Taxing the Rich More: Preliminary Evidence from the 2013 Tax Increase

Why it matters, in detail. eM = log(s2015/s_cf2015)/dlog(1-tau), with dlog(1-tau) = -0.114 and s_cf2015 = 22.70%. The numerator is -3.0 log points with the preliminary 22.03% and -5.0 with the final 21.59%. So eM moves from 0.26 to 0.44, e*a*tau/(1-tau) from 18.8% to 31.4%, and the implied revenue-maximizing rate 1/(1+a*e) from 72% to about 60%. The 2011-14 estimate moves the other way (0.21 -> 0.17): the medium-run estimate is effectively pinned down by single-year data noise of 1-2.5 log points. The author disclosed the preliminary status and could not have used final data; the point is that the published headline is not supported by them.

Evidence. Adjudicator recomputation (final/scripts/adj_reproduce.py; output/adj_reproduce.txt), same eq. (3), same Table 1 rates, same 2009-11 counterfactual: top 1% 0.264 -> 0.439 (TabFig2016) / 0.442 (TabFig2024); top .1% 0.239 -> 0.470; top 1-.1% 0.290 -> 0.412; top .01% 0.116 -> 0.103; income excl. gains 0.317 -> 0.487. Eq. (4) loss (a = 1.5, tau = 0.322): 18.8% -> 31.4%. The revision is in the numerator: final 2015 top-1% income is 2.9% below the projection, total income 0.9% below (scripts/decompose_revision.py). Independent check from final IRS SOI Publication 1304 Table 1.4 for 2009-2016 (Pareto interpolation within AGI brackets, Piketty-Saez tax-unit counts and denominators; scripts/irs_top1_check.py): shares within 0.05 pp of the final Piketty-Saez series in every year; eM = 0.465, eS = 1.166. The two auditors' separate IRS rebuilds give 0.456 and 0.47. 2014 was also revised (21.43 -> 21.52), so the 2011-14 estimate (Table 3 panel D) falls from 0.21 to 0.17. Latest-year preliminary-to-final revisions of the top-1% share for 2011-2017 were -0.18, +0.36, -0.07, +0.28, -0.44, +0.04, +0.54 pp (scripts/prelim_vs_final.py), comparable to the 0.67 pp gap (22.03% actual vs 22.70% counterfactual) on which eM rests. Saez's 'Striking it Richer' updates of 2017-2026 keep 'By 2015, top incomes shares are back to their upward trajectory' and do not revisit eM. Scheuer & Slemrod (2020, NBER w26207) cite 'about 0.25', and the Hendren & Sprung-Keyser Policy Impacts entry reuses FE = -0.19.

Why this severity. With the paper's own estimator, the headline medium-run elasticity rises by about two-thirds and the revenue loss from 19% to 31%, which breaks 'at most 20%'. The qualitative conclusions survive: the lasting response stays far below the short-run 1.16, and most of the mechanical revenue is retained.

The authors' response. Endnote 18 (p. 117) discloses that 2015 is extrapolated from preliminary IRS tabulations, notes that final statistics are due in August 2017, and says preliminary statistics are 'generally very close to final statistics'. No later re-estimate was located; the author's later 'Striking it Richer' updates restate only the qualitative reading.

Why it matters, in detail. The estimator has one free parameter, the counterfactual slope, pinned down by two pre-period observations; d eM/d slope is about 1.5 per pp/yr. 'At most 20%' requires a slope of no more than about 0.77 pp/yr. Alternatives give: log-linear reading of the same recovery, 0.42 (about 30%); paces of the validation recoveries, about 1 (about 70%); long-run trend, -0.44. On final data the 2009-11 framework yields 0.44-0.59 (31-42%). The preferred estimate is a point inside a wide, non-statistical sensitivity band, not an upper bound. Do not add these effects to those of F1, F4 or F5.

Evidence. Adjudicator, on the paper's data (scripts/adj_reproduce.py, scripts/slope_scenarios.py). (1) The same 2009-11 endpoints extrapolated at a constant growth rate give eM = 0.416 (loss 29.6%). (2) Each +0.1 pp/yr in the assumed slope adds about 0.15 to eM and about 11 points to the loss. (3) The 2009-11 slope averages a +1.74 pp rebound in 2009-10 with a -0.22 pp dip in 2010-11. (4) The paces of the two recoveries the paper cites as validation (1994-2000: 1.22 pp/yr; 2002-07: 1.33 pp/yr) give eM of 0.93-1.09 and losses of 66-78%; the paper calls such paths 'not very realistic' (p. 104). (5) Placebo: the paper's rule (2-year linear extrapolation, 4-year horizon) applied at every base year 1964-2007 gives forecast errors with SD 0.30 log points, i.e. 2.6 elasticity units (N = 44); excluding windows containing 1986-88, 1992-93 or 2012-13, the SD is 2.9 (N = 30). This is indicative only: it pools all windows, not just post-trough ones. (6) The text (p. 104) says 2011-15 growth was 'only very slightly lower' than in 2009-11. It was 22% lower in pp/yr (0.60 vs 0.76) and 29% lower in log terms, and 37% and 42% lower on final data.

Why this severity. The headline elasticity and the 20% ceiling rest on an unvalidated identifying assumption. Changing that assumption within the paper's own framework moves the loss from below zero to well above 20%, so the magnitude is materially uncertain. No defensible variant reverses the finding that the lasting response is smaller than short-run retiming, but several put the loss far above 20%.

The authors' response. Pp. 73, 99-104 and 114. The medium-term elasticity is 'not as compellingly identified as the short-term elasticity', and the benchmark estimates 'have large implicit confidence intervals'. Negative elasticities from flatter trends are judged unrealistic. A large elasticity would require 'a very aggressive path of growth for the top 1%, which is not very realistic in light of the moderate growth path of top income shares from 2009 to 2011'.

Why it matters, in detail. The 'first two years of recovery' rule is validated on n = 2 episodes. For the 1990s, the stated window under-predicts the 2000 share by 8.6 pp, and only a window chosen after the 1993 reform's retiming fits. The validation therefore cannot discriminate between the paper's 0.76 pp/yr counterfactual and the faster (about 1.2-1.3 pp/yr) paces observed in those same recoveries, which would imply eM of about 1 (see F2).

Evidence. Adjudicator (scripts/adj_reproduce.py, validation block). 1992-94 slope -0.22 pp/yr: predicts 13.4% for 1998 and 12.9% for 2000, against actual 19.1% and 21.5%. 1991-93 slope +0.44: predicts 17.3% for 2000. 1994-96 slope +1.23: predicts 19.1% (1998) and 21.6% (2000), close to actual. 2002-04 slope +1.44: predicts 22.6% (2006) vs 22.8% and 24.1% (2007) vs 23.5%; this window spans the 2003 JGTRRA cuts in dividend, capital-gains and top ordinary rates.

Why this severity. Removes much of the stated empirical support for the identifying assumption behind C3 and C4: one clean validation episode remains, plus one with a post-hoc window. It does not by itself change the point estimate.

Why it matters, in detail. For dtau = 7.3 points on tau0 = 32%, the second-order term is not negligible. The exact loss ratio a*tau1*(1-q^e)/dtau, with q = (1-tau1)/(1-tau0) = 0.892, exceeds e*a*tau0/(1-tau0) by about 28% at e = 0.26. A state fiscal externality of a*e*tau_s/(1-tau) adds about 4-5 points. Direction: the paper's 19% understates the loss. Do not stack this mechanically with F1 and F5.

Evidence. Adjudicator, with the paper's eM = 0.264 and a = 1.5 (scripts/adj_reproduce.py). First-order formula at tau0: 18.8%. At the midpoint rate: 22.1%. Valuing lost income at tau1, e*a*tau1/(1-tau0): 23.1%. Exact discrete formula a*tau1*[1-((1-tau1)/(1-tau0))^e]/(tau1-tau0): 24.1% (39.8% with final-data eM). Adding a 5% state rate to tau0: 23.5%. The Policy Impacts entry that reuses Saez's FE = -0.19 itself adds a 5% state tax and averages pre- and post-reform fiscal externalities.

Why this severity. Raises the paper-data loss by 3-5 points, to 22-24%; each variant alone exceeds the stated ceiling. The effect is modest next to F1-F2, and the paper labels the calculation an illustrative first-order approximation.

The authors' response. P. 112: 'our computations should be seen as an illustrative first-order approximation capturing the most important aspects of the reform and its behavioral responses.'

Why it matters, in detail. Under the paper's own premise that the reform leaves the bottom 99% unaffected, the elasticity needed for the revenue formula is d log(T/B)/d log(1-tau) = e_share/(1-s). That gives eM = 0.34 (paper data) or 0.57 (final data), and eS = 1.47. If the reform did lower bottom-99% incomes (spillovers), neither normalisation is clean. The direction is upward for all estimates, so the short-run 'lower bound' label survives, but the medium-run loss is understated.

Evidence. Adjudicator, log-odds normalisation (scripts/adj_reproduce.py). eS: top 1% 1.155 -> 1.470; top .1% 1.84 -> 2.06. eM: 0.264 -> 0.340, loss 18.8% -> 24.2%. On final data, eM 0.442 -> 0.567 (loss about 40%). The paper's statement that eS is 'very likely below 1.5' for the top 1% (p. 97) also fails: about 1.9 with the 2009-11 trend in this normalisation, against ASN panel estimates of 2.6 (top .1%) and 0.9 (P99-99.9).

Why this severity. Raises the medium-run elasticity by about 29% and the paper-data loss by about 5 points, enough to cross 20%. But it is a normalisation choice the paper flagged, and it strengthens rather than weakens the short-run conclusion.

The authors' response. Endnote 16 (p. 117): 'An alternative would be to use as denominator the share of income going to the bottom 99%, which would purge the denominator of tax effects. We stick to using top income shares for simplicity.'

Why it matters, in detail. Group-level co-movement of deductions and reported income cannot separate individual retiming of gifts from composition (re-ranking) effects. The long-run parallelism is a joint test of no avoidance, a near-zero long-run price elasticity (1970s top rates of 50-70% made giving far cheaper), stable generosity and stable composition. It rejects 'real 1970s shares as high as today' (a roughly two-fold discrepancy). It has little power against reporting changes of 10-30% of top income, the range at issue in the Auten-Splinter debate.

Evidence. Adjudicator, from the author's data-charitable sheet (scripts/giving_ratios.py). Top-1% giving/income was 3.4-3.6% in 1974-78 and 3.8% in 2014. Normalised giving rose by a factor of 2.54-2.64, while the top-1% share rose by 2.35-2.42; the text says 'exactly the same factor of 2.4', and its 'mid-1970s 33%' is actually 30.9-32.1%. Auditor B built a counterexample in which re-ranking of under-reporters makes both series rise by the same factor with no change in true inequality. However, P90-99 giving/income is stable (about 2.0% in 1974-78, 2.1% in 2014), whereas a re-ranking story predicts elevated 1970s ratios just below the top 1%. The counterexample therefore establishes non-identification but is not supported by the data. The evidence does reject the extreme scenario the paper sets up (true 1970s top shares as high as today's), which would imply 1970s giving/reported-income ratios roughly double today's. It cannot exclude moderate reporting-driven changes.

Why this severity. Affects a secondary, interpretive result that the paper uses against the tax-avoidance critique of top-share series. It does not affect C1-C4.

The authors' response. Endnotes 22-24 (p. 117): few top earners hit the deduction caps; accumulation inside closely held firms does not prevent giving; and the alternative that generosity rose in tandem with falling avoidance 'looks like a stretch'.

Why it matters, in detail. Under pure one-year shifting with a constant counterfactual, dlog(s2013/s2012) is about -2x/c. The shifted flow is then (eS/2)*c*|dlog(1-tau)|, and the loss is eS*a*dtau/[2(1-tau)], about 9.4%; equivalently, the response of 2013 income relative to its no-reform path is about half of eS (about 0.58). Under trend counterfactuals the 2012 excess and 2013 shortfall are unequal (2.42 vs 1.17 pp), which implies multi-year shifting. That could depress 2014-15 and bias eM upward.

Evidence. Adjudicator (scripts/adj_reproduce.py, short_run block). Under the constant-share benchmark, x/c = (22.83 - 20.01)/(22.83 + 20.01) = 6.6%, giving a short-run loss of 9.4-9.9% rather than 18.7%. The '11%' figure matches the 2012 excess over the 2009-11 trend (2.42 pp, 11.4% of the 2013 trend value). On that same trend, however, the 2013 shortfall is only 1.17 pp (5.5%), so at most about half of the 2012 excess can have come out of 2013. If the whole 2012 excess was pulled from 2013 and later years, the loss is about 17%.

Why this severity. A factor-of-two translation error in secondary quantities, but in the conservative direction. Correcting it lowers the short-run revenue cost, which reinforces C4, and leaves the eS estimate (a two-year contrast) unchanged. Auditor B rated it major; it is downgraded here because it does not undermine any core finding.

Why it matters, in detail. These are framing claims. The 1993-vs-2013 ranking depends on the margin (labor vs capital) and on bracket thresholds. The growth comparison is an uncontrolled before/after correlation and carries no information about the elasticity.

Evidence. Auditor A, applying the paper's Table 1 method to the 1992 income composition: +7.5 points in 1993 (+8.9 including 1994), against +7.3 in 2013. Adjudicator note: that calculation assumes the whole top 1% faced 39.6% in 1993, but the bracket started at $250k of taxable income, so the true 1993 average was somewhat lower; the comparison is metric-dependent either way. Bottom-99% real income growth (scripts/bottom99_growth.py), paper vintage: +0.7% in 2013, +2.1% in 2014 and +3.9% in 2015; 2014-15 later revised to +2.7% and +2.9%. The descriptive ranking roughly holds, but 2013 itself was weak and the causal reading is post hoc.

Why this severity. Rhetorical overstatements outside the estimates; they change no number in Tables 1-3.

Why it matters, in detail. Cumulatively negligible for the estimates: the payroll-share correction changes the top-1% post-reform MTR by about 0.1 point. The others are text-table mismatches and cross-reference errors.

Evidence. Workbook cells Table 1!D22 = 1-(1+D7/2-(D15+D7+D19))/(1+D7/2) and E22 = E15+E7+E19; IRS Pub. 15 (2013): 'There is no employer share of Additional Medicare Tax'. Correcting (a) moves eM only from 0.264 to about 0.260. Table 2!C31 = 0.376. data-charitable rows 58 and 61: 0.009*I/M = 2.473% and 2.512%. data!N,O rows 56-58. Giving ratios from scripts/giving_ratios.py. WP text line: 'Memo: wages and salaries (SSA data) 0.43 0.17 0.88 1.28'.

Why this severity. Presentation and transcription slips, none of which changes a conclusion (the largest moves eM by 0.004).

Why it matters, in detail. Shifting income between NIIT-liable and NIIT-exempt pass-through income changes revenue by tau_NIIT times the shifted amount, with no change in reported income, so e*a*tau/(1-tau) misses it. At ASN magnitudes (under $1bn a year) it adds well under 1 point to the loss ratio. ASN's panel elasticities group taxpayers by multi-year average income, so they are not like-for-like with the cross-sectional shares.

Evidence. ASN, National Tax Journal 69(4). Table 3, p. 956: the elasticities above. Table 4 and fn. 35, p. 957: in the 2011-13 panel, passive S-corporation income fell by $6bn (top .1%) and $5bn (P99-99.9). P. 958: about a third of predominantly-passive filers switched to predominantly active. Adjudicator scale check: 3.8% x about $11bn is about $0.4bn a year, against roughly $85bn a year of mechanical revenue from the reform on the top 1% (0.073 x [$1.82tn - 1.63m x about $0.40m]), i.e. about 0.5%.

Why this severity. A real avoidance margin outside the estimator, but its revenue scale is about 0.5% of mechanical revenue, and the larger panel short-run elasticities reinforce C2. Auditor B rated it moderate; it is downgraded because the quantified impact on C4 is small and the paper acknowledges the channel.

The authors' response. P. 115 and endnote 28: Saez cites ASN, calls the S-corporation exemption 'a significant loophole in the health care tax law', and notes that ASN, 'like us', find large short-run elasticity estimates.