Migration and Wage Effects of Taxing Top Earners: Evidence from the Foreigners' Tax Scheme in Denmark

Why it matters, in detail. Identification in the threshold design requires that counts of foreigners above, and at 80-99% of, a threshold indexed to average earnings would have trended in parallel; a thickening of the top of the earnings distribution after 1991 biases it upward, and the percentile design, which fixes each group's position in the natives' distribution, is the paper's own test. That test gives log effects of 0.37-0.46 (vs 0.66), elasticities 30-43% lower, and an effect that erodes after 1999 instead of 'remaining stable'. The two designs use somewhat different treated and control populations, but Figure IV shows no disproportionate response in the band the percentile design omits, so composition alone is unlikely to close the gap. A defensible reading of the paper's own evidence is a long-run ITT stock elasticity of roughly 1.0-1.6 rather than 1.6, and a 1/(1+e) revenue-maximizing scheme rate of roughly 38-50% rather than 33-40% (B1 alone implies 44-50%).

Evidence. QJE p. 336, p. 361, Table II p. 358. Online Figure A2 (PDF p. 52), recovered from the PDF vector paths (scripts/figA2_extract.py): foreigner share above P99.5 = 3.39% (1980-90 mean) -> 7.51% (2005); DiD of log shares, 1995-2005 vs 1980-90 = 0.371 against control P95-97 (x1.45) and 0.457 against P97-99 (x1.58); year by year against the geometric mean of the two controls: 1.72 (1995), 1.61 (1999), 1.47 (2000), 1.33 (2003), 1.32 (2005). Figure III by contrast (scripts/fig3_did.py): x1.92-1.96 (1992-2005), x2.0 (1995-2005), T/C 1.94-2.14 in 1997-2005. Figure IV recovered (scripts/fig4_density.py): post/pre density ratio 2.47 (1.00-1.05 of threshold, bunching), 2.06 (1.05-1.20), 2.08 (1.20-1.50), 1.69 (1.50-1.81), so the band between the threshold and P99.5 omitted by the percentile design did not respond disproportionately. The authors' industry split of the scheme (Kleven, Landais & Saez 2013 AER Fig. 4, reproduced in Kleven, Landais, Munoz & Stantcheva 2020 JEP Fig. 4, p. 130; scripts/klms_fig4.py) gives T/C outside sports/entertainment of 1.99 (1995), 1.75 (2000), 1.59 (2005), DiD 0.575, and KLMS (p. 129) state the number of foreigners 'increased by a factor of less than two in other industries'; those panels are, however, built differently (non-sports treatment x3.41 and control x2.15 by 2005 vs x3.17 and x1.62 for Figure III), so they are weak corroboration only. At the first stage implied by Table II col. (1) (0.407), the long-run stock elasticity is 1.63 in the Figure III design and 0.91-1.12 in the percentile design.

Why this severity. The 1.5-2 range is the upper part of the paper's own estimates: under its own fanning-out-robust design the intent-to-treat elasticities are 1.0-1.26 and the long-run relative increase is about x1.5 rather than x2, a magnitude 25-40% lower. The qualitative result (an elasticity of about one or more, far above within-country earnings responses) is not affected.

The authors' response. None published. In the paper, B1 is described as 'slightly attenuated ... but remain very large around 1.2' (p. 361), and fn. 12 invokes 'the great stability of the earnings distribution in Denmark'.

Why it matters, in detail. Using Figure A2's control percentiles (P95-97, P97-99) and a log-linear DiD, the 2004-05 counterfactual is 5.1-6.0%, so the scheme raised the foreign share of the top 0.5% by about 1.5-2.5 pp (a x1.25-1.5 effect). The 4% figure implicitly imports the threshold design's x1.9 effect into a series whose own controls show about x1.5, contradicting the paper's direct evidence on that share.

Evidence. Recovered Figure A2 (scripts/figA2_extract.py): actual 7.63% (2004) and 7.51% (2005); 1980-90 mean 3.39%. Proportional counterfactual (pre-level x control growth, geometric pre-means): 5.14-5.71% (2004) and 5.35-6.02% (2005), i.e. an effect of +1.5 to +2.5 percentage points (x1.25-1.49), not +3.5 pp (x1.88). Additive counterfactual: 4.39-4.66%, i.e. +2.9 to +3.2 pp. Both auditors obtained the same ranges independently (A: 5.25-5.86%; B: 5.31-6.02%, additive 4.51-4.66%).

Why this severity. A prominent introductory statistic overstates the scheme's effect on the top-0.5% foreigner share by about 40-130% in percentage-point terms under the paper's log difference-in-differences logic (10-25% under additive trends); the regression estimates are not affected.

Why it matters, in detail. The Heckman model finds significant selection in both cohorts and shifts the placebo by +0.05 log points while shifting the treatment estimate by only -0.01. Either the correction is invalid (the exclusion restriction fails), in which case column (2) is no independent selection check, or it is valid, in which case an untreated tenure differential of about 0.04 exists and the selection-adjusted scheme effect is 0.045 (CI -0.02 to 0.11). The OLS triple difference remains 0.106 (t about 3.3). The evidence is therefore consistent with a positive lapse effect whose size lies between about 0.045 and 0.10, not pinned at 0.0955.

Evidence. QJE Table III p. 373 (signs checked on the rendered page): (1) 0.0955 (0.0261); (2) 0.0860 (0.0248); (3) -0.0100 (0.0190); (4) 0.0415 (0.0218); lambda 0.187 (0.0158) and 0.136 (0.0214); LR tests reject independence in both cohorts (chi2 = 106.5 and 34.36). Contrast (2)-(4) = 0.0445, SE = sqrt(0.0248^2 + 0.0218^2) = 0.0330, t = 1.35, 95% CI [-0.020, 0.109], assuming independent samples; contrast (1)-(3) = 0.1055, SE 0.0323, t = 3.27. NBER WP Table 4 had the same pattern (Heckman 0.0829 vs placebo 0.0314; contrast 0.0515, SE 0.036), where the text said the effect 'cannot be attributed to selection effects only'; the QJE dropped 'only'. Graph-based placebo (Figure VII B, recovered): -0.006 (years 3-5 vs 1-2).

Why this severity. Under one defensible alternative (a Heckman-corrected triple difference) the panel effect falls by about 53% and loses significance. But the OLS placebo is clean, the child-birth split (Figure A4) is similar, and the repeated cross-section, with expatriate and longer-resident controls, independently supports a negative wage effect. The sign of C4 survives; the panel magnitude and the claim that selection is ruled out do not.

The authors' response. None published; the paper's arguments are on pp. 373-375 (pay set by contract in advance, similar year 1-2 profiles, the Figure A4 birth split).

Why it matters, in detail. Readers see one cross-section estimate (-10.4 log points) whose design was changed between versions in ways that doubled it (within the WP's own trend-adjusted range), and a panel elasticity whose near-doubling is driven entirely by the denominator (F2), on data that appear unchanged despite relabelled sample bands. The claimed agreement between the two designs (delta about -0.355/-0.356) also held in the WP, but at about half the level (-0.18/-0.20). The early concentration of the cross-section effect (1995-97) points to composition or timing factors that a stable bargaining wedge would not predict.

Evidence. NBER WP 18885 Table 3 (RF -0.0476 (0.0103), delta -0.180, N 18,518; col. (4) trend-adjusted -0.130 (0.0535), delta -0.390) vs QJE Online Table A1 (-0.104 (0.0101), delta -0.355, N 13,662). NBER Table 4 (RF 0.0925 (0.0256), delta -0.196, N 2,943, lambda 0.187 (0.0149)) vs QJE Table III (0.0955 (0.0261), delta -0.356, N 2,951, lambda 0.187 (0.0158)). Recovered series (scripts/wage_figs.py): NBER Fig. 9A vs QJE Fig. VII A control 93.31/93.30 (year 1) and 103.00/103.00 (year 3); treatment 91.89/91.67 (year 1) and 129.51/129.25 (year 3); differences up to 3.5 index points in years 4-5. NBER Fig. 8: above x1.594 vs below x1.898 (1980-90), log-gap trend -0.018 per year; QJE Fig. VI pre-trend -0.003 per year. QJE Fig. VI DiD -0.108 overall (Table A1: -0.104); sub-periods as above. QJE Figure A4 notes (PDF p. 54).

Why this severity. The sign of the wage effect is stable across versions and designs. But its magnitude (cross-section reduced form -4.8 to -13 log points; delta -0.17 to -0.41) depends on undisclosed specification changes, and the panel sample actually used cannot be identified from the published text.

Why it matters, in detail. Ex ante, 1991-96 entrants faced a notch at 4-7 years of total stay on top of the 36-month kink, and originally a contract of at most 36 months. The duration response attributed to the 3-year kink (-0.136) and the rounders counterfactual built on years 4-5 are therefore not cleanly identified; claw-back-induced spikes at 4-5 years would make the year-3 excess-bunching estimate conservative. For migration, ITT tax rates overstate the effective incentive for would-be long stayers, biasing per-unit elasticities down, not up. For the 1995-2002 wage panel (years 1-5), the binding 7-year limit lies outside the window and was abolished in 2002, so it cannot explain the year-3 earnings jump.

Evidence. B 109 (2000-01), Folketingstidende 2000-01 Tillaeg A pp. 4450-4453: history of KSL s. 48 E. It covers Act 489 of 24 June 1992 (contracts from 1 June 1991; 'tidsbegraenset ansaettelse paa mellem 6 og 36 maaneder'; a further 12 months under ordinary tax, extended to 24 months by Act 296 of 27 April 1994 and to 4 years by Act 398 of 22 May 1996), states 'Hvis noeglemedarbejderen bliver i Danmark ud over disse 7 aar, vil der ... ske efterbeskatning', and records that scheme use fell between 1 June 1997 and 1 June 1998, when the 7-year rule first bit. L 108 (2001-02) remarks: taxpayers 'er omhyggelige med rettidigt at bringe den fulde skattepligt til Danmark til ophoer'; abolition applies from income year 2002, including current participants. L 81 (2010-11) remarks to s. 1 no. 7: the claw-back 'originally applied to everyone' and was 'abolished in 1998 for researchers and in 2002 for most others'. SKM2022.528.OLR legal history reproduces the 1992 text (contract 'af mindst 6 og hoejst 36 maaneders samlet varighed'). QJE p. 364 attributes bunching at 4-5 years to full-year contracts; Appendix A.2 treats years 4-5 as 'not kinks in the budget set'.

Why this severity. This is an important undisclosed feature of the incentive structure during 1992-2001, bearing mainly on the secondary duration result (C6) and on how the tax incentive is interpreted. It does not affect the migration reduced form, and if anything implies a larger elasticity per unit of effective incentive. Each extension took effect before any cohort reached the old limit, so the binding constraint in practice was the 7-year rule (June 1998-2001), which lies outside the five-year wage panel.

Why it matters, in detail. With intent-to-treat tax rates, the stock and arrivals regressions for the same above-threshold band and years should have similar first stages; the paper even attributes the larger take-up correction for the stock (A4: 2.892 vs 1.625) to long-stayers' ineligibility, implying the ITT stock rate assumes everyone is on the scheme. Yet the implied values differ by ~30% (0.41 vs 0.53), and the two verbal descriptions of the tax change match one column each. Wage first stages (0.26-0.33) are lower still for a similar population, and the panel first stage moved from -0.47 to -0.27 between versions with an essentially unchanged reduced form, which alone moved delta from -0.196 to -0.356. The magnitudes of e and delta, hence the Laffer rates and the claim that the two wage designs give 'very similar' delta, cannot be reproduced from what is published.

Evidence. Implied first stages (reduced form / elasticity): Table II col. (1) stock 0.402-0.413 long run and 0.444-0.462 short run; col. (2) arrivals 0.521-0.538 and 0.566-0.600, for the same earnings bands and years (range over the two plotted controls; scripts/fig3_did.py). Repeated cross-section wages: Online Table A1 0.27-0.32 across columns (e.g. 0.104/0.355 = 0.293); NBER WP Table 3 0.26-0.33. Panel: QJE Table III -0.268 to -0.270 in all four columns vs NBER WP Table 4 -0.467 to -0.472, with nearly the same reduced form (0.0955 vs 0.0925) and N (2,951 vs 2,943). Text: net-of-tax rate 'from about 0.4 to about 0.7' (p. 359) implies 0.56; regular average tax rate 'around 55%' vs a ~30-31% scheme rate (pp. 335, 338) implies 0.43. Statutory check with official 2009 parameters (single earner, average municipality, no deductions; scripts/notch_and_atr.py): average tax rate 51.1% at 1.0x, 55.0% at 1.5x and 56.9% at 2.0x the threshold, i.e. a 2009 first stage of 0.34-0.47 (0.43 at the scheme mean of 1.53x), larger in 1992-93 when the top marginal rate was 68%. KLMS (2020, fn. 2): the elasticity 'will be biased' if the denominator is mismeasured.

Why this severity. The denominators set the headline elasticities but cannot be verified; plausible alternatives move them by roughly 10-30% in either direction (e.g. stock 1.625 -> ~1.3-1.4 at a first stage of 0.47-0.50; arrivals 1.78 -> ~2.2 at 0.43; cross-section wage elasticity -0.355 -> ~-0.23 at 0.45). Signs and the 'very large' characterization are unaffected.

Why it matters, in detail. Bunching of B = 1.3 with an insignificant M is predicted both by bargaining with little worker power and by competitive behaviour with tax-induced entrants locating at the notch, so the test cannot tell the models apart. Within eq. (1), the observed delta of about -0.36 is hard to square with beta near 0 unless the match surplus is several times the reservation wage. The case for a pay-productivity wedge therefore rests mainly on the negative wage effects (C4), which are qualified by F4 and F5, and on ruling out cohort-specific demand effects that the paper explicitly cannot rule out.

Evidence. QJE pp. 337, 347 (fn. 17), 351-353 (eq. 1, Predictions 1-4), 363, 375-376; Figure IV (bunching 1.3 (0.35); missing mass 0.21 (0.14)); recovered Figure IV: post/pre density ratio 0.88 for 0.95-1.00 of the threshold (a small, imprecise dip). Auditor B's numerical competitive-entry example (pay equal to productivity, an outside option) produces entry and bunching at the notch with no pre-scheme missing mass. From eq. (1), point elasticity: y/y0 = 0.644(1-beta)/(0.356*beta), giving 1.81 at beta = 0.5, 7.24 at beta = 0.2 and 16.3 at beta = 0.1. Externally, Timm, Giuliodori & Muller (2025) find 'bunching from above' and limited wage-bargaining responses for the Dutch 30% scheme.

Why this severity. The abstract's mechanism claim ('can be rationalized') survives. The claims that the density evidence rejects the competitive model and that employers hold most of the bargaining power do not. The existence and sign of the wage effect (C4) are unaffected.

The authors' response. In-paper caveats only (p. 363; pp. 375-376).

Why it matters, in detail. The 1994 dating affects the scheme tax rate in one year by about 1.25 pp, and the 2008 changes affect only pooled descriptive statistics and the 1995-2010 density. Because eligibility for returning Danes was looser before 1998, the 'expatriate' group (at least 3 years abroad) is not the full set of eligible returnees in 1992-98, which could attenuate the A7 expatriate response.

Evidence. SKM2022.528.OLR legal history (1992 text; Act 913/1998 three-year condition); B 109 (2000-01) p. 4453 (L 149 / Act 296 of 27 April 1994: rate reduced to 25% 'i forbindelse med indfoerelsen af arbejdsmarkedsbidrag'); Act 522 of 17 June 2008, s. 1 (new s. 48 E(2); s. 48 F(3): 33% for up to 60 months), with elections effective for the whole 2008 income year; BDO, 'The Danish Expatriate Tax Regime' (May 2009): 'It is no longer a requirement that two thirds of the work should be performed in Denmark'. QJE pp. 338-339, fn. 9-11; Table I note ('30% before 1995').

Why this severity. The effects on tax rates (about 28.75% vs 30% in 1994; a few 2008-10 observations) and on sample definitions are small; core estimates end in 2005-06 and are not materially affected.

Why it matters, in detail. A mislabelled robustness figure; the expatriate estimate itself (-0.0813, delta -0.300) is unaffected.

Evidence. Recovered series (scripts/wage_figs.py): maximum |Figure VI - Figure A3 Panel A| = 0.001 index points, while Panel B differs by up to 13.4 points. The annotations match Table II A1/A7 and Online Table A1 cols. (1)/(5). QJE p. 369; Figure A3 notes (PDF p. 53).

Why this severity. Presentation error only; the Table A1 estimates are labelled correctly.

Why it matters, in detail. The estimator cannot be reproduced from the printed equations. The unstated bin width (apparently 1% of the threshold) matters for converting B = 1.3 into the '< 0.01' elasticity; with 1% bins the marginal-buncher calculation gives e of about 0.002-0.004, consistent with the paper.

Evidence. Online Appendix A.1, printed p. 40 (PDF p. 47). Auditor B's check: observed 20 vs counterfactual 10 gives normalized excess mass 1, while the printed count formula gives -1 and the printed log formula -0.30.

Why this severity. A documentation error with no evidence of an implementation error.

Why it matters, in detail. With full domestic consumption, the current wedge (about 49.5%) exceeds 1/(1+e) for every e of 1.1 or more. With e from the percentile design (about 1.1), the Laffer rate (about 48%) is close to that wedge. The policy number (~35%) is therefore sensitive to both e (F1, F2) and the unmeasured share of income consumed in Denmark.

Evidence. QJE pp. 336, 366-367, fn. 25-27; Immervoll, Kleven, Kreiner & Saez (2007), Economic Journal 117, Table A3: Denmark consumption tax 36.6% (Mendoza method; consumption-adjusted rates computed as (TR + CTR)/(1 + CTR)); Kleven, Landais, Munoz & Stantcheva (2020), JEP 34(2), pp. 135-136 ('despite its apparent generosity, the Danish tax rate for foreigners may actually be higher than optimal'). With e from Table II B1 (1.0-1.26), 1/(1+e) = 44-50%.

Why this severity. This affects the precision of a derived policy statement. The qualitative conclusion that preferential schemes can raise revenue for a small country holds for any elasticity above about 0.8 (1/(1+e) below the ~55% regular average rate).

The authors' response. KLMS (2020) state that, once social-security and value-added taxes are counted, the Danish scheme rate 'may actually be higher than optimal'.

Why it matters, in detail. It illustrates F2: the two verbal descriptions of the tax change (0.4 -> 0.7 vs 55% -> 31%) imply first stages of 0.56 and 0.43.

Evidence. QJE p. 359; scripts/fig3_did.py (ln 2.2 / ln 1.75 = 1.409; ln 1.94 / ln 1.75 = 1.18; ln 1.94 / ln(0.69/0.45) = 1.55).

Why this severity. An illustrative calculation only; the Table II estimates are separate.

Why it matters, in detail. They make exact reproduction of the wage and duration analyses harder (sample years, bands and the panel's balance are ambiguous), but they do not bear on the identification of any core result.

Evidence. p. 372 says both the reduced-form coefficient and delta are 'negative and significant' (the reduced form is +0.0955; the same slip appears in the NBER WP). p. 375 'close to the initial estimates in columns (1) and (2)' should be (1) and (3). p. 374 says Figure A4 uses 'the model of Figure VII, Panel B', while the A4 notes say the top panel. Table III col. (3) SE is printed '(0071)'. The Table A1 note cites 'appendix A.2' instead of A.3, and gives '27-digit industry codes'. p. 369 'As we saw in Section III.A' should be IV.A. The Figure III legend says '.9 to .99*threshold' while the caption says 90-99.5%. Figure VII gives placebo entrants as 1980-1991, Table III as 1980-1990. p. 364 says 'about 15 percentage points' vs -0.136 in Figure V. p. 354 says 'close to 3,000 by 2005' vs 2,702 recovered. p. 357 describes arrivals 'from 1980 to 2006', but Figure III B ends in 2005. Figure VI plots 2007 while Table A1 states 1980-2006. The Figure A3 note mixes 'first full calendar year' with arrival in t-1 or t-2. Table III col. (1) N = 2,951 is not divisible by 5 for a five-year balanced panel. The composition shares in the text (1991-2006) describe Figure A1, which covers 1991-2010.

Why this severity. Editorial slips; none changes an estimate or conclusion.

Why it matters, in detail. The natives' Laffer rate depends on the elasticity of the resident native top-earner base, which is dominated by emigration. The return-migration elasticity of a small expatriate pool is mechanically a small part of that base and says little about emigration responses.

Evidence. QJE p. 367 and fn. 27; Table II A7; SKM2022.528.OLR legal history (three-year condition from Act 913/1998); KLMS (2020) p. 129 on how the size of the initial base drives these elasticities.

Why this severity. Footnote 27 discloses the limitation, and the base-size argument makes a small native elasticity plausible; the overstatement concerns a side claim.

The authors' response. Footnote 27: the emigration margin 'cannot be directly estimated with our scheme-induced tax variation'.