Better Late than Never? Quantifying Funding and Liquidity Effects of the PPP on Pandemic-Era Employment Recovery (April 8, 2026)
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This paper, dated April 8, 2026, by Olga Gorbachev, Maria Luengo-Prado and J. Christina Wang examines how the Paycheck Protection Program (PPP) supported employment during the COVID-19 period, distinguishing between its short-term liquidity and broader funding effects. Using county-level data, the authors show that delays in loan disbursement had prolonged negative impacts only on the smallest urban businesses. Instrumental-variable and firm-level results reveal that PPP funding improved business survival and employment recovery substantially and broadly, with an estimated cost of roughly $89,000 per job-year. Gorbachev and Luengo-Prado are listed with the University of Delaware and Wang with the Federal Reserve Bank of Boston.
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“Better Late than Never? Quantifying Funding and Liquidity Effects of the PPP on Pandemic-Era Employment Recovery (April 8, 2026).”
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Better Late than Never? Quantifying Funding and
Liquidity Effects of the PPP on Pandemic-Era
Employment Recovery*
Olga Gorbachev Maria Luengo-Prado
University of Delaware ICAE
J. Christina Wang
Federal Reserve Bank of Boston
April 8, 2026
Abstract
This paper examines how the Paycheck Protection Program (PPP) supported
employment during the COVID-19 period by distinguishing between its short-
term liquidity and broader funding effects. Using county-level data, we show that
delays in loan disbursement had prolonged negative impacts only on the smallest
urban businesses. To identify the causal impact of funding itself, we develop
an instrument based on the pre-pandemic payroll share in small establishments.
Instrumental-variable and firm-level analyses reveal that PPP funding improved
business survival and employment recovery substantially and broadly, with an
estimated cost of roughly $89,000 per job-year, consistent with other large-scale
fiscal interventions.
Keywords: COVID-19, Paycheck Protection Program, CARES Act, small busi-
ness credit, employment.
JEL Codes: J21, H81, G28.
* We thank Rachel Cummings and Kelly Jackson for excellent research assistance, and Daniel Cooper
and three anonymous referees for helpful comments. The views expressed here are solely those of the
authors and do not reflect the opinions of the Federal Reserve Bank of Boston, or the Federal Reserve
System. All errors are our own. Declarations of interest: none. Contact: olgag@udel.edu.
1 Introduction
As the COVID-19 pandemic swept through US coastal cities in March 2020, Congress
passed the Coronavirus Aid, Relief, and Economic Security (CARES) Act, dispens-
ing broad-based fiscal assistance on an unprecedented scale. A key component of this
package was the Paycheck Protection Program (PPP), which provided loans that were
effectively grants to most small businesses whose operations were disrupted by the
pandemic.1 One of the primary goals of the PPP was to help small businesses retain
workers despite having to reduce operations or shut down completely. Using primarily
county-level data, we examine the mechanisms through which the PPP influenced em-
ployment retention and recovery, distinguishing between its short-term liquidity effect
linked to the timing of a loan and its broader funding receipt effect tied to receiving
a loan. A key contribution of our study is to isolate and compare these two effects,
thereby enhancing the understanding of how different features of the PPP influenced
its efficacy. This can help inform the design of government support programs if similar
needs arise in the future.
The short-term liquidity effect of PPP stems from differences in the timing of loan
disbursement to recipients. Timely funding may have allowed firms to bridge tempo-
rary cash-flow shortfalls, helping them retain workers during the initial weeks of the
crisis. The broader funding receipt effect goes beyond the immediate liquidity relief and
captures the longer-term impact of capitalization provided by a government transfer.
These mechanisms are conceptually distinct but empirically intertwined.2 To isolate
the liquidity effect, we exploit variation in loan timing across recipients. We then es-
timate the funding effect using an instrumental-variable approach, where PPP receipt
is instrumented by pre-COVID payroll shares of small firms, while controlling for loan
timing. Our results show that delays in funding, which isolate the short-term impact
due to liquidity constraints, were especially harmful for the smallest urban businesses,
1
In the rest of the article, “small” refers to businesses with fewer than 500 employees, and “smallest”
refers to businesses with fewer than 20 employees.
2
We thank the referees for highlighting these subtleties.
1
while the receipt of PPP funds substantially improved business survival and employ-
ment recovery more broadly across businesses.
From the early days of PPP, researchers have examined the effectiveness of the
program in supporting small business operations and local economies, as well as its
efficiency in funding allocation.3 As an early study, Hubbard and Strain (2020) use
Dun & Bradstreet data to compare firms that applied for loans with those that did
not (without observing actual receipt). They found that eligible firms, those under
500 employees, were less likely to close and recovered more quickly in employment
and payment behavior than slightly larger, ineligible firms. Granja et al. (2022) use
Homebase microdata and a supply-side instrument based on preexisting small business
bank relationships, which captures distortions in access to financing during the early
months of the PPP. They show that greater local access to PPP funds significantly
reduced missed payments and increased the share of firms with at least three months
of cash reserves at the state-industry level, highlighting the program’s direct impact on
firm liquidity. Kurmann, Lalé, and Ta (2025), also using Homebase data at the firm
level, further underscore the importance of timely liquidity support.
Our analysis complements and extends these studies in three key ways. First, we
distinguish between two conceptually distinct but empirically related effects of the PPP:
a short-term liquidity effect and the broader impact of receiving funds. Second, unlike
previous studies that focus primarily on firm-level outcomes over a short horizon, we
examine these effects across firm sizes and geographic areas over a two-year horizon,
capturing both longer-term impacts and potential local spillovers. Third, we exploit
demand-side variation in area-level PPP take-up to identify these effects, complement-
ing supply-side studies such as Granja et al. (2022) and short-term timing analysis such
as Doniger and Kay (2023).
To capture the short-term liquidity effect, we follow Doniger and Kay (2023) (here-
after DK), who exploit a 10-day pause in PPP funding triggered by the exhaustion of
3
In addition to the studies explicitly cited in this section, a partial list of additional important or
closely related studies includes Autor et al. (2022c) (which contains a more complete review of the
literature), Dalton (2023), Faulkender, Jackman, and Miran (2023) and Chetty et al. (2024).
2
the initial appropriation. This pause provides plausibly exogenous variation in loan
timing, allowing DK to estimate the causal effect of a funding delay on local employ-
ment. They find that the adverse consequences of the funding delay were concentrated
among the self-employed and the smallest firms. Intriguingly, these effects persisted
throughout 2020, even after the economy began reopening in May and despite the fact
that $145 billion of the $670 billion allocated for the 2020 PPP remained unused when
the program closed on August 8, 2020. To understand the persistent effects of a brief
funding delay, we first analyze the determinants of the PPP delay à la DK, referred
to as the “share delayed” in all subsequent analysis. We find that the share delayed
correlates with preexisting county-level banking conditions (namely, the presence of
community versus large national banks and the prevalence of small-business lending).4
These correlations indicate that the share delayed is partly endogenous, reflecting local
financial infrastructure and lending capacity constraints. Counties with higher demand
for loans, combined with these institutional constraints, experienced a larger proportion
of delayed loans. As a result, when employment is measured in levels, the estimated
coefficient of share delayed appears significantly negative, largely reflecting the impact
in large counties with the largest delays.
Using county-level monthly employment data from the Quarterly Census of Em-
ployment and Wages (QCEW), we confirm that the share delayed correlates negatively
with total private employment through January 2021 in the full sample of US coun-
ties when the employment outcome is specified in levels. However, once the outcome
is specified in logarithms, normalized by population, or (normalized) changes, as is
commonly done in policy evaluation studies using state- or county-level data to avoid
undue influence of the largest states or counties (see, e.g., Chodorow-Reich et al. 2012),
the coefficients on the share delayed lose their significance. In some cases, they even
change signs. As a further test, we estimate the specification in levels separately for
urban versus rural counties. This exercise reveals that the statistical significance of the
4
Granja et al. (2022), Balyuk, Prabhala, and Puri (2020), and Li and Strahan (2021) also find that
firms with preexisting bank ties received better access to PPP loans early on.
3
negative association between the share delayed and the level of employment is driven
by urban counties. These results align with the proposed mechanism, indicating that
unobserved vulnerability factors in urban communities during COVID-19 led to both
higher shares of loans delayed and greater declines in employment levels.
Nevertheless, the share delayed likely contains an exogenous component that cap-
tures a genuine short-term liquidity shock. This component should be most strongly
associated with employment outcomes among firms for which timely access to liquid-
ity was critical, particularly the smallest businesses. For these firms, which typically
operate with thin cash buffers and weaker banking relationships, even brief cash flow
shortfalls could be especially damaging. Using Quarterly Workforce Indicators (QWI)
data on stable employment by firm size (since QCEW measures employment by size only
annually), we find that the share delayed had a prolonged negative impact specifically
on employment in urban establishments with fewer than 20 employees (the smallest size
category in the QWI).5 This finding is consistent with Kurmann, Lalé, and Ta (2025),
who document that PPP share delayed imposed significant costs on the smallest firms,
contributing to higher rates of business closures.
Having examined the cross-sectional properties of the effect of share delayed, the
second part of our paper focuses on estimating the funding effect of PPP. To do so, we
construct an instrumental variable (IV) to address endogeneity concerns: the amount
of PPP funds received may be endogenous because small businesses most likely consider
both the degree of pandemic-induced disruptions and their future prospects in deciding
whether and when to apply for loans. Our IV is inspired by Chodorow-Reich et al.
(2012), who use pre-recession Medicaid spending to instrument fiscal transfers delivered
through the Medicaid reimbursement process during the Great Recession. Analogously,
we exploit the exogenously imposed eligibility threshold of the PPP, limiting access to
firms with fewer than 500 employees, to construct a county-level instrument based on
the 2019 payroll share in small establishments. Counties with a higher concentration
5
QWI stable employment tallies the number of jobs held on both the first and the last day of each
quarter with the same employer.
4
of payroll in small establishments were positioned to receive relatively more PPP funds
per dollar of payroll, mechanically generating cross-county variation in potential PPP
exposure. When analyzing employment in the smallest establishments (fewer than 20
employees), we refine the instrument to reflect their specific payroll share, excluding
self-employed recipients not captured in the QCEW or QWI data. Since many rural
counties lack large establishments and the share delayed affects only urban counties,
our analysis focuses on urban areas where both program exposure and employment
measurement are more reliable, allowing us to compare the magnitude of the two effects.
The instrument demonstrates a strong first stage: counties with higher small-
establishment payroll shares received significantly more PPP funding relative to payroll.
Its validity rests on the exclusion restriction, namely that local employment changes
were affected by the small-establishment payroll share solely through its effect on PPP
receipt. We mitigate potential violations by expressing outcomes in changes and includ-
ing a rich set of controls, such as local banking structure, industry mix, demograph-
ics, and COVID-19 exposure, allowing each to have time-varying effects. Moreover,
placebo tests using pre-pandemic data confirm that the instrument was uncorrelated
with changes in employment to population prior to 2020, supporting the exclusion
restriction. Together, these results indicate that our instrument captures plausibly ex-
ogenous variation in PPP funding intensity, enabling a credible identification of the
program’s employment effects.
We find that counties receiving greater PPP funding relative to their pre-COVID
payroll experienced significantly stronger employment recovery. Based on our estimates,
PPP receipt preserved approximately 5.85 million job-years in the urban counties in
our sample during the study period. About 53 percent of these job-years were real-
ized in 2020 and the remainder in 2021, corresponding to 2.9 and 2.5 percent of 2019
employment in these counties, respectively. We also calculate an implied cost per job-
year (the cost of sustaining one job for a year) of $88,997, assuming PPP preserved
employment through the end of 2021. These estimates are broadly consistent with
5
prior studies, which generally report costs between $100,000 and $250,000. The lower
cost in our analysis likely reflects the longer time horizon and/or spillover effects not
captured in firm-level analysis. Whereas previous studies measure employment impacts
only through 2020, mainly capturing short-term effects, our extension through the end
of 2021 allows employment gains to accumulate and persist, spreading program cost
over a longer period of time. Moreover, our use of county data naturally incorporates
spillovers from PPP recipients to the broader local economy.
Finally, we use Advan firm-level data to more precisely isolate the effect of loan
receipt from loan timing. Specifically, to measure the funding effect of PPP receipt, we
study differences in business foot traffic between PPP recipients and closely matched
(by industry, pre-pandemic visits, and geography) peer firms that did not receive PPP
funds. We match firms based on geographic proximity to ensure that peers faced similar
local conditions but exclude a “donut” zone around each PPP firm to reduce potential
bias from competition dynamics among closely located firms. Our baseline defines
peers as firms with similar pre-pandemic visits, in the same 6-digit NAICS code and
county, but outside the PPP firm’s Census block group, located 5 to 50 miles from the
PPP firm.6 In addition, we compare average treatment effects for late borrowers (those
receiving loans just after the 10-day pause) and early borrowers (those receiving loans
just before the 10-day pause). Applying either a difference-in-differences estimator or
a staggered treatment estimator à la Sun and Abraham (2021), we find that both early
and late borrowers benefited significantly from receiving PPP loans. Compared to their
matched non-recipient peers, both groups of borrowers experienced a notable increase
in visits and significantly fewer closures beginning in the second half of 2020. However,
the difference in the treatment effect between early and late borrowers is small (about
one-third of the funding effect) and statistically insignificant. This suggests that the
funding effect was more important than the liquidity effect, even for most of the firms
in the Advan sample, which tend to be small.
The remainder of the paper is organized as follows. Section 2 describes our method-
6
Results are robust to alternative distance thresholds.
6
ology and the data sources. Section 3 examines the determinants of the share delayed.
Section 4 presents our empirical findings on how the timing of PPP loans (the short-
term liquidity effect) affected local employment recovery. In Section 5, we use two
methods to estimate the effect of PPP funding and compare it with the effect of liquid-
ity due to loan timing: an instrumental variable approach using county-level QCEW
and QWI data, and a closest neighbor matching estimator using firm-level activity data.
Section 6 discusses potential implications for policy and concludes.
2 Empirical Design and Data
2.1 Empirical Design
To investigate the impact of PPP funding on the local economy, we adopt the following
empirical specification:
T
Yous, = bls + T+ S- [6:Policy, , + Xe,s + mYc,s,2019:M12| + East, (1)
t#2020:M1
where Y,.,4 is the measure of local employment of interest in area c (county or CBSA
depending on the specification) of state s at time t (month-year or quarter-year de-
pending on the data source). Our analysis covers 2020 and 2021. Yq. 2019:a12 is a
lag of the dependent variable, measured in 2019:M12 (or 2019:Q4 for QWI quarterly
data), to control for possible preexisting heterogeneity. X,,, denotes a set of area-level
controls, while wz, and 7 are state- and time-fixed effects, respectively. Policy, , refers
to the PPP program, whose effect on employment is the key object of interest. Note
that our regressors [Policy,.., Xc,s, Ye,s,2019: miz| are allowed to influence the outcome
Y.s2 dynamically (that is, differently in each period), with the coefficients [6;, 72, 7]
summarizing their respective dynamic effects.
To receive PPP funds, businesses had to apply for a loan through an approved
lender. A business’ decision to apply for a loan was likely based, at least initially, on
the severity of the pandemic-induced disruptions it suffered and its survival prospects.
Thus, to obtain the causal effect of PPP funds on employment, one needs to take into
account the endogenous nature of the receipt of funds. We employ two measures to
identify effects of the policy along two dimensions: loan timing versus loan receipts.
The first is the measure of loan timing proposed by DK, denoted Share-Delayedc,s ,
which represents the share of PPP funds delayed due to the 10-day pause in lending
that occurred after the first round of PPP funding was exhausted mid-day on April
16, 2020. Lending resumed on April 27 after Congress appropriated additional funds.
Specifically, it is defined as:
Lc,s
Share-Delayedc,s = , (2)
Lc,s + Ec,s
where Lc,s denote funds received late (on April 27 and 28, 2020, just after funding
resumed) and Ec,s denote funds received early (on April 14 through 16, just before
funding ran out). DK argue that this measure is as good as randomly assigned, con-
ditional on the controls, in which case it can directly enter Equation (1) as the policy
treatment variable. As defined, Share-Delayedc,s mainly reveals the impact of liquidity
on employment, as represented by the timing of the PPP loan. That is, by how much
a ten-day delay impeded employment recovery.
To identify the direct treatment effects of actual PPP receipts, we employ an in-
strumental variable (IV) strategy. We instrument PPP receipts (normalized by the
average monthly 2019 payroll) with a variable that plausibly captures the PPP com-
ponent uncorrelated with circumstances following the pandemic outbreak, such as the
degree of the initial disruption. Our instrument is the 2019 small-business share of each
county’s payroll, effectively measuring the degree of purchasing power of an area that
was restored by the program. Small businesses are defined as those with fewer than
500 employees, the size cutoff for 2020 PPP eligibility. Accordingly, the first stage can
be expressed as:
PPPc,s,τ Payroll≤500
c,s,2019
all
= θt + Wc,s ϕt + uc,s,τ , (3)
Payrollc,s,2019 Payrollall
c,s,2019
8
where PPPc,s,τ denotes PPP loans received by county c in state s in program year
≤500
τ = 2020, 2021; Payrollall
c,s,2019 and Payrollc,s,2019 denote average monthly 2019 payroll
across all and small establishments, respectively; and Wc,s encompass all the pre-
pandemic county-level controls as in Equation (1).
The small business share of payroll should be correlated with the actual amount
of loans received because the vast majority of borrowers obtained the maximum PPP
funds for which they were eligible (equal to 2.5 months of their average monthly payroll
for 2019, except for those whose receipts were capped by the $10 million total limit
or the $100,000 limit on individual employee compensation). That is, PPPc,s,τ can be
decomposed into an extensive margin (i.e., which small businesses borrowed) and an
intensive margin (i.e., how much each firm borrowed):
X ≤500
X
PPPc,s,τ ≡ 1PPPi (λ · Payrolli,2019 ) = λ · Payrolli,2019
i∈(c,s) i∈(c,s)
>500
X ≤500
X
+ 1PPPi (λ · Payrolli,2019 ) − 0PPPi (λ · Payrolli,2019 ) + ec,s,τ , (4)
i∈(c,s) i∈(c,s)
where indicators 1 and 0 denote whether small business i borrowed or not, while λ ·
Payrolli,2019 denotes the intensive margin with λ ≈2.5. The term ≤500
P
i∈(c,s) λ · Payrolli,2019
equals (the numerator of) our IV, while the terms in square brackets form the com-
posite error term measuring the deviation of actual PPP take-up from pre-COVID
small business payroll. Deviations via the extensive margin arise if some qualifying
firms did not borrow [ ≤500
P
i∈(c,s) 0PPPi (λ · Payrolli,2019 )] or if some non-qualifying firms
did [ >500
P
i∈(c,s) 1PPPi (λ · Payrolli,2019 )]. ec,s,τ captures any deviation in the intensive mar-
gin from the maximum of 2.5-month payroll. The total deviation is likely small on
average because the first two terms are offsetting (at least partially), while the third
term should be small.
Since small-business payroll is predetermined at the county level, it is orthogonal
to the initial pandemic-induced variation in local conditions. As a result, it should
be uncorrelated with the unexpected component of actual PPP (i.e., the composite
9
error in Equation [4]), especially conditional on all the controls (Wc,s ). Equivalently,
the 2019 small-business payroll share should be uncorrelated with the error term uc,s,τ
in Equation (3). Our exclusion restriction requires that, conditional on controls, the
2019 small-business payroll share does not itself influence the trajectory of recovery, so
that its effect on the outcome in Equation (1) is entirely through shifting the amount of
PPP funds received. Thus, to account for possibly systematic differences in employment
recoveries between counties with higher versus lower small-business payroll shares, we
include a lagged dependent variable in the regressions, along with numerous fixed effects
and controls whose effects are allowed to vary over time.
Our IV strategy is conceptually similar to Chodorow-Reich et al. (2012), who use
pre-recession Medicaid spending to instrument the fiscal relief delivered through the
Medicaid reimbursement mechanism. The underlying logic is analogous: fiscal trans-
fers during the downturn were based on pre-recession spending levels, adjusted for the
severity of local economic conditions. Consequently, predetermined spending provides
a valid source of exogenous variation in actual fiscal receipts during the recession, con-
ditional on prior trends in the outcome variable. Extending this logic, we construct a
similar instrument for any subset of small businesses using their share of total payroll.
This approach allows the IV to capture variation beyond the aggregate treatment for
all small businesses and does not rely solely on the discontinuity in treatment status
around the program’s size threshold. In particular, for the smallest firms (those em-
ploying up to 20 workers), PPP receipts are instrumented using their payroll share.
The validity of this instrument is examined in detail in Section 5.1.
2.2 Data
This section briefly documents the array of data, along with the construction of the
variables used in our analysis. Summary statistics are reported in Table 1, and more
details are provided in Appendix A.
10
Employment Counts We use the most timely high-frequency (monthly) employ-
ment data available at the county level from the QCEW. The QCEW employee counts
cover more than 95 percent of US jobs, making it pertinent for evaluating the PPP,
a chief goal of which was to preserve employer-employee matches. Our sample spans
2020–2021.
We consider specifications with the employment outcome expressed in levels, loga-
rithmic levels, relative to the adult (16-year-old and older) population (denoted E/P ),
and changes in employment relative to the adult population (denoted ∆E/P ). Popula-
tion is measured as of 2019 from the American Community Survey (ACS). To control for
possible county-specific pre-trends, we include a lag of the dependent variable defined
as of the end of 2019 of the corresponding employment measure.
To more accurately assess how the PPP impacted employment among the smallest
establishments, which are generally deemed to need liquidity assistance the most, we
use QWI data on employment by establishment size.7 An additional advantage of the
quarterly QWI is that its employment counts are based on longitudinal job histories
linking an individual with an employer over time. Thus, QWI data enable a more pre-
cise evaluation of whether PPP funds helped maintain existing employment matches.
To this end, we focus much of our analysis on QWI stable employment, which tallies
the number of jobs held on both the first and the last day of each quarter with the same
employer. Given its definition, stable employment is probably the most suitable mea-
sure to assess whether PPP funds supported the continuity of preexisting employment
relationships, while other employment measures are more “contaminated” by churns in
the labor market.
PPP Loans and Borrowers For PPP lending, we use official data released by the
Small Business Administration (SBA).8 We match each borrower’s business name and
full address to a unique Placekey identifier. These identifiers then map the borrowers
7
Employment by establishment size in the QCEW is only available once annually.
8
We use PPP data released as of August 2021 and available at https://www.sba.gov/
funding-programs/loans/COVID-19-relief-options/paycheck-protection-program/ppp-data.
11
to their US Census county (or CBSA), allowing us to calculate loan statistics at the
desired level of geography, including the share of loans delayed.9 In the specifications
where the policy variable is the volume of funds received, we use overall PPP funds
disbursed in 2020 for all quarters of 2020, but the combined total of 2020 and 2021
funds for all 2021 quarters, all normalized by the 2019 average monthly payroll for
total private employees as reported in the QWI data.
Preexisting Local Conditions Since existing relationships with banks were found
to be important for loan underwriting in the first phase of the PPP (see Li and Stra-
han 2021, for example), we control for the following indicators of local banking market
conditions as of 2019: bank branch density (number of bank branches normalized by
population); community banks’ and four largest banks’ shares of deposits; and the vol-
ume of small business loans (SBL) in 2019 each county (from data reported pursuant
to the Community Reinvestment Act), normalized by the number of small establish-
ments (under 500 employees) from the QCEW data for 2019. We further control for
the following pre-pandemic local demographic and economic conditions: median family
income, commuter-to-resident population ratios, and the share of minors from the ACS;
and urban or rural classifications from the 2013 National Center for Health Statistics
scheme.
Pandemic-Related Factors Counts of COVID-19 cases and deaths are provided
by Johns Hopkins University. The extent of county-level lockdowns is measured as the
share of days in lockdown for early (before April 17, 2020) and late (April 17 through 30,
2020) periods using data from the Keystone-Strategy COVID-19 Intervention dataset.
To account for differential state-level measures in response to COVID-19, we include
the stringency index constructed by the Oxford Coronavirus Government Response
Tracker.10 To account for potential heterogeneous effects of the COVID-19 shock due
9
Placekey is a free, universal standard identifier for any physical place. For more details, see
https://docs.placekey.io/ and the corresponding white paper.
10
The index construction is described in Roser (2021).
12
to pre-pandemic industrial composition, we control for the share of work that could
potentially be done remotely (Dingel and Neiman 2020), the share of employees working
in “most impacted” industries (with two-digit NAICS codes 44–45, 61, 71, 72, and
81), and the share of employees working in essential industries (as defined by the US
Department of Homeland Security’s Cybersecurity and Infrastructure Security Agency,
DHS-CISA).
Table 1 provides summary statistics for the monthly employment data sample of
QCEW, as of April 2020.
3 What Explains the Share of PPP Loans Delayed?
What makes the delay in PPP loans attractive as a policy treatment variable is that it
provides a causal interpretation under the plausible assumption that the distribution of
the delay in the localities was as good as random. That is, the share delayed should be
conditionally uncorrelated with any unobserved factors that might have influenced the
employment recovery. This assumption is satisfied if the interruption point of the queue
of PPP applicants, which determines the share of loans delayed when the initial funding
runs out, is effectively random. Thus, we first examine this assumption at the county
level by modeling the first-order (linear) relationship between the share delayed and
local conditions before the delay period began (on April 16, 2020) that could separately
impact the subsequent economic recovery.11
The coefficients reported in Table 2 show that the delay in loan volume is closely
related to several characteristics at the county level, especially the existing lending
relationships of small businesses.12 Counties with a higher 2019 SBL volume per small
establishment experienced lower shares of delayed loans: A one-standard-deviation (SD)
higher level of SBL per small establishment is associated with a 0.13 SD lower share of
11
Appendix B further discusses changes in PPP rules over time, which could lead to different behavior
of late versus early recipients, especially in hard-hit areas such as urban centers.
12
In all subsequent analysis, the share delayed is based on the volume unless otherwise specified.
Qualitatively similar results are found for the number of loans delayed, as reported in the Appendix
Table A.1, and for a CBSA-level sample, as reported in the appendix Table A.2.
13
delayed loan volume.13 Moreover, counties with a larger share of deposits at the four
largest banks and at community banks were significantly more likely to experience a
delay (a result driven by urban counties). We find that a one percentage point increase
in deposits in the four largest banks (community banks) led to a 13.9 percentage point
(7.5 percentage point) increase in funding delay in urban counties. This is likely due
to the fact that the largest banks had significantly pulled out of small business lending
since the Great Recession (see Chen, Hanson, and Stein 2017), and because smaller
banks were likely less able to meet high demand due to capacity constraints.14
Differences in the determinants of the share delayed between urban and rural coun-
ties likely relate to how the virus transmission depended on the size and density of the
population and on people’s modes of interaction. On average, urban counties had a
lower share of loans delayed than rural counties (44 vs. 50 percent). However, urban
counties with higher COVID-19 case rates early on had a significantly higher share
of delay. This correlation for urban counties supports the conjecture that areas hit
hardest by COVID-19 suffered a greater disruption of commercial activity at the be-
ginning of the pandemic, which also impeded PPP lending. Higher demand combined
with impaired supply would result in worse delays in PPP lending. In fact, the most
populous counties (defined as those in the top 1 percent by population), plausibly the
counties most disproportionately impacted by COVID-19 initially, experienced signifi-
cantly larger shares of funding delay, even after many covariates are taken into account.
Moreover, preexisting county attributes explain a higher fraction of the cross-county
variation in the share delayed for urban counties than for rural counties—about 7 per-
centage points higher in terms of the adjusted R-squared.
Given that the share delayed is correlated with several preexisting local attributes
and public health conditions right after the COVID-19 outbreak, we include these co-
13
Alternatively, counties at the 5th percentile of SBL per small establishment experienced a 0.39 SD
higher delay in funding than counties at the 95th percentile.
14
Before the pandemic, the share of small firms that borrowed from community banks was on average
lower in urban counties than in rural counties. The lack of preexisting relationships likely hampered
urban small firms’ chances of obtaining a PPP loan early in the pandemic. As Balyuk, Prabhala, and
Puri (2020) show, early in the program, small firms were better able to obtain funding from community
banks with which they had a preexisting relationship.
14
variates in our employment regressions as controls.15 The assumption supporting the
inclusion of these covariates is that these public health conditions and preexisting bank-
ing and relationship lending conditions could in principle influence the recovery path
of a local economy and their influence should not be attributed to PPP. Furthermore,
we allow these covariates to influence employment dynamically throughout the sample
months (that is, differently in each month), as we do with the share delayed, PPP re-
ceipts, and other controls. This flexible specification is likely prudent given the unique
nature of the pandemic downturn.
4 Effects of PPP Timing on Employment
Our ultimate goal is to estimate the treatment effect of the PPP on local employment
recovery. We begin by analyzing the effects of the timeliness of PPP loans, as rep-
resented by the share of loans delayed proposed by DK. To better understand how
funding timeliness may influence a locality’s economic recovery, our analysis examines
how the estimated effects of this policy metric vary depending on the specification of
the employment outcome (such as in levels, logs, relative to adult population, etc.), the
geography of local labor markets (urban vs. rural counties, counties vs. CBSAs), data
sources (QCEW and QWI), and across different establishment sizes.
To summarize, our analysis indicates that the share delayed has a negative impact
on employment when measured in levels and on urban employment when measured
either in levels or as a share of adult population, particularly in the smallest urban
businesses (those with fewer than 20 employees). However, this effect is not robust
beyond these specific segments of firms or employment measures.
Different Employment Specifications
First, we examine how alternative employment specifications affect the estimated
impact of the PPP timing. Different outcome specifications imply different assumptions
15
Including these attributes as controls also enables consistent inference after variable selection
according to Chernozhukov, Hansen, and Spindler (2015).
15
about parallel trends if the analysis is interpreted in a difference-in-difference frame-
work. For example, if parallel trends hold in log levels (growth), they generally do
not hold in levels. Thus, treatment effect estimates are not invariant with outcome
specification.
We begin with employment in levels. However, this specification disproportion-
ately weights the largest counties, which are several orders of magnitude larger than
the smallest counties.16 To reduce this skew, we consider employment measures that
are less scale-dependent and more commonly used in the policy evaluation literature.
For example, studies of the impact of minimum wage changes use log employment
(Jha, Neumark, and Rodriguez-Lopez 2024) or employment-to-population ratios (Cen-
giz et al. 2019), while studies analyzing fiscal stimulus effects often use the change in
the employment-to-population ratio (Chodorow-Reich et al. 2012).17 These alternative
employment specifications are likely to provide a more accurate reflection of economic
growth dynamics at our level of analysis, as they better capture proportional changes,
account for population size, and reflect regional heterogeneity.
Figure 1 reports coefficient estimates from Equation (1) using all counties and al-
ternative specifications of total private employment (levels, logs, E/P , and ∆E/P ).
February 2020 serves as the reference period. The regressions include state and time
fixed effects, a lag of the dependent variable to capture pre-trends,18 and extensive con-
trols for preexisting conditions and COVID-19 impacts. Standard errors are clustered
at the state level.19
We account for a broad set of preexisting county characteristics. These include
socioeconomic factors (median family income, share of minors, commuter-to-residential
population ratio, and 2013 NCHS urban-rural classification) and financial access (bank
16
In our data, employment in the top 10 largest counties exceeds that in the smallest county by more
than four orders of magnitude. Moreover, as noted above, funding delays were disproportionately larger
in the top 1 percent of counties by population.
17
Hershbein and Stuart (2024) use changes in log employment.
18
The lag of LHS is December 2019 for levels, logs, and E/P ; for ∆E/P, it is the change from
December 2018 to December 2019, normalized by the 2019 adult population.
19
Results are robust to replacing state and time fixed effects with county and state-by-month fixed
effects, or clustering by county instead of state; see Appendix Table A.3.
16
branch density, deposit shares held by community banks and the four largest banks).
We also incorporate indicators of relationship banking, proxied by the volume of small
business lending in 2019 per small establishment. The latter measures are particularly
relevant, as counties with greater financial diversity and stronger bank ties were likely
to experience fewer delays, consistent with the results in Table 2.
We also account for variation in the impact of the pandemic. On the public health
side, we control for cumulative COVID-19 deaths and cases per million. On the policy
side, we include a stringency index of state containment measures and an indicator for
early lockdown implementation (before April 16, 2020). On the labor-market side, we
incorporate pre-pandemic industry and occupational composition: the share of essential
workers, the potential to switch to remote work, and exposure to the most impacted
industries.
These controls are important for several reasons. Counties with early or stricter
lockdowns likely experienced sharper initial disruptions, raising PPP demand while
slowing loan processing. Such counties also tended to have higher population density,
higher rates of early infection and death, and higher inherent vulnerability to infectious
diseases, all of which could have hindered recovery. Industry structure and occupational
mix also shaped recovery dynamics. A higher share of jobs in directly affected indus-
tries or remote-work occupations may have either accelerated recovery (if large early
job losses rebounded quickly) or slowed it (if demand for in-person services lagged).
In contrast, counties with larger essential sectors likely saw more muted employment
swings, since those businesses remained open or reopened sooner.
The results show that loan delays have a clear negative effect on employment recov-
ery only when employment is measured in levels. For logs, E/P , and ∆E/P , we find no
negative effect—and in some cases a positive and significant one (e.g,, for ∆E/P ). As
Appendix Table A.3 confirms, sequentially adding controls does not change this conclu-
sion. The negative effect in the level regressions likely reflects model misspecification
or unobserved heterogeneity, rather than a true widespread impact of PPP delays.
17
Urban versus Rural Counties
To further examine regional heterogeneity, we re-estimate the regressions separately
for urban and rural counties (Figure 2). For urban counties (shown in the left panel), the
coefficients are (mostly) negative in both the employment-level and E/P regressions,20
and negative but never statistically significant in the log-employment specification.
For E/P , the negative effect becomes statistically significant only with a long delay—
November 2020 through March 2021—casting doubt on a causal interpretation. In
contrast, for rural counties, where the share of PPP delayed was larger on average (50
vs. 44 percent in urban counties), the estimated coefficients are rarely negative and
never statistically significant.21
Effects on Employment in the Smallest Establishments
To evaluate the impact of funding delays on the smallest establishments, we examine
the impact of PPP funding delays on establishments with fewer than 20 employees.
We use quarterly QWI data because the QCEW provides this level of detail only on
an annual basis. An additional advantage of QWI is that its employment measures
are based on longitudinal job histories, allowing individuals to be linked to the same
employer over time. Among the various QWI employment measures, stable employment
is the most relevant for tracking ongoing employment relationships. It counts jobs held
continuously throughout an entire quarter, providing a clearer picture of sustained
employment. For establishment size, QWI reports employment across five brackets: 0-
19, 20-49, 50-249, 250-499, and 500+ employees. For simplicity, we focus on employment
counts in the smallest bracket (under 20 employees), where DK identified notable effects.
Figure 3 illustrates that although the trends in QCEW and QWI employment data
are broadly similar, as expected, the stable employment series of QWI is considerably
20
These specifications align more closely with the approach of DK using individual-level CPS data,
where the share delayed is matched to an individual’s county and the outcome is a binary employment
indicator.
21
Because many workers commute across county lines, we repeat the analysis at the CBSA level
to better assess local labor market dynamics (Appendix Table A.4). At this level, the share delayed
exhibits a negative but insignificant effect in level regressions, while the other specifications yield
positive and often significant effects.
18
smoother than the QCEW series. Interestingly, both datasets show that by the end
of 2021, total employment had not yet returned to its 2019:Q4 level, remaining about
1 percentage point lower relative to population. However, stable employment in the
smallest establishments rebounded more quickly, reaching its 2019:Q4 level as early as
2021:Q2.
Table 4 summarizes our findings on the impact of funding delay using the entire
county sample in columns (1)–(4) and the urban subsample in columns (5)–(8). These
regressions include the same comprehensive set of controls as in the QCEW results (Fig-
ure 1) and use 2020:Q1 as the reference period. When reporting results for the smallest
establishments, the share delayed is defined specifically for establishments with fewer
than 20 employees, excluding loans to the self-employed.22 To construct this measure,
we exclude borrowers reporting one or fewer jobs saved and receiving no more than
$20,833, the maximum loan amount available to self-employed individuals (including
independent contractors and sole proprietors). The table shows that the negative im-
pact of the share delayed, documented by DK, is apparent only in the urban subsample.
Although the coefficients for share delayed are sometimes negative in the full sample,
they are not statistically significant at conventional thresholds. Similar regressions
using employment counts for all establishments regardless of size yield negative and
sometimes statistically significant effects only in the levels specification (see appendix
Table A.5). Although these total employment results are consistent with our previous
QCEW findings, albeit less persistent, the size-specific QWI data reveal that the neg-
ative coefficients are driven by establishments with more than 500 employees, casting
further doubt on a causal interpretation of the effect of the funding delay for total
employment.
In sum, we find limited evidence that the share delayed influenced overall employ-
ment. However, when considering the QCEW and QWI results together, we cannot
rule out an effect on employment when measured in levels or among the smallest urban
22
Including loans to self-employed individuals does not change the results regarding the share de-
layed.
19
employers (fewer than 20 employees) more generally.
5 The Relative Importance of PPP Receipt and Timing
The impact of a delay in PPP funding may differ from the impact PPP receipt itself.
We propose two methods to study the impact of PPP receipt and to distinguish it from
the timing of receipt: (1) an instrumental variable technique using county-level QCEW
and QWI data, and (2) a closest-neighbor matching strategy using firm-level activity
data from Advan. We discuss each in turn.
5.1 County-Level Evidence
So far, we have found that, when using county-level data, the timing of PPP funding is
not robustly correlated with local employment recoveries outside the smallest establish-
ments in urban counties. However, this finding does not imply that PPP funding was
not important for employment dynamics. We further explore the relationship between
PPP funds and employment by augmenting our previous county-level regressions to in-
clude county-level PPP receipts normalized by the average monthly payroll of 2019.23,24
Normalized PPP receipts effectively measure the degree of purchasing power restored by
the program in a given area. PPP receipts relative to pre-pandemic payroll—whether
by preserving preexisting employment relationships, supporting new employment, or
through spillover effects across firms—were likely the most relevant metric for employ-
ment dynamics after the outbreak.
To identify the causal effect of PPP funds on employment, we propose an instru-
ment that is conceptually similar to Chodorow-Reich et al. (2012), who use pre-recession
Medicaid spending to instrument fiscal relief delivered through the Medicaid reimburse-
ment mechanism. The logic behind their instrument is that predetermined spending
23
The 2019 payroll is calculated by multiplying average monthly earnings by beginning-of-period
employment for each quarter using QWI data, separately by establishment size (total, under 500, and
under 20). The quarterly results are then averaged across all four quarters of 2019.
24
We use payroll rather than population or employment to normalize receipts because it better
reflects the purchasing power of the money allocated, given substantial differences in wages and the
cost of living across the country.
20
provides a valid source of exogenous variation in actual fiscal receipts during the reces-
sion, conditional on prior trends in the outcome variable. In our case, the instrument
is the county-level average share of monthly 2019 payroll in small establishments, as
measured in the QWI. Given the exogenously imposed size restriction (establishments
with fewer than 500 employees were eligible for funding), counties with higher shares of
payroll in small establishments were better positioned to receive relatively more funds
per dollar of payroll, potentially supporting stronger employment recoveries.25 When
studying employment in the smallest establishments (fewer than 20 employees), we cal-
culate the PPP receipt specific to these establishments, excluding funds allocated to
self-employed individuals.26 In this case, the instrument is the share of payroll in the
smallest establishments.27 Also, since many rural counties do not have large establish-
ments, we restrict our analysis to urban areas.
In our baseline regressions, we use PPP funds disbursed in 2020 for all quarters
of 2020, but the combined total of 2020 and 2021 funds for all quarters of 2021. The
rationale is that 2020 funds could have continued to influence employment outcomes into
2021, whereas 2021 funds were unlikely to have been anticipated in 2020. As robustness
checks, we also estimate the regressions using either cumulative PPP disbursements by
quarter (funds allocated up to each quarter) or the final total amount (summing 2020
and 2021) for all periods. We discuss how these alternative specifications affect the
results later in the paper.
Instrument Validity
Figure 4 illustrates the relationship between PPP receipt relative to payroll and
the share of small-establishment payroll at the end of 2020 and 2021 (left panel), and
25
We use average monthly 2019 payroll because each eligible small business was entitled to a 2020
PPP loan not to exceed ten weeks of average 2019 payroll, or $10 million. All evidence indicates that
PPP applicants generally requested the maximum eligible amount. In our data, the average county
received 2.2 (3.06) months of monthly small-establishment payroll in 2020 (by the end of 2021), see
Table 3.
26
For consistency, we exclude PPP funds allocated to self-employed individuals because the self-
employed are not covered by the QCEW or QWI employment data.
27
Regressions that use the share of under 500 payroll produce similar results, however, the strength
of this instrument is, not surprisingly, significantly weaker.
21
between PPP receipt for the smallest establishments and their corresponding payroll
share (right panel). The correlation is strongest for the smallest firms—0.91 versus 0.68.
The positive association between these measures is confirmed by the results in Table 5,
which include the complete set of covariates. Together, these results demonstrate a
strong first stage: the under-500 (and under-20) payroll share is highly predictive of
the amount of PPP funds received per dollar of payroll in urban counties. Further-
more, Figure 5 illustrates that the correlation between PPP receipt relative to payroll
(total versus smallest establishments) and the share delayed is nonzero, albeit modest:
0.08 for total and 0.13 for the smallest establishments. Consequently, our regressions
incorporate both measures.
The validity of our instrument rests on the exclusion restriction: the share of pay-
roll in small establishments must not directly affect employment, except through its
correlation with PPP receipt. This condition is potentially problematic, since employ-
ment dynamics may have been influenced by the establishment size composition during
the pandemic, and thus by the small-establishment share of payroll. For example, es-
tablishments in the hardest-hit industries tended to be relatively small, so counties
with a larger concentration of such establishments may have recovered more slowly,
independent of PPP funding. To mitigate this concern, we take several steps.
First, we specify employment outcomes as changes, ensuring that our results are
not driven by time-invariant differences between counties with higher versus lower
small-establishment payroll shares. Following Chodorow-Reich et al. (2012), we use
the change in employment-to-population specification (∆E/P ).28 Second, we include
state and time fixed effects in our regressions, along with the extensive set of controls
discussed earlier, which are allowed to have dynamic effects by interacting them with
time dummies. Moreover, when focusing on the evolution of employment in the smallest
(under 20) establishments in urban counties rather than in all businesses, we further
mitigate concerns, as the industrial composition within the smallest-establishment cat-
egory is likely more uniform.
28
Our results for logs and E/P are qualitatively similar.
22
Even with an extensive set of controls, a nonzero possibility still remains that an
omitted variable is correlated with both our instrument and the dependent variable.
To investigate this, we examine how our instrument relates to changes in the total
employment-to-population ratio prior to the 2020 pandemic. Figure 6 presents these
results for the 2003:Q1–2021:Q4 period. The figure shows two sets of estimates: one
using a basic set of controls (fixed effects only) and another using the full set of controls
discussed earlier.29 The figure indicates that the share of under-500 payroll did not have
a significant effect on ∆E/P before COVID-19. In fact, during the previous 20 years,
the conditional correlation between the instrument and the dependent variable was
consistently weak, occasionally negative, and several orders of magnitude lower than its
relationship during and after the COVID-19 recession. The conditional correlation of
the share of funding delayed and employment was also mostly insignificant throughout
the period.
Figure 7 presents a similar analysis for employment in establishments with fewer
than 20 employees. In this case, the conditional correlation between the instrument
and the dependent variable was distinctly negative during the Great Recession, which
was not observed during the COVID-19 recession. Employment recovery in counties
with larger shares of under-20 payroll was slower than in other counties. In contrast,
the conditional correlation of the change in employment with the share delayed was
positive during the Great Recession. It is possible that places with higher shares of
community banks (i.e., lower shares of large banks) and less reliance on small business
loans, both of which correspond to a higher share delayed on average (see Table 2),
fared better during the Great Recession because large banks slashed lending, especially
to small businesses, to repair damages inflicted by the subprime crisis on their balance
sheets. In sum, the employment dynamics for the smallest establishments were clearly
different during the COVID-19 pandemic, possibly due to the support of PPP funding.
These long-run patterns support the validity of our instrumental-variable approach and
provide evidence that the exclusion restriction is likely satisfied.
29
Results for the QCEW sample of private employment show similar trends; see Appendix Figure A.2.
23
Estimates of Jobs Retained
Table 6 presents our IV estimates, showing results for total QCEW employment,
stable QWI employment across all establishments, and for those with fewer than 20
employees.30 In our baseline specification, changes in the employment-to-population
ratio are measured relative to 2019:Q4.31 As shown in the table, the OLS estimates of
the impact of PPP receipt are positive and significant across all employment measures.
The instrument is strong, with Kleibergen-Paap Wald F-statistics ranging from 48.8
to 96.3 and Anderson-Rubin Wald χ2 tests of weak instruments producing p-values of
0.00 across all specifications. IV estimates are generally larger than OLS estimates
for overall employment measures, but slightly smaller for the smallest establishments.
One likely reason for the negative OLS bias in overall employment is that larger firms
(within the eligible range) account for a disproportionate share of both PPP outlays
and total employment changes. However, these firms likely benefited less from the
PPP—owing to stronger banking relationships and greater liquidity buffers—so their
heavy weight in the data causes OLS to understate the true effect of PPP. Among the
smallest establishments, this negative bias is attenuated because treatment effects are
more homogeneous within size groups. Moreover, any remaining negative bias may be
offset by a positive selection bias: smaller firms that managed to apply for PPP—despite
facing greater access hurdles—were likely those most in need and thus most responsive
to support. These offsetting forces help explain why the OLS and IV estimates are
more similar for employment among the smallest establishments.
Our IV estimates in column (2), based on QCEW private employment, imply that
PPP funds saved approximately 5.85 million job-years in the urban counties in our
sample over the study period.32 Roughly 53 percent of these job-years materialized
30
Our instrument identifies the local average treatment effect on compliers, under the standard
assumption that there are no defiers. Appendix C provides a discussion of why this assumption is most
likely satisfied in our context. Also note that our IV specification directly estimates the treatment effect
of receiving funds, not the intent-to-treat effect, and therefore does not require the Wald adjustment,
as in Autor et al. (2022a).
31
Results are similar when changes are measured against 2019 annual averages or when each quarter
is compared with its corresponding quarter in 2019. These results are not reported for brevity.
32 PPP pop
Job-year figures are computed by rearranging Equation (1) to derive ∆E = β payroll 100 , substi-
24
in 2020 and the remainder in 2021, corresponding to 2.9 percent and 2.5 percent of
2019 employment in these counties, respectively. Notably, our estimates capture both
direct and indirect spillover effects of the PPP. However, since the estimates are based
on an urban subsample of counties, extrapolating to the full US is not straightforward.
Nevertheless, the magnitudes reported are broadly consistent with Autor et al. (2022b),
who estimate that the program boosted employment by up to 3 percent by the end of
2020, and fall near the midpoint of the estimates reported in previous studies.33
We also estimate the number of stable jobs saved. Using the coefficients in column
(4), we find that PPP receipt preserved 4.28 million job-years, about 41 percent of which
occurred in 2020 and the remainder in 2021, equivalent to 1.8 percent and 2.6 percent
of 2019 stable employment, respectively. As far as we are aware, our estimates of stable
jobs saved represent a novel contribution, as most existing studies measure job preser-
vation using employment flows—similar to our QCEW results—without accounting for
job stability or worker attachment.
Cost of Jobs Retained
The cost per job-year retained implied by our baseline IV estimates of the PPP’s
effect on employment is reported in Table 7. Specifically, we calculate the cost of
retaining a job-year with PPP funds as follows. We first calculate the total number
of job-years that would have been saved during the two-year period if the total PPP
funding available by May 2021 (the program’s end) had been in place throughout the
whole period. This involves scaling the previously calculated job-years saved in 2020
by the ratio of total PPP outlay to 2020 PPP outlay (with no adjustment is necessary
for 2021 job-years). We then divide this estimate of job-years by the total program
outlay.34 Accordingly, estimates based on total QCEW employment imply that saving
tuting total PPP outlays for the corresponding year for PPP, the all-firm average monthly 2019 payroll
for payroll, and total 2019 population for pop. The division by 100 is necessary because ∆E/P enters
the regressions in percent. The resulting quarterly estimates are summed across the sample period
and divided by four to obtain job-years saved.
33
See Table 5 in Dalton (2023) for a comprehensive summary of the estimated employment effects
of PPP and the methodological differences across studies.
34 PPP pop
The scaling factor is implied by the linearity of Equation (1): ∆E = β payroll 100 , thus job-years
25
a job-year costs $88,997. Consistent with our expectations, the cost of saving a stable
job for a year is considerably higher at $127,179. The cost of maintaining a stable job in
one of the smallest establishments is substantially greater, at $546,777 per year, likely
reflecting the characteristically high turnover rates of these establishments.
Table 7 also presents alternative estimates of the costs of jobs retained under two
different assumptions regarding the timing of funding expectations: 1) the full amount
of PPP funds was anticipated in 2020 (“Total PPP” panel), and 2) only the cumulative
funds received up to a given quarter (“Cumulative PPP” panel) affected employment
in that quarter.35 Not surprisingly, costs are lowest in the cumulative PPP scenario
and highest in the total PPP scenario.36 For example, for total QCEW employment,
the cost of saving a job-year is $108,201 under the Total PPP assumption compared to
$87,503 under the Cumulative PPP assumption.
Our cost estimates, between $87,503 and $108,201 depending on our assumptions
regarding the timing of funding expectations, lie toward the lower end of the range
reported in previous studies. Event-study analyses yield estimates similar to ours: for
example, Dalton (2023) reports a cost of $141,000 per job-year saved, and Splinter et al.
(2025) report costs in the range of $133,000–$146,000. Other studies using different
methodologies find varying results: Doniger and Kay (2023) estimate approximately
$100,000 per job-year, Autor et al. (2022c) and Autor et al. (2022b) report $169,000–
$258,000, and Granja et al. (2022) reports about $175,000 per job-year saved. The range
of estimated costs of saving one job-year through the PPP in fact compares favorably
with the cost of nearly $603,000 per job-year in terms of state and local government
employment saved by federal fiscal assistance, as estimated by Clemens, Hoxie, and
Veuger (2025). The authors provide an incisive discussion of the likely reasons for the
retained would change proportionally to funding (normalized by 2019 payroll).
35
Note that the job-years retained corresponding to these two assumptions are computed using the
coefficients estimated from separate regressions, where the policy regressor is measured in accordance
with the respective assumption. These coefficients are not shown for brevity.
36
The logic is the same as that underlying our baseline estimate of total job-years retained—by
scaling the jobs saved in 2020 by the ratio of eventual total funding to funding through a specific
quarter. Hence, the lower the funding assumed for a quarter in 2020, the higher the ratio, and in turn
the more job-years retained, which translates into a lower cost.
26
high price tag. In contrast, Chodorow-Reich (2019) estimate a cost of just over $50,000
per job-year saved through American Recovery and Reinvestment Act of 2009 (ARRA).
The ARRA was an $800 billion policy package, with roughly $600 billion disbursed in
the year of analysis—placing it on a scale comparable to the PPP in terms of fiscal
magnitude. The substantially greater cost-effectiveness of ARRA likely reflects the
distinct financial nature and depth of the Great Recession relative to the COVID-19
downturn.
Effects of PPP Receipt versus Timing on Small Establishments
We now compare the impact and cost of PPP receipts with that of PPP delay. Con-
sistent with previous regressions that excluded PPP receipt, the estimated effects of the
share delayed are generally insignificant, except for employment in the smallest estab-
lishments in urban counties and when using the size-specific share delayed (columns (5)
and (6) in Table 6). This pattern is intuitive: The smallest establishments probably
needed the most immediate liquidity assistance. Because both PPP receipts and share
delayed are significant for these smallest establishments, we can compare the magnitude
of their estimated effects, contrasting job-years saved from earlier funding (i.e., a lower
share delayed) with job-years saved from additional funding. Using the coefficients from
column (6) in Table 6, we estimate that the PPP funds received (conditional on the
share delayed) saved approximately 332,290 stable job-years in those smallest urban
establishments during the sample period. This corresponds to roughly 0.61 percent of
2019 employment in those establishments in 2020 and 1.36 percent in 2021, respectively.
In comparison, conditional on the funds received, if the share delayed had been reduced
from 48 percent (the sample aggregate for the smallest establishments) to zero, 379,136
job-years would have been saved.37 Combining these two effects implies that PPP would
have preserved approximately 711,426 job years had the delay not occurred, equivalent
to about 4.2 percent of their average 2019 employment over the two combined years.38
37
Relevant sample statistics can be found in Table 3.
38
A note of caution around these estimates is warranted. QWI does not track establishments longi-
tudinally for size, so when a firm crosses a threshold, all of its employment shifts to the new size bin.
27
Overall, our results suggest that the funding effect was more important than the
short-term liquidity effect on aggregate employment at the county level. However, the
timing of receipt was critical for the smallest establishments in urban areas, some of
which may have exited altogether due to delayed assistance as documented by Kurmann,
Lalé, and Ta (2025). Importantly, our findings complement their work by showing
that PPP operated through two distinct channels—funding volume and timing—and
that, after accounting for the timing, PPP support still helped the smallest businesses
preserve an additional 332,290 stable job-years. The firm-level evidence discussed in
the next section reinforces this conclusion.
5.2 Firm-Level Evidence
To study the effects of PPP receipt versus timing at the firm level, we apply a match-
ing estimator using Advan foot traffic data. We compare visits to each PPP borrower
with a closely matched non-recipient control firm (hereafter, peer) matched on indus-
try, economic activity (measured by visits), and geolocation. Importantly, peers are
firms that were active before the pandemic (as of December 2019 or earlier) and did
not receive PPP loans. Our matching criteria, detailed below, are designed to max-
imize the likelihood of satisfying the conditions needed for causal inference based on
difference-in-differences (DiD) estimates. First, they are sufficiently stringent to satisfy
the assumption of parallel-trends: had the treated firms not received PPP, they would
have evolved similarly to their peers because both groups faced comparable conditions
in terms of demand, COVID-19 severity, and non-pharmaceutical interventions. Sec-
ond, the criteria minimize the likelihood of interference between a PPP firm and its
peer, helping satisfy the stable unit treatment value assumption (SUTVA).
Advan data measures foot traffic by tracking movements to and from points of
interest (POI, mostly business establishments) using GPS location data from mobile
Thus, estimated PPP effects for establishments under 20 employees reflect both within-size employ-
ment changes and firms moving into or out of the bin, rather than effects on a fixed group of pre-PPP
small firms. Early in the pandemic, estimates may be inflated by slightly larger firms shrinking below
20 employees, while later they may miss PPP-driven employment growth as some originally small firms
may expand beyond the 20 threshold.
28
devices. Each POI is uniquely identified by a Placekey, which is based on its precise
geographic location (address, latitude, and longitude) and its business type, determined
by a detailed 6-digit NAICS code. This combination enables precise differentiation of
stores, even within large structures like strip malls. Although Advan does not cover
all POI in the US, its dataset provides extensive coverage, particularly in urban areas
and across the retail and service sectors, making it a valuable resource for analyzing
economic activity.39 We use visits to each POI as a proxy for business performance,
as data indicate that the number of visits is strongly correlated with employment and
revenue (see Gorbachev, Luengo-Prado, and Wang 2023).
Using the unique Placekey assigned to each POI, we identify PPP recipients within
the Advan data. To be consistent with our previous county-level analysis, our Advan
sample excludes self-employed PPP recipients, defined as those with loan sizes up to
$20,833 and reporting only one job. For simplicity, it also excludes PPP firms that
received more than one loan, which constitute only a very small subset of the data. To
estimate the effects of receiving a PPP loan on visits, we identify peer firms within the
same 6-digit NAICS industry and with pre-pandemic activity within 5 percent of the
PPP firm (as measured by the absolute percentage difference in the average number
of visits from December 2019 to February 2020).40 In terms of location matching,
we balance the need for geographic proximity (so that peer firms faced similar local
economic conditions and COVID-related policies) and the need to avoid possible direct
competition between a PPP firm and its peer. For our baseline estimates, we restrict
the peer firm to operate within the same county but outside the Census block group
(CBG) of the PPP firm, and at least 5 but no more than 50 miles away.41 This
39
For details on data quality and industry-specific coverage rates, see Advan’s documentation on
places and metrics. Kurmann, Lalé, and Ta (2025) also provide a helpful summary.
40
6-digit NAICS classifications represent highly specific categories of business activity, ensuring that
the control firms we identify are closely aligned in terms of demand for their products. When multiple
peer businesses satisfy the matching criteria for a given PPP recipient, we select one randomly.
41
CBGs tend to correspond to city blocks bounded by streets in urban areas, which means that
retailers and restaurants in the same 6-digit NAICS operating in such proximity may compete for the
same set of customers. The supply shortfall of a peer firm could mechanically increase the demand
for the PPP firm, potentially violating SUTVA. We thank an anonymous referee for highlighting this
possibility.
29
“donut” exclusion zone substantially increases the likelihood of satisfying SUTVA. As
an additional robustness check, we estimate separate treatment effects for subsets of
PPP firms grouped by geographic distance from their peers, varying the distance to the
PPP firm from 1-5 miles to 15-50 miles (see Figure A.3 in the appendix).
Selecting a random peer firm subject to the matching criteria detailed above, we
obtain a sample of 65,136 pairs. Our data span December 2018 through February
2022. Table 8 presents summary statistics showing that our sample consists mainly of
small firms: more than 75 percent of matched borrowers reported fewer than 20 jobs
in their PPP applications (with mean and median counts of 19 and 8, respectively).42
Correspondingly, mean and median PPP loan amounts in our sample are relatively
small at about $139,000 and $49,000, respectively. Furthermore, since Advan data are
based on visits to physical locations, the vast majority of firms in our sample (about 90
percent) are in urban counties and are concentrated in the service and retail sectors.
To study the effects of PPP, we first examine the impact of receipt by comparing
the evolution in the number of total visits to PPP establishments with the evolution in
visits to comparable non-PPP establishments over time. We then examine how much
that gap varies depending on the timing of the loan.43 Although the Advan data are
available at a daily frequency, we aggregate visits to the monthly frequency for the
analysis to avoid high-frequency noise. Importantly, if a firm is not observed at all in
a given month, its value is “filled in” as zero visits to ensure that the firm remains
in the dataset and the panel stays balanced. The dependent variable (LHS) in our
regressions is either Log Visits (defined as the log of visit counts plus one) or Zero
Visits (an indicator equal to one when visits are recorded as zero in the Advan data,
or when we fill in the data). Zero Visits serve as our proxy for business closure, which
may be temporary or permanent.44 With our matched-pair sample, we first trace out
42
Summary statistics for matched pairs by varying geographic distances show similar patterns and
can be found in Appendix Table A.6.
43
The Advan data also provide information on the number of distinct visitors, and results based on
visitors are very similar (omitted for brevity).
44
Some service businesses could have operated fully remotely during the peak weeks of the pandemic
and thus registered zero visits. As a result, this measure may overstate closures for some non-retail
30
PPP’s effects on visits in calendar time by estimating essentially two-way fixed-effects
regressions of the form:
Yijt = αi + δjt + βt PPPi + ϵijt , (5)
where Yijt is the outcome variable (either Log Visits or Zero Visits) for a POI i of pair
j in month t, and PPPi is an indicator variable equal to one if POI i received PPP
funding and zero otherwise. αi denotes POI fixed effects, and δjt denotes pair-time fixed
effects. Given the lack of detailed pre-pandemic firm characteristics in Advan, we rely
on these firm- and pair-by-time fixed effects to control for unobserved heterogeneity.
We then apply the Sun and Abraham (2021) estimator, which accounts for the
staggered timing of PPP receipts and maps out the effects in event time:
−2
X T
X
l l
Yijt = αi + δjt + µl Dijt + µl Dijt + ϵijt , (6)
l=−T +1 l=0
l
where Dijt = I{t − Ki = l} is the event-time indicator, with Ki indexing the month
when firm i received its PPP loan. Standard errors are clustered at the pair ID level in
both regressions.
The left panels of Figure 8 plot estimated βt coefficients (PPP effects over calendar
time) from regression (5), while the right panels plot estimated µl coefficients (PPP
effects relative to funding approval months) from regression (6). These estimates clearly
indicate that businesses that received PPP funding saw significantly better recovery in
visits (and fewer closures, bottom panel) than their non-PPP peers, starting in May-
June 2020. The relative difference in visits between PPP and non-PPP firms grew over
time, reaching close to 10 percent by December 2020 and nearly 20 percent by February
2022 (the end of our sample).45 PPP funding also reduced the probability of closure by
about 2 percentage points by December 2020 and close to 4 percentage points by the
sectors early on in the pandemic.
45
Cole (2022) uses a matched-pair estimator on administrative payroll data and finds that, among
very small firms, PPP recipients increased employment five months after receipt by 7.5 percent relative
to comparable small firms that did not receive funding.
31
end of the sample.46 Importantly, these patterns are robust to the distance between
firm pairs. Appendix Figure A.3 shows consistent results for distance bands from 1-5
miles to 15-50 miles.
To assess the relative importance of short-term liquidity versus funding effects of
PPP, we compare PPP’s effects on firms with PPP loans approved either early (April
14-16) or late (April 27-28), as defined by DK. We identify about 8,575 early PPP
recipients and 8,870 late PPP recipients, respectively. The coefficient estimates for this
subsample, depicted in Figure 9, show a moderate difference in foot-traffic recovery
between early and late PPP loan recipients compared to their respective peers between
mid-2020 and mid-2021, but the difference is not statistically significant and vanishes by
the end of 2021.47 This pattern suggests that the receipt of funds was more important
for economic recovery than the timing of the loan.48 Moreover, we find little difference
in the odds of Zero Visit between early and late recipients.
We must acknowledge that even our stringent matching along with fixed effects may
not fully eliminate the bias resulting from endogenous selection into the PPP. The ulti-
mately untestable parallel trend assumption—that non-borrowers and borrowers would
share the same post-COVID trend in the absence of PPP—can be challenged in the
wake of an unprecedented shock such as COVID-19. Heterogeneity in attributes that
were irrelevant before the shock can result in divergent post-shock trends between the
treated and control groups. Specifically, certain business characteristics might both
determine their PPP choice and influence their post-pandemic trend.49 However, po-
tential selection biases are two-sided. If some eligible firms did not borrow because of
managerial shortcomings or owners’ retirement decisions, our funding-effect estimate
could be upward biased. In contrast, some eligible firms did not borrow because they
46
This likely accounts for about 4 (out of 20) percent of the difference in visits by the end of the
sample because firms that suffered closures tended to be smaller than average.
47
We find a similar and still insignificant difference using an alternative, wider, event window from
April 10 to May 2 (that is, using firms that received loans five-days before or five-days after the 10-day
delay). The exact estimates are omitted for brevity but are available upon request.
48
Splinter et al. (2025) find that the 10-day delay’s effect was about one-fifth of the total estimated
PPP effect on employment changes.
49
We thank an anonymous referee for highlighting this potential bias.
32
did not need the funds and obeyed the program rule that required owners to attest
that PPP funds were necessary to support operations.50 These firms might have done
well regardless, and including them in our control group might bias estimates of the
PPP’s effect downward. Our estimates could also be downward biased to the extent
that some firms we classify as non-recipients may have actually borrowed but could not
be matched in our data. In Appendix D, we discuss additional reasons why some eligi-
ble firms may not have taken PPP funds and argue that any resulting biases are likely
small on net. Nevertheless, further research on non-participation would be valuable to
inform future policy design.
One additional caveat regarding the timing effect of funds is that firms that needed
liquidity early on but were unable to obtain a loan in time might have either been too
discouraged to reapply or gone out of business altogether. If some of these discouraged
or failed firms are matched to PPP recipients and serve as non-recipient controls in our
difference-in-differences analysis, we would underestimate the effect of funding delay
because our estimate would attribute the entire effect to the receipt of funds, instead
of partly to the delay.51 However, such an underestimate would be relevant for both
early and late borrowers, so the differential effect we estimate is not necessarily biased.
Equally important, this issue is not unique to our analysis and is also present in other
studies that examine the impact of the PPP using the share delayed. Overall, our
findings indicate that the receipt of PPP funding played a more significant role in
retaining and expanding employment than the timing of the loan.
6 Summary and Concluding Remarks
This study examined how the PPP affected employment recovery after the COVID-
19 outbreak, distinguishing between short-term liquidity and funding effects. Using
county-level small-firm payroll share as an instrument for PPP receipt, we show that
50
On the loan application form, “the Applicant must certify in good faith to all of the below . . . ”
which includes “current economic uncertainty makes this loan request necessary to support the ongoing
operations of the Applicant.”
51
We thank anonymous referees for pointing out this potential bias.
33
receiving funds was generally more important than timing for most firms. The adverse
effects of funding delays were concentrated among the smallest businesses, those with
fewer than 20 employees, which were particularly vulnerable to cash flow disruptions.
For the broader population of firms, funding delays played a relatively minor role, while
ensuring sufficient funding was the primary driver of overall recovery. PPP receipt saved
approximately 5.85 million job-years in urban counties over the two-year period, at an
approximate cost of $89,000 per job-year, and 4.28 million stable job-years at $127,000
per stable job-year. Since funding delay was particularly detrimental to the smallest
establishments, eliminating delays entirely for these firms would have added 379,136
stable job-years, while broader funding effects (conditional on delay) accounted for an
additional 332,290 stable job-years.
Our findings highlight that effective emergency interventions require both timely
disbursement for the smallest firms and sufficient funding for broader recovery. In the
case of the PPP, because urban businesses experienced more persistent dislocation,
directing aid to these regions and enabling earlier access for the smallest firms through
specialized lenders would have further increased program efficacy.52 More broadly,
it is not surprising that grants, a form of government transfers, are more effective
than loans at sustaining employment, especially for firms facing large cost increases
or significant revenue losses during an emergency. Designating a program as grants
from the outset, thereby removing uncertainty about repayment, could further improve
program effectiveness. With greater certainty, firms might be more willing to invest
and hire.53
Congress also authorized several other programs via the CARES Act, including ex-
panded UI benefits, direct cash transfers, fiscal aid to state and local governments, and
credit support programs. There is substantial work analyzing these programs individu-
52
Our results confirm and extend the recommendations put forth by existing studies such as Granja
et al. (2022) and Autor et al. (2022c).
53
Potential concerns about moral hazard associated with grant programs during a pandemic are
likely minimized due to the exogenous nature of the shock if the grant is intended to allow businesses
to remain closed to curb the spread of a virus. Furthermore, concerns about adverse selection could be
mitigated through measures such as those incorporated into the PPP: eligibility restrictions, funding
caps, and program rules linking support to employment or verified business expenses.
34
ally.54 Ideally, these programs should be evaluated jointly to assess their combined and
interactive effects on employment and firm outcomes during post-pandemic recovery.
Among the few studies considering interactions, Splinter et al. (2025) find that PPP
costs were partially offset by positive fiscal spillovers—specifically reduced UI claims
and higher income tax revenues from continued employment. Similarly, Sledz (2025)
develops a structural model of optimal stimulus allocation between firms and workers,
concluding that given the scarring effects of job loss, joint transfers to both are more
effective.
Taken together, our results indicate that the impact of the PPP on employment re-
covery operated primarily through funding rather than liquidity channels for most firms,
with liquidity effects concentrated among the smallest establishments. Understanding
these distinctions is essential for interpreting the aggregate effects of the program and
situating the PPP within the larger set of pandemic-era interventions, whose interac-
tions remain an important subject for future research.
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Table 1: Summary Statistics: County-Level QCEW Sample
All Urban Rural
Mean SD Mean SD Mean SD
PPP Receipt
No. of Early PPP Loans (4/14–4/16/2020) 197.01 570.29 445.10 877.11 49.41 53.29
No. of Late PPP Loans (4/27–4/28/2020) 226.94 622.71 492.92 959.08 68.70 65.97
Volume of Early PPP Loans, in Millions (4/14-16/2020) 29.11 111.75 71.15 174.99 4.10 5.65
Volume of Late PPP Loans, in Millions (4/27-28/2020) 21.90 94.51 52.92 149.64 3.44 4.16
Total PPP Volume (in Millions) for 2020 167.91 661.24 406.14 1,039.69 26.25 31.11
Total PPP Volume (in Millions) for 2020+2021 254.50 1,034.35 613.34 1,631.46 41.12 45.42
Total PPP Volume for (< 20) (in Millions) for 2020 50.58 192.73 120.26 302.87 9.15 10.54
Total PPP Volume for (< 20) (in Millions) for 2020+2021 78.85 311.25 187.79 490.47 14.07 16.05
Avg No of Jobs Claimed (in Thousands) 12.01 4.41 13.92 3.90 10.87 4.30
Share of PPP Loans Delayed (By Count) 0.58 0.12 0.55 0.10 0.59 0.13
Share of PPP Loans Delayed 0.48 0.18 0.44 0.14 0.50 0.20
Share of PPP Loans Delayed to(< 20) 0.51 0.15 0.49 0.11 0.52 0.16
COVID-19 Impacts
Cum Covid-19 cases per million 151.70 327.54 213.17 402.48 115.14 266.89
Cum Covid-19 deaths per million 66.41 185.02 104.53 237.53 43.73 140.30
COVID-10 Stringency Index (Oxford University) 69.02 8.86 69.82 8.07 68.55 9.27
Share of days in lockdown (pre-04/17/2020) 0.50 0.12 0.50 0.11 0.49 0.12
Share of days in lockdown (04/17 and 04/30/2020) 0.99 0.05 0.99 0.03 0.99 0.06
Share of Work Done Remotely 0.35 0.04 0.35 0.06 0.35 0.03
Share of Emp. in Essential Industries 0.88 0.02 0.87 0.02 0.88 0.02
Share of Emp. in Impacted Industries 0.32 0.08 0.32 0.07 0.31 0.09
Share of Wages in Impacted Industries 0.19 0.07 0.19 0.06 0.19 0.08
Preexisting Conditions
Rural County Dummy 0.63 0.48
Total Residential Population (in Thousands) 104.47 333.04 240.41 516.99 23.63 22.16
Share of Minors 0.22 0.03 0.22 0.03 0.22 0.04
Commuter to Residential Population Ratio 1.15 0.17 1.13 0.12 1.17 0.19
Median Family Income (in Thousands) 66.55 16.35 75.60 18.39 61.17 12.15
Community Bank Share of Branches 0.59 0.32 0.43 0.29 0.68 0.30
Community Bank Share of Deposits 0.57 0.34 0.39 0.31 0.67 0.32
Number of Branches 27.46 69.53 57.95 106.73 9.32 7.51
Bank Branch Density (Population per Branch), in Thousands 3.18 1.92 4.08 1.99 2.64 1.65
Big4 Bank Share of Deposits 0.08 0.15 0.15 0.18 0.04 0.11
Number of Small Business Loans (in Thousands) 2.32 10.23 5.64 16.21 0.34 0.42
Volume of Small Business Loans (in Millions) 80.31 311.49 194.43 488.97 12.45 16.44
Avg Small Business Loan (in Thousands) 35.04 13.95 36.79 11.65 34.00 15.07
SBL Volume per Estab< 500 (in Thousands), CBP 2019Q1 24.03 11.74 29.12 9.96 21.01 11.68
Private Establishments (< 500) (in Thousands), CBP 2019Q1 2.54 8.94 5.92 13.99 0.54 0.56
Private Employment (in Thousands), QCEW 2019 Average 39.54 146.16 94.68 228.83 6.74 7.60
Private Establishments (in Thousands), QCEW 2019 Average 2.97 12.50 6.97 19.83 0.59 0.63
Share of Estabs (< 500), CBP 2019Q1 0.99 0.02 1.00 0.01 0.99 0.02
Share of Employment in Estabs (under 500), QWI 2019 0.62 0.16 0.55 0.13 0.66 0.16
Observations 3,100 1,156 1,944
Notes: The values for PPP receipt and COVID-19 Impacts pertain to April 2020 unless otherwise specified. Val-
ues for Preexisting Conditions are based on 2019 data. Measures related to PPP loans to establishments with fewer
than 20 employees (< 20) exclude loans to the self-employed (i.e, we exclude borrowers who reported one or fewer jobs
saved and received no more than $20,833, the maximum allowed for self-employed individuals). Data sources described
in Section 2.2.
38
Table 2: Determinants of Share of PPP Loan Volume Delayed, April 16–26, 2020
All Urban Smaller Rural
Cum Covid-19 cases per billion up to Apr 15 0.011 0.063∗∗ 0.069∗∗ –0.014
(0.020) (0.027) (0.027) (0.035)
Cum Covid-19 deaths per billion up to Apr 15 0.065 0.016 –0.004 0.099
(0.049) (0.064) (0.064) (0.094)
Share of days in lockdown (pre-04/17/2020) 0.028 –0.016 –0.018 –0.053
(0.054) (0.064) (0.067) (0.077)
Share of days in lockdown (04/17 and 04/30/2020) 0.147 0.025 0.022 0.329∗∗∗
(0.127) (0.177) (0.176) (0.070)
Share of essential empl by county –0.196 –0.280 –0.304 –0.014
(0.218) (0.386) (0.386) (0.255)
Share of Employment - Impacted Industries 0.003 –0.149 –0.152 0.147∗
(0.055) (0.113) (0.114) (0.079)
Share of Work Done Remotely 0.102 0.134 0.134 –0.417
(0.091) (0.086) (0.087) (0.693)
Share of Minors 0.205 –0.201 –0.200 0.437∗
(0.155) (0.165) (0.164) (0.237)
Rural County Dummy 0.004
(0.010)
Most Populous County (Top 1%) 0.068∗∗∗ 0.054∗∗
(0.021) (0.021)
Ln(Residential Population) –0.027∗∗∗ –0.023∗∗∗ –0.023∗∗∗ –0.034∗∗∗
(0.005) (0.008) (0.008) (0.010)
Commuter to Residential Population Ratio –0.015 –0.008 –0.006 –0.034
(0.029) (0.030) (0.030) (0.059)
Ln Median Family Income 0.014 0.003 0.002 0.036
(0.027) (0.033) (0.034) (0.049)
Community Bank Share of Deposits 0.037∗∗ 0.075∗∗∗ 0.075∗∗∗ 0.012
(0.017) (0.019) (0.019) (0.024)
Big4 Bank Share of Deposits 0.093∗∗∗ 0.139∗∗∗ 0.137∗∗∗ 0.003
(0.033) (0.039) (0.040) (0.054)
Ln Bank Branch Density 0.000 0.001 0.000 0.004
(0.009) (0.015) (0.015) (0.015)
SBL Volume per Estab< 500 (QCEW 2019 Avg) –0.002∗∗∗ –0.001∗∗ –0.001∗∗ –0.002∗∗∗
(0.000) (0.000) (0.000) (0.000)
Ratio of s Small (Under 500) Employment in 2020Q1 to 2019Q1, QWI –0.026 –0.091 –0.091 0.011
(0.049) (0.080) (0.080) (0.066)
UB replacement rate, industry weighted –0.020 0.030 0.027 –0.035
(0.049) (0.074) (0.074) (0.064)
Constant 0.585 0.970 1.005 0.206
(0.436) (0.707) (0.708) (0.619)
Adjusted R-squared 0.14 0.18 0.18 0.11
Observations 2710 1120 1110 1590
Notes: Results from regressions of the share delayed on selected county-level characteristics. “Smaller” refers to urban
counties excluding those in the top 1 percent by population. All regressions include state fixed effects. Standard errors
clustered at the state level in parentheses. Data sources described in Section 2.2.
39
Table 3: Summary Statistics: County-Level Urban QWI Sample
County-Level Total
Mean SD Aggregate
PPP Receipt
Share of PPP Loans Delayed 0.44 0.14 0.43
Share of PPP Loans Delayed to < 20 0.49 0.11 0.48
Total PPP Volume (in Millions) for 2020 391.93 1,010.10 449,148.69
Total PPP Volume (in Millions) for 2020+2021 555.01 1,472.41 636,041.15
Total PPP Volume for < 20 (in Millions) for 2020 119.27 303.26 136,684.23
Total PPP Volume for < 20 (in Millions) for 2020+2021 186.16 491.10 213,341.68
Employment
Population 16+ (in Thousands), 2019 190.93 413.55 218,803.13
Employment All Estabs (in Thousands), QCEW 2019 94.18 229.31 107,934.07
Stable Employment All Estabs (in Thousands), QWI 2019 84.68 211.40 97,045.02
Stable Employment < 500 Estabs (in Thousands), QWI 2019 39.74 95.79 45,545.45
Stable Employment < 20 Estabs (in Thousands), QWI 2019 14.73 37.43 16,878.84
Mthly Total Payroll (All Establ, in Millions), QWI 2019 463.66 1,417.86 531,351.34
Mthly Payroll < 500 Estabs (in Millions), QWI 2019 182.95 510.02 209,660.43
Mthly Payroll < 20 Estabs (in Millions), QWI 2019 57.73 160.94 66,163.10
Share of Stable Employment < 500, QWI 2019 0.55 0.13 0.47
Share of Stable Employment < 20, QWI 2019 0.23 0.09 0.17
Share of Mthly Earnings < 500, QWI 2019 0.50 0.14 0.39
Share of Mthly Earnings < 20, QWI 2019 0.18 0.08 0.12
Establishments
Private Establishments (in Thousands), CBP 2019Q1 5.90 14.06 6,760.71
Share of Establishments < 500, CBP 2019Q1 1.00 0.01 1.00
Share of Establishments < 20, CBP 2019Q1 0.86 0.04 0.85
PPP to Payroll
PPP to (Mthly) Total Payroll, 2020 1.10 0.41 0.85
PPP to (Mthly) Total Payroll, 2020 +2021 1.53 0.58 1.20
PPP < 20 to (Mthly) Total Payroll, 2020 0.40 0.19 0.26
PPP < 20 to (Mthly) Total Payroll, 2020 +2021 0.60 0.30 0.40
PPP to (Mthly) < 500 Payroll , 2020 2.20 0.46 2.14
PPP to (Mthly) < 500 Payroll , 2020 +2021 3.06 0.61 3.03
PPP < 20 to < 20 (Mthly) Payroll , 2020 2.16 0.35 2.07
PPP < 20 to < 20 (Mthly) Payroll , 2020 +2021 3.29 0.58 3.22
Observations 1146
Notes: This table provides county-level and aggregate statistics for the urban sample used in our
regressions based on QWI data. Whenever possible, statistics are provided for two establishment-
size categories (fewer than 20, and fewer than 500 employees per establishment). Measures related
to PPP loans to establishments with fewer than 20 employees (< 20) exclude loans to the self-
employed (i.e, we exclude borrowers who reported one or fewer jobs saved and received no more
than $20,833, the maximum allowed for self-employed individuals). Data sources described in Sec-
tion 2.2.
40
Table 4: Effects of Share of PPP Loans Delayed on Stable Employment in
Establishments with Under 20 Employees, QWI
(1) (2) (3) (4) (5) (6) (7) (8)
All Counties Urban Counties
Level Log E/P ∆E/P Level Log E/P ∆E/P
2020Q2 × Share Delayed 0.04 0.01 0.14 0.12 –0.41 –0.02 –0.09 0.04
(0.12) (0.01) (0.09) (0.10) (0.71) (0.02) (0.10) (0.12)
2020Q3 × Share Delayed –0.02 –0.00 –0.02 –0.06 –0.62 –0.06*** –0.28** –0.17
(0.13) (0.01) (0.12) (0.15) (0.82) (0.02) (0.12) (0.13)
2020Q4 × Share Delayed 0.04 0.01 0.02 –0.01 –0.17 –0.05** –0.26* –0.15
(0.10) (0.01) (0.09) (0.11) (0.58) (0.02) (0.14) (0.13)
2021Q1 × Share Delayed 0.06 0.00 0.03 –0.00 –0.18 –0.06*** –0.29*** –0.19
(0.10) (0.01) (0.11) (0.11) (0.60) (0.02) (0.09) (0.12)
2021Q2 × Share Delayed 0.12 0.01 0.05 0.04 0.03 –0.06*** –0.22** –0.13
(0.10) (0.02) (0.12) (0.13) (0.58) (0.02) (0.10) (0.12)
2021Q3 × Share Delayed –0.05 –0.02 –0.16 –0.18 –0.47 –0.09*** –0.42** –0.36*
(0.12) (0.02) (0.14) (0.16) (0.72) (0.02) (0.17) (0.20)
2021Q4 × Share Delayed 0.13 –0.01 –0.11 –0.11 0.13 –0.07*** –0.33*** –0.24**
(0.11) (0.02) (0.12) (0.14) (0.58) (0.02) (0.10) (0.12)
Avg. LHS 6.09 7.39 7.33 –0.25 14.05 8.45 6.67 –0.29
Std. Dev. LHS 22.63 1.47 3.16 0.80 35.63 1.50 2.12 0.56
Share Delayed 0.51 0.51 0.51 0.51 0.49 0.49 0.49 0.49
Within R-squared 1.00 1.00 0.93 0.12 1.00 1.00 0.96 0.24
Observations 24,525 24,525 24,525 24,525 9,142 9,142 9,142 9,142
State FE, Time FE, Lag LHS Yes Yes Yes Yes Yes Yes Yes Yes
Pre-conditions Controls Yes Yes Yes Yes Yes Yes Yes Yes
Covid-19 Controls Yes Yes Yes Yes Yes Yes Yes Yes
Notes: Results from estimating Equation (1). Standard errors clustered at the state level in parentheses. Sam-
ples of all counties and urban counties. Employment in columns (1) and (6) is in thousands. All regressions
control for state, quarter-year fixed effects, and a lag of the dependent variable (last quarter of 2019), in ad-
dition to preexisting conditions and COVID-19 controls. Preexisting conditions: median family income,
share of minors, commuter-to-residential-population ratio, indicators for 2013 NCHS urban-rural designation,
community-bank share of deposits, largest four banks’ share of deposits, bank branch density, and 2019 small-
business-loan volume per small establishment. COVID-19 controls: cumulative COVID-19 cases and deaths
per population, share of days in April 2020 in early lockdown, share of remote jobs, share of employment in
essential industries, and share of employment in most impacted industries. Share Delayed is the share (by vol-
ume) of county-level PPP loans delayed as defined in Equation (2). The reference period is the first quarter
of 2020.
41
Table 5: PPP Receipt and Small-Establishment Payroll: First Stage
(1) (2)
All PPP PPP to < 20
IV < 500 Payroll Share < 20 Payroll Share
2020Q2 × Payroll Share 2.08*** 2.00***
(0.09) (0.09)
2020Q3 × Payroll Share 2.08*** 2.00***
(0.09) (0.09)
2020Q4 × Payroll Share 2.08*** 2.00***
(0.09) (0.09)
2021Q1 × Payroll Share 2.92*** 3.05***
(0.13) (0.16)
2021Q2 × Payroll Share 2.91*** 3.06***
(0.13) (0.16)
2021Q3 × Payroll Share 2.91*** 3.05***
(0.13) (0.16)
2021Q4 × Payroll Share 2.91*** 3.06***
(0.13) (0.16)
Within R sq. 0.61 0.83
Observations 9,142 9,142
State FE, Time FE Yes Yes
Pre-conditions Controls Yes Yes
COVID-19 Controls Yes Yes
Notes: Regression of PPP receipt by the end of the indicated quarter-
year on payroll share and (time-varying) controls. The regression in col-
umn (1) can be interpreted as the first stage regression of the IV regres-
sions in columns (2) and (4) of Table 6, while the regression in column (2)
corresponds to the first stage of column (6) in Table 6.
42
Table 6: Funding Receipt versus Funding Delay. Urban Counties
(1) (2) (3) (4) (5) (6)
QCEW QWI (stable)
All All Under 20
OLS IV OLS IV OLS IV
2020Q2 × PPP per Total Payroll 1.25*** 3.06*** 0.43*** 0.76*** 0.09 0.05
(0.23) (0.57) (0.12) (0.21) (0.08) (0.11)
2020Q3 × PPP per Total Payroll 1.19*** 2.38*** 0.88*** 1.74*** 0.44*** 0.43***
(0.25) (0.60) (0.17) (0.29) (0.10) (0.11)
2020Q4 × PPP per Total Payroll 0.70*** 1.31** 0.75*** 1.28*** 0.34*** 0.25***
(0.17) (0.53) (0.14) (0.27) (0.07) (0.08)
2021Q1 × PPP per Total Payroll 0.33*** 0.84** 0.41*** 0.65*** 0.18*** 0.14**
(0.12) (0.40) (0.09) (0.18) (0.04) (0.06)
2021Q2 × PPP per Total Payroll 0.70*** 1.29*** 0.55*** 1.03*** 0.20*** 0.18***
(0.13) (0.42) (0.08) (0.20) (0.05) (0.06)
2021Q3 × PPP per Total Payroll 0.91*** 1.36*** 0.75*** 1.26*** 0.46*** 0.45***
(0.17) (0.46) (0.11) (0.25) (0.12) (0.13)
2021Q4 × PPP per Total Payroll 0.38*** 0.67 0.52*** 0.92*** 0.27*** 0.27***
(0.14) (0.47) (0.10) (0.24) (0.07) (0.08)
2020Q2 × Share Delayed 1.71* 1.47 0.45* 0.42* 0.04 0.04
(0.86) (0.88) (0.25) (0.25) (0.12) (0.11)
2020Q3 × Share Delayed 0.51 0.37 0.65 0.54 –0.21 –0.21
(0.64) (0.63) (0.40) (0.40) (0.15) (0.14)
2020Q4 × Share Delayed 0.16 0.10 0.28 0.23 –0.18 –0.17
(0.41) (0.39) (0.41) (0.41) (0.15) (0.14)
2021Q1 × Share Delayed –0.09 –0.21 0.09 0.04 –0.22* –0.21*
(0.45) (0.44) (0.42) (0.42) (0.12) (0.12)
2021Q2 × Share Delayed –0.18 –0.32 0.32 0.21 –0.17 –0.16
(0.63) (0.60) (0.42) (0.41) (0.12) (0.12)
2021Q3 × Share Delayed –0.00 –0.10 0.18 0.06 –0.44** –0.44**
(0.80) (0.75) (0.46) (0.45) (0.21) (0.21)
2021Q4 × Share Delayed –0.20 –0.26 0.09 –0.01 –0.29** –0.29**
(0.66) (0.62) (0.44) (0.43) (0.12) (0.13)
Avg. LHS –1.89 –1.89 –1.49 –1.49 –0.29 –0.29
Avg. PPP/Payroll 1.34 1.34 1.34 1.34 0.51 0.51
Share Delayed 0.44 0.44 0.44 0.44 0.49 0.49
Pop 16+, thousands 190.8 190.9 190.8 190.9 190.8 190.9
KP Wald F 96.3 95.8 48.8
AR Wald χ2 134.4 74.8 48.7
AR Wald p-val. 0.00 0.00 0.00
Observations 9,142 9,142 9,142 9,142 9,142 9,142
State FE, Time FE, Lag LHS Yes Yes Yes Yes Yes Yes
Pre-conditions Controls Yes Yes Yes Yes Yes Yes
COVID-19 Controls Yes Yes Yes Yes Yes Yes
Notes: Results from estimating augmented Equation (1). The LHS is the county-level change in
employment relative to 2019 population in the category indicated in the column headings. Stan-
dard errors clustered at the state level in parentheses. All regressions control for state, quarter-year
fixed effects, and a lag of the dependent variable (last quarter of 2019), in addition to preexist-
ing conditions and COVID-19 controls. Preexisting conditions: median family income, share
of minors, commuter-to-residential-population ratio, indicators for 2013 NCHS urban-rural designa-
tion, community-bank share of deposits, largest four banks’ share of deposits, bank branch density,
and 2019 small-business-loan volume per small establishment. COVID-19 controls: cumulative
COVID-19 cases and deaths per population, share of days in April 2020 in early lockdown, share of
remote jobs, share of employment in essential industries, and share of employment in most impacted
industries. Share Delayed is the share (by volume) of county-level PPP loans delayed, as defined in
Equation (2) for all loans in columns (1)–(6), and for loans whose applicants reported fewer than
20 employees in columns (7)–(8). PPP per total payroll in columns (7)–(8) is specific to establish-
ments with under 20 employees and excludes loans to the self employed. The instrument is the 2019
share of total payroll in establishment with fewer than 500 employees in columns (1)–(6) and the
2019 share of total payroll in establishment with fewer than 20 employees in columns (7)–(8). The
reference period is the first quarter of 2020.
43
Table 7: Job-Years Retained by PPP Receipts and Implied Cost
Total Employment, QCEW Stable Employment, QWI
Baseline: Total PPP by year
All All Under 20
Job-year saved
2020 3,124,115 1,743,543 103,223
2021 2,722,683 2,532,101 229,067
Total 5,846,798 4,275,644 332,290
Cost per job-year $88,997 $127,179 $546,777
Total PPP (2020+2021)
All All Under 20
Job-year saved
2020 3,156,332 1,762,309 105,299
2021 2,721,992 2,530,567 228,888
Total 5,878,324 4,292,876 334,187
Cost per job-year $108,201 $148,162 $638,390
Cumulative PPP
All All Under 20
Job-year saved
2020 3,118,488 1,742,294 103,109
2021 2,724,361 2,533,553 229,675
Total 5,842,849 4,275,847 332,784
Cost per job-year $87,503 $125,593 $539,165
Notes: This table presents estimates of job-years saved and the associated costs under
different scenarios of PPP receipt anticipation. All scenarios assume past receipts af-
fected job retention/creation until the end of the sample, 2021:Q4. The baseline panel
uses the estimates of Table 6 and the aggregate values in Table 3. Job-years
retained are
PPP pop
calculated by rearranging the terms in Equation (1): ∆E = β payroll 100 . The result-
ing numbers are summed up for the corresponding quarters and divided by 4 to convert
to job-years. The implied cost is computed by dividing the ultimate total PPP outlay at
the end of the entire program (May 31, 2021) by the number of job-years saved. In the
baseline scenario, jobs retained over 2020 must be scaled up to account for the fact that
only a portion (roughly $525 out of $800 billion) of the ultimate outlay was disbursed
in the 2020 PPP. The scaling factor is thus the ratio of ultimate PPP outlay over 2020
outlay, equivalent to the PPP/payroll ratio at program end in 2021 relative 2020. Anal-
ogous (but in this case quarter by quarter) scaling is needed to compute the implied cost
in the Cumulative-PPP scenario (i.e., the RHS is the cumulative PPP received up to a
given quarter).
44
Table 8: Summary Statistics: Firm-Level Advan Sample
N(Pairs) Mean P25 Median P75
PPP Business Avg. Weekly Visits 65,136 43.45 8.23 21.85 49.08
% Diff. in Visits: PPP vs. non-PPP Business 65,136 0.02 -2.42 0.00 2.48
Distance (Miles): PPP vs. non-PPP Business 65,136 13.65 7.96 11.64 17.14
PPP Loan Size ($1,000) 65,136 139.01 21.89 49.10 114.30
No. of Jobs Saved 65,136 18.74 4.00 8.00 17.00
Early DK PPP Firms
PPP Business Avg. Weekly Visits 8,575 44.70 8.31 22.00 48.85
% Diff. in Visits: PPP vs. non-PPP Business 8,575 0.02 -2.46 0.00 2.52
Distance (Miles): PPP vs. non-PPP Business 8,575 13.51 7.97 11.59 16.98
PPP Loan Size ($1,000) 8,575 169.98 29.40 63.20 142.76
No. of Jobs Saved 8,575 21.28 5.00 10.00 20.00
Late DK PPP Firms
PPP Business Avg. Weekly Visits 8,870 42.00 8.08 21.15 47.31
% Diff. in Visits: PPP vs. non-PPP Business 8,870 0.03 -2.43 0.00 2.48
Distance (Miles): PPP vs. non-PPP Business 8,870 13.65 8.00 11.75 17.31
PPP Loan Size ($1,000) 8,870 133.29 23.31 51.35 116.38
No. of Jobs Saved 8,870 17.63 4.00 8.00 17.00
Notes: 2020 PPP recipient firms are matched to non-PPP firms that operate in the same
6-digit NAICS industry, have similar pre-pandemic visits (within 5% between December 2019
and February 2020) and are located in the same county and between 5 and 50 miles away.
Early DK PPP firms are those that received PPP loans between April 14 and 16, 2020, while
late DK PPP firms received loans on April 27 and 28, 2020, as defined in Doniger and Kay
(2023). The sample excludes the self-employed. Business visits are averages for the months of
December 2019 to February 2020.
45
Figure 1: Effect of Share Delayed on Total Private Employment, QCEW
All Counties
Level of Employment Log of Employment
1 .04
.02
0
Coefficients
0
-.02
-1
-.04
-2 -.06
Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021 Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021
Emp. /Pop 16+ ∆Emp. /Pop 16+
4
2
2
0
Coefficients
0
-2
-2
-4
-4
-6
Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021 Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021
Notes: Coefficients for the share delayed, defined in Equation (2), estimated using Equation (1). All
regressions control for state, month-year fixed effects, and a lag of the dependent variable (as of Decem-
ber 2019), in addition to preexisting conditions and COVID-19 controls. The reference period is the
February 2020, as indicated by the vertical dotted lines. Standard errors clustered at the state level.
Employment levels are measured in thousands. Preexisting conditions: median family income, share
of minors, commuter-to-residential-population ratio, indicators for 2013 NCHS urban-rural designation,
community-bank share of deposits, largest four banks’ share of deposits, bank branch density, and 2019
small-business-loan volume per small establishment. COVID-19 controls: cumulative COVID-19
cases and deaths per population, Stringency index, share of days in April 2020 in early lockdown, share
of work done remotely, share of employment in essential industries, and share of employment in most
impacted industries. Most Impacted industries include NAICS 44-45, 61, 71, 72 and 81.
46
Figure 2: Effect of Share Delayed on Total Private Employment, QCEW
Urban versus Rural Counties
Urban Counties Rural Counties
Level of Employment Level of Employment
.2
2
0
.1
Coefficients
-2
0
-4
-6
-.1
Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021 Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021
Log of Employment Log of Employment
.1 .05
.05 0
Coefficients
0
-.05
-.05
-.1
Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021 Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021
Emp. /Pop 16+ Emp. /Pop 16+
3
2
2
0
Coefficients
1
-2
0
-1 -4
-2 -6
Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021 Jan 2020 Mar 2020 May 2020 Jul 2020
Sept 2020 Nov 2020 Jan 2021 Mar 2021 May 2021 Jul 2021
Sept 2021 Nov 2021
∆Emp. /Pop 16+ ∆Emp. /Pop 16+
6
2
4
0
Coefficients
2
-2
0 -4
-2 -6
Jan 2020 Mar 2020 Sept 2020 Nov 2020 Jan 2021 Mar 2021 Sept 2021 Nov 2021 Jan 2020 Mar 2020 Sept 2020 Nov 2020 Jan 2021 Mar 2021 Sept 2021 Nov 2021
May 2020 Jul 2020 May 2021 Jul 2021 May 2020 Jul 2020 May 2021 Jul 2021
Notes: Coefficients for the share delayed, defined in Equation (2), estimated using Equation (1). All
regressions control for state, month-year fixed effects, and a lag of the dependent variable (as of Decem-
ber 2019), in addition to preexisting conditions and COVID-19 controls. The reference period is the
February 2020, as indicated by the vertical dotted lines. Standard errors clustered at the state level.
Employment levels are measured in thousands. Preexisting conditions: median family income, share
of minors, commuter-to-residential-population ratio, indicators for 2013 NCHS urban-rural designation,
community-bank share of deposits, largest four banks’ share of deposits, bank branch density, and 2019
small-business-loan volume per small establishment. COVID-19 controls: cumulative COVID-19
cases and deaths per population, Stringency index, share of days in April 2020 in early lockdown, share
of work done remotely, share of employment in essential industries, and share of employment in most
impacted industries.
47
Figure 3: Evolution of Employment
All Establishments Establishments under 20
0 0
-1 -1
-2 -2
-3 -3
-4 -4
-5 -5
2019q4 2020q2 2020q4 2021q2 2021q4 2019q4 2020q2 2020q4 2021q2 2021q4
QCEW QWI, Stable QWI Stable
Notes: The figure shows the change in employment to 2019 population relative to the last quarter of 2019,
E −E2019:Q4
or ∆et = t P2019 × 100. Mean across counties in our urban regression sample.
48
Figure 4: Correlation of PPP receipts and Payroll Share
PPP to All Establishments PPP to under 20 Establishments
8 4
2021 Correlation = 0.69 2021 Correlation = 0.91
2020 Correlation = 0.68 2020 Correlation = 0.91
6 3
PPP relative to Payroll PPP relative to Payroll
4 2
2 1
0 0
0 .2 .4 .6 .8 1 0 .2 .4 .6
Under 500 Payroll Share (IV) Under 20 Payroll Share (IV)
Total PPP by the end of 2020 Total PPP by the end of 2021
Notes: The sample underlying this figure includes only counties in our urban-regression sample. For
both panels, the corresponding PPP receipts are normalized by total monthly payroll in each county. To
facilitate interpretation of the left panel, note that with an under-500 payroll share of 1, all employment
would be in establishments with under 500 employees, implying a maximum PPP-to-payroll ratio of about
2.5 in 2020 (10 weeks, or equivalently 2.5 months, of payroll). With a share of 0.5, the predicted maximum
would be 1.25 (that is, 0.5×2.5). Actual ratios would differ if some eligible businesses did not borrow, some
borrowers exceeded 500 employees, certain ineligible firms borrowed, or due to other irregularities. In the
right panel, we plot PPP receipts specific to under-20-employee establishments relative to total payroll (on
the y axis) against under-20 payroll share (x axis), but the interpretation is analogous.
49
Figure 5: Correlation of PPP receipts and Share Delayed
PPP Receipts and Share Delayed PPP Receipts and Share Delayed
All Establishments Under 20 Establishments
8 4
2021 Correlation = 0.10 2021 Correlation = 0.13
2020 Correlation = 0.08 2020 Correlation = 0.13
6 3
PPP relative to Payroll PPP relative to Payroll
4 2
2 1
0 0
0 .2 .4 .6 .8 1 0 .2 .4 .6 .8 1
share delayed share delayed
Total PPP by the end of 2020 Total PPP by the end of 2021
Notes: PPP receipts on both panels are normalized by total monthly payroll in each county. The share
delayed is defined in Equation (2). Counties in our urban regression sample.
50
Figure 6: Stable Employment Evolution based on 2019 payroll and DK delay, QWI
All Establishments
Share Payroll under 500 Share Delayed
6 6
4 4
2 2
0 0
-2 -2
-4 -4
2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1 2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1
(a) Basic Controls
Share Payroll under 500 Share Delayed
6 6
4 4
2 2
0 0
-2 -2
-4 -4
2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1 2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1
(b) All Controls
Notes: Let et = E Pt × 100 and ∆et = et − et−4 . The figures plot βt and γt from the regression ∆et =
t
α + βt share2019 + γt delay + ζt L4.∆et + Xt Πt + ϵt . Regressions also include state and quarter-year fixed
effects. The bottom panel regressions include all controls in our baseline regressions (including banking
variables) adjusted to the relevant time period whenever possible. The top panel excludes Xt Πt .
51
Figure 7: Stable Employment Evolution based on 2019 payroll and DK delay, QWI
Establishments under 20 Employees
Share Payroll under 20 Share Delayed
2 2
1 1
0 0
-1 -1
2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1 2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1
(a) Basic Controls
Share Payroll under 20 Share Delayed
2 2
1 1
0 0
-1 -1
-2 -2
2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1 2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1
(b) All Controls
Notes: Let et = E Pt × 100 and ∆et = et − et−4 . The figures plot βt and γt from the regression ∆et =
t
α + βt share2019 + γt delay + ζt L4.∆et + Xt Πt + ϵt . Regressions also include state and quarter-year fixed
effects. The bottom panel regressions include all controls in our baseline regressions (including banking
variables) adjusted to the relevant time period whenever possible. The top panel excludes Xt Πt .
52
Figure 8: Effect of PPP on Visits
Matching Estimates using Advan Firm Pairs
Log Visits over Calendar Time Log Visits over Event Time
.2 .2
April 2020 January 2021
Average Effect Average Effect
0 .1 0 .1
-.1 -.1
Dec2018 Dec2019 Dec2020 Dec2021 -16 -12 -8 -4 0 4 8 12 16 20
Month Months Relative to Loan Approval
Pr(Zero Visits) over Calendar Time Pr(Zero Visits) over Event Time
.02 .02
Average Effect Average Effect
-.04 -.02 0 -.04 -.02 0
April 2020 January 2021
-.06 -.06
Dec2018 Dec2019 Dec2020 Dec2021 -16 -12 -8 -4 0 4 8 12 16 20
Month Months Relative to Loan Approval
Notes: The left panels plot the βt coefficients estimated from Equation (5), while the right panels plot the
µl coefficients from Equation (6). 2020 PPP recipient firms are matched to non-PPP firms that operate in
the same 6-digit NAICS industry, have similar pre-pandemic visits (within 5% between December 2019 and
February 2020) and are located in the same county and between 5 and 50 miles away. The sample excludes
the self-employed. Log visits are defined as the log of visit counts plus one. Zero visits is a dummy equal
to one when Advan records zero visits or when missing observations are filled in. Shaded areas represent
95 percent confidence intervals, with standard errors clustered by firm pair.
53
Figure 9: Effect of PPP on Visits
Early versus Late PPP Recipients in Advan
Log Visits over Calendar Time Log Visits over Event Time
Average Effect Average Effect
April 2020 January 2021
-.05 0 .05 .1 .15 .2 -.05 0 .05 .1 .15 .2
Dec18 Jun19 Dec19 Jun20 Dec20 Jun21 Dec21 -16 -12 -8 -4 0 4 8 12 16 20
Month Months Relative to Loan Approval
Pr(Zero Visits) over Calendar Time Pr(Zero Visits) over Event Time
Average Effect Average Effect
-.06 -.04 -.02 0 .02 -.06 -.04 -.02 0 .02
April 2020 January 2021
Dec18 Jun19 Dec19 Jun20 Dec20 Jun21 Dec21 -16 -12 -8 -4 0 4 8 12 16 20
Month Months Relative to Loan Approval
Early DK PPP Firms Late DK PPP Firms
Notes: These graphs compare PPP’s effects on visits depending on the date of loan approval. Early firms
are those that received PPP loans between April 14 and 16, 2020, while late firms received loans on
April 27 and 28, 2020, as defined in Doniger and Kay (2023). PPP firms are matched to non-PPP firms
that operate in the same 6-digit NAICS industry, have similar pre-pandemic visits (within 5% between
December 2019 and February 2020) and are located in the same county and between 5 and 50 miles away.
The sample excludes the self-employed. The shaded areas represent 95 percent confidence intervals, with
standard errors clustered by firm pair.
54
Online Appendix – Not for Publication
A Data: Additional Details
Pre-pandemic Local Conditions
The Quarterly Census of Employment and Wages (QCEW) reports employment
data at a monthly frequency, while the total number of establishments and payroll
(wages) at a quarterly frequency. According to QCEW, right before the COVID-19
outbreak, there were, on average, about 39,500 employees working in 3,000 establish-
ments (Table 1) in an average county.
On average, a county had about 27.5 bank branches serving around 104,500 people,
corresponding to a commuter-adjusted daytime population of 120,000, with a median
family income of $66,500 (Table 1). In 2019, an average county received 2,320 small
business loans (SBL) with a total volume of $80.31 million and an average amount of
$35,000. In our sample, 63 percent of counties are classified as rural according to the
2013 National Center for Health Statistics (NCHS) urban-rural classification scheme.
We classify a county as rural if its urban-rural 2013 classification scheme is greater than
4 (the scale of population density ranges from 1 to 6, from most to least populated).
On average, a rural county has a population of 23,650 people vs. 240,400 living in an
urban county. Rural population accounts for 14 percent of the total population in our
sample.
Public Health Measures and Relative Size of the PPP
In mid-March 2020, in response to the pandemic, the federal, state, and local govern-
ments instituted non-pharmaceutical interventions to curb the spread of the COVID-19
virus, which led to a significant drop in employment, especially for small businesses.
The Coronavirus Aid, Relief, and Economic Security (CARES) Act was introduced to
reduce the economic impact of mandatory shutdowns. In April 2020, an average county
had received 907 PPP loans for a total of $133 million and an average loan of $97,200.
However, 48 percent of PPP loans were delayed (58 percent if we use the total number
of delayed loans instead of the volume of loans) because PPP funding ran out on April
16 and was reinstated on April 27 (see Table 1). By August 2020, the average county
had received a total volume of $188 million. Importantly, the volume of 2020 PPP loans
substantially exceeded each county’s SBL volume in 2019. In fact, by the end of April
2020, each county had already received, on average, almost twice the 2019 SBL volume
in PPP funding, and this multiple increased to three by the end of the 2020 PPP.
B Evolution of the PPP Provisions and Their Potential Im-
plications
The 2020 CARES Act, signed into law on March 27, 2020, appropriated $349 billion in
PPP loans in response to the widespread shutdowns caused by the COVID-19 pandemic.
The PPP funds were provided to businesses that employed no more than 500 workers
so that they would have the resources to maintain or hire back employees that had been
laid off, and to cover overhead costs incurred as a result of the pandemic. This section
describes the changes in program rules over time, and their potential implications for
55
the relative trajectory of employment recovery in urban centers, which were hit hard
by the outbreak and were fundamentally more likely to suffer longer-lasting damages.
Several key provisions in the CARES Act for the PPP were later modified in the
Paycheck Protection Program Flexibility Act (PPPFA).1 Four of these amended pro-
visions had the greatest potential to slow the recovery of employment after the initial
acute phase of the pandemic, especially in places that were hardest hit by the initial
outbreak. This effect carries the same sign as that of the delay in funding or lack of
funding for small businesses. More importantly, the likely amendments to the original
CARES Act provisions became known before April 27, 2020, when bank lending under
the PPP resumed with the additional funding appropriation, and thus it could have
led to differential behavior of firms that received loans just before the 10-day window
(referred to as the early recipients) versus those that received loans just after the win-
dow (the late recipients). In other words, the cross-sectional disparity in the impact of
these amendments could be correlated with the degree of funding delay.
First, the PPPFA extended the period in which borrowers could spend their PPP
funds in order to be considered for loan forgiveness from eight weeks following the date
of the loan (that is, disbursement of loan proceeds) to the earlier of 24 weeks following
the date of the loan or December 31, 2020. However, businesses that obtained PPP loans
before the effective date of the PPPFA could elect to use the original eight-week period,
allowing them to apply for forgiveness earlier. The proposal to extend the covered period
was first raised by the Main Street Alliance on April 22, 2020, and was reported by
the Adhesives & Sealants Industry Magazine on April 23. On April 29, 2020, it was
reported by all journals (including the Portland Business Journal ) under the umbrella
of American City Business Journals. The Small Business & Entrepreneurship Council
more specifically proposed the 24-week expansion on April 30, which was then reported
by the Wall Street Journal on May 3, 2020.2
The PPPFA also changed the loan proceeds use formula from 75 percent on payroll
and 25 percent on eligible fixed expenses (such as rent, interest on debt, and utilities)
to 60 percent on payroll and 40 percent on other eligible expenses. The formula change
was first reported by a major news outlet, USA Today, on April 20, 2020. That article
noted that the trade publication Nation’s Restaurant News reported a similar proposed
change to the formula on April 9, 2020. This provision permitted borrowers to keep or
hire back fewer employees because the firms were required to spend less of a given PPP
loan on payroll. The amount of a loan was still capped at 2.5 months of pre-pandemic
payroll.
Perhaps more importantly, the PPPFA relaxed the requirement that borrowers must
rehire employees by June 30, 2020: The amount that could potentially be forgiven would
not be reduced due to a decrease in the borrower’s full-time equivalent (FTE) work-
force count if the firm could document that it (1) attempted, but was unable, to rehire
previous employees as of February 15, 2020; and (2) was unable to hire “similarly qual-
ified employees” before December 31, 2020. This change was implemented to recognize
that some businesses may not have been allowed to reopen by June 30, 2020, and even
if they were allowed to reopen by that date, they may have had to reopen in stages,
allowing them to hire back employees over a longer period of time.
1
The PPPFA passed the House on May 28, 2020, and the Senate on June 3 of that year. It was
signed into law on June 4, 2020.
2
See ASI and SBE Council.
56
Additionally, the amount potentially forgiven would not be reduced due to a de-
crease in the FTE workforce count if the borrower, in good faith, could document an
inability to return to the “same level of business activity” with which it operated prior
to February 15, 2020, due to sanitation, social distancing, or safety requirements for
workers or customers. This provision recognized that businesses may not have been
able to locate and hire qualified employees, because in many industries, the workforce
could have relocated due to the pandemic and become unavailable to employers. These
last two provisions made it less or not at all necessary for businesses to operate at close
to their pre-pandemic levels by June 30, and businesses could cut back permanently yet
still have their PPP loans forgiven. This change, among all the changes described so far,
can probably best help explain the persistent effect of the 10-day delay on employment
in those hardest hit industries.
News about the broad contour of potential changes to the PPP program (resembling
the actual changes just described) that might be incorporated into a new bill to enhance
the program’s flexibility started circulating widely as early as April 11, 2020, when it
was reported by the New York Times and the Washington Post.3 Also, a bipartisan
group of House representatives sent a letter to House leadership on April 16 requesting
greater flexibility in the program in order to better assist small businesses.4 These dates
suggest that many small businesses, if they had already closed early due to the outbreak
and the resulting containment measures, could reasonably begin to reconsider over the
10 days (when additional funding appropriation for the PPP was going through the
legislative process) their reopening plan. To the extent that a higher fraction of late
borrowers had closed by April 27, 2020, when PPP lending resumed, the additional
“options” offered by the new provisions would have greater impact on late borrowers
than on early borrowers. This effect is likely more pronounced for businesses in urban
centers, which had been much more severely disrupted at the outset and thus more
likely to have closed before the PPP restarted.
In sum, several important changes became widely anticipated by small businesses
over the 10-day period of funding delay that could lead to reoptimization, in particular
to delaying reopening, since businesses could reasonably expect a much longer period
over which to spend the funding without having to worry about a reduced amount
of loan forgiveness. This incentive to delay reopening should be particularly strong
for May and June 2020, when demand was far from fully recovered. With the program
changes, businesses were able to preserve PPP funds for later use (to pay employees and
fixed operating expenses) when they could expect a higher volume of demand and/or
when the public health situation improved sufficiently.
The incentive to wait was likely stronger for businesses that closed before April
27, since they would need to spend a fixed cost (such as restocking the kitchen or
store shelves) to reopen. Thus, it likely also applies more to essential businesses that
had chosen to close, along with all nonessential businesses, which had to shut down in
most states during the lockdown phase in response to the initial COVID-19 outbreak. In
addition, it should be more relevant for localities that experienced less demand recovery
in May and June, such as densely populated urban centers, because they were subject
3
Similar reporting appeared as early as April 8, 2020, in Maine’s Bangor Daily News and in Restau-
rant Hospitality, a trade publication.
4
This effort was led by representatives Abigail Spanberger, Brian Fitzpatrick, and Josh Gottheimer;
see this House webpage.
57
to greater mandatory containment measures or voluntary cutbacks in mobility (due
to greater perceived risk of infection, which could depend on many factors, including
higher density or media communication, not just actual infection rates).
More importantly, we argue that the option value of waiting was higher for small
firms that had not received PPP loans before the first round of funding ran out (on
April 16) because they were more likely to have closed due to the lack of liquidity.
In addition, they had not used any of the funds to pay and retain their employees
and thus faced no countervailing incentive to adhere to the original eight-week covered
period so that they could apply for loan forgiveness earlier. Moreover, it is possible
that, even among the recipients within the set considered for the natural experiment
(that is, those that received loans over April 15 and 16 versus April 27 and 28—just
before versus just after the 10-day window of delay), the firms that received PPP loans
earlier had, on average, better prospects even without the PPP, which at the margin
made it more likely for them to have stayed open or to be better equipped to reopen
sooner when public health conditions improved sufficiently. To the extent that such
correlation is present, the difference in reopening dynamics observed cannot be solely
attributed to the lack of funding effects. Given that this is unobserved heterogeneity,
the only indication we can test is that such firms were more likely to have stayed open
prior to receiving any funding, if they were allowed to, under the assumption that their
better prospect made it more valuable for them to stay open (to gain market share
from their rivals, for example). At the level of the locality, the implication is that those
places with relatively higher shares of PPP loans delayed may have had higher shares
of firms with a poorer prospect, after we control for observables.
In conclusion, the general idea is that the effect of the PPP on employment is not
just due to the liquidity it provided, let alone the timing delay. Instead, it is also the
consequence of other design features of the PPP, as well as the cross-sectional difference
in inherent susceptibility to COVID-19 disruptions.
C IV estimates Subject to Imperfect Compliance
Imperfect compliance with the 500-employee threshold (as documented, for example, in
Splinter et al. 2025) could bias estimates of the LATE for compliers. However, this is
unlikely in our setting. As shown in Angrist, Imbens, and Rubin (1996), instrumental-
variable estimators using program assignment as an instrument for actual treatment
recover the correct LATE for compliers as long as there are no defiers among the
non-compliers. In the PPP setting, the non-compliant firms fall into two groups: i)
those with no more than 500 employees that did not borrow, and ii) those with more
than 500 employees that borrowed. To be a defier, a firm would need to act contrary
to its assignment. In other words, it would borrow when not eligible and not when
eligible. Intuitively, such behavior is likely to be extremely rare if it exists at all. More
plausibly, group i) consists of never-takers or firms that would not borrow regardless of
the eligibility threshold because they were not adversely affected, because they perceived
the costs (pecuniary or otherwise) as exceeding the benefits, or due to other idiosyncratic
reasons.5 Group ii) most likely includes firms eligible under exceptions to the 500
5
Note that small firms that went out of business before they could borrow due to congestion or
PPP funding delay are not defiers, since they did not act contrary to assignment: they would have
58
employee threshold or other qualifying criteria. These non-compliers are most likely
always-takers.
As long as non-compliance takes the form of always-takers and never-takers, the
standard IV estimator continues to identify the correct LATE for compliers. Accord-
ingly, our estimates of the job-years retained and the associated costs do not require
adjustments due to the imperfect compliance. This appendix discusses this issue in
more detail and also provides an alternative estimate that treats all non-borrower small
firms and borrower large firms as defiers. Our robustness check shows that, if anything,
our main results might underestimate the job-years retained.
When the monotonicity condition is violated, i.e., there are defiers among non-
compliers, the IV coefficient becomes a biased estimate of the LATE on compliers. As
clearly noted in Angrist, Imbens, and Rubin (1996) (Table 1 in particular), there can
be three types of non-compliers: never-takers, always-takers, and defiers. These types
are defined within the counterfactual framework, and it is not typically feasible to map
a type to an individual subject. Specific to the PPP setting, non-borrowers with 500
or fewer employees were not necessarily defiers but could simply be never-takers, i.e.,
they would not have borrowed regardless of the eligibility rule. In fact, this seems
more plausible than classifying them as defiers—that they would instead have taken
PPP funding had they been explicitly excluded. Likewise, borrowers with over 500
employees might not be defiers but simply always-takers. Unless we classify either or
both of the two subsets of firms as defiers, the standard IV coefficient remains valid as
a LATE estimate.
We use the notation and derivations à la Angrist, Imbens, and Rubin (1996) to show
this conclusion. Denote the potential outcome Y as a function of assignment Z and
treatment D, which is itself a function of Z (i.e., D(Z)), as Y (Z, D(Z)). Thus, compliers
and defiers are characterized by Pr(D(1) − D(0) = 1) and Pr(D(1) − D(0) = −1),
respectively, while never-/always-takers are those with Pr(D(1) − D(0) = 0). The
definitions of these types using the counterfactual notation makes it clear that it is
generally impossible to identify an individual i’s type because we only observe one of
the outcomes (e.g., the outcome of either D(0) or D(1)) but not both (D(0) or D(1)).
(Note that all these terms are defined at the individual level, but we omit the i subscript
for brevity.)
Denote the potential outcome if treated versus not Y (1) and Y (0), respectively.
Denote the coefficient from the IV regression of Y on treatment D using IV Z as β IV ,
the reduced-form coefficient of Y on Z and D on Z as θY and θD , respectively, and the
borrowed had they had a chance.
59
correct LATE estimate as β ∗ . When there is imperfect compliance, we can write:
β ∗ = E{Y (1) − Y (0) | D(1) − D(0) = 1} ≡ E{∆Y | complier},
θY = E{Y (1, D(1))} − E{Y (0, D(0))}
= E{Y (1) − Y (0) | D(1) − D(0) = 1} · Pr(D(1) − D(0) = 1)
− E{Y (1) − Y (0) | D(1) − D(0) = −1} · Pr(D(1) − D(0) = −1)
≡ E{∆Y | complier} Pr(complier) − E{∆Y | defier} Pr(defier)
θD = E{D(1) − D(0)}
= Pr(D(1) − D(0) = 1) − Pr(D(1) − D(0) = −1),
IV θY
β = D.
θ
It is clear that neither always-takers nor never-takers appear in θY or θD , because
for both types, Y (1, D(1)) − Y (0, D(0)) = 0 and D(1) − D(0) = 0. Once we rule out
defiers among non-compliers, β IV recovers β ∗ . In fact, as noted in Angrist, Imbens, and
Rubin (1996), the standard latent index specification of the relationship between D and
Z in the first stage implies that the monotonicity condition is implicitly satisfied.
If the monotonicity condition is violated due to defiers, then the bias β IV − β ∗ can
be expressed as follows:
Pr(defier)
(E{∆Y | complier} − E{∆Y | defier}) . (A.1)
Pr(complier) − Pr(defier)
The first term is the difference in treatment effects between compliers and defiers,
while the second term depends on the relative share of compliers and defiers. Without
defiers, the second term is zero and hence no bias. If there are defiers, the smaller the
share of defiers, the smaller the bias, ceteris paribus. (As noted already, we believe that
there should be essentially no defiers in the PPP setting.) In the unlikely event that
compliers and defiers have the same treatment effect, the bias is also zero.
However, we explore the most plausible situation concerning defiers in our setting.
In our setting, defiers would be firms that borrowed even though they did not qualify;
however, they would not have borrowed if they qualified for funding. As noted, this
definition, stated within the framework of counterfactuals, cannot be verified for any
individual firm because we only observe one outcome. To conduct robustness checks,
we lower the standard and thus expand the set of firms that we would classify as defiers
for this purpose. Specifically, we define all small establishments that did not borrow
and all large firms that borrowed as defiers. Compliers are small firms that borrowed
and large ones that did not. Among small establishments, defiers are on average smaller
than compliers, because the majority of small non-borrowers are among the smallest
establishments. Both our estimates and those of previous studies indicate that the
treatment effects are greater for smaller firms, especially the smallest establishments.
Thus, it is reasonable to assume that treatment effects are on average larger for defiers
than for compliers among small firms. At the same time, lacking evidence to the con-
trary, we assume the same treatment effect for compliers and defiers among large firms.
Combined with the additional assumption of the same proportion of large and small
60
firms among compliers and defiers, this suggests that the first term in Equation (A.1)
would more likely be negative, biasing our IV estimates.
D Late and Non-Participation in the PPP
In this appendix, we enumerate what we hope is a comprehensive list of plausible expla-
nations for why some businesses either borrowed later than they would have preferred or
ultimately chose not to borrow. We distinguish between factors that constrained firms’
short-term ability to borrow in the early days of the pandemic from those that were
more likely to persist through the end of the 2020 PPP on August 8, 2020. Short-term
factors were more likely to cause delays in loan receipt, while persistent factors are
those that plausibly led firms to forgo participation. Because our identification concern
centers on the funding effect estimated relative to “never” borrowers, bias would re-
sult from persistent reasons, not necessarily short-term factors, unless these cause some
businesses to fail. We argue that there is no compelling evidence that points to upward
bias in our estimates, as biases could go both ways. On net, the bias is likely small.
A. Short-term reasons that most likely caused delays in loan approval but
not the eventual failure to borrow
i. Lack of banking relationships, application complexity, and administrative
barriers: Community Development and Financial Institutions (CDFIs) and
fintech lenders were approved to make PPP loans as of April 30, and there
is ample evidence that they streamlined the process and expanded access to
small businesses that had previously struggled to participate in the program.
In principle, any small business that wanted to borrow should have been able
to do so through one of these lenders.
ii. Informational frictions and lack of awareness: it appears unlikely that any
small business would still have been unaware of the program by August 8,
2020.
iii. Owner illness due to COVID: with the exception of a small fraction of severe
long-COVID cases and related deaths, it seems improbable that illness alone
would have prevented owners from borrowing over the four-month duration
of the 2020 PPP.
iv. Our news search identified a few reports describing anecdotal cases in which
owners, discouraged by an initial rejection of their applications, chose not to
reapply.
v. In addition, some instances of delayed access to the PPP in its early stages
may have contributed to business closures, with potentially longer-lasting
consequences. We have already acknowledged that this possibility may partly
underlie the estimated effect of PPP receipt for the smallest establishments
in particular.
B. Persistent reasons that could have led to non-borrowing
i. According to the program’s rules, business owners had to certify on their
loan applications that they were adversely affected by the pandemic and
61
needed the assistance. This implies that, to the extent some small businesses
were honest and law-abiding, they would not have borrowed because they
did not meet these conditions. Relative to such non-borrowers, borrowers’
hypothetical non-PPP trend would almost certainly have been lower.
ii. Uncertainty concerns regarding forgiveness: more risk-averse owners may
have been less equipped to navigate the COVID shock, but their caution
could also have led them to build larger liquidity buffers, leaving them better
positioned initially.
iii. Selection into PPP participation was not solely driven by financial distress.
For example, some firms initially received PPP funds but later returned them
for ethical reasons, despite being potentially eligible for forgiveness.6 Con-
versely, some firms experienced unexpectedly strong performance during the
pandemic and therefore did not require financial support, yet still received
loans and had them forgiven.7 Without firm-level survey data, we cannot
directly tell what margin might have been at play for a given firm.
iv. Fear of government scrutiny and audit risk: if these owners were more willing
to take risks pre-pandemic, they may also have been better positioned to
adapt to the new environment.
v. Program design did not fit some businesses’ needs: firms with cost structures
that placed relatively little weight on payroll would have derived limited
benefit from the PPP. As a result, some owners may have sought alternative
assistance, such as the EIDL, which offered greater flexibility in allowable
uses of funds. In such cases, there is no clear reason to expect that PPP
non-borrowers would have been on a lower trajectory in the absence of the
PPP.
vi. Apart from the reasons above, some owners may have chosen to exit follow-
ing the COVID shock. Note that these exit decisions were not driven by
pre-existing weakness, as our matching ensured that each PPP firm and its
peer had similar pre-COVID scale and operational trends. Owners may have
exited for various reasons, such as facing higher adaptation costs than ob-
servationally similar peers or making a pandemic-induced early-retirement
or closing decision. Among all the reasons discussed so far, these are the
only ones for which non-borrowers would clearly be expected to have a lower
post-COVID trajectory than borrowers even in the absence of the PPP. For
example, older owners might have been less interested in growing the busi-
ness absent the shock. Our news search identified only a couple of such cases
within a large volume of PPP reporting, suggesting that they likely represent
a very small share of non-borrowers.
6
Heard on Morning Edition. “Why did some companies repay PPP loans that could have
been forgiven?” NPR, 2024, January 10. https://www.npr.org/2024/01/10/1223890080/
why-did-some-companies-repay-ppp-loans-that-could-have-been-forgiven.
7
Morgenson, Gretchen. “Some Firms Thrived During Covid and Then Got Their PPP
Covid Relief Loans Forgiven.” NBC News, 18 Nov. 2021. https://www.nbcnews.com/news/
firms-thrived-covid-got-ppp-covid-relief-loans-forgiven-rcna5697.
62
Table A.1: Determinants of the Number of PPP Loans Delayed, April 16–26, 2020
All Urban Smaller Urban Rural
∗ ∗∗
Cum. COVID-19 Cases per bil. up to 4/15/2020 –0.017 0.035 0.044 –0.031
(0.023) (0.018) (0.018) (0.026)
Cum. COVID-19 Deaths per bil. up to 4/15/2020 0.108∗∗∗ 0.041 0.014 0.200∗∗∗
(0.031) (0.039) (0.038) (0.038)
Share of days in lockdown (pre-4/17/2020) 0.004 –0.034 –0.043 0.018
(0.030) (0.032) (0.032) (0.053)
Share of days in lockdown (4/17–4/30/2020) 0.066 0.013 0.020 0.102∗∗
(0.042) (0.134) (0.135) (0.040)
Share of Emp. in Essential Industries 0.021 –0.183 –0.199 0.164
(0.156) (0.261) (0.260) (0.190)
Share of Emp. in Impacted Industries –0.090∗ –0.110 –0.106 –0.065
(0.050) (0.077) (0.077) (0.063)
Rural County Dummy 0.009
(0.006)
Most Populous County (Top 1%) 0.023
(0.018)
Ln Residential Population –0.015∗∗∗ –0.013∗∗∗ –0.014∗∗∗ –0.017∗∗∗
(0.004) (0.004) (0.004) (0.005)
Commuter to Residential Population Ratio –0.053∗∗ –0.030 –0.026 –0.078∗∗
(0.020) (0.022) (0.023) (0.038)
Ln Median Family Income 0.028∗ 0.014 0.016 0.047
(0.016) (0.019) (0.019) (0.028)
Community Bank Share of Deposits 0.018∗ 0.001 0.001 0.021∗
(0.010) (0.017) (0.017) (0.012)
Big4 Bank Share of Deposits 0.070 0.059 0.056 0.071
(0.046) (0.079) (0.078) (0.048)
Ln Bank Branch Density 0.001 –0.014 –0.014 0.010
(0.009) (0.011) (0.011) (0.012)
SBL Vol. per Small Estabs. (< 500 Emp.) (CBP 2019Q1) –0.001∗∗∗ –0.001∗∗∗ –0.001∗∗∗ –0.001∗∗
(0.000) (0.000) (0.000) (0.000)
Proportion of Small Employment in 2020Q1 to 2019Q1, QWI 0.012 –0.102 –0.101 0.038
(0.045) (0.081) (0.080) (0.051)
UI Benefits Replacement Rate (Industry-Wtd.) 0.012 0.061∗ 0.059 –0.016
(0.029) (0.036) (0.036) (0.040)
Constant 0.385 0.926∗ 0.923∗ 0.010
(0.334) (0.502) (0.507) (0.397)
Adjusted R-squared 0.28 0.32 0.32 0.25
Observations 2644 1108 1096 1536
State FE Yes Yes Yes Yes
Notes: Results from regressions of the share delayed on selected county-level characteristics. “Smaller” refers to
urban counties excluding those in the top 1 percent by population. Standard errors clustered at the state level in
parentheses.
63
Table A.2: Determinants of Lending Delay, April 2020. CBSA Sample
All All Smaller by Smaller by
Population Density
Cum. COVID-19 Cases per billion up to 4/15/2020 –0.037 –0.038 –0.039 –0.038
(0.040) (0.040) (0.041) (0.041)
Cum. COVID-19 Deaths per billion up to 4/15/2020 0.836 0.733 0.729 0.738
(0.534) (0.544) (1.091) (1.110)
Share of days in lockdown (pre-04/17/2020) –0.033 –0.031 –0.037 –0.030
(0.064) (0.063) (0.066) (0.065)
Share of days in lockdown (04/17 and 04/30/2020) 0.102 0.105 0.103 0.106
(0.139) (0.139) (0.137) (0.139)
Share of essential empl –0.206 –0.199 –0.201 –0.199
(0.298) (0.300) (0.296) (0.297)
Share of Employment - Impacted Industries –0.075 –0.073 –0.074 –0.069
(0.087) (0.087) (0.087) (0.087)
Share of Work Done Remotely –0.024 –0.029 –0.027 –0.032
(0.020) (0.021) (0.023) (0.023)
Share of Minors 0.054∗ 0.059∗ 0.060 0.063∗
(0.032) (0.034) (0.036) (0.037)
Ln(Residential Population) –0.016∗∗ –0.016∗∗ –0.017∗∗ –0.016∗∗
(0.007) (0.007) (0.008) (0.007)
Commuter to Residential Population Ratio 0.098 0.102 0.099 0.104
(0.081) (0.082) (0.083) (0.083)
Most Populous CBSA 0.050∗∗ 0.052∗∗
(0.021) (0.021)
Most Dense CBSA –0.002 –0.002
(0.024) (0.024)
Most Populous × Most Dense CBSA 0.028
Ln Median Family Income 0.030 0.034 0.035 0.033
(0.054) (0.054) (0.054) (0.055)
Community Bank Share of Deposits 0.036 0.035 0.035 0.034
(0.028) (0.028) (0.028) (0.028)
Big4 Bank Share of Deposits 0.051 0.048 0.048 0.046
(0.042) (0.044) (0.045) (0.045)
Ln Bank Branch Density –0.012 –0.011 –0.011 –0.011
(0.023) (0.023) (0.023) (0.023)
SBL Volume per Estab< 500 (QCEW 2019 Avg) –0.002∗∗∗ –0.002∗∗∗ –0.002∗∗∗ –0.002∗∗∗
(0.001) (0.001) (0.001) (0.001)
Ratio of s Small (Under 500) Employment in 2020Q1 to 2019Q1, QWI 0.272∗ 0.274∗ 0.273∗ 0.275∗
(0.149) (0.150) (0.150) (0.150)
UB replacement rate, industry weighted 0.053 0.054 0.056 0.053
(0.074) (0.075) (0.076) (0.076)
(0.041)
Constant 0.137 0.079 0.078 0.080
(0.732) (0.735) (0.739) (0.741)
Adjusted R-squared 0.14 0.14 0.14 0.14
Observations 916 916 906 906
Notes: Results from regressions of the share delayed on selected CBSA-level characteristics. “Smaller by Population”
refers to CBSAs excluding those in the top 1 percent by population; and “Smaller by Density” refers to CBSAs excluding
those in the top 1 percent by population density. Standard errors clustered at the state level in parentheses.
64
Table A.3: Which Controls Drive the Effects of PPP Share Delayed on Total Private
Employment? All Counties, QCEW
(1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11) (12)
Level ∆E/P
Apr 2020 × Share Delayed –0.21 –0.15 –0.16 –0.11 0.01 –0.56* 3.59*** 2.12*** 1.83*** 1.69*** 1.50*** 1.06***
(0.56) (0.47) (0.47) (0.40) (0.38) (0.28) (0.62) (0.44) (0.42) (0.37) (0.38) (0.37)
May 2020 × Share Delayed –1.19** –0.79 –0.60 –0.46 –0.52 –0.75** 2.90*** 1.36*** 1.19*** 1.16*** 1.29*** 1.04***
(0.58) (0.48) (0.46) (0.37) (0.36) (0.29) (0.54) (0.37) (0.35) (0.32) (0.33) (0.34)
Jun 2020 × Share Delayed –1.86** –1.19* –0.85 –0.66* –0.73* –0.79*** 1.64** 0.17 0.09 0.13 0.99*** 0.95***
(0.72) (0.60) (0.54) (0.39) (0.37) (0.29) (0.69) (0.74) (0.80) (0.77) (0.34) (0.35)
Jul 2020 × Share Delayed –2.32*** –1.48** –1.11** –0.95** –0.99** –0.87*** 0.77 –0.74 –0.96 –0.90 1.01*** 1.01***
(0.76) (0.58) (0.51) (0.38) (0.37) (0.29) (1.30) (1.69) (1.80) (1.76) (0.34) (0.37)
Aug 2020 × Share Delayed –2.34*** –1.46** –1.08** –0.89** –1.04*** –0.81*** 1.39*** 0.29 0.23 0.28 0.76** 0.75**
(0.75) (0.56) (0.49) (0.36) (0.35) (0.29) (0.45) (0.44) (0.46) (0.44) (0.33) (0.35)
Sept 2020 × Share Delayed –2.18*** –1.32** –0.95** –0.77** –0.91*** –0.72*** 1.37*** 0.54 0.49 0.52* 0.55* 0.65*
(0.69) (0.52) (0.46) (0.34) (0.33) (0.28) (0.41) (0.33) (0.30) (0.29) (0.31) (0.33)
Oct 2020 × Share Delayed –1.81*** –1.07** –0.72* –0.51 –0.64** –0.52** 1.12*** 0.58 0.56 0.56 0.39 0.48
(0.58) (0.46) (0.41) (0.31) (0.30) (0.25) (0.41) (0.42) (0.39) (0.39) (0.31) (0.32)
Nov 2020 × Share Delayed –1.61*** –0.94** –0.61 –0.46 –0.59* –0.43* 0.82* 0.52 0.57 0.56 0.35 0.50*
(0.54) (0.46) (0.40) (0.32) (0.31) (0.26) (0.42) (0.46) (0.42) (0.43) (0.29) (0.30)
Dec 2020 × Share Delayed –1.73*** –1.03** –0.67** –0.57** –0.69** –0.41 0.89** 0.61 0.63 0.56 0.36 0.50*
(0.51) (0.39) (0.33) (0.27) (0.26) (0.27) (0.40) (0.46) (0.43) (0.41) (0.28) (0.27)
Jan 2021 × Share Delayed –1.97*** –1.17*** –0.77** –0.65** –0.77*** –0.50* 0.90* 0.60 0.69 0.65 0.38 0.56*
(0.61) (0.43) (0.36) (0.31) (0.29) (0.29) (0.47) (0.54) (0.51) (0.48) (0.39) (0.30)
Feb 2021 × Share Delayed –1.42** –0.84* –0.50 –0.39 –0.48 –0.36 0.59 0.42 0.53 0.50 0.24 0.36
(0.53) (0.47) (0.39) (0.32) (0.32) (0.26) (0.49) (0.56) (0.55) (0.54) (0.48) (0.35)
Mar 2021 × Share Delayed –1.47*** –0.87* –0.53 –0.39 –0.45 –0.39 0.51 0.27 0.35 0.35 0.09 0.14
(0.51) (0.44) (0.37) (0.30) (0.29) (0.25) (0.54) (0.66) (0.65) (0.64) (0.62) (0.48)
Apr 2021 × Share Delayed –1.45*** –0.85* –0.53 –0.31 –0.35 –0.37 0.29 –0.01 –0.02 0.01 0.06 0.14
(0.52) (0.46) (0.40) (0.34) (0.32) (0.25) (0.55) (0.59) (0.60) (0.60) (0.70) (0.52)
May 2021 × Share Delayed –1.45** –0.86* –0.53 –0.29 –0.33 –0.35 0.40 –0.00 –0.06 0.01 0.01 0.14
(0.56) (0.50) (0.44) (0.37) (0.36) (0.25) (0.67) (0.69) (0.70) (0.72) (0.83) (0.60)
Jun 2021 × Share Delayed –1.65*** –0.98** –0.64 –0.40 –0.43 –0.38 0.35 –0.32 –0.44 –0.33 0.12 0.25
(0.53) (0.46) (0.40) (0.33) (0.31) (0.25) (0.80) (0.85) (0.87) (0.89) (0.96) (0.69)
Jul 2021 × Share Delayed –1.54** –0.96* –0.66 –0.38 –0.42 –0.44* –0.57 –1.48 –1.68 –1.56 0.08 0.12
(0.58) (0.53) (0.47) (0.38) (0.39) (0.26) (1.24) (1.61) (1.67) (1.65) (0.94) (0.73)
Aug 2021 × Share Delayed –1.28** –0.81 –0.54 –0.27 –0.33 –0.40 0.27 –0.22 –0.33 –0.24 0.14 0.17
(0.59) (0.55) (0.49) (0.40) (0.40) (0.25) (0.75) (0.77) (0.79) (0.83) (0.88) (0.71)
Sept 2021 × Share Delayed –0.95* –0.53 –0.31 –0.08 –0.12 –0.23 0.32 0.02 –0.04 0.01 –0.12 –0.07
(0.50) (0.47) (0.42) (0.36) (0.35) (0.23) (0.88) (0.91) (0.95) (1.00) (1.05) (0.87)
Oct 2021 × Share Delayed –0.58 –0.26 –0.06 0.15 0.07 –0.11 –0.11 –0.13 –0.27 –0.24 –0.56 –0.65
(0.47) (0.44) (0.40) (0.37) (0.37) (0.23) (0.92) (0.99) (1.06) (1.10) (1.13) (1.03)
Nov 2021 × Share Delayed –0.41 –0.13 0.05 0.24 0.18 –0.02 –0.27 –0.04 –0.16 –0.16 –0.57 –0.64
(0.43) (0.41) (0.37) (0.36) (0.37) (0.23) (0.87) (0.98) (1.05) (1.08) (1.06) (1.02)
Dec 2021 × Share Delayed –0.37 –0.13 0.07 0.20 0.16 0.00 –0.24 0.11 –0.03 –0.04 –0.50 –0.59
(0.39) (0.36) (0.33) (0.32) (0.33) (0.23) (0.83) (0.92) (0.99) (1.02) (0.96) (0.97)
Within R-squared 1.00 1.00 1.00 1.00 1.00 0.87 0.05 0.14 0.15 0.16 0.16 0.12
Observations 74,400 74,400 74,400 74,400 70,936 70,936 74,400 74,400 74,400 74,400 70,936 70,936
State, Time FE, Lag LHS Yes Yes Yes Yes Yes No Yes Yes Yes Yes Yes No
County FE, State by Time FE, Lag LHS Yes Yes Yes Yes Yes Yes Yes Yes Yes Yes Yes Yes
Demographic Controls No Yes Yes Yes Yes Yes No Yes Yes Yes Yes Yes
Financial Pre-Conditions No No Yes Yes Yes Yes No No Yes Yes Yes Yes
COVID-19 Controls No No No Yes Yes Yes No No No Yes Yes Yes
CARES Act Controls No No No No Yes Yes No No No No Yes Yes
Notes: Standard errors, in parentheses, are clustered at the state level in columns (1)–(5) and (7)–(11) and at the county level in columns (6) and
(12). Employment for columns (1)–(6) is measured in thousands. Lags of LHS variables are computed using 2019 employment as of December 2019.
Demographic controls: median family income, share of minors, commuter-to-residential-population ratio, indicators for 2013 NCHS urban-rural
designation; Financial Pre-Conditions controls: community-bank share of deposits, largest four banks’ share of deposits, bank branch den-
sity, and 2019 small-business-loan volume per small establishment; COVID-19 controls: cumulative COVID-19 cases and deaths per population,
Stringency index, share of days in April 2020 in early lockdown, share of work done remotely, share of employment in essential industries, and share
of employment in most impacted industries CARES Act controls: industry-employment-share-weighted UI benefits replacement rate relative to
its March 2020 level, and rebates (“stimulus checks”) per capita. Share Delayed is the share (by volume) of county-level PPP loans delayed as
defined in Equation (2). The reference period is February of 2020.
65
Table A.4: Effects of Share of PPP Loans Delayed on Total Private Employment
CBSA Sample, QCEW
(1) (2) (3) (4) (5) (6) (7) (8)
Level Log E/P ∆E/P
Apr 2020 × Share Delayed 0.08 0.43 0.06** 0.05*** 2.82*** 2.25*** 3.30*** 3.10***
(2.47) (3.11) (0.02) (0.02) (0.98) (0.79) (1.02) (0.95)
May 2020 × Share Delayed –1.95 –4.11 0.04** 0.04** 2.35*** 1.75** 2.80*** 2.69***
(2.76) (3.46) (0.02) (0.02) (0.87) (0.71) (0.89) (0.82)
Jun 2020 × Share Delayed –2.90 –4.96 0.04** 0.04** 2.47*** 2.00** 2.86*** 2.81***
(3.19) (3.87) (0.02) (0.02) (0.88) (0.77) (0.89) (0.86)
Jul 2020 × Share Delayed –2.85 –3.88 0.04** 0.04** 2.39** 2.09** 2.75*** 2.84***
(2.82) (3.34) (0.02) (0.02) (0.92) (0.87) (0.93) (0.94)
Aug 2020 × Share Delayed –2.72 –2.95 0.03 0.03* 1.75** 1.50* 2.10** 2.24**
(2.69) (2.97) (0.02) (0.02) (0.83) (0.79) (0.86) (0.86)
Sept 2020 × Share Delayed –2.39 –2.55 0.02 0.02 1.34* 0.97 1.70** 1.71**
(2.48) (2.62) (0.02) (0.02) (0.80) (0.72) (0.82) (0.78)
Oct 2020 × Share Delayed –1.79 –1.51 0.02 0.02 1.23* 0.78 1.57** 1.52**
(2.22) (2.37) (0.02) (0.01) (0.67) (0.58) (0.70) (0.67)
Nov 2020 × Share Delayed –1.81 –1.38 0.02 0.02 0.89 0.55 1.22* 1.21*
(2.12) (2.43) (0.01) (0.01) (0.59) (0.54) (0.62) (0.62)
Dec 2020 × Share Delayed –2.07 –2.23 0.01 0.01 0.56 0.31 0.85 0.82
(1.95) (2.48) (0.01) (0.01) (0.62) (0.61) (0.65) (0.66)
Jan 2021 × Share Delayed –2.63 –2.13 0.01 0.00 0.57 0.37 0.88 0.91
(2.19) (2.95) (0.02) (0.02) (0.72) (0.69) (0.73) (0.73)
Feb 2021 × Share Delayed –2.03 –1.69 0.01 0.01 0.74 0.57 1.04 1.10
(2.24) (3.13) (0.02) (0.02) (0.71) (0.68) (0.72) (0.73)
Mar 2021 × Share Delayed –1.94 0.11 0.02 0.02 0.94 0.86 1.23* 1.36*
(2.12) (2.97) (0.02) (0.02) (0.68) (0.63) (0.68) (0.69)
Apr 2021 × Share Delayed –1.74 –0.19 0.01 0.01 0.88 0.83 1.18* 1.32*
(2.05) (2.79) (0.02) (0.02) (0.66) (0.61) (0.66) (0.68)
May 2021 × Share Delayed –1.65 –0.58 0.02 0.02 0.96 0.86 1.28* 1.38*
(2.13) (2.74) (0.02) (0.02) (0.71) (0.67) (0.71) (0.73)
Jun 2021 × Share Delayed –1.41 –0.41 0.02 0.03 1.36* 1.38* 1.63** 1.77**
(2.03) (2.54) (0.02) (0.02) (0.81) (0.80) (0.81) (0.84)
Jul 2021 × Share Delayed –1.33 –0.55 0.03 0.04 1.97* 2.04* 2.22** 2.38**
(2.20) (2.70) (0.02) (0.02) (1.10) (1.05) (1.08) (1.05)
Aug 2021 × Share Delayed –1.32 –0.50 0.03 0.03 1.52 1.58 1.78* 1.93*
(2.26) (2.66) (0.02) (0.02) (1.03) (0.98) (1.02) (0.98)
Sept 2021 × Share Delayed –0.73 0.06 0.03 0.03 1.38 1.36 1.66* 1.74*
(1.98) (2.44) (0.02) (0.02) (0.95) (0.88) (0.94) (0.90)
Oct 2021 × Share Delayed 0.03 0.49 0.03 0.03 1.39* 1.30* 1.65** 1.66**
(1.81) (2.41) (0.02) (0.02) (0.81) (0.74) (0.80) (0.76)
Nov 2021 × Share Delayed 0.26 0.51 0.03* 0.03* 1.11* 1.09* 1.36** 1.38**
(1.71) (2.26) (0.01) (0.01) (0.63) (0.60) (0.64) (0.62)
Dec 2021 × Share Delayed 0.34 0.16 0.02 0.02 0.84 0.98 1.04* 1.16*
(1.62) (2.12) (0.01) (0.01) (0.58) (0.60) (0.59) (0.60)
Avg. LHS 122.05 122.05 10.35 10.35 39.82 39.82 –1.97 –1.97
Share Delayed 0.44 0.44 0.44 0.44 0.44 0.44 0.44 0.44
Within R-squared 1.00 1.00 1.00 1.00 0.95 0.95 0.13 0.16
Observations 21,984 21,984 21,984 21,984 21,984 21,984 21,984 21,984
Pre-conditions Controls Yes Yes Yes Yes Yes Yes Yes Yes
COVID-19 Controls No Yes No Yes No Yes No Yes
Notes: Results from estimating Equation (1). Standard errors clustered at the state level in parentheses. Employment
in columns (1) and (2) is in thousands. All regressions control for state, month-year fixed effects, and a lag of the
dependent variable (as of December 2019), in addition to preexisting conditions and COVID-19 controls. Preexist-
ing conditions: median family income, share of minors, commuter-to-residential-population ratio, indicators for 2013
NCHS urban-rural designation, community-bank share of deposits, largest four banks’ share of deposits, bank branch
density, and 2019 small-business-loan volume per small establishment. COVID-19 Controls: cumulative COVID-19
cases and deaths per population, share of days in April 2020 in early lockdown, share of work done remotely, share of
employment in essential industries, and share of employment in most impacted industries. NAICS codes for most af-
fected industries: 44-45, 61, 71, 72, and 81. Share Delayed is the share (by volume) of PPP loans delayed, as defined in
Equation (2), computed at the CBSA level. The reference period is the first quarter of 2020.
66
Table A.5: Effects of Share Delayed on Stable Employment
Total and Large Establishments, All Counties, QWI
(1) (2) (3) (4) (5) (6) (7) (8)
Total Employment Employment 500+
Level Log E/P ∆E/P Level Log E/P ∆E/P
2020Q2 × Share Delayed –0.44* 0.03** 0.39 0.69*** –0.18* 0.03 0.27 0.36***
(0.24) (0.01) (0.25) (0.17) (0.10) (0.03) (0.17) (0.13)
2020Q3 × Share Delayed –0.46 0.02* 0.41* 0.77*** –0.20** 0.03 0.30* 0.44***
(0.29) (0.01) (0.24) (0.22) (0.10) (0.03) (0.17) (0.15)
2020Q4 × Share Delayed –0.44* 0.01 0.26 0.60** –0.24** 0.02 0.20 0.34*
(0.24) (0.01) (0.28) (0.23) (0.10) (0.03) (0.20) (0.17)
2021Q1 × Share Delayed –0.36 0.02 0.24 0.53* –0.19 0.02 0.10 0.21
(0.26) (0.01) (0.31) (0.28) (0.12) (0.03) (0.26) (0.23)
2021Q2 × Share Delayed –0.13 0.02 0.16 0.59* –0.05 0.01 0.08 0.22
(0.22) (0.01) (0.33) (0.31) (0.10) (0.04) (0.34) (0.31)
2021Q3 × Share Delayed –0.15 0.00 0.04 0.37 0.05 –0.01 –0.07 0.08
(0.29) (0.01) (0.43) (0.46) (0.12) (0.04) (0.45) (0.42)
2021Q4 × Share Delayed 0.21 0.00 –0.31 0.06 0.16 –0.00 –0.31 –0.14
(0.30) (0.02) (0.56) (0.59) (0.15) (0.05) (0.62) (0.58)
Avg. LHS 33.46 8.74 28.95 –1.22 17.80 7.70 12.25 –0.44
Share Delayed 0.48 0.48 0.48 0.48 0.47 0.47 0.47 0.47
Observations 24,525 24,525 24,525 24,525 24,229 24,229 24,229 24,183
State FE, Time FE, Lag LHS Yes Yes Yes Yes Yes Yes Yes Yes
Pre-conditions Controls Yes Yes Yes Yes Yes Yes Yes Yes
COVID-19 Controls Yes Yes Yes Yes Yes Yes Yes Yes
Notes: Results from estimating Equation (1). Standard errors clustered at the state level in parentheses. All re-
gressions control for state, quarter-year fixed effects, and a lag of the dependent variable (last quarter of 2019), in
addition to preexisting conditions and COVID-19 controls. Preexisting conditions: median family income, share
of minors, commuter-to-residential-population ratio, indicators for 2013 NCHS urban-rural designation, community-
bank share of deposits, largest four banks’ share of deposits, bank branch density, and 2019 small-business-loan
volume per small establishment. COVID-19 controls: cumulative COVID-19 cases and deaths per population,
share of days in April 2020 in early lockdown, share of remote jobs, share of employment in essential industries, and
share of employment in most impacted industries. Share Delayed is the share (by volume) of county-level PPP loans
delayed as defined in Equation (2). The reference period is the first quarter of 2020.
67
Table A.6: Summary Statistics by PPP-Peer Firm Distance: Advan Sample
N(Pairs) Mean P25 Median P75
Pair Distance [1, 5) Miles
PPP Business Avg. Weekly Visits 26,466 46.40 9.77 24.69 53.08
% Diff. in Visits: PPP vs. non-PPP Business 26,466 -0.00 -2.45 0.00 2.44
Distance (Miles): PPP vs. non-PPP Business 26,466 2.95 1.98 2.91 3.92
PPP Loan Size ($1,000) 26,466 145.92 22.39 50.24 118.70
No. of Jobs Saved 26,466 19.06 4.00 8.00 17.00
Pair Distance [5, 10) Miles
PPP Business Avg. Weekly Visits 25,820 45.99 8.77 23.31 52.08
% Diff. in Visits: PPP vs. non-PPP Business 25,820 0.01 -2.42 0.00 2.45
Distance (Miles): PPP vs. non-PPP Business 25,820 7.37 6.13 7.30 8.61
PPP Loan Size ($1,000) 25,820 141.81 22.15 49.70 118.00
No. of Jobs Saved 25,820 19.06 4.00 8.00 18.00
Pair Distance [10, 15) Miles
PPP Business Avg. Weekly Visits 17,722 44.00 8.38 22.00 49.46
% Diff. in Visits: PPP vs. non-PPP Business 17,722 0.04 -2.41 0.00 2.49
Distance (Miles): PPP vs. non-PPP Business 17,722 12.29 11.06 12.20 13.48
PPP Loan Size ($1,000) 17,722 141.07 22.24 49.60 114.60
No. of Jobs Saved 17,722 18.99 4.00 8.00 17.00
Pair Distance [15, 50) Miles
PPP Business Avg. Weekly Visits 21,594 39.96 7.54 20.23 45.08
% Diff. in Visits: PPP vs. non-PPP Business 21,594 0.02 -2.44 0.00 2.51
Distance (Miles): PPP vs. non-PPP Business 21,594 22.27 17.19 20.25 25.27
PPP Loan Size ($1,000) 21,594 133.96 21.31 48.06 110.58
No. of Jobs Saved 21,594 18.16 4.00 8.00 17.00
Notes: Each pair of firms operates in the same 6-digit NAICS industry and is located in the same
county. The PPP firm and its peer are located in difference Census block groups within different
distance bands, as indicated in each panel. Pre-COVID visits are averages for the months of De-
cember 2019 and February 2020.
68
Figure A.1: Map of Share of PPP Volume Delayed by County
Share Delayed
(.62,1]
(.5,.62]
(.42,.5]
(.33,.42]
[0,.33]
Notes: This map depicts, by quintile, the share of PPP volume delayed across all US counties.
Source: Small Business Administration.
69
Figure A.2: Total Employment Evolution based on 2019 payroll and DK delay
All Establishments, QCEW
Share Payroll under 500 Share Delayed
10 10
5 5
0 0
-5 -5
2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1 2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1
(a) Basic Controls
Share Payroll under 500 Share Delayed
8 8
6 6
4 4
2 2
0 0
-2 -2
2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1 2003q1 2005q1 2007q1 2009q1 2011q1 2013q1 2015q1 2017q1 2019q1 2021q1
(b) All Controls
Notes: Let et = E Pt × 100 and ∆et = et − et−4 . The figures plot βt and γt from the regression ∆et =
t
α + βt share2019 + γt delay + ζt L4.∆et + Xt Πt + ϵt . Regressions also include state and quarter-year fixed
effects. The bottom panel regressions include all controls in our baseline regressions (including banking
variables) adjusted to the relevant time period whenever possible. The top panel excludes Xt Πt .
70
Figure A.3: Effect of PPP on Visits
Estimates by Distance between Advan Matched Firm Pairs
Peer Distance [1, 5) Miles Peer Distance [5, 10) Miles
Average Effect Average Effect
0 .1 .2 0 .1 .2
-.1 -.1
-16 -12 -8 -4 0 4 8 12 16 20 -16 -12 -8 -4 0 4 8 12 16 20
Months Relative to Loan Approval Months Relative to Loan Approval
Peer Distance [10, 15) Miles Peer Distance [15, 50] Miles
Average Effect Average Effect
0 .1 .2 0 .1 .2
-.1 -.1
-16 -12 -8 -4 0 4 8 12 16 20 -16 -12 -8 -4 0 4 8 12 16 20
Months Relative to Loan Approval Months Relative to Loan Approval
Notes: The panels plot the µl coefficients from regressions following Equation (6) for log visits, defined
as the log of visit counts plus one. 2020 PPP recipient firms are matched to non-PPP firms that operate
in the same 6-digit NAICS industry, have similar visit volumes (within 5%) between December 2019 and
February 2020, and located in the same county but at the distances indicated in each panel’s subtitle.
Shaded areas represent 95 percent confidence intervals, with standard errors clustered by firm pair.
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