Spending and Job-Finding Impacts of Expanded Unemployment Benefits: Evidence from Administrative Micro Data
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NBER Working Paper No. 30315, Spending and Job-Finding Impacts of Expanded Unemployment Benefits: Evidence from Administrative Micro Data, by Peter Ganong, Fiona E. Greig, Pascal J. Noel, Daniel M. Sullivan and Joseph S. Vavra, dated August 2022, Revised August 2023. The abstract states that the largest increase in unemployment benefits in U.S. history had large spending impacts and small job-finding impacts. It lists three implications, including that increased benefits were important for explaining aggregate spending dynamics but not employment dynamics during the pandemic, and that normally low-liquidity households in a high-liquidity state still have high MPCs. The paper states that the research was made possible by a data-use agreement between three of the authors and the JPMorgan Chase Institute.
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“Spending and Job-Finding Impacts of Expanded Unemployment Benefits: Evidence from Administrative Micro Data.”
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NBER WORKING PAPER SERIES
SPENDING AND JOB-FINDING IMPACTS OF
EXPANDED UNEMPLOYMENT BENEFITS:
EVIDENCE FROM ADMINISTRATIVE MICRO DATA
Peter Ganong
Fiona E. Greig
Pascal J. Noel
Daniel M. Sullivan
Joseph S. Vavra
Working Paper 30315
http://www.nber.org/papers/w30315
NATIONAL BUREAU OF ECONOMIC RESEARCH
1050 Massachusetts Avenue
Cambridge, MA 02138
August 2022, Revised August 2023
We thank Joe Altonji, Adrien Auclert, Gabriel Chodorow-Reich, Arin Dube, Jason Furman, Jon
Gruber, Greg Kaplan, Rohan Kekre, Bruce Meyer, Matt Notowidigdo, Heather Sarsons, Jesse
Shapiro, Daphne Skandalis, Amir Sufi, Rob Vishny, and numerous seminar participants for
helpful conversations. We thank Maxwell Liebeskind, who was a coauthor on several of the
earlier JPMCI policy briefs on pandemic UI. We thank Philips Ametsikor, Samantha Anderson,
Timotej Cejka, Rupsha Debnath, Jonas Enders, Theodore Grayer, Jay Leeds, Isaac Liu, Michael
Meyer, Liam Purkey, Peter Robertson, John Spence, Nicolas Wuthenow, and Katie Zhang for
excellent research assistance. We thank the Becker Friedman Institute and the Kathryn and Grant
Swick Faculty Research Fund at the University of Chicago Booth School of Business for financial
support. This research was made possible by a data-use agreement between three of the authors
and the JPMorgan Chase Institute (JPMCI), which has created de-identified data assets that are
selectively available to be used for academic research. All statistics from JPMCI data, including
medians, reflect cells with multiple observations. The opinions expressed are those of the authors
alone and do not represent the views of JPMorgan Chase & Co. The views expressed herein are
those of the authors and do not necessarily reflect the views of the National Bureau of Economic
Research.
NBER working papers are circulated for discussion and comment purposes. They have not been
peer-reviewed or been subject to the review by the NBER Board of Directors that accompanies
official NBER publications.
© 2022 by Peter Ganong, Fiona E. Greig, Pascal J. Noel, Daniel M. Sullivan, and Joseph S.
Vavra. All rights reserved. Short sections of text, not to exceed two paragraphs, may be quoted
without explicit permission provided that full credit, including © notice, is given to the source.
Spending and Job-Finding Impacts of Expanded Unemployment Benefits: Evidence from
Administrative Micro Data
Peter Ganong, Fiona E. Greig, Pascal J. Noel, Daniel M. Sullivan, and Joseph S. Vavra
NBER Working Paper No. 30315
August 2022, Revised August 2023
JEL No. E21,E24,E32,E62,E71,G5,H3,J18,J65
ABSTRACT
We show that the largest increase in unemployment benefits in U.S. history had large spending
impacts and small job-finding impacts. This finding has three implications. First, increased
benefits were important for explaining aggregate spending dynamics—but not employment
dynamics— during the pandemic. Second, benefit expansions allow us to study the MPC of
normally low-liquidity households in a high-liquidity state. These households still have high
MPCs. This suggests a role for permanent behavioral characteristics, rather than just current
liquidity, in driving spending behavior. Third, the mechanisms driving our results imply that
temporary benefit supplements are a promising countercyclical tool.
Peter Ganong Daniel M. Sullivan
Harris School of Public Policy 875 15th St NW
University of Chicago Washington, DC 20005
1307 East 60th Street and Harvard University
Chicago, IL 60637 sullivan.dm3@gmail.com
and NBER
ganong@uchicago.edu Joseph S. Vavra
Booth School of Business
Fiona E. Greig University of Chicago
JP Morgan Chase Institute 5807 South Woodlawn Avenue
601 Pennsylvania Avenue Chicago, IL 60637
Suite 07 and NBER
Washington, DC 20004 joseph.vavra@chicagobooth.edu
fiona_greig@vanguard.com
Pascal J. Noel
Booth School of Business
University of Chicago
5807 S. Woodlawn Avenue
Chicago, IL 60637
and NBER
pascal.noel@chicagobooth.edu
1 Introduction
This paper analyzes the spending and labor market impacts of the largest increase in unemployment
insurance (UI) benefits in U.S. history. The government added supplements of $300-$600 per week on
top of regular UI benefits at various points during the pandemic as part of its policy response. These
supplements more than doubled typical benefit levels, leading most unemployed workers to receive
more income from unemployment than they had from their prior jobs (Ganong, Noel, and Vavra
2020). In total, nearly half a trillion dollars in supplements were paid out through this program. We
combine administrative bank account data, several causal research designs, and a dynamic structural
model to estimate and interpret the effects of this unprecedented increase in benefits. Overall, we find
that this increase had large effects on spending but small effects on job-finding.
Analyzing this massive increase in benefits is useful for three reasons. First, this program was
large enough to have major impacts on aggregate economic activity and cross-household inequality.
Second, the scale and persistence of these transfers provides a unique laboratory for testing implica-
tions of heterogeneous agent macro models. The supplements were big enough to push unemployed
households from what is usually a low-liquidity state into a high-liquidity state. This setting allows us
to directly assess the common and quantitatively important assumption that high marginal propen-
sities to consume (MPCs) arise from temporarily low liquidity. Third, countercyclical benefit levels
have never before been attempted at this scale, and there is no prior evidence about their impact.
Understanding their effects can inform future policy design.
Measuring the impact of expanded benefits requires a dataset with information on spending, liq-
uidity, employment transitions, and unemployment benefit receipt. We build such a dataset by using
de-identified bank account transactions from the universe of Chase customers. We observe the pre-
cise week that millions of individual households begin receiving UI supplements and trace out the
high-frequency impact of these supplements on spending, job finding, and the evolution of liquid
balances.
We first analyze spending impacts. Beginning with time-series patterns, we find a strong rela-
tionship between supplement levels and the spending of the unemployed. Spending rises when $600
supplements begin in April 2020, falls when they end in July 2020, rises when $300 supplements begin
in January 2021, and falls again when they end in the summer of 2021.
Most strikingly, we see that while the $600 supplement is available, the spending of unemployed
households rises after job loss, both in absolute terms and relative to the spending of employed
households. The increase is a reversal of the usual decline in spending that occurs during unemploy-
ment. Moreover, this increase is particularly notable since employed households substantially reduced
spending during the pandemic.
Next, we estimate MPCs out of benefits using two types of research designs. First, we use variation
induced by processing constraints from overwhelmed state UI agencies at the onset of the pandemic.
We compare unemployed workers who receive benefits immediately after job loss to those who lose jobs
at the same time but face delays in benefit receipt. Second, to identify the effects of other supplement
changes, we compare the spending of unemployed workers to that of employed workers matched on
relevant observable characteristics.
Across all designs, spending responds sharply in the exact week in which benefit levels change.
These spending responses are large across all specifications—with estimated one-month MPCs between
0.27 and 0.42—and statistically precise with standard errors of three cents or less. These findings are
1
robust to a number of measurement and sample choices, are not driven by the unusually high recall
rate during the pandemic, and are not driven by any unusual category-specific spending patterns of
the unemployed.
This high MPC is particularly notable because the supplements are themselves so large that
recipient households have elevated liquidity. Indeed, the median household who becomes unemployed
during the pandemic moves up an entire tercile of the pre-pandemic liquidity distribution. Yet these
households still have large spending responses to subsequent supplement changes. Thus, temporarily
low current liquidity cannot be the main force driving these high MPCs.
Additional analysis of MPC heterogeneity within the unemployed further bolsters this conclusion.
As an extreme example, consider a lottery jackpot winner. Whether they were short on cash before
winning the lottery should have no impact on their post-lottery-winning MPC. This same logic applies
to a policy-driven liquidity increase: it should erase any correlation between pre-lottery wealth and
post-lottery-winning MPC. Yet we find that households with lower liquidity measured years before
the pandemic have higher MPCs to UI supplements throughout the pandemic, suggesting that some
permanent household characteristic drives both high MPCs and low liquidity.
We next examine the impact of supplements on job-finding. In contrast to the supplements’ large
effect on spending, we find that they had only small effects on job finding. Looking first at descriptive
patterns, we see a dramatic decline in the job-finding rate at the start of the pandemic beginning
a month before the start of the $600 supplements. We then see a small increase in the job-finding
rate when the $600 supplements expire and a small decline in the job-finding rate when the $300
supplements begin.
To estimate the precise causal effects of the supplements on job finding, we use two research designs
that exploit distinct sources of variation in benefits. First, we use an interrupted time-series design
which relies on the overall expiration or onset of benefits. Second, we use a dose-response difference-in-
difference design which compares workers with smaller and larger changes in benefits. Both research
designs yield similar results. The implied duration elasticity of the $600 supplements is 0.06-0.11 while
for the $300 supplements it is 0.10-0.22. These job-finding effects are small, both relative to overall
fluctuations in job finding during the pandemic and relative to pre-pandemic estimates of the effects
of benefits on unemployment duration.
In the second part of the paper we interpret these empirical results through the lens of an inten-
tionally standard dynamic structural model. We discipline key features of the model using the causal
estimates from our empirical analysis.
The model is crucial for three reasons. First, the model helps us translate the high-frequency
reduced-form effects around policy changes we measure into the total dynamic effects of the policy that
we are interested in. For example, if households search harder as the expiration of the $600 supplement
approaches, then the change in job finding at expiration would understate the supplement’s effect in
earlier months. Second, it helps us interpret the magnitudes of our empirical estimates. For example,
using our model, we can compare the MPC that we estimate out of targeted UI supplements to
the much larger literature on the MPC out of untargeted stimulus checks, after accounting for the
differences between these two policies. Third, the model enables us to quantify the role of specific
mechanisms driving the spending and job-finding effects. Understanding mechanisms is necessary
both for explaining this key episode in recent macroeconomic history and for identifying which forces
generalize beyond the pandemic. Such forces may provide new lessons about household behavior and
2
future policy design.
Although a standard model is unable to match the data, we show that a model with two key
departures from the standard model is able to closely replicate our empirical results. The standard
model features perfect foresight and moderate discount rates calibrated to prior evidence on average
MPCs. In this model, households respond in anticipation of future policy changes and save most of
their UI supplements. In contrast, the data shows no anticipatory response and less-than-expected
incremental saving, even though households have relatively high liquidity. To match these empiri-
cal patterns, it is necessary for households in the model to have myopic expectations, acting as if
they are surprised by supplement changes even when such changes should be perfectly predictable.
Furthermore, to match the high MPCs we document even for high-liquidity households, unemployed
households must have especially high discount rates. In particular, in order for our model to match
both prior evidence on the MPC out of universal stimulus payments and our evidence on the MPC
out of targeted UI supplements, we need unemployed households to have discount rates that are twice
as high as those in the general population.
We first use this adjusted model to quantify the overall effects of UI supplements. Since households
in the model have limited anticipatory responses, the policy’s dynamic effects are muted. Mirroring
the reduced-form empirical estimates, the model implies that expanded UI supplements had large
effects on spending and small effects on employment. This conclusion holds both relative to overall
fluctuations during the pandemic as well as compared to pre-pandemic evidence. When comparing
to aggregate fluctuations during the pandemic, we estimate that UI supplements explain only 5%
of aggregate employment shortfalls while they explain more than 20% of the recovery in aggregate
spending. If we compare the best fit model to a standard pre-pandemic calibration, we find an
elasticity of unemployment duration to supplements that is 80% smaller and an increase in spending
while supplements are in effect that is 66% larger.
This leads to the first of three main lessons from our paper: benefit supplements were important
for explaining the aggregate dynamics of spending–but not the dynamics of employment–during the
pandemic. Furthermore, from a distributional perspective, the large spending responses that we
document can help explain why spending rose most for low-income households during the pandemic
(Cox et al. 2020) even though these same households had the biggest declines in labor income (Cajner
et al. 2020).
We next dig deeper to understand why the spending response was so large and the job-finding
response was so small.
For spending, two forces explain the large response to supplements. First, supplements target
households who have lost their jobs. In the absence of supplements, these households are low liquidity
since regular benefits do not fully replace lost earnings. This fact can help explain why unemployed
households respond strongly to the first dollar of supplements they receive. However, in total, the
supplements are so large that they actually drive households fully out of this liquidity-constrained
state. Thus, low liquidity alone cannot explain why supplements drive the spending of unemployed
above that of employed workers. Instead, unemployed households must also have some permanent
behavioral characteristics such as impatience or present-bias that lead to high MPCs even with high
liquidity. This is especially important for explaining our empirical finding that households with lower
liquidity years before the pandemic have higher MPCs to UI supplements throughout the pandemic,
even after the supplements substantially increase liquidity.
3
This leads to the second of three main lessons from our paper: permanent household characteristics—
and not just current liquidity—are also important for understanding household consumption patterns.
Prior work has documented an empirical correlation between low liquidity and high MPCs. Drawing
on this evidence, a large literature has developed models in which high MPCs arise solely from tem-
porarily low liquidity (see Kaplan and Violante 2014 and Angeletos et al. 2001). In most economic
environments, it is hard to disentangle the direction of causality that drives the liquidity-MPC cor-
relation: households facing a temporary liquidity crunch will have high MPCs, and households with
permanently high MPCs will run down their liquidity. However, the pandemic UI supplements pro-
vide a quasi-random positive shock to liquidity which allows us to observe the spending responses of
previously low-liquidity households in a high-liquidity state. The high spending responses we observe
provide direct evidence that temporarily low liquidity cannot be the only explanation for high MPCs.
For job finding, two types of forces explain why the employment distortion is small relative to
pre-pandemic estimates. First, supplements were temporary and implemented in a recession, when
the new job-finding rate was already depressed. This limits the scope for supplements to affect
employment. Second, businesses recalled many laid-off workers when they reopened and there were
pandemic-induced reductions in the sensitivity of job finding to benefits. The second group of forces
are unlikely to generalize beyond the pandemic, but the first force explains about half of the reduced
employment distortion and should generalize: short-lived increases in unemployment benefit levels,
when the job-finding rate is depressed, are likely to induce small employment distortions.
The particular forces driving large spending and small employment effects lead to the third main
lesson from our paper: temporary benefit supplements are a promising countercyclical tool. The effect
of temporary supplements on unemployment duration will be reduced when the job-finding rate is
depressed during a recession. The large spending effects of temporary supplements to the unemployed
will simultaneously be beneficial in recessions if aggregate demand is too low. Our results suggest
that targeted payments to unemployed households during recessions can provide a useful complement
to near-universal stimulus checks, which the federal government has frequently relied on to stimulate
demand. Even for a policymaker who is indifferent to distributing $1 to unemployed households versus
$1 to employed households, we find that it would be preferable from a stimulus perspective to give
up to a $2,000 one-time payment targeted to unemployed households before giving $1 of untargeted
stimulus to all households.
Our paper connects to several additional strands of past research. There is a rich empirical
literature analyzing the effect of pandemic UI supplements.1 Our paper makes two main contributions
relative to this literature. First, while other contemporaneous work has evaluated the labor market
impacts of expanded benefits, our paper is the first to study spending impacts.2 We show that the
effects on spending were much larger than the effects on employment. Second, we develop a structural
model to help interpret the empirical patterns in the data. This is crucial for enabling us to identify
which lessons are likely to generalize beyond the pandemic environment as well as for interpreting the
magnitude of the results.
Our paper is also connected to a growing literature on the relationship between MPCs and liquidity.
For example, Kueng (2018) finds that high-income households with substantial liquidity have a high
1 See, e.g., Bartik et al. (2020), Coombs et al. (2022), Dube (2021), Finamor and Scott (2021), Holzer, Hubbard,
and Strain (2021), Hornstein et al. (2022), Marinescu, Skandalis, and Zhao (2021), and Petrosky-Nadeau and Valletta
(2021).
2 This complements other work studying the spending response to pandemic stimulus checks: Baker et al. (2023),
Parker et al. (2022), Chetty et al. (2023).
4
MPC out of payments from the Alaska Permanent Fund, Fagereng, Holm, and Natvik (2021) finds
that even high-liquidity households still have a substantial MPC out of lottery winnings, and Gerard
and Naritomi (2021) shows that unemployed households have high MPCs out of severance payments
that substantially increase liquidity. In addition, Baugh et al. (2021) shows that high-liquidity house-
holds exhibit substantial MPCs to tax refunds, and Aydin (2022) shows that high-liquidity households
exhibit substantial responses to credit limit increases. Theoretical models by Lian (2021), Boutros
(2022), Andreolli and Surico (2021), and Ilut and Valchev (2023) provide psychological foundations for
such high MPCs. Furthermore, several papers provide complementary evidence that permanent het-
erogeneity is important for explaining high MPCs.3 Aguiar, Bils, and Boar (2020), and Gelman (2021)
combine panel data with a structural consumption model to disentangle the separate role of perma-
nent and transitory forces on MPCs. Parker (2017) shows that MPCs are correlated with persistent
characteristics like impatience in surveys, Patterson (2023) shows a relationship between unemploy-
ment risk and MPCs, and Garber et al. (2021) shows that “consumption binging” is systematically
related to individual characteristics in administrative data.
Our setting complements prior empirical work in this area because we directly observe pre-transfer
liquidity positions paired with a large and persistent increase in liquidity. We can use this variation
to show that households who were low liquidity years before they received a transfer continue to have
high MPCs even after they have been moved to a high liquidity state. This new evidence bolsters the
case that permanent household characteristics are important drivers of spending behavior.
Finally, our paper also contributes to a literature analyzing the optimal cyclicality of unemployment
benefits.4 Relative to this literature, we provide direct empirical micro evidence of the powerful
demand impacts of countercyclical benefits. We also identify a mechanism (permanent heterogeneity)
that amplifies the potency of countercyclical UI relative to untargeted stimulus checks. In addition,
we document a force in favor of countercyclical benefit levels arising from the interaction between
supplement length and labor market conditions. This builds on important prior work by Schmieder,
von Wachter, and Bender (2012), which shows that a similar force also applies to countercyclical
benefit durations.
2 Institutions and Data
We begin with a brief discussion of the changes in unemployment insurance policies over the course
of the pandemic and then describe the data that we use to analyze their impacts.
2.1 Expansion of Unemployment Benefits
The Coronavirus Aid, Relief and Economic Security (CARES) Act implemented a variety of policies
in response to the emerging pandemic. One provision was a massive expansion of unemployment
benefits. The CARES Act established a $600 per week supplement from April-July 2020 paid in
addition to any amount already allotted by regular state unemployment insurance. The CARES
Act also expanded eligibility for unemployment benefits to many self-employed and gig workers, who
3 We use the term “permanent” to follow the existing literature, but we are unable to distinguish between truly
permanent heterogeneity and persistent heterogeneity.
4 See e.g., Kroft and Notowidigdo (2016), Landais, Michaillat, and Saez (2018a), Landais, Michaillat, and Saez
(2018b), Mitman and Rabinovich (2015), Kekre (forthcoming), and McKay and Reis (2021).
5
would not otherwise qualify for regular benefits, through the creation of the Pandemic Unemployment
Assistance (PUA) program. Unemployed workers who qualified for UI through the PUA program
were also eligible for the $600 supplements. Because of data constraints, our analysis does not distin-
guish between regular benefits and PUA. However, most benefit recipients in the analysis sample are
receiving regular benefits.5 Finally, the CARES Act also established Pandemic Emergency Unemploy-
ment Compensation (PEUC), which extended benefit eligibility to those who would have otherwise
exhausted unemployment benefits.
The original CARES Act legislation authorized $600 supplements through the end of July 2020.
As the end of July approached, the fate of the expanded unemployment benefits remained unclear.
Congressional Democrats advocated a continuation of the $600 supplement, while some congressional
Republicans advocated a $400 supplement. Perhaps surprisingly, the two sides failed to reach any
legislative compromise and the supplement fell to zero at the start of August.6
At the end of December 2020, new legislation authorized a $300 per week supplement through
mid-March 2021. The supplement was later extended to last a total of eight months. The PEUC and
PUA supplements were also extended through early September 2021. In June 2021, several states un-
expectedly ended expanded unemployment benefits sooner than the legislated end date out of concern
that these programs were having negative effects on labor markets. We discuss how multiple policies
changing at the same time in summer 2021 complicates measurement of the effects of supplements
during this time period in Appendix A.1.
2.2 Data
Our analysis sample is drawn from the 44 million households with a checking account in the JPMorgan
Chase Institute (JPMCI) data from January 2018 through October 2021. Our primary sample runs
through February 2021 because this is when we can most reliably measure job finding and separate
the effects of supplements from effects of expanded benefit eligibility. However, we also provide some
analysis of supplements through the summer of 2021. Benefit eligibility extensions mean that UI exits
from April 2020 through February 2021 rarely reflect benefit exhaustion and therefore usually reflect a
return to work.7 For this reason, we generally use job finding and UI exit interchangeably throughout
the paper. The unit of observation is household-by-week. Our primary analysis sample consists of
1,458,481 unemployment benefit spells from 44 states in 2020. Figure A-1 shows a map of which states
are in the sample. The exact set of states included in each part of the analysis is dependent on data
availability and is described in Appendix A.2.
We measure unemployment insurance spells and labor income using information from direct de-
posits. We combine information on unemployment and employment spells to separate UI exits to a
new job from UI exits to recall, which is when an unemployed worker returns to their prior employer.
The details of how we construct these spells are described in Appendix A.3. We impose activity
5 In the two states where JPMCI can distinguish between regular benefits and PUA (Ohio and New Jersey), 74%
of observed UI spells are for households receiving regular benefits. Among households who meet the account activity
screens described below, the share is even higher.
6 On August 8, an executive order announced a “Lost Wages Assistance” (LWA) program to provide supplements for
six more weeks. However, long delays meant these LWA payments nearly always occurred after the program expired,
so we focus on the $600 and $300 supplements.
7 For example, the California Policy Lab (Bell et al. 2022) calculates that fewer than 3 in 1000 recipients exhausted
benefits during this time period. However, beginning in March 2021, there are a number of UI exits that do not reflect
job finding, due to a technical issue with how UI systems pay claims for spells that last longer than a year.
6
screens to ensure we capture workers whose primary bank accounts are at Chase and who have stable
employment prior to the pandemic (see Appendix A.4 for details).
We construct two main measures of spending. Our preferred total spending measure sums spending
on Chase credit cards, Chase debit cards, cash withdrawals, paper checks, and various electronic
payments. This measure excludes debt payments on mortgages, cars, student loans, and credit cards,
as well as transfers to other accounts. While this is the most comprehensive measure of spending
we can observe in Chase accounts, we note that it nevertheless excludes most durable purchases and
so most closely corresponds to broad non-durable spending.8 Nevertheless, two concerns arise from
this measure. First, it includes some payments where the payee cannot be identified.9 It is thus
possible that some of these transactions may not actually be spending. Second, it includes spending
with potential for timing-related measurement error if there is a delay between when a paper check is
written and when it is deposited.
We therefore also report results for a more narrow card and cash spending measure which ex-
cludes all paper checks and most electronic payments.10 Since it omits many recurring payments and
eliminates the timing-related measurement error induced by paper checks, card and cash spending is
better suited for measuring week-to-week spending changes caused by week-to-week income changes.
Nevertheless, this more narrow measure omits all payments to unknown recipients, even though many
of these actually are spending. In this sense it understates actual MPCs.
We also measure household income and checking account balances. We define income as total
inflows to Chase deposit accounts, excluding transfers. This definition captures take-home income
because we only observe income after taxes and other deductions (such as retirement account contri-
butions and health insurance premiums) are withheld. We exclude transfers (e.g., from other bank
accounts, money market accounts, and investment accounts) to avoid double-counting income. Check-
ing account balances are measured at a monthly frequency as the account balance on the final business
day of the month. We sum balances across all accounts for households with multiple Chase checking
accounts. Finally, we observe stimulus check receipt, age, number of children, and industry of work
for selected subsamples. Additional detail is provided in Appendix A.5.
Table A-1 provides summary statistics on the main flow measures of interest—income, UI benefits,
total spending, and card and cash spending—as well as checking account balances.
2.2.1 Comparison to External Benchmarks
The massive increase in unemployment benefits is readily apparent in the JPMCI data. We compare
the number of continued claims in Department of Labor (DOL) data to the number of households
receiving unemployment benefits in the JPMCI data. From early March to June, Figure A-2a shows
that these series rose by a factor of 15 in DOL and a factor of 17 in JPMCI.11
The JPMCI data also reproduce differences across states in the magnitude of the increase in UI
as well as the level of weekly UI benefits. Figure A-2b shows that the states with the largest increase
8 Most durables like cars and houses are financed, and our spending measure will not include these purchases.
9 We are unable to identify the recipient of payments made by paper check. Furthermore, apart from debt payments
and transfers to other bank accounts, we are unable to categorize the majority of remaining electronic account outflows
(e.g., those made via wire transfer, ACH, and other electronic channels).
10 We include electronic payments for utility bills because this is a form of non-durable spending.
11 The increase in UI payments to households that meet the account activity screens in JPMCI is slightly smaller,
likely reflecting the fact that the pandemic recession was particularly severe for underbanked households, who are likely
to be omitted because of these account activity screens.
7
in UI claims in DOL also have the largest increase in JPMCI, and vice versa. Figure A-2c shows that
there is a strong cross-state correlation between benefit levels in DOL and benefit levels in JPMCI,
although weekly benefit levels are a bit higher in JPMCI than in DOL. This implies that UI recipients
in JPMCI have slightly higher pre-separation earnings than the average UI recipient in each state. This
pattern is largely explained by the effect of the account activity screen, which imposes a minimum
level of pre-separation earnings that is more stringent than the eligibility requirements for UI. We
conjecture that the consumption responses we estimate are a lower bound for consumption responses
among the full population of UI recipients since this screen induces mild positive selection in terms of
labor market attachment and financial well-being.
Finally, the JPMCI data capture shifts in the industry composition of unemployment. Figure
A-3 shows that industries with the largest increase in unemployment in DOL, such as retail and
accommodation & food services, also have the largest increase in JPMCI. Industries with the smallest
increase in unemployment in DOL such as construction also have the smallest increase in JPMCI.
We conclude that the JPMCI data does a good job of capturing both the massive national in-
crease in UI receipt as well as the cross-state and cross-industry heterogeneity which can be captured
using statistics reported by the DOL. For additional analysis of the representativeness of unemployed
households in JPMCI data, see Ganong and Noel (2019).
3 Spending Responses to Expanded Unemployment Benefits
This section explores the empirical effects of unemployment benefits on spending. We begin with
descriptive analysis. We next identify MPCs separately out of the onset of benefits, the expiration of
the $600 supplement, the onset of the $300 supplement, and the expiration of the $300 supplement.
Each of these empirical exercises has distinct advantages and disadvantages, but they all lead to the
same conclusion: spending is highly sensitive to changes in unemployment insurance benefits.
3.1 Time-Series Patterns: Spending of the Unemployed Rises After Job
Loss When Expanded Benefits Available
Figure 1 compares changes in income, spending, and checking account balances for households who
become unemployed and receive UI from April 2020 through February 2021 to similar households
who remain employed through February 2021. Throughout the paper, whenever we compare em-
ployed to unemployed households, we reweight the employed sample so that it exactly matches two
observable characteristics of the unemployed: 2019 income quintile and date of stimulus check receipt.
Matching by income is potentially important since low-income households were more likely to become
unemployed during the pandemic (see Table A-1) and households at different points of the income
distribution may have spending that evolves differently over the pandemic. Matching by stimulus
check date is potentially important since these stimulus checks arrive around the time that both the
$600 and $300 supplements start. We later show results for a richer set of observable controls, and
conclusions are also similar without any matching.
Figure 1 shows that income for the unemployed rises and falls with the ebb and flow of benefit sup-
plements. Prior to the start of unemployment, month-to-month changes in income are nearly identical
for the two groups. Note that the matching procedure described above generates similarity in only
8
Figure 1: Income, Spending, and Account Balances of Unemployed Versus Employed
Percent difference from January 2020 (mean)
Income
$300
supplement
available
20%
● ●
●
● ● ●
● ●
0% ●
●
●
● ●
●
● ● ●
● ● ● ●
● ●
●
●
$600
●
supplement
−20% available
Spending (total)
15%
10% ●
●
● ●
5% ● ●
●
●
● ●
● ●
0% ●
●
● ●
●
● ●
● ●
● ● ●
−5% ●
●
Checking account balance
50%
25% ●
●
●
● ●
●
●
●
● ●
●
●
● ●
●
0% ● ●
● ●
●
●
●
● ● ●
●
Jan '19 Apr '19 Jul '19 Oct '19 Jan '20 Apr '20 Jul '20 Oct '20 Jan '21
Unemployed (get benefits from April 2020 through February 2021)
● Employed
Notes: This figure compares income, spending, and checking account balances of unemployed and employed households
using JPMCI data. The blue line shows households that receive unemployment benefits from April 2020 through at
least February 2021. The orange line shows employed households who are matched on 2019 income quintile as well as
date of receipt of stimulus checks. The $600 supplement is first paid in the middle of April, so May is the first complete
month during which households have the opportunity to spend the supplement.
the level of income; the similarity of pre-pandemic changes in income between the two groups is not
mechanical. Beginning with the start of unemployment, income of the two groups diverges substan-
tially. Since the combination of regular UI plus the $600 supplement results in average replacement
rates above 100 percent, income actually rises substantially for the unemployed from April through
July 2021. At the end of July, the $600 supplements expire, and so the income of the unemployed
falls below that of the employed. Income rises briefly in September 2020 with the payment of tempo-
rary LWA (Lost Wages Assistance) supplements. Finally, income rises again for the unemployed in
January 2021 when the $300 supplement begins.
After households become unemployed and receive $600 weekly supplements, their spending rises
substantially above pre-pandemic levels. The middle panel of Figure 1 shows the evolution of monthly
9
spending for the two groups. Like income, spending of the unemployed evolves nearly identically to
the employed prior to the point of unemployment and then rises sharply at the start of unemployment
in April 2020. This is especially notable when compared to the declining spending of employed
households in this early part of the pandemic. Usually unemployed households reduce spending
relative to employed households (Gruber 1997), but during the period of $600 supplements, these
normal patterns are reversed. This sustained increase in relative spending occurs for the entire time
the $600 supplement is in place. When the supplement terminates at the end of July, there is then an
immediate decline in spending. This is followed by a temporary rebound when unemployed households
receive temporary LWA supplements in September. Spending then remains depressed until the $300
supplements begin in January 2021. These supplements lead to a median replacement rate of 100%
and the spending of unemployed and employed households is similar after they begin. Thus, we
find a strong relationship between unemployment benefit levels and the spending of the unemployed
throughout the pandemic.12
The bottom panel of Figure 1 shows that there is also a large and sustained increase in the
checking account balances of unemployed households, both in absolute terms and relative to employed
households. Increases in income for unemployed households during this period were so large that they
accumulated additional savings even as their spending increased.
Our finding of significantly increased spending among unemployed workers is reminiscent of the
striking pattern documented in Gerard and Naritomi (2021). That paper shows that unemployed
workers who receive severance pay in Brazil from 2010 to 2012 sharply increase spending upon un-
employment. Thus, both severance pay in Brazil and pandemic supplements in the U.S. are settings
where workers should expect low income in the future (if they remain unemployed) and nevertheless
increase their spending in absolute terms in the present because of a temporary influx of cash. We
complement the Gerard and Naritomi (2021) evidence in two ways. First, we show that such an
increase in spending can last for many months. Second, because we can also track liquid balances,
we are able to show that such an increase can persist even when households have been pushed far
off their liquidity constraints. These relationships between liquidity and spending will be important
when we turn to model interpretations and policy implications.
We now use difference-in-difference research designs to estimate the MPC out of benefits. Some of
these research designs will use comparisons between unemployed and employed, as in Figure 1, while
others will rely on comparison between various groups of unemployed households.13
3.2 Estimating MPCs
3.2.1 Waiting for Benefit Receipt
State unemployment agencies were overwhelmed by the large increase in unemployment claims at the
start of the pandemic, meaning that the payment of many claims was delayed. We use these delays
in payment to identify the causal impact of benefits on spending. We compare the spending of a
treatment group of unemployed households who receive benefits promptly after filing a claim to the
spending of a control group of unemployed households who experience delays in receiving benefits.
12 Figure A-4 shows that similar patterns hold for medians instead of means, and Figure A-5 shows that all of the
same patterns are present when looking at the subset of spending on card and cash.
13 The employed are only a valid control group for the unemployed in times where their income would have moved
similarly absent supplements. This assumption would clearly be violated at the start of unemployment in April 2020,
when the income of unemployed would have fallen relative to the employed absent supplements.
10
To construct these groups, we compare cohorts of unemployed households, all of whom stop receiving
paychecks at the end of March but differ in the date of first benefit payment. Since households who
face delays ultimately receive back pay for missed payments, the treatment is therefore the timing of
the arrival of liquidity, analogous to how Johnson, Parker, and Souleles (2006) study variation in the
timing of stimulus checks.14 Focusing on the difference between two groups of unemployed households
removes any direct effects of job loss itself on spending and isolates the effect of benefit receipt.
The top panel of Figure 2 shows weekly patterns of unemployment benefits for four different
groups of unemployed households. We look at weekly relationships because this provides the sharpest
illustration of the exact temporal relationship between benefits and spending. We note that this
requires spending which can be measured precisely at the weekly level. For this reason, we focus on
weekly card and cash spending for this high frequency analysis. By construction, benefits are zero for
each group prior to the first benefit week and then jump in the first week of benefits. Groups that
start benefits later have larger jumps because of back pay. All groups have similar spending in levels
and trends prior to the start of UI benefits. The bottom panel shows that spending jumps sharply in
exactly the week when benefits start. It then remains at an elevated level in subsequent weeks.
Figure 2: Impact of Delays in Unemployment Benefits on Spending
Weekly unemployment insurance benefit
$2,000
$1,500
●
● ●
$1,000 ●
● ● ●
●
$500
$0 ● ● ● ● ● ● ● ● ● ● ● ● ●
Spending (card and cash)
●
$700 ●
● ●
●
●
●
●
● ●
● ● ●
$600 ●
●
● ● ●
$500
●
●
$400 ●
Jan '20 Feb '20 Mar '20 Apr '20 May '20
● April 5 April 19
Week of first benefit
May 10 May 31 (control)
Notes: This figure shows mean benefits and spending for several cohorts of unemployed households using JPMCI data.
All households stop receiving paychecks at the end of March, but differ in the date of first benefit payment.
To estimate a monthly MPC for total spending we use a difference-in-difference design which
compares spending for a treatment group that receives benefits at the start of April 2020 to a control
14 If the waiting group expects to receive benefits in the future, then the waiting MPC will only capture liquidity
effects and not any income effects of benefit receipt on spending. Thus, the waiting MPC should be a weak lower bound
on the true MPC out of benefits.
11
group that receives benefits at the start of June.15 We compute a monthly MPC because it allows us
to use this broader spending measure and because it eases comparison to the prior literature. Figure
A-6 shows that patterns for total spending are similar patterns to card and cash spending in Figure
2. We estimate an instrumental variables (IV) regression with the second stage given by equation (1)
and the first stage given by equation (2):
ci,t = ψ + M P C × ybi,t + T reati + P ostt + εi,t , (1)
yi,t = α + βP ostt × T reati + T reati + P ostt + ϵi,t (2)
where t = {M arch, M ay}, T reat = 1 for households who become unemployed at the end of March
and start benefits in April and T reat = 0 for households who become unemployed at the end of March
but start benefits in June, P ostt = 1 if t = M ay and P ostt = 0 if t = M arch.16 The identifying
assumption is that absent the start of unemployment benefits, the change in spending between March
and May for the treatment group would be the same as the change in spending for the control group
(cov(P ostt × T reati , εi,t ) = 0).17
We estimate a one-month MPC out of UI benefits of 0.42 in Table 1. This estimate implies that
nearly half of unemployment benefits are spent in the first month after receipt. Gauging whether this
is large or small requires a model, since the MPC out of benefits depends on the expected persistence of
benefit changes, whether these changes are anticipated or not, and on household liquidity. In Section
5, we develop such a model and show that this MPC is large relative to prior work.
Although we think this waiting design provides our sharpest identification strategy, it has two im-
portant limitations: First, it measures the MPC out of total unemployment benefits (regular benefits
plus the $600 supplements) rather than the response to the supplements alone. Second, it measures
spending during the early, most uncertain days of the pandemic and so it might have less generaliz-
ability. For these reasons, we turn to an analysis of supplement changes at later dates.
3.2.2 Supplement Changes
We next show that changes in benefit supplements alone also have a substantial impact on spending.
We study the expiration of the $600 supplement at the end of July 2020, the onset of the $300
supplement in January 2021, and the end of the $300 supplement in the summer of 2021.
Our main identification strategy compares unemployed and employed households, so our identifying
assumption is that spending changes at a point in time would have been the same for the unemployed
and employed absent supplement changes. While this assumption is unlikely to hold for the time-series
as a whole, there are no obvious economic events that should violate this assumption at the exact
time that the supplements expire or begin. As in Section 3.1, we use a group of employed households
15 Because this is a two-period two-group research design, it is not subject to the concerns raised in the recent literature
on staggered implementation difference-in-differences.
16 The $600 supplement is first paid in the middle of April 2020, so M ay is the first complete month during which
households have the opportunity to spend the supplement.
17 Two types of evidence suggest that delays in benefits are orthogonal to other determinants of spending behavior.
First, owing to the high volume of claims, overall delays in payments to eligible claimants were much longer than usual
(Bitler, Hoynes, and Schanzenbach 2020) and it is unlikely that state UI systems were able to prioritize claims in ways
that would be correlated with spending behavior. Second, Figure 2 shows that not only are the trends in card and cash
spending prior to benefit receipt similar by cohort (the standard parallel pre-trends test), but the levels of spending
are similar across cohorts as well. The similarity of levels and of pre-trends for spending suggests that the identifying
assumption is satisfied.
12
Table 1: Marginal Propensity to Consume out of Unemployment Benefits
Research Design One Month MPC
(Total Spending)
1 Waiting for benefits 0.42
(0.01)
2 Expiration of $600 supplement 0.31
(0.01)
3 Onset of $300 supplement 0.28
(0.01)
4 Expiration of $300 supplement (June states) 0.35
(0.02)
5 Expiration of $300 supplement (September states) 0.27
(0.01)
6 Expiration of $300 supplement (June vs. September states) 0.39
(0.03)
Notes: This table shows estimated one-month MPCs using spending (total) for several different unemployment benefit
changes using equations (2) and (1). The waiting for benefits design compares unemployed households receiving benefits
to those who face benefit delays. Rows (2) through (5) compare unemployed households to a sample of employed
households matched on pre-separation income and date of stimulus checks. Row (6) compares unemployed households
in states which ended $300 in June to unemployed households in states which ended $300 in Sept. The total number
of observations (treatment + control) in these five designs is respectively N=52,094; N = 247,770; N = 145,978; N=
153,277; N=47,623. Standard errors are clustered by household.
matched on pre-pandemic income and stimulus check date, since these are the most obvious potential
confounds. To validate this identifying assumption, we study the evolution of spending for unemployed
and employed households prior to the policy changes. Figures A-7 and A-8 show similar pre-trends
prior to the expiration of the $600 supplement and the onset of the $300 supplement respectively.
The supplements have an immediate visible impact on spending. Spending on card and cash drops
sharply at the expiration of the $600 supplement (Figure A-7) and rises sharply at the onset of the
$300 supplement (Figure A-8). Effects on total spending are also noticeable in Figures A-9 and A-10,
but a bit harder to detect visually because of week-to-week fluctuations in spending for both the
unemployed and employed.
We estimate the one-month MPC out of supplement changes using the IV approach in equations
(2) and (1). For expiration of the $600 supplements, we define t = {July, August}, and set P ost
equal to one in August and zero in July. The control group is the set of households with continuous
employment, and the treatment group is the set of households who begin benefits by June 14 at the
latest and continue receiving benefits through at least August 30. For onset of the $300 supplements,
we define t = {December, January}, and set P ost equal to one in January and zero in December.
The treatment group is households that are unemployed from November 2020 through February 2021.
Table 1 shows that we find an MPC of 0.31 at the expiration of $600 and an MPC of 0.28 at the onset
of $300 supplements.
Figures A-11 and A-12 show the time-series of spending for the summer of 2021. Table 1 also
shows estimates of MPCs to the end of $300 supplements. As we discuss in more detail in Appendix
A.1, the fact that these supplements expire at the same time as expanded eligibility programs (PEUC
and PUA) means that we can only estimate these MPCs for a subset of short-duration unemployed
13
households who continue to receive benefits after all pandemic unemployment programs end. Thus,
we focus less on these results. However, two observations are of note: first, the estimate of MPCs in
row (5) of Table 1 for the expiration of the $300 supplements is similar to the estimate in row (3) for
the start of the $300 supplements. Second, since states vary in the timing of their expiration, we can
construct controls that use unemployed households in other states and compare this to identification
strategies that instead compare to employed households. Row (6) in Table 1 shows that a design
using unemployed households as controls produces an estimate similar to the design in row (4), which
uses employed households as controls. This suggests that employed households are likely to be an
appropriate control group even in the other instances where we have no natural unemployed group as
a control. Appendix B.1 provides additional detail on this analysis.
3.3 Persistent Spending Differences within the Unemployed
Our results thus far have focused on estimating the average MPC to UI supplements for the unem-
ployed. In this section we show that there is a strong relationship between liquidity buffers measured
long before the pandemic and spending responses to UI supplements. We measure median monthly
liquidity buffers for each household in 2018, intentionally choosing a measure years before the UI
supplements in 2020-2021. See Appendix B.2 for additional details.
Figure 3 shows that households with below-median liquidity buffers in 2018 have larger spending
responses to UI supplements than households with above-median liquidity buffers in 2018. Table 2
repeats our causal identification strategies splitting by liquidity and similarly shows that the MPC
to each supplement change is about twice as large for households with low liquidity years before the
pandemic.
Figure 3: Spending by Pre-Pandemic Liquidity
Percent difference from January 2020 (mean total spending)
High 2018 Liquidity Low 2018 Liquidity
$300 $300
supplement supplement
20% available 20% available
10% 10% ● ●
● ● ●
●
●
● ●
●
● ● ●
● ● ●
●
● ●
● ● ● ●
● ●
0% ●
●
●
● 0% ● ●
● ● ● ●
●
● ● ● ●
● ● ●
●
● ●
● ●
● ●
●
−10% ●
−10%
$600 $600
supplement supplement
available available
Jan '19 Jul '19 Jan '20 Jul '20 Jan '21 Jan '19 Jul '19 Jan '20 Jul '20 Jan '21
Unemployed (get benefits from April 2020 through February 2021)
● Employed
Notes: This figure compares the spending of unemployed and employed households separately by liquidity. The left
panel shows results for households with high (above median) 2018 liquidity and the right shows results for those with
low (below median) 2018 liquidity.
In Section 5.3.3, we interpret this evidence through the lens of a structural model of consumption.
This evidence is useful for evaluating the extent to which “temporary low liquidity causes high MPCs”
14
Table 2: Marginal Propensity to Consume out of Unemployment Benefits by Liquidity
Design High Liquidity MPC Low Liquidity MPC Difference
Waiting for Benefits 0.29 0.53 0.24
$600 expiration 0.20 0.42 0.22
$300 onset 0.19 0.35 0.16
$300 expiration Sept states 0.18 0.36 0.18
$300 expiration June states 0.22 0.46 0.24
$300 expiration June vs. Sept states 0.24 0.51 0.26
Notes: This repeats Table 1 splitting by high (above median) 2018 liquidity and low (below median) 2018 liquidity.
versus “permanently high MPCs cause low liquidity”. The fact that pandemic-era MPCs are so much
higher for households with low liquidity years prior to the pandemic supports the latter view.
3.4 Robustness and Additional MPC Results
Appendix B.3 shows four additional results. First, we decompose the MPCs into separate categories,
and show that the category-level MPCs do not suggest unusual spending patterns. Further, the fact
that the spending of employed households is depressed during the pandemic makes the large MPCs
we estimate even more noteworthy. Second, we show that spending patterns are nearly identical for
households who are recalled and those are who are not, suggesting that MPCs are not driven by the
unusually high recall rates during the pandemic. Third, to address concerns about MPC estimates
being biased by selection into unemployment, we show that our results are robust to using a richer set
of controls when comparing employed and unemployed households. Fourth, our conclusions are also
robust to limiting the sample to households for whom we observe a more complete lens on spending,
and also to alternative measures of spending.
4 Disincentive Effect of Benefit Supplements
This section estimates the effect of benefit supplements on the exit rate from unemployment. This
is particularly useful because there was widespread uncertainty over whether more generous benefits
were responsible for low re-employment rates during the pandemic.18 Our estimates imply an elasticity
of unemployment duration with respect to both the $300 and $600 supplements which is smaller than
typical estimates in the past literature.
We focus primarily on the exit rate to new jobs rather than to recalls. This is because UI eligibility
requires recipients to accept any offer of “suitable work,” which should reduce the sensitivity of recalls
to benefits. Nevertheless, Figure A-13 shows patterns for the recall rate and the total exit rate, and
Section 4.4 discusses additional results for recall.
Figure 4 shows that at the start of the pandemic, the weekly new job-finding rate plunges by four
percentage points and remains depressed thereafter. It also shows that the job-finding rate modestly
18 For example, a contemporaneous IGM survey of economists showed that a majority were uncertain about whether
supplements were a “major disincentive to work” (Initiative on Global Markets 2021). The share who were uncertain
about the disincentive was higher than for more than 93% of the other IGM survey questions asked since January 2020.
15
rises and falls with the expiration and onset of the supplements. These descriptive patterns suggest
that the supplements may modestly reduce job-finding rates, but that these effects were dwarfed by
other factors holding back job finding during the pandemic.19 We turn next to research designs that
identify the causal effect of supplements on job finding.
Figure 4: Exit Rate from Unemployment Benefits to New Job
Exit rate to new job from unemployment benefits
6% ●
● ● ●
●
●
● ●
●
●
4%
●
●
●
● ● ● ● ● ●
●
●
● ● ● ● ● ●
● ● ●
● ● ●
● ●
2% ●
● ● ●
●
●
● ●
● ● ● ●
● ● ●
● ● ● ●
●
● ●
$600 supplement $300 supplement
available available
0%
Feb '20 Apr '20 Jun '20 Aug '20 Oct '20 Dec '20 Feb '21
Notes: This figure shows the exit rate to new jobs in JPMCI data. There was a brief lapse in pandemic UI eligibility
expansions (PUA and PEUC) at the end of 2020, so many workers stop receiving UI benefits on January 3 and January
10, as shown in Figure A-15. However, this does not reflect a change in the new job-finding rate, so we drop these dates
in the figure and estimation.
4.1 Research Design 1: Interrupted Time-series
We use an interrupted time-series design to estimate the effect of the supplements on the new job-
finding rate. Specifically, we study the change in the average job-finding rate in the two weeks prior
to the policy change relative to the first four weeks after the policy change as illustrated in Figure
A-16. The identifying assumption is that this rate would have been constant had there been no
change in the supplement. This is a strong assumption, but we are using high-frequency weekly data
so any confounding changes must occur at exactly the same time as the changes in supplements. In
the next section, we use an alternative research design which is not subject to potential confounding
high-frequency aggregate shocks. We find that the job-finding rate rises by 0.76 p.p. when the $600
supplement expires, and falls by 0.59 p.p. after the onset of the $300 supplement. These effects are
economically small, as we discuss in more detail in Section 4.3.
To assess statistical significance, we rely on the fact that the legislated duration of pandemic
unemployment policies in the CARES Act was based on a highly uncertain forecast in March 2020
about the duration of the pandemic. This motivates an approach to inference which treats the exact
19 The sharp decline in the new job-finding rate during the pandemic is not driven by changes in the composition of
who is unemployed; Figure A-14 shows that very similar aggregate dynamics are apparent for the subset of workers who
were unemployed before the pandemic began.
16
Figure 5: Distribution of Placebo Estimates
Change in exit rate: supplement change vs. placebo dates with no change
8
Number of placebo estimates
6
4
Onset of $300 Expiration of $600
supplement supplement
2 Change: Change:
−0.59 p.p. 0.76 p.p.
0
−0.004 0.000 0.004 0.008
Change in exit rate
Notes: This figure shows the distribution of the test statistic for every placebo date from April 2020 through February
2021, where we define placebo windows as those with no policy change. The changes at the actual supplement changes
are more extreme than the changes at any of the placebo dates. If we assume that the date of the supplement change
is random, this implies that we reject the null hypothesis of no effect of the supplement with p = 1/31.
date of the policy change as random. We compare the change in the job-finding rate at the actual
dates of policy implementation to the change in the job-finding rate at 30 placebo dates where there
was no implementation of a new policy. Figure 5 compares the distribution of the changes in the
job-finding rate at the placebo dates to the changes at the actual implementation dates. The observed
changes at the policy implementation dates are more extreme than any of the changes at the 30
placebo dates. Thus the p-value for the null hypothesis that the policy has no effect and the change
we observe occurred at random is .032 = 1/31 if we include the own implementation date and exclude
the implementation date of the other policy.
4.2 Research Design 2: Difference-in-difference
As a complement to the interrupted time-series analysis, we use an alternative difference-in-difference
design to estimate the impact of supplements on job finding. Because the supplements added a con-
stant dollar amount to every worker’s benefit, there is heterogeneity in the change in the replacement
rate (the ratio of benefits to pre-separation earnings). For example, a worker with pre-separation
earnings of $600 per week and a regular weekly benefit of $300 would see their replacement rate rise
to 150% under a $600 supplement, while a worker with pre-separation earnings of $1,200 per week and
a regular weekly benefit of $600 would see their replacement rate rise to 100%. This heterogeneity in
the intensity of treatment motivates a dose-response difference-in-difference research design. To mea-
sure the intensity of treatment for each worker we compute the symmetric percent change in benefits
around supplement changes:
2(bi,post − bi,pre )
P ctChangei = . (3)
bi,pre + bi,post
17
We measure the worker’s pre-treatment benefit bi,pre as the median weekly payment in the two-month
period before a policy change. Given bi,pre , we then impute bi,post based on statutory rules.20
Figure 6 shows the evolution of exit rates, dividing workers into groups with higher-than-median
P ctChangei and lower-than-median P ctChangei . Two lessons emerge from the figure. First, the two
groups have similar trends in the job-finding rate before the policy changes. Second, the policy changes
induce differential changes in exit rates for those who are differentially treated by the policy changes:
when the $600 supplement ends, the job-finding rate rises more for the higher P ctChange group, and
when the $300 supplement begins, the job-finding rate falls more for the higher P ctChange group.
Figure 7 uses a bin scatter of benefit growth and exit rate changes to show that the same conclusions
hold using the full range of P ctChange instead of splitting by above/below median changes, and that
this relationship is roughly linear in P ctChange.
To quantify the causal effect of replacement rates on the job-finding rate, we use a difference-in-
differences regression that captures the variation in Figure 7. Let t index periods, i index workers,
and eit be an indicator for exit to new job. We use data on eight weeks where the supplement is not
available and eight weeks where the supplement is available as captured by the indicator SuppAvailt .
We estimate the model:
eit = γP ctChangei + αSuppAvailt + βSuppAvailt × P ctChangei + εit (4)
We discuss the assumptions needed for this regression to identify the causal effect of benefits on
job-finding in Appendix C.2.21 The key coefficient of interest in equation (4) is β̂, which captures how
the job-finding rate changes for more-treated vs less-treated workers. Table A-2 shows that at $600
expiration, we estimate β̂ = −0.016 and at $300 onset, we find a similar coefficient of β̂ = −0.020.
These effects are precisely estimated with a standard error of 0.001 with standard errors clustered at
the household level.
4.3 Interpreting Magnitudes
What do the results from our two different identification strategies imply for the effect of supplements
on job finding? Table 3 shows our headline estimates of how UI supplements affect the job-finding
rate. We estimate that the $600 supplement reduces the weekly job-finding rate by 0.76 p.p. using the
interrupted time-series estimates and by 1.45 p.p. using the difference-in-difference estimates. The
$300 supplement reduces the job-finding rate by 0.59 p.p. using time-series estimates and by 1.18 p.p
using difference-in-difference estimates. Thus, the difference-in-difference estimates are about twice
the size of the time-series estimates.22 However, as we discuss below, all four of these estimates are
economically small. Because the two different research designs rely on orthogonal sources of variation
in benefits, the similarity of the estimates (in terms of their economic effects) across the two designs
20 This imputation is necessary because we do not observe b
i,post for workers who find a job before the $600 supplement
has expired or before the $300 supplement has been reinstated. See Appendix C.1 for details.
21 We note that while Cox models are frequently used in the literature on UI disincentives, they are not suited for
studying within-spell policy changes. Our baseline specification uses a linear probability model given the linearity shown
in Figure 7 as well as the linearity implied by our theoretical model in Section 5.
22 This effect is directly implied by the interrupted time-series estimate, but additional assumptions are required to
get to this total effect from the marginal effects identified by the difference-in-difference design. Although our analysis
treats the two research designs as estimating the same parameter, one possibility for why time-series estimates are
smaller is if “micro” disincentive effects of UI (the effect of giving one worker more benefits) is bigger than the “macro”
disincentive effect (the effect of giving all workers more benefits). See Appendix C.3 for further discussion.
18
Figure 6: Effect of Expanded Benefits: Event Study
(a) Expiration of $600
Exit rate to new job relative to June/July group average
250%
●
200% ●
● ●
●
●
●
●
●
150%
●
●
●
100% ●
●
●
●
●
50%
Higher PctChange
$600 supplement
● Lower PctChange
available
0%
Jun '20 Jul '20 Aug '20 Sep '20 Oct '20
(b) Onset of $300
Exit rate to new job relative to November/December group average
$300 supplement
available
150%
●
● ● ●
● ●
●
100% ● ● ●
●
● ●
● ● ●
●
●
50%
Higher PctChange
● Lower PctChange
0%
Nov '20 Dec '20 Jan '21 Feb '21 Mar '21
Notes: This figure shows the exit rate to new jobs around the expiration of the $600 weekly supplement and the
onset of the $300 weekly supplement in the JPMCI data. The orange line shows workers with a lower-than-median
replacement rate with the supplement and the blue line shows workers with a higher-than-median replacement rate
with the supplement. Exit rates are normalized by the average exit rate during the period before the policy change
(June and July for the expiration of the $600 and November and December for the onset of the $300). Panel (b) omits
a mechanical surge in exits on January 3 and 10 arising from the lapse in expanded UI eligibility. Figures A-17a and
A-17b show the same figure but without a normalization in the pre-period. Figures A-17c and A-17d show that the
same patterns hold when we look at the total job-finding rate (which includes both new job finding and recalls).
bolsters the conclusion that the supplements had small effects on the job-finding rate.
It is also useful to compare the effects of the $600 supplement to the effects of the $300 supplement.
We report comparisons in two ways. First, we convert each estimate of the full supplement effect
into an implied per-week causal effect of increasing benefits by $100 relative to a no-supplement
baseline.23 Table 3 shows that effects per $100 were similar for both the $600 supplements and the
23 The models in Section 4.2 are estimated using symmetric percent change P ctChange . The average of P ctChange
i i
is 81% for the $600 supplement and 57% for the $300 supplement. Note that because we are using symmetric percent
change in equation (3), P ctChangei is not linear in the size of the supplement. Relative to a no-supplement baseline,
paying a $100 supplement has an average value of 20% for P ctChangei . We therefore rescale the estimates from the
$600 supplement by 20%/81% and the estimates from the $300 supplement by 20%/57%.
19
Figure 7: Effect of Expanded Benefits: Difference-in-Difference Binscatter
(a) Expiration of $600
Change in average exit rate to new job
●
0.015
●
Slope:−0.016
Standard error: 0.001 ●
●
●
0.010
● ●
●
●●
0.005 Larger decrease Smaller decrease
in benefits in benefits
−120% −100% −80% −60%
Change in benefits
(b) Onset of $300
Change in average exit rate to new job
●
0.000 ●●
●
●
●
Slope:−0.020 ●
−0.005 Standard error: 0.001
●
−0.010 ●
●
Smaller increase Larger increase
in benefits in benefits
−0.015
30% 50% 70% 90% 110%
Change in benefits
Notes: This figure shows the change in the new job-finding rate at the expiration and onset of benefit supplements
separately for deciles of the change in benefits as measured using equation (3). The top panel shows the difference in
the average new job-finding rate between Jun 1-Jul 31 and Aug 1-Sep 31. The bottom panel shows the difference in
the average new job-finding rate between Nov 1-Dec 31 and Jan 15-Mar 15. The slope estimates correspond to the β̂
coefficients reported in Table A-2.
Table 3: Effect of Supplements on Weekly Job-Finding Rate
Interrupted time-series Difference-in-difference
Effect of... Entire supplement per $100 Entire supplement per $100
$600 expire -0.76 -0.19 -1.40 -0.35
$300 onset -0.59 -0.20 -1.18 -0.45
Notes: This table shows the effect in percentage points of benefit supplements on the weekly new job-finding rate. Row
one uses estimates from the $600 expiration and row two uses estimates from the $300 onset. Note that because we use
symmetric percent changes, the per $100 effect is not 1/6 (1/3) of the total effect of $600 ($300). See footnote 23.
20
$300 supplements. Second, since elasticities are scale invariant, we compute a duration elasticity to
benefit levels. We calculate this duration elasticity from the effects in Table 3 by assuming constant
per-week effects on the job-finding rate while supplements are in place. Details of this calculation are
in Appendix C.4. We find that the duration elasticity is 0.06 to the $600 supplements and 0.10 to the
$300 supplements using estimates from the time-series design, and 0.11 and 0.22 using estimates from
the difference-in-difference design. While elasticities using difference-in-difference estimates are larger,
overall Figure 8 shows that these duration elasticities are significantly smaller than estimates in the
prior literature surveyed in Schmieder and von Wachter (2016). These findings are consistent with the
hazard elasticities reported in Bell, Hedin, and Schnorr (2022), Petrosky-Nadeau and Valletta (2021),
and Coombs et al. (2022).24
Figure 8: Pandemic Elasticity Estimates Compared to Prior Literature
Notes: The pre-pandemic estimates are from the literature review by Schmieder and von Wachter (2016).
4.4 Additional Job-Finding Results and Robustness
Appendix C.5 shows various robustness results and extensions, which we briefly summarize here.
First, we include additional fixed effects so that identification comes only from comparing the job-
finding rate for workers with different P ctChange who are in the same state, are the same age, and
worked in the same industry. Second, we show that similar results obtain when re-estimating a weekly
event study design rather than our baseline specification which pools together all pre- and post-weeks.
Third, we show that specifications which look at proportional changes or explicitly model exit as a
binary outcome deliver similar conclusions.
Fourth, we analyze how the supplements affect recalls. While it appears that the expiration of
the $600 supplement might have had a small effect on recalls, this evidence is hard to interpret, and
24 Other studies which tend to find small effects but do not report hazard or duration elasticities include Bartik et al.
(2020), Finamor and Scott (2021), Holzer, Hubbard, and Strain (2021), and Marinescu, Skandalis, and Zhao (2021).
21
even the upper bound of plausible causal impacts on recalls still implies small aggregate employment
effects. There is no evidence of any effect of the $300 supplement on recalls.
Finally, we estimate the disincentive effects of benefits on job finding using the expiration of
the $300 supplements in September 2021. The analysis of this policy change is complicated by the
simultaneous expiration of expanded benefit eligibility (PEUC and PUA programs). This complication
ultimately reduces precision of our estimates substantially. Nevertheless, we find point estimates which
are similar to those that we estimate for the start of the $300 supplements.
5 Model
In this section, we develop a model that helps us interpret the reduced form results along three
dimensions. First, it helps us better gauge whether the effects we measure are big or small. Second,
it lets us explore whether accounting for dynamics changes our interpretation of the reduced-form
empirical results. For example, if households gradually increase search as the expiration of supplements
approaches, then the change in job finding at expiration would understate the supplement’s overall
effect. Third, it helps us to understand what effects are likely to generalize beyond the pandemic and
to what extent alternative policies would have had different effects.
5.1 Model Description
Our model combines an incomplete markets consumption-savings problem with a model of costly job
search. Each of these elements is intentionally standard because part of the goal of the model is to
understand what a standard model calibrated to pre-pandemic evidence predicts about the effect of
supplements on spending and job finding. We describe the main elements here and provide additional
details in Appendix D.1.
Households choose consumption c and savings a to maximize Constant Relative Risk Aversion
utility, subject to a no-borrowing constraint a ≥ 0. When employed, a household i receives a constant
wage wi . wi differs across households but is constant over time for each household. When employed,
households face a constant exogenous separation rate into unemployment.
When unemployed, households find a job with probability fi,t = recallt + searchi,t where recallt
is a common exogenous recall rate and searchi,t ∈ [0, 1 − recallt ] is household i′ s endogenous choice
of search effort. Search effort induces additive disutility ψ(searchi,t ). When unemployed, households
receive regular unemployment benefits, which are proportional to wi . Regular benefits last for 6
months in normal times but are extended to 12 months at the start of the pandemic.
Beginning from this initial steady state, the economy is hit by a sequence of aggregate policy
changes that capture changes in UI policy over the pandemic: weekly supplements of $600 are added
to unemployment benefits from April-July 2020 and then $300 supplements are added from January-
August 2021. We focus on the evolution of unemployed households relative to employed households
in both the model and data to remove pandemic effects that affect everyone equally.25
25 For example, the model includes stimulus checks and transitory changes in impatience to match the large increase
in savings in April 2020, but these play little role in our analysis and so we leave their discussion to Appendix D.1.
22
5.1.1 Modeling Choices: Disciplining Job Search Costs, Expectations, and Impatience
Most of our parameter choices follow the prior literature. We summarize them in Table A-3 and
discuss them further in Appendix D.1. Here, we discuss three key model components: search costs,
expectations, and impatience. For each component, we examine two scenarios. First, we study a
“standard” calibration which targets empirical evidence from the pre-pandemic literature and makes
assumptions about beliefs which are standard in the literature. This model has low job-search costs,
perfect foresight, and moderate discounting. However, relative to the data this model produces too
much anticipatory behavior and too much saving. We therefore also study an “alternative” calibration
with higher search costs, myopic expectations, and high discounting in order to fit these data patterns.
(1+ϕ)
Cost of Job Search: We assume that ψ(search) = k0 (search) 1+ϕ + k1 and pick the search cost
parameters in one of two ways. In the standard calibration, we calibrate search costs to generate
a monthly new job-finding rate of 0.28 to match the JPMCI data before March 2020 and a benefit
duration elasticity of 0.5 to match the median estimate from Schmieder and von Wachter (2017). In
the alternative pandemic calibration, we instead calibrate search costs to minimize squared deviations
between the model and data time-series of new job-finding over the course of the pandemic.26
Expectations: We must make an assumption about how long households expect supplements
to last. In the standard calibration, we assume that households have perfect foresight (which, by
construction, is correct ex post) about the length of supplements. In the alternative “myopic expecta-
tions” calibration, households instead expect supplements to continue through the end of their benefit
spell, and they are then surprised when supplements actually end.
Impatience: We also calibrate the discount factor in one of two ways. In the standard calibration,
we assume a normal level of patience and set β = 0.99 monthly (an 11 percent annual discount rate) to
generate a 3-month MPC of 0.25 in response to a $500 stimulus check sent to all households. Kaplan
and Violante (2022) argues that macro models should target a value for this MPC of 0.15-0.25.
Havranek and Sokolova (2020) and Orchard, Ramey, and Wieland (2022) argue that this empirical
range may be overstated. We purposely choose an MPC at the high end of empirical estimates to
be conservative, since even using this high target generates spending responses to UI which are too
small. In the alternative high impatience calibration, we instead pick β = 0.98 (a 22 percent annual
discount rate) to target the 1-month MPC of 0.42 in the waiting for benefit receipt design.
5.1.2 Model Fit Comparisons
Figure 9a shows that the standard model calibration is a poor fit to both job-finding and spending
patterns. This model calibrated to match pre-pandemic job-search behavior predicts that almost no
workers take a new job while the generous supplements are in place, and that job-finding rises sharply
when they expire. But the data shows much more muted patterns. In contrast, the opposite is true
with respect to spending. Even though this model is calibrated to match the upper end of MPC
estimates to $500 stimulus checks, it still implies responses to supplements which are much smaller
than the data. This is especially true when the $600 supplements end: households in this model with
perfect foresight anticipate the end of supplements and thus save to smooth consumption.
Panel 9b shows the effect of progressively introducing each of the three alternatives discussed in
Section 5.1.1. The model in red shows the effect of re-calibrating search costs to target the pandemic
26 We assume constant search costs over the pandemic, so we have 3 parameters and 11 targets for monthly job-finding
(Apr 2020-Feb 2021).
23
Figure 9: Job-Finding and Spending Responses to $600 Supplement: Models vs. Data
(a) Standard Model w/Pre-Pandemic Search Costs
(b) Alternative Models
Notes: This figure shows monthly time-series of various models vs. the data in response to the $600 supplements. The
left panels show the new job-finding rate (based on converting Figure 4 to a monthly frequency) and the right panels
show the spending of unemployed (as a ratio to employed, based on Figure 1). The standard pre-pandemic model
calibrates to pre-pandemic evidence on duration elasticities and MPCs out of stimulus checks. The alternative models
all calibrate search costs to match the level of job-finding in the data and then the three models vary in the expectations
about the renewal of the $600 and in what MPC is targeted.
job-finding series instead of pre-pandemic duration elasticity estimates. Because the level of the job-
finding rate even with no supplements is so much lower than than during normal times, and the change
in the job-finding rate in response to large changes in supplements is so modest, the calibration that
best matches these patterns implies that job search was more costly and less responsive to monetary
incentives during the pandemic. This model is by design a better fit for the job-finding rate than the
pre-pandemic model, but it implies that both the job-finding rate and spending evolve too smoothly:
if households anticipate that the $600 will expire in August, they begin searching more in the months
before that, and they smooth consumption in response to this predictable decline in income.
24
We next change from perfect foresight to myopic expectations, so that households are surprised
by each change in supplements. The orange line shows that this model is capable of generating a
sharp jump in the job-finding rate, and roughly symmetric spending responses to the start and end
of supplements, as in the data.
Nevertheless, spending responses in this model are still too small. Both the increase in spending
while the supplements are in effect and the decrease in spending when they expire in August are about
half that in the data. Notably, households in the data remain highly sensitive even after they have
accumulated significant liquidity. We therefore need some force above and beyond temporarily low
liquidity to explain why the MPC of unemployed households is greater than the MPC of the general
population (as measured by stimulus check MPCs).27
Hence, in the third and final change to the standard pre-pandemic model we increase impatience
of unemployed households relative to the general population to target the reduced form MPC of 0.42
when waiting for benefits. This calibration requires unemployed households to have discount rates
twice as high as those of the general population (22% annually versus 11%). The green line shows
that this “best fit” model which includes all three changes closely matches time-series patterns for
both job-finding and spending.28
Figure A-19 shows that this best-fit model with all three changes is also a good fit to the $300
supplements in January 2021. Furthermore, an additional untargeted job-finding moment is consistent
with the best-fit model. Although we pick search costs in the best fit model to target the time-series
for the average job-finding rate, Figure A-20 shows that this best-fit model also matches the results
from the difference-in-difference research design for job-finding, which provides additional validation
for the linearity assumption in the difference-in-difference design.
Thus, the key elements necessary to jointly fit empirical job-finding and spending patterns are
more costly job search during the pandemic, unemployed households that behave more impatiently
than the general population, and unemployed households who act as if they are surprised by changes
in benefits. Although these three elements are departures from the standard pre-pandemic model,
each seems plausible relative to actual household behavior.
First, job search may have indeed been more costly during the pandemic. For example, face-to-
face interviews were logistically challenging and working conditions were more difficult. This modeling
choice echoes the decline in search efficiency in the model by Mitman and Rabinovich (2021).
Second, the relationship between unemployment risk and impatience that we need to fit the data
is consistent with the correlation between ex-ante unemployment risk and MPCs shown in Patterson
(2023). The fact that a high degree of impatience among the unemployed can help explain their
spending patterns is also consistent with the models of present-bias in Ganong and Noel (2019) and
Gerard and Naritomi (2021).29
27 In Appendix D.5, we provide more quantitative decompositions of the specific forces like targeting and persistence
which shape the MPC out of stimulus checks relative to the MPC out of UI.
28 The model overstates spending of unemployed relative to employed in March and April 2020 because of two mea-
surement issues. First, most unemployed households experience a delay of a few weeks between job loss and the start
of benefits. Second, the $600 weekly supplement is not paid out until halfway through April. Appendix E.1 and Figure
A-18 show that our conclusions are unchanged in a more complicated model that is fit to these high frequency patterns
immediately after job loss.
29 However, as we discuss in Appendix E.2, these models miss the pandemic patterns unless they further introduce
myopic expectations. Specifically, a model with heterogeneity in present-bias and search costs but with correct ex-
pectations implies spending responses which are asymmetric relative to the data (responding much more to the start
than to the end of the $600 supplements) and implies a temporary spike rather than a sustained increase in job finding
when the $600 supplements expire. Nevertheless, after assuming myopic expectations, a model with high exponential
25
Third, the myopic expectations needed to fit the data imply that households respond strongly
today to policy changes today but respond little today to policy changes in the future. There are
three ways to rationalize this pattern: 1) The policy changes may have truly been surprises, even
to those paying attention. 2) Households may pay limited attention to policy news even after it is
announced. 3) Households may pay attention to policy news but nevertheless fail to fully adjust
their behavior due to some behavioral frictions. Without explicit data on expectations, these three
interpretations are observationally equivalent. Although there was substantial policy debate (and
therefore uncertainty) surrounding the expiration of the $600, there was no similar debate around
the expiration of $300 supplements in September 2021. This suggests that information or behavioral
frictions are probably more likely explanations for the consistently large spending responses than are
explanations based on legitimate legislative uncertainty.
5.2 Magnitudes
We now use the model to quantify how supplements affected job-finding and spending during the
pandemic, including accounting for dynamic effects. For job-finding, we estimate a duration elasticity
of 0.07 in response to the $600 supplements and 0.11 in response to the $300 supplements. These
estimates are similar to the ones in Section 4.3 which do not allow for dynamics. This implies that
job-finding dynamics in the model are of limited quantitative importance, a point to which we return
below in Section 5.3.1.
Table 4: Effects of Supplements on Spending
$600 $300
supplement supplement
1-month MPC out of 1st month of supplements 0.29 0.31
3-month MPC out of 1st 3 months of supplements 0.38 0.34
Total MPC through month supplement ends 0.40 0.46
Total MPC through 3 months after supplement ends 0.53 0.60
Using the model we can measure the effect of supplements on spending at different horizons. Table
4 reports spending effects over various horizons in the best fit model. Defining ∆ct and ∆yt as the
difference P
in consumption and income for a household with and without supplements in month t, we
T
∆ct
compute PTt=1 for various values of T . In particular, for each supplement we show results for T
∆yt
t=1
equal to 1 month, 3 months, the length of the supplement period, and the length of the supplement
period plus 3 months. It is these longer horizon MPCs which most directly answer policy questions
about the overall effects of supplements on spending of the unemployed, but these cannot be reliably
measured in the data.
We find one-month MPCs of 0.29 and 0.31 to the $600 and $300 supplements respectively. The
share of all supplements spent in the period while the supplements are still in place is even higher,
with an MPC of 0.40 and 0.46 to the $600 and $300 supplements. By three months after supplement
expiration, MPCs rise to 0.53 and 0.60. As already noted in Section 5.1.2, these MPCs are large
discounting or a model with present-bias in time preference can be equally successful in fitting the spending data.
26
relative to quarterly MPCs out of stimulus checks of 0.15-0.25. We discuss this comparison in more
detail in Appendix D.5.
These MPCs imply that households who received the supplement for all the weeks it was available
increased their spending by several thousand dollars. A worker unemployed from April through July
2020 receives $10,200 in $600 weekly supplements. $4,080 is spent by the end of July and $5,400 is
spent by the end of October.
Drawing on these individual effects (small for job-finding and large for spending), it is natural to
then ask how the supplements affected aggregate fluctuations in employment and spending during the
pandemic. In Figure 10 we use the best fit model scaled by the total number of workers receiving
unemployment benefits in the data to generate a simple partial equilibrium counterfactual for ag-
gregate employment and spending over the course of the pandemic had there been no $300 or $600
supplements.30
Figure 10 shows that although the supplements had some negative effects on employment, these
effects were small relative to overall employment changes during the pandemic. The $600 weekly
supplements from April 2020 to July 2020 reduced employment by an average of 0.6% while the $300
supplements reduced employment by an average of 0.4%. Overall this amounts to only around 5% of
the overall employment gap generated by the pandemic, so these supplements played a small role in
explaining aggregate employment dynamics during this time period.
The effects of supplements on spending were three to five times larger than their effects on employ-
ment. Specifically, the $600 and $300 supplements boosted aggregate spending by an average of 2.7%
and 1.5%, respectively. This means that supplements helped to close a large fraction of the aggregate
spending gap during the pandemic.31 Before they expired at the end of July 2020, the supplements
were responsible for 21% of the spending recovery during the pandemic.
Figure 10: Aggregate Implications
(a) Employment (b) Spending
Notes: This figure shows aggregate employment and spending dynamics implied by the best-fit model. We first estimate
individual effects and then aggregate up these individual effects by scaling by the number of workers receiving benefits
at each date to arrive at a (partial equilibrium) aggregate effect. The left panel compares to total employment from the
BLS Bureau of Labor Statistics (2019 - 2021) establishment survey while the right panel compares to PCE spending
from the Bureau of Economic Analysis (2019 - 2021).
30 Since the payroll survey excludes self-employed workers we reduce the counts of benefit recipients when scaling
employment effects by the number of self-employed PUA UI recipients in DOL data.
31 We emphasize that this is the micro effect of the supplements, aggregated up to the level of the entire economy. It
is possible that general equilibrium channels could further amplify or dampen the aggregate impact of the supplements.
27
5.3 Understanding Mechanisms
Now that we have quantified the effects of supplements on job finding and spending, we use the best
fit model as well as additional empirical work to shed light on three additional questions: First, why
are dynamic job-finding effects limited? Second, why are job-finding effects smaller than most prior
estimates (as shown in Figure 8)? Third, what can we learn about the role of permanent heterogeneity
versus temporary low liquidity for explaining high MPCs?
5.3.1 Limited Job-Finding Dynamics
In the model, the potential for dynamic search effects arises from two sources: anticipatory search
and liquidity accumulation.32 However, both effects end up being quantitatively small.
The fact that there are limited dynamics from anticipatory search follows immediately from the
fact that the model only fits the spending and job-finding time-series if households are surprised by
policy changes. The lack of anticipatory dynamics is thus explained simply by the fact that households
do not adjust behavior in advance of policy changes they do not anticipate.
Another potential concern about dynamics arises from liquidity effects on job search. Prior research
finds that unemployment benefits reduce job search in part by relaxing liquidity constraints (Card,
Chetty, and Weber 2007; Chetty 2008). Figure 1 shows that the supplements were associated with a
large increase in liquidity for the unemployed. If the job-finding rate remains depressed after the $600
supplement expires because of this elevated liquidity, then the research designs in Section 4 will under-
state the full effect of the supplements. We use two complementary approaches to address this concern.
First, we show that this bias is small in the model because liquidity constraints only affect search
when they bind. Liquidity is already elevated by April 2020 when supplements start and then grows
further from there, so the additional liquidity accumulation caused by supplements has little additional
effect on search.33 The model implies that supplements reduce the monthly job finding rate by 3.6%
just prior to expiration (capturing both the effect of incentives and the effect of liquidity) and by only
0.16% after expiration (capturing only the effect of liquidity). Thus, liquidity effects account for only
4% of the total causal effect in this context.
Second, we study empirically how the estimates in Section 4 vary with liquidity. Using a triple-
difference design, Tables A-4 and A-5 show that a one-standard deviation increase in liquidity is
associated with a decline in the disincentive effect of the $600 from -.0163 to -.0135, and with a
decline in the disincentive effect of the $300 from -.020 to -.0186. A simple extrapolation from this
cross-sectional heterogeneity in treatment effects to the time-series of liquidity for the unemployed
during the pandemic implies that liquidity accumulation reduces the disincentive coefficient β̂ by only
5%, from -.017 in April 2020 to -.0164 in July 2020.34 This 5% estimate based on cross-sectional
heterogeneity is in line with the 4% estimate from the structural model.
32 We note that it is possible that other forces not captured by the model such as changing aggregate conditions might
also lead to effects of supplements which vary over time. However, we note that the dynamic event study specification
shown in Figure 6 also suggests that effects in the data are relatively constant over time.
33 The model includes borrowing constraints, and it replicates the finding from the prior literature that liquidity has
important effects on job search. Specifically, it replicates untargeted results from Card, Chetty, and Weber (2007)
that two months of severance pay reduces the subsequent log job-finding hazard by 0.076-0.109. Performing this same
exercise in the model delivers a value of 0.076, so the model yields credible liquidity effects.
34 Mean checking account balances increase $1,388 for unemployed relative to employed households from April to July
2020, and the standard deviation of balances in the regression sample is $4,897. Thus -.0164-(1328/5018)*.0022=-.017.
28
5.3.2 Small Employment Magnitudes
Four forces explain why the unemployment duration elasticity we estimate is lower than estimates in
the prior literature. First, the supplements we study are temporary. Second, the supplements are
implemented in a labor market with a depressed job-finding rate. These two forces are likely to also
be relevant in “normal” (non-pandemic-induced) recessions. Third, the large share of recalls further
dampens the effect of the supplements. Fourth, the per-week behavioral response to the supplements
while they are in effect (the hazard elasticity) is also lower than in prior times. The analysis is sum-
marized in Figure 11, which use five dots—with four transitions from the first dot to the fifth dot—to
quantify the importance of each force.
The most important conclusion from Figure 11 is that there is a mechanical wedge between duration
and hazard elasticities which varies with supplement length. For example, if the hazard elasticity is
one, then permanently doubling benefits will double the average duration of unemployment. Thus,
the duration elasticity will also be one.
In contrast, the shorter the supplement, the more that effects on the total duration of unem-
ployment spells are muted relative to effects on the per-week hazard rate of re-employment. As an
extreme example, suppose that the hazard elasticity were so large that job-finding dropped to zero
when supplements were in place. The effect on unemployment duration would be negligible if the
benefit increase lasted only for a single day.35 The past literature typically studies the effect of rel-
atively long-lived benefit changes where the mechanical wedge is small and there is little distinction
between the hazard and duration elasticities. In our context, this distinction matters.
The left panel of Figure 11 quantifies the extent to which distortions shrink as supplement length
becomes shorter. We choose a job-finding hazard elasticity of 0.5, to match pre-pandemic estimates
from the past literature and the horizontal blue line captures this hazard elasticity.36 The orange
circle captures the response to long-lived benefit changes, and the red line shows the implied duration
elasticity for shorter supplements. A mechanical wedge between the duration elasticity in red and
hazard elasticity in blue emerges since a change in the hazard translates less than one-for-one into a
change in duration if that change is short-lived. The green square at four months corresponds to the
length of the $600 supplement and shows that the short length of the supplement alone can explain
a reduction in the duration elasticity from 0.5 to about 0.4.
Second, the effect of temporary supplements is further diminished in a setting where the base-
line job-finding rate is depressed. Suppose that a large UI supplement cuts the job finding rate in
half. Reducing the job-finding rate from 50% to 25% for one month will lead to larger growth in the
duration of unemployment than will reducing the job-finding rate from 5% to 2.5% for that month.
The yellow line in Figure 11 repeats the same exercise as the red line but with a level of the baseline
job-finding rate chosen to match the depressed job-finding rate during the pandemic (in fall 2020
when no supplements were in place). When the baseline job-finding rate is low, the hazard elasticity
converges more slowly to the duration elasticity and so the wedge is larger for any supplement length.
The blue triangle shows that the duration elasticity in response to a four-month supplement is then
around 0.25, even though the hazard elasticity remains at 0.5. Accounting for these first two forces—
short supplements and a depressed job-finding rate—explains about half of the difference between the
35 We further explore the likely effects of a one-day benefit increase (also known as severance pay) in Section 6.
36 To simplify intuition, we analyze these effects under the assumption of a constant hazard elasticity, both over time
and as a function of supplement length. In models of optimal search, the hazard elasticity itself would decline as the
length of supplements declines, amplifying the conclusion that short supplements lead to lower duration elasticities.
29
Figure 11: Forces for the Low Unemployment Duration Elasticity
Notes: The figure computes the duration elasticity to supplements of different lengths. Within each panel we compute
the duration elasticity under a normal pre-pandemic level of the total job-finding rate as well as for a depressed job-
finding rate. Within a panel we do not change the recall share as we move from the normal to the depressed scenario,
meaning both recall and new job-finding rates decline proportionately. Moving from the left panel to the middle panel,
we raise the recall share from its pre-pandemic to its pandemic value. Moving from the middle panel to the right panel,
we lower the new job hazard elasticity from its pre-pandemic value to its pandemic value. This means that the yellow
line in the right panel corresponds the full set of pandemic forces while the red line in the left panel corresponds to the
full set of normal conditions.
pre-pandemic duration elasticity of 0.5 and the pandemic duration elasticity of 0.07.
In addition to these first two forces—which should remain relevant in “normal” recessions outside
the pandemic—there are additional forces for generating the low duration elasticity that are pandemic-
specific. The third force for a low duration elasticity is the large recall share of total exits during
the pandemic. We assume that recalls are insensitive to changes in benefit levels based on both
institutional constraints as well as empirical evidence in Appendix C.5. If a larger fraction of exits
from unemployment are insensitive to benefit increases, then these increases will generate smaller
employment distortions. The purple cross in the middle panel of Figure 11 shows that the elevated
recall share in the pandemic combined with the depressed pandemic level of job-finding implies a
duration elasticity of 0.18 in response to a four month supplement. Fourth and finally, the job-finding
effects that we estimate in Table 3 imply a lower per-week hazard elasticity than implied by pre-
pandemic estimates.37 The right panel of Figure 11 recomputes the results with this lower hazard
elasticity and shows that this reduced sensitivity of search to benefits during the pandemic lowers
the duration elasticity of a four month supplement from 0.18 (the purple cross) to 0.07 (the black
diamond). This black diamond corresponds to the $600 supplement duration elasticity in our best fit
model and completes the steps moving us from the pre-pandemic yellow dot to our pandemic estimate.
37 In prior drafts, we explored whether any worker-level observable characteristics like age (as a proxy for health risk),
the presence of kids (as a proxy for childcare constraints) or differential recall rates help account for the reduction in
the hazard elasticity but ultimately found no systematic evidence of heterogeneity. Since the small behavioral response
to supplements does not appear to be driven importantly by any of these obvious channels, we think that the most
likely remaining explanation is a shift induced by the pandemic’s effect on working conditions, including exposure to
health risk (which may be only imperfectly proxied by age), discomfort from masking, and more challenging customer
interactions.
30
5.3.3 High MPCs: Permanent Heterogeneity vs. Transitory Low Liquidity
Our spending results have implications for consumption modeling. Many papers document an empiri-
cal correlation between MPCs and low liquidity, and a large literature has developed models in which
liquidity constraints play a key role in generating high MPCs. For example, the leading two-asset
precautionary savings models are able to simultaneously match the distribution of wealth and the
high MPC out of stimulus checks in the data, because many households have high wealth but little
liquidity (see Kaplan and Violante 2022 for a review of this literature). However, it is hard to know
whether temporary low liquidity is the primary cause of high MPCs, as these models typically assume,
or if some households with permanently high propensities to spend will save less and therefore have
low liquidity.
Differentiating “temporary low liquidity causes high MPCs” from “permanently high MPCs cause
low liquidity” is challenging because both liquidity and MPCs are endogenous. The large pandemic
UI transfers generate a unique, quasi-random increase in liquidity. The spending responses that
we observe in this environment imply that permanent heterogeneity—and not just temporary low
liquidity—is important for explaining high MPCs. Three empirical results lead to this conclusion.
First, we find large MPCs to UI supplements throughout the pandemic, even though unemployed
households have much higher than normal liquidity during this time. The median household who
becomes unemployed during the pandemic moves up an entire tercile of the pre-pandemic liquidity
distribution (from the 35th percentile to the 65th percentile). Indeed, the fact that the replacement
rate with supplements is above 100% means that the typical unemployed household has temporarily
high rather than temporarily low liquidity during the pandemic. The fact that MPCs remain large even
in this high liquidity environment suggests that the people who became unemployed in the pandemic
have high MPCs for some reason above and beyond low liquidity. Indeed, the precise reason that the
best-fit model requires unemployed households to be more impatient than the general population is to
hit the fact that the MPC remains high even when supplements push households into this temporarily
high liquidity state.
Second, as discussed in Section 3.3, liquidity measured years before the pandemic predicts higher
MPCs to UI supplements throughout the pandemic. In a model where temporary bad luck is the
source of low liquidity and high MPCs, one’s liquidity position years in the past should have little
impact on future MPCs. This is especially true if some specific “good luck” occurs in between.
As an extreme example, consider a lottery winner. Whether they were short on cash before winning
the lottery should have no impact on their post-lottery-winning MPC. This same logic applies when
all households experience a policy-driven liquidity increase, as is the case at the start of the pandemic.
The fact that low past liquidity predicts high future MPCs, even after large UI transfers erase this
low liquidity state, implies that this pattern must reflect some permanent household characteristic
and not just temporary low liquidity.
To illustrate this more concretely, we return to the best-fit model. First, to evaluate the view that
“temporary low liquidity causes high MPCs”, we split households into two groups and exogenously
vary liquidity across the two groups in March 2020 to match the variation in pre-pandemic liquidity
underlying Figure 3. Figure 12 shows that the model predicts very similar spending behavior for both
groups. This is because even though this model (by construction) matches the substantial empirical
heterogeneity in pre-pandemic liquidity, once households begin receiving $600 supplements, they are
no longer liquidity constrained. At that point, no further source of heterogeneity remains in this
31
model to drive heterogeneous spending effects.
Figure 12: Spending Responses by Liquidity: Data vs. Alternative Models
Notes: This figure compares spending by liquidity in two alternative models and in the data. Each line shows the
spending of unemployed relative to the spending of employed households for a particular liquidity group. The model
with no permanent heterogeneity splits unemployed households in the best-fit model into two groups and exogenously
varies the liquidity state to match the variation across groups in pre-pandemic liquidity in the data. The model with
permanent heterogeneity varies the discount factor across groups to match this same variation. See text for details. In
the right panel, the yellow data line is the ratio of the two lines in Figure 3 panel (a) while the purple line is the ratio
of the two lines in Figure 3 panel (b). The average of the yellow and purple lines is not equal to the spending response
in Figure 9b because here we match treatment and control groups on liquidity.
Second, to evaluate the “permanently high MPCs cause low liquidity” view, we again divide
unemployed households into two groups and this time vary the discount factor across the two groups
to match the same variation across groups in pre-pandemic liquidity. Both versions of the model
thus match the heterogeneity in liquidity in the data, but the model with permanent heterogeneity
does so by varying discount factors across groups while the model with no permanent heterogeneity
does so by varying only households’ liquidity state variable. Figure 12 shows that the model with
permanent heterogeneity in discount factors implies substantial heterogeneity in spending responses
by pre-pandemic liquidity, in line with the data.38
Finally, the “permanently high MPCs cause low liquidity” view is supported by a third dimension
of the data on pre-pandemic liquid assets. Specifically, we split the sample into two groups: workers
who become unemployed during the pandemic and those who do not. We then measure liquidity prior
to the pandemic, when both groups are still employed. Even when employed pre-pandemic, households
who later become unemployed have about 25% less liquidity conditional on income than households
who remain employed, suggesting those households have a lower propensity to save. Thus, finding
low liquidity for households who will become unemployed directly connects the first piece of evidence
in this section which compares across groups (high MPCs of unemployed relative to employed) to the
second piece of evidence which compares within-group (among those who become unemployed).
38 Note that liquidity still also matters for MPCs in the model. With no discount factor heterogeneity and in a normal
environment (no supplements and no pandemic-induced liquidity increases), the MPC of unemployed households is 0.3
larger than that of employed households, reflecting the role of current income and liquidity. Adding discount factor
heterogeneity raises the gap to 0.44, implying that two-thirds of the MPC variation with unemployment status in the
best-fit model is explained by current economic circumstances, while one-third is due to permanent characteristics.
32
Together, this evidence strongly points to permanent heterogeneity: some households have high
propensities to spend. These spenders are going to spend when they have money, and so they will
generally also have low liquidity. In this sense, low liquidity is a symptom of persistent propensities
to spend and not just a transitory state.
Our result that permanent heterogeneity is important for explaining spending patterns comple-
ments recent research arriving at similar conclusions using a different source of variation and method-
ology. Athreya, Mustre-del Río, and Sánchez (2019), Gelman (2021), Calvet et al. (2022) and Aguiar,
Bils, and Boar (2020) document empirical patterns in household panel data, which they show require
permanent heterogeneity when viewed through the lens of structural household consumption mod-
els. Parker (2017) uses Nielsen data to show that high MPCs are correlated with survey measures
of impatience and lack of financial planning as well as income from years in the past. These studies
use observational data in normal economic environments, so they do not have exogenous variation
in liquidity and must therefore rely on more structure to infer causality. In contrast, we study an
environment with a large quasi-random increase in liquidity as an identifying source of variation.
6 Policy Implication
The mechanisms driving the small employment effects and large spending effects of UI supplements
have a policy implication that is likely to extend beyond the pandemic. Specifically, short-lived
“severance-like” UI supplements that trigger on during recessions could provide boosts to aggregate
demand without much distortion to job finding.
6.1 A New Countercyclical Motive for Temporary Supplements
In the classic Baily-Chetty formula, it is optimal to provide greater insurance when resulting em-
ployment distortions are smaller. We show that short-lived benefit increases during recessions are
likely to induce small employment distortions. If workers are only eligible for increased benefits for a
small part of their spell, this will have a small effect on job search decisions. Indeed, pure severance
payments that pay out only at the start of an unemployment spell should not distort job search de-
cisions.39 Furthermore, the job-finding rate typically declines during recessions. Even if the hazard
elasticity is constant, the fact that job-finding rates typically fall during recessions provides a ratio-
nale for temporary countercyclical benefits. When the no-supplement job-finding rate falls, the wedge
between duration and hazard elasticities grows (as shown in Figure 11). This means that the duration
elasticity—which is the welfare-relevant cost of expanding benefits—is lower for any given level of the
hazard elasticity, and this pushes up optimal benefit levels.
This conclusion is complementary to two prior strands of work on optimal benefit levels over the
business cycle. First, the hazard elasticity may be lower in recessions.40 Second, Schmieder, von
Wachter, and Bender (2012) show that even if the behavioral response to more generous benefits (in
the form of longer Potential Benefit Duration) is constant over the business cycle, the welfare-relevant
distortion is smaller. This is because PBD extensions mechanically affect more workers when the
39 If households are liquidity constrained, then severance payments may also reduce inefficiency (Chetty 2008).
40 Kroft and Notowidigdo (2016) evaluate this channel by studying how the hazard elasticity changes with the unem-
ployment rate (they then make the common assumption that this hazard elasticity is the same as the duration elasticity).
They find that the hazard elasticity falls modestly as the unemployment rate rises, suggesting that UI benefits should
be slightly more generous during recessions. See also Landais, Michaillat, and Saez (2018b).
33
job-finding rate is depressed. Although we study a different temporary benefit policy (supplements),
we similarly find a smaller distortion in recessions for the same underlying economic reason: the ratio
of the behavioral cost (which is constant) to the mechanical cost (which rises as more households
benefit from the expansion) is lower.
6.2 Aggregate Demand Management via Targeted Payments
For spending, targeted one-time stimulus to unemployed households (“severance”) can boost aggregate
demand more cost effectively than universal one-time payments to all households (“stimulus checks”).
To explore the effects of severance payments, we analyze the effects of one-month supplements. We
do this in a model environment that removes any pandemic-specific effects in order to more closely
approximate a typical recession. Since employment effects from severance are minimal, we focus on
the spending impacts. We focus on how the spending impacts of severance (which is targeted to the
unemployed) compares to the spending impacts of alternative universal stimulus payments (which go
to the population as a whole), as a way to evaluate their potential as tools for aggregate demand
management. This analysis is shown in Figure 13. The solid lines compare the average quarterly
MPC out of a severance to the MPC out of an equal-sized stimulus check, for an individual receiving
each transfer. The dashed line shows the marginal effect of the last $50 of severance.
Figure 13: Spending Impacts of Severance vs. Untargeted Stimulus
Notes: This figure shows the quarterly spending responses to severance as well as to one-time stimulus checks of
various sizes in a non-pandemic environment with normal liquidity levels. The x-axis compares severance payments
and untargeted stimulus of equal size and the y-axis reports the quarterly MPC. We compute these responses in the
best-fit model with discount factor heterogeneity. We calibrate the degree of heterogeneity in this model so that it still
produces a quarterly MPC out of $500 stimulus checks of 0.25. Solid lines show MPCs out of the entire transfer while
the dashed line shows MPCs out of the last $50 of UI.
We find that the spending impact of severance is larger than the impact of universal stimulus checks,
although this difference declines with the size of the transfer. The impact of severance is larger than
that of universal stimulus checks because severance targets individuals with a high propensity to spend
34
while universal stimulus checks do not. The difference is largest for small transfers, because when
transfers are small the unemployed are temporarily liquidity constrained and have a high propensity
to spend for any level of liquidity due to the permanent heterogeneity discussed in Section 5.3.3.
For large transfers, unemployed households are no longer liquidity constrained and only the effect of
targeting those with permanently high propensities to spend remains.
The combination of low pre-transfer liquidity and high persistent propensity to spend at any
liquidity means that even large severance payments targeted specifically to the unemployed may be
beneficial relative to untargeted stimulus. Figure 13 shows that the spending impact from the last
dollar of a $2,000 one-time payment to the unemployed is larger than the spending impact of the first
dollar of untargeted stimulus.
The conclusion that severance pay is an attractive way to stimulate aggregate demand builds on two
prior strands of the literature on unemployment benefits. First, it expands on Gerard and Naritomi
(2021), which shows that unemployed households have a high propensity to spend severance payments.
Second, severance payments can be interpreted as a means of front-loading UI benefits, and in this
sense our results relate to several other papers which argue for front-loading (Shavell and Weiss 1979;
Hopenhayn and Nicolini 1997; Mitman and Rabinovich 2021). Lindner and Reizer (2020) provides
empirical evidence showing front-loading benefits led to shorter durations. Our analysis of severance
adds a novel motive for front-loading, which is that it is an effective way to stimulate aggregate demand.
The analysis in this section is relatively simple, but it demonstrates the potential power of tem-
porary UI supplements that are triggered by recessions. This is potentially a much cheaper way of
providing fiscal stimulus than unconditional stimulus checks. However, there are two caveats worth
emphasizing. First, severance pay is not targeted to the long-term unemployed who are most in need
of insurance. A full analysis of optimal policy would incorporate both the aggregate demand motive
we study and the insurance motive studied in much of the prior literature. Second, the larger the
“severance-like” payment, the larger incentive there might be for employees and employers to collude,
generating false terminations to claim this benefit. Such a policy would therefore need to be carefully
designed to mitigate this risk.
7 Conclusion
We use administrative bank account data to estimate the causal effects of the largest UI expansion
in U.S. history. Our reduced-form research designs and dynamic structural model deliver consistent
conclusions: expanded benefits had large effects on spending but small effects on job finding. The small
job-finding effects were driven in part by the fact that supplements were temporary and implemented
in an environment with an already depressed job-finding rate. The large spending effects were driven
in part by the fact that they were targeted towards households with high spending propensities. These
conclusions have lessons for future policy design: countercyclical severance-like payments should be
considered alongside stimulus checks as an additional instrument for fiscal stimulus.
These conclusions also suggest some avenues for future research. First, it would be useful to
understand what the behavioral characteristic is that gives rise to differences in consumption behavior
(and is correlated with unemployment risk). This is important for determining whether other forms
of targeted stimulus might achieve the same ends without working through the UI system. Second,
it would be interesting to understand why households had myopic expectations about changes in UI
35
supplements. If households exhibit myopic expectations with respect to other policy changes, this
likely alters trade-offs between current and future actions and has important consequences for the
design of dynamic policies.
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38
Online Appendix to “Spending and Job-Finding
Impacts of Expanded Unemployment Benefits:
Evidence from Administrative Micro Data”
Peter Ganong, Fiona Greig, Pascal Noel, Daniel M. Sullivan, Joseph Vavra
Contents
A Additional Institutional Detail and Data Description 1
A.1 Simultaneous Policy Changes in the Summer of 2021 . . . . . . . . . . . . . . . . . . . 1
A.2 States Included . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1
A.3 Unemployment and Employment Spells . . . . . . . . . . . . . . . . . . . . . . . . . . 2
A.4 Sample Restrictions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 3
A.5 Additional Variable Detail . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 3
B Appendix to Section 3 (Spending Responses) 5
B.1 Summer MPCs . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 5
B.2 MPCs by Pre-pandemic Liquidity: Additional Details . . . . . . . . . . . . . . . . . . 5
B.3 MPC Robustness . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 6
C Appendix to Section 4 (Job-Finding Responses) 9
C.1 Measuring Weekly Benefit Amount . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 9
C.2 Identification in the Difference-in-Difference Research Design . . . . . . . . . . . . . . 9
C.3 Comparison of Estimates Across Research Designs and Episodes . . . . . . . . . . . . 10
C.4 Calculating Duration Elasticities . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 11
C.5 Additional Job-Finding Results and Robustness . . . . . . . . . . . . . . . . . . . . . . 12
D Additional Model Details and Results 16
D.1 Model Setup . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 16
D.2 Model Parameters . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 18
D.3 Model Solution . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 19
D.4 Best Fit Model - Additional Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . 20
D.5 Understanding High MPCs out of UI vs. Stimulus . . . . . . . . . . . . . . . . . . . . 20
E Alternative Models 22
E.1 Time-Aggregation Issues . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 22
E.2 Alternative Behavioral Models without Myopic Expectations . . . . . . . . . . . . . . 23
Additional Figures and Tables 25
A Additional Institutional Detail and Data Description
A.1 Simultaneous Policy Changes in the Summer of 2021
Nearly every state terminated expanded benefit eligiblity (PEUC) at the same time that they termi-
nated the $300 weekly benefit supplement in the summer of 2021.41 The presence of two simultaneous
policy changes is a conceptual challenge for trying to estimate the separate effect of the $300 supple-
ment. Unemployed workers who are still eligible for regular benefits will see a decline in benefits of
$300 per week (call this treatment 1) while those who were only eligible under PEUC will lose their
benefits entirely, and hence will see a decline in benefits of $300 + regular benefits (call this treatment
2).
We can partially separate households subject to treatment 1 from those subject to treatment 2 by
focusing on either households with short observed unemployment duration or on households where we
see benefits continuing after PEUC expires. However, using this approach to analyze of the expiration
of the $300 supplement has two limitations relative to the analysis of earlier supplement changes.
First, while all UI recipients maintained eligibility around earlier supplement changes, in the summer
of 2021 only 30% of recipients maintained eligibility because of the simultaneous expiration of PEUC
(treatment 2). This means that the sample size of workers who continue to receive benefits after these
changes is smaller than in prior time periods. Second, and related, those recipients that do remain
are not randomly selected. They are specifically those with low UI durations who have not yet rolled
onto PEUC.
A.2 States Included
We divide states into three groups:
1. Fully included (15 states)
2. Partially included (29 states + DC)
3. Not in sample (6 states)
44 states plus DC are included in the benchmarking analysis in Section 2.2.1 and in the spending
analysis in Section 3. Six states are excluded because we are unable to identify a transaction string
that is unique to UI payments. In some states we are able to identify a transaction string that appears
to include both UI payments but they are mixed with other transfer programs. The one exception to
this is that we include California, which appears to use the same transaction string for UI, Disability
Insurance, and Paid Family Leave. However, in public data, only 7% of California recipients of
payments from the Employment Development Department in 2020 are receiving disability insurance
(DI) or paid family leave (PFL). In addition, we drop anyone with benefits greater than the maximum
weekly benefit for UI, which drops a large share of the DI and PFL recipients.
Relative to the 44 state sample, additional data cleaning is needed for the job-finding analysis in
Section 4 because we need to know the state’s withholding rate for income taxes (discussed below)
41 Congress also set up a second program (PUA) for workers ineligible for regular UI. Most states also terminated
PUA at the same time that they terminated PEUC. In most states we are not able to separate regular UI from PUA
in the JPMCI data. Based on data from a few states for which we can separate PUA payments, PUA recipients are
a very small share of the main analysis sample in our paper. We believe that PUA is a smaller share of our analysis
sample because our filters require consistent labor market attachment in 2018 and 2019.
1
and we drop workers receiving more than the state’s weekly maximum benefit and less than the state’s
weekly minimum benefit. We attempted to clean data for the 16 largest states by number of UI pay-
ments, which collectively account for 97% of the UI payments in the bank data. We succeeded for all
of the states except Florida, which accounts for 6% of the UI payments, and Colorado, which accounts
for 2% of the UI payments. Florida has a high rate of false exits because of PUC overpayments in May
2020 (enough to distort the aggregate time-series for job-finding) and Colorado has an anomalously
high exit rate at the start of December 2020. The set of states that are included in the job-finding
analysis therefore accounts for 89% of the total UI payments in the bank data.
Finally, we make two further restrictions for some parts of the job-finding analysis. In the
difference-in-difference expiration analysis in Section 4.2, we exclude states for which we are un-
able to separate LWA from regular payments (LWA payments make it impossible to measure the true
date of exit): Texas, Connecticut, Louisiana, and Wisconsin. The remaining sample is CA, GA, IL,
IN, MI, NJ, NY, OH, OR, and WA. In the difference-in-difference onset analysis, we exclude Oregon
and Michigan. Oregon has an anomalously high exit rate for December 2020. Michigan sees a very
high share of its low-benefit workers exit UI receipt because of the PUA/PEUC cliff. Unfortunately,
the data cleaning procedure we use for other states to handle the cliff (described in the note to Figure
4) is not effective in Michigan because there still is a sharp increase in measured exits even after data
cleaning. The remaining sample is CA, CT, GA, IL, IN, LA, NJ, NY, OH, TX, WA, and WI. Finally,
for analysis which requires a consistent job-finding rate throughout the entire sample period (e.g.,
Figure 4 and Section 4.1) we use the nine states (CA, IL, IN, NJ, NY, OH, OR, and WA) that are
present in both the expiration analysis and the onset analysis.
A.3 Unemployment and Employment Spells
We measure unemployment insurance spells (henceforth “unemployment spells”) using the payment
of unemployment benefits. An unemployment spell starts with a worker’s first benefit payment in the
sample frame, which is January 2019. In most states, a spell ends when a worker has three consecutive
weeks with no benefit receipt. In states which pay benefits every other week, we instead define a spell
end as four consecutive weeks without benefit receipt.
We measure employment outcomes using receipt of labor income paid by direct deposit. An
employment spell begins with a worker’s first paycheck from an employer. We identify employers
using a version of the transaction description associated with a payroll direct deposit which is purged
of personal identifying information (see Ganong et al. 2020 for additional details). An employment
spell ends (henceforth a “separation”) if a worker has five consecutive weeks with no paycheck from
that employer. We define a separation as being associated with an unemployment spell if a worker has
a separation between eight weeks before and two weeks after the start of an unemployment spell. This
eight week lag allows for time for UI claims to be filed, processed, and paid, while the two week lead
accounts for the fact that last paychecks can be paid after the date of last employment. 55 percent of
benefit recipients have a detected separation at the time of benefit receipt.
We do not detect separations for every benefit recipient for two reasons. First, the JPMCI data do
not include labor income paid via paper check or direct deposit labor income without a transaction
description that mentions payroll or labor income. Second, in some cases more than eight weeks elapse
between the last paycheck and first benefit payment; this scenario can arise if a state UI agency is
slow to process a worker’s benefit claim or if a worker does not file for benefits immediately after
2
separation.
We combine information on unemployment and employment spells to separate UI exits to a new
job from UI exits to recall, which is when an unemployed worker returns to their prior employer. We
are able to observe recalls only for unemployed workers for whom we also observe a job separation.
We define a worker as having been recalled when they begin an employment spell with their prior
employer between five weeks before and five weeks after the end of a benefit spell. We choose these
thresholds based on the timing of job starts relative to the end of unemployment spells. The data on
unemployment spells and employment spells jointly offer something comparable to the administrative
datasets used to study unemployment in European countries (DellaVigna et al. 2017; Kolsrud et al.
2018; Schmieder, von Wachter, and Bender 2012).
A.4 Sample Restrictions
Households in our analysis sample must meet two account activity screens: 1) at least five transactions
per month and 2) annual pre-pandemic labor income of at least $12,000. We impose these screens to
focus on workers whose primary bank account is at Chase. For households that get benefits in 2020
(but not in 2019), we impose the transaction screen from Jan 2018-Mar 2020, and the labor income
screen in 2018 and again in 2019. For households that get benefits in 2019, we impose the transaction
screen for Jan 2018-Mar 2020 and the labor income screen in 2018. Among households that meet
the activity screens, 11.6 percent receive unemployment benefits at some point during the pandemic.
This is lower than the rate for the U.S. as a whole, primarily because JPMCI only captures benefits
paid by direct deposit. The Census Household Pulse Survey shows that 31 percent of households with
at least one working-age person received UI benefits between March 13, 2020 and the end of October
2020. Finally, we limit the sample to customers who are present in the sample from January 2020
through March 2021 with positive inflows, positive outflows, and non-null account balance in every
month.
The narrowest sample we use is a sample of customers who meet the account activity screens
described in the prior paragraph and receive benefits from one of nine states (CA, IL, IN, MI, NJ,
NY, OH, OR, and WA). Figure A-21 shows that aggregate unemployment surges at the start of the
pandemic and then declines as the economy recovers. We also analyze data on a random sample of
187,000 employed workers who meet the transaction and labor income screens for 2018 and 2019, do
not ever receive UI benefits in 2019 and 2020, and do not have a job separation in 2020.
A.5 Additional Variable Detail
We measure age as the age of the primary account holder (the first name listed on the bank account)
at the start of an unemployment spell.
The 2020 stimulus checks authorized by the CARES Act had maximum amounts of $1200 per
single adult (and $2400 per married filing jointly) and $500 per child. For the subset of people who
receive stimulus by direct deposit, we can infer the number of children in the household from the
stimulus amount. If a household receives multiple stimulus checks, we use the value of the first. If a
household does not receive a payment by direct deposit, but deposits a paper check whose sum is a
multiple of $1200 (or $2400) and a multiple of $500, we infer the number of children from that.
JPMCI has hand-categorized firms into 20 industry groups based on NAICS codes for approxi-
3
mately 2,000 employers associated with the most bank accounts. Some households have multiple labor
income streams in their bank account. We assign households to industries using the firm that paid
them the most in the three months prior to UI receipt. Industry is available for about one-quarter of
UI spells.
To limit the influence of high income, high spending, and high asset households on means and
MPC estimates, income, spending, and balances are winsorized at the 90th percentile.
4
B Appendix to Section 3 (Spending Responses)
B.1 Summer MPCs
In this section we discuss the estimation of MPCs to the expiration of $300 supplements in the summer
of 2021. We focus on households that receive UI benefits for the entire month after supplements end
so that we can estimate an MPC. However, we note that since the PEUC extended benefit program
expired at the same time as $300 supplements, this restriction means we measure MPCs only for
a selected subset of short-duration unemployed. We must focus on this subset of households with
continuing benefits because for households without continuing benefits, we cannot distinguish benefit
exhaustion from job finding. This in turn means that we cannot estimate an MPC for these households
since we do not know whether they face a benefit change of $300 or of $300 + regular benefits.
We analyze the expiration of $300 supplements in September for many states but also analyze the
expiration of $300 at the end of June for states which ended supplements early. We follow the same
empirical strategy discussed in Section 3.2. For the September states, our IV approach compares
unemployed to employed households, with P ost equal to one in October and zero in August 2021.
For the early states, P ost equals one in August and zero in June 2021. For the MPCs based on early
expiration of benefits, the treatment group is always the unemployed in those early states, while we
consider two different control groups. One compares to employed households in the same early states
while the other compares unemployed households in early states to unemployed households in states
which kept supplements until September. Figures A-11 and A-10 show that just like for the end of
$600 and start of $300 supplements, there is a sharp change in weekly spending in the exact week
when $300 supplement expire. Table 1 shows we also find similar MPCs.
The MPCs that we estimate when using employed workers as a control group are very similar
to the MPCs we estimate when using unemployed workers in other states as a control group. This
is useful because all of the other policy changes except for the summer 2021 expirations apply to
all unemployed workers at the same time, and so we must rely on employed workers as the control.
The similarity of these results in the one episode where we can use both control groups suggests that
employed workers are indeed a valid control group more generally.
B.2 MPCs by Pre-pandemic Liquidity: Additional Details
This section provides additional detail on the MPC heterogeneity calculations in Section 3.3.
Since we measure checking account balances once per month, we define the liquidity buffer for
household i in month t as (checking balancei,t − 0.5 spendi,t )/(spendi,t ). Dividing by spendi,t ac-
counts for differences across households in permanent income (as proxied by the level of spending).
Subtracting 0.5 spendi,t from the numerator accounts for the fact that funds in the checking account
are both a financial reserve and used to cover monthly transaction costs. Simpler definitions of the
liquidity buffer generate similar results. See Kaplan, Violante, and Weidner (2014) for more discussion.
For both Figure 3 and Table 2, we define the employed control groups by matching on income
quintile and stimulus check timing (as in our other MPC results) and also by (above or below-median)
liquidity. We then re-weight the above-median and below-median liquidity unemployed to have the
same income and stimulus check timing as the average unemployed household in the data. We do this
so that our analysis captures the differences across the two liquidity groups in liquidity and is not
5
driven by confounding differences in income or stimulus check timing.
B.3 MPC Robustness
This section describes a number of robustness checks for the MPC estimates in Section 3.2.
First, we decompose our MPCs into separate categories. This is useful for understanding how
benefit expansions affected households’ lives, for gauging whether MPCs might be driven by pandemic-
specific forces which might not generalize to other recessions, and for assessing whether spending
responses to UI might differ from more general spending patterns. Table A-6 reports the MPCs on
the subset of spending transactions we can assign to granular categories based on merchant category
codes (for card transactions) and text descriptions (for electronic transactions). The category with
the largest response was groceries, accounting for around 20% of the increase in categorized spending
in each episode.
In general, the MPCs do not appear to be driven by any unusual spending patterns. In particular,
this table shows that the share of the MPC explained by each category is similar to these households’
spending shares across categories in 2019, prior to the pandemic.42 That is, marginal spending
responses by category are similar to average spending levels across categories. While there are some
shifts in spending relative to pre-pandemic patterns, these mirror aggregate trends and return to more
normal patterns later in the pandemic. For example, unemployed households in April 2020 have an
elevated share of spending on home improvement, but this is not surprising since overall spending on
home improvement went up early in the pandemic. By 2021, spending patterns out of UI are close to
pre-pandemic spending patterns.
While our analysis focuses on spending responses to UI, it is also interesting to look at effects on
debt. Table A-7 shows that the marginal propensity to repay auto, mortgage, and student loan debt
is very small. This may be a consequence of various debt moratoria during the pandemic reducing
incentives to pay down debt. The fact that debt paydown is slightly larger for car payments than
for mortgage loans and student loan debt is consistent with this explanation. We note that there
is a separate literature that often finds sizable marginal propensities to repay debt in response to
stimulus checks. It would not be particularly surprising if unemployed households valued liquidity
more than employed households and so were less likely to pay down debt than the population as a
whole. Furthermore, we note that we cannot distinguish revolving credit card payments (i.e. debt
paydown) from non-revolving credit card payments (i.e. spending paid off within the month) so we
do not include credit card bill payments in this table. It is possible that households used some of the
UI benefit supplements to pay off revolving credit card debt, which are unable to measure.
Second, we explore the robustness of our results to controlling for more observable differences
between the unemployed and employed since any deviations between these groups not driven by
supplements would contaminate our MPC estimates. All of our MPC results control for the pre-
separation income of the unemployed as well as for the timing of stimulus checks because we view
these as the most salient identification threats. Table A-8 shows the results of controlling for additional
observable characteristics that potentially differ between unemployed and employed. This table re-
computes MPCs progressively adding controls for location, for age, and for the presence of children,
which we think of as capturing other potential differences that might affect spending patterns during
42 Since each MPC design comes from a different month in 2020/2021, we compare to spending levels in the same
months in 2019 to eliminate potential seasonality.
6
this time period. Location captures differential pandemic threats as well as government restrictions
on spending, age proxies for differential health risk of spending, and the presence of children proxies
for school-closure related constraints. Putting in all of these controls makes essentially no difference
for point estimates (generally they are within .01 of the original estimates), but slightly decreases
precision.
Third, spending patterns are nearly identical for unemployed households who are recalled and
those are who are not, suggesting that spending responses are not driven by the unusually high recall
rates during the pandemic. For example, Figure A-22 selects all households who are continuously
unemployed from April 2020 through August 2020 and exit unemployment in September 2020 (the
first month after $600 supplements expire) and then further splits these households into those who
return to their old employers (“Exit to recall”) and those who do not (“Exit to new job”). This figure
shows that spending patterns over this entire period are nearly identical for both groups, suggesting
that different patterns of recall are not driving spending patterns.43 We obtain similar conclusions if
we repeat these comparisons of recalled and non-recalled households exiting in each month from June
2020 through November 2020.
Fourth, our results are also robust to limiting the sample to households for whom we are likely
to observe a more complete lens on spending. For example, many Chase customers have non-Chase
credit cards. We will understate MPCs if these households increase spending on non-Chase credit
cards when receiving supplements. Table A-9 shows that when we limit the sample to households
with no ACH payments made towards non-Chase credit cards, MPCs are two to five cents higher.
This suggests that the presence of non-Chase credit cards leads us to slightly understate MPCs in
our baseline sample. As further evidence of this point, we have computed the response of non-chase
credit card debt payments to supplements and find an increase in payments of 0.04. As noted when
we discussed debt payments, we cannot separate these marginal payments between revolving and
non-revolving credit. However, it is likely that at least some of this increase in debt payments is a
result of increased spending rather than increased pay down of revolving credit on non-Chase credit
cards.
As a second example of a potential bias arising from having an incomplete lens on spending, Chase
customers may make some debt payments using paper checks, which our methodology will misattribute
as spending (because we do not observe the content of account outflows where the payment method is
paper check). This might lead us to overstate the MPC. Table A-9 therefore reports a robustness check
which limits the sample to households which use their account for debt payments via ACH—thereby
mitigating the concern that paper checks are mistakenly including some debt payments as spending—
and finds that MPCs are indeed slightly (zero to four cents) lower than the baseline estimates but
still large.
In addition, although our baseline MPC estimate follows much of the prior literature by looking
at means, Table A-9 shows that estimates using the median change in spending and income results in
MPCs that are two to seven cents higher.
Fifth, our conclusions are robust to alternative spending measures. For example, using the narrow
card and cash measure of spending which is less subject to concerns about misclassification still delivers
large spending responses. Table A-10 shows that MPCs out of this more narrow spending measure
43 Since we do not know how recall expectations evolve, we show the entire time-series and not just the MPC in August
to demonstrate that spending evolves identically over the whole period.
7
are mechanically slightly smaller but the elasticity of this narrow spending measure to benefits is
actually larger. For example, Table A-1 shows that the narrow measure drops 40% of spending, but
the MPC is reduced across the three research designs by only 24 to 33%. This implies that the
responses observed in card and cash spending are proportionally larger than the responses in total
spending and so when expressed as elasticities, the response of this subset of spending is larger than
the response of total spending. This suggests that the large spending responses that we find are not
driven by misclassification.
Sixth and finally, the MPC estimates in this paper define the denominator as household income
(more specifically: total inflows to Chase deposit accounts, excluding transfers). However, one could
also define the denominator as the change in UI benefits alone, excluding all the other components
of income. Relative to Table 1, using UI benefits as the denominator leads to a smaller MPC in four
cases and a larger MPC in two cases. We prefer the MPC estimates which use supplement changes
as instruments for the change in total income because they implicitly adjust for differential shocks to
income between the treatment and control group.
8
C Appendix to Section 4 (Job-Finding Responses)
C.1 Measuring Weekly Benefit Amount
Some individuals have UI inflow amounts that vary from week to week, for example, due to backpay.
We require a single weekly benefit amount to calculate a percentage change in benefits from a sup-
plement. We estimate the benefit amount bi,pre as the median benefit paid to an individual in the
two-month period before the $600 supplement expiration or the two-month period before the $300
supplement onset. We then drop the first payment and the final payment and compute a median for
the remaining weeks. Some states (CA, FL, MI, CO, TX, and IL) pay benefits once every two weeks
and so we divide the median payment by two to capture the amount paid per week.
We measure state UI minimum and maximum benefits using the January 2020 “Most Recent Sig-
nificant Provisions of State UI Laws” publication from the Department of Labor. If a state pays a de-
pendent allowance we use the maximum benefit with dependents and the minimum benefit without de-
pendents. We measure each state’s rate of income tax withholding using Whittaker and Isaacs (2022).
For the difference-in-difference analysis, we estimate workers’ regular weekly benefit amounts in
the absence of any supplements. For the $300 supplement reinstatement, we estimate workers’ regular
weekly benefit amount as wbai = bi,pre /(1 − withholding). For the $600 supplement expiration, we
b −(1−withholding)600
estimate workers’ regular weekly benefit amount as wbai = i,pre 1−withholding . California and
bi,pre −600
New Jersey did not withhold from the supplement so we instead use wbai = 1−withholding .
We limit the sample to workers with plausible regular weekly benefit amounts wbai . Define each
state’s minimum weekly benefit as bmin and maximum as bmax . We keep workers with wbai ∈
[(1 − withholding)bmin , bmax ]. These restrictions will remove customers who have a median payment
that includes substantial backpay.
Calculating wbai requires knowing whether a worker decided to withhold, but we generally do
not observe withholding at the worker level. Because more than 50% of UI recipients withhold
in every state in our sample, our default assumption is that workers are withholding at the rates
reported in Whittaker and Isaacs (2022). However, if a worker has wbai > (1 − withholding)bmax
then the withholding assumption implies that they are receiving an invalid weekly benefit amount.
Thus, for workers with wbai ∈ ((1 − withholding)bmax , bmax ], we recalculate wbai assuming that
withholding = 0.
Recall that our object of interest is the change in benefits from the expiration or onset of a
supplement, which we construct in equation (3). For the $300 supplement reinstatement, we estimate
2×300
equation (3) as P ctChangei = 2wba i +300
. For the $600 supplement expiration, we estimate equation
−2×600
(3) as P ctChangei = 2wbai +600 .
C.2 Identification in the Difference-in-Difference Research Design
Identification in the dose-response difference-in-difference design requires three assumptions.
First, we make the standard orthogonality assumption: εit ⊥ SuppAvailt , P ctChangei . The
economic content of this assumption is that high and low-wage workers (who differ in P ctChangei )
would have had the same trend in job-finding absent the policy change. This assumption has a testable
prediction: parallel trends prior to the policy change. Figure 6 shows that the data are consistent
with this assumption for the exit rate to new jobs. While this parallel pre-trend is reassuring, one
9
might still be concerned about differential labor market trends for high and low-wage workers due
to the uneven incidence of the pandemic across industries, locations, and workers of different ages,
all of which are potentially correlated with wage levels. However, in Appendix C.5, we show that
nearly identical conclusions obtain when exploiting only within state-age-industry group variation.
In addition, we note that if there were a persistent difference in job-finding trends (e.g., low-wage
workers have faster employment growth because of business reopenings) then the bias in β̂ will have
opposite signs across the two policy changes because one is a decrease in benefits while the other is
an increase in benefits.
Second, we assume that the causal effect of replacement rates on job-finding is homogeneous in the
treatment group and control group. This assumption implies that raising a low-wage worker’s replace-
ment rate will have the same absolute effect on job-finding as raising a high-wage worker’s replacement
rate by the same absolute amount, thereby implying a linear relationship between replacement rates
and exit rates. De Chaisemartin and D’Haultfœuille (2018) show that this assumption is necessary
for identification in dose-response designs.
Two pieces of evidence are consistent with the homogeneity of treatment effects. First, the apparent
linearity of the effect of benefit changes on the job-finding rate in Figure 7. Second, we also test this
assumption using the structural model from Section 5. Specifically, we calculate the change in the
job-finding rate for low-wage and high-wage workers at different sizes of benefit decreases ranging
from -70% to -120% (following the support of the x-axis variation in Figure 7). We find that when
exposed to the same percentage change in benefits, low-wage workers and high-wage workers in the
model have very similar changes in job-finding.
Third, we assume that job seekers did not anticipate the changes in supplements. This is consistent
with the results from our best-fit model that households act surprised by policy changes.
C.3 Comparison of Estimates Across Research Designs and Episodes
Comparing the estimates of job-finding disincentive effects across episodes and research designs re-
quires re-scaling the four estimates (two research designs and two policy changes) into common units.
Comparing within a given policy change, the interrupted time-series estimates tell us the average
effect of the entire supplement while the difference-in-difference estimates tell us the effect of a
marginal change in P ctChange across workers. We convert from the difference-in-difference esti-
mate β̂ to an estimate of the average effect of the entire supplement by assuming a homogeneous
treatment effect over the entire range [0, E(P ctChangei )] and computing τ̂ = β̂E(P ctChangei ). We
note that this is a stronger assumption than that in the previous sub-section (Appendix C.2) since
min(P ctChangei ) > 0, and so this requires linear extrapolation out of sample.44
Two types of evidence bolster the plausibility of such an extrapolation. First, within the empirical
variation available in the data, the relationship between the intensity of treatment (size of the change
in benefits) and the outcome (change in the exit rate) appears to be linear (Figures 7a and 7b).
Second, in the best-fit model, the effect of the supplement on the job-finding rate is also close to
linear, as shown in Figure A-20.
Although our analysis treats the two research designs as estimating the same parameter, one pos-
44 Ideally, we would like to compare a treated group receiving a supplement (and thus P ctChange > 0) to an untreated
control group with no supplement (and thus P ctChange = 0) but we have no such untreated control group and must
instead extrapolate from comparisons across groups with different positive P ctChange.
10
sibility for why time-series estimates are smaller is if the “micro” disincentive effect of unemployment
benefits (the effect of giving one worker more benefits) is bigger than the “macro” disincentive effect
(the effect of giving all workers more benefits).45 The macro effect includes additional equilibrium
effects.46 The difference-in-difference estimate, which compares changes in the job-finding rate for
more- and less-treated workers, may be closer to a micro elasticity, while the interrupted time-series
estimate, which measures the change in the job-finding rate for all workers, may be closer to a macro
elasticity.
C.4 Calculating Duration Elasticities
The duration elasticity is defined as the percentage change in expected unemployment duration caused
by a given change in benefit size divided by the percentage change in benefits:47
EDwith supp
EDno supp − 1
ϵ= ,
Supp Size/Ave Regular Benefit Size
where ED is the expected duration of unemployment. We now describe the calculation of these
objects in more detail. Call the total exit hazard observed in the data (which includes the effect of
the supplement when it is in place) λt,with supp = et + recallt , with observed new job-finding rate et
and observed recall rate recallt . We assume et and recallt are constant at their sample averages after
the end of the observed data.
We then construct a counterfactual total exit hazard with no supplement: λt,no supp = λt,with supp +
τt × It (supp = on), where τt is an estimate of the effect of a given supplement on the job-finding rate
at date t, and It (supp = on) is an indicator for whether a supplement is on or off in week t. For the
statistical exercises assuming constant effects, τt is assumed constant at values from Table 3, while in
the model τt is calculated from the full model dynamics. Thus, the simple statistical counterfactual
without supplements just shifts up the observed job-finding rate by the constant amount τ while the
supplement is in effect, while in the model τt varies with any dynamic forces. Based on the discussion
in Appendix C.5 we assume the recall rate in period t is the same with and without the supplement.
So, the shift in the total exit rate λ is given by just the change in the new job-finding rate τt .
Given λt,with supp and λt,no supp we can compute expected unemployment durations with and with-
out the supplements and thus the duration elasticity by converting the job-finding hazards λ to a sur-
vival function. Specifically, let St,with supp = Πtj=1 (1−λj,with supp ) and St,no supp = Πtj=1 (1−λj,no supp )
be the cumulative survival functions with and without supplements. The expected duration with sup-
plements is then given by
∞
X
EDwith supp = λ1,with supp + (λj+1,with supp ) (Sj,with supp ) (j + 1),
j=1
45 Many theoretical papers on UI (e.g., Hagedorn et al. 2013 and Landais, Michaillat, and Saez 2018) argue that the mi-
cro disincentive effect is insufficient to determine optimal benefit levels; one must also know the macro disincentive effect.
46 First, it captures the response of new vacancies to more generous benefits. More generous benefits could decrease
vacancy creation by reducing match surplus (Hagedorn et al. 2013) or increase it by increasing aggregate demand (Kekre
forthcoming). Second, it captures the “rat-race” effects in Michaillat (2012), where discouraging one worker from taking
a job may simply lead to another worker taking the job instead.
47 Elasticities are sometimes approximated using log changes, but this approximation is poor in our context since we
study large changes.
11
and the average duration without supplements is given by
∞
X
EDno supp = λ1,no supp + (λj+1,no supp ) (Sj,no supp ) (j + 1).
j=1
Expected duration will depend on both the time-series of job-finding and the number of weeks in
which It (supp = on) = 1. The latter will vary for cohorts that enter unemployment at different dates
since those entering closer to supplement expiration will have a shorter period with supplements in
effect. This means that the statistical-based duration elasticity will differ for different cohorts but will
be maximized in most cases for cohorts starting unemployment in the same week that supplements
start. For this reason, we conservatively report duration elasticities for an unemployed cohort starting
April 1, 2020 for the $600 supplements and January 1, 2021 for the $300 supplements.
Together this procedure gives the numerator of ϵ. The denominator is more straightforward since
we know the size of supplements and can directly measure the benefit amount in the data.48
C.5 Additional Job-Finding Results and Robustness
C.5.1 Robustness
We conduct three tests to validate the difference-in-difference estimates. First, we estimate a version
of equation (4) by week:
eit = γP ctChangei + αW eekt + βt W eekt × P ctChangei + εit (C1)
This enables an event study interpretation of the coefficients. Figure A-23 shows that treatment effects
from the expiration of the $600 are largest in the three weeks after the policy expires and smaller in the
subsequent five weeks. This suggests that long-term effects of expiration on the weekly job-finding rate
may be even smaller than the baseline estimates from equation (4) which pool the eight weeks after
expiration in Table A-2. The figure also shows a stable treatment effect from the onset of the $300.49
In a second group of checks in Tables A-11a and A-11b, we re-estimate equation (4), adding
controls Xi and Xi SuppAvailt to address concerns about differential trends by group. First, we add
state (and state-by-supplement-available) fixed effects, so that identification comes from comparing the
job-finding rate for higher- and lower-wage workers with different benefit replacement rates in the same
state. Second, we add age (and age-by-supplement-available) fixed effects, so that identification comes
from comparing the job-finding rate for higher- and lower-wage workers with different replacement
rates who are in the same state and are the same age. Third and finally, we add industry (and
industry-by-supplement-available) fixed effects. In this richest specification, identification comes from
comparing the job-finding rate for higher- and lower-wage workers with different replacement rates
who are in the same state, are the same age, and worked in the same industry. Our estimates of β̂
change little from incorporating these control variables.
48 To limit the influence of outliers, our empirical specification for computing τ uses the symmetric percent change in
benefits as the regressor. Using an empirical specification with the “regular” percent change produces a lower value of
τ and thus a lower implied ϵ. Thus, our conclusion of a low ϵ from our preferred specification is conservative.
49 Figure A-23b indicates that even prior to the onset of the $300 supplement there is already a gradual trend downward
in the job-finding rate for households that receive the largest increase in benefits on January 1, 2021. If we were to use
a specification that accounted for this pre-trend in estimation we would likely find that the $300 supplement has even
smaller effects on the job-finding rate.
12
Third, we explore the robustness of our results to alternative functional forms for estimating job
finding effects. Our baseline empirical specification estimates a dose-response difference-in-difference
design using a linear probability model, which assumes a constant relation between the absolute change
in the exit rate (in percentage points) and the relative change in benefits. This empirical specification
is supported by our theoretical model, as shown in Figure A-20. However, the most common empirical
specification for estimating disincentive effects of UI is a Cox proportional hazard model, which instead
assumes constant proportional rather than absolute effects. The Cox model cannot be used in our
setting where policy changes affect unemployed workers in the middle of a spell. However, we can
explore the robustness of our results to alternative specifications which estimate relative rather than
absolute outcomes (i.e. using the percent change in exit rates rather than the absolute change in
exits as the outcome). We explore two alternative specifications. The first is a binned version of
our baseline regression which uses 10 deciles of the percent change in benefits but switching to the
percent change in exit as the outcome. This specification allows us to measure percent changes for
our binary exit outcome, but it collapses the micro data to bins. The second specification is a logit
specification which lets us use the micro data with percent changes in outcomes. Table A-12 shows that
these alternative specifications produce very similar conclusions to our baseline empirical specification.
Duration elasticities remain low and very similar to the baseline specification. Furthermore, duration
elasticities are all below hazard elasticities, as implied by the discussion in Section 5.3.2.
C.5.2 Recalls
How did the supplements affect the exit rate to recall? There is some evidence that the expiration of
the $600 supplement might have had a small effect on recalls but the evidence is hard to interpret, and
even the upper bound of plausible causal impacts on recalls still implies small aggregate employment
effects. There is no evidence of any effect of the $300 supplement on recalls.
Figure A-13a shows time-series patterns of recall. The recall rate is highest while the $600 sup-
plement is still in place, suggesting it did not substantially deter recall. Indeed, more than half of
unemployed workers return to work before the $600 supplement expires. This figure also illustrates
that the recall rate is falling over time (making it hard to know what the counterfactual recall rate
would have been in the absence of the supplement) and volatile (making it hard to assess statistical
significance). There is evidence of a short-lived increase in recalls in the three weeks after the supple-
ment expires. However, even if we make the aggressive assumption that recalls would have trended
down through these three weeks in the absence of supplement expiration, the implied effect on the
average duration of unemployment is tiny because this increase in the recall rate is so short lived.
The time-series evidence around the start of the $300 also suggests it had no effect on recalls. If
anything recalls rise after the supplement takes effect. We also note that the aggregate recall rate is
already low even before the onset of the $300 supplement, meaning there is little scope for a further
reduction from the $300.
Difference-in-difference results cast further doubt on the possibility of substantial effects of sup-
plements on recalls. Figure A-17e shows that recall is higher for the high replacement rate group after
the $600 supplement expires, but not in the three weeks when the aggregate recall rate is elevated.
Instead, the recall rate for the high replacement group only rises differentially in the subsequent six
weeks. Table A-13a finds a β̂ coefficient for recall that is about two-thirds of the size of the exit to
new job coefficient. However, the figure illustrates that this effect is again short-lived, implying that
13
even if this delayed differential recall response is causal, it has a small effect on aggregate employment
patterns.
The difference-in-difference evidence that the $300 had tiny effects on recall is even more clear cut.
Figure A-17f shows that there is little difference in recalls between workers with above- and below-
median replacement rates. Table A-13b re-estimates equation (4) and reports a coefficient (0.003)
that is one-seventh of the already small effect on new job-finding and economically indistinguishable
from zero.
Overall, the supplement may have changed the timing of some recalls, but there is no evidence of
substantial recall effects which would change the conclusions we describe in Section 5.2 that effects
of supplements on employment were small. However, alternative data and/or research designs are
needed to precisely quantify the effect of the $600 supplement on recalls.
C.5.3 Effects in Summer 2021
We replicate the job-finding analysis from Section 4.2 for the expiration of the $300 supplement. We
are unable to replicate the interrupted time series analysis because of the contemporaneous expiration
of PEUC (discussed in Appendix A.1).50 To illustrate this, Figure A-24a shows that the exit rate
from UI rises sharply to extremely high levels in September 2021 as many workers mechanically lose
benefits when PEUC expires.
We thus focus our analysis on a subset of workers who are ex ante likely to be in the regular
UI benefit program (not PEUC) and thus exposed only to the supplement expiration. To do so, we
limit the sample to workers who have received UI benefits for no more than four weeks as of July
11, 2021.51 A worker who received UI benefits continuously through the end of October 2021 would
therefore only have received 20 weeks of benefits and therefore receive regular UI benefits (and not
PEUC) throughout the analysis period.
However, restricting to low observed duration does not guarantee that a worker is indeed covered
under regular UI and not PEUC. There is potential for measurement error in duration (for example,
a worker might receive payment for many weeks of benefits in a single calendar week because of back
pay) meaning that some of these workers may actually be covered by PEUC instead of regular benefits.
Indeed, Figure A-24b shows that the exit rate rises substantially at expiration, even after we limit
the sample to workers with short observed duration. Nevertheless, if the extent of measurement error
in PEUC eligibility is the same in groups with larger and smaller changes in benefits then it still is
possible to identify the causal effect of the expiration.
Figures A-24b and A-25 shows workers with a larger decline in benefits had a larger increase in
the job-finding rate. However, we note the large rise in the job-finding rate for workers with a -110%
decline in benefits. These are workers who would have had regular benefit without the supplement
of only about $150 per week. If there is measurement error in the weekly benefit amount and people
for whom the weekly benefit amount is particularly noisy also have a particularly high exit rate then
that will artificially inflate our estimate of the disincentive.
Table A-14 shows regression estimates as well as several related specifications. Depending on
whether we define the maximum allowed observed duration in July as four or eight weeks and whether
50 We are only able to replicate the job-finding analysis for the expiration in September 2021. Estimates for the
expiration in June 2021 are under-powered, so we are unable to make any economically meaningful statement.
51 We start the counter on benefit receipt as of January 1, 2020. If a worker goes 26 consecutive weeks without
receiving UI we assume that they have re-established eligibility for benefits and reset the counter to zero.
14
or not we include the weeks when the exit rate is mechanically the highest we find that the regression
coefficient varies from -0.0137 to -0.0305.
15
D Additional Model Details and Results
D.1 Model Setup
This section describes the model setup in additional detail. Each month, households choose con-
sumption c and savings a with return r and a no-borrowing constraint a ≥ 0 to maximize expected
P∞
discounted utility E t=0 β t U (c). When employed, household i has constant wage wi which dif-
fers across households but is constant over time. Employed households become unemployed with
constant probability π. When unemployed, a household finds a job at wage wi with probability
fi,t = recallt +searchi,t , where recallt is a common exogenous recall rate and searchi,t ∈ [0, 1−recallt ]
is household i′ s endogenous choice of search effort. Search effort induces disutility ψ(searcht ). Recall
requires no search effort or disutility. When households are unemployed, they receive unemployment
benefits as well as additional secondary income proportional to the lost job: hwi .
Income for an unemployed household depends on aggregate UI policy and whether they are waiting
for benefits. Regular benefits last 6 months. Benefits for a household newly unemployed during the
pandemic last 12 months.52 Benefit levels depend on the current aggregate UI supplement in place:
m ∈ {0, 300, 600}. To speak to our empirical research design, we allow for the possibility that an un-
employed household may face delays in receipt of UI and in turn later receive backpay. This means un-
employed households can be in one of four receipt statuses: d ∈ {normal, delayed, backpay, expired}.
The regular benefit policy is intentionally simple: unemployed households receive benefits which
replace a constant fraction b of wi . When available, supplements add m to these baseline benefits.
This means that an unemployed household getting benefits without delay receives bwi + m.
Unemployed households can also be in a delayed receipt status and not currently receiving benefits
if d = delayed. In this case, current earnings are given by hwi . When households exit this status, they
receive backpay equal to α(bwi +m), where α is chosen to match “backpay” observed in the data. When
regular benefits expire after 12 months, income again drops to hwi . This means that total earnings y
for a household with wage wi , employment status s, supplement m, and delay status d are given by:
wi if s = e
bw + m + hwi if s = u and d = normal.
i
y(wi , s, m, d) = hwi if s = u and d = delayed. (D1)
α(bwi + m) + hwi if s = u and d = backpay.
hwi if s = u and d = expired.
The economy begins in a steady-state UI policy environment with m = 0 and d = normal.
Households expect UI policy will never change. Beginning from this initial steady state, the economy
is hit by policy changes which mimic UI policy changes over the pandemic. In April 2020, the economy
switches from m = 0 to m = 600 and remains in this state for 4 months. In August 2020, it switches
to m = 0. In January 2021, it switches to m = 300, and in September 2022 it switches back to m = 0.
This describes the evolution of actual policy through this period, but we must also specify expec-
tations. We assume the initial switch from m = 0 to m = 600 is unanticipated.53 Once the 600 is
52 To simplify the computational setup, we assume that pandemic benefits are only available for the first unemployment
spell and that when a household returns to employment they return to the regular benefits policy for future UI spells.
53 For computational tractability, we assume employed households continue to expect regular benefits after the pan-
demic starts until they actually become unemployed. Since we focus on a cohort of unemployed households beginning
16
implemented, households know for sure that it will last at least 4 months. In our main results, we
consider two different specifications for expectations about m after these 4 months.54 In the perfect
foresight specification, households correctly expect that m will revert from 600 to 0 in August. In the
alternative myopic expectation specification, households instead expect that m = 600 for the dura-
tion of their remaining benefit spell and are then surprised in August when it expires. Once m = 600
expires in August, households expect that m = 0 forever. For the $300 weekly supplements, we study
a newly unemployed household in November of 2020. They either anticipate or are surprised that
the m = 300 supplement begins in January, 2021.55 Once the $300 supplement begins, households
anticipate that supplements will expire in September 2021.
Expectations about UI delay are simpler. Households who are in the d = nodelay state anticipate
that they will remain in this state. That is, households do not anticipate delays in benefit receipt.
When households are in the d = delay they always assume that they will be in d = backpay next period
and that they will be in d = nodelay the period after that. That is, households always anticipate
that benefit delays will be resolved next month. However, even though households always anticipate
that delays will be resolved once they enter this state, the realized length of d = delay can extend for
multiple periods. That is, just as households are surprised by initial delays in benefits, they can also
be surprised by a longer than expected waiting period. In our main simulations, the actual benefit
delay lasts two months to match what we observe in the waiting design. In prior drafts we explore
other specifications for expectations over delays and found similar quantitative conclusions.
Households anticipate a constant recall rate throughout the pandemic, although results are similar
if we instead assume perfect foresight over the actual recall rate. We deal with pandemic effects in
two ways: First, we focus on the evolution of unemployed households relative to employed house-
holds in both model and data. This means any effects of the pandemic which affect all households
equally are effectively removed. Second, we directly model several pandemic events. We introduce
a one-month discount factor shock to all households in April 2020, which we calibrate to match the
decline in spending for employed households during the pandemic.56 Since we focus on the behavior
of unemployed households relative to employed households, this shock has little effect on our con-
clusions, but it means that we do a better job of hitting absolute spending and liquidity changes
over the pandemic rather than just matching relative changes. We also introduce additional one-time
unanticipated transfers to replicate stimulus checks in April 2020 and January 2021 as well as LWA
payments in September 2020, but this again has little effect on our conclusions.
Letting n represent the expected number of periods until m = 0, the household optimization
problem of a household unemployed during the pandemic can be written as:57
in April, this choice has little practical effect beyond simplifying computation.
54 Intermediate versions of expectations unsurprisingly produces results between these two version.
55 We simulate a separate cohort of unemployed households becoming unemployed in November so that we do not
have to also model extensions of the duration of regular benefits which happened periodically throughout the pandemic.
56 Using a sequence of discount factor shocks introduces additional complication but does not change the results much
since only April 2020 exhibits a very sharp swing in spending.
57 For simplicity, this notation ignores the discount factor shock. In April 2020, the model is solved using a different
β for a single period before transitioning back to this specification
17
Vu (a, s = u, m, d, n) = max U (c) − ψ(search)
c,a′ ,search
+ βEm′ ,n′ ,d′ [(search + recall)Ve (a′ , s = e, m′ , d′ , n′ )
+ (1 − search − recall)Vu (a′ , s = u, m′ , d′ , n′ )]
s.t.
a′ + c = y(wi , s, m, d) + (1 + r)a,
a′ ≥ 0,
Equation D1,
and expectations of s′ , m′ , d′ , n′ .
The value function of an unemployed household pre-pandemic is analogous except that m is always
0, d is never delayed and n lasts for 6 instead of 12 months. The value function of an employed house-
hold is also analogous except that s = e so y(wi , s, m, d) = wi , they have no search decision and they
transition to the regular pre-pandemic unemployment value function with exogenous separation rate π.
D.2 Model Parameters
Many of our parameters are standard or map directly to observable objects in the data. We describe
these parameters first. We then describe more complicated parameter choices that target simulated
moments in more complicated ways. Table A-3 summarizes the resulting model parameters.
1−γ
We set the annual interest rate r = .04. We assume that the utility function is given by U (c) = c1−γ
and set γ = 2. We set the exogenous separation probability π = 0.028 to match pre-pandemic transi-
tions from Krueger, Mitman, and Perri (2016). We set the expected recall rate recallt to be constant
at its average value of 0.08 but use the actual evolution over the pandemic where relevant. Figure
A-26 illustrates the environment by showing income for the unemployed relative to employed in the
model and data for a newly unemployed worker with and without a benefit delay in our calibrated
model. We set b = 0.21, h = 0.7, m = 0.35, α = 2.35 to match household income series for the waiting
and receiving UI groups over the pandemic. Specifically, h targets mean household income for unem-
ployed households waiting for benefits, relative to employed households. Then given h we pick b so
that h + b targets mean household income for unemployed households receiving benefits in fall 2021
when no supplements were in place, relative to employed households in these same months. Given h
and b we then pick m so that h + b + m hits the ratio of mean income for unemployed to employed
when the $600 supplements were in place. Finally we pick α = 2.35 to match the mean income of the
waiting group relative to the not-waiting group in the first period where the waiting group receives
benefits (and thus backpay). We solve the model for five different wi groups and choose the variation
to match mean household income by five quintiles of the replacement rate in JPMCI data.
We pick the remaining parameters of the model to target more complicated model objects using
an indirect inference procedure to choose the discount factor and simulated method of moments to
choose the search cost parameters.58
58 While we use these estimation procedures for point estimations, we do not perform inference on these parameters
18
(1+ϕ)
We assume that ψ(searcht ) = k0 (search t)
1+ϕ + k1 and pick the parameters of this search cost
function in one of two ways. In our “pre-pandemic” calibration, we calibrate search costs to generate
a pre-pandemic job-finding rate of 0.28 and an elasticity of average unemployment duration to a small
6 month change in benefits of 0.5. This is the median estimate from the Schmieder and von Wachter
(2017) meta-analysis. Since we only have two moments and three parameters, the pre-pandemic
calibration is not identified without additional restrictions and so we impose k1 = 0.59
In our “best-fit” calibration, we instead calibrate search costs to target the time-series of job-finding
over the course of the pandemic. Specifically, we pick search cost parameters in the model to minimize
the squared percentage deviation between the monthly job-finding rate in the model and data from
April 2020 to February 2021. This simulated method of moments-like procedure is over-identified
because we have 3 parameters and 11 moments to target.
Table A-3 shows that this yields k1 < 0, implying a disutility of unemployment. This contrasts
with a common assumption in macro models that unemployment delivers positive utility because of
the time available for home production but is consistent with recent experimental findings in Hussam
et al. (2022).
The search cost parameters are most interpretable in terms of implications for job search elasticities.
The calibrated pre-pandemic search cost parameters imply a job search hazard elasticity to a small
benefit change for 6 months of 0.66 and the best-fit search cost parameters imply a hazard elasticity
of 0.29.60
We calibrate the discount factor in one of two ways. In the pre-pandemic calibration, we pick β so
the model matches pre-pandemic evidence on the response of spending to stimulus checks summarized
in Kaplan and Violante (2022). Specifically, we pick set β = .99 monthly to generate a 3-month MPC
of 0.25 in response to a 500 stimulus check sent to all households. In our alternative best-fit calibration,
we instead pick β = 0.978 to target the MPC out of UI payments in our waiting design. There is not
a mapping directly from the discount factor to the MPC in the model, so this is a simple version of
indirect inference. Since we target a single MPC that declines in β, β is exactly identified through
this procedure.
D.3 Model Solution
We solve the model using the endogenous grid method with linear interpolation for policy functions off
grid points. We use 100 grid points for assets distributed exponentially from 0 to 2000 times median
household income. The model must be solved for several different benefit profiles with length up to
13 months (pandemic era benefits last for 12 months and then expire as an absorbing state; regular
benefits last for 6 months) as well as the different delay statuses. We solve the model separately for each
of the five wage groups. We solve for the value function for employment and regular unemployment
benefits iterating to stationary policy functions and then solve for the pandemic-era temporary policies
using backward induction from these stationary value functions. We similarly backward induct one
period from the stationary value functions to solve for the solutions with the discount factor shock.
To solve for optimal search, we use the first order condition given next period’s value functions
to account for statistical uncertainty. In our context there is little cross-sectional uncertainty since we have very large
samples, and we have no aggregate shocks in our model so there is no aggregate uncertainty. Thus, statistical uncertainty
over parameters in the model would be approximately zero.
59 If we instead impose the value of k we estimate for the pandemic, qualitative conclusions are unchanged.
1
60 Note that the hazard elasticity of 0.66 in the former case implies the targeted duration elasticity of 0.5.
19
of employment and unemployment. Given optimal policies, we then simulate the model for 1,000
households of each of each wage group (5,000 households total) and compute average statistics.
D.4 Best Fit Model - Additional Results
The main text focuses on the model-fit for the $600 supplements, but Figure A-19 shows that our
conclusions also apply for the model fit to the $300 supplements.
We pick search costs in our best fit model to target time-series variation in the job-finding rate.
Since our model features heterogeneity in wages it also has implications for job-finding over the wage
distribution which can be compared to our difference-in-difference research design. Figure A-20 shows
that the model calibrated to time-series evidence produces difference-in-difference results which align
closely with those from the data. This means that the choice of targeting time-series vs. cross-sectional
variation makes little difference for our model conclusions. This figure also provides additional support
for the linearity assumption imposed by our empirical difference-in-difference research design.
Figure A-27 shows that liquidity effects on job-finding after supplements expire are small demon-
strating that dynamic liquidity effects imply little bias for our reduced-form specifications.
D.5 Understanding High MPCs out of UI vs. Stimulus
What explains the large spending responses to unemployment supplements? To understand this, it
is useful to compare them to more commonly studied one-time stimulus payments. In particular,
recall that our pre-pandemic model is calibrated to match a 0.25 quarterly MPC out of a one-time
$500 payment. Relative to these one-time payments, UI supplements differ in their targeting, size,
and persistence. Furthermore, these supplements were implemented in a pandemic environment with
depressed overall spending and elevated liquidity.
Table A-15 shows that each of these forces is important for understanding the spending responses
to supplements. Each row varies one element at a time to illustrate the forces shaping spending
responses to supplements during the pandemic. The first row shows the one month MPC out of
combined regular benefits plus the $600 supplement ($2,400 monthly) for an unemployed household
who is currently receiving no benefits during the pandemic in our best fit model. This combination
of elements replicates the empirical environment for the waiting design in Section 3.2.1. Since our
best-fit model is calibrated to match this MPC, the model MPC equals the empirical MPC of 0.42 by
construction. This MPC mixes the spending responses to regular benefits and supplements. Thus, in
row 2 we compute the model MPC to supplements alone, which are targeted at a household already
receiving regular unemployment benefits. This MPC of 0.29 corresponds to the supplement MPC in
Table 4. We note that this value is essentially the same as the untargeted MPC of 0.30 and 0.26 to
the end of the $600 and start of $300 supplements estimated in Section 3.
In row 3, we compute this same MPC but in a “normal” economic environment which eliminates
pandemic stimulus checks and discount factor shocks. Since turning off these pandemic forces decreases
liquidity, the MPC to UI supplements rises to 0.45. Row 4 then shows that the MPC out of a one-time
$2,400 payment falls to 0.29, implying that some of the spending response to supplements comes from
the fact that they are persistent rather than transitory transfers. In row 5, we decrease the size of
the transfer from $2,400 to $500, which corresponds to the stimulus check sizes that we target in
pre-pandemic model calibrations. This increases the MPC substantially due to the concavity of the
20
consumption function. Unemployed households’ liquidity constraints and MPCs are relaxed more in
response to a large transfer than in response to a small transfer.
Next, we modify who receives the the transfer. Row 6 shows that providing a $500 transfer to ev-
eryone instead of just to unemployed households reduces the MPC from 0.45 to 0.21 since unemployed
households have higher MPCs. Finally, row 7 and row 8 show the effect of changing the calibration of
the discount factor so that the model hits a quarterly MPC of 0.25 to this $500 transfer. Row 8 shows
that the model hits this quarterly MPC of 0.25 by construction, and row 7 shows that the monthly
MPC to this same shock is 0.09 so it can be compared to MPCs from other rows which are calculated
at monthly horizons.
Putting all these forces together leads to a one month MPC out of supplements that is more than
three times larger than the one month MPC out of $500 stimulus checks (0.29 vs 0.09).
Summarizing the results from this Appendix, persistence and targeting towards households with
high propensities to spend are key forces for high MPCs out of supplements. Their large size decreases
the MPC since it relaxes liquidity constraints, but on net the first two forces (i.e. persistence and
targeting) dominate and so spending responses to UI supplements are much larger than spending
responses to stimulus checks. This conclusion should generalize beyond the pandemic, since these
forces are not pandemic-specific. Indeed, this conclusion is likely to be even stronger in a more normal
recession when aggregate spending is not reduced due to pandemic-specific reasons (i.e., Table A-15
row 3 is greater than row 2).
21
E Alternative Models
This section discusses model extensions and alternative models which are mentioned in the main text.
E.1 Time-Aggregation Issues
Our baseline model is monthly and assumes that benefits start immediately upon job loss: households
are employed until March 2020 and then become unemployed and start receiving regular benefits plus
$600 supplements immediately in April. In the data, there are some high frequency changes around job
loss not captured by this simple model. Our data sample selects households who receive their last pay-
checks at the end of March and receive benefits starting in April. Furthermore, most states did not be-
gin paying supplements until the second half of April even though the amount of supplements covered
benefit weeks for the entire month of April. What this means in practice is that in the data, households
who become unemployed at the end of March see a small decline in income at the end of March and
start of April before benefits start, and then a jump up in income in the second half of April that makes
up for the decline in the first half of the month. When aggregated to calendar months, this manifests as
a small decline in income in March and a jump up in income in April as households start receiving sup-
plements, but at the weekly frequency, this jump up in April is concentrated in the second half of the
month. This means that although April income is above that when employed, this increase occurs pri-
marily in the second half of the month and so does not allow for a full month of spending opportunities.
To address both high frequency timing issues around the start of unemployment and the start of
supplements, we make two changes while still maintaining the monthly model period for tractability.
First, we assume that both in regular times as well as during the pandemic, households have a
decline in income in the month that they lose their job but do not start unemployment insurance until
the following month. We choose this drop in income in the month of job loss to match the observed
decline in income in the data. In practice, this drop in income is small since we define the month of
job loss as the month when the last paycheck is received. However, this small decline in income in the
month of job loss is sufficient to generate declines in spending in the month of job loss. Given this
adjusted income process, we assume that households in this extended model lose their jobs in March
rather than in April. This model change is sufficient to generate the spending declines in March 2020
observed in the data, as shown in Figure A-18.
Second, we assume the income increase arising from supplements occurs in the second half of April.
Specifically, we assume that in the first half of the month, households spend as if they are receiving
the regular benefits profile but not supplements. Concretely, we compute spending in April in the
time-aggregation model as an equal weighted average of spending under the regular benefits profile
and spending under the benefits profile with supplements. Figure A-18 shows that the model with
this extension is a good fit to spending in April. Since it is more parsimonious, we use the simpler
model in the main text, but this figure shows that that all of our conclusions about our “best fit”
model relative to alternative models also hold in this extended model so our results are unchanged if
we complicate the model to match these high frequency patterns around the first two weeks of job
loss.
22
E.2 Alternative Behavioral Models without Myopic Expectations
Our best-fit model needs myopic expectations in which households act surprised by benefit changes
in order to fit spending and job-finding patterns over the pandemic. It is natural to wonder whether
models with more heterogeneity in impatience and job search costs might be able to explain these
patterns without “incorrect” expectations. For example, Ganong and Noel (2019) show that a model
that includes both hyperbolic and exponential discounting households together with a mix of high
and low job search costs can fit empirical patterns around the predictable expiration of benefits.
Specifically, a behavioral model with this type of heterogeneity can generate a sharp spending decline
and a sharp jump in job finding in response to the predictable end of regular UI benefits. Can a
similar model with hyperbolic discounting and heterogeneous job search costs explain patterns in the
pandemic without having to introduce myopic expectations? We show now that it cannot.
We consider an extension of our model that allows for the potential for substantial heterogeneity
in search costs parameters and discounting across households but that assumes perfect foresight ex-
pectations. To include the potential for hyperbolic discounting, we allow for households to discount
between now and the next period at a higher rate (using discount factor β) than they discount between
all future periods (using discount factor δ). We then re-solve the model for a range of search costs
(ten for each parameter), and discount factors (12 for δ and up to 12 for β, with the restriction that
β <= δ where β = δ corresponds to exponential discounting). In total this allows for approximately
81,000 different types of households.
The average value of spending and the job-finding rate then depend on the number of households
of each type remaining unemployed at each date. This depends on both the initial weight of each
household and how quickly each type of household exits unemployment. To pick the initial weights, we
use an iterative process to minimize the squared deviation between average job-finding and spending
in the model and the data. We begin by picking the weights on each household using the entire vector
of 81,000 types. We then further prune this model by iteratively dropping any type assigned a weight
< 0.25%. We do this pruning to yield a more parsimonious degree of heterogeneity, which makes it
easier to interpret results, but the conclusions are similar when allowing for unrestricted heterogeneity.
This pruning process ultimately results in a parsimonious model with three types: one “hyperbolic”
with persistently high MPCs and low elasticity of search costs (31% of households), one hyperbolic
type with persistently high MPCs and high elasticity of search costs (12% of households), and a more
standard household with exponential discounting and high elasticity of search costs, who has a high
MPC when liquidity constrained and a low MPC when not liquidity constrained (57% of households).
Figure A-28 Panels (a) and (b) show that this model misses on two dimensions. First, while the
model is able to generate a sharp increase in job finding when supplements expire, it is unable to
generate a sustained increase in job finding. Second, this model implies counterfactual asymmetry in
spending: in the model, the response to the start of the $600 supplements is substantially larger than
the response to the end of the $600 supplements.
The reason this model does not generate a sustained increase in job finding is because of compo-
sition effects. Panel (c) shows that the jump in job finding is driven by the hyperbolic type with low
elasticity of search costs (the orange line). This group barely searches when supplements are in place
and then searches hard after supplements expire. However, since this type searches at much higher
rates after expiration relative to the exponential type, it exits more rapidly and so its share of the
population declines, as shown in Panel (e). This composition effect leads to a decline in the average
23
job finding rate which is inconsistent with the data.61
The reason this model implies counterfactual asymmetry in spending is because households respond
more strongly to an unexpected change in income (the start of $600) than to an expected change in
income (the end of $600 with perfect foresight). This is especially true for the standard consumers
without hyperbolic discounting, but holds even for the hyperbolic households because even these
households save some small amount in anticipation of expiration.
The myopic expectations in our best-fit model fix both of these issues: if households are surprised
by the benefit expiration then search patterns shift in a sustained way after expiration, and spending
responses to the start and end of benefits are more similar when both are a surprise.
61 The type shown in red searches at a high rate throughout the sample period (which is helpful for matching the
initial average level of job finding) but few of these households remain by the time of supplement expiration.
24
Additional Figures and Tables
Figure A-1: States included in the JPMCI sample
Notes: This figure shows the subset of states which are included in various analyses. See Appendix A.2 for details.
25
Figure A-2: UI Claims in JPMCI versus DOL
(a) Time-series
(b) State-level Change at Pandemic Onset
(c) Weekly Benefit Amount Pre-Pandemic
Notes: This figure compares total claims and benefits levels in JPMCI data to Department of Labor ETA Form 539
Employment and Training Administration (2019 - 2020c) and Form 5159 Employment and Training Administration
(2019 - 2020b). Panel (a) compares aggregate time-series patterns, panel (b) compares state-by-state changes, and
panel (c) compares benefit levels by state. Panel (b) depicts the ratio of the number of payments in May 2020 to the
number of payments in 2020 prior to the declaration of national emergency. Panels (b) and (c) include a 45-degree line
and drop states with less than 300 observations.
26
Figure A-3: Changes in Industry Composition of Unemployment, JPMCI vs DOL
Retail Trade Accommodation
Symmetric percentage change in industry mix (JPMCI)
●
Arts, Entertainment, and Food Services
●
Mining, Quarrying, and Recreation
●
Extraction
●
0.5 Health Care and
Wholesale Trade
● ● Social Assistance
Management of ●
● Companies ●
Manufacturing Other Services
●
Educational Services Real Estate
●
●
0.0 Information Transportation and
Warehousing
●
Public Administration
●
●
● Utilities
Finance and Insurance Professional, Scientific,
27 −0.5 Construction and Technical Services
●
●
●
Administrative
and Support Services
−1.0 ●
Agriculture, Forestry,
Fishing and Hunting
−1.5 −1.0 −0.5 0.0 0.5 1.0
Symmetric percentage change in industry mix (DOL)
Notes: This figure compares the change in unemployment composition in DOL to JPMCI. The diagonal line is a 45-degree line. Making these data sets comparable requires two
adjustments. Letting i denote industry, t denote period and s state, we start by defining total JPMCI claims as cJPit
M CI and state-specific claims from DOL ETA Form 203 as
cDOL
ist (Employment and Training Administration 2019 - 2020a). Form 203 excludes recipients of federal programs for the long-term unemployed, so we drop recipients in JPMCI
data with spells > 26 weeks. We also re-weight the DOL data to account for the fact that Chase has more customers in some states than others using weight wst = P st JP M CI .
cJP M CI
P
c
s ′ s′ t
cJP M CI (wst cDOL
M CI = P = P s
P ist )
We then measure industry share in JPMCI as pJP
it
it
JP M CI
and industry share in DOL as pDOL
it DOL
. Unsurprisingly, UI claim shares by industry
c ′ (wst c ′ )
i′ i t i′ s i st
differ between the two datasets (“Construction” and “Agriculture” are most under-represented in JPMCI and “Administrative and Support Services” and “Finance and Insurance”
are most over-represented) but we are primarily interested in the extent to which the changes in the composition of unemployment during the pandemic appear in the JPMCI
data. To quantify this, we analyze the shift in the composition of UI claims from pre-covid (January 2019 to March 2020) to the height of the pandemic (April 2020 to December
2020). Because the increases in UI claims are so large (and therefore the changes in proportions are highly skewed), we measure composition changes with the symmetric percent
p −p
change: 2 × pit +pi,t−1 .
it i,t−1
Figure A-4: Income, Spending, and Balances of Unemployed Versus Employed (Me-
dian)
Percent difference from January 2020 (median)
Income
50%
$300
supplement
available
25%
●
●
●
● ●
●
● ● ●
0% ● ● ●
●
● ●
● ●
● ●
● ●
● ●
●
●
● $600
supplement
−25% available
Spending (total)
20%
●
10% ● ●
●
●
●
●
● ●
● ●
● ●
0% ●
● ●
● ●
● ●
● ●
●
●
●
●
−10%
Checking account balance
100%
50% ●
● ●
●
●
● ●
● ●
● ● ●
● ● ●
0% ●
● ●
● ●
●
●
● ● ● ●
Jan '19 Apr '19 Jul '19 Oct '19 Jan '20 Apr '20 Jul '20 Oct '20 Jan '21
Unemployed (get benefits from April 2020 through February 2021)
● Employed
Notes: This figure replicates Figure 1 using sample medians instead of means.
28
Figure A-5: Spending of Unemployed Versus Employed (card and cash)
Percent difference from January 2020 (mean)
Income
$300
supplement
available
20%
● ●
● ●
● ●
● ●
0% ●
●
●
● ●
●
● ● ●
● ● ● ●
● ●
● $600
● ●
supplement
−20% available
Spending (card and cash)
20%
●
●
10% ●
●
●
●
● ● ● ● ●
● ●
●
● ●
0% ●
● ●
● ● ●
●
● ●
−10% ●
Jan '19 Jul '19 Jan '20 Jul '20 Jan '21
Unemployed (get benefits from April 2020 through February 2021)
● Employed
Notes: This figure shows that the spending (total) patterns in Figure 1 also hold for spending (card and cash).
29
Figure A-6: Impact of Delays in Unemployment Benefits on Spending (Total, Differ-
ences)
Difference from control group (receives first benefit May 31)
Income
$2,000
$1,500
$1,000 ●
● ●
● ● ●
$500 ●
●
$0 ● ●
●
●
● ●
●
●
● ● ● ●
●
Spending (total)
$300 ●
●
●
●
●
●
$200
●
$100
●
● ●
$0 ● ● ● ●
●
● ●
●
● ●
●
Jan '20 Feb '20 Mar '20 Apr '20 May '20
Week of first benefit ● April 5 April 19 May 10
Notes: This figure shows mean income and spending (total) differences from the May 31 control group for various
cohorts in the waiting for benefit receipt research design. Our MPC is based on the April 5th treatment group, which
has no benefit delay.
30
Figure A-7: Impact of Expiration of the $600 Supplement on Spending (Card and
Cash)
Difference from first week of July
Weekly unemployment insurance benefit
$0 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●
$−200
$600
$−400 supplement
expires
Spending (card and cash)
● ●
$40 ●
●
●
● ● ●
●
●
$0 ● ● ● ●
●
$−40
$600
$−80 supplement
expires
$−120
Jun '20 Jul '20 Aug '20 Sep '20
Unemployed (get benefits from June through the end of August)
● Employed
Notes: This figure measures the causal impact of the expiration of the $600 supplement on spending. The benefit
amount declines over two weeks in August (rather than one week) because some states pay benefits once every two
weeks and therefore paid out the supplement for the last week of July during the first week of August. The benefit
amount rises in September because states begin to pay the temporary $300 supplement. The control group is employed
workers who are matched on 2019 income levels as well as on the date of stimulus check receipt. The dependent variables
are mean benefits and mean spending, measured as a change relative to the first week of July. See Section 3.2.2 for
details.
31
Figure A-8: Impact of Onset of the $300 Supplement on Spending (Card and Cash)
Difference from first week of December
Weekly unemployment insurance benefit
$300
$200
$300
$100 supplement
begins
$0 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●
Spending (card and cash)
$200
$300
$100 supplement ●
● begins
●
● ●
●
$0 ●
● ●
● ●
●
●
● ● ● ●
●
Nov '20 Dec '20 Jan '21 Feb '21 Mar '21
Unemployed (get benefits from Nov through end of Jan)
● Employed
Notes: This figure measures the causal impact of the onset of the $300 supplement on spending. The benefit amount
rises over two weeks in January (rather than one week) because some states pay benefits once every two weeks. The
control group is employed workers who are matched on 2019 income levels as well as on the date of stimulus check
receipt. The dependent variables are mean benefits and mean spending, measured as a change relative to the last week
of December. The figure depicts November 2020 through March 2021. See Section 3.2.2 for details.
32
Figure A-9: Impact of Expiration of the $600 Supplement on Spending (Total)
Income: difference from first week of July
●
●
$300 ●
● ● ●
● ● ●
$0 ● ●
●
●
●
●
$600
$−300 supplement
expires
$−600
Spending: difference from first week of July
$200 ●
●
● ●
$100
●
$0 ●
●
● ● ● ● ●
$−100 ●
●
●
$−200
Spending: unemployed minus employed
$0
$−50
$−100
$−150
Jun '20 Jul '20 Aug '20 Sep '20
● Employed
Unemployed (get benefits from June through the end of August)
Unemployed minus employed
Notes: This figure measures the causal impact of the expiration of the $600 supplement on spending. The benefit
amount declines over two weeks in August (rather than one week) because some states pay benefits once every two
weeks and therefore paid out the supplement for the last week of July during the first week of August. The benefit
amount rises in September because states begin to pay the temporary $300 supplement. The control group is employed
workers who are matched on 2019 income levels as well as on the date of stimulus check receipt. The dependent variables
are mean benefits and mean spending, measured as a change relative to the first week of July. Spending is noticeably
higher in weeks which contain the first of the month, likely because many households pay bills at this time. See Section
3.2.2 for details.
Figure A-10: Impact of Onset of the $300 Supplement on Spending (Total)
Income: difference from first week of December
●
$1,000
$750 $300 ●
supplement
begins
$500
●
● ●
●
$250 ●
●
●
●
●
$0 ●
● ●
●
● ●
●
Spending: difference from first week of December
●
$300 ●
●
$200 ●
●
$100
● ●
$0 ●
● ● ●
●
●
●
●
$−100 ● ●
●
Spending: unemployed minus employed
$100
$50
$0
$−50
Nov '20 Dec '20 Jan '21 Feb '21 Mar '21
● Employed
Unemployed (get benefits from Nov through end of Jan)
Unemployed minus employed
Notes: This figure repeats Figure A-8 but for total income and spending. The control group is employed workers who
are matched on 2019 income levels as well as date of receipt of stimulus checks. The dependent variables are mean
benefits and mean spending, measured as a change relative to the last week of December. The figure depicts November
2020 through March 2021. Spending is noticeably higher in weeks which contain the first of the month, likely because
many households pay bills at this time, so the third panel differences out these high-frequency fluctuations. Income for
employed households similarly exhibits spikes at the end of the month for the same reason.
Figure A-11: Impact of Expiration of the $300 Supplement on Spending (Card and
Cash)
Difference from end of August
Weekly unemployment insurance benefit
$0 ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ● ●
$−100
$−200
$−300
$300
$−400 supplement
expires
Spending (card and cash)
$100 ●
●
●
●
$50 ● ● ● ●
● ●
● ● ● ●
●
●
$0 ●
● ●
$−50 $300
supplement
expires
Jul '21 Aug '21 Sep '21 Oct '21 Nov '21
Unemployed
● Employed
Notes: This figure measures the causal impact of the expiration of the $300 supplement on spending. The benefit
amount falls over two weeks in September (rather than one week) because some states pay benefits once every two
weeks. The control group is employed workers who are matched on 2019 income levels as well as on the date of stimulus
check receipt. The dependent variables are mean benefits and mean spending, measured as a change relative to the first
week of September. The figure depicts July 2021 through November 2021.
35
Figure A-12: Impact of Expiration of the $300 Supplement on Spending (Total)
Income: difference from end of August
● ●
●
● ●
$500 ● ●
● ●
$250 ● ● ●
● ●
● ● ● ●
$0 ● $300
supplement
$−250
expires
Spending: difference from end of August
●
● ●
$200
● ●
$100
● ● ●
$0 ●
● ● ● ● ● ● ● ●
● ●
$−100
Spending: unemployed minus employed
$50
$0
$−50
$−100
$−150
Jul '21 Aug '21 Sep '21 Oct '21 Nov '21
● Employed
Unemployed
Unemployed minus employed
Notes: This figure repeats Figure A-11 but for total income and spending. The control group is employed workers who
are matched on 2019 income levels as well as date of receipt of stimulus checks. The dependent variables are mean
benefits and mean spending, measured as a change relative to the first week of September. The figure depicts July 2021
through November 2021. Spending is noticeably higher in weeks which contain the first of the month, likely because
many households pay bills at this time, so the third panel differences out these high-frequency fluctuations. Income for
employed households similarly exhibits spikes at the end of the month for the same reason.
36
Figure A-13: Exit Rate from Unemployment Benefits
(a) Recall
Exit rate to recall from unemployment benefits
6% $600 supplement $300 supplement
available available
●
●
●
●
4% ●
●
● ●
●
●
●
● ●
● ● ●
●
● ● ●
● ●
2% ●
●
● ● ● ●
● ●
● ●
● ● ● ●
● ● ●
● ● ● ●
●
● ● ● ●
● ● ● ●
● ● ● ●
●
●
●
0%
Feb '20 Apr '20 Jun '20 Aug '20 Oct '20 Dec '20 Feb '21
(b) Total (New Job + Recall)
All exits
8% ●
●
● ● ● ●
● ●
● ●
6% ● ●
●
●
●
● ●
● ●
●
● ●
● ● ●
● ● ●
●
● ● ● ●
●
4% ● ●
● ●
●
● ● ●
● ● ●
● ● ● ● ●
●
● ● ●
● ● ●
2%
●
●
$600 supplement $300 supplement
available available
0%
Feb '20 Apr '20 Jun '20 Aug '20 Oct '20 Dec '20 Feb '21
Notes: This figure shows the exit rate to recall and the total exit rate in the JPMCI data. UI exit is defined as three
contiguous weeks without receipt of UI benefits. Recall is measured using receipt of labor income from a prior employer.
Exit rate to new job is from Figure 4.
37
Figure A-14: Exit Rate by Start Date of Unemployment Benefit Spell
Exit rate to new job from unemployment benefits
●
● ●
5% ●
●
4%
●
●
● ●
●
3% ●
● ●
● ●
● ● ● ●
● ● ● ● ●
● ● ● ● ● ● ●
● ● ● ● ● ● ● ● ● ● ●
● ● ● ● ● ● ● ● ●
●
● ● ● ● ● ● ● ● ● ● ● ●
2% ● ● ●
●
●
●
●
●
●
●
●
●
●
●
●
●
● ●
●
●
●
●
●
●
●
● ●
●
●
● ●
●
●
● ● ● ● ●
● ● ● ● ● ● ● ●
● ● ● ●
● ● ● ● ●
●
● ● ● ● ● ● ● ●
● ● ● ● ● ● ●
● ● ● ● ●
● ● ● ● ● ●
● ● ●
1% ● ● ●
●
●
● ● ●
●
●
●
● ● ●
●
● ● ●
● ●
●
●
0%
Feb '20 Apr '20 Jun '20 Aug '20 Oct '20 Dec '20
●
Pre−pandemic ●
Mar ●
Apr ●
May ●
Jun
Notes: We define the pre-pandemic group as those who started receiving unemployment insurance benefits during or
before the week of March 15, 2020.
Figure A-15: Exit Rate at Expiration of PEUC
Exit rate not to recall
4% ●
3% ●
●
● ● ●
● ● ●
●
● ● ● ●
● ●
●
2% ● ● ●
●
●
key
1% ● All
Drop PEUC in 4 states
0%
Nov 20 Jan 21 Mar 21
Notes: This figure shows the evolution of the exit rate not to recall from October 2020 through February 2021. The
orange series is the same as the one shown in Figure 4, except that here the series includes January 3 and January 10.
The y-axis title is the “exit rate not to recall” instead of the “exit rate to new jobs” because some of the exits arise
from a policy seam. The blue series drops the 71,000 households that have received at least 20 weeks of benefits in
2019 and 2020 in Indiana, California, New Jersey, and Ohio. These households are likely to be recipients of Pandemic
Emergency Unemployment Compensation, which temporarily lapsed at the end of December and these four states were
slow to restore benefits after the lapse. The difference between the blue series and the green series reveals that the lapse
triggered a surge in measured exits in four states. In additional unreported results, we find that the measured exits
in the blue series do not show evidence of starting a new job via direct deposit of payroll from a new employer. We
therefore omit January 3 and January 10 from the plot in Figure 4.
38
Figure A-16: Effect of Expanded Benefits on Job-Finding: Interrupted Time-series
Design
Exit rate to new job from unemployment benefits
●
● ● ●
● ●
● ● ●
● ●
● ●
● ● ●
● ●
●
● ●
● ● ●
2% ● ● ●
●
● ●
●
● ●
● ●
● ●
● ● ● ● ●
●
●
●
1% Expiration of Onset of $300
$600 supplement supplement
Change: Change:
0.76 p.p. −0.59 p.p.
0%
Apr '20 Jun '20 Aug '20 Oct '20 Dec '20 Feb '21
Notes: This figure shows the exit rate to a new job in the JPMCI data from April 2020 through February 2021. The
red horizontal bars indicate the average exit rate in the two weeks prior to and four weeks following a change in the
supplement amount.
39
Figure A-17: Exit Rate by Replacement Rate
(a) Expiration – New Job (b) Onset – New Job
Exit rate to new job from unemployment benefits Exit rate to new job from unemployment benefits
2.5% $300 supplement
available
●
●
2.0% ●
●
● ●
3%
●
●
●
●
● ● ●
1.5% ● ●
● ● ●
●
● 2% ●
●
●
● ● ●
●
●
●
● ●
1.0% ●
●
●
●
1%
0.5%
Higher PctChange Higher PctChange
$600 supplement
● Lower PctChange ● Lower PctChange
available
0.0% 0%
Jun '20 Jul '20 Aug '20 Sep '20 Oct '20 Nov '20 Dec '20 Jan '21 Feb '21 Mar '21
(c) Expiration – Total (d) Onset – Total
Exit rate from unemployment benefits Exit rate from unemployment benefits
$300 supplement
available
●
6% 4%
● ● ●
●
●
● ●
● ●
● ●
● ●
● ● ● ● ● ●
●
●
● ●
●
● 3% ●
●
● ●
●
●
● ● ●
● ● ●
4% ● ● ● ●
●
●
●
●
2%
2%
1%
Higher PctChange Higher PctChange
$600 supplement
● Lower PctChange ● Lower PctChange
available
0% 0%
Jun '20 Jul '20 Aug '20 Sep '20 Oct '20 Nov '20 Dec '20 Nov '20 Dec '20 Jan '21 Feb '21 Mar '21
(e) Expiration – Recall (f) Onset – Recall
Exit rate to recall from unemployment benefits Exit rate to recall from unemployment benefits
5% ●
● $300 supplement
● Higher PctChange
available ●
● Lower PctChange
● ●
●
4% ● ●
● 0.8% ●
● ●
●
●
●
● ●
●
●
●
3% ●
●
●
●
●
0.5% ●
● ●
● ●
●
2% ●
● ●
● ●
●
● 0.2%
1% ● ●
●
● ●
● ● Higher PctChange
$600 supplement
● Lower PctChange
available
0% 0.0%
Jun '20 Jul '20 Aug '20 Sep '20 Oct '20 Nov '20 Dec '20 Nov '20 Dec '20 Jan '21 Feb '21 Mar '21
Notes: This figure shows several alternative specifications for Figure 6. Panels (a) and (b) report raw (unnormalized)
exit rates to new job. Panels (c) and (d) report “total” exit rates including exit to new job and exit to recall. Panels
(e) and (f) report exit rates to recall.
40
Figure A-18: Spending in Model that Accounts for Time-Aggregation
Notes: This figure shows the behavior of spending in the model more closely matches high-frequency data patterns after
accounting for time-aggregation issues.
Figure A-19: Job-Finding and Spending Responses to $300 Supplement: Models vs.
Data
Notes: This figure repeats Figure 9 but showing models vs. data in response to the $300 supplement. In all models
except the perfect foresight specification (including the standard model with pre-pandemic search costs), we assume the
start of the $300 supplements in January is a surprise. We assume this even in the pre-pandemic model since this is
the more natural baseline expectations assumption, as it is unlikely households anticipated the announcement of this
policy two months in advance.
41
Figure A-20: Model vs. Data Dose-Response Difference-in-Difference
Notes: This figure compares the dose-response difference-in-difference for the $600 expiration in our best fit model to
the empirical difference-in-difference.
42
Figure A-21: Patterns of Unemployment Insurance Receipt
Number of active spells
● ● ●
● ●
●
150,000 ● ●
●
●
● ●
●
● ●
●
●
●
● ●
●
●
●
●
●
100,000 ● ●
● ●
● ● ● ● ●
● ● ● ●
● ● ● ● ● ●
● ●
●
50,000
●
$600 supplement $300 supplement
●
● ● ● ● ● ● ● ● ● ● available available
0
Feb '20 Apr '20 Jun '20 Aug '20 Oct '20 Dec '20 Feb '21
Number of benefit recipients
30,000 Start
Exit to recall
Exit to new job
20,000
10,000
0
−10,000
Feb '20 Apr '20 Jun '20 Aug '20 Oct '20 Dec '20 Feb '21
Notes: The first panel of this figure reports the number of active unemployment spells by week in JPMCI data. The
second panel shows the number of households starting unemployment and leaving unemployment for new jobs and for
recall (i.e., returning to their former employer).
43
Figure A-22: Spending of Recalled vs. Non-Recalled Workers
Total Spending
10%
0%
Exit to new job $600 supplement
−10% available
Exit to recall
Jan '20 Feb '20 Mar '20 Apr '20 May '20 Jun '20 Jul '20 Aug '20
Notes: This figure shows total spending for two different groups of workers who are unemployed continuously from
April 2020 through August 2020 and exit unemployment in September 2020. The “Exit to recall” group returns to their
previous employer when they exit unemployment while the “Exit to new job” group exits to a new employer.
44
Figure A-23: Weekly Event Study Coefficients (Continuous Specification)
(a) Expiration of $600
Continuous treatment effect estimate (difference from June/July average)
0.03 ●
●
●
0.02
●
$600 supplement ● ●
0.01 available ● ●
●
●
●
0.00 ● ● ● ● ●
●
−0.01
Jun '20 Jul '20 Aug '20 Sep '20 Oct '20
(b) Onset of $300
Continuous treatment effect estimate (difference from November/December average)
0.02
$300 supplement
available
●
●
0.00 ●
● ●
●
●
●
●
−0.02 ●
● ●
●
● ●
●
●
Nov '20 Dec '20 Jan '21 Feb '21 Mar '21
Notes: This figure shows the results from the weekly difference-in-difference specification defined in Section C.5.1
equation (C1). This specification captures the effect of supplements on job-finding in each week around the supplement
change. Panel (b) indicates that even prior to the onset of the $300 supplement there is already a gradual trend
downward in the job-finding rate for households that receive the largest increase in benefits on January 1, 2021. If we
were to use a specification that accounted for this pre-trend in estimation we would likely find that the $300 supplement
has even smaller effects on the job-finding rate.
45
Figure A-24: Exit Rates Around Expiration of Multiple Programs in September 2021
(a) Raw Exit Rate
Exit rate from unemployment benefits
50
●
40
30
●
●
20 ●
●
$300 supplement ●
10 ● ●
●
available ●
● ●
● ● ● ● ●
●
0
Aug'21 Sep'21 Oct'21 Nov'21
(b) Cleaned Exit Rate by Benefit Level
Exit rate to new job relative to July/August group average
400%
300%
200%
100% Lower PctChange
Higher PctChange
$300 supplement
available
0%
Aug '21 Sep '21 Oct '21 Nov '21
Notes: The top panel of this figure shows the raw exit rate from UI benefits. The surge in exits is caused by the
expiration of multiple programs (see Appendix A.1 for details). The bottom panel of this figure replicates Figure 6 for
the expiration of the $300 supplement in September 2021, for the subset of workers with short observed duration.
46
Figure A-25: Effect of Expanded Benefits: Binscatter (Summer 2021)
Change in average exit rate to new job
●
0.05
0.04
●
●
0.03 ●
● ● ●
●
0.02 ●
●
Slope:−0.024
Standard error: 0.009
0.01
Larger decrease Smaller decrease
in benefits in benefits
−120% −100% −80% −60% −40%
Change in benefits
Notes: This figure replicates Figure 7 for the expiration of the $300 supplement in September 2021.
Figure A-26: Income: Model vs. Data
Notes: This figure shows income of unemployed (relative to employed) households in the model and data for unemployed
workers receiving benefits immediately in April 2020 as well as those who face a delay in benefit receipt until June 2020.
47
Figure A-27: Job-Finding Rates with and without $600 supplements
Notes: This figure shows the job-finding rate in the best-fit model with a $600 supplement compared to a counterfactual
job-finding rate had there been no supplement. This shows that liquidity accumulation caused by the supplement
slightly lowers the job finding rate even after the supplement expires.
48
Figure A-28: Model With Multiple Types and Perfect Foresight
(a) Job Finding - Average (b) Spending - Average
(c) Job Finding - By Type (d) Spending - By Type
(e) Shares of Each Type By Month
Notes: This figure shows job-finding and spending behavior in a model with perfect foresight and heterogeneity in both
discounting and job-search costs. Panels (a) and (b) show behavior averaging across all types, panels (c) and (d) show
the behavior of each of the three types, and panel (e) shows the share of each type in each month. See Section E.2 for
details.
49
Table A-1: Monthly Income and Spending in Employed and Unemployed Households
Spending
Group (months) Income Benefits Card Total Account
and cash balance
Mean
Employed (Jan-Feb 2020) $6850 $0 $2470 $4669 $5262
Employed (Apr-Oct 2020) $6839 $0 $2322 $4538 $5884
Pandemic unemployed (Jan-Feb 2020) $5854 $16 $2506 $4248 $3488
Pandemic unemployed (Apr-Oct 2020) $7036 $3947 $2780 $4638 $5249
Median
Employed (Jan-Feb 2020) $5353 $0 $2064 $3834 $2815
Employed (Apr-Oct 2020) $5466 $0 $1925 $3739 $3389
Pandemic unemployed (Jan-Feb 2020) $4549 $0 $2109 $3495 $1624
Pandemic unemployed (Apr-Oct 2020) $5784 $3834 $2477 $4044 $3242
Notes: This table shows monthly values of income, unemployment benefits, spending (card and cash), spending (total),
and checking account balances for employed and unemployed households, before and during the start of pandemic.
“Employed” households do not receive benefits or have a job separation from January 2020 through February 2021.
“Pandemic unemployed” households begin an unemployment spell in April 2020. A very small number of these house-
holds also received benefits in a separate spell which ended prior to April 2020 in January and February 2020, which is
why the pre-pandemic mean benefits for this group is $16.
50
Table A-2: Regression Estimates for Effect of Expanded Benefits on Job-Finding
Dependent variable:
Exit to new job
Expiration of $600 Onset of $300
(1) (2)
PctChange 0.021∗∗∗ 0.022∗∗∗
(0.001) (0.001)
SuppAvail 0.003∗∗∗ 0.008∗∗∗
(0.001) (0.001)
PctChange:SuppAvail −0.016∗∗∗ −0.020∗∗∗
(0.001) (0.001)
Constant 0.002∗∗∗ 0.009∗∗∗
(0.001) (0.001)
Observations 2,120,887 1,790,138
Number of Households 183,144 131,464
Notes: This table estimates the difference-in-difference model eit = γP ctChangei + αSuppAvailt + βSuppAvailt ×
P ctChangei + εit from equation (4) using a window of eight weeks prior to and eight weeks after the two policy changes
(expiration of the $600 supplement and onset of the $300 supplement). For expiration, the supplement available period
is June and July 2020 and the no-supplement period is August and September 2020. For onset, the supplement available
period is January 15-March 15 2021 and the no-supplement period is November and December 2020. Standard errors
are clustered at the household level. ∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01.
51
Table A-3: Model Parameters
(a) Parameters Used in All Models
Parameter Parameter Value Target
Preferences r Interest Rate 0.04 (annual)
γ Relative Risk Aversion 2
Income π Separation Rate 0.028 Converted from Quarterly CPS
transition rates in Krueger, Mitman
and Perri (2016)
Wage Quintiles 0.8154 HH Income by Replacement Rate Bins
0.9077
1
1.1080
1.2161
h Secondary Income 0.56 h=HH income U / HH income E when
not receiving UI
Expected Recall Rate 0.08 Monthly Recall Rate 2019
Benefit Regular Benefit Max Length 6 months
Rules
b Regular Benefit Replacement 0.21 h+b = HH income U / HH income E
Rate when receiving UI
m UI Supplement 0.345 h+b+m = HH income U/ HH income
E when receiving UI supplements
(b) Model Specific Choices
Model Expectations Monthly Discount Factor Search Parameters Search Target
β Target
k0 ϕ k1
Pre- Anticipated 0.9905 Quarterly MPC 19.2 3.2 0 Duration Elasticity
Pandemic Supplement from $500 check = = 0.5 & No supp JF
Expiration 0.25 Rate = 0.28 monthly
Pandemic Anticipated 0.9905 Quarterly MPC 20.8 0.50 -0.63 Pandemic Job Find
Supplement from $500 check = Time-Series
Expiration 0.25
Pandemic Surprise 0.9905 Quarterly MPC 120.5 1.6 -0.33 Pandemic Job Find
Supplement from $500 check = Time-Series
Expiration 0.25
Pandemic Surprise 0.9811 UI Waiting Design 56.1 1.22 -0.40 Pandemic Job Find
Supplement MPC = 0.42 Time-Series
Expiration
Notes: This table summarizes model parameters. See Section D.2 for details
52
Table A-4: Disincentive by Liquidity – Expiration of $600
Dependent variable:
Base Control for liquidity Triple difference
(1) (2) (3)
PctChange 0.0212∗∗∗ 0.0216∗∗∗ 0.0214∗∗∗
(0.0010) (0.0010) (0.0010)
SuppAvail 0.0034∗∗∗ 0.0034∗∗∗ 0.0032∗∗∗
(0.0010) (0.0010) (0.0010)
Std Balance 0.0006∗∗∗ 0.0024∗∗∗
(0.0001) (0.0008)
PctChange*SuppAvail −0.0163∗∗∗ −0.0163∗∗∗ −0.0160∗∗∗
(0.0011) (0.0011) (0.0011)
SuppAvail*Std Balance −0.0018∗
(0.0010)
PctChange*Std Balance −0.0023∗∗
(0.0010)
PctChange*SuppAvail*Std Balance 0.0025∗∗
(0.0012)
Constant 0.0025∗∗∗ 0.0021∗∗∗ 0.0023∗∗∗
(0.0008) (0.0008) (0.0008)
PctChange*SuppAvail if balance 1 sd above mean -0.0135
PctChange*SuppAvail if balance 1 sd below mean -0.0185
Observations 2,120,802 2,120,802 2,120,802
Number of Households 183,138 183,138 183,138
Note: “Std Balance” measures liquidity using checking account balance at the end of March 2020. Balances are
winsorized at the 90th percentile and then standardized to have mean 0 and standard deviation 1. By measuring
liquidity in March, we capture liquidity before the household has received any supplement payments. See Section 5.3.1
for additional discussion. Standard errors are clustered at the household level. ∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01.
53
Table A-5: Disincentive by Liquidity – Onset of $300
Dependent variable:
Base Control for liquidity Triple difference
(1) (2) (3)
PctChange 0.0220∗∗∗ 0.0220∗∗∗ 0.0215∗∗∗
(0.0010) (0.0010) (0.0010)
SuppAvail 0.0077∗∗∗ 0.0077∗∗∗ 0.0075∗∗∗
(0.0008) (0.0008) (0.0008)
Std Balance −0.0001 0.0027∗∗∗
(0.0001) (0.0005)
PctChange*SuppAvail −0.0204∗∗∗ −0.0204∗∗∗ −0.0200∗∗∗
(0.0013) (0.0013) (0.0013)
SuppAvail*Std Balance −0.0003
(0.0008)
PctChange*Std Balance −0.0054∗∗∗
(0.0010)
PctChange*SuppAvail*Std Balance 0.0014
(0.0013)
Constant 0.0091∗∗∗ 0.0091∗∗∗ 0.0093∗∗∗
(0.0006) (0.0006) (0.0006)
PctChange*SuppAvail if balance 1 sd above mean -0.0186
PctChange*SuppAvail if balance 1 sd below mean -0.0214
Observations 1,789,831 1,789,831 1,789,831
Number of Households 131,444 131,444 131,444
Note: “Std Balance” measures liquidity using checking account balance at the end of October 2020. Balances are
winsorized at the 90th percentile and then standardized to have mean 0 and standard deviation 1. By measuring
liquidity in October, we capture liquidity before the household has received any supplement payments. See Section
5.3.1 for additional discussion. Standard errors are clustered at the household level. ∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01.
54
Table A-6: MPC by Spending Category
UI onset (waiting) FPUC expiration
MPC MPC Share Pre-Pandemic MPC MPC Share Pre-Pandemic
Spend Share Spend Share
Auto Repair 0.006 0.036 0.025 0.003 0.029 0.027
Clothing 0.007 0.041 0.020 0.008 0.075 0.026
Department Stores 0.002 0.009 0.005 0.002 0.018 0.007
Discount Stores 0.012 0.071 0.056 0.008 0.072 0.050
Drug Stores 0.002 0.011 0.017 0.001 0.013 0.013
Entertainment 0.003 0.020 0.025 0.001 0.013 0.025
Flights 0.002 0.009 0.003 0.000 0.002 0.003
Groceries 0.040 0.228 0.217 0.020 0.184 0.187
Healthcare 0.003 0.018 0.020 0.004 0.033 0.024
Home Improvement 0.020 0.116 0.063 0.008 0.079 0.050
Hotels & Rental Cars 0.003 0.015 0.019 0.001 0.010 0.027
Insurance 0.004 0.020 0.032 0.003 0.025 0.027
Orgs & Institutions 0.004 0.020 0.025 0.002 0.017 0.025
Other Retail 0.030 0.170 0.104 0.018 0.171 0.103
Prof & Personal Services 0.009 0.048 0.047 0.005 0.048 0.047
Restaurants 0.017 0.094 0.097 0.010 0.093 0.124
Schools 0.000 0.001 0.002 0.001 0.006 0.008
Telecom 0.005 0.029 0.074 0.003 0.032 0.062
Transport 0.005 0.027 0.052 0.002 0.020 0.065
Utilities 0.003 0.016 0.096 0.006 0.060 0.099
$300 onset $300 expiration
MPC MPC Share Pre-Pandemic MPC MPC Share Pre-Pandemic
Spend Share Spend Share
Auto Repair 0.001 0.005 0.027 0.002 0.016 0.025
Clothing 0.006 0.053 0.025 0.006 0.050 0.030
Department Stores 0.002 0.017 0.009 0.001 0.009 0.010
Discount Stores 0.009 0.083 0.051 0.008 0.065 0.049
Drug Stores 0.002 0.019 0.013 0.001 0.006 0.012
Entertainment 0.002 0.020 0.026 0.004 0.037 0.030
Flights 0.000 0.000 0.004 0.002 0.020 0.009
Groceries 0.023 0.211 0.185 0.017 0.147 0.161
Healthcare 0.002 0.018 0.028 0.003 0.026 0.026
Home Improvement 0.003 0.031 0.044 0.005 0.043 0.040
Hotels & Rental Cars 0.000 0.004 0.026 0.007 0.065 0.037
Insurance 0.001 0.012 0.027 0.001 0.009 0.025
Orgs & Institutions 0.003 0.029 0.025 0.003 0.023 0.023
Other Retail 0.032 0.292 0.108 0.016 0.139 0.100
Prof & Personal Services 0.006 0.056 0.047 0.007 0.061 0.049
Restaurants 0.013 0.115 0.120 0.020 0.170 0.139
Schools -0.001 -0.008 0.008 0.001 0.009 0.005
Telecom 0.003 0.025 0.066 0.002 0.018 0.058
Transport -0.000 -0.002 0.062 0.005 0.046 0.082
Utilities 0.002 0.022 0.099 0.005 0.040 0.090
Notes: This table computes MPCs by spending category for the subset of spending transactions we can assign to granular
categories based on merchant category codes (for card transactions) and text descriptions (for electronic transactions).
MPC share corresponds to the ratio of the category-specific MPC to the MPC for all categorized spending. Pre-pandemic
spending share calculates the spending share on a given category using spending of unemployed households in the same
calendar months in 2019.
55
Table A-7: Marginal Propensity to Repay Debt
UI onset (waiting) FPUC expiration $300 onset $300 expiration
Auto Loans 0.003 0.001 0.002 0.003
(0.001) (0.001) (0.001) (0.001)
Mortgages 0.000 0.004 -0.004 0.008
(0.002) (0.002) (0.003) (0.002)
Student Loans 0.000 0.000 -0.001 0.000
(0.001) (0.000) (0.000) (0.000)
Notes: This table computes marginal propensities to repay debt by debt category. Debt payments are categorized using
text descriptions from electronic payments. Standard errors are clustered by household.
Table A-8: MPC Robustness to Additional Controls
Research Design Total Spending MPC
Waiting for benefit 0.42 0.40 0.40 0.41
(0.01) (0.02) (0.02) (0.02)
Expiration of $600 supplement 0.31 0.30 0.30 0.30
(0.01) (0.01) (0.01) (0.01)
Onset of $300 supplement 0.28 0.28 0.28 0.27
(0.01) (0.01) (0.01) (0.02)
Expiration of $300 supplement (June states) 0.35 0.35 0.35 0.35
(0.02) (0.03) (0.03) (0.04)
Expiration of $300 supplement (September states) 0.27 0.26 0.27 0.30
(0.01) (0.02) (0.02) (0.02)
State∗SuppAvail FE X X X
Age∗SuppAvail FE X X
HasKids∗SuppAvail FE X
Notes: This table re-computes MPC results with additional controls: state, age of the primary account holder, and the
presence of children. We do not report results for the June vs. Sept states research design, since these regressions are
not identified when including state fixed effects. See Appendix B.3 for additional details. Standard errors are clustered
by household.
Table A-9: MPC Robustness to Summary Statistic and Sample
Episode (1) (2) (3) (4)
Waiting for benefits 0.42 0.48 0.45 0.41
Expiration of $600 supplement 0.31 0.38 0.34 0.28
Onset of 8-month $300 supplement 0.28 0.31 0.30 0.26
Summary Statistic Mean Median Mean Mean
Sample All All No non-Chase credit card Make ACH debt payments
Notes: This table re-computes our MPC results for a number of alternative samples. The rows compute MPCs to the
three identification strategies shown in the main text. Column 1 repeats the main specification from Table 1. Column
2 computes MPCs using median instead of mean spending. Column 3 excludes households who make debt payments
to non-Chase credit cards (for whom we are potentially missing some spending). Column 4 restricts to households who
make debt payments via ACH (whom we are more confident are not making mis-classified debt payments via paper
check). See Appendix B.3 for additional details.
56
Table A-10: MPC Robustness to Spending Measure
Spend Total Spend card and cash
Episode MPC Elasticity MPC Elasticity
Waiting for benefits 0.42 0.57 0.31 0.72
Expiration of $600 supplement 0.31 0.42 0.21 0.48
Onset of 8-month $300 supplement 0.28 0.38 0.20 0.45
Lost Wages Assistance 0.31 0.42 0.21 0.48
Notes: This table shows the robustness of our MPC results to the measure of spending. The first columns show MPCs
and elasticities for spending (total), which is our preferred specification. The third and fourth columns recompute MPCs
and elasticities for spending (card and cash) instead of spending (total).
57
Table A-11: Effect of Expanded Benefits: Robustness to Controls
(a) Expiration of $600
Dependent variable:
Exit to New Job
(1) (2) (3) (4)
PctChange*SuppAvail −0.0163∗∗∗ −0.0133∗∗∗ −0.0139∗∗∗ −0.0141∗∗∗
(0.0011) (0.0012) (0.0013) (0.0023)
PctChange X X X X
SuppAvail X X X X
State*SuppAvail FE X X X
Age*SuppAvail FE X X
Industry*SuppAvail FE X
Observations 2,120,887 2,120,887 1,886,942 519,245
Number of Households 183,144 183,144 163,930 44,165
(b) Onset of $300
Dependent variable:
Exit to New Job
(1) (2) (3) (4)
PctChange*SuppAvail −0.0204∗∗∗ −0.0178∗∗∗ −0.0199∗∗∗ −0.0207∗∗∗
(0.0013) (0.0013) (0.0014) (0.0026)
PctChange X X X X
SuppAvail X X X X
State*SuppAvail FE X X X
Age*SuppAvail FE X X
Industry*SuppAvail FE X
Observations 1,790,138 1,790,138 1,604,130 454,135
Number of Households 131,464 131,464 116,276 32,689
Notes: This table reports estimates of β̂ from equation (4), adding increasingly stringent control variables. The first
column is the same as in Table A-2. Column (2) adds state by time fixed effects. Column (3) adds age bin by time fixed
effects. Column (4) adds prior industry by time fixed effects. Prior industry is available only for workers who worked
at the 1,000 largest firms in the data and therefore uses a smaller sample than the other columns. Standard errors are
clustered at the household level. ∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01.
Table A-12: Effect of Expanded Benefits: Alternative Functional Forms
Functional Form Aggregation Hazard Elasticity Duration Elasticity
$600 Expiration $300 Onset $600 Expiration $300 Onset
Baseline: Absolute pp Worker-level 0.19 0.27 0.11 0.22
Relative Percent Change Benefit change deciles 0.16 0.33 0.09 0.27
Logit Worker-level 0.16 0.23 0.09 0.19
Notes: This table explores alternative functional forms for estimating job-finding effects. See Section C.5.1 for details.
58
Table A-13: Effect of Expanded Benefits: Alternative Measures of Exit
(a) Expiration of $600
Dependent variable:
New job Recall Total
(1) (2) (3)
SuppAvail*PctChange −0.0163∗∗∗ −0.0125∗∗∗ −0.0288∗∗∗
(0.0011) (0.0013) (0.0017)
Observations 2,120,887 2,120,887 2,120,887
Number of Households 183,144 183,144 183,144
(b) Onset of $300
Dependent variable:
New job Recall Total
(1) (2) (3)
SuppAvail*PctChange −0.0204∗∗∗ −0.0031∗∗∗ −0.0234∗∗∗
(0.0013) (0.0008) (0.0015)
Observations 1,790,138 1,790,138 1,790,138
Number of Households 131,464 131,464 131,464
Notes: This table reports estimates of β̂ from equation (4) specified for four different outcome variables. The first
column is the same as in Table A-2. Column (2) is exit to recall and column (3) is total exit (new job or recall).
Standard errors are clustered at the household level. ∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01.
Table A-14: Effect of Expanded Benefits: Summer 2021
Dependent variable:
Exit to New Job
Max Observed Weeks Starting from 11 July 2021
4 weeks 4 weeks 8 weeks 8 weeks
PctChange*SuppAvail −0.0171∗ −0.0244∗∗∗ −0.0137 −0.0305∗∗∗
(0.0098) (0.0091) (0.0090) (0.0087)
Donut Excluded Yes No Yes No
Observations 48,376 55,132 69,346 78,591
Number of Households 5,513 5,532 7,638 7,665
Notes: This table estimates the difference-in-difference model from equation (4) using a window of eight weeks prior to
and eight weeks after the September expiration of the $300 supplement. The supplement available period is July 11,
2021 to September 4, 2021 and the no-supplement period is from September 5, 2021 to 7 November 7, 2021. Columns
(1) and (3) exclude the “donut” period September 5 through 24. Standard errors are clustered at the household level.
∗ p<0.1; ∗∗ p<0.05; ∗∗∗ p<0.01.
59
Table A-15: Interpreting MPC Differences Between Waiting for Benefits and $500
Stimulus
MPC
Nature of transfer Who receives Calibration Environment Horizon Model Data
(1) $2400 Persistent+Reg UI Unemp no UI Waiting Pandemic Month 0.42 0.42
(2) $2400 Persistent Unemp w/ reg UI Waiting Pandemic Month 0.29
(3) $2400 Persistent Unemp w/ reg UI Waiting Normal Month 0.45
(4) $2400 One Time Unemp w/ reg UI Waiting Normal Month 0.29
(5) $500 One Time Unemp w/ reg UI Waiting Normal Month 0.45
(6) $500 One Time Everyone Waiting Normal Month 0.21
(7) $500 One Time Everyone $500 Normal Month 0.09
(8) $500 One Time Everyone $500 Normal Quarter 0.25 0.25
Notes: This table compares MPCs across various model specifications and shows empirical counterparts, where available.
The “Nature of transfer” column shows the particular transfer for which we compute an MPC. The $2,400 monthly
transfer corresponds to $600 weekly supplements while $500 transfers correspond to past stimulus checks. “Who receives”
shows which households are receiving that transfer. “Calibration” shows the target calibration used in that model.
Models either target the MPC from the waiting design or target a 0.25 quarterly MPC out of $500 stimulus checks sent
to everyone. “Environment” is either a pre-pandemic environment which includes discount factor shocks and stimulus
checks or a normal environment which does not. MPCs are calculated primarily at the monthly horizon but we show also
a quarterly result for stimulus checks to everyone to ease comparison with empirical estimates. Note that even though
we show effects one element at a time, these interactions are non-linear and so this is not an additive decomposition.
60
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