Emmanuel Saez · NBER Reporter 2014 No. 2 (research summary)

Taxes and International Mobility of Talent

14 problems found: 2 major · 5 moderate · 7 minor

What the paper claims

Football players' location decisions are very responsive to tax rates. When Spain introduced the Beckham Law in 2004, the foreign share in the Spanish league 'immediately and sharply' diverged from the Italian league, and the extra influx was 'driven entirely by players eligible for the scheme with no effect on ineligible players'.
Because football labour demand is rigid there is 'strong evidence of sorting': top-quality players are much more responsive, and tax cuts to foreigners 'attract top-quality foreign players, but crowd out lower-quality foreign players as well as some domestic players'.
The Danish foreigners' scheme (flat ~30% for up to 3 years above a threshold of ~EUR 100,000) doubled the number of foreigners above the threshold relative to foreigners slightly below it; the effect builds up over five years and remains stable; the foreign share of the top 0.5% of earners is 7.5% versus a 4% counterfactual.
The revenue-maximizing tax rate for a scheme targeting highly paid foreigners is about 35%, which 'corresponds roughly' to the current Danish scheme rate once VAT and excises are counted; the revenue-maximizing rate on natives is much higher because expatriate natives' migration response is very small.
Preferential schemes can be desirable for a single country but impose negative fiscal externalities on others; 'our paper provides the first compelling evidence that this is indeed a major empirical issue'; absent coordination such schemes 'could substantially weaken tax progressivity at the top'.
Framing: football players 'may provide an upper bound on the migration response to taxation for the labor market as a whole'; there is 'almost no empirical work' on tax-induced mobility across countries.

Every problem found

1majorconfirmed · newly identified here · methodology

The Reporter says tax breaks for foreign footballers pull in stars but push out weaker foreign players and some local players. That result depends on assuming weaker and stronger players are equally attached to their home country, which the data clearly reject, and on the Dutch league. With a more realistic assumption weaker foreign players are attracted too, and without the Netherlands there is no measurable push-out of local players; only the finding that stars respond more holds up.

Technical detail and evidence

Why it matters, in detail. The common home-bias term is rejected: LR 328 with one quality interaction, 917 with full interactions. Once it is relaxed, the lower-quality coefficient is +0.48 to +0.58 (SE about 0.20), so Table 3 no longer separates rigid from flexible demand. The domestic cross-effect (-0.62 to -0.70 with the Netherlands) is -0.02 (0.15) without it. Across all variants the top-quality coefficient (0.46-1.49) exceeds the lower-quality one (-0.76 to +0.58).

Evidence. scripts/football_sorting_clogit.py and football_sorting_extra.py on base_multinomial_lowerleagues.dta (KLS AER replication archive), Stata asclogit translated from table3.do (read as text); outputs scripts/out/football_sorting_clogit.log/.json, football_sorting_extra.json. Published specification, top leagues (N=47,727): col 4 low -0.391 (0.158), top 1.494 (0.136); col 5 low -0.448 (0.154), top 1.409 (0.133), log(1-tf)x domestic -0.635 (0.134), log(1-td)x foreign -0.201 (0.192). Adding domestic x (quality index above the bottom group): low +0.578 (0.203), top 1.175 (0.132), interaction -0.887 (0.063), LR = 328 (1 df); col 5 low +0.510 (0.198). Fully quality-specific home bias (domestic x three quality dummies and x national-team indicator): low +0.537 (0.199), top 1.170 (0.134), LR = 917 (4 df); col 5 low +0.482 (0.192). Dropping the Dutch alternative and its choosers (consistent under IIA; N=43,454): col 5 displacement -0.021 (0.148); with quality-specific home bias -0.009 (0.146) and low -0.066 (0.198). Sample with second leagues without NL: displacement +0.166 (0.125). The AER's own case studies are mixed and insignificant: Spain lower-quality elasticity +1.43 (0.88), Denmark -0.70 (0.54) (AER Table 1, p.1906).

Why this severity. Two of the three components of a finding the Reporter calls 'strong evidence' (lower-quality crowd-out and domestic displacement) disappear under a data-preferred generalisation or after dropping one country. The football migration response itself (C1) is not affected.

The authors' response. AER p.1921 calls Table 3 'strong evidence of ability sorting and displacement effects'; fn 38 concedes limited power for the domestic-rate cross-effect. No response on the home-bias restriction located.

2majorlikely · newly identified here · selective presentation

The best-known Danish result, that the tax break doubled the number of well-paid foreigners, comes from one way of counting. The authors' own cross-check, built to rule out a known distortion, finds a smaller effect that fades over time, which would also mean Denmark could tax these foreigners somewhat more before losing revenue. The effect is large either way; the Reporter gives only the largest version and does not say so.

Technical detail and evidence

Why it matters, in detail. Long-run log DD is 0.662 (x1.94) in counts and 0.449 (x1.57) in shares, with the same implied first stage (about 0.40), so e falls from 1.63 to 1.13. If the gap reflects fanning-out, the doubling itself is overstated. If instead scheme migrants cluster just above the threshold (the P99.2-99.5 band that Panel B excludes), the count doubling is right but the earnings-weighted base elasticity that enters t* = 1/(1+e) is below 1.6. Either way the revenue-maximizing rate is plausibly about 40-47% rather than about 35%. The elasticity exceeds 1 in every specification.

Evidence. Reporter p.19 cols.1-2 and Fig. 1; QJE Table II p.358 (A1 1.625 (0.162), 1.779 (0.168), 2.049 (0.148); B1 1.133 (0.0802), 1.015 (0.169), 1.257 (0.109)); QJE p.361. Adjudicator recovered both figures exactly from the PDF vector graphics (scripts/extract_qje_figures.py, scripts/danish_counterfactuals.py; scripts/out/fig3a_vector.csv, figA2_vector.csv, danish_counterfactuals.json). Fig. III-A: treatment/control ratio 1.82-2.14 in 1993-2005 (1.96 in 2005); long-run log DD 0.662 (x1.94). Fig. A2 (P99.5-100 vs pooled P95-99, 1980-90 base): relative ratio 1.72 (1995), 1.62 (1999), 1.48 (2000), 1.33-1.46 (2001-05); long-run log-odds DD 0.449 (x1.57). Implied first stages are the same (0.407 for Fig. III with e=1.625; 0.397 for Fig. A2 with e=1.13), so the elasticity gap is a reduced-form gap. Laffer rate 1/(1+e): 38.1% (e=1.625) vs 46.9% (1.133), 49.6% (1.015), 44.3% (1.257). The QJE's own back-of-envelope net-of-tax change (0.4 to 0.7, log 0.56; p.359) would turn the Fig. 1 reduced form into an elasticity of about 1.18, so the published 1.62 cannot be rebuilt from published information. Supporting but inconclusive: reading the undocumented 'frac' column of the authors' collapsed data (KLS AER archive) as a band's foreign share implies the population above the threshold grew x2.21 in 1990-2005 while all wage earners grew 4.5% (Statistics Denmark INDKP101), i.e. fanning out; but the series jumps 40% in 1997 alone (about 40% of its 1990-2005 log growth), which looks like a data break (see F11).

Why this severity. The alternative design is the authors' own answer to a confounder they identify. It lowers the stock elasticity by 30% (1.63 to 1.13), lowers the 2001-05 effect from about x1.96 to x1.39-1.46, and raises the revenue-maximizing rate from about 35-38% to 44-50%, a change of a quarter or more in each headline magnitude. The qualitative finding (a very large response, elasticity above 1) survives both designs, and the microdata needed to decide which design is less biased are confidential.

The authors' response. QJE p.361 describes the percentile-based estimates as 'slightly attenuated relative to our baseline specification ... but remain very large around 1.2'. The authors' 2020 review (Kleven, Landais, Munoz & Stantcheva, JEP 34(2), p.129) restates the count-based 'more than doubles ... about 1.6'. No response to the gap was located.

3moderateconfirmed · newly identified here · internal inconsistency

The Reporter says that without the tax break foreigners would make up 4% of Denmark's top earners instead of 7.5%. The authors' own chart for that same group points to about 5-5.5% (or about 4.4% with a less standard calculation). The effect at the very top is therefore smaller than the 4% figure suggests.

Technical detail and evidence

Why it matters, in detail. On the paper's own P99.5-100 series, the 2001-05 counterfactual is 5.05-5.28% under proportional or log-odds trends (x1.39-1.46, +2.1-2.3 pp) and 4.35-4.38% under additive trends (x1.68, +3.0 pp), against 4% (x1.875, +3.5 pp). The 4% equals 7.5%/1.95, i.e. the count-based doubling applied to a group for which the paper's own figure shows a smaller and eroding effect.

Evidence. Reporter p.19 col.2; QJE p.336; QJE online Fig. A2 (PDF p.52) recovered from vectors (scripts/out/figA2_vector.csv, danish_counterfactuals.json). Observed P99.5-100 foreign share 7.36% (2001-05 mean) and 7.51% (2005); pre-scheme mean 3.39% (1980-90). Pooled P95-99 control, 1980-90 base, 2001-05: proportional 5.28%, log-odds 5.23%, additive 4.38%; 1990 base: 5.09%, 5.05%, 4.35%; 2005 alone: 5.46-5.66% (proportional), 4.55-4.58% (additive). Implied effect +39-46% (log framework) or +68% (additive), against the +88% implied by 7.5 vs 4; in points 2.1-2.3 or 3.0 pp against 3.5 pp. A counterfactual near 4% arises only for 1995-97 (3.8-4.0%) or with additive 1995-2005 averaging (4.07-4.11%). Both auditors' figures agree with these to within about 0.1-0.3 pp.

Why this severity. A prominent illustrative number overstates the scheme's effect on the top-0.5% share by about half in the paper's own log framework (about a sixth, in percentage points, under additive trends). It translates the main result rather than being the main result.

4moderateconfirmed · newly identified here · speculative assumption

The Reporter says Denmark's special rate for foreigners, once sales taxes are counted, is already about at the level that brings in the most tax revenue. With the authors' own figures, that is true only if these foreigners spend less than about a quarter of their take-home pay in Denmark. Otherwise the effective rate is nearer 45-50%, and the authors' later review says the rate may be too high; this is a policy detail, not the main finding.

Technical detail and evidence

Why it matters, in detail. With TR = 31% and CTR = 36.6% (tax-exclusive), T = (TR+CTR)/(1+CTR) = 49.5% under full domestic spending (44.8% with VAT only), against t* = 33-40%. T = t + (1-t) f c/(1+c) reaches 35% only for f <= 0.22-0.29. Because c is common to treated and control groups, the estimated elasticity applies to the all-in wedge, so the correct comparison is T versus 1/(1+e). Under the source's own parameters the scheme sits above its Laffer rate.

Evidence. Reporter p.19 col.2; QJE p.336 (same sentence), pp.366-367 ('Taking into account consumption taxes, the Laffer rate on foreigners could be slightly lower than the current total tax rate under the scheme'), fn 26 (average consumption tax 36%, to be scaled if income is consumed abroad), fn 9 (8% + 0.92 x 25% = 31%). Immervoll, Kleven, Kreiner & Saez (2007, EJ 117:1-44), Table A3 p.42: Denmark 36.6% (1998), tax-exclusive by construction, combined as (TR+CTR)/(1+CTR) (fn 14). All-in rate (0.31+0.366)/1.366 = 49.5%; 44.8% with 25% VAT only. The authors' own AER tax file (mtr.dta) codes Denmark's foreigner rate at 0.448-0.454 for 1997-2008, i.e. the scheme rate with full VAT. Reaching 35% requires spending at most 22% (36.6% basket) or 29% (VAT only) of net pay in Denmark; reaching 40% requires at most 49% (36.6% basket) or 65% (VAT only). Kleven, Landais, Munoz & Stantcheva (2020, JEP 34(2):119-142, pp.135-136): e = 1.6 implies 38%, 'lower than the total top marginal tax rate when accounting for social security taxes and value-added taxes ... the Danish tax rate for foreigners may actually be higher than optimal.' scripts/danish_counterfactuals.py.

Why this severity. This is a substantive but secondary policy claim. It rests on an undisclosed assumption, and with the source's own parameters the scheme's all-in rate exceeds the Laffer rate by 5-16 points. Correcting it reinforces rather than weakens the tax-competition message, and it does not affect the migration estimates.

The authors' response. QJE p.367 and fn 26 note that consumption taxes raise the total rate and must be scaled for consumption abroad; KLMS (2020, pp.135-136) conclude the Danish foreigner rate 'may actually be higher than optimal'.

5moderateconfirmed · newly identified here · overclaiming

To show that Spain's tax break caused an inflow of foreign players, the Reporter says only players who qualified came, with 'no effect' on those who did not. The published paper's own numbers show a smaller but not zero effect on non-qualifying players, based on very few players, and the authors say the difference is not statistically significant. The check is much weaker than the Reporter suggests.

Technical detail and evidence

Why it matters, in detail. The placebo elasticity of 0.57 (0.49) cannot be distinguished from the eligible 1.29 (0.22) (z about 1.3), and the ineligible cells are tiny, so the test has little power to rule out a non-tax Spanish shock. The Spain-Italy DD is driven mostly by Italy's 2003-06 fall (11.5% to 5.2%) and by Spain's rebound from a 2003 low. The case study is suggestive rather than a clean falsification test.

Evidence. Reporter p.18 col.3; KLS NBER WP 16545 (2010) p.3 (same sentence); AER Table 1 Panel B1 p.1906 (eligible 1.29 (0.22); non-eligible placebo 0.57 (0.49); ATR version 1.41 (0.31) vs 0.45 (0.78)) and p.1910 ('Due to large standard errors however, the difference between those two estimates is not statistically significant'). Auditor A reproduced 1.290 (0.217) and 0.591 (0.513) from the replication files; difference z = 1.25-1.34, p = 0.18-0.21. Adjudicator (scripts/spain_italy_raw.py on ddd.dta and basesynthetic_control.dta): ineligible group 3-31 players per year in Spain and 1-15 in Italy (1996-2008); raw foreign-share gap Spain minus Italy -3.9 pp (2003), +0.3 (2004), +4.0 (2005), +7.7 (2006), +6.9 (2007), +2.0 (2008); DD 2004-08 vs 1996-2003 = +4.8 pp, of which Spain +0.6 pp and Italy -4.1 pp.

Why this severity. One of only two pieces of football identification evidence that the Reporter describes is presented as decisive when the published paper says it is not. The football migration response rests on other evidence as well (cross-country, other reforms, multinomial models), so the core claim is only modestly affected.

The authors' response. AER p.1910 itself states that the difference between the eligible and placebo estimates is not statistically significant.

6moderatelikely · newly identified here · methodology

The Reporter uses the small number of Danes abroad who came home under the scheme as evidence that Danes hardly react to taxes. But until 2002 the scheme back-taxed people who stayed in Denmark long term, so it was of little use to Danes coming home for good. Their weak response says little about how Danes react to taxes, although other studies also find that natives move much less than foreigners.

Technical detail and evidence

Why it matters, in detail. For permanent returnees the scheme's value was zero or negative until 2002 (back-taxation of all scheme income), so Table II A7's null (0.019, SE 0.028) is close to what one would expect whatever natives' elasticity is. Only 2002-05 offers clean variation, and it is diluted in the 1992-2005 estimate. The claw-back also made the scheme a subsidy to temporary stays, which bears on interpreting the foreigner response as permanent relocation.

Evidence. Reporter p.19 cols.1-3. Lov nr. 489 of 25 June 1992 (L 158, 1991-92, as adopted), KSL section 48 E stk. 5 ('Beskatningen efter stk. 4 bortfalder, hvis den skattepligtige ikke senest 1 maaned efter ophoeret af et ansaettelsesforhold ... har bragt skattepligten ... til ophoer'; scheme pay is then included in ordinary taxable income for the years concerned) and stk. 7 (12-month extension, after which stk. 5 applies). Bill L 108 (2001-02), general remarks sections 1-3: current rules allow up to 48 months in Denmark after the 36 scheme months, otherwise efterbeskatning; abolished for researchers by Lov nr. 913 of 16 Dec 1998 (in force 13 May 2000); the bill notes that only after the reform can 'hoejtloennede danskere, der vender hjem ... og som oensker varig bosaettelse' use the scheme without back-taxation. KLSS NBER WP 18885 (2013) p.8 mentions 'the original claw-back rule after 7 years'; the QJE does not. QJE Table II A7: 0.0185 (0.0280), -0.0913 (0.0708), -0.0998 (0.0613); QJE fn 27 p.367. Skatteministeriet fact sheet, 8 April 2014.

Why this severity. The undisclosed rule removes most of the Danish evidentiary basis for the natives' 'much higher' revenue-maximizing rate, a secondary claim. The conclusion that natives move much less than foreigners is still supported by other evidence (football domestic estimates; Munoz 2019: 0.1-0.3 for European top-10% earners).

The authors' response. QJE fn 27 notes that the expatriate response is 'only one side of the natives behavioral response'. No discussion of the claw-back in the QJE or the Reporter.

7moderatelikely · previously known · overclaiming

The Reporter's conclusion, that this is a 'major' problem that could substantially undermine taxing the rich in Europe, goes further than the published research. That research stresses that Denmark is a small country and that its results may not carry over to larger ones. The warning is reasonable, but it is stated more strongly than the evidence supports.

Technical detail and evidence

Why it matters, in detail. The Danish elasticity is a stock elasticity for a small jurisdiction with a small foreign base; by the authors' own argument (QJE p.337; KLMS 2020 p.136) such elasticities shrink with jurisdiction size and base share and are not transportable. No estimate of revenue lost by sending countries is offered, and the 2020 review finds no race to the bottom in statutory top rates. 'Could substantially weaken progressivity' is therefore a conjecture, not a result.

Evidence. Reporter p.19 col.3. KLSS WP 18885 p.3 ('major empirical issue. Absent coordination, it is conceivable that such schemes could unravel tax progressivity in Europe') vs QJE p.336 ('significant empirical issue'), QJE p.337 and p.376 (small-country caveat), QJE p.336 (wage effect). Kleven, Landais, Munoz & Stantcheva (2020, JEP 34(2)), p.129 (mobility elasticities 'are not structural parameters') and p.136 ('there is no clear indication of a race to the bottom'). AER abstract and conclusion p.1922 (foreign elasticity 'around one'); AER uniform revenue-maximizing rate about 81% under flexible demand (appendix Table A3, per Auditor A; not re-checked).

Why this severity. The empirical estimates are untouched, but the work's policy message extrapolates small-country, foreigner-specific elasticities without the caveats the published papers attach.

The authors' response. The QJE (pp.337, 376) and KLMS (2020, pp.129, 136) state the small-country and non-structural caveats; the Reporter does not.

8minorconfirmed · newly identified here · misrepresentation of source

The Reporter says Danes living abroad 'do come back more because of the scheme'. The study it summarizes found that they did not. It looks like a missing word, but as written it says the opposite of the finding.

Technical detail and evidence

Why it matters, in detail. All three A7 estimates are insignificant and two are negative; the correct statement is 'no detectable increase in returns', not a positive response.

Evidence. Reporter p.19 col.2-col.3 (identical in the HTML version); QJE Table II A7 p.358: 0.0185 (0.0280), -0.0913 (0.0708), -0.0998 (0.0613); QJE p.360.

Why this severity. This is a wording error that a careful reader can detect from the preceding sentence; no estimate changes. The weakness of the underlying inference is treated separately in F6.

9minorconfirmed · newly identified here · arithmetic or transcription

There are small factual slips. Two of the 14 countries (Norway and Switzerland) are not in the EU, and the data cover about 24 seasons rather than 30 years. David Beckham also moved to Spain before the tax break he supposedly moved for existed, although he did benefit from it later.

Technical detail and evidence

Why it matters, in detail. Labelling and chronology only. The sample is 14 countries as stated, and Beckham could use the regime from 2004 under its 'five following periods' rule (per the AER, he did).

Evidence. Reporter p.18 cols.2-3; AER p.1893 ('14 Western European countries from 1985 to 2008') and p.1896 (country list incl. Norway and Switzerland); KLS WP 16545 p.3 ('14 European Union countries over the past 30 years'); AER fn 23 p.1907 ('became one of the first foreigners to take advantage of it'); BBC Sport, 2 July 2003 ('signed a four-year deal ... on Tuesday'); BOE Ley 62/2003, art. 1.Primero.Cuatro (new art. 9.5 Ley 40/1998, 'Con efectos desde el dia 1 de enero de 2004').

Why this severity. These are descriptive and anecdotal errors; no estimate or conclusion depends on them.

10minorconfirmed · newly identified here · version instability

An earlier version of the same Danish data, published by the authors with another paper, matches the Reporter's chart until 1996 but then shows a smaller effect that fades by 2005. The difference is not explained anywhere.

Technical detail and evidence

Why it matters, in detail. In the 2012 vintage the relative effect erodes after 1995 (x1.96 to x1.64), as it does in the percentile design (F1), so the 'stable doubling' appears only in the QJE construction.

Evidence. scripts/collapsed_vs_fig1.py (scripts/out/collapsed_vs_fig1.json): treatment 2,209 vs 2,054 (1997), 3,125 vs 2,532 (2004), 3,006 vs 2,702 (2005); ratio 2.01 (1994), 1.97 (1995), 1.64 (2005); log DD 0.587 vs 0.662. Under the 'frac' reading the band population jumps 40% in 1997 (27.7k to 38.6k) while wage earners grow 1.4%. prog/prog_graph/read_me.txt in the AER archive.

Why this severity. The discrepancy is about 11% of the average effect and its cause (likely a data revision) is unknown. It qualifies 'remains stable afterward' but does not change the qualitative result.

11minorconfirmed · newly identified here · internal inconsistency

In the football paper, two sets of results in one table carry each other's labels. The numbers and their direction are right, so the Reporter's summary is not affected.

Technical detail and evidence

Why it matters, in detail. The swap changes which sample supports which statement, not the coefficients. The substantive fragility of these coefficients is F2.

Evidence. Adjudicator re-estimation (scripts/football_sorting_clogit.py): sample with second leagues col 4 -0.512 (0.149)/1.409 (0.136), col 5 -0.529 (0.145)/1.301 (0.132)/-0.618 (0.119)/-0.149 (0.178), equal to printed Panel A; top leagues col 4 -0.391 (0.158)/1.494 (0.136), col 5 -0.448 (0.154)/1.409 (0.133)/-0.635 (0.134)/-0.201 (0.192), equal to printed Panel B. AER p.1921-1922. Auditor B's Newton-polished refits give the same numbers.

Why this severity. Signs and approximate magnitudes are similar in both samples and the Reporter quotes no numbers from the table. To avoid double counting, this should be counted under KLS (2013), not this summary.

12minorconfirmed · newly identified here · internal inconsistency

The chart's legend and its caption describe one comparison group slightly differently. This is a labelling slip with no effect on the results.

Technical detail and evidence

Why it matters, in detail. The control band definition differs by 0.5% of the threshold between legend and notes; it does not affect the plotted ratios or estimates.

Evidence. Reporter p.19, Figure 1 legend and notes; QJE Fig. III p.355 and Table II notes p.358.

Why this severity. A labelling slip with no bearing on the results.

13minorlikely · newly identified here · misrepresentation of source

The Reporter quotes a football manager blaming the expected end of English dominance on a new tax. Other reports of the same remark show he also blamed the falling pound, and the omitted words appear to be exactly that part. It is an anecdote, so the findings are unaffected.

Technical detail and evidence

Why it matters, in detail. This is framing, not evidence; the original wording in the cited Sunday Times article is unverified.

Evidence. Reporter p.18 col.2 (citing Northcroft, Sunday Times, 25 April 2009); Irish Examiner, 26 April 2009, and Arsenal Mania report (cached by Auditor A); the same ellipsis is in KLS WP 16545 p.2. The Sunday Times original could not be obtained.

Why this severity. An illustrative anecdote; no finding depends on it.

14minorplausible · previously known · overclaiming

The Reporter suggests footballers show the most any workers would move for tax reasons. The authors' own Danish study of all well-paid foreigners found a reaction at least as large, so footballers are not a reliable 'upper limit', although the Reporter's 'may' softens the claim.

Technical detail and evidence

Why it matters, in detail. Because foreign-stock elasticities scale inversely with the foreign base share, 'upper bound' has no well-defined numerical content across settings. The authors' own non-football estimate (1.5-2) exceeds the football headline (about 1).

Evidence. Reporter p.18 col.3; AER conclusion p.1922 ('around one'); QJE abstract and p.359 (1.5-2); AER Fig. 4 and KLMS (2020) on the Danish sports/entertainment sector. Auditor A recorded this tension as a caveat to a passed check; Auditor B treated the 'may' as a sufficient qualification.

Why this severity. The claim is hedged ('may') and correct as a statement about relative mobility within Denmark. Only its reading as a numerical bound is unsupported.

The authors' response. QJE fn 3 notes that football players 'might be substantially more mobile than other high-skilled workers'.

Claims examined and rejected

Problems one auditor raised that did not survive checking.

The authors' own fanning-out-robust evidence implies 'roughly half the effect' of the headline doubling (I1). — Partly rejected (magnitude). Panel B's long-run elasticity is 30% lower (1.13 vs 1.625) and its average effect is +57% vs +94% (log DD 0.449 vs 0.662, adjudicator's vector recovery). 'About half' holds only for 2001-05 in Figure A2 (log effect 0.33-0.37 vs 0.68). The issue is retained as F1 with the smaller magnitude.
The authors' collapsed data show the eligibility threshold drifting from about P99.1 to about P98.0, contradicting the QJE's statement that it always lies between the 99.2th and 99.4th percentiles (I1 point 4, R9). — Not established. It rests on reading an undocumented column ('frac') as a band's foreign share, and the implied population jumps 40% in 1997 alone (about 40% of its 1990-2005 log growth) while wage earners grew 1.4%. That points to a data break in this vintage rather than fanning out. It is kept only as a caveat in F1 and F11.
Accounting for post-scheme revenue from foreigners who stay beyond three years lowers the revenue-maximizing rate to 22-34% (I3 point 2). — Not retained as a finding. It is the auditor's own illustrative calculation, which ignores duration responses, the claw-back and wage incidence. The direction is plausible but the magnitude has no empirical support.
Stating 'about 35 percent' without its range is itself a defect (I3 point 1). — Not a separate issue. A summary may quote a central value, and the QJE's 33-40% range brackets it. The substantive sensitivity (the percentile design) is covered by F1.
The Reporter's 'no effect on ineligible players' can be read as acceptable statistical shorthand for an insignificant placebo (assumptions table). — Rejected. The published AER explicitly says the eligible/ineligible difference is not statistically significant, the placebo point estimate is 44% of the eligible estimate, and the ineligible cells hold 3-31 players a year. The Reporter repeats the pre-publication working-paper sentence (F5).
The failure of the AER-archive collapsed Danish data to reconcile with QJE Figure III implies no error (R6). — Partly rejected. The cause is unknown, but an undocumented revision between two public versions of the same series, identical to 1996 and diverging afterwards (2005 ratio 1.64 vs 1.96), is a version-instability issue. Retained as minor (F11).
The expatriate-return misstatement, the dropped fn 27 caveat and the claw-back form a single moderate misrepresentation (I4). — Regraded rather than rejected. The reversed sentence is a minor wording error (F8, agreeing with Auditor B). The claw-back and the dropped caveat are a separate, moderate weakness of the natives inference (F6).

Audit notes

What reproduced. Reproduced: (i) QJE Figure III-A / Reporter Figure 1 and online Figure A2, recovered from the PDF vector graphics (linear axis fits reproduce every tick mark to within 0.1 count or 0.000001 share). The count-based doubling (x1.96 in 2005; long-run log DD 0.662) and the 7.5% top-0.5% share reproduce. The percentile design gives log-odds DD 0.449 with the same implied first stage (0.40), so the 1.13 vs 1.625 elasticity gap is a reduced-form gap. The '4% counterfactual' does not reproduce from Figure A2 (5.0-5.7% proportional, 4.3-4.6% additive for recent years). (ii) Laffer and consumption-tax arithmetic: the all-in scheme rate is 49.5% with the source's 36.6% consumption tax (44.8% with VAT only, matching the authors' AER tax file 0.448-0.454). (iii) KLS (2013) Table 3 cols 4-5: reproduced exactly (coefficients and player-clustered SEs to three decimals) with an independent conditional-logit estimator, confirming that the printed panels are swapped. Quality-specific home bias (LR 328-932) turns the lower-quality coefficient positive (+0.48 to +0.58), and dropping the Netherlands removes domestic displacement (-0.635 to -0.021). (iv) Spain-Italy raw foreign shares and placebo cell sizes from the replication files. (v) Collapsed Danish CSVs match Figure 1 to 1996 and diverge after. (vi) Danish 1992 law, 2002 bill, 2009 Ministry tables and the 2014 fact sheet read in the original. Not reproduced: QJE Table II regressions and first stages (confidential Statistics Denmark data); AER Table 2 within-country estimates and synthetic-control weights (not re-run; published weights used by Auditor A); the Sunday Times quotation.

Limits of this audit. The Danish register data are confidential, so the count-based vs percentile-based gap (F1) cannot be attributed to fanning-out or to scheme migrants clustering just above the threshold, and the unreported first stages cannot be checked. Figure data are recovered from vector graphics, exact to plotting precision but not raw data. The football checks re-estimate Table 3 only; AER Table 2 (within-country foreign elasticity), the synthetic-control weights and the Laffer appendix were not re-run (the Dutch dependence of Table 2 reported in this project's KLS adjudication was not independently verified here). The claw-back's quantitative effect on the expatriate estimate was not modelled. The Sunday Times original of the Wenger quote and the OECD (2011) table were not consulted directly. No published critique of, or author reply to, this summary or its two source papers' migration estimates was located; the critique corpus records none. Several issues (F1-F6, F12) are inherited from the underlying papers and are also recorded in this project's adjudications of KLS (2013) and KLSS (2014); they should not be double-counted when results are aggregated.