The Economic Consequences of Major
Tax Cuts for the RichDavid Hope, Julian Limberg
Working Paper 55
December 2020

III Working Paper 55

Hope, Limberg

LSE International Inequalities Institute
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Web site: www.lse.ac.uk/III@LSEInequalities© David Hope and Julian Limberg. All rights reserved.

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Abstract
This paper uses data from 18 OECD countries over the last five decades to estimate thecausal effect of major tax cuts for the rich on income inequality, economic growth, and unemployment. First, we use a new encompassing measure of taxes on the rich to identify instances of major reductions in tax progressivity. Then, we look at the causal effect of these
episodes on economic outcomes by applying a nonparametric generalization of the difference-in-differences indicator that implements Mahalanobis matching in panel data analysis.
We find that major reforms reducing taxes on the rich lead to higher income inequality as
measured by the top 1% share of pre-tax national income. The effect remains stable in themedium term. In contrast, such reforms do not have any significant effect on economic growthand unemployment.
Keywords: Tax cuts for the rich, income inequality, growth, unemployment, difference-indifferences, Mahalanobis matching3III Working Paper 55

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1. Introduction
Recent years have seen a resurgence in academic research on income inequality, driven by
the influential body of work by Piketty and co-authors charting the evolution of top incomesin the advanced economies over the course of the 20th century (Alvaredo et al., 2013;
Atkinson et al., 2011; Piketty, 2014). A central finding from that literature is that while top
incomes fell for several decades after the Second World War, they turned a corner and began
rising, most dramatically in the Anglo–Saxon economies, from the 1980s onwards (Alvaredo
et al., 2013; Atkinson and Piketty, 2007). Correlational evidence from cross-country panel
studies has found that lower taxes on the rich, especially top marginal income tax rates, arestrongly associated with rising top incomes over this period (Huber et al., 2019; Piketty et al.,2014; Roine et al., 2009; Volscho and Kelly, 2012). Although, studies exploring the effects ofindividual tax reforms paint a less clear picture, with some finding persistent effects on income
inequality (Rubolino and Waldenström, 2020) and others only short-term effects (Saez,
2017).
Proponents of tax cuts for the rich often argue for their beneficial effects on economic
performance. In fact, this line of reasoning, focusing on efficiency gains and the reduction of
behavioural distortions, was central to the arguments made for major tax reforms in the US(Auerbach and Slemrod, 1997; Bartels, 2005; Gale and Samwick, 2017). There are few
empirical studies exploring the relationship between taxes on the rich and economic
performance, however, and the evidence we do have is mixed. While some cross-country
empirical studies find higher top marginal income tax rates and tax progressivity adversely
affect economic growth (Gemmell et al., 2014; Padovano and Galli, 2002), a number of otherstudies find no significant association (Angelopoulos et al., 2007; Lee and Gordon, 2005;
Piketty et al., 2014).
Given the lack of consensus in existing studies and the difficulties of drawing causal
conclusions from macro-level panel data analyses, it remains an open empirical question
how cutting taxes on the rich affects economic outcomes. In this paper, we use data from 18
OECD countries covering the last fifty years to investigate the effects of major tax cuts for therich on income inequality, economic growth, and unemployment. We contribute to the existing
empirical literature in two ways: first, we use a newly constructed, comprehensive measureof taxes on the rich to identify years in which major tax cuts occurred across a wide range ofadvanced economies; and second, we move beyond correlational evidence on the economic

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effects of taxing the rich by applying a novel matching method that allows for the estimationof causal effects from time-series cross-sectional data.
Our approach to identify major tax cuts utilises a newly constructed indicator of taxes on therich (Hope and Limberg, 2020). The indicator was developed using Bayesian latent variable
analyses covering a wide range of taxes and indicators, which allows for the comparison oftaxes on the rich across countries and over time. We code major tax cuts as years in which
the index fell by over 2 standard deviations. Across our sample of 18 OECD countries from1965 to 2015, this provides us with 30 country-year observations where taxes on the richwere significantly reduced.
Our empirical identification strategy relies on our binary variable for major tax cuts for therich, which permits us to apply a nonparametric generalization of the difference-in-differencesindicator for panel data analysis (Imai et al., 2020). The technique uses Mahalanobis
matching to compare treated and untreated units that have similar treatment histories andpre-treatment covariate trajectories. Furthermore, the methodology allows for explicit checksof covariate balance. We use this approach to estimate the causal effect of major reductions
in taxes on the rich on income inequality, economic growth and unemployment. We obtain
estimates of the cumulative effects for up to half a decade after the reform, so can also assess
the extent to which effects persist over time.
Our results show that, for both matching methods, major tax cuts for the rich increase the top
1% share of pre-tax national income in the years following the reform (𝑡 + 1 to 𝑡 + 5). The
magnitude of the effect is sizeable; on average, each major reform leads to a rise in top 1%
share of pre-tax national income of 0.8 percentage points. The results also show that
economic performance, as measured by real GDP per capita and the unemployment rate, is
not significantly affected by major tax cuts for the rich. The estimated effects for thesevariables are statistically indistinguishable from zero, and this finding holds in both the shortand medium run.
Our findings align closely with the existing correlational evidence showing that tax cuts forthe rich are associated with rising top income shares (Atkinson and Leigh, 2013; Huber et al.,2019; Piketty et al., 2014; Roine et al., 2009; Volscho and Kelly, 2012). We make an important
contribution to this literature, however, as our empirical strategy allows for the estimation of
causal effects. This is particularly pertinent in this case, as there is a large political science
literature on the power of rich voters and organised business interests to shape public policies
5III Working Paper 55

Hope, Limberg(incl. tax policies) in their favour (Bartels, 2009; Emmenegger and Marx, 2019; Gilens, 2005;
Hacker and Pierson, 2010; Svallfors, 2016), which suggests reverse causality could be amajor issue in empirical studies lacking a clear identification strategy.
Existing causal evidence is limited to one study. Rubolino and Waldenström (2020) utilise thesynthetic control method and find that three major reductions in top marginal income tax rates
in Australia, New Zealand, and Norway had lasting and large positive effects on top income
shares. We build upon this study by identifying major reductions in tax progressivity using amore comprehensive measure of taxes on the rich that goes beyond income tax progressivity.
We also look at all major reductions in taxes on the rich across 18 advanced economies from1965 to 2015, which allows us to draw stronger and more generalizable conclusions.
Our findings on the effects of growth and unemployment provide evidence against supplyside theories that suggest lower taxes on the rich will induce labour supply responses fromhigh-income individuals (more hours of work, more effort etc.) that boost economic activity(see standard models of optimal labour income taxation in Piketty and Saez, 2013 and Saez,
2001). They are, in fact, more in line with recent empirical research showing that income tax
holidays and windfall gains do not lead individuals to significantly alter the amount they work
(Akee et al., 2010; Jones and Marinescu, 2018; Martinez et al., 2018).
Overall, our analysis finds strong evidence that cutting taxes on the rich increases income
inequality but has no effect on growth or unemployment. We do not directly test mechanisms
in our analysis, but using a measure of top 1% share of pre-tax national income that includes
both labour and capital income makes it less likely that tax shifting and avoidance are driving
the results. Our results are in line with those in Piketty et al. (2014), which suggest that lower
taxes on the rich encourage high earners to bargain more forcefully to increase their own
compensation, at the direct expense of those lower down the income distribution.
The remainder of the paper proceeds as follows. Section 2 sets out our approach for
identifying major tax cuts for the rich and presents a visualisation of the resulting binary
variable. Section 3 presents the data, empirical strategy, and results for our analysis of theeffects of major tax cuts for the rich on income inequality. We turn our attention to the effects
on growth and unemployment in Section 4, before carrying out a series of robustness tests
in Section 5. Finally, Section 6 provides some concluding remarks.

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2. Identifying major tax cuts for the rich
Many empirical studies look at single tax policy indicators to identify tax cuts for the rich.
However, there is some disagreement on measuring taxes on the rich in the literature. First,
there is no consensus on which taxes to look at. Whilst some authors look at taxes on
personal income (Egger et al., 2019; Rubolino and Waldenström, 2020), others focus on
corporate taxation (Devereux et al., 2002) or inheritance taxation (Piketty and Saez, 2013b).
Second, economists have used different tax policy indicators. Some look at top marginalincome tax rates (Piketty et al., 2014), while others look at effective tax rates (Egger et al.,2019) or revenue generation (Baunsgaard and Keen, 2010). We propose an encompassing
approach that utilises Bayesian latent variable analysis on a range of different taxes andindicators to overcome these problems. This allows us to detect shared variance across 7
indicators that are commonly used proxies for taxes on the rich (see Table A1 in the
Appendix). In total, the data cover 18 OECD democracies over 5 decades (1965-2015). We
estimate the latent variable using a Bayesian Markov-Chain Monte Carlo (MCMC) approachwith diffuse normal priors, three MCMC chains and 1000 burnin iterations (for more
information on the estimation of the latent variable, see Hope and Limberg, 2020).
Figure 1 shows the development of the taxing the rich indicator in the sample.1 In line withother empirical studies that have found substantially declining taxes on the rich in the last
decades (Egger et al., 2019; Scheve and Stasavage, 2016), the indicator decreases
substantially from the mid-1980s onwards. From the late 1960s to the end of the 1990s, theaverage value of the latent variable for taxes on the rich across the sample dropped by morethan 30%. Furthermore, the cross-sectional standard deviation of the indicator steadily
declined from the late 1960s. This indicates that tax policies on the rich have converged
among OECD countries over time.

1

See Figure A1 in the Appendix for country-specific time series.

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Figure 1. Latent variable for taxes on the rich, 18 OECD countries, 1965-2015

Source: Authors’ calculations; Hope and Limberg (2020).

In a second step, we use the latent variable to detect major tax cuts for the rich. We calculate
country-specific first-differences of the indicator and define major tax cuts as years in which
the indicator drops by at least 2 standard deviations. Since we are interested in the effects ofmajor tax cuts for the rich, this high threshold is in line with our theoretical focus. Furthermore,
two standard deviation shocks are often employed in the empirical literature in
macroeconomics (Dell’ Erba et al., 2015; Fernández-Villaverde et al., 2015) and this size
threshold is in line with the size of tax and spending changes identified in the literature
exploring the effects of large fiscal policy adjustments on economic outcomes (Alesina andArdagna, 2010; Blanchard and Perotti, 2002).
Figure 2 visualises the resulting binary variable that picks out years in which taxes on the richwere reduced substantially.2 In total, we identify 30 country-year observations where taxes
on the rich were significantly reduced. Governments enacted major tax reforms in all
countries in our sample and across the whole observation period. Many countries
implemented major tax cuts for the rich in the late 1980s. Furthermore, the identification of2

Figure A2 in the Appendix shows how changes in the latent variable translate into the binary variable of major
tax cuts based on the 2 standard deviations threshold.

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tax cuts is also in line with previous studies that have focused on income tax progressivity(Rubolino and Waldenström, 2020) or on overall tax progressivity single specific countries(Saez and Zucman, 2019). For instance, echoing these authors’ findings, we find two major
reforms that reduced taxes on the rich in the US: 1982 (First Reagan Tax Cut) and 1986/1987(Second Reagan Tax Cut).

Figure 2. Distribution of major tax cuts for the rich, 1965-2015
United States
United Kingdom
SwedenNew Zealand
Italy
Netherlands
Germany
CanadaAustralia
NorwayJapan
IrelandFinlandDenmark
Belgium
Austria
Switzerland
FranceSource: Authors’ calculations.

3. The effect on income inequality of major tax cuts for the rich
Our empirical design leverages variation in tax reform timings to estimate effects of cutting
taxes on the rich on income inequality. Let us consider classical approaches of estimating
causal effects for time-series cross-sectional data with 𝑁 countries and 𝑇 years. Up to date,most analysis of panel data rely on linear regression techniques with two-way fixed effects
and control variables. Such models typically take the following form:

4

𝑌*+ = 𝛼* + γ+ + 𝛽1 𝑋*+ +(𝛽3 𝑋3*+ ) + 𝜀*+
356

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(1)

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for 𝑖 = 1, … , 𝑁 and 𝑡 = 1, … , 𝑇 and where 𝑌*+ denotes our main outcome variable and incountry 𝑖 and year 𝑡 and 𝛽1 is the estimated effect of the binary variable 𝑋*+ , which measures
major tax cuts for the rich. 𝛼* is the unobserved time-invariant country-specific effect and γ+
is the unobserved year-specific effect.

4356(𝛽3 𝑋3*+ )denotes a set of 𝐾 time-varying

covariates and 𝜀*+ is the error term. Using such an approach to estimate the causal impact ofmajor tax reforms that cut taxes on the rich on income inequality creates three methodologicalchallenges. First, the effect of reforms might vary over time. However, Equation 1 requires
the researcher to specify a lag of the treatment registration. For instance, Equation 1 would
estimate the contemporaneous reform effect (𝑡 + 0). Second, related to this, the standard
approach does not account for previous reform trajectories. Put differently, if 𝛽1 ≠ 0 for 𝑋*,+>? ,where 𝑛 ∈ ℕ, estimating the effect of tax reforms might run danger of being biased due toprevious reform trajectories (Rubolino and Waldenström, 2020). Thus, we need to compare
cases with similar reform trajectories. Third, reforms do not come at random. Instead, politicaland economic factors might make reforms more likely, and these factors can also affectsubsequent income inequality dynamics. Furthermore, the practice of adding potential
confounders as covariates like in Equation 1 does not allow for the assessment of covariatebalance.
To deal with these challenges to causal identification, we use a new econometric approachthat implements a nonparametric generalisation of the difference-in-differences indicator forpanel data analysis (Imai et al., 2020). This technique compares units with a major tax reform
in a respective year (treated units) with units that have a similar pre-treatment trajectory oftax reforms but have not enacted a tax cut in the same year (control units). Furthermore, themethod allows us to estimate how the treatment effects evolves over time. Most importantly,
Imai et al. (2020) introduce 𝐹, which denotes the number of years after a tax reform, and 𝐿,
which denotes the amount of lags prior to the treatment. Specifying 𝐹 allows the researcher
to estimate varying treatment effects over time. For instance, setting 𝐹 = 5 measures the
cumulative treatment effect for 5 years after a major tax cut for the rich. In contrast, 𝐿 allows
the researcher to adjust for treatment histories, e.g. 𝐿 = 5 adjusts for the treatment history up
5 years prior to the treatment. As a consequence, the average treatment effect on the treated(ATT) takes the following form,

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H𝛿 𝐹, 𝐿 = 𝔼 𝑌*,+EF 𝑋*+ = 1, 𝑋*,+>6 = 0,

𝑋*,+>ℓℓ5I
H− 𝑌*,+EF 𝑋*+ = 0, 𝑋*,+>6 = 0,(2)

𝑋*,+>ℓ | 𝑋*+ = 1, 𝑋*,+>6 = 0ℓ5I

where countries that experience a major tax cut in year 𝑡 are the treated unit, hence 𝑋*+ = 1
as well as 𝑋*,+>6 = 0. Hence, 𝑌*,+EF 𝑋*+ = 1, 𝑋*,+>6 = 0,H
ℓ5I 𝑋*,+>ℓis the potential outcome forcountries that have enacted a major tax cut and 𝑌*,+EF 𝑋*+ = 0, 𝑋*,+>6 = 0,H
ℓ5I 𝑋*,+>ℓis thecounterfactual potential outcome. We are interested in the cumulative effect up to 𝐹 years
after a tax reform and adjust for treatment histories up to 𝐿 years prior to a tax reform.
Unfortunately, the counterfactual outcome for treated countries, i.e. 𝑌*,+EF 𝑋*+ = 0, 𝑋*,+>6 =H

0, 𝑋*,+>ℓ ℓ5I | 𝑋*+ = 1, 𝑋*,+>6 = 0, cannot directly be observed. Thus, we have to takepotential outcome for countries without a major tax cut for the rich instead.

H𝛿 𝐹, 𝐿 = 𝔼 𝑌*,+EF 𝑋*+ = 1, 𝑋*,+>6 = 0,

𝑋*,+>ℓ | 𝑋*+ = 1, 𝑋*,+>6ℓ5I
H= 0 − 𝑌*,+EF 𝑋*+ = 0, 𝑋*,+>6 = 0,

𝑋*,+>ℓ | 𝑋*+ = 0, 𝑋*,+>6 = 0

(3)

ℓ5I

However, tax cuts are not random. In particular, observed confounders,

4356(𝑋3*+ ), as wellas unobserved confounders can lead to biased results. Thus, we use a difference-indifferences estimator as well as nonparametric matching techniques for additional timevarying covariates (Imai et al., 2020 p. 14). Matching is an intuitive and powerful tool to deal
with selection into treatment (Diamond and Sekhon, 2012; Ho et al., 2007). In contrast to
adding confounders as covariates like in Equation 1, it is less prone to modelling decisions
and allows for the assessment of covariate balance. Furthermore, the difference-indifferences estimator relaxes the unconfoundedness assumption, but crucially assumes aparallel trend in the outcome variable after adjusting via matching on the previous treatment
history,Hℓ5I 𝑋*,+>ℓ , as well as on the covariate trajectory,Hℓ51

to explicitly check whether the parallel trend assumption holds.
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We use the block-bootstrap procedure proposed by Imai et al. (2020) to calculate standard
errors. Following Otsu and Rai (2017) and Imbens and Rubin (2015), this approachcircumvents the inference problems caused by standard bootstrapping procedures formatching by calculating the weight that each observation gets in the matching procedure.
This weight-variable is used as a conditioning factor and is not recomputed in thebootstrapping procedure (Imai et al., 2020, p. 20).
Our main treatment variable is therefore the presence of a major tax cut for the rich. The
first dependent variable we look at is income inequality, as measured by the top 1% share of
pre-tax national income.3 This measure includes both labour and capital income. Data comefrom the World Inequality Database (Alvaredo et al., 2018) and are calculated fromadministrative tax sources using a common methodology, so allow for comparison over timeand across countries (Atkinson et al., 2011; Roine and Waldenström, 2015). Top income
shares are also used in many existing studies looking at the relationship between taxes on
the rich and income inequality (Huber et al., 2019; Piketty et al., 2014; Roine et al., 2009;
Rubolino and Waldenström, 2020; Volscho and Kelly, 2012). We start by estimating thecausal effect of major tax cuts for the rich on inequality while solely matching on the treatment
trajectory. We match units based on a 5-year pre-treatment window (i.e. 𝐿 = 5). Only 1
observation could not be matched to control units with a similar treatment trajectory (see also,
Figure A3 in the Appendix). Figure 3 visualises the matching approach by looking at four
exemplary cases of major tax cuts and the matched-on control groups.

3

There are some missing data points for top income shares (less than 10% of cases). In these cases, we haveused an exponentially weighted 5-year moving averages interpolation procedure.

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Figure 3. Visualisation of the matching approach, using four major tax cuts as
examples

Source: Authors’ calculations.

Figure 4 shows the treatment effect after matching on the previous treatment trajectory. In
order to differentiate between short- and medium-term effects of tax cuts for the rich, we lookat the effects for up to 5 years after the reform (i.e. 𝐹 = 5). For each year, the graph displays
the cumulative treatment effect and 95% confidence intervals. The results show that major
tax cuts lead to a significant increase in inequality and that this effect becomes stronger withtime. Three years after the reform, the top 1% income share increases by almost 0.6
percentage points in countries with a major tax cut. Over five years, tax reforms increase the
top 1% share of pre-tax national income by more than 0.8 percentage points. This effect ishighly statistically significant, with P<0.0001. Furthermore, the graph also shows a placebo
test by estimating the effect of tax cuts in the years before the reform. These placebo models
test whether there have been significant different trajectories of inequality development in the

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countries with and without a major tax cut prior to the reform.4 The point estimates of theplacebo tests are close to zero and statistically insignificant. In other words, the findings show
strong support for the parallel trends assumption that underlies the difference-in-differences
estimator.

Figure 4. Effect of major tax cuts for the rich on top 1% income shares after matchingon treatment trajectory

Source: Authors’ calculations.

In a second step, we match units with a similar treatment history and with similar covariate
trajectories. We match on a battery of time-varying covariates, covering economic factors,
such as real GDP per capita (in 2011 US dollars), capital openness via the Chinn-Ito Index(Chinn and Ito, 2006), and trade openness (imports and exports as % of GDP), as well as
political factors like the vote share of leftist parties and government expenditure (as % ofGDP). Table A2 in the Appendix shows the different covariates and their data sources. We
choose a matching approach that is based on the Mahalanobis distance as opposed topropensity score matching, as recent studies have found that the latter can be inefficient andcreate model dependency (King and Nielsen, 2019). Similar to the previous analysis, we
4

Since the model calculates the first differences in relation to the year before the tax reform (i.e. t-1), the effectis 0 for this year.

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match upon 5-year pre-treatment windows. Importantly, matching on pre-treatment values
has the advantage that we do not have a problem with post-treatment bias.
Unlike multivariate regression analysis, the matching approach allows us to assess
improvements in covariate balance. Figure 5 visualises the covariate balance by comparing
standardised mean differences of the covariates before and after matching on the
Mahalanobis distance. Before matching, several variables showed significant imbalance withstandardised mean differences beyond the commonly accepted threshold of 0.25
(Rosenbaum and Rubin, 1985). After matching, the standardised mean differences no longer
exceed this threshold.

Figure 5. Standardised mean difference of covariates before and after matching

Source: Authors’ calculations.

When rerunning the difference-in-differences model after matching on both pre-treatment
treatment trajectories and covariate history, our results hold (Figure 6). Reforms that reducetaxes on the rich have a substantial short- and medium-term effect on the top 1% share of
pre-tax national income. On average, such reforms increase the top 1% income share bymore than 0.8 percentage points after 5 years. We run placebo tests by estimating the effectof major tax reforms on pre-treatment changes in inequality. In line with the previous findings,
the parallel trend assumption holds. The point estimate for the time periods 4 and 5 years
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prior to the treatment are negative (around 0.2 percentage points), but fail to reachconventional levels of statistical significance.

Figure 6. Effect of major tax cuts for the rich on top 1% income shares after matchingon treatment trajectory and covariates

Source: Authors’ calculations.

4. The effect on economic growth and unemployment of major tax cutsfor the rich
Let us now turn to the effect of major tax cuts for the rich on economic growth andunemployment. First, we analyse whether such reforms boost growth by looking at the effecton real GDP per capita. In line with other studies, we look at logged real GDP per capita(Piketty et al., 2014; Rubolino and Waldenström, 2020). Again, we estimate the ATT by using
a nonparametric generalisation of the difference-in-differences estimator. Like in the previous
section, we match upon the treatment trajectory, as well as on an additional battery ofcovariates via the Mahalanobis distance. Models are matched upon 5-year pre-treatment
windows and we look at the effects of up to 5 years after the tax reform. Again, we use theblock-bootstrap procedure designed by Imai et al. (2020) to calculate standard errors for
TSCS matching.
Figure 7 presents the results. The left panel shows the model without covariates. The
results suggest that tax reforms do not lead to higher economic growth. The effect size of16

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major tax cuts for the rich on real GDP per capita is close to zero and statistically insignificant.
The findings are very similar when matching upon pre-treatment covariate trajectories (rightpanel). Major tax cuts for the rich do not lead to higher growth in either the short or mediumrun. Furthermore, we do not find any effect of tax cuts on pre-treatment changes. Thus, theparallel trend assumption holds. We also calculated the same model by replacing (log) real
GDP per capita with the real GDP per capita growth rate. Again, we find no significant effectof tax reforms on changes in GDP per capita growth (see Figure A5 in the Appendix).

Figure 7. Effect of major tax cuts for the rich on (log) real GDP per capita after matchingon treatment trajectory (left panel) and treatment trajectory and covariates (right panel)

Source: Authors’ calculations.

Let us now look at the effect of major tax cuts for the rich on unemployment. To ensure crossnational comparability, we use harmonised unemployment rates as provided by the OECD
(2020a). Figure 8 shows the results. In general, we see more fluctuation in the estimates. In
the years right after the tax reform, the point estimate becomes negative. In the medium term,
the estimate becomes close to zero again. However, none of these estimates is significant at
the 0.05 level. Furthermore, we can see slight fluctuation in the development of
unemployment rates prior to the tax reform. Whilst the placebo estimate for the 𝑡 − 5 time
period is negative, yet statistically insignificant, unemployment grew slightly faster in the year
prior to the reform. However, these placebo tests do not show indications of a clear pre17

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treatment trend. In sum, although the results show very slight indications of a flash in the pan
effect of tax cuts for the rich on unemployment, these findings are neither statisticallysignificant nor robust.

Figure 8. Effect of major tax cuts for the rich on unemployment rates after matchingon treatment trajectory (left panel) and treatment trajectory and covariates (right panel)

Source: Authors’ calculations.

5. Robustness checks
We run several alternative specifications to check whether our results are robust. First, weapply a lower threshold of 1 standard deviation to detect major tax cuts for the rich. Using a
1 standard deviation threshold means that we include tax cuts of smaller magnitude. Hence,
it is a more conservative approach of testing the impact of tax cuts on economic outcomes.
Figure 9 visualises the effects on inequality, economic development, and unemployment.5
The findings hold when using this alternative threshold. Cutting taxes for the rich increases
the top 1% share of pre-tax national income significantly and this effect persists over time.
The effect size decreases slightly. The new models using the lower threshold estimate thattax cuts lead to an increase of top 1% income shares by 0.5 percentage points. The smaller
effect size is unsurprising given the lower threshold for identifying major reforms.

5

Again, all models are calculated with 5-year lags and by matching on the Mahalanobis distance.

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Furthermore, we find no effect of tax reforms on real GDP per capita. When looking at theeffect on unemployment rates, the estimates show a slightly different pattern. Here, tax cutsfor the rich lead to slightly higher unemployment rates in the short term. However, this effectdoes not hold over time either. Hence, it supports our previous finding that the effects of tax
cuts for the rich on unemployment rates are not robust.

Figure 9. Effect of major tax cuts for the rich, 1 standard deviation threshold for tax
cuts

Source: Authors’ calculations.

Second, we check the robustness of our findings by changing the length of our time lags. So
far, we have calculated all models with 5-year lags. Choosing longer time lags has theadvantage that it reduces potential bias from long-term effects of confounders. However, italso makes it harder to find suitable matches. Thus, we check our results by running models
that use 1-year lags. This allows for more variance, but the findings are more vulnerable tobias. Figure 10 shows the results. In line with the previous analyses, tax cuts for the rich raise
top 1% income shares significantly by around 0.7 percentage points in the medium run. In
contrast, tax reforms do not lead to higher economic growth.6 We find a slightly negative
short-term effect on unemployment rates (𝑡 + 1). However, this effect disappears in themedium run (𝑡 + 2 to 𝑡 + 5).

6

The fact that this model matches on shorter time windows also leads to larger confidence intervals for theplacebo tests.

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Figure 10. Effect of major tax cuts for the rich, 1-year lag

Source: Authors’ calculations.

Third, we use a different matching technique. Instead of matching on the Mahalanobis
distance, we match on propensity scores (Rosenbaum and Rubin, 1985). Although somestudies have argued that propensity score matching is based on modelling assumptions andmight therefore increase bias compared to nonparametric matching procedures (King andNielsen, 2019), it is an intuitive and widely used matching approach (Caliendo and Kopeinig,2008). Figure 11 presents the results when matching on propensity scores.7 The results arevery similar to our main approach that matches upon the Mahalanobis distance. Whereas tax
cuts for the rich lead to higher income inequality, they do not have a robust effect on either
economic growth or unemployment rates.

Figure 11. Effect of major tax cuts for the rich, propensity score matching

Source: Authors’ calculations.

7

In line with the main models, we use 5-year lags again.

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6. Conclusion
This paper uses a two-stage process to estimate the causal effects of major tax cuts for therich on economic outcomes. First, we identify instances of major reductions in tax
progressivity by looking at substantial falls (greater than 2 standard deviations) in a new,comprehensive indicator of taxes on the rich that covers 18 OECD countries from 1965 to2015. Second, we apply a nonparametric generalization of the difference-in-differencesindicator that implements Mahalanobis matching in panel data analysis to estimate the causal
effect of major tax cuts for the rich on income inequality, economic growth, andunemployment.
We find that major tax cuts for the rich push up income inequality, as measured by the top
1% share of pre-tax national income. The size of the effect is substantial: on average, eachmajor tax cut results in a rise of 0.8 percentage points in top 1% share of pre-tax national
income. The effect holds in both the short and medium term. Turning our attention toeconomic performance, we find no significant effects of major tax cuts for the rich. Morespecifically, the trajectories of real GDP per capita and the unemployment rate are unaffectedby significant reductions in taxes on the rich in both the short and medium term.
Our results have important implications for current debates around the economic
consequences of taxing the rich, as they provide causal evidence that supports the growing
pool of evidence from correlational studies that cutting taxes on the rich increases top income
shares, but has little effect on economic performance (Lee and Gordon, 2005; Piketty et al.,2014; Roine et al., 2009). They also align with the causal findings in Rubulino andWaldenstrom (2020), but provide stronger and more generalizable conclusions, as ourapproach allows us to move beyond looking at tax changes in only handful of selected
countries.
There are several potentially fruitful avenues for future research that come out of our analysis.
While our choice of dependent variable (including both capital and labour income) makes itless likely the results are being driven by tax shifting or avoidance, we do not specifically test
the mechanisms at work. Follow up research could therefore assess whether themacroeconomic effects we find are being driven by the mechanism outlined in Piketty et al.
(2014), which is that lower taxes on top incomes induce the rich to bargain more aggressively
to increase their own rewards, to the direct detriment of those lower down the income
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distribution. The analysis could also be extended outside of the OECD to see if the findings
hold in countries with lower fiscal capacity. Lastly, from a policy perspective, it would also be
important to understand more about the extent to which individuals’ attitudes to taxing therich are influenced (or not) by the provision of new information about its economic
consequences.

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Appendices
Table A1. Indicators and data sources for the Bayesian latent variable analysis
Tax
type

Indicator

Time span

SourceIncomeTop personal income tax rate

1965-2015

Scheve & Stasavage (2016),
expanded by the authors forthe years 2011-2015.

IncomeEffective tax rate on top 1%
wage earners

1980-2007

Egger et al. (2019)

Income/Capital

Top tax rate dividend income

1981-1999;
OECD (2020b)
2000-2015

CapitalCorporate income tax rate

1965-2015

Lierse & Seelkopf (2016),
expanded by the authors forthe years 1965-1980 and2011-2015.

CapitalEffective tax rate on capital

1965-2015

McDaniel (2007)

AssetsTop inheritance tax rate

1965-2015

Scheve & Stasavage (2016),
expanded by the authors forthe years 2011-2015.

Assets

Revenue from taxes on
assets (inheritance, net
wealth, and property taxes,% of GDP)

1965-2015

OECD (2020b)

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Table A2. Covariates and data sources
Indicator

SourceTop 1% share of pre-tax national income

Alvaredo et al. (2018)

Harmonised unemployment rate (%)

OECD (2020a)

Real GDP per capita (in 2011 US dollars)

Penn World Table (Feebstra et al.,2015)

Capital account openness (Chinn–Ito Index)

Chinn & Ito (2006)

Trade openness (imports and exports as % of GDP)IMF (2020)

Government expenditure (as % of GDP)OECD (2019)

Left vote share in last election

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Figure A1. Latent variable for taxes on the rich, 18 OECD countries, 1965-2015

Source: Authors’ calculations; Hope and Limberg (2020).

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Figure A2. Changes in the latent variable for taxes on the rich and major tax cuts

Note: Country-year observations in red show tax cuts for the rich that exceed the 2 standard deviation threshold.
Source: Authors’ calculations.

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Figure A3. Distribution of number of matched control units

Source: Authors’ calculations.

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Figure A4. Distribution of major tax cuts for the rich, 1 standard deviation threshold, 19652015
Ireland
New ZealandUnited States
United Kingdom
CanadaNorwayJapan
Italy
FranceDenmark
Germany
FinlandSwedenNetherlands
Belgium
Austria
Australia
Switzerland

Source: Authors’ calculations.

Figure A5. Effect of major tax cuts for the rich on real GDP per capita growth rates after
matching on treatment trajectory (left panel) and treatment trajectory and covariates (rightpanel)

Source: Authors’ calculations.

33