Raj Chetty, John N. Friedman, Emmanuel Saez, Nicholas Turner, Danny Yagan · Quarterly Journal of Economics 135(3): 1567-1633

Income Segregation and Intergenerational Mobility Across Colleges in the United States

15 problems found: 1 major · 2 moderate · 12 minor

What the paper claims

Parental-income segregation across colleges is very high: elite colleges draw overwhelmingly from high-income families, and segregation is large within as well as across selectivity tiers.
Income segregation across colleges is similar to (approximately as large as) segregation across the childhood neighborhoods (ZIP codes) in which children grow up.
Within a college, children from low- and high-income families have relatively similar earnings; most of the national parent-child income gradient is accounted for by differences between colleges.
Colleges with the best earnings outcomes predominantly enroll high-income students, but some mid-tier public colleges combine high low-income access with good outcomes (high bottom-to-top 'mobility rates'); upper-tail (top-1%) mobility is concentrated at highly selective private colleges.
Income-neutral allocation conditional on SAT/ACT score, state and race would reduce segregation substantially, mainly by raising middle-class representation at selective colleges; it would barely raise low-income shares at Ivy-Plus colleges because few low-income students have high scores; a sliding-scale preference (160/128/96/64 SAT points by parent quintile), comparable to legacy preferences, would essentially equalize parental income distributions across tiers.
Assuming 80% of observational earnings differences across colleges (conditional on test scores, race and parental income) are causal, income-neutral allocation would reduce intergenerational income persistence among college students by about 15% and need-affirmative allocation by about 25%.

Every problem found

1majorlikely · previously known · speculative assumption

The 'about 25%' figure is not measured; it is simulated by assuming that 80% of the extra earnings of graduates of better colleges is caused by the colleges rather than by the kind of students they admit. Other research finds anything from almost no such effect to a large one. The simulated gain moves almost one-for-one with that assumption, and more than half of it comes from assuming that richer students who lose their places would earn less, so the true figure could easily be 10-20% rather than 25%.

Technical detail and evidence

Why it matters, in detail. Gap closure is approximately 0.33 x lambda (OA Table XVI), so the level of the headline is an input, not an estimate. lambda-hat ~ 0.85 is the slope of college FEs re-estimated with HS FE and score-sending proxies on the baseline FEs. Under positive residual selection (Altonji-Elder-Taber/Oster-type reasoning) the causal share lies below it, so it is not a lower bound. External analogues span ~0.24 (Mountjoy-Hickman, Texas publics, mean earnings VA) to ~0.82 (Chetty-Deming-Friedman, Ivy-Plus vs flagships, top-1% outcome). lambda is estimated on mean-rank FEs but applied to the whole earnings distribution through an 80/20 mixture. The 22.0 -> 16.2 pp narrowing decomposes into +2.6 pp for Q1 and -3.2 pp for Q5; with no losses for displaced students, closure is ~12% (lambda = 0.8) or ~15% (lambda = 1). Plausible range ~8-33%; central alternatives ~12-21% (lambda = 0.5: 16.7%; Table XVII heterogeneity: 21.3%) vs the reported ~25-27%. Population-wide the top-quintile gap falls ~12%.

Evidence. OA Table XVI (160-point column): gap closure 33.1/29.8/26.5/23.2/20.0/16.7/13.4/10.1/6.9/3.6/0.3% for causal shares 100...0%. Table VII p.1625: 1.003, 0.907, 0.903, 0.857, 0.850, 0.850; p.1626: 'lambda >= 0.85, with a lower bound on the 95% confidence interval of around 0.82'; Intro p.1574: 'at least 80%' and 'high-school GPA' (adjudicator text search: GPA occurs nowhere else except fn 40 on Hoxby-Avery). Fn 55 p.1626 and p.1629: Zimmerman comparison asserted, no numbers in the paper or the Online Appendix. Table VIII p.1627: top-quintile rates Q1 18.2% -> 20.8%, Q5 40.2% -> 37.0%; gap 22.0 -> 16.2 pp = +2.6 pp gains (45%) and -3.2 pp losses (55%); closure without losses 11.8%; college-goers' top-quintile share 29.52% -> 29.45%; population gap (MRC Table 6 attendance weights) 28.1 -> 24.7 pp (-11.9%) (scripts/repro_secondary.py; the decomposition and scaling agree with Auditor A). Mountjoy & Hickman (2021, NBER WP 29276) fn 50, p.42: the paper's specification 'involves features we flag in Section 4.3.4 as liable to under-correct for selection bias'; p.41: correlation of raw mobility statistics with VA for disadvantaged students 'roughly zero'. Slope of their portfolio-controlled VA on 'typical controls' VA across 28 Texas publics (OA Table B.2) = 0.24-0.25 (Auditor A's script, re-run by the adjudicator; portfolio-VA standard errors ~$500-1,700, so the slope is imprecise). Chetty, Deming & Friedman (NBER WP 31492, rev. Aug 2025; QJE 141(1): 51-145) Sec. 4.4: slope 0.82 of portfolio-controlled on observational VA for Ivy-Plus/flagships, Texas the exception (fn 36); Sec. 4.5: effects on top-quartile and mean-rank outcomes 'much smaller'. Black, Denning & Rothstein (2023, AEJ: Applied 15(1): 26-67; NBER WP 26821 abstract): students losing access 'do not see declines in overall college enrollment, graduation, or earnings'. Dale & Krueger (NBER WP 17159, Table 3): 0.076 -> -0.001 with application controls; the paper's own replication 0.016 -> 0.012 (OA Table XV).

Why this severity. The ~25% is one of the abstract's headline results and is set almost one-for-one by an unvalidated parameter. Within the range the paper itself treats as defensible (lambda = 0.5-1) it runs from 17% to 33%, and Texas-type causal shares or no losses for displaced students would roughly halve it or more. The direction survives if colleges have any causal effect and the authors flag the assumption as strong, so this is major rather than critical.

The authors' response. Abstract: 'a strong assumption, but one consistent with prior work'; p.1574: magnitudes 'must of course be interpreted with caution'; a full 0-100% grid (OA Table XVI) and a heterogeneous scenario giving 21.3% (OA Table XVII; fn 57). In later work, two of the authors (Chetty, Deming & Friedman, NBER WP 31492 rev. 2025; QJE 141(1): 51-145) report that observational estimates conditional on test scores and parent income closely match quasi-experimental ones for Ivy-Plus vs flagship and UC/CSU colleges, and call Texas 'unique' (fn 36).

2moderateconfirmed · newly identified here · overclaiming

The paper says colleges are about as divided by family income as neighborhoods. That holds only if all young people who do not go to college are counted as attending one huge imaginary 'college' together. Among actual college students, colleges mix rich and poor considerably more than the neighborhoods those students grew up in, even though elite colleges remain extremely skewed toward the rich.

Technical detail and evidence

Why it matters, in detail. Whole-cohort exposure indices mix the extensive margin (attendance gradient 38% -> 88%) with sorting across institutions. Under the pooled convention, bottom-quintile children's 11.8% top-quintile peer share is a ~62/38 mixture of the nationwide non-goer pool (6.4% top quintile) and college exposure among goers (22.5%). Restricting to goers and normalizing by group share, eta2 = 0.056 (Q1) and 0.116 (Q5) in colleges vs 0.094 and 0.195 in the same students' childhood ZIPs. Raw exposure among goers points the same way for low-income students (22.5% vs 13.7% top-quintile peers); top-quintile goers have slightly more own-group peers in college (38.8% vs 35.6%).

Evidence. p.1589; Figure II notes ('pooling non-college-goers into a single group'); OA Table V (ZIP codes: bottom-quintile own-group share 29.7%, bottom->top 11.5%, top-quintile own-group 34.5%; colleges incl. pooled non-goers: 26.8%, 11.8%, 33.3%); OA Table VII (college-goers' ZIPs: 27.5%, 13.7%, 35.6%; colleges among goers: 15.7%, 22.5%, 38.8%). Adjudicator (scripts/repro_secondary.py), eta2 = (own-group share - population share)/(1 - population share): ZIP, all children 0.121 (Q1) / 0.181 (Q5); colleges with the non-goer pool 0.085 / 0.166; college-goers' own ZIPs 0.094 / 0.195; colleges among goers 0.056 / 0.116. Ratios 0.60 / 0.59 vs the same students' ZIPs, 0.46 / 0.64 vs all-children ZIPs (the latter as Auditor A found). MRC Table 6: 61.6% of bottom-quintile children not in college at 19-22; the non-goer pool is 38.2% of the cohort, 32.3% bottom-quintile and 6.4% top-quintile. The 2017 WP instead compared a national college Theil index among goers (0.075) with the median within-CZ tract index (0.084) (WP p.16; reproduced by Auditor A).

Why this severity. It qualifies one of the two empirical results the Conclusion highlights. Read as a statement about college students, the comparison does not hold (about 0.6x neighborhood segregation on a normalized index). The 'very high' segregation facts (Ivy-Plus composition, 77x) are untouched.

The authors' response. The convention is stated (p.1589; Figure II notes) and the college-goer statistics are reported (p.1591; OA Table VII), with the explanation that low-income college-goers have more high-income peers in college because attendance rises with income; the comparison is framed as the age-20 environment of the whole cohort.

3moderateconfirmed · newly identified here · overclaiming

About a quarter of college students never took the SAT or ACT, so the authors filled in plausible scores for them, and the check they offer is weaker than the paper says. The headline fact that few poor students have top scores does not depend on it, but the simulations of alternative admissions do use these filled-in scores.

Technical detail and evidence

Why it matters, in detail. Nearest-earnings donor imputation within parent-quintile x state x tier cells embeds observed tier sorting and own outcomes in the imputed score. Missing-not-at-random selection of non-takers relative to takers cannot be tested with masked takers, and demeaned within-cell QQ plots cannot detect level errors. Imputed scores are ~15% over-dispersed within cells. Impact on C5's 3.7% is bracketed by the no-imputation 3.1% and NPSAS 4.0%. Impact on the 63.9% 'unexplained' segregation share and on C6 is unquantified, with plausible direction toward overstating low-income students' counterfactual gains.

Evidence. p.1610-1611; OA Figure VI notes (slope 1.15, constant 0.20; 1.12-1.20 by parent quintile; 1.14-1.23 selective/unselective). Adjudicator fit of appx_paper_fig_6.dta (scripts/imputation_validation_check.py): slope 1.148, intercept 0.20, mean |imputed - actual| 16.1 SAT points, max 38.6; 5th ventile -269 vs -230, 95th +273 vs +245 (as Auditor B found). Robustness the paper does provide: bottom-quintile share of >=1300 scorers 3.7% (all), 3.1% excluding imputed scores (OA Table X), 4.0% in NPSAS (OA Table XI); the lambda regressions exclude imputed scores (fn 51).

Why this severity. The headline scarcity statistic is robust to dropping imputed students, but imputed students take part in every counterfactual allocation. If non-takers' latent scores are below those of comparable takers, the imputation overstates low-income non-takers' qualifications and the simulated gains. That is a robustness concern with undemonstrated, probably second-order (relative to F1) impact.

The authors' response. The imputation assumption is stated (p.1610). The appendix reports the validation procedure and slopes, and the no-imputation and NPSAS checks give similar scarcity results (OA Tables X-XI). The lambda regressions exclude imputed scores (fn 51).

4minorconfirmed · previously known · selective presentation

Some colleges look like 'mobility engines' partly because they sit in very unequal places such as New York, Los Angeles and the Texas border, with many poor families and some very high wages. The authors' own adjusted measure mostly corrects for this, and the colleges they highlight stay near the top, but the exact 'top 10' order should not be over-read.

Technical detail and evidence

Why it matters, in detail. Against national thresholds, mobility rates load on local inequality through access (many poor families nearby) and success (high top-end local wages). Local norming of access removes most of this (r 0.54 -> 0.22); cost-of-living deflation alone does not (0.50). Top-10 identity is fragile because adjacent ranks differ by less than sampling error, but membership of the top ~2% is stable.

Evidence. Adjudicator, scripts/location_checks.py (CHKS 2014 Online Data Table VIII Gini; MRC Tables 2, 4, 14, 15): corr with CZ Gini raw +0.535, normed +0.215, cost-of-living-adjusted +0.500; between-CZ variance share 0.44 (dof-corrected) / 0.57 (plain). Ranks normed/COL: Cal State LA #2/#13; Pace #4/#3; Stony Brook #3/#4; UT-Pan American #11/#1; CUNY #6/#17; Glendale #18/#31; South Texas #318/#2; Cal Poly Pomona #13/#16; UTEP #26/#10; St. John's #7/#7. Paper: p.1605, fn 33-34; OA App. H p.15; OA Table XX. Hoxby & Turner (2019, NBER WP 25479): the measure 'penalizes universities that face relatively equal income distributions ... and rewards universities that face very unequal income distributions'. Delisle & Christensen (AEI, June 2020, 'Economic Mobility Conundrums'): state-level correlation 0.57 between Gini and mean college mobility rate; New York, California and Texas hold 75% of high-mobility colleges vs 23% of institutions. SEs: Auditor A's binomial approximation (table4_sampling_se.py), not re-run.

Why this severity. It affects how a secondary exhibit (Table IV) is read and which colleges top it, not the descriptive claim that some mid-tier publics combine high access with good outcomes. The authors already publish normed and cost-of-living-adjusted versions that absorb most of the location channel; downgraded from Auditor A's 'moderate'.

The authors' response. Normed and cost-of-living-adjusted measures are released and discussed (p.1605, fn 33-34; OA App. H; OA Table XX). The paper says norming is 'open to debate', reports the 0.26 correlation with CZ income, and stresses that mobility rates mix selection and causal effects (p.1600).

5minorconfirmed · newly identified here · misrepresentation of source

An appendix claims the paper's numbers agree closely with a well-known earlier study. They are statistically compatible but not as close as stated, and the earlier study found that most of the payoff to selective colleges disappears once you account for where students applied.

Technical detail and evidence

Why it matters, in detail. Prior application-control evidence implies near-complete attenuation of the selectivity coefficient, whereas the paper's data show 25% attenuation. The 'within one SE' framing understates that tension, which bears on whether lambda ~ 0.8 is 'consistent with prior work'.

Evidence. OA App. K pp.17-18; OA Table XV: 0.016 (0.002), 0.012 (0.003). Dale & Krueger, NBER WP 17159 (2011), Table 3: cols 1-2 0.076 (.008), -0.001 (.012); cols 11-12 (SSA earnings, minimum-wage threshold $13,822) 0.061 (.007), -0.023 (.012). JHR (2014) table numbering not verified (published PDF unavailable).

Why this severity. A misstatement in an appendix reconciliation; it matters only because it is offered as support for the 80% causal share (F1).

The authors' response. Fn 54 acknowledges that 'our findings differ' from Dale & Krueger and attributes this to more precise parental-income controls and the stronger predictive power of test scores today.

6minorconfirmed · newly identified here · internal inconsistency

One sentence in the introduction slightly exaggerates how much of the rich-poor earnings gap is explained by which college people attend. The detailed tables give the right numbers and the main point stands.

Technical detail and evidence

Why it matters, in detail. Between-college share of the national rank-rank gradient: 52% (college FE, full population) vs 62% implied by the intro, and 65% among college-goers.

Evidence. p.1570; Table III pp.1597-1598; paper_fig_3a.dta (adjudicator, scripts/repro_secondary.py): college-FE series slope 0.137, p100-p1 gap 12.0; college x SAT series slope 0.123, gap 10.9 (consistent with Auditors A and B).

Why this severity. Mislabeled summary prose. The body and Table III are correct and the qualitative conclusion (the gradient is much flatter within colleges) holds on every definition; downgraded from Auditor B's moderate.

7minorconfirmed · newly identified here · arithmetic or transcription

A coding slip makes one appendix number say about 1% of low-income college students reach the top 1% of earners, when the right figure is about 0.6%. Nothing else in the paper depends on it.

Technical detail and evidence

Why it matters, in detail. The low-income-weighted mean of colleges' unconditional top-1% shares is ~1.6x the mean of P(top 1% | Q1, college). Joint mobility rates are unaffected.

Evidence. paper_tab_1.do:128 and app_paper_tab_3.do:124 ('egen kp99_cond_parq1_mean = wtmean(k_top1pc), weight(count * par_q1)'). Adjudicator recomputation from MRC Table 2 (scripts/repro_core.py): as coded 1.003%/0.924%, correct 0.615%/0.563% (= joint/access). WP 2017 appendix Table III (text line 2736): 1.00/0.92.

Why this severity. An appendix summary statistic that no result in the paper uses; Table II (0.59) and the Table IV rankings use the correct variable. Downgraded from Auditor B's moderate.

8minorconfirmed · newly identified here · data error

A college-size variable described as counting undergraduates actually also counts graduate students. This changes some secondary correlations but none of the paper's conclusions.

Technical detail and evidence

Why it matters, in detail. Graduate enrollment loads on research universities with high upper-tail outcomes, inflating enrollment-outcome correlations by up to ~2x (0.24 vs 0.13 for upper-tail MR).

Evidence. Adjudicator (scripts/ipeds_enrollment_check.py, raw NCES EF2000A + HD2013): 2,192 of 2,192 matched values equal line 29 (grand total); 1,266 (57.8%) equal lines 8+22 (undergraduates). UC Berkeley 31,277 vs 22,678 undergraduates; Stony Brook 19,924 vs 13,257; Cal State LA 19,593 vs 13,476. Correlations on the matched sample (n = 2,005; scripts/enrollment_corr_impact.py), total -> undergraduate: access -0.18 -> -0.11; Q1 top-20% rate +0.40 -> +0.27; mobility rate +0.17 -> +0.14; Q1 top-1% rate +0.23 -> +0.12; upper-tail MR +0.24 -> +0.13. Auditor B found the same on 2,094 colleges.

Why this severity. A mislabeled covariate in a secondary correlational table: magnitudes change but signs do not, and neither does the table's message that observables predict upper-tail far better than bottom-to-top mobility. Downgraded from Auditor B's moderate.

9minorconfirmed · newly identified here · misrepresentation of source

The paper describes a rival study's method as cruder than it really was; the paper's own estimate does not depend on this description.

Technical detail and evidence

Why it matters, in detail. Geography-heavy prediction can overstate low-income high achievers if income and scores are positively correlated within areas, as the paper argues. But the estimator is multivariate and conservatively thresholded, and the paper's two proposed reasons are not quantified.

Evidence. QJE p.1613 (and fn 6 p.1572); Hoxby & Avery (2013), Brookings Papers on Economic Activity, Spring 2013, pp.11-13.

Why this severity. A mischaracterized competing method in a literature reconciliation. C5's own estimate (3.7%; 3.1% and 4.0% in robustness checks) does not depend on it.

10minorconfirmed · newly identified here · arithmetic or transcription

A small coding inconsistency slightly understates a few correlations in one table; no conclusion changes.

Technical detail and evidence

Why it matters, in detail. The factor SD_pair/SD_all < 1 understates the affected correlations by ~10-20%.

Evidence. paper_tab_5.do (mobility x panel a branch: 'su ... [aw=...]' without the pairwise 'if' condition). Adjudicator (scripts/repro_core.py): faculty salary r = 0.229 vs code 0.205; graduation 0.069 vs 0.062; endowment 0.020 vs 0.016; enrollment and STEM unaffected (as Auditors A and B found).

Why this severity. Second-decimal changes in a secondary table; no conclusion changes.

11minorconfirmed · newly identified here · internal inconsistency

Two tables give different figures for for-profit colleges, apparently because they use slightly different samples; this does not affect the main results.

Technical detail and evidence

Why it matters, in detail. Probably a different sample or for-profit tier coding in the counterfactual microdata; immaterial to aggregate results.

Evidence. Table II p.1584 (= MRC Table 6; reproduced: 4-year for-profit 126,025 of 5,708,899 students = 2.2%) vs Table VI pp.1618-1619.

Why this severity. Concerns the for-profit tiers (about 2-3% of college-goers) and does not affect any headline counterfactual.

12minorconfirmed · newly identified here · internal inconsistency

The text says the colleges where the largest share of students rise from poor families to the top 1% of earners tend to be small, but the paper's own table shows they tend to be larger.

Technical detail and evidence

Why it matters, in detail. Sign error in prose: the enrollment-weighted r(enrollment, upper-tail MR) is positive under either enrollment definition.

Evidence. QJE p.1607 vs Table V Panel B p.1608; 2017 WP section on upper-tail mobility ('Colleges that have higher mobility rates tend to be smaller...') and its Table VIb (Enrollment 0.23); adjudicator recomputation +0.24 (total) / +0.13 (undergraduate) (scripts/enrollment_corr_impact.py).

Why this severity. A verbal mis-summary of a secondary table; the rest of the characterization (endowments, completion, STEM, spending) matches it.

13minorconfirmed · newly identified here · documentation gap

A few tables and claims cannot be fully checked from the released files, mostly because of missing code or data or inconsistent descriptions.

Technical detail and evidence

Why it matters, in detail. Public-data reproducibility is otherwise very high. The gaps concern one covariate row, one appendix table's data vintage, stale notes, and a validation claim (Zimmerman) whose numbers are never shown.

Evidence. paper_tab_5.do covariate list; MRC Table 10 has no CZ income variable; adjudicator ranking from MRC Table 4 (UT-Pan American 9.45, South Texas 9.27, Pace 9.26, Stony Brook 8.68, UT Brownsville 7.78, NJIT 7.69, St. John's 7.44 vs OA Table XX 9.6/9.5/9.3/8.7/7.9/7.7/7.4); Table II notes p.1584; p.1592; OA Table VII notes; MRC Table 14 codebook (lines 3-6).

Why this severity. These gaps limit verification of a few secondary exhibits; no result changes.

14minorconfirmed · newly identified here · internal inconsistency

A number of small typos and wrong cross-references; none changes what the paper finds.

Technical detail and evidence

Why it matters, in detail. None affects an estimate or a conclusion.

Evidence. Page references as listed; MRC Tables 2, 9 and 10 (scripts/repro_core.py, scripts/small_number_checks.py: flagship 5.18/33.41 vs 5.46/35.32; 6.8%; parent p99 1980/81/82 = $512,000/$531,900/$552,900, mean $532,267); 2017 WP text lines 58 and 1131-1133.

Why this severity. Presentation slips; each underlying number is reported correctly elsewhere in the paper or data.

15minorplausible · newly identified here · documentation gap

The paper says it converted ACT scores with a table built for the newer SAT, which scores roughly 50-80 points higher than the older SAT the other students took. If that was really done, some students' scores were overstated. This probably changes the main results little, but it should be clarified.

Technical detail and evidence

Why it matters, in detail. A literal implementation shifts ACT-only takers up ~45-85 points relative to old-scale SAT-takers. Within state x race cells dominated by one test the shift is near-uniform and allocation-neutral. In mixed states it advantages ACT-only takers in the counterfactual ranking, and the lambda regressions absorb the level shift through test-type dummies. A rough adjudicator illustration suggests the bottom-quintile share of >=1300 scorers (3.7%) would move by no more than a few tenths of a point, direction unknown.

Evidence. OA App. E p.11 and appendix references (Summit 2016: https://mytutor.com/wp-content/uploads/2018/06/sat-act-concordance-chart-2016-v-2018-rev.pdf; Internet Archive capture of 2022-01-20 in the shared cache). Chart '2016 ACT' column: ACT 22 -> 1100-1120, 28 -> 1310-1340, 30 -> 1390-1410, 32 -> 1450-1480. Dorans (1999), College Board Research Report 99-1, Table A.1 (ACT -> recentered SAT I V+M): 22 -> 1030, 28 -> 1260, 30 -> 1340, 32 -> 1420. Adjudicator midpoint comparison: +80, +65, +60, +45 points. Identical wording in WP 26748 (Feb/June 2020) and the author QJE manuscript. Raised by Auditor B (scripts/concordance_check.py).

Why this severity. The scale inconsistency in the documentation is confirmed, but whether the confidential implementation used it is unknown. Even if it did, within-state allocation and test-type controls make large effects on the segregation and mobility counterfactuals unlikely; downgraded from Auditor B's moderate/likely.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

The colleges highlighted as high-mobility examples (CUNY, Cal State and UT campuses) 'do not survive robustly' the authors' own cost-of-living and norming adjustments (Auditor A, I3). — Overstated. Under both adjustments, 9 of the 10 Table IV colleges remain within the top 31 of 1,394 colleges with >=300 students: CUNY #6/#17, Cal State LA #2/#13, Cal Poly Pomona #13/#16, UT-Pan American #11/#1, UTEP #26/#10. Only South Texas College falls far (#318 normed). Exact top-10 membership is what is fragile; the issue is retained at minor severity as F4.
Mountjoy & Hickman's Texas lambda-analogue (~0.24, implying a ~8% effect) is the relevant external benchmark for the national causal share (Auditor A, I1 magnitude). — Reproduced (0.24-0.25) but rejected as a central estimate. It is an unweighted, imprecise analogue for 28 Texas public universities (portfolio-VA SEs ~$500-1,700). The same matriculation design applied by Chetty, Deming & Friedman (NBER WP 31492 rev. 2025, Fig. 12, fn 36) gives a slope of 0.82 for Ivy-Plus vs flagships and strong relationships for UC/CSU, with Texas the exception. It is kept only as the low end of F1's range.
Shared sampling noise in the two college fixed-effect vectors mechanically pulls the lambda slope toward 1. — Not demonstrated. With child-count weights over ~2,000 colleges and large cells the effect is likely negligible (Auditor A itself called it slight); it plays no role in grading F1.
Lifecycle and attenuation biases (Mazumder 2016; Mitnik et al. 2015; corpus optimal-tax-behavior-22/23) as problems for this paper's estimates. — Examined by both auditors and the adjudicator; they do not undermine the results. Child ranks at 32-34 are stable to age 36 (college-level r = 0.990 at 32; Ivy-Plus mean rank 78.7 -> 79.2; appx_paper_fig_2acd/2b.dta). The findings are rank-based between- and within-college comparisons, not the national IGE level those critiques target. Auditor A's back-of-envelope bound (not re-run) suggests parental-income measurement error could raise the Ivy-Plus within/national slope ratio only from ~0.30 to ~0.33. Recorded as a scope limitation, not an issue.
Davis & Mazumder (2026, REStat) on declining mobility (corpus optimal-tax-behavior-24) bears on this paper. — Not applicable. The QJE paper makes no claims about trends across cohorts; the 2017 WP's 2000-2011 access trends were dropped, and Auditor A reproduced them from public data, so dropping them reflects editing, not fragility.
Pineda & Drummond (2018, Journal of College Access) as a critique of the paper. — It critiques a third-party report's interpretation of the Mobility Report Cards (debt, majors, nontraditional students), not the paper's estimates; as Auditor B concluded, no issue for the stated estimands.

Audit notes

What reproduced. Reproduced independently from the public Mobility Report Card tables (adjudicator scripts in final/scripts, logs in final/output). These include: Table II tier shares and the 77x ratio (77.35); attendance gradient; Section IV correlations (0.780/0.703/-0.499) and mobility-rate distribution; Ivy-Plus means; all 20 Table IV entries; normed and cost-of-living top-10 retention (5 and 6 of 10); within-tier variance shares (66.4% vs 66.8%; 97.9% vs 98.4%); the national rank-rank slope (0.288); and the Table VIII / Figure VI-C arithmetic (14.6%, 26.5%). Primary-source checks against raw IPEDS (coverage r = 0.991; enrollment definition) and against the cited ACT/SAT concordances (Summit 2016 chart vs Dorans 1999) were run. Not reproducible because they require confidential IRS/NSLDS/College Board/ACT microdata: Table III regressions, Table VII (lambda), the score imputation, and all counterfactual allocations including the continuous rank-correlation '25%'. For these only internal arithmetic, the released figure data and the published sensitivity grids were checked. Discrepancies: OA Table III row (F8), Table V standardization (F11), enrollment definition (F9), OA Table XX data vintage (F14), Table VI vs Table II for-profit rows (F12), and several text/number slips (F7, F13, F15).

Limits of this audit. No access to the confidential IRS, NSLDS, College Board and ACT microdata, so Table III, Tables VI-VIII, Table VII's lambda, the imputation and all counterfactuals were checked only for internal consistency and against published sensitivity grids. Public college-level statistics are blurred model predictions (OA App. F); reproductions match the public outputs, not exact confidential values. Chetty-Deming-Friedman and Mountjoy-Hickman were read in their NBER versions (rev. Aug 2025; Sept 2021), not the QJE 141(1) published text. Black-Denning-Rothstein was read only via the NBER abstract, and Dale & Krueger (2014, JHR) only via NBER WP 17159, so JHR table numbering is unverified. Zimmerman (2014) was not re-analysed. The ACT-conversion implementation cannot be verified. The CZ-Gini analysis uses CHKS (2014) CZ Ginis rather than contemporaneous measures. Some supporting items (Theil indices, 2017 WP trend reproductions, Table IV sampling SEs, the attenuation bound) rely on Auditor A's computations, as noted. The search for direct critiques was limited (one web search plus the auditors' searches), so others may exist.