard deviations of log income (not reported). The inconsistency is kept in F6 on firmer evidence: the population age-26 IGE falls 21% while the rank slope falls 3% (App. Table 1 cols 7, 12).
Hypothesis: the forecast window coincides with the Great Recession (age 26 in 2009-12 for the 1983-86 cohorts; age 19 in 2009-12 for the 1990-93 cohorts), which may have distorted the age-26 and college gradients (raised as an unverified hypothesis in Claude I1). — Not graded as a finding because it was not tested. It is consistent with dips in both the 2014 age-26 series (1984-85 cohorts) and CO's age-27 series (1983 cohort) for incomes measured in 2009-11, but cohort and calendar effects cannot be separated with the published tabulations.
Stable rank summaries do not identify an unchanged copula, graded moderate (Codex I4). — Not rejected as a point, but downgraded to minor (F7): it is a wording overreach with no demonstrated empirical consequence beyond the change in the slope itself (F2).

Audit notes

What reproduced. Reproduced from the authors' posted files (Dataverse doi:10.7910/DVN/HM91JN, app_tables.xls, md5 a66630bc..., identical to the Opportunity Insights copy): scaling factors (1.1178, 0.3948); the 23-point consolidated series (maximum deviation 6.9e-8); the trend of -0.000573 (SE 0.000658) and its t(21) upper bound of 0.000796 (0.265%/yr); gender trends; transition probabilities (8.40%, 9.01%); college gradients (0.7445, 0.6922); Census-division figures; the CHKS coefficient 0.548 (709 CZs) and 7.55%; the CPS F-4 levels (0.369, 0.436); and, from the 1981 SOI public-use file, the tax-data bottom-99% G-S (0.3375 vs 0.337). Values of Chetty et al. (2025) App. Fig. A.3 were extracted from the PDF's vector paths; the plotted 2014 SOI series matches col. 5 exactly. Not reproducible: the confidential IRS cohort-level regressions and their SEs, the Fig. 1 bins, sample construction, and the 2003 SOI endpoint (0.382; the original 2003 public-use file is not openly available). The openICPSR deposit was not accessed (both auditors report an access challenge); the identical Dataverse copy was used.

Limits of this audit. The underlying IRS microdata are confidential, so cohort-level slopes, their sampling errors, Fig. 1 bins and sample construction could not be reproduced. The SOI noise estimate (sigma about 0.027) is inferred from the dispersion of published estimates and from deviations from Chetty et al. (2025). The later-evidence comparison relies on values extracted from CO's vector figure (validated against the 2014 series) and on a later sample that differs in coverage (authorized immigrants included), outcome age (27, 29-30), parental-income window (ages 13-17; 2-4 years for 1978-84 inferred from CO's stated data years, which the paper does not tabulate) and possibly parent ranking (the figure note is ambiguous); no same-sample forecast-error decomposition is possible. The 'updated headline' splices are illustrative. The published REStat version of Davis & Mazumder was not read; figures come from the January 2022 working paper and match the published abstract. Jacome et al.'s later-cohort estimates are, by their own account, less reliable than their early-cohort results. PSID, NLS and survey microdata were not re-estimated. The 2003 SOI public-use endpoint was not verified. The Great Recession hypothesis is untested.