# Payroll Tax Incidence: Evidence from Unemployment Insurance

Audrey Guo Santa Clara University. Contact<EMAIL_ADDRESS>I would like to
thank Katarzyna Bilicka, Maria Fitzpatrick, Tatiana Homonoff, John Ifcher,
Kris Mitchener, and seminar participants at Georgetown Law, UC Davis, Santa
Clara University, IIPF Annual Congress, and All-California Labor Conference
for helpful comments. Any views expressed are those of the authors and not
those of the U.S. Census Bureau. The Census Bureau’s Disclosure Review Board
and Disclosure Avoidance Officers have reviewed this information product for
unauthorized disclosure of confidential information and have approved the
disclosure avoidance practices applied to this release. This research was
performed at a Federal Statistical Research Data Center under FSRDC Project
Number 1632. (CBDRB-FY22-P1632-R9305-R9674) This research uses data from the
Census Bureau’s Longitudinal Employer Household Dynamics Program, which was
partially supported by the following National Science Foundation Grants
SES-9978093, SES-0339191 and ITR-0427889; National Institute on Aging Grant
AG018854; and grants from the Alfred P. Sloan Foundation.

(March 2023)

###### Abstract

Economic models assume that payroll tax burdens fall fully on workers, but
where does tax incidence fall when taxes are firm-specific and time-varying?
Unemployment insurance in the United States has the key feature of varying
both across employers and over time, creating the potential for labor demand
responses if tax costs cannot be fully passed on to worker wages. Using state
policy changes and matched employer-employee job spells from the LEHD, I study
how employment and earnings respond to payroll tax increases for highly
exposed employers. I find significant drops in employment growth driven by
lower hiring, and minimal evidence of pass-through to earnings. The negative
employment effects are strongest for young and low-earning workers.

##  1 Introduction

Employer taxes on labor earnings are used to fund a variety of social
insurance programs, and policymakers frequently view payroll tax cuts as a way
to stimulate employment. In the theory of tax incidence, the resulting
employment and wage change depends on the elasticities of labor demand and
labor supply; because labor demand is assumed to be much more elastic than
labor supply (especially in the long run), most models assume payroll tax
costs are born entirely by workers, resulting in little to no effect on
employment.111As evidenced by early estimates from Brittain (1971) and Gruber
(1997). However, there may be imperfect pass-through in the presence of
downward wage rigidities, leading to a decline in employment rather than
wages.222Using data from a large payroll processing firm, Grigsby et al.
(2021) find very low rates of wage cuts, providing strong evidence for
downward nominal wage rigidity. Using Census Bureau data, Murray (2021)
estimates that downward nominal wage rigidity accounted for at least 23% of
excess job destruction during the financial crisis of 2008. Hamermesh (1979)
points out that if the entire burden of a payroll tax could be shifted onto
wages, employers would not so vehemently oppose tax increases. Furthermore,
payroll tax changes that only affect a subset of firms may prevent employers
from fully passing costs through to wages.333Likewise, Saez et al. (2012) and
Saez et al. (2019) found that payroll tax changes only affecting a subset of
workers within a firm also failed to result in full pass-through.

In this paper, I exploit state Unemployment Insurance (UI) tax increases to
estimate payroll tax incidence in the United States. The third largest payroll
tax in the U.S., UI is an employer-specific and time-varying tax that is
administered at the state level. Employer tax rates are an increasing function
of the amount of UI benefits paid out to previous employees, and in 2010 and
2011, state-legislated UI tax increases raised the payroll tax costs for
highly exposed employers. I use administrative data from the US Census
Bureau’s Longitudinal Employer-Household Dynamics (LEHD) to study the impact
of these state tax increases on worker earnings and employment growth.

I identify a subset of highly exposed employers, defined as those with a
history of previous layoffs, and use a difference-in-differences research
design to compare the outcomes of employers based in treatment versus control
states. I estimate minimal pass-through of state tax increases to earnings,
and instead find negative impacts on employment growth. For each $100 increase
in payroll taxes per worker, employment growth declined by 0.43 percentage
points over the course of the year. Event study estimates found the largest
effects in the 2nd and 3rd year after the initial policy changes, which
suggest that UI tax increases hindered the economic recovery after the Great
Recession. These results are further confirmed using a triple-difference
research design that compares high exposure and low exposure employers within
the same state, to control for potential differences in state economic
conditions in the wake of the Great Recession.

I test whether this drop in employment growth is driven by increased
separations or reduced hiring, and find clear evidence of the latter. The
quarterly share of new hires fell by up to 0.2 percentage points for each $100
tax increase, while the effect on the separation share was small and
statistically insignificant. These findings align with firm tax incentives, as
each additional new hire would incur another instance of UI tax; on the other
hand, additional separations provide no UI tax savings, since low UI tax bases
cause most earnings to exceed the tax base by the end of the first quarter.
Heterogeneity analysis shows that the negative employment effects are stronger
for young (age under 25) and low-earning workers. Low-earning workers also
experienced larger drops to earnings growth than the average worker, but still
well below full pass-through. Additionally, single-establishment firms were
more likely to reduce hiring than multi-establishment firms, suggesting that
cash constraints may also play an important role.

The main contribution of this paper is providing a U.S. context to study
payroll tax incidence, as the lack of variation in federal payroll taxes has
caused US-based studies to be largely absent from the recent literature. Given
differences in labor market institutions, the estimates of tax incidence in
one country may not generalize in the same way to another. State-level UI tax
increases provide a setting similar to Ku et al. (2020), who found that
regional payroll tax increases in Norway lowered employment, because firms
were only partially able to pass the costs on to workers. Saez et al. (2021)
finds that the positive employment effects from a young workers payroll tax
cut persisted even after workers aged out of eligibility. Likewise, I estimate
a gradual and sustained decrease in employment growth due to payroll tax
increases. Benzarti and Harju (2021a) found that a payroll tax cut in Finland
helped treated firms weather the Great Recession despite having minimal impact
on employment beforehand, suggesting a cyclical component to firm responses.
My findings of a negative employment response to tax increases following the
Great Recession confirms the symmetry of this effect.

Another contribution is the estimation of heterogeneous effects across worker
and employer characteristics. Benzarti and Harju (2021b) found that firms with
greater payroll taxes substituted away from low-skilled and manual workers. I
find greater drops in labor demand for low-earning and young workers, but not
for those with less education. My finding that single-establishment firms were
especially likely to decrease hiring in response to higher UI taxes, is
consistent with the finding in Lobel (2021) that small firms were more
responsive to payroll tax cuts. Biró et al. (2022) estimate heterogeneity in
payroll tax incidence by firm productivity, finding that lower productivity
firms experienced employment responses while higher productivity firms passed
tax cuts on to workers. While I do not observe firm productivity, my sample of
high exposure employers likely overlaps with lower productivity firms, as they
suffered layoffs prior to the tax increases.

Finally, my paper contributes to the small literature on UI tax incidence by
revisiting the question using recent data and exogenous policy changes from
multiple states. Early studies by Anderson and Meyer (1997) and Anderson and
Meyer (2000) found evidence of pass-through for industry-specific UI taxes but
not employer-specific rates, although the variation in employer-specific rates
included both high and low exposure employers together. My findings also
complement the results in Johnston (2021), which found little effect of annual
changes in employer-specific rates on worker earnings, but large impacts on
hiring.

The next section provides institutional details on US Unemployment Insurance.
Section 3 describes the research design, and Section 4 discusses the data and
construction of my analysis sample. Section 5 presents the main employer-level
results, and Section 6 presents a worker-level analysis focusing on low-
earning workers. Section 7 concludes.

##  2 Institutional Background

Unemployment insurance in the U.S. is funded solely through payroll taxes on
employers.444With the exception of New Jersey, which also charges workers a
uniform payroll tax of 0.5%. Unlike Social Security or Medicare taxes, which
are uniform across all employers, UI is experience-rated and therefore
employer-specific. UI tax revenues reached a height of 1 percent of total
wages in 2012, but this masks considerable heterogeneity across employers.
Employers that lay off workers who then claim UI benefits are assigned a
higher future tax rate - up to a statutory maximum.555Guo and Johnston (2021)
provides a brief history of U.S. unemployment insurance, which was modeled
after the experience rating in workers’ compensation. Since its inception,
policymakers have recognized the tradeoff between disincentivizing layoffs,
and the cyclical tax burdens that dynamic experience rating would create.
These employer-specific rates are calculated annually, and Appendix Figure A.1
illustrates a sample tax schedule from the state of Florida, where the maximum
tax rate is capped at 5.4%. Appendix Figure A.2 plots total UI contributions
over time as a percentage of total wages, and reveals the cyclical pattern of
UI tax collections, where tax rates are highest in the years following
recessions. Due to this time-varying nature of UI tax rates, businesses may
have more difficulty passing the costs on to their workers, and changes in UI
tax liabilities have the potential to influence employment as well as
earnings.

Another unique aspect of UI is the low tax base in most states. Throughout the
last half-century, taxable wages have not kept up with inflation, leading to
an errosion of the tax base. In 2009, the year before the first UI tax
increases, the median UI tax base was only $10,000 – with the median state’s
taxable wages covering only 28% of total payroll. This low tax base causes UI
to become a lump-sum tax on workers, independent of earnings. Thus UI taxation
is regressive in the sense that seasonal, part-time, and low-wage workers are
taxed at a higher effective tax rate (as a share of earnings), and these types
of workers become relatively more costly for a business facing high UI tax
rates. Huang (2022) finds that higher state taxable wage bases increases
teenage employment rates, and Duggan et al. (2022) finds that higher tax bases
increase labor demand for low-wage part-time workers.

There is substantial variation in UI tax schedules across states, and a tax
increase in one state raises payroll costs for incumbent employers, without
affecting tax regimes in any other. Many state UI programs are underfunded,
leading them to deplete their UI trust funds during recessions. During the
Great Recession, 36 states depleted their UI trust funds and were forced to
take out loans from the federal government; this occurred again for 18 states
during the height of the COVID-19 pandemic. While many states recognized the
need to update their UI tax schedules to replenish their trust funds following
the Great Recession, the timing and the size of the legislated tax increases
varied greatly. At the same time, there were proposals to increase the
federally mandated UI tax base (of $7,000), which would have given states a
way to obtain more tax revenue without needing to legislate their own UI tax
policy. California, for example, did not legislate any UI tax increases
despite a UI trust fund debt of over $10 billion.

##  3 Research Design

In 2010 and 2011, a total of sixteen states implemented UI tax increases in
order to replenish their trust funds. Coupled with the mechanical increase in
employer-specific tax rates due to experience rating, these tax hikes could
amount to a 2-5% increase in effective tax rates. For my LEHD research sample
of 23 states and District of Columbia, Figure 1 graphs the distribution of
maximum tax increases (tax base * maximum rate) from 2009 to 2011. Among this
subsample, I exclude 7 states from my analysis due to basline differences in
UI tax regimes. Six of these excluded states automatically index UI tax bases
to wage growth, resulting in incremental and predictable tax increases every
year throughout my sample period (and thus greater tax costs at baseline than
the treatment states). I also exclude Pennsylvania, which experienced a UI tax
decrease in 2011-12.

From the remaining states, I identify 9 treatment states whose statutory
maximum UI taxes rose by more than $100 from 2009 to 2011, leaving a remainder
of 8 control states with minimal tax changes during this window. From 2009 to
2011, treatment states experienced per-capita maximum UI tax increases ranging
from just under $200 to over $600, and the average increase was $378. In
percentage terms, maximums increased by 67% on average, and the largest tax
increase was experienced by South Carolina (in both level and percentage
terms).666Appendix Figure A.3 plots maximum and average UI taxes over time for
each control state, and appendix Figure A.4 and Figure A.5 plots them for
treatment and excluded states, respectively. Figure 2 plots the locations of
these 17 LEHD states, and the change in maximum UI taxes from 2009 to 2011.

In order to focus on employers for whom these state UI tax increases would be
binding, I create a sample of high exposure employers that are likely to be
close to the maximum tax rate following the Great Recession. I first estimate
event study regressions to test for differential pre-trends in treatment
states relative to control states. I then estimate pooled difference-in-
differences regressions to estimate a continuous treatment effect from UI tax
increases. To establish a consistent sample for both regression
specifications, I restrict to the period 2008 to 2013, to allow for at least
two years of pre-change data and three years of post-change data.

Estimating an event study requires defining a single starting date for each
state tax increase. While some state increases occurred all at once, other
states legislated a more gradual increase from 2010 to 2012. The pooled
difference-in-differences estimation will incorporate this variation in
magnitude and timing, but for the event study I simply define event time
relative to the quarter before the initial tax increase occurs ($event=0$ in
either 2009:Q4 or 2010:Q4 for treatment states, and event time always equals
zero for control states). I then estimate the following regression
specification:

$Y_{fst}=\alpha_{f}+\sum_{k=-8,k\neq-1}^{13}\beta_{k}(event=k)+NAICS*\delta_{t}+\gamma
minwage_{st}+\epsilon_{fst}$ (1)

Here $f$ indexes employer (SEIN), $s$ indexes state, $t$ indexes year-quarter,
and $k$ indexes the quarter relative to the policy change. I group all
quarters more than two years before the policy change together into one
estimate $k=-8$, and all quarters more than three years after the policy
change together into $k=13$. To allow for potential anticipation effects, the
treatment effects are estimated relative to the outcome two quarters prior to
the tax change (ie: if a state increased taxes in 2010, the baseline would be
Q3 of 2009, and if a state increased taxes in 2011, the baseline would be Q3
of 2010). Thus the excluded quarter is $k=-1$, and the first quarter of the
tax change is labeled $k=1$.777States with 2010 increases are Arkansas, Maine,
Maryland, Tennessee, and West Virginia; States with 2011 increases are
Illinois, Indiana, Oklahoma, and South Carolina. Coefficients $\beta_{-8}$ to
$\beta_{-2}$ test for differential pre-trends prior to the policy changes.
Fixed effects are included for the SEIN, as well as the year-quarter
interacted with 2-digit NAICS sector, as some sectors such as construction
were disproportionately impacted by the Great Recession. The primary outcomes
of interest include mean log quarterly earnings for stable employees (excludes
hires and separations), as well as year-over-year employment growth and hiring
rates.

I also estimate a pooled difference-in-differences regression with a
continuous treatment variable, $Taxchange_{st}$, defined as the dollar change
in maximum UI tax relative to 2009 (and defined to equal zero in years 2008
and 2009). The baseline regression specification is as follows:

$Y_{fst}=\alpha_{f}+\sum_{q=1}^{4}\beta_{q}*Taxchange_{st}+NAICS*\delta_{t}+\gamma
minwage_{st}+\epsilon_{fst}$ (2)

Here $f$ indexes employer, $s$ indexes state, and $t$ indexes year-quarter. I
estimate four coefficients of interest $\beta_{1}$ to $\beta_{4}$ to allow for
differential responses by calendar quarter, because UI tax burdens are largest
in Q1. The identifying assumption is that in the absence of UI tax policy
changes, employers in the same 2-digit NAICS sector in treatment states and
control states would have evolved similarly in the years following the Great
Recession.

It is worth noting that after the Great Recession, there was also a
significant federal extension of UI benefit duration beyond the typical 26
weeks, through both the Emergency Unemployment Compensation (EUC) program and
the Extended Benefits (EB) program. Benefit duration reached a potential
maximum of 99 weeks in 2010-2011, before dropping in 2012 and coming abruptly
to an end at the close of 2013. Farber and Valletta (2015) and Farber et al.
(2015) found little impact of these benefit extensions on job finding, as they
primarily caused fewer workers to leave the labor force and led to long-term
unemployment. Thus, I assume the extension of UI benefits does not
differentially impact worker labor supply during my analysis period.

##  4 Data

This project uses the Census Bureau’s Longitudinal Employer-Household Dynamics
(LEHD), an administrative employer-employee matched dataset of quarterly
earnings, directly sourced from state UI records. Each employer in the LEHD is
assigned a state EIN number (SEIN), and this will be my firm definition. A
SEIN is also the level at which UI tax rates are assigned to employers. It can
encompass multiple establishments within a state, but no employment outside
the state. And just as large firms may have multiple EINs associated with
their business, these firms may also own multiple SEINs within a given state.

To construct my sample, I include employers from 9 treatment states and 8
control states, covering the time period from 2008 to 2013 (allowing for an
unbalanced panel). I also drop the Retail Trade and Accommodation & Food
Services sectors (NAICS 44-45 and NAICS 72). These two sectors experience high
turnover and low UI take-up rates, such that it is very difficult to classify
employers into high versus low experience rating. The exclusion of these
sectors should not affect the generalizability of my results, as they rank
among the sectors with the lowest average UI tax costs, just above Healthcare
and Education (Guo and Johnston (2021)).

The first outcome of interest is average quarterly earnings, either calculated
for stable workers (which excludes hires and separations) or for all workers.
Since no information on hours is collected, incidence on earnings may also
reflect changes in hours. In additional analyses in Section 6, I identify low-
earning workers in the LEHD to separately estimate the impacts on these
workers with the highest relative UI tax burdens. To study employment
outcomes, I count hires and separations based on the beginning and end of
employment spells, and divide by employment to define quarterly shares of new
hires and separations. I also measure quarterly employment growth using DHS
growth rates.

###  4.1 Calculating UI Tax Exposure

State UI tax increases affected either the maximum tax rate or tax base, both
of which require a sufficiently high experience rating to be binding. Because
I do not directly observe employers’ payroll tax rates in the LEHD, I impute
exposure to UI tax increases based on separation history. Employers who never
separate workers into non-employment are inferred to have a low UI tax rate
(low exposure), and employers who separate a significant share of workers into
non-employment will be inferred to have a tax rate close to the state maximum
(high exposure).

It is not layoffs themselves that impact employer-specific tax rates, but
rather the amount of UI benefits claimed by laid off workers. In order to
identify separations that could be eligible for UI benefits, I first limit the
scope of consideration to workers with at least 2 consecutive quarters of
earnings, and high quarter earnings of at least $1500 (minimum requirement to
be eligible for UI benefits in most states). I also ignore workers younger
than age 18 (to abstract from job separations driven by schooling) or older
than age 60 (to abstract from retirement timing). I then impute a layoff as a
job separation in quarter $t$ that results in at least one quarter of zero
earnings from quarters $t+1$ to $t+3$. Separations that were the result of
moves to a different state will not be captured in the LEHD data, so these
could also be miscoded as layoffs. I also drop employers with less than 20 or
greater than 500 workers at baseline (2009:Q3), to minimize measurement error
in this imputation.

Then for each SEIN, I aggregate the number of imputed layoffs over two
separate pre-periods, and use these two cumulative shares to define inclusion
in my analysis sample as a high exposure firm. The first pre-period runs from
2006:Q1 to 2007:Q4, and the second runs from 2008:Q1 to 2009:Q2 (the Great
Recession began in December 2007 and ended in June 2009).888I use the three-
year period before the first state tax increases in order to best capture
layoffs that could lead to potential UI tax increases. Layoffs that occurred
prior to 2006 are unlikely to impact tax rates in 2010 and later, because most
firms will have already finished experiencing tax increases. For example,
layoffs during the 2008-09 Great Recession caused tax rates to peak in
2011-12. In both treatment and control states, I restrict the sample to SEINs
that in each of the two pre-periods experienced total layoffs of 33-100% of
their 2009:Q3 baseline employment.

I also reserve a subset of SEINs with imputed layoffs of less than 15% from
2006:Q1-2007:Q4, and less than 10% from 2008:Q1-2009:Q2. Given the likelihood
of overestimating layoffs, an SEIN with an imputed layoff rate less than 10%
very likely experienced zero or very little UI benefit claims. This set of
employers, which are expected to be the least affected by UI tax increases due
to their distance from the maximum tax rate, will act as a “placebo” or low
exposure sample in triple-difference analyses.

Separation into non-employment is still an imperfect predictor of eventual
experience rating, because of imperfect take-up rates and substantial
variation in UI duration. Thus I view this exercise as accepting there will be
Type I error, in favor of minimizing Type II error. My results are also robust
to using alternative thresholds to define this sample of high exposure
employers. In new work using administrative data from Washington, Lachowska et
al. (2021) find that the take-up of UI among workers plays as important a role
as the separation rate in determining a given employer’s future UI tax rate.
Thus the measurement error introduced by inadvertently including some
employers with low UI tax exposure may attenuate my estimates.

###  4.2 Summary Statistics

LABEL:summstats reports summary statistics for my sample of firms in treatment
and control states at baseline in the third quarter of 2009. They are very
similar in size, with average employment of roughly 67 workers. Average layoff
histories also match extremely well, with the average employer having
experienced cumulative layoffs in 2006-07 that amounted to 57% of their
2009:Q3 employment, and 50% for the period of 2008:Q1 to 2009:Q2. One area of
mismatch, however, is annual earnings, with control states paying higher wages
than treatment states. This is likely due to state-level differences in cost-
of-living and minimum wages. Federal mininum wage increases occurred in July
of 2007, 2008, and 2009, and treatment states were more likely to have faced
binding minimum wage increases. Thus I also include a control for the state
minimum wage in all of my regression specifications. This table also shows
that the construction sector is overrepresented among high-exposure firms;
nationally the industry only accounts for 10% of establishments, while in my
analysis sample construction employers make up over 20%.

##  5 Results

I first establish that increases to the statutory maximum UI tax translated
into increases in actual taxes paid. In the absence of employer-specific tax
rates, I estimate an event study regression using aggregate data from the
public-use Quarterly Census of Employment and Wages (QCEW). The observation
level is a 4-digit industry, state, and quarter, and effective UI tax rates
are calculated by dividing quarterly UI contributions by taxable quarterly
payroll.

Using construction industries as a proxy for high exposure employers (as they
have the highest average tax costs), Figure 3 shows that the policy changes in
treatment states led to an increase in UI tax costs, predominantly in the
first two quarters of the calendar year (Q1 coincides with event times -7, -3,
1, 5, and 9). On average, Q1 tax rates in treatment states increased by 0.83,
1.1, and 1.0 percentage points over the three years following a policy change,
relative to control states. Estimates from a difference-in-differences
specification in Appendix LABEL:erateDD find that each $100 increase in
maximum UI taxes increased effective UI tax rates by 0.16 percentage points in
the first quarter of the year. However, this average effect at the industry
level masks substantial heterogeneity in effective tax rates that occurs at
the worker level, especially for workers that earn below the taxable wage
base. This will be explored further in section 6.

###  5.1 Event Study

To study the impact on earnings, Figure 4 plots event study estimates from
Equation 1 using log quarterly earnings as the outcome. Log earnings are
calculated by taking the firm-level average of log quarterly earnings for all
stable employees continuously employed from quarter t-1 to t+1. By excluding
new hires and separations, this ignores any potential drops in earnings due to
incomplete job spells. The baseline estimates in Panel A show that even after
controlling for state minimum wages, employers in treatment states paid lower
wages than those in control states prior to the policy change, and had a
pattern of lower first quarter earnings relative to the rest of the year. This
persistent seasonality in earnings is likely driven by regional differences in
climate. Two of the largest control states, California and Florida, are known
to have very mild winters and thus less seasonal employment in high exposure
industries such as construction. Panel B shows that including state-by-
calender quarter fixed effects helps to smooth out these seasonal patterns.
After controlling for state-specific seasonality, we still observe small drops
in average earnings in the first quarter (when tax burdens are greatest), but
the magnitudes are very small and not statistically significant (implying at
most a 1.2% drop in Q1 earnings). This therefore suggests that UI tax
increases have a minimal impact on workers’ average quarterly earnings.

Turning next to the employment margin, Panel A of Figure 5 plots baseline
estimates of year-over-year employment growth, and Panel B includes state-by-
calendar quarter fixed effects. Employment growth shows a sustained decline in
treatment states after the tax increase, with a 2 percentage point drop by the
end of the first year, and a 4 percentage point drop after the second. This
growing treatment effect over time could be driven by two factors. Looking at
a breakdown of taxes by treatment state in Figure A.4, we see that some states
experienced a gradual tax increase that peaked in 2012 (either a year or two
after the initial increase). Secondly, average tax rates were also highest in
2011-2012, as layoffs from the Great Recession took a few years to translate
into higher tax rates. Panel B shows that this pattern is also robust to the
inclusion of state-specific calendar quarter fixed effects, which account for
differences in geographic seasonality.

###  5.2 Difference-in-Differences

I next use a difference-in-differences estimation strategy to estimate average
treatment magnitudes. In these specifications, I now use a continuous
treatment measure equal to the change in the maximum UI tax schedule between
time $t$ and 2009, and equal to zero prior to 2009. I estimate specifications
described by Equation 2, which include employer (SEIN) and industry-by-time
fixed effects, as well as a control for the state minimum wage.

LABEL:earntable reports estimates for three earnings outcomes, with unweighted
estimates in the odd columns, and estimates weighted by firm employment in the
even columns. The baseline specifications are unweighted, since the analysis
sample is already restricted to SEINs between 20 and 500 workers in 2009,
although weighting generally has little impact on the estimated magnitudes.
Columns 1 and 2 calculate the employer’s average quarterly earnings across
stable workers who were employed for the full quarter, while Columns 3 and 4
include all workers when calculating the average. Both outcomes show a small
increase in log quarterly earnings after the tax change in all quarters except
for Q1, consistent with the observed pre-trend in Figure 4. The absence of an
increase in the Q1 DD coefficient implies a maximum tax incidence of 40% for
every additional dollar of UI tax (given that $100 is roughly 1% of mean
quarterly earnings), although this effect is likely driven by seasonal
employment patterns and is not robust to a triple-difference specification.

In Columns 5 and 6 I estimate an alternative measure, which is how likely
workers are to experience an earnings increase in a given quarter. Because
quarterly earnings vary throughout the year (especially when inclusive of
hours), I define a simple indicator for whether the worker earned more in the
current quarter than in the previous two quarters (ignoring any workers with
less than 3 quarters of tenure). The firm-level outcome is then calculated as
the share of workers satisfying the previous definition. This measure is
expected to be correlated with the share actually receiving raises, but
estimates are likely to be attenuated by measurement error due to the
quarterly frequency. These estimates provide further evidence for a minor
degree of tax incidence in the first quarter of the year; for every $100
increase in per-capita maximum UI taxes, the share of workers receiving a
raise in earnings in Q1 falls by 0.4 percentage points.

Given the evidence against full tax incidence on earnings, I next investigate
employment-related outcomes. LABEL:emptable reports estimates for three
different outcomes, and estimates are robust to weighting by firm employment
(even columns). I define year-over-year employment growth as the DHS growth
rate of quarterly employment relative to the same quarter of the previous
year, $\frac{Emp_{t}-Emp_{t-1}}{\frac{1}{2}(Emp_{t}+Emp_{t-1})}$, which
creates a symmetric growth measure that allows for entry and exit. The
baseline unweighted specification in Column 1 estimates that UI tax increases
lower year-over-year employment growth, and the effect compounds throughout
the year. A $100 increase in per-capita UI taxes lowers employment growth by
0.43 percentage points by the end of the year, and the magnitude is even
larger if weighted by firm employment. This implies that in a state like
Indiana, which experienced a $500 jump in maximum UI taxes in 2011, employment
growth fell by 2.2 percentage points in high exposure firms, relative to
similar counterparts in control states.

To decompose this employment change into hires and separations, I define the
quarterly new-hire share as the number of new hires divided by employment, and
the quarterly separation share as the number of separations divided by
employment. The estimates show a negative impact on hiring, with no
statistically significant effect on separations. Column 3 finds that a $100
increase in per-capita maximum UI taxes lowers both the first quarter and last
quarter hiring rate by 0.17 percentage points. This pattern of negative
employment growth and hiring is consistent with the mechanism of greater UI
tax burdens. At the start of the calendar year all earnings up to the tax base
are eligible for UI taxes, and thus create a large payroll tax burden for the
employer. Each additional worker hired incurs an additional UI tax burden,
whereas additional separations do not incur a tax saving and could even push
future costs higher if they claim UI benefits. Towards the end of the calendar
year, most if not all existing workers have exceeded the UI tax base and no
longer cost their employer any additional payroll tax. However, the earnings
of new hires still incur taxes up to the same tax base, resulting in a much
higher effective tax rate for new hires; this could explain the observed
reluctance to hire in the last quarter of the year. Although I am unable to
observe this, another possible explanation for the drop in labor demand is
substitution to contract workers, who would not be subject to UI
taxation.999For example, Kugler et al. (2017) found that payroll tax cuts in
Colombia increased rates of formal employment among affected workers.

###  5.3 Heterogeneity by Worker and Employer Characteristics

To allow for heterogeneous responses for different types of workers,
LABEL:subgroup analyzes employment outcomes for three specific groups of
workers. First, I study the impact on the hiring rate of low-earning workers,
who are defined to be those who earned less than $3000 in the quarter after
being hired (inflation adjusted to 2015 dollars).101010The $3000 threshold was
chosen to coincide with the federal poverty level for a single person
household ($11,770 in 2015). Column 1 shows that a $100 increase in the
maximum UI tax lowered the Q1 share of low-earning new hires by 0.1pp;
benchmarked to the sample mean of 6.5%, this indicates a larger negative
response than for the overall share of new hires from the previous table.

Next I calculate year-over-year employment growth rates for two subgroups of
interest: workers younger than 25 years of age, and those with only a high
school education or less (conditional on being 25 or older).111111Outcomes for
workers older than age 55 were also estimated, but the results did not warrant
submission for disclosure. Since small firms may not always employ these types
of workers, growth rates are defined to equal zero if a firm did not employ
any of these workers in either the current or previous calendar quarter,
resulting in a larger difference between the weighted and unweighted estimates
when weighting by firm employment. Recall the previous estimate of a $100
increase in maximum UI taxes lowering employment growth in Q4 by 0.43
percentage points (Column 1 of LABEL:emptable). For young workers, the impact
is an even larger decline of 0.66 percentage points for each $100 increase.
Growth rates for low-educated workers are more similar to the overall effect,
with an estimated decline of 0.39 percentage points by the end of the year.
This suggests that young workers who are just entering the workforce are the
most impacted by falls in labor demand due to UI tax increases.

To test for heterogeneous responses by different types of employers, I
classify employers based on their characteristics at baseline (2009:Q3). I
focus on three observable characteristics: median worker earnings, multi-
establishment status, and firm age. The latter two are also potential proxies
for whether the employer would face cash or financing constraints, as a
surprise increase in UI taxes could restrict available cash flow. Recall that
all firms in the analysis sample are already age 5 or older by 2010, as they
needed a long enough layoff history to be identified as high exposure.

The main outcome of interest is the new hire share, and the estimation
augments the differences-in-differences specification described by Equation 2.
In each specification, I add four additional interaction terms interacting UI
tax changes with one of the following indicators defined at baseline: Median
quarterly earnings below $6000, single-establishment firm (both in-state and
nationally), or firm age less than 20 years old. Figure 6 plots estimates for
each of the three characteristics. The estimates show little difference in
hiring whether an employer has a majority of low-earning workers or not.
However, the single establishment interactions show a large negative response
for firms that only have a single location (seen by the interactions for Q1,
Q3, and Q4), while multi-establishment firms are essentially unaffected. This
indicates that single-establishment firms with less access to resources are
the most likely to lower hiring in response to UI tax increases. Among these
employers, a $100 maximum tax hike lowered hiring by 0.23pp, 0.22pp, and
0.41pp in quarters 1, 3, and 4 respectively. Finally, the last set of markers
shows that younger firms are also more likely than older firms to reduce
hiring in response to a UI tax increase, although the magnitudes are smaller
than those for single-establishment firms.

Appendix Figure A.6 plots estimates for the separations share as well. While I
estimated no overall effect on separations, the quarterly interactions suggest
that single establishment firms exposed to a tax increase were actually less
likely to experience separations in the first two quarters of the year,
relative to multi-establishment firms. A potential mechanism could be a
greater effort towards worker retention in the absence of hiring.

###  5.4 Triple-Difference Design and Robustness

In order to control for state-specific factors that could be confounding our
estimates, I also conduct a difference-in-difference-in-differences estimation
comparing the main sample of high-exposure employers to the placebo sample
that experienced minimal layoffs. Because UI tax increases are more binding
for employers near the maximum tax rate, we can use employers with minimal
layoffs – and therefore low exposure to UI tax increases – to control for
state-level variation that may influence both tax policy and employment
outcomes.

Figure 7 plots event study estimates for year-over-year employment growth
using this triple differences design on the expanded sample of both high tax
and low tax employers. It estimates Equation 1 with not only the event-time
treatment dummies, but also a set of treatment dummies interacted with whether
the employer is classified as high-tax. These interactions become our new
coefficients of interest, while the baseline event-time estimates control for
confounding conditions in treatment states. The estimates show no differential
pre-trend prior to the tax increases, and a sustained drop in growth after,
reaching negative 5 percentage points by the end of the second year. This
provides further evidence of a causal relationship between UI tax increases
and drops in labor demand.

LABEL:triplediff reports estimates of a pooled triple-difference regression
specification studying earnings, hiring, and separations. While the
Taxchange*High coefficients for the new hire share and separation share are
consistent with those from the baseline difference-in-differences
specification, we no longer observe an impact on log earnings or the share
receiving raises. This implies that the previously observed negative impact on
Q1 earnings and raises was due to underlying differences in treatment and
control states unrelated to UI tax increases, and the wage incidence of UI tax
increases are minimal.

LABEL:triplediff2 reports estimates for employment growth outcomes. The
triple-difference interactions are all statistically significant and larger in
magnitude than the original difference-in-differences estimates. Within just
the first quarter of the year, employment growth drops by 0.5 percentage
points for every $100 UI tax increase. And this negative effect grows to
-0.74pp by the end of the year. The employment growth of young workers were
even more negatively impacted, with each $100 in tax increases lowering end-
of-year growth by 0.9pp. These results are also robust to the inclusion of
state-by-year-quarter fixed effects, reported in LABEL:triplediff_styear.

My results are also robust to a number of sensitivity checks of sample
composition.121212Estimates from robustness checks have not been disclosed
from the Census RDC, but would be available for additional disclosure should
they be required. First, while I opted to exclude the retail trade and
food/hospitality sectors due to higher likelihood for measurement error, both
the difference-in-differences and triple-differences estimates are robust to
the inclusion of these employers. Second, because I do not observe actual
employer-specific tax rates, I measure expected UI tax costs based on imputed
layoff histories. Small changes to the cutoff of layoff shares that warrant
inclusion in my main analysis sample had no qualitative effect on my
estimates. Additionally, the results are not driven by the inclusion of any
one state in the analysis sample, nor does the restriction to a balanced panel
impact the estimates.

Finally, to address potential concerns with the differential timing of state
UI tax increases, I have estimated separate event study regressions including
only 2010 treatment states or only 2011 treatment states, respectively. This
ensures that each group of treatment states are only compared to the control
states, and there is no longer an issue of staggered treatment, since all tax
increases occur at the same time. Treatment effects from this exercise are
qualitatively similar to those using the pooled sample.

##  6 Incidence for Low-Earning Workers

Due to low UI tax bases (the median tax base in 2009 was only $10,000), low-
wage workers face higher effective tax rates and thus bear a larger relative
tax burden than their higher-earning counterparts. They may also have less
bargaining power and are more likely to work part-time. I identify existing
workers of highly exposed firms, and estimate the impact of UI tax increases
on their subsequent earnings trajectories. The added precision of a worker-
level analysis allows for the identification of earnings impacts within this
subgroup of interest.

Focusing on the main analysis sample of high-exposure firms, I construct a
worker-level sample consisting of workers employed by the firm for at least a
year, with annual earnings between $5000 and $24,000 in 2009.131313Because the
LEHD reports total earnings and not wage rates, this definition may pick up
high-wage workers who work very few hours, although this should be fairly
uncommon. Additionally, since UI taxes are based on earnings and not wages,
part-time high-wage workers are equally costly to an employer from a payroll
tax standpoint. To ensure these workers make up a non-negligible share of the
firms’ employment, I also drop any firms that did not employ 10 or more of
these low-wage workers as of 2009:Q3. This subsample includes approximately
549,000 low-wage workers, employed by 13,000 employers (44% of the highly
exposed employers in the main analysis sample). I estimate worker-level event
study regressions, where event time is defined in the same way as Equation 1.

$EarnGrowth_{ifst}=\alpha_{f}+\sum_{k=-8,k\neq-1}^{8}\beta_{k}Taxchange_{s}(t-Increase_{s}=k)\\\
+\delta_{t}+\rho log(earn_{ifs,t-4})+\gamma minwage_{st}+\epsilon_{ifst}$ (3)

Here $i$ indexes worker, $f$ indexes employer, $s$ indexes state, $t$ indexes
year-quarter, and $k$ indexes the quarter relative to the policy change. I
group all quarters more than two years before the policy change together into
one estimate $k=-8$, and I follow workers for up to three years after the
policy change, through the end of 2012. $Taxchange_{s}$ is defined for
treatment states to equal the average maximum UI tax increase between 2009 and
2010-11 (in hundreds), and equal to zero for control states. The main outcome
of interest, $EarnGrowth_{ifst}$ is defined as the year-over-year earnings
growth relative to the same quarter in the previous year. Thus inclusion in
the sample requires the worker to have been employed at the firm a year
earlier, limiting the analysis to a more stable subset of workers.

Figure 8 plots the estimates of the event time interactions with
$Taxchange_{s}$; thus the magnitude of each estimate reflects the effect of a
$100 UI tax increase. In the first quarter after the tax increase (event time
= 1), each $100 UI tax increase lowered earnings growth by 0.63% for
continuing workers in treated firms, relative to their counterparts in control
firms. This negative impact is small and precisely estimated, and does not
last beyond the first year. This allows us to rule out negative earnings
impacts beyond 1% in Q1 and 0.9% in Q3, for each $100 increase. Since 1% of
quarterly earnings equates to $48 on average among this subsample, together
these estimates imply a maximum pass-through rate of 90% ($90 out of $100) for
existing low-wage workers. Therefore, even amongst a subgroup that bears the
largest effective tax burden, we find evidence that short-run tax increases
result in less than full tax incidence on the earnings of existing workers.

##  7 Conclusion

The employer-specific and time-varying aspects of UI payroll taxation provides
researchers with extensive policy variation that can be used to understand how
firms respond to temporary payroll tax changes. Given previous proposals of
cutting employer payroll taxes to stimulate employment during recessions,
there is debate over whether such tax cuts would have the intended effect or
whether they would simply increase firm profits. I estimate significant
negative employment responses to unexpected tax increases, which suggests that
temporary payroll tax cuts are likely to have a positive impact on employment
as well, especially for young and low-earning workers that face higher
relative tax burdens, and for smaller employers with less access to financial
resources.

In response to state maximum UI tax increases in the years following the Great
Recession, UI tax burdens rose for employers with large layoff histories, with
minimal evidence of tax incidence on workers. With little ability to pass tax
increases on to workers, employers lowered hiring rates and employment growth,
and this effect grew over time. Using the Q1 treatment estimates of hiring
rates from LABEL:emptable, I calculate an implied labor demand elasticity of
-1.1. This measure is obtained by dividing the Q1 DD coefficient estimate of
-0.170 by 0.161, the first quarter effective UI tax increase estimated using
the QCEW in Appendix LABEL:erateDD. An alternative measure can be calculated
by dividing the triple-difference drop in Q4 employment growth of -0.74 by
0.31, the share of average annual earnings a $100 tax increase is equivalent
to; this equates to an end-of-year labor demand elasticity of -2.4. These
elasticity estimates fall within the range of elasticities from the labor
demand literature, although they are on the lower end of those from recent
payroll tax studies.141414Ku et al. (2020), estimates a labor demand
elasticity of -3.6 using place-based payroll tax increases in Norway, while
Benzarti and Harju (2021a) estimates elasticities of -2.9 to -4.16 in response
to firm-specific increases in Finland. And in the U.S. setting, Johnston
(2021) estimates a UI tax labor demand elasticity of -4 while Guo (2021)
estimates an elasticity of -1.1.

The tax incidence of unemployment insurance payroll taxes has been an
understudied topic in the payroll taxation literature. The experience rating
of employer-specific tax rates creates the benefit of reducing avoidable
layoffs (particularly temporary layoffs) and the associated externalities
imposed upon the UI system. However, the cyclical pattern in which tax rates
are highest in years following economic recessions also slows hiring and
employment growth during the recovery. More work is needed to understand the
unintended consequences and inherent tradeoffs of US unemployment insurance’s
current design.

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FIGURES

Figure 1: Maximum UI Tax Increase from 2009 to 2011

Source: Significant Measures of State UI Tax Systems. Maximum tax calculated
as taxable wage base multiplied by maximum tax rate.

Figure 2: UI Tax Policy Variation

Source: Significant Measures of State UI Tax Systems. The 7 treatment states
are shaded in blue corresponding to the tax change they experienced, and the 8
control states are shaded with vertical lines (and also include Delaware and
District of Columbia). States in grey are excluded.

Figure 3: Effective UI Tax Rates (2008-2013)

Source: Quarterly Census of Employment and Wages. (N = 4,062) Sample limited
to ten 4-digit construction industries and years 2008 to 2013 (cells too small
to meet disclosure requirements are missing). Effective tax rates calculated
by dividing quarterly UI contributions by quarterly payroll. Event study
estimated with state-industry and year-quarter fixed effects, and weighted by
industry employment. Error bars denote 95% CI for standard errors clustered at
state level.

Figure 4: Event Study of Log Quarterly Earnings (2008-2013)

A: Baseline Estimates

B: Controlling for State-by-Calendar Quarter

N = 651,000. Outcome variable is the mean quarterly earnings of stable workers
(employed in both t-1 and t+1). Also includes a control for state minimum
wage, and includes SEIN and Year-Quarter-N2 fixed effects. Panel B also
includes state-by-calendar quarter fixed effects. Error bars denote 95% CI for
robust standard errors clustered at state level.

Figure 5: Event Study of Year-Over-Year Employment Growth (2008-2013)

A: Baseline Estimates

B: Controlling for State-by-Calendar Quarter

N = 651,000. Outcome variables denoted in percentage points. Also includes a
control for state minimum wage, and includes SEIN and Year-Quarter-N2 fixed
effects. Panel B also includes state-by-calendar quarter fixed effects. Error
bars denote 95% CI for robust standard errors clustered at state level.

Figure 6: Heterogeneity in New Hire Share by Firm Type (2008-2013)

N = 651,000. Also includes a control for state minimum wage, and includes SEIN
and Year-Quarter-N2 fixed effects. Error bars denote 95% CI for robust
standard errors clustered at state level. The share of employers with median
earnings below $6000 equals 0.29. The share that are single-establishment
firms equals 0.69. The share with firm age under 20 equals 0.22.

Figure 7: Year-Over-Year Employment Growth - Triple Difference (2008-2013)

N = 1,109,000. Figure plots the estimates from treatment dummies interacted
with event time and high-tax status. Regression also includes treatment
interacted with event time, a control for state minimum wage, and SEIN and
Year-Quarter-N2-High fixed effects. Error bars denote 95% CI for robust
standard errors clustered at state level.

Figure 8: Year-Over-Year Earnings Growth - Worker Level (2008-2012)

N = 4,954,000. Includes 549,000 unique workers across 13,000 unique employers.
Figure plots the estimates from taxchange measure interacted with event time.
Regression also includes a control for state minimum wage, lagged log
earnings, and SEIN, Year-Quarter, and state-by-calendar quarter fixed effects.
Error bars denote 95% CI for robust standard errors clustered at state level.

TABLES

Table 1: Summary Statistics (2009:Q3)

| Control | Treatment
---|---|---
|  00 Mean 00 |  00 SD 00 |  00 Mean 00 |  00 SD 00
Employment | 66.74 | 72.28 | 67.29 | 70
Cumulative Layoff Share 2006-07 | 0.5668 | 0.1689 | 0.5668 | 0.1679
Cumulative Layoff Share 2008-09 | 0.5037 | 0.1473 | 0.5065 | 0.1493
Average Annual Earnings | 36,900 | 27,990 | 32,350 | 23,340
Share of Workers Earning $<\$5000$ | 0.1518 | 0.1647 | 0.1572 | 0.1619
Construction Sector | 0.245 |  | 0.2282 |
$N$ | 18000 | 11500

Employer-level observations from 3rd quarter of 2009. Control states include
AZ, CA, CO, DE, DC, FL, NE, and MO. Treatment states include AR, IN, IL, ME,
MD, OK, SC, TN, and WV.

Table 2: Log Quarterly Earnings (2008–2013)

| Stable Workers | All Workers | Share with Raise
---|---|---|---
| (1) | (2) | (3) | (4) | (5) | (6)
Tax $\Delta$*Q1 ($100’s) | -0.00113 | -0.000855 | 0.000158 | -0.0000151 |  -0.419∗∗∗ |  -0.398∗∗∗
| (0.00190) | (0.00123) | (0.00109) | (0.000735) | (0.113) | (0.0805)
Tax $\Delta$*Q2 ($100’s) |  0.00380∗∗∗ |  0.00331∗∗∗ |  0.00209∗∗ |  0.00214∗∗∗ | 0.111 | 0.137
| (0.000938) | (0.000754) | (0.000869) | (0.000706) | (0.0929) | (0.157)
Tax $\Delta$*Q3 ($100’s) |  0.00353∗∗∗ |  0.00334∗∗∗ |  0.00309∗∗∗ |  0.00287∗∗∗ | -0.00947 | -0.0320
| (0.00101) | (0.00101) | (0.000864) | (0.000729) | (0.0985) | (0.0922)
Tax $\Delta$*Q4 ($100’s) |  0.00494∗∗∗ |  0.00432∗∗∗ |  0.00484∗∗∗ |  0.00471∗∗∗ | 0.0281 | -0.0218
| (0.00130) | (0.000902) | (0.00105) | (0.000824) | (0.139) | (0.132)
Minimum Wage |  0.0152∗∗∗ |  0.0121∗∗∗ |  0.0181∗∗∗ |  0.0126∗∗∗ | 0.170 | 0.260
| (0.00279) | (0.00276) | (0.00363) | (0.00316) | (0.227) | (0.229)
$R^{2}$ | 0.869 | 0.905 | 0.884 | 0.921 | 0.191 | 0.193
Mean of Dep Var | 9.232 | 9.240 | 9.067 | 9.057 | 31.0 | 31.7
Weighting |  | YES |  | YES |  | YES
$N$ | 651000 | 651000 | 651000 | 651000 | 651000 | 651000

Regressions include SEIN and year-quarter-N2 fixed effects. Share with Raise
equals the percentage of continuing workers who received a raise relative to
the previous two quarters. Even columns are weighted by employment. Robust
standard errors clustered at state level in parentheses. ∗∗ $p<0.05$, ∗∗∗
$p<0.01$

Table 3: Employment Outcomes (2008–2013)

| Employment Growth | New Hire Share | Separation Share
---|---|---|---
| (1) | (2) | (3) | (4) | (5) | (6)
Tax $\Delta$*Q1 ($100’s) | -0.142 |  -0.469∗∗ |  -0.170∗∗ |  -0.163∗∗ | -0.0968 | -0.0350
| (0.129) | (0.177) | (0.0723) | (0.0672) | (0.0832) | (0.0583)
Tax $\Delta$*Q2 ($100’s) |  -0.287∗∗ |  -0.571∗∗ | 0.240 | 0.224 | -0.0746 | -0.0494
| (0.120) | (0.205) | (0.193) | (0.168) | (0.0897) | (0.0757)
Tax $\Delta$*Q3 ($100’s) |  -0.318∗∗ |  -0.674∗∗∗ | -0.104 | -0.0962 | 0.0514 |  0.102∗∗
| (0.115) | (0.194) | (0.0752) | (0.0756) | (0.0652) | (0.0410)
Tax $\Delta$*Q4 ($100’s) |  -0.431∗∗∗ |  -0.759∗∗∗ |  -0.170∗ |  -0.178∗ | 0.0587 | 0.110
| (0.127) | (0.171) | (0.0954) | (0.0879) | (0.169) | (0.147)
Minimum Wage | -0.912 | -0.792 |  -0.330∗ | -0.196 | 0.107 | 0.190
| (0.696) | (0.781) | (0.182) | (0.201) | (0.208) | (0.200)
$R^{2}$ | 0.193 | 0.254 | 0.427 | 0.529 | 0.405 | 0.521
Mean of Dep Variable | -4.201 | 0.349 | 13.40 | 14.98 | 14.74 | 15.87
Weighting |  | YES |  | YES |  | YES
$N$ | 651000 | 651000 | 651000 | 651000 | 651000 | 651000

Regressions include SEIN and year-quarter-N2 fixed effects. Outcomes denoted
in percentage points, and even columns are weighted by employment. Robust
standard errors clustered at state level in parentheses. ∗ $p<0.10$, ∗∗
$p<0.05$, ∗∗∗ $p<0.01$

Table 4: Employment Growth of Subgroups (2008–2013)

|  | Employment Growth:
---|---|---
| Low-Earn Hire Share | Age Under 25 | HS or Less
| (1) | (2) | (3) | (4) | (5) | (6)
Tax $\Delta$*Q1 ($100’s) |  -0.102∗∗ |  -0.0956∗∗ | -0.218 |  -0.511∗∗ | -0.0956 |  -0.450∗∗
| (0.0460) | (0.0433) | (0.246) | (0.234) | (0.133) | (0.182)
Tax $\Delta$*Q2 ($100’s) | 0.0929 | 0.106 | -0.325 |  -0.643∗∗ |  -0.249∗ |  -0.563∗∗
| (0.0777) | (0.0694) | (0.254) | (0.226) | (0.122) | (0.209)
Tax $\Delta$*Q3 ($100’s*) | -0.0701 | -0.0457 |  -0.510∗ |  -0.896∗∗∗ |  -0.288∗∗ |  -0.655∗∗∗
| (0.0521) | (0.0434) | (0.287) | (0.250) | (0.108) | (0.200)
Tax $\Delta$*Q4 ($100’s) | -0.0822 | -0.0714 |  -0.655∗ |  -0.951∗∗∗ |  -0.393∗∗∗ |  -0.735∗∗∗
| (0.0543) | (0.0454) | (0.328) | (0.264) | (0.132) | (0.172)
Minimum Wage |  -0.237∗ | -0.151 | 0.0461 | -0.446 |  -1.589∗ | -1.217
| (0.120) | (0.118) | (1.383) | (1.497) | (0.778) | (0.836)
$R^{2}$ | 0.515 | 0.647 | 0.101 | 0.154 | 0.156 | 0.218
Mean of Dep Var | 6.478 | 7.399 | -11.44 | -5.683 | -2.712 | 1.972
Weighting |  | YES |  | YES |  | YES
$N$ | 651000 | 651000 | 651000 | 651000 | 651000 | 651000

Regressions include SEIN and year-quarter-N2 fixed effects. Outcomes are
denoted in percentage points, and even columns are weighted by employment.
Robust standard errors clustered at state level in parentheses. ∗ $p<0.10$, ∗∗
$p<0.05$, ∗∗∗ $p<0.01$

Table 5: Triple Difference (2008–2013)

| Log Earnings | Share with Raise | New Hire Share | Separation Share
---|---|---|---|---
| (1) | (2) | (3) | (4)
Tax $\Delta$*Q1 ($100’s) | -0.000610 |  -0.247∗∗ |  -0.0286∗ | -0.0385
| (0.00147) | (0.108) | (0.0143) | (0.0373)
Tax $\Delta$*Q2 ($100’s) | 0.00313 | 0.130 | 0.0739 | 0.0305
| (0.00274) | (0.489) | (0.0660) | (0.0624)
Tax $\Delta$*Q3 ($100’s) | -0.000553 | 0.0416 | 0.0382 | -0.0480
| (0.00283) | (0.219) | (0.0289) | (0.0485)
Tax $\Delta$*Q4 ($100’s) |  0.00291∗∗ | -0.000309 | 0.0380 |  -0.0719∗∗∗
| (0.00128) | (0.149) | (0.0231) | (0.0240)
Tax $\Delta$*Q1 $\times$ High | -0.000246 | -0.171 |  -0.155∗∗ | -0.0544
| (0.00172) | (0.114) | (0.0654) | (0.0508)
Tax $\Delta$*Q2 $\times$ High | 0.00112 | 0.0285 | 0.155 | -0.0995
| (0.00261) | (0.506) | (0.156) | (0.0574)
Tax $\Delta$*Q3 $\times$ High | 0.00433 | -0.0328 |  -0.151∗∗ | 0.110
| (0.00326) | (0.278) | (0.0596) | (0.0797)
Tax $\Delta$*Q4 $\times$ High | 0.00223 | 0.0103 |  -0.220∗∗ | 0.135
| (0.00172) | (0.0873) | (0.101) | (0.164)
Minimum Wage |  0.0108∗∗∗ | 0.00649 | -0.170 | -0.00830
| (0.00271) | (0.262) | (0.118) | (0.144)
$R^{2}$ | 0.901 | 0.178 | 0.476 | 0.482
Mean of Dep Var | 9.323 | 31.7 | 10.61 | 11.28
$N$ | 1109000 | 1109000 | 1109000 | 1109000

Regressions include SEIN, year-quarter-N2, and year-quarter-High fixed
effects. The necessary DDD interactions are either absorbed by the SEIN fixed
effects or the year-quarter-High fixed effects. Robust standard errors
clustered at state level in parentheses. ∗ $p<0.10$, ∗∗ $p<0.05$, ∗∗∗ $p<0.01$

Table 6: Triple Difference - Employment Growth (2008–2013)

| Overall Growth | Age under 25 | HS or Less
---|---|---|---
| (1) | (2) | (3)
Tax $\Delta$*Q1 ($100’s) |  0.330∗∗ | 0.379 |  0.371∗∗
| (0.116) | (0.228) | (0.135)
Tax $\Delta$*Q2 ($100’s) |  0.303∗∗ | 0.295 |  0.309∗
| (0.127) | (0.287) | (0.154)
Tax $\Delta$*Q3 ($100’s) |  0.315∗∗ | 0.208 |  0.357∗∗
| (0.135) | (0.242) | (0.149)
Tax $\Delta$*Q4 ($100’s) |  0.284∗ | 0.222 |  0.299∗∗
| (0.140) | (0.265) | (0.139)
Tax $\Delta$*Q1 $\times$ High |  -0.503∗∗ |  -0.618∗ |  -0.525∗∗
| (0.190) | (0.293) | (0.233)
Tax $\Delta$*Q2 $\times$ High |  -0.622∗∗∗ |  -0.659∗∗ |  -0.617∗∗
| (0.212) | (0.290) | (0.274)
Tax $\Delta$*Q3 $\times$ High |  -0.664∗∗∗ |  -0.750∗∗ |  -0.705∗∗
| (0.222) | (0.326) | (0.253)
Tax $\Delta$*Q4 $\times$ High |  -0.743∗∗∗ |  -0.904∗∗ |  -0.748∗∗∗
| (0.234) | (0.387) | (0.252)
Minimum Wage | -0.383 | 0.598 | -0.801**
| (0.336) | (0.872) | (0.369)
$R^{2}$ | 0.203 | 0.086 | 0.167
Mean of Dep Variable | -1.373 | -7.296 | 0.419
$N$ | 1109000 | 1109000 | 1109000

Growth measures are multiplied by 100. Regressions include SEIN, year-
quarter-N2, and year-quarter-High fixed effects. The necessary DDD
interactions are either absorbed by the SEIN fixed effects or the year-
quarter-High fixed effects. Robust standard errors clustered at state level in
parentheses. ∗ $p<0.10$, ∗∗ $p<0.05$, ∗∗∗ $p<0.01$

##  Appendix A APPENDIX TABLES AND FIGURES

Figure A.1: Empirical UI Tax Schedule for Florida (2008)

Source: US Dept of Labor ETA 204 Experience Rating Report. The Benefit Ratio
is a measure of the employer’s layoff experience in the last three years.

Figure A.2: Total UI Contributions, as % of total wages (1967 - 2018)

Source: US Dept of Labor Unemployment Insurance Chartbook.
Shaded regions denote US recession years, as defined by NBER.

Figure A.3: State UI Tax Schedules - Control

Compares average UI taxes paid and maximum UI taxes. Average taxes for
specialty trade contractors obtained from Quarterly Census of Employment and
Wages. Specialty trade contractors (NAICS 238) was chosen as an industry whose
employers often face rates close to the maximum, to proxy for high exposure
firms.

Figure A.4: State UI Tax Schedules - Treatment

Compares average UI taxes paid and maximum UI taxes. Average taxes for
specialty trade contractors obtained from Quarterly Census of Employment and
Wages. Specialty trade contractors (NAICS 238) was chosen as an industry whose
employers often face rates close to the maximum, to proxy for high exposure
firms.

Figure A.5: State UI Tax Schedules - Excluded

Compares average UI taxes paid and maximum UI taxes. Average taxes for
specialty trade contractors obtained from Quarterly Census of Employment and
Wages. Specialty trade contractors (NAICS 238) was chosen as an industry whose
employers often face rates close to the maximum, to proxy for high exposure
firms.

Figure A.6: Heterogeneity in Separations Share by Firm Type (2008-2013)

N = 651,000. Also includes a control for state minimum wage, and includes SEIN
and Year-Quarter-N2 fixed effects. Error bars denote 95% CI for robust
standard errors clustered at state level. The share of employers with median
earnings below $6000 equals 0.29. The share that are single-establishment
firms equals 0.69. The share with firm age under 20 equals 0.22.

Table A.1: Average Industry Effective UI Tax Rate (2008–2013)

| Unweighted | Employment-Weighted
---|---|---
| (1) | (2)
Tax $\Delta$*Q1 ($100’s) |  0.0996∗ |  0.161∗∗∗
| (0.0498) | (0.0646)
Tax $\Delta$*Q2 ($100’s) |  0.138∗∗∗ |  0.136∗∗∗
| (0.0242) | (0.0270)
Tax $\Delta$*Q3 ($100’s) |  0.0752∗∗∗ |  0.0490∗
| (0.0209) | (0.0254)
Tax $\Delta$*Q4 ($100’s) |  0.0536∗ | 0.0207
| (0.0280) | (0.0335)
Minimum Wage | 0.0865 | 0.206
| (0.104) | (0.0987)
$R^{2}$ | 0.881 | 0.914
Mean of Dependent Variable | 1.382 | 1.217
$N$ | 4062 | 4062

Uses average industry data from the public-use QCEW. Sample limited to ten
4-digit construction industries, and observations are at the industry by state
by quarter level (cells too small to meet disclosure requirements are
missing). Effective tax rates calculated by dividing quarterly UI
contributions by quarterly payroll. Regressions include state-industry and
year-quarter fixed effects. Robust standard errors clustered at state level in
parentheses. ∗∗ $p<0.05$, ∗∗∗ $p<0.01$

Table A.2: Triple Difference Controlling for State-Time FEs (2008–2013)

|  |  |  |  | Growth: | Growth:
---|---|---|---|---|---|---
| Log Earn | Growth | New Hires | Separations | Under 25 | HS or Less
| (1) | (2) | (3) | (4) | (5) | (6)
Tax $\Delta$*Q1 $\times$ High | -0.00292 |  -0.528∗∗ |  -0.154∗ | -0.0456 |  -0.665∗∗ |  -0.551∗∗
| (0.00320) | (0.190) | (0.0739) | (0.0601) | (0.284) | (0.231)
Tax $\Delta$*Q2 $\times$ High | 0.00184 |  -0.642∗∗∗ | 0.196 | -0.0838 |  -0.717∗∗ |  -0.640∗∗
| (0.00322) | (0.215) | (0.185) | (0.0528) | (0.277) | (0.275)
Tax $\Delta$*Q3 $\times$ High |  0.00511∗∗ |  -0.672∗∗∗ |  -0.131∗∗ |  0.130∗∗ |  -0.776∗∗ |  -0.723∗∗
| (0.00239) | (0.218) | (0.0504) | (0.0607) | (0.301) | (0.249)
Tax $\Delta$*Q4 $\times$ High | 0.00256 |  -0.737∗∗∗ |  0.199∗ | 0.195 |  -0.939∗∗ |  -0.754∗∗∗
| (0.00219) | (0.227) | (0.102) | (0.181) | (0.370) | (0.244)
$R^{2}$ | 0.914 | 0.205 | 0.479 | 0.485 | 0.087 | 0.168
Mean of Dep Var | 9.096 | -1.373 | 10.61 | 11.28 | -7.296 | 0.419
$N$ | 1109000 | 1109000 | 1109000 | 1109000 | 1109000 | 1109000

Outcomes in percentage points. Regressions include SEIN, year-quarter-state,
year-quarter-N2, and year-quarter-High fixed effects. The necessary DDD
interactions are either absorbed by the SEIN, year-quarter-state, or year-
quarter-High fixed effects. Robust standard errors clustered at state level in
parentheses. ∗ $p<0.10$, ∗∗ $p<0.05$, ∗∗∗ $p<0.01$