Niels Johannesen, Johan Sæverud, Emmanuel Saez · American Economic Review: Insights 8(2): 247-264

Taxing the Wealth of the Poor: Evidence from the Danish Old-Age Support Asset Test

14 problems found: 3 moderate · 11 minor

What the paper claims

Among age- and income-eligible singles (65+, low income) the liquid-wealth density shows large, diffuse excess mass below the asset-test threshold relative to two ineligible control groups; the excess is the same in third-party (default) and self-reported wealth, so it is not misreporting, and it rises with age.
A cohort analysis (same 1941-45 cohorts at ages 60-64 vs 70-74) 'suggests that the program reduces liquid assets by 20 percent around the threshold'; 'our headline number'.
Reform variation supports a causal reading: there is no excess mass before the 2003 introduction, it emerges and grows afterwards, and it shifts when the threshold is raised in 2010; adjustment is sluggish.
High-frequency bank data show the excess mass exists in all months (only 'somewhat more pronounced in December'), so the reduction in liquid wealth is 'largely permanent rather than temporary'; temporary responses take the form of December cash withdrawals, not spending or debt repayment.
(Secondary) Responses are diffuse and build up gradually with age and time since introduction, interpreted as learning/frictions; reduced liquid buffers imply an insurance-efficiency trade-off of asset testing.

Every problem found

1moderateconfirmed · newly identified here · methodology

The savings limit studied in the paper governs two benefits at once: the yearly cash payment and a health subsidy for medicine, dental care and glasses. The paper credits the whole savings response to the cash payment, and the 2003 and 2010 rule changes it uses as tests also changed the health subsidy. The response is real, but how much of it is due to the cash payment alone is not known.

Technical detail and evidence

Why it matters, in detail. The notch at DKK 89,800 is the check (up to 18,000, taxable) plus the expected value of the health supplement (tax-free; about 24% of the marginal fiscal cost in the 2010 costing). Any response-per-krone reading must use the combined notch. The 2003 and 2010 contrasts identify responses to bundled changes. Exposure of pre-2003 disability pensioners in the 60-64 control would bias treated-control and cohort gaps toward zero; the controls show no bunching, so this is probably small.

Evidence. LBK 983/2019 s.72 d(2) ('...overstiger formuegraensen for tildeling af helbredstillaeg'), s.14 a, s.14 b. 2020 rates VEJ 10025/2019 Tabel 12 row 8: 'Formuegraense, helbredstillaeg og supplerende pensionsydelse 89.800'. Bill L 54 (2000/01): asset test of 50,100 kr in 2001 prices, in force 1 March 2001, with transitional protection until 1 March 2003. Bill L 50 (2002/03): extension with effect from 1 January 2003, same limit 53,100 kr. Bill L 79 (2003/04): check limit 'svarende til formuegraensen efter de gaeldende regler om helbredstillaeg'; 2003 was a one-off of up to 5,000 kr. Bill L 71 (2009/10): both limits raised 64,100 to 74,100 kr; 'Der gaelder saaledes samme formuegraense'; costing DKK 125m (check) plus 40m (health supplement, tax-free, grossed up) for about 13,000 plus 14,000 extra recipients. VEJ 53/2007 points 121-123: wealth at the time of application decides eligibility for the extended supplement. The supplement is not mentioned in any version of the paper.

Why this severity. The measured densities and quantile gaps are unaffected, and the adjudicator's bunching check finds no excess in 2001-02, when the supplement's test already applied to new applicants, so the check is plausibly the main driver. But the paper attributes the whole response to the check and presents 2003 and 2010 as clean single-programme reforms when both were bundled. This is an important undisclosed caveat on attribution, not on the existence of the response.

2moderatelikely · newly identified here · overclaiming

The 20% figure compares savings on 31 December, the day the government checks them, which is also when these pensioners' bank balances are lowest because the yearly payment arrives in January and is spent over the year. Using the paper's own monthly bank data, the reduction over the year as a whole is closer to 15-16%. The conclusion that the rule lowers savings, and that most of the reduction lasts all year, still holds.

Technical detail and evidence

Why it matters, in detail. The P66 quantile gap (-23.7k DKK) is measured at the annual trough of a saw-tooth balance path. Net of control seasonality, the treated threshold quantile is about 4.5k DKK higher on average in Feb-Nov, so the time-averaged gap at P66 is about -15% to -16% instead of -20.2% (peak about -17% at P67). The window-mass statistic used for 'permanence' is insensitive to a 4-5k horizontal shift because the window is 50k wide. 'Largely permanent' is therefore right qualitatively, but '20 percent' is an end-of-year, not a year-round, buffer reduction.

Evidence. Adjudicator digitisation of published Fig. 4A/B (scripts/fig4.py, sensitivity.py). Mass in DKK 90-130k: treated 4.45% (Dec) vs 5.85% (other months), -24%; control 5.04% vs 5.19%, -3%; DiD -1.25 pp. Horizontal shift of the December threshold quantile into other months (assuming equal mass above DKK 150k): treated +6,229 DKK, control +1,734 DKK, net +4,496 DKK. Applying this to the cohort's P66 (93,252 vs 116,915 DKK) gives a year-round effect of -16.4%. Applying the DiD December-only mass to the cohort CDF instead gives -15.4% (P65: -18.7% to -14.1%). The window excess (treated minus control, 10-bin) is 5.82 pp in December vs 5.74 pp in other months, which confirms the persistence the paper reports. Auditor A's illustrative scaling (DiD mass 1.21 pp / cohort cross-threshold shift 3.21 pp, giving about -12.6%) scales a horizontal quantile distance by a mass share and overstates the correction. Paper p.260 ('the difference is rather small'), fn 19, p.262; abstract.

Why this severity. The end-of-year number is correctly measured and labelled as end-of-year. The bank data confirm that most of the reduction (about 75-80% at the threshold percentile) persists all year. But the year-round reduction at the headline percentile, which is the welfare-relevant one, is about a fifth to a quarter smaller than -20%: a noticeable, not transformative, change in how C2 should be read. The estimate combines a 2014-16 bank sample of all low-income 65+ singles with the 1941-45 cohort, so it is approximate.

The authors' response. No published response. The paper notes the December-to-January outward shift (p.260, attributed to receipt of the check) but does not quantify the year-round gap.

3moderateplausible · newly identified here · speculative assumption

To estimate the effect, the paper compares the same people at ages 60-64 and at 70-74, assuming their savings would otherwise have looked the same ten years later. That assumption is checked only for the better-off quarter; for the poorer half, savings were 10-17% higher at 70-74, so it does not clearly hold everywhere. The true effect near the limit could plausibly be anywhere between about 15% and 25%.

Technical detail and evidence

Why it matters, in detail. Before-after quantile treatment effects require a stable counterfactual quantile function across a decade and stable selection into the income-eligible sample. Upper-tail alignment is necessary but not sufficient. Observed tail departures (+8-17% below P55; -3 to -5% above P90) and the pre-eligibility FE slope bound neither the sign nor the size of the drift in P55-P75. A defensible reading of C2 is a year-end reduction of roughly 15-25% at the threshold percentile. No standard errors, placebo cohorts or DiD versions of the quantile analysis are reported.

Evidence. Adjudicator digitisation of Fig. 3B and Fig. A.3(b)-(c) (scripts/fig3.py, figA3.py, upper_tail.py): P20 +12.2%, P25 +8.5%, P40 +16.6%, P50 +9.7%; P76-P90 mean +0.2%; P92 -3.2%, P94 -4.6%. FE coefficients relative to age 64: -0.56, -1.15, -1.38, -1.03 at ages 60-63; +2.82 at 65 (CI 2.47-3.17); +7.26 at 74. Linear pre-trend 0.125 pp/yr, i.e. 1.25 pp over 10 years, equal to 20% of the 6.27 pp FE excess. Sensitivity (Codex's construction, re-computed in scripts/sensitivity.py): effect = 0.798/(1+g) - 1. Decade drift g of -10/-6/-3/+3/+5/+10% gives P66 effects of -11.4/-15.1/-17.8/-22.6/-24.0/-27.5%. Nov-2024 NBER WP Sec. 3, Fig. 4; Table 1 (fraction low-income 0.46 at 60-64); p.258 and fn 15.

Why this severity. The evidence for a local negative effect is strong: the gap is localised at the threshold, the upper tails align (P75-P90), there is a discrete within-person jump at 65, and the cross-section and the reforms agree. But the size of the headline rests on an untested zero-drift assumption in P55-P75. Drifts of plus or minus 3-6% over a decade, within the range the authors' own tails display, move P66 to between about -15% and -25%. The direction of any bias is ambiguous: the lower tail suggests positive drift, which would make the estimate conservative, while the pre-trend and the top decile suggest negative drift.

The authors' response. No published response to these critiques. The paper validates the assumption only through upper-tail alignment (p.258; Fig. A.3(c), 'up to the 90th percentile') and explains in fn 15 why the income-ineligible are not used as a DiD control.

4minorconfirmed · newly identified here · selective presentation

The same comparison that shows lower savings near the limit also shows 10-17% higher savings among the poorer half of these pensioners. The paper mentions this only in passing. It matters for judging the programme's overall effect, not for the paper's claim about people near the limit.

Technical detail and evidence

Why it matters, in detail. Either the check raises liquid wealth in the bottom half (saving out of the transfer), in which case the programme's net effect on mean liquid wealth is close to zero (about -1% over P5-P100), or the zero-change assumption fails by 8-17% a few percentiles below the headline region. Either way, the cross-sectional window excess (C1) partly reflects mass moving up from below, not only down from above.

Evidence. scripts/fig3.py: P5-P54 ratio of quantile sums +13.0%. CDF at 44.9k falls from 49.95% to 47.87% (2.08 pp moved up from below); CDF at 89.8k rises from 62.08% to 65.29% (3.21 pp moved down from above). Paper p.248, p.251 ('the old-age check could boost wealth mechanically'), p.259.

Why this severity. The paper discloses the gaps and its reason for not reporting them, the DKK amounts are small, and the headline is explicitly local. Their main implication, for the credibility of the identifying assumption, is graded under F3. Auditor A's 'moderate' is therefore downgraded.

The authors' response. The paper says it is 'less confident about the validity of the identification assumption and the estimated effects at the very bottom, and we do not report them' (p.259).

5minorconfirmed · newly identified here · version instability

An earlier version of the paper used a different method and found an effect about half as large, though over a shorter period and when the payment was smaller. The published paper does not mention this, and some summary figures changed between versions without explanation. None of this overturns the findings.

Technical detail and evidence

Why it matters, in detail. The earlier DiD shows that with a control group the medium-run peak was about half the published headline. That is useful context for F3's design uncertainty, though not a like-for-like contradiction. If the earlier control trend (+1.6 pp) applies, the raw Fig. 2A rise (6.2 pp) overstates the programme-induced rise, but the localised bunching (+3.7 to +7.3 pp in 2006-07) shows most of it is programme-related. The +5-7% rescaling of DKK levels points to a change of deflator or sample and does not affect relative effects.

Evidence. NBER w33189 rev0 (Nov 2024) pp.2, 10-12, Figs. 3-4, fn 13, Table A.1; published pp.252-259, Table 1. Adjudicator's bunching check on the published Fig. 2A (log-polynomial counterfactual outside an excluded window; scripts/fig2.py): 2001-02 -1.7 to 0.0 pp; 2003-05 +1.6 to +3.2 pp; 2006-07 +3.7 to +7.3 pp. The emergence therefore survives a smooth-trend counterfactual.

Why this severity. The estimands differ: 1-4 years of exposure in 2006-07 to a check little more than half as large (about DKK 9,400 vs 13,100-18,000 in 2020 terms; Fig. A.1(a)), versus 5-9 years. The earlier version itself predicted larger long-run effects, so this is a legitimate design change, not a silent revision of one estimate (Codex's reading is accepted). The qualitative reform evidence survives the shape-based check. Auditor A's 'moderate' is downgraded.

The authors' response. The November 2024 version anticipated that 'the long-run treatment effects could be 4 times larger'. The published version gives no account of the change.

6minorconfirmed · newly identified here · overclaiming

In principle some pensioners could keep money as cash at home, which the data would not capture and the rules forbid. The paper's check covers only cash taken out in December, so it cannot fully rule this out. But the bank records show no sign that people near the limit take out unusual amounts during the rest of the year, so this is unlikely to explain much.

Technical detail and evidence

Why it matters, in detail. The add-back bounds only the change in cash during December. A permanent shift from deposits into unreported cash would generate year-round bank-balance bunching indistinguishable from reduced saving. The cross-section of other-month withdrawals by wealth limits ongoing conversion in 2014-16 but not a pre-2014 stock. The magnitude is unidentified.

Evidence. Paper pp.250-251, 255, 260, 262 ('We cannot tell whether the cash is spent, given to family or friends, or kept as liquid reserves outside the bank'). Heisel (2023, Danmarks Nationalbank Analysis), the paper's own source, reports that 14% of the population held more than DKK 10,000 in cash savings in 2017 (under 8% in 2023) and that older citizens prefer cash. Adjudicator check against this concern (scripts/fig4.py): in Fig. 4C the treated group's other-month withdrawals fall smoothly with wealth (2,990 DKK at 40k, 2,857 at 85k, 2,856 at 90k, about 2,500 at 110-145k), with no threshold-specific rise.

Why this severity. The paper's inference outruns its test. But the alternative requires illegally unreported cash stocks accumulated before the bank-data window, the 2014-16 withdrawal profiles show no year-round excess near the threshold, and the paper's wording is hedged. Codex's 'moderate' is downgraded because no evidence points to a material hidden-cash share.

7minorconfirmed · newly identified here · documentation gap

The month-by-month evidence comes from one bank's customers, and among them the savings response is about a third smaller than in the whole population. The finding that the response lasts all year is therefore shown for a group that reacts less than average.

Technical detail and evidence

Why it matters, in detail. If within-year dynamics differ for more responsive groups (e.g. the 80+, window mass 24.3%), the temporary share may differ in either direction. C4 should be read as evidence for a subsample with roughly two-thirds of the population's excess mass.

Evidence. scripts/fig4.py ('December (admin)' series: 18.04 treated, 12.02 control); scripts/fig1.py (Fig. 1C: 20.58, 11.57); Nov-2024 NBER fn 13; published p.252 and fn 18. Pooling 2014-16 rather than 2014-18 cannot plausibly explain a 2.6 pp gap in level.

Why this severity. The permanence result is valid within the bank sample, and its excess (6.0 pp) is close to the cohort's (5.5 pp). Extrapolating it to the full eligible population, where bunching is 50% larger, is untested. This is an undisclosed caveat with limited demonstrated impact.

8minorconfirmed · newly identified here · documentation gap

The 20% is the largest effect found at any single point. Averaged over the range around the limit, the effect is about 10%, and the abstract's wording can make the typical effect sound twice as large.

Technical detail and evidence

Why it matters, in detail. With hundreds of thousands of observations, quantile sampling error is likely a fraction of a percentage point, and max-selection bias over about 20 percentiles is small. The substantive issue is presentational: '20 percent around the threshold' versus a band average of 9.9%.

Evidence. Abstract; pp.248-249; Fig. 3B inset; Table 1 B2; p.262. The printed P55-75 figures equal the mean over integer percentiles P56-P75: -11,947 DKK exactly and -9.87% (scripts/fig3.py).

Why this severity. With administrative samples, sampling error is small and the peak's location is predicted by theory. But the abstract's wording roughly doubles the apparent typical effect near the threshold, and design uncertainty (F1, F3) is not quantified anywhere.

9minorconfirmed · newly identified here · internal inconsistency

The paper's 'share of people between half the limit and the limit' actually counts people up to about 6% above the limit. The differences between groups, which are what matter, are almost unchanged.

Technical detail and evidence

Why it matters, in detail. Including [90k, 95k) adds about 0.8-1.1 pp to every level and about 0.2-0.3 pp to treated-control gaps. No conclusion changes.

Evidence. scripts/fig1.py: 10-bin sums 20.55/19.03/20.58/11.57/11.23/16.20/18.35/20.47/24.34, matching every printed value; strict 9-bin sums 19.45/18.59/19.48/10.80/10.29. scripts/fig3.py (CDF windows); scripts/figA3.py (12.93/15.72/18.36); scripts/fig2.py (14.41/16.81/20.56). The Fig. 3A density curves are drawn a constant 0.00103 below the identical A.3(a) curves, which explains Codex's 'discrepant' cohort masses.

Why this severity. Treated-control gaps are essentially unchanged (cross-section 8.7-9.2 pp strict vs 9.0-9.4 pp printed; cohort 5.3 vs 5.5 pp). This is a definitional and documentation inconsistency.

10minorconfirmed · newly identified here · arithmetic or transcription

A few details of the benefit rules are described incorrectly, for example how much other income a pensioner can have before the payment starts to shrink. The authors' charts suggest they used the correct rules in the analysis itself.

Technical detail and evidence

Why it matters, in detail. There is no evidence the misstated disregards entered the sample definitions. The earnings deduction could misclassify some working pensioners as income-ineligible, mildly contaminating the higher-income control and biasing it toward zero; that control shows no bunching. In 2003-05 some '65+' observations were not yet pensioners, which slightly attenuates the short-run reform response.

Evidence. VEJ 10025/2019 Tabel 15 rows 6-9 and fn 1; Aeldre Sagen (2023) 'Supplerende ydelser' (35,800/71,000; full phase-out at 88,200); VEJ 53/2007 point 66 ('Folkepensionsalderen for personer foedt foer den 1. juli 1939 er 67 aar'); bill L 79 (2003/04); paper pp.248-251.

Why this severity. These are descriptive errors. Fig. A.1(c) indicates the analysis used the correct singles' threshold; the pension-age exception touches only the early reform samples.

11minorconfirmed · newly identified here · internal inconsistency

One appendix chart is labelled as showing one savings measure but actually shows another, and some details on it are slightly off. The findings are unaffected.

Technical detail and evidence

Why it matters, in detail. The mislabelled curve and offset markers affect only a supplementary illustration of the full distribution.

Evidence. scripts/figA2.py; Nov-2024 NBER WP Fig. A.2 title; published fn 11 (p.255) and Fig. A.2 notes.

Why this severity. This is an appendix presentation error with no bearing on the main analyses, which use default wealth from other figures; the two curves are close.

12minorconfirmed · newly identified here · internal inconsistency

Several small labelling and cross-referencing mistakes appear in the text and charts. None changes the results.

Technical detail and evidence

Why it matters, in detail. The reported numbers are unaffected. The ambiguous grouping variable matters for reading Fig. 4C-D: grouping by same-December wealth mechanically links withdrawals with low balances, whereas grouping by the previous December's wealth does not.

Evidence. scripts/fig1.py, fig3.py, figA3.py, fig4.py, cash_versions.py; paper pp.252, 256, 258-259, 261-262; appendix Figs. A.3-A.4.

Why this severity. These are presentation and documentation errors; correct readings are recoverable from legends and printed numbers, and none changes a result.

13minorlikely · newly identified here · overclaiming

The paper calls itself the first clear evidence that asset limits make poor households save less, but at least one earlier study it cites found a similar-sized effect with weaker data. The paper's data are better; 'first' is too strong.

Technical detail and evidence

Why it matters, in detail. Earlier survey-based evidence (SIPP; Medicaid eligibility expansions) did find quantitatively important asset-test effects. The contribution here is in measurement and identification, not in being the first to find large effects.

Evidence. Paper pp.248, 262; Gruber & Yelowitz (1999), 'Public Health Insurance and Private Savings', JPE 107(6): 1249-1274 (NBER WP 6041 abstract).

Why this severity. This is novelty framing. The paper's genuine advance (administrative wealth data for eligible and ineligible people, and a notch design) is unaffected.

14minorplausible · newly identified here · speculative assumption

The paper reads the slow build-up of the response as people gradually learning about the rule. But the payment itself also grew a lot over those years, so people may simply have been reacting to a bigger reward.

Technical detail and evidence

Why it matters, in detail. The rise in excess mass over 2003-07 coincides with a growing notch and a loosening income test, so 'sluggishness' and 'learning' are not separately identified from the incentive path. The age gradient mixes exposure, cohort and health-cost effects.

Evidence. Fig. A.1 notes; Fig. A.3(b) coefficients (scripts/figA3.py); bills L 79 (2003/04) and L 50 (2002/03); VEJ 53/2007 point 66.

Why this severity. This concerns the interpretation of secondary dynamics. The 2014-18 cross-sectional age gradient is observed at a constant check value, which partly supports learning or exposure effects. Core findings are unaffected.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

The cash-withdrawal series were revised between versions: the 'other months' baseline is 250-600 DKK higher in the published Fig. 4C than in Nov-2024 Fig. A.3(a), cutting the December excess near the threshold by about one third (80k bin: 1,560 to 914 DKK) (part of Claude I10). — Matching the curves by value rather than colour shows no revision (scripts/cash_versions.py). The Nov-2024 'Other months' curve (red dashed) equals the published 'Other months' curve (brown dash-dot) to within 53 DKK on average, and the Nov-2024 'January' curve (brown dotted) equals the published 'January' curve (red dashed) to within 55 DKK; only the colours swapped. 1,560 DKK is December minus January in the old figure; the like-for-like December excess at 80k is 1,015 DKK (Nov 2024) vs 913 DKK (published). The softer wording ('at least partly' to 'only to a small extent') is an interpretive change, not a data revision.
The statement that the bank sample is 'around 20 percent of the Danish elderly population' is contradicted by Table 1, whose counts imply about 30% (part of Claude I10). — Table 1 covers singles only (153,824 of 505,284 per year); the 20% statement refers to the whole elderly population including couples. No contradiction can be demonstrated (Codex reached the same view).
If the 2010 discretionary threshold increase was included in the normaliser ('indexed to the asset test threshold'), the threshold-normalised -20.2% would be about -8.2% on a wage-index basis (unresolved question). — The data rule out threshold indexing. In the 1941-45 cohort at ages 65-69 (2006-14, straddling 2010), the excess over age 60-64 fades at the 80k bin (+0.0019) and disappears at 85k (+0.0001). In the post-2010 cross-section (Fig. 1D) and the 70-74 cohort it extends to the 85k bin (+0.0034, +0.0031). That is the mixture pattern expected under ordinary wage indexing, the convention stated on p.252 and visible in Fig. 2 and Fig. A.1. Upper-tail alignment would also otherwise require an offsetting +15.6% real drift (scripts/figA3.py, fig1.py).
The cohort window masses printed as 12.9%/18.4% are discrepant with the plotted data (CDF 12.1%/17.4%; density-bin sums 11.9%/17.3%), an unresolved count-definition question. — This is not a data error. The Fig. 3A density curves are drawn a constant 0.00103 below the numerically identical Fig. A.3(a) curves, whose 10-bin sums are 12.93%/18.36%. The CDF over [45k, 95k) gives 13.0%/18.3%. The discrepancy is fully explained by the window definition (retained as F10) and a plotting offset (F14).
The year-round effect at P66 is 'nearer -12% than -20%' (about 39% of the cross-threshold shift is December-specific), making the December-trough issue major (Claude I1 magnitude and severity). — The scaling multiplies a horizontal quantile distance by a share of mass. Mapping the bank-data December dip into quantiles directly gives a year-round P66 effect of -16.4%, or -15.4% when the DiD December-only mass is applied to the cohort CDF (scripts/sensitivity.py). The issue is retained as F1, but at moderate severity with a correction of about 4-5 percentage points, not 8.

Audit notes

What reproduced. No microdata or code were available. The openICPSR deposit E231843V1 ('Data and Code', registered 2026-03-25) returned Cloudflare 403 to both auditors and to the adjudicator, and the underlying Statistics Denmark registers and Danske Bank data are confidential. All reproduction therefore used the vector paths embedded in the published PDF, which store the authors' plotted series; several curves (Figs. A.2, A.3(a), A.3(c)) extend beyond the visible axes. Reproduced from the plotted data: the Fig. 3B/Table 1 B2 quantile effects, including the -20.24% headline at P66; the P55-75 band (-11,947 DKK, -9.87%); every printed window mass; the reform patterns of Fig. 2; the A.3(b) FE coefficients; and the bank-data and cash-withdrawal patterns of Fig. 4. Not reproducible here: anything requiring the microdata (sample construction, income-eligibility coding, raw counts, standard errors, quantiles above about P95). New adjudicator computations: a year-round re-estimate of the P66 effect from the authors' monthly bank data (-15% to -16%); shape-based bunching checks for 2001-07 and 2010-15; a test showing wage, not threshold, indexing; a value-based cross-version comparison of the cash-withdrawal curves (no revision); proof that Fig. A.2 plots reported wealth; and a comparison of bank-sample and population bunching (6.0 vs 9.0 pp excess).

Limits of this audit. Without the replication package or the microdata, every check verifies the authors' plotted series, not their computations from the raw data. Sample construction, the income-eligibility variable (including the treatment of transfers at ages 60-64 and the earnings deduction), mortality and composition effects, and standard errors could not be examined. The year-round re-estimate in F1 combines the 2014-16 bank sample (all low-income singles 65+) with the 1941-45 cohort, and assumes equal mass above DKK 150k across months, so it is approximate (a range of -15% to -16% at P66). The health supplement's contribution to the response (F2), and the share of pre-2003 disability pensioners in the 60-64 control group, could not be quantified. Bank-data curves are clipped at DKK 25k-145k, so full within-year quantiles could not be computed. No published critique of or author reply to this paper was found: OpenAlex lists one citing work and a web search found no comment, although the OpenAlex search endpoint was rate-limited during the adjudication. The Folketing's 2009 analysis of the old-age check could not be retrieved.