Smbliq B 038 Did The Paycheck Protection Program Hit The Target 2021

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Did the paycheck protection program hit the target? is a research article by João Granja, Christos Makridis, Constantine Yannelis and Eric Zwick, published in the Journal of Financial Economics 145 (2022) 725–761 and available online 12 July 2022. Using loan-level data for all PPP loans and high-frequency employment data from Homebase, the article presents three main findings: banks played an important role in mediating program targeting, the short- and medium-term employment effects were small compared to the program's size, and many firms used loans for non-payroll fixed payments and savings buffers. It reports aggregate impacts equal to 4% of eligible employment, a cost-per-job-year of at least $175,000, and estimates that more than 90% of jobs supported were inframarginal. The article closes with its reference list.

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Journal of Financial Economics 145 (2022) 725–761

Contents lists available at ScienceDirect

Journal of Financial Economics
journal homepage: www.elsevier.com/locate/jfec

Did the paycheck protection program hit the target?
João Granja a, Christos Makridis b, Constantine Yannelis c, Eric Zwick c,∗
a
Chicago Booth, United States
b
Arizona State and Stanford, United States
c
Chicago Booth and NBER, United States

a r t i c l e i n f o a b s t r a c t

Article history: This paper provides a comprehensive assessment of ﬁnancial intermediation and the eco-
Received 14 November 2020 nomic effects of the Paycheck Protection Program (PPP), a large and novel small business
Revised 21 May 2022
support program that was part of the initial policy response to the COVID-19 pandemic
Accepted 21 May 2022
in the US. We use loan-level microdata for all PPP loans and high-frequency administra-
Available online 12 July 2022
tive employment data to present three main ﬁndings. First, banks played an important
JEL classiﬁcation: role in mediating program targeting, which helps explain why some funds initially ﬂowed
G38 to regions that were less adversely affected by the pandemic. Second, we exploit regional
H81 heterogeneity in lending relationships and individual ﬁrm-loan matched data to study the
G21 role of banks in explaining the employment effects of the PPP. We ﬁnd the short- and
G28 medium-term employment effects of the program were small compared to the program’s
G01 size. Third, many ﬁrms used the loans to make non-payroll ﬁxed payments and build up
H12 savings buffers, which can account for small employment effects and likely reﬂects pre-
Keywords: cautionary motives in the face of heightened uncertainty. Limited targeting in terms of
PPP who was eligible likely also led to many inframarginal ﬁrms receiving funds and to a low
Fiscal stimulus correlation between regional PPP funding and shock severity. Our ﬁndings illustrate how
Banking business liquidity support programs affect ﬁrm behavior and local economic activity, and
Small business how policy transmission depends on the agents delegated to deploy it.
Policy targeting
© 2022 Elsevier B.V. All rights reserved.

1. Introduction This paper studies a large and novel business support
program that was part of the crisis response in the US, the
The COVID-19 pandemic triggered an unprecedented Paycheck Protection Program (PPP), and the role of banks
economic freeze and a massive immediate policy response. in explaining the employment effects of the PPP. Part of
Among the ﬁrms most affected by the freeze were mil- the Coronavirus Aid, Relief, and Economic Security (CARES)
lions of small businesses without access to public ﬁnancial Act, the PPP offered guaranteed, forgivable loans to pro-
markets or other ways to manage short-term costs. With-
out an existing system of social insurance to support these
ﬁrms, policymakers around the world rushed to develop 1
For example, the UK, France, Germany, Spain, Italy, and Australia in-
new programs to contain the damage, including wage sub- troduced or expanded loan guarantee and small business grant schemes
sidies, small business grants, and guaranteed business loan in response to the pandemic. Hanson et al. (2020b) provide a theoreti-
cal discussion of business credit support programs in the pandemic and
schemes, often relying on banks to rapidly deploy funds to
a review of key programs in Europe. Many of these countries also sep-
ﬁrms.1 arately implemented temporary wage subsidy programs to provide in-
comes to unemployed workers directly through ﬁrms (see Hubbard and
Strain, 2020 for a comprehensive list). While the program we study com-
∗
Corresponding author. bines these features, the larger source of wage support in the US came
E-mail address: Eric.Zwick@chicagobooth.edu (E. Zwick). via the unemployment insurance system.

https://doi.org/10.1016/j.jﬁneco.2022.05.006
0304-405X/© 2022 Elsevier B.V. All rights reserved.
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

vide liquidity to small and mid-sized businesses and pre- play in mediating policy targeting? Third, why did some
vent job losses. The PPP deployed more than $500 billion banks systematically under- or overperform in disbursing
within just four months of passage, making it one of the PPP loans relative to their share of the small business loan
largest ﬁrm-based ﬁscal policy programs in US history. The market?
program was administered by the Small Business Adminis- Preventing unnecessary mass layoffs and ﬁrm bankrupt-
tration (SBA) with the loan application process operated by cies by injecting liquidity into ﬁrms were central goals of
commercial banks. We document substantial heterogene- the program and the beneﬁts of PPP were likely greatest
ity across banks in disbursing PPP funds and ﬁnd that this in areas with more pre-policy economic dislocation. How-
heterogeneity led to meaningful differences across ﬁrms ever, we ﬁnd no evidence that funds ﬂowed to areas that
and regions in terms of targeting and employment impacts. were more adversely affected by the economic effects of
We have three main ﬁndings. First, banks played an the pandemic, which we proxy using declines in hours
important role in mediating program targeting. The ex- worked, employee counts, business shutdowns, and coron-
tent of bank participation in the initial phase of the pro- avirus infections and deaths. If anything, we ﬁnd evidence
gram depends intuitively on ex ante bank characteristics, that funds ﬂowed to areas less hard hit. Over both rounds
including relationships with the SBA, greater reliance on of funding, the correlation between pre-policy economic
labor relative to automation, and active enforcement ac- dislocation and program participation was approximately
tions against banks. These differences in bank participa- zero, which likely reﬂects the program’s broad deﬁnition
tion explain spatial differences in the initial distribution of eligibility (Barrios et al., 2020).
of funds and why some funds initially ﬂowed to regions We ﬁnd signiﬁcant heterogeneity across banks in terms
that were less adversely affected by the pandemic. Sec- of disbursing PPP funds, which reﬂects more than mere
ond, the short- and medium-term employment effects of differences in underlying loan demand and contributes to
the program were small compared to the program’s size. the weak correlation between economic declines and PPP
Our analysis reveals how bank performance differences in lending. Ex ante bank characteristics, including greater la-
loan deployment contribute to these employment effects bor capacity to process loans, pre-existing SBA relation-
over time. Third, many ﬁrms used the loans to make non- ships, and active enforcement actions against banks, pre-
payroll ﬁxed payments and build up savings buffers, which dict banks’ relative performance in disbursing PPP loans.
can account for small employment effects and likely re- The PPP program required lenders to collect and enter in-
ﬂects precautionary motives in the face of heightened un- formation into a custom application and submit it via the
certainty.2 Limited targeting in terms of who was eligible SBA portal. Thus, reliance on labor rather than automa-
likely also led to many inframarginal ﬁrms receiving funds tion, as well as pre-existing access and familiarity with
and to a low correlation between regional PPP funding and the SBA portal facilitated disbursement of PPP loans, espe-
shock severity. cially in the initial phase. Conversely, banks subject to for-
We bring data from two sources to study the PPP. First, mal enforcement actions were not automatically approved
we use loan-level microdata from the SBA for all PPP loans, to make PPP loans, initially leading to lower PPP disburse-
which includes lender, geography, and borrower- and loan- ment for these banks.
level information. The data offer a clear look at which Our results on bank participation motivate two comple-
lenders are most active in disbursing loans, how program mentary research designs to evaluate the PPP using ZIP-
participation evolves over time, and the geographic distri- level variation in banks’ propensity to disburse loans. We
bution of PPP lending across the US economy. Additionally, use these research designs to study business shutdowns,
we obtained high-frequency employment data from Home- employment levels, reductions in hours worked, initial un-
base, a software company that provides free scheduling, employment insurance (UI) claims, and small business rev-
payroll reporting, and other services to small businesses, enues. We construct measures of geographic exposure to
primarily in the retail and hospitality sectors. The granu- bank performance in the PPP using (1) the distribution
larity of the data, coupled with the focus on sectors most of bank branches across geographic regions and (2) geo-
adversely affected by the pandemic, allows us to trace out graphic exposure to the ex ante bank characteristics that
the response of employment, wages, hours worked, and predict PPP disbursement. Both measures exploit the fact
business closures in almost real-time and evaluate the ef- that most small business lending is local (Brevoort et al.,
fects of PPP support. We complement these primary data 2010; Granja et al., 2018). Our ﬁrst measure compares re-
sources with a number of other sources, including county- gions exposed to high-performance banks—whose share of
level unemployment insurance claims, the Census Small PPP lending exceeded what would be expected from them
Business Pulse survey, small business revenue data from given their national share of the small business lending
Womply, and employment rates from the COVID-19 eco- market—to regions exposed to low-performance banks—
nomic tracker (Chetty et al., 2020). whose PPP lending share underperformed relative to their
We consider three dimensions of program targeting. national share of the small business lending market. This
First, did the funds ﬂow to where the economic shock was bank-driven variation across regions allows us to isolate
greatest? Second, given that the PPP used the banking sys- the effect of the PPP from differences in loan demand or
tem as a conduit to access ﬁrms, what role did the banks confounding correlations between PPP funding and local
economic outcomes. Our second measure further attempts
2 to isolate speciﬁc elements of bank performance that we
Almeida et al. (2004) and Riddick and Whited (2009) show that un-
certainty increases ﬁrms’ precautionary motives to hold cash, particularly can trace back to bank-supply frictions prevailing prior to
when external ﬁnancing is diﬃcult to obtain. the pandemic.

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J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

We do not ﬁnd evidence that the PPP had a substan- that exposure to higher-performing banks is associated
tial effect on local employment outcomes or business shut- with fewer permanent ﬁrm shutdowns, deﬁned as the
downs during the ﬁrst round of the program, and ﬁnd ﬁrm being closed for all weeks from the beginning of the
modest effects on hours worked and employee counts dur- program through the end of August. This result suggests
ing the second round. We conﬁrm the ﬁrm-level evidence that initial bank-driven distortions may have had persis-
by documenting limited impacts on initial UI claims, small tent effects on the ability of ﬁrms to reopen after the
business revenues, and employment rates in small busi- initial shock.
nesses at the county level. Our conﬁdence intervals on em- At the same time, because program eligibility was de-
ployment outcomes are wide enough to permit modest ef- ﬁned broadly, many less-affected ﬁrms received PPP fund-
fects of the program, but precise enough to reject large ef- ing and may have continued as they would have in the ab-
fects. Results are qualitatively and quantitatively similar for sence of the funds, either by spending less out of retained
both measures of exposure to bank performance. Aggregate earnings or by borrowing less from other sources. For these
impacts over the ﬁrst ﬁve months of the program equal 4% ﬁrms, while the statutory incidence of funding falls on la-
of eligible employment, implying a cost-per-job-year of at bor and creditors, the economic incidence falls mainly on
least $175,0 0 0. Our estimates suggest that more than 90% business owners.
of jobs supported by the PPP were inframarginal. If wages Our work complements several contemporaneous stud-
for inframarginal workers did not adjust, then the bulk of ies that also focus on the employment effects of the PPP,
the program’s economic beneﬁts appear to accrue to other although with less emphasis on the role of ﬁnancial in-
stakeholders, including owners, landlords, lenders, suppli- stitutions. Three studies (Autor et al., 2020; Chetty et al.,
ers, customers, and possibly future workers. 2020; Hubbard and Strain, 2020) use the size threshold
Both research designs are akin to Bartik instruments of 500 employees to study the employment effects of the
and rely on the assumption that pre-policy bank branch program. This research design estimates a different treat-
shares in a given region are not correlated with the out- ment effect, as it uses variation local to larger ﬁrms, while
comes we study. This assumption likely holds once we most PPP loans were disbursed to much smaller ﬁrms. Ap-
condition on key observables, including the relationship proximately 0.4% of PPP loans were disbursed to ﬁrms with
between PPP funding and the initial severity of the crisis. more than 250 employees, which account for only 13% of
Our preferred speciﬁcation conditions on ﬁrm- and state- covered employment among all borrowers. Nevertheless,
by-time ﬁxed effects, which remove many potential con- despite using different primary data sources and a differ-
founding factors from the analysis. We present further ev- ent research design, these papers tend to ﬁnd either mod-
idence supporting the Bartik assumption from pre-trends est or negligible effects on employment, consistent with
comparisons between high- and low-exposure groups and our ﬁndings.3
diagnostics for unpacking the Bartik instrument following Several other studies use differences in the timing of
Goldsmith-Pinkham et al. (2020). PPP receipt to examine the program’s employment ef-
We complement our aggregate regional designs with a fects, while also exploiting differences in timing due to
timing design using matched ﬁrm-loan data. We match by pre-existing variation in bank lending relationships. Li and
name 10,694 ﬁrms in Homebase to PPP loans and then Strahan (2020) use variation in the strength of the re-
compare ﬁrms that received loans earlier versus later. We lationships between local banks and ﬁrms and, similar
instrument for the date of PPP receipt using regional ex- to us, ﬁnd modest employment effects of the program.
posure to lenders that disbursed different amounts of PPP Faulkender et al. (2020) leverage the faster pace that com-
funding or predicted PPP funding. This variation allows us munity banks approved and disbursed funds relative to
to capture the effect of ﬁrms receiving loans during a cri- their counterparts and ﬁnd large employment effects of
sis in earlier versus later weeks. Results from this research the program. Bartik et al. (2020b) ﬁnd signiﬁcantly lower
design also show modest effects that fall within the conﬁ- self-reported survival probabilities for ﬁrms whose primary
dence interval of our bank exposure design. lender was a top-four bank. Doniger and Kay (2021) ﬁnd
The fact that the program disbursed signiﬁcant funds, that areas with a greater fraction of businesses receiving
yet had little effect on employment, raises the natural PPP funds right before the end of the ﬁrst round rather
question of what ﬁrms did with the money. We draw on than at the start of the second round had higher employ-
the Census Small Business Pulse Survey to show that PPP ment rates, with magnitudes that align with our uninstru-
funds allowed ﬁrms to build up liquidity and to meet loan mented matched sample analysis. While the conceptual
and other non-payroll spending commitments. For these approach in these papers is similar to ours, a key source
ﬁrms, the PPP may have strengthened balance sheets at a of difference is the extent to which the research design ac-
time when shelter-in-place orders prevented workers from counts for nonrandom program targeting. Given the role
doing work, and when UI was more generous than wages lenders played in allocating funds to areas that were ini-
for a large share of workers. tially less affected by the pandemic, accounting for target-
This ﬁnding is important because it implies that, while ing differences across areas is crucial for identifying the
employment effects are small in the short run, they may employment effects of the PPP. Our paper also contributes
well be positive in the longer run because ﬁrms are less
likely to close permanently. The program also likely had
important effects in terms of promoting ﬁnancial stability 3
Hubbard and Strain (2020) present some speciﬁcations that yield
by avoiding corporate loan defaults and business evictions. larger estimates, but the overall takeaway from their analysis appears in
Consistent with this notion, we ﬁnd suggestive evidence line with these other threshold designs.

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by identifying and exploiting ex ante bank characteristics (including FinTech) as a conduit for providing liquidity to
that affected banks’ ability to deploy funds quickly.4 ﬁrms is that, because nearly all small businesses have pre-
More broadly, this paper joins a literature focusing on existing relationships with banks, this connection could be
how government interventions following crises impact re- used to ensure timely transmission of funds.5
covery and the broader economy (Agarwal et al., 2017; The lending program was generally targeted toward
Mian and Suﬁ, 2012; Zwick and Mahon, 2017). Specif- small businesses of 500 or fewer employees.6 Although the
ically, we offer a comprehensive evaluation of the role initial round of funding was exhausted on April 16th, a
that banks played in allocating PPP funds, and the im- second round of $320 billion in PPP funding was passed
pact that this force had on program targeting and eco- by Congress as part of the fourth COVID-19 aid bill. Small
nomic outcomes. We contribute to an understanding of businesses were eligible as of April 3rd and independent
government responses to crises, including subsidized lend- contractors and self-employed workers were eligible as of
ing, tax incentives, and loan guarantees, a widely-used April 10th. The initial deadline for ﬁrms to apply to the
form of government intervention in credit markets (Smith, program was June 30th, but this was eventually extended
1983; Gale, 1990; 1991; Lucas, 2016; Kelly et al., 2016; to August 8th. Our analysis of the program runs through
Atkeson et al., 2019). A burgeoning empirical literature the end of August.7
examines the transmission and effects of loan guaran- The terms of the loan were the same for all businesses.
tees or tax-based stimulus on credit supply, employment, The maximum amount of a PPP loan is the lesser of 2.5
and small business outcomes (House and Shapiro, 2008; times the average monthly payroll costs or $10 million. The
Lelarge et al., 2010; Bachas et al., 2020; Barrot et al., 2019; average monthly payroll is based on prior year’s payroll af-
Mullins and Toro, 2017; Gonzalez-Uribe and Wang, 2019; ter subtracting the portion of compensation to individual
Zwick, 2021). Our paper contributes directly to this litera- employees that exceeds $10 0,0 0 0.8 The interest rate on all
ture by showing how policy transmission depends on the loans is 1% and their maturity is two years. Under SBA’s
agents delegated to deploy it (e.g., banks). These results are interpretation of the initial bill, the PPP loans can be for-
consistent with those of studies that emphasize the impor- given if two conditions are met. First, proceeds must be
tance of proximity (Granja et al., 2018), as well as emerging used to cover payroll costs, mortgage interest, rent, and
evidence from the pandemic that ﬁrms with pre-existing utility costs over the eight-week period following the pro-
borrowing and lending relationships received access to PPP vision of the loan, but not more than 25% of the loan for-
funds faster than their counterparts (Balyuk et al., 2020; giveness amount may be attributable to non-payroll costs.
Amiram and Rabetti, 2020; Li and Strahan, 2020). Second, employee counts and compensation levels must be
The article is organized as follows. Section 2 describes maintained. If companies cut pay or employment levels,
the PPP. Section 3 discusses the main data sources used. loans may not be forgiven.9 However, if companies lay off
Section 4 describes how the distribution of relative perfor- workers or cut compensation between February 15th and
mance in the PPP is correlated with bank and other char- April 26th, but subsequently restore their employment lev-
acteristics, documents how differences across banks in PPP els and employee compensation, their standing can be re-
activity imply geographic differences in PPP exposure, and stored.
explores the implications for PPP targeting to different ge- Congress expanded PPP on June 3rd, allowing more
ographic areas. Section 5 analyzes the effects of the PPP on ﬂexible terms for loan forgiveness. The updates to the PPP
local labor market and economic outcomes using our bank
exposure and timing research designs. Section 6 presents
aggregate impact estimates. Section 7 explores mecha- 5
Many of these relationships are limited to having trans-
nisms behind our results. Section 8 concludes. action accounts. Using data from a large survey on Facebook,
Alekseev et al. (2020) ﬁnd that half of ﬁrms report not having pre-
2. The Paycheck Protection Program (PPP) existing relationships as borrowers with banks, which appears to have
led to such ﬁrms initially struggling to access the program and eventually
switching lenders in order to receive funds.
The Paycheck Protection Program (PPP) began on April 6
A notable exception was made for ﬁrms operating in NAICS Code
3rd, 2020 as part of the CARES Act as a temporary source 72 (accommodations and food services), which are eligible to apply
of liquidity for small businesses, authorizing $349 billion insofar as they employ under 500 employees per physical location. Firms
in forgivable loans to help small businesses pay their em- whose maximum tangible net worth is not more than $15 million and
average net income after Federal income taxes (excluding any carry-over
ployees and additional ﬁxed expenses during the COVID-
losses) of the business for the two full ﬁscal years before the date of
19 pandemic. Firms applied for support through banks and the application is not more than $5 million can also apply. See https:
the Small Business Administration (SBA) was responsible //www.sba.com/funding- a- business/government- small- business- loans/
for overseeing the program and processing loan guarantees ppp/faq/small- business- concerns- eligibility/ for further information about
and forgiveness. A motivation for using the banking system the program.
7
The Consolidated Appropriations Act of 2021 included $284 billion
in additional forgivable loans for a second draw of PPP loans for small
4
Other studies take a more theoretical approach (Elenev et al., 2020; businesses. This program began in January 2021 and its eligibility criteria
Joaquim and Netto, 2020; Barrios et al., 2020), or study speciﬁc aspects were targeted to small businesses that experienced reductions in revenue.
of the PPP, such as the role of Fintechs, bank lending relationships, and Our analyzes do not encompass the effects of this second draw of PPP.
8
ﬁrm size in the allocation of funds under the program, the impact of Payroll costs include wages and salaries but also payments for vaca-
the program in supporting liquidity for ﬁrms of different size, and how tion, family and medical leave, healthcare coverage, retirement beneﬁts,
the distribution of funds varied with businesses’ ability to work remotely and state and local taxes.
9
(Erel and Liebersohn, 2020; Cororaton and Rosen, 2020; Papanikolaou and Loan payments on the remainder of the loan can be deferred for six
Schmidt, 2020; Morse and Bartlett, 2020; Chodorow-Reich et al., 2020). months and interest accrues at 1%.

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expanded the duration from eight weeks to twenty-four while our individual research design uses a matched sam-
and extended the deadline to rehire workers until the end ple of loans that we were able to match to the Homebase
of the year. This change effectively gave small businesses dataset.
more time to use program funds and rehire workers. Ad- We merge this data set with the Reports of Condition
ditionally, the minimum amount of funds used for payroll and Income (Call Reports) ﬁled by all active commercial
while still qualifying for forgiveness was lowered from 75% banks as of the ﬁrst quarter of 2020. We are able to match
to 60%. 4,370 bank participants in the PPP program to the Call Re-
An important feature of the program is that the SBA ports data set. We did not match 795 commercial and sav-
waived its standard “credit elsewhere” test used to grant ings banks that ﬁled a Call Report in the ﬁrst quarter of
regular SBA 7(a) loans. This test determines whether the 2020. We assume that these banks did not participate in
borrower has the ability to obtain the requested loan funds the PPP program and made no PPP loans. Overall, lenders
from alternative sources and poses a signiﬁcant barrier in in the PPP sample that we match to the Call Reports ac-
the access to regular SBA loans. Instead, under PPP rules, count for 90.5% of all loans disbursed under the PPP.
applicants were only required to provide documentation We obtain information about the ﬁnancial characteris-
of their payroll and other expenses, together with a sim- tics of each bank from the Call Reports. This data set in-
ple two-page application process where they certify that cludes information about the size, capital structure, and
the documents are true and that current economic uncer- portfolio composition of all banks operating in the US.
tainty makes this loan request necessary to support on- Importantly, we obtain information on the number and
going operations. In sum, the PPP program was designed amount of small business loans outstanding of each com-
to be a “ﬁrst-come-ﬁrst-served” program with eligibility mercial and savings bank from the “Loans to Small Busi-
guidelines that allowed it to reach a broad spectrum of ness and Small Farms Schedule” of the Call Reports. Us-
small businesses.10 ing this information, we benchmark the participation of all
During the ﬁrst weeks of April, demand for PPP loans commercial and savings banks in the PPP program relative
outstripped supply, which was limited by statute. Between to their share of the small business lending market prior
April 3rd and 16th all of the initial $349 billion was dis- to the program. We also use Call Report data to compute
bursed, and the program stopped issuing loans for a period measures of average capitalization and liquidity of banks
of time. The House and Senate passed a bill to add an ad- serving a region and to compute some ex ante characteris-
ditional $320 billion in funding on April 21st and 23rd, re- tics that limited banks’ ability to quickly deploy funds un-
spectively, which was signed into law on the 24th. The PPP der the program.
began accepting applications on April 27th for the second To compute measures of exposure of each state, county,
round of funding. While 60% of the second round funds and ZIP to PPP lenders, we combine the matched-PPP-Call-
were allocated within two weeks of initial disbursement, Reports data set with Summary of Deposits data containing
the remaining second round funds were disbursed slowly, the location of all branches and respective deposit amounts
with unallocated PPP funds being available in late June. for all depository institutions operating in the US as of
By early July, more than $130 billion remained available June 30th, 2019. In our bank exposure research design,
in PPP funds. Loan disbursement remained low through- we take advantage of the idea that small business lend-
out July and August, suggesting that the second round had ing is mostly local (e.g., Granja et al., 2018) and use the
suﬃcient funds to meet demand. The program stopped ac- distribution of deposits across geographic regions to cre-
cepting applications on August 8th, culminating in $525 ate our Bartik-style measure of exposure of these regions
billion in total disbursements. to lenders that over- or underperformed. We deﬁne per-
formance using each bank’s national share of PPP lending
relative to its national share of the small business lending
3. Data
market. We use County Business Patterns data to approxi-
mate the amount of PPP lending per establishment and the
Our primary source for data on the PPP comes from
fraction of establishments receiving PPP loans in the region
microdata made available through the Small Business Ad-
and to investigate whether the fraction of establishments
ministration (SBA) and the Department of Treasury. We are
receiving PPP loans in a region is affected by that region’s
able to observe all loans approved under the program. For
exposure to the performance of its local banks in the PPP.
all loans, the data include borrower and lender name, the
To evaluate whether PPP amounts were allocated to
borrower’s self-reported industry, location, corporate form,
areas that were hardest-hit by the COVID-19 crisis and
and workers covered by the loan. Our targeting analysis
whether the program improved economic employment and
and bank exposure research design use data for all loans
other economic outcomes following its passage, we use
aggregated to either the regional or local geography level,
data from multiple available sources on the employment,
social distancing, and health impact of the crisis. We ob-
10
The traditional SBA program responding to disasters is the Economic
tained detailed data on hours worked among employees
Injury Disaster Loan (EIDL) program. Recipients of an EIDL loan can re- of ﬁrms that use Homebase software to manage their
ceive a $10,0 0 0 loan advance that does not need to be paid back. EIDL scheduling and time clock.11 Homebase processes exact
loan advance amounts are deducted from PPP forgiveness. The EIDL loan hours worked by the employees of a large number of
itself is capped at a maximum of $2 million, is not forgivable, and the
funds can be used ﬂexibly for operating expenses. The EIDL and PPP pro-
grams functioned in tandem, and EIDL loans are further discussed in Ap-
11
pendix E. See https://joinhomebase.com/ for more information.

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J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

businesses in the US. We use information obtained from whole program, which is measured as
Homebase to track employment indicators at a weekly fre-
Share PPP − Share SBL
quency at the establishment level. The Homebase dataset P P P Eb = × 0.5
Share PPP + Share SBL
disproportionately covers small ﬁrms in food and beverage
service and retail; therefore, it is not representative of ag- where Share PPP is the share of PPP for bank b, and
gregate employment. At the same time, the Homebase data Share SBL is the bank’s small business loan share. In our
are quite useful for evaluating the employment impacts of main analysis, we use the PPPE measure of relative bank
the PPP speciﬁcally, since many hard-hit ﬁrms are in the performance that is based on the share of the number of
industries Homebase covers and much of the early employ- PPP and SBL loans of each bank.13 We prefer the number-
ment losses came from these ﬁrms. We use the Homebase based measure of relative bank performance because larger
data in our bank exposure and matched-sample analysis to businesses had prompter access to PPP loans (Balyuk et al.,
measure the impact of PPP funding on employment and 2020) and the volume-based measure of bank performance
business shutdowns. puts greater weight on large loans and less weight on
To broaden this analysis, we supplement the Homebase smaller loans to businesses whose access to the program
data with three additional data sources. First, we obtain was more likely constrained by lack of local access to com-
county-by-week initial unemployment insurance claims mercial banks that were quick to deploy loans.
from state web sites or by contacting state employment Fig. 1 shows the cumulative share of PPP (blue trian-
oﬃces for data. Second, we obtain small business revenue gles) and small business loans (red circles) by all banks at
data from Womply, a company that aggregates data from the end of the ﬁrst (Panel A) and second funding rounds
credit card processors. The Womply data includes aggre- (Panel B), with banks ordered by number-based PPPE.14
gate card spending at small businesses at the county level, Recall that values close to -0.5 indicate little to no par-
deﬁned by the location where a transaction occurred. We ticipation in the program relative to a bank’s initial small
complement these data sources with additional county- business lending share.
level employment data from Opportunity Insights, which There are signiﬁcant dislocations between the share of
are described in detail in Chetty et al. (2020).12 The em- PPP lending of underperforming banks and the share of
ployment data come from Paychex, Earnin, and Intuit. PPP that we would expect had these banks issued PPP
We additionally obtain counts of COVID-19 cases by loans in proportion to their share of the small business
county and state from the Center for Disease Control and lending market. If there were no heterogeneity in PPP per-
use data on the effectiveness of social distancing from Un- formance, the PPP and SBL shares would follow similar
acast. To understand the mechanisms underlying our re- patterns. This is not the case, and the S-shaped pattern
sults, we draw on data from the Census Bureau’s Small for PPP indicates that many banks disbursed relatively few
Business Pulse Survey (SBPS), a new representative sur- PPP loans, while roughly a third of banks disbursed half
vey that was launched to obtain real-time information tai- of the PPP loans. Panel A shows that commercial and sav-
lored towards small businesses. In Appendix A, we provide ings banks representing 20% of the small business lend-
a more detailed discussion of each data source and ﬁnal ing market simply did not participate at all in the ﬁrst
dataset construction. Finally, we obtain data from the Bu- round of the program (P P P E = −0.5 ). At the end of the
reau of Economic Analysis (BEA) on the median household ﬁrst round, the group of banks whose share of the program
income at the county level between 2017 and 2019 to con- was below their share of the small business lending mar-
trol for differences in economic activity at the local level ket (P P P E < 0 ) made less than 20% of the PPP loans, but
that could be related to the evolution of our outcomes of account for approximately half of the entire small business
interest during the pandemic. lending market. The top-4 banks are central to this fact, as
Table 1 shows that these banks accounted for 36% of total
4. Program targeting and bank performance pre-policy small business loans, but disbursed less than 3%
of all PPP loans in the ﬁrst round.
4.1. Paycheck Protection Program exposure Fig. 1, Panel B shows that these dislocations became
less pronounced during the second round, which ac-
Table 1 shows summary statistics for the 20 largest ﬁ- counted for 30% of total PPP lending. In the second round,
nancial institutions in the US, as measured by total assets. the banks that underperformed in the ﬁrst round were
Columns (2) and (3) report the share of total PPP volume able to catch up and partly close the performance gap.
in the ﬁrst round and overall, respectively, while columns
(7) and (8) report the share of the number of PPP loans of 13
Small business loans include outstanding balances on credit cards is-
each bank in the ﬁrst round and overall. Columns (4) and sued to small businesses, but it is not possible to ascertain what fraction
(9) show the share of the small business loan (SBL) market of these loans are credit card accounts. To the extent that these balances
could represent the most important lending relationship of many small
as of the fourth quarter of 2019 in terms of total volume
businesses, including these balances could be useful to capture the share
and number of loans, respectively. of ﬁrms that consider each bank as a banking relationship. Nevertheless,
In columns (5)–(6) and (10)–(11), we compute a mea- our ﬁndings that large banks underperform their respective share of small
sure of relative bank performance in round one and for the business loans are not affected when we consider only small business
loans with a principal amount between $10 0,0 0 0 and $1 million, which
are less likely to include outstanding credit card balances.
12 14
We also refer readers to Chetty et al. (2020) who provide comparisons Although the PPP application window continued into August, we refer
between Homebase and alternative high-frequency measures of aggregate to the end of June as the end of the second round because nearly all funds
employment. were disbursed by then.

730
Table 1 J. Granja, C. Makridis, C. Yannelis et al.
PPP Performance and PPPE for the Largest 20 Banks. Table 1 reports individual bank statistics and the PPPE index for the 20 largest ﬁnancial institutions in the United States. Total Assets is computed using
information from fourth quarter 2019 Call Reports. Share of PPP Volume is the total amount disbursed by each ﬁnancial institution relative to the total amount disbursed under either the ﬁrst round or both
rounds of the program. Share of SBL Market is the share of the total outstanding amount of small business loans held by each ﬁnancial institution relative to the total outstanding amount of small business loans
as of the fourth quarter of 2019. PPPE (Vol.) is the volume-based bank PPPE index. Total assets are in millions of USD. Share of PPP Loans is the total number of loans processed by each ﬁnancial institution
relative to the total number of loans processed in either the ﬁrst round or in both rounds of the program. Share of SBL Loans is the share of the total number of outstanding small business loans held by each
ﬁnancial institution relative to the total outstanding number of small business loans as of the fourth quarter of 2019. PPPE (Nbr.) is the number-based bank PPPE index.

(1) (2) (3) (4) (5) (6) (7) (8) (9) (10) (11)
Financial Institution Name Total Assets Share of PPP Share of PPP Share of PPPE R1 PPPE R1&2 Share of Share of Share of PPPE R1 PPPE R1&2
Volume R1 Volume R1&2 SBL Market (Vol.) (Vol.) PPP Loans PPP Loans SBL Loans (Nbr.) (Nbr.)
R1 R1&2

JPMORGAN CHASE BANK, NATIONAL ASSOCIATION 2337707 3.74% 5.84% 6.54% -0.136 -0.028 1.71% 6.16% 10.4% -0.360 -0.130
BANK OF AMERICA, NATIONAL ASSOCIATION 1866841 1.13% 5.10% 9.51% -0.393 -0.151 .595% 7.79% 11.8% -0.452 -0.103
WELLS FARGO BANK, NATIONAL ASSOCIATION 1736928 .038% 2.08% 6.50% -0.494 -0.257 .066% 4.14% 4.30% -0.485 -0.009
CITIBANK, N.A. 1453998 .394% .702% 2.12% -0.343 -0.251 .456% .693% 9.72% -0.455 -0.433
U.S. BANK NATIONAL ASSOCIATION 486004 .723% 1.48% 3.32% -0.321 -0.192 1.15% 2.25% 5.64% -0.331 -0.215
731 TRUIST BANK 461256 2.97% 2.62% 2.01% 0.096 0.066 2.02% 1.77% 1.73% 0.040 0.006
CAPITAL ONE, NATIONAL ASSOCIATION 453626 .022% .243% 2.82% -0.492 -0.421 .012% .335% 10.3% -0.499 -0.469
PNC BANK, NATIONAL ASSOCIATION 397703 2.75% 2.60% 1.12% 0.210 0.199 1.35% 1.70% 1.37% -0.004 0.054
BANK OF NEW YORK MELLON, THE 342225 0% 0% .002% -0.500 -0.500 0% 0% .000% -0.500 -0.500
TD BANK, N.A. 338272 1.83% 1.69% .687% 0.228 0.212 1.70% 1.88% .569% 0.249 0.268

STATE STREET BANK AND TRUST COMPANY 242148 0% .000% 0% 0.000 0.500 0% .000% 4.49% -0.500 0.413
CHARLES SCHWAB BANK 236995 0% 0% .074% -0.500 -0.500 0% 0% .003% -0.500 -0.500
MORGAN STANLEY BANK, N.A. 229681 0% 0% .144% -0.500 -0.500 0% 0% .008% -0.500 -0.500
GOLDMAN SACHS BANK USA 228836 0% 0% .003% -0.500 -0.500 0% 0% .000% -0.500 -0.500
HSBC BANK USA, NATIONAL ASSOCIATION 172888 .129% .240% .084% 0.105 0.240 .067% .093% .014% 0.328 0.369

Journal of Financial Economics 145 (2022) 725–761
FIFTH THIRD BANK, NATIONAL ASSOCIATION 167845 1.01% 1.06% .458% 0.188 0.200 .625% .861% .192% 0.265 0.318
ALLY BANK 167492 .213% .145% 2.11% -0.408 -0.436 .055% .021% 1.38% -0.461 -0.485
CITIZENS BANK, NATIONAL ASSOCIATION 165742 1.14% .992% .807% 0.086 0.051 1.60% 1.15% .527% 0.253 0.187
KEYBANK NATIONAL ASSOCIATION 143390 2.19% 1.59% .729% 0.251 0.186 2.14% .932% .274% 0.387 0.273
BMO HARRIS BANK NATIONAL ASSOCIATION 137588 1.20% .919% 1.95% -0.120 -0.181 .683% .489% .541% 0.058 -0.025

ALL OTHER BANKS 6889908 80.4% 72.6% 58.9% -0.042 -0.048 85.7% 69.6% 40.9% 0.215 0.212
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Fig. 1. PPPE and PPP Allocation. Fig. 1 plots the cumulative share of PPP and small business lending by all banks whose PPPE is below x, where x ∈
(−0.5, 0.5 ). Panel A plots cumulative amounts using PPP data as of the end of the ﬁrst round (April 16th, 2020), and Panel B reports cumulative amounts
using PPP data as of when the ﬂow of second round funds approximately ends (June 30th, 2020). Data is obtained from the SBA and commercial bank Call
Reports.

Yet, there remains a wide spread between banks. If most 4.2. Bank performance over time
eligible borrowers ultimately received funding, this pat-
tern suggests considerable reallocation of borrowers across Fig. 2 traces the evolution of PPP lending over time and
lenders during the program. Overall, the evidence is con- by bank size using different metrics. We plot cumulative
sistent with substantial heterogeneity across lenders in average PPPE using a number-based approach (Panel A),
their responses to the program’s rollout. average PPPE using a volume-based approach (Panel B), av-

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J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Fig. 2. Evolution of PPPE and Average Loan Size by Bank Size. Fig. 2 plots the evolution of average PPPE based on the number of PPP loans (Panel A),
average PPPE based on the volume of PPP loans (Panel B), the average loan amount (Panel C), and the fraction of loans above $1 million (Panel D) by bank
size bin. The size bins stratify all commercial banks operating as of the fourth quarter of 2019 based on their total assets. Data is obtained from the SBA
and commercial bank Call Reports.

erage loan size (Panel C), and the fraction of loans above In spite of this partial convergence, large banks still un-
$1 million (Panel D). Panels A and B show that banks with derperformed overall, consistent with press accounts sug-
total assets below $50 billion deployed a greater share of gesting that clients were frustrated by large banks’ inabil-
PPP loans relative to their respective share of small busi- ity to process PPP loans and switched to smaller banks
ness loans. In contrast, large banks underperformed rela- and non-banks. As demand for PPP funds waned during
tive to their share of small business lending. The differ- May, the evolution of bank PPPE across size categories
ences in bank PPPE across categories of bank size were stabilized.
very large throughout the ﬁrst round. These differences Fig. 2, Panels C and D suggest that all banks made
partly converged at the beginning of the second round.15 larger loans in the earliest weeks of the program. The av-
erage size of loans declines signiﬁcantly over time and
jumps down at the beginning of the second round. Nearly
50% of the loans disbursed by banks whose total assets
ranged between $50 billion and $1 trillion were over $1
15
The differences were noted in the popular press. For example, see the million as of April 3rd. That ﬁgure falls to roughly 30%
April 6th Wall Street Journal article, “Big Banks Favor Certain Customers
by April 8th and 20% by April 13th. By April 18th, loan
in $350 Billion Small-Business Loan Program” (https://www.wsj.com/
articles/big- banks- favor- certain- customers- in- 350- billion- small- business- sizes across banks of different sizes begin to converge be-
loan- program- 11586174401) and the July 31rd Wall Street Journal tween $20 0,0 0 0 and $450,0 0 0. This fact may be consistent
article, “When Their PPP Loans Didn’t Come Through, These Busi- with higher awareness and sophistication by larger bor-
nesses Broke Up With Their Banks” (https://www.wsj.com/articles/ rowers (Humphries et al., 2020), or with banks prioritiz-
when- their- ppp- loans- didnt- come- through- these- businesses- broke- up-
with- their- banks- 11596205736).
ing certain customers, such as existing loan customers who

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tend to be larger (Balyuk et al., 2020).16 Interestingly, the We use Call Report data to measure how much a bank
top-4 banks disbursed a relatively smaller fraction of large spends in wages relative to data processing expenses. This
loans compared to other large banks, which likely reﬂects measure serves as a proxy for bank reliance on a lending
the large number of microbusinesses and small businesses model that depends relatively more on labor from loan of-
connected to these banks, especially in urban regions. ﬁcers and less on information technology.
Overall, these ﬁndings suggest that the banking sys- Another critical factor in determining banks’ ability to
tem did not play a neutral role in mediating the alloca- quickly deploy PPP loans during the ﬁrst round of PPP
tion of PPP funds during the program. There were large was whether they had a pre-existing SBA lending relation-
differences in performance across banks, which likely re- ship. Lenders needed valid SBA portal credentials (E-Tran
ﬂect differences in the ability and willingness of banks to accounts) and access to the SBA’s Capital Access Financial
respond to the sudden inﬂux of PPP applications. In the System (CAFS) to submit PPP applications for their clients.
second round, most underperforming banks were able to Fintechs and other commercial banks with no previous SBA
improve their performance and ultimately process many lending experience had to wait until almost the end of the
PPP applications. Despite this improvement, differences in ﬁrst round of PPP to gain access to the SBA portal.18 To
ﬁrst round performance resulted in substantial differences measure the role of prior relationships with the SBA in ex-
in the timing of access to the program because of the ﬁrst- plaining relative bank performance during the ﬁrst round,
come-ﬁrst-served nature of the program and limited ﬁrst we create an indicator variable that captures whether the
round PPP budget. In Appendix B, we plot the Kaplan- bank had any prior experience working with the SBA in
Meier curve of the fraction of small businesses receiving the three years prior to the program. To capture the inten-
PPP approval. Only 25% of all PPP borrowers located in ZIP sity of the SBA relationship, we compute the fraction of the
codes whose banks underperformed obtained PPP approval number of SBA-guaranteed loans that the bank originated
prior to the end of the ﬁrst round. By contrast, approxi- relative to the average number of small business loans in
mately 42% of all PPP borrowers in ZIP codes whose banks the bank’s balance sheet over the previous three years.
overperformed had access to funds in the ﬁrst round. Finally, many banks were operating under active formal
supervisory enforcement actions related to deﬁciencies in
4.3. Bank attributes and predicted PPPE their commercial lending operations and in their compli-
ance with the Bank Secrecy Act and Anti-Money Launder-
A potential concern with our PPPE measure of relative ing requirements. Lenders subject to formal enforcement
bank performance is that it might reﬂect differences in lo- actions related to unsafe or unsound practices were not
cal demand for the program rather than differences in the automatically approved to make PPP loans according to the
ability or willingness to process applications. The broad el- April 2nd, Interim Final Rule of the SBA, which provided
igibility criteria and generous terms of the program likely information for lenders interested in participating in the
meant that demand for the program was high across most program. Accordingly, banks under a formal enforcement
locations and industries. Nevertheless, we address this spe- action could not submit PPP loan applications for their
ciﬁc concern by attempting to isolate variation in rela- clients without ﬁrst getting approval from the SBA, which
tive bank performance that is explained by differences in likely delayed their ability to quickly submit those applica-
banks’ ability to process applications under the program. tions.19
Speciﬁcally, we focus on three factors that capture differ- The most important case of a bank whose ability to
ences in pre-existing conditions and capacity constraints lend under the PPP was restricted by a formal enforce-
at the bank-level, which led some banks to respond more ment action is that of Wells Fargo. Wells Fargo had been
quickly to the program’s rollout. operating under an asset growth restriction imposed by
The ﬁrst factor is motivated by the fact that banks had its primary regulator since the aftermath of the 2016 fake
to employ an unprecedented amount of labor hours in a accounts scandal. Because of this restriction, Wells Fargo
short amount of time to process the unexpected and sud- could not make PPP loans because they would risk breach-
den inﬂux of PPP loan applications. Bank staff had to in-
teract with clients to collect and review their loan docu-
mentation and then submit the information in those ap- 18
For instance, according to Sparks (2020), Carter Bank & Trust of Mar-
plications through the SBA portal.17 Moreover, Bank Se- tinsville, Virginia was forced to wait for its SBA portal credentials and
only got access to the SBA portal for PPP applications 48 hours before
crecy Act and Anti-Money Laundering regulations meant
round one funds were exhausted. Another account of these diﬃculties can
that the staff had to perform customer due diligence for be found in Wooten (2020). Furthermore, even banks that had previously
new clients. Thus, banks with greater labor capacity had worked with the SBA had diﬃculties submitting applications either be-
a relative advantage in processing PPP loans more quickly. cause they needed additional authorizations or because they “forgot their
credentials or their login expired.”
19
For instance, PeopleFirst Bank from Joliet, Illinois was issued a formal
16
See for example, “Biggest banks ’prioritized’ larger clients for supervisory actions in 2019 due to weaknesses in its Bank Secrecy Act
small business loans, lawsuits claim,” (http://www.cbsnews.com/ and Anti-Money Laundering controls. Another example is Home Bank of
news/paycheck-protection-program- big- banks- loans- larger- clients- over- Arkansas from Portland, Arkansas which was under an active formal su-
smaller-businesses/). It is also the case that sole proprietors, who repre- pervisory written agreement for deﬁciencies in management and in their
sent approximately 15% of total PPP loans, were only allowed to apply internal audit control programs. Both banks did not disburse any PPP loan
with a delay that likely excluded many such ﬁrms from accessing funds in the ﬁrst round of PPP but processed a number of loans more com-
until the second round. mensurate with their small business lending share in the second round of
17
Sparks (2020) provides an account of the critical role of staﬃng limi- the program suggesting that the enforcement actions limited these banks’
tations in the deployment of the ﬁrst round of PPP. ability to respond quickly to the program.

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Table 2
Bank PPPE and Capacity Constraints. Table 2 examines the relation between bank performance in deploying PPP during the ﬁrst round of the program and
Wages
bank characteristics. The dependent variable, Bank PPPE, is the number-based bank PPPE index. (DataExpenses +Wages )
is a measure of labor intensity at the
bank that we compute as the ratio between bank wages (RIAD4135) and the sum of wages and data processing expenses (RIADC017). I(SBA Lender=1) is an
indicator variable that takes the value of one if the bank originated at least one SBA 7(a) guaranteed loan between 2017 and 2019. SBA Loans/SBL Loans is
the ratio between the number of SBA government-guaranteed loans that a bank originated between 2017 and 2019 and the number of all small business
loans (SBA and non-SBA) that the bank held on its balance sheet at the end of 2019. Active Enforcement Action is an indicator variable that takes the value
of one if the bank had an active enforcement action when the PPP was launched. I(Wells Fargo=1) is an indicator variable that takes the value of one for
Wells Fargo Bank. Columns (5) – (8) include controls for size deciles to ensure that the results are not driven by differences in size. Standard errors are
presented in parentheses, and are clustered at the state level. ∗ ∗ ∗ , ∗ ∗ , and ∗ , represent statistical signiﬁcance at 1%, 5%, and 10% levels, respectively.

(1) (2) (3) (4) (5) (6) (7) (8)
LHS is Bank PPPE
Wages
(DataExpenses+Wages ) 0.330∗ ∗ ∗ 0.251∗ ∗ ∗ 0.295∗ ∗ ∗ 0.283∗ ∗ ∗
(0.072) (0.060) (0.060) (0.055)
I(SBA Lender=1) 0.172∗ ∗ ∗ 0.170∗ ∗ ∗ 0.149∗ ∗ ∗ 0.150∗ ∗ ∗
(0.012) (0.011) (0.016) (0.016)
SBA Loans/SBL Loans 0.158∗ ∗ ∗ 0.173∗ ∗ ∗ 0.162∗ ∗ ∗ 0.176∗ ∗ ∗
(0.036) (0.036) (0.038) (0.037)
Active Enforcement Action -0.283∗ ∗ ∗ -0.280∗ ∗ ∗ -0.254∗ ∗ ∗ -0.256∗ ∗ ∗
(0.054) (0.052) (0.051) (0.050)
I(Wells Fargo=1) -0.418∗ ∗ ∗ -0.554∗ ∗ ∗ -0.470∗ ∗ ∗ -0.522∗ ∗ ∗
(0.053) (0.053) (0.056) (0.057)

Observations 5204 5212 5212 5204 5204 5212 5212 5204
Adjusted R2 0.005 0.076 0.009 0.088 0.058 0.103 0.062 0.114
Other Controls Yes Yes Yes Yes Yes Yes Yes Yes
Size Deciles No No No No Yes Yes Yes Yes

ing the asset cap. It was not until April 8th, 2020 that Fargo performed signiﬁcantly worse, on average, during the
the Federal Reserve issued a press release modifying the ﬁrst round. Column (4) shows that the explanatory power
growth restriction such that the bank could disburse PPP of each of these variables is not subsumed when we in-
loans. This delay meant that Wells Fargo could not process clude them in a multivariate speciﬁcation. In columns (5)–
PPP loans until the asset cap restriction was modiﬁed. As a (8), we further show that these estimated coeﬃcients are
result, its share of PPP lending in the ﬁrst round was just very similar when we include controls for bank size. Thus,
a small fraction of its share of small business lending.20 these factors are not merely capturing differences in per-
We examine how pre-PPP variation in these character- formance across banks of different sizes. We compute the
istics across banks affects their relative performance in de- predicted values of the empirical speciﬁcation in column
ploying the PPP during the ﬁrst round. We estimate cross (8) of Table 2 as a measure of relative bank performance
sectional regressions of the form: that is explained by these predetermined supply-side fric-
tions and likely to be orthogonal to differences in local de-
PPPE j = α j + ζ B j + ε j mand for PPP funds.
where P P P E j is PPPE for bank j at the end of the ﬁrst
round of the program, α j are size deciles, and B j are mea- 4.4. Geographic exposure to bank PPP performance
sures of the bank attributes: wages over wages plus data
expenses, pre-existing SBA lending relationships, and en- Signiﬁcant heterogeneity across lenders in processing
forcement actions. PPP loans would not necessarily result in aggregate dif-
The ﬁrst three columns of Table 2 represent the three ferences in PPP lending across regions if small businesses
factors discussed above. Column (1) shows that a mea- can easily substitute to lenders that are willing to accept
sure of labor capacity at the bank correlates positively with and expedite applications. If many lenders, however, prior-
bank PPPE, consistent with our hypothesis that greater ca- itize their existing business relationships in the processing
pacity to hand-process loan applications allowed banks to of PPP applications, ﬁrms’ pre-existing relationships might
disburse PPP loans at a faster rate. Column (2) shows that determine whether and when they are able to access PPP
the existence and strength of a prior relationship with funds. In this case, the exposure of geographic areas to
the SBA are both positively associated with bank perfor- banks that underperformed as PPP lenders might signiﬁ-
mance in rolling-out PPP funds.21 Column (3) shows that cantly determine the aggregate PPP amounts received by
banks with active enforcement actions as well as Wells small businesses located in these areas.
To examine if geographic areas that were exposed to
underperforming banks received fewer PPP funds, we con-
20
We highlight the case of Wells Fargo due to the importance of Wells struct regional measures of PPPE by distributing bank-level
Fargo in the economy and to the fact that we can point to an external
reason that was the subject of public discussion and directly explains the
21
underperformance of Wells Fargo during the ﬁrst round of the program. In Appendix B, we provide a plot of the relation between bank PPPE
In Appendix C, we repeat our main results using the exposure of each and the labor intensity of the bank as well as the existence and strength
local area to Wells Fargo branches as our main exposure measure. of the pre-existing SBA relationship.

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J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Table 3
Correlates of PPPE Exposure. Table 3 presents bivariate regressions of PPPE and Predicted PPPE on ZIP-level observables. Both PPPE, Predicted PPPE, and
observables are residualized with respect to state dummies. Variables have been normalized, so the coeﬃcients can be interpreted as a one-standard
deviation change in x produces a β -standard deviation change in PPPE exposure, where β is the reported coeﬃcient. ∗ ∗ ∗ , ∗ ∗ , and ∗ , represent statistical
signiﬁcance at 1%, 5%, and 10% levels, respectively.

LHS is Resid PPPE as of R1 LHS is Pred Resid PPPE as of R1

Coeﬃcient R2 N Coeﬃcient R2 N

Exposure Correlates:
Share of Top 4 Banks -0.703∗ ∗ ∗ 0.3619 35882 -0.603∗ ∗ ∗ 0.2584 35882
(0.006) (0.013)
Number of Branches per Capita -0.020∗ ∗ ∗ 0.0006 29545 -0.010∗ ∗ ∗ 0.0002 29545
(0.002) (0.001)
Share of Small Banks Deposits 0.400∗ ∗ ∗ 0.1592 35830 0.193∗ ∗ ∗ 0.0364 35830
(0.006) (0.006)
Other Correlates:
Log(Population) -0.203∗ ∗ ∗ 0.0476 29545 -0.065∗ ∗ ∗ 0.0046 29545
(0.005) (0.006)
Log(Population Density) -0.336∗ ∗ ∗ 0.1044 29545 -0.116∗ ∗ ∗ 0.0118 29545
(0.006) (0.006)
Social Distancing 0.225∗ ∗ ∗ 0.0412 35549 0.099∗ ∗ ∗ 0.0078 35549
(0.007) (0.008)
Covid Cases per Capita -0.262∗ ∗ ∗ 0.0797 35870 -0.120∗ ∗ ∗ 0.0161 35870
(0.007) (0.003)
Deaths per Capita -0.160∗ ∗ ∗ 0.0344 35870 -0.059∗ ∗ ∗ 0.0045 35870
(0.006) (0.004)
Unemployment Filing Ratios 0.012 0.0001 24576 0.056∗ ∗ ∗ 0.0019 24576
(0.008) (0.008)
Employment Opportunity Insights -0.075∗ ∗ ∗ 0.0071 19525 -0.012∗ 0.0002 19525
(0.007) (0.007)
Revenue Change of Small Business 0.159∗ ∗ ∗ 0.0333 29715 0.075∗ ∗ ∗ 0.0073 29715
(0.006) (0.006)

PPPE and predicted PPPE based on the share of the num- fewer constraints in deploying PPPE. Perhaps surprisingly,
ber of branches of each bank in a region.22 We ﬁrst con- ZIP codes with a greater branch density have slightly lower
sider the spatial distribution of PPPE during the ﬁrst round PPPE.
of funding. Exposure varies across the United States with The table suggests that early PPP disbursement may
western areas exhibiting much lower levels of PPPE and have been targeted towards areas less affected by the pan-
more rural areas in the Midwest and Northeast showing demic. More populous areas, areas with higher popula-
higher PPPE.23 tion density, and areas with higher COVID-19 cases and
To further understand the conditional distribution of deaths see lower PPPE. Greater social distancing—measured
PPPE and predicted PPPE, Table 3 reports the results of by a greater decline in the social distancing index—also see
bivariate regressions of ZIP-level PPPE and ZIP-level Pre- lower PPPE. There is no statistically signiﬁcant relationship
dicted PPPE on ZIP-level observables. The variables are nor- between unemployment and PPPE and areas that saw a
malized so that coeﬃcients can be interpreted as the ef- smaller decline in revenue for small businesses also have
fect of a one-standard-deviation change. The results are higher PPPE. In contrast, in the OI data, areas with greater
quite similar using both PPPE and predicted PPPE. The ta- employment declines have higher PPPE, which suggests
ble conﬁrms our earlier descriptive evidence—the top-4 better targeting by this measure. However, the magnitude
banks disbursed signiﬁcantly fewer PPP loans relative to of this relation is small. The coeﬃcients from regressions
their overall market share, while regions served by smaller using predicted PPPE have similar signs but smaller mag-
banks performed better and were served by banks with nitudes than those using PPPE. This pattern is consistent
with the idea that predicted PPPE captures supply-side
22
frictions that are less correlated with local economic, de-
By using the share of number of branches rather than the share of
deposits of each bank in a region, we implicitly downweight branches mographic, and health factors.
with signiﬁcant amounts of brokered and internet-deposit balances that Fig. 3 explores the relation between PPPE and PPP lend-
do not necessarily represent a commensurate share of the local small ing at the state-level using data from the Census Small
business relationships. If data were available, each bank’s respective pre- Business Pulse Survey at the end of the ﬁrst round of the
pandemic share of small business loans in each local area would be the
ideal weighting scheme. However, the best-available data, the Commu-
PPP.24 We plot the relationship between the percent of
nity Reinvestment Act (CRA) small business lending dataset, only includes ﬁrms receiving funds and state exposure to bank perfor-
county-level data and only provides data for large banks whose total as- mance. Panel A plots the fraction of all small businesses
sets exceed $1 billion.
23
Appendix B provides further information on the geography of target-
ing, a national map of county-level PPPE and the ﬁrst round distribution
24
of PPP funds, and a map of ZIP-level PPPE for the Chicago and New York Most of our analyzes are at the ZIP-level but the Census survey is only
metro areas. available at the state-level.

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Fig. 3. State Exposure to PPPE and Share of Small Businesses Requesting and Receiving PPP. Fig. 3 presents scatter plots comparing state-level exposure to
PPPE and Predicted PPPE and Census survey outcomes from after the ﬁrst round of funding. Panels A and C plots the percentage of ﬁrms receiving PPP
at the end of the ﬁrst round, and Panels B and D plots the percentage of small businesses reporting having applied to PPPE funds at the end of the ﬁrst
round of the PPP program. Data come from the Census Bureau Small Business Pulse Survey, SBA, Call Reports and Summary of Deposits.

reporting receiving PPP loans in each state during the ﬁrst funds at the state level does not seem to correlate with our
round of lending. There is a strong positive relationship be- state-level PPPE measure of relative bank performance.
tween PPP lending and PPPE at the state level. States with The bottom panels of Fig. 3 repeat the analysis using
the highest PPPE saw nearly 50% of small businesses re- predicted PPPE measure at the state level. We see very
ceiving PPP funding in round one; states with the lowest similar patterns as with our regular PPPE measure. Fig. 3,
PPPE saw just 20% of small businesses receiving funding. Panel C shows that there is a strong positive relationship
A potential concern with these results is that the between state exposure to banks with supply-side con-
causality runs in reverse. That is, banks do relatively better straints and the percentage of small businesses receiving
in deploying PPP in areas where demand for PPP loans is PPP at the end of the ﬁrst round. Panel D shows that there
strong. To address this concern, we compare survey mea- is little to no relationship between our predicted PPPE and
sures on ﬁrm applications and PPP receipt. The Small Busi- PPP applications. This fact supports the idea that our pre-
ness Census survey includes questions on both PPP appli- dicted PPPE measure captures supply-side frictions that af-
cation and receipt. Fig. 3, Panel B compares PPPE to the fected banks’ ability to process PPP loans and not differ-
percentage of businesses in each state that report having ences in exposure to local demand.
applied for PPP funds as of the end of round one in each Fig. 4 explores the relation between exposure to bank
state. Between 65% and 80% of small businesses in each PPP performance during the ﬁrst round and PPP lending at
state report having applied for PPP funds at the end of the a ﬁner geographic level. Speciﬁcally, we compute the local
ﬁrst round. Importantly, the likelihood of PPP application is exposure to bank performance at the ZIP level by taking
unrelated with state PPPE. In other words, demand for PPP the weighted average of bank PPPE or predicted PPPE for

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Fig. 4. ZIP Exposure to First Round PPPE and PPP Coverage over Time. Fig. 4 plots binned scatter plots of the average fraction of small business establish-
ments that received a PPP loan versus ZIP-level PPPE (Panel A) and Zip-level Predicted PPPE (Panel B). Eligible establishment counts equal all establishments
in a ZIP less an estimate of the share of establishments with more than 500 employees (which are not eligible for PPP) plus an estimate of the number of
proprietorships likely to apply for PPP. Both variables are demeaned at the state level to present the within-state relationship. Data come from SBA, Call
Reports, Summary of Deposits, and County Business Patterns.

all branches that are either in the ZIP or within ten miles variation. Panel A shows the relationship between zip-level
of the center of the respective ZIP code. We then partition PPPE and the fraction of businesses receiving PPP, while
ZIPs in bins based on their PPPE after demeaning using Panel B shows the same relationship replacing PPPE with
the average PPPE of their respective state to ensure that predicted PPPE. Both panels show similar results. A strong
the empirical relations hold when we use only within-state positive relation between ZIP PPPE and ZIP predicted PPPE

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J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

and the fraction of businesses receiving PPP during the ﬁrst through both rounds of the program. Consistent with the
round further supports the idea that the initial allocation ﬁndings above, local ZIP exposure to banks that over- or
of funds was shaped by exposure to the performance of underperformed in the ﬁrst round is no longer positively
local banks.25 associated with the fraction of businesses receiving PPP
The strong positive relation between ZIP PPPE or pre- after both rounds of the program. If anything, there is
dicted PPPE and the fraction of businesses receiving PPP a modest negative relationship between round one PPPE
during the ﬁrst round of the program persists over the fol- and total PPP loans per establishment. This relationship
lowing weeks but becomes gradually weaker later in May is signiﬁcant using PPPE, and insigniﬁcant at conventional
and into June. This pattern offers further evidence that levels using predicted PPPE. This result further suggests
the relation between PPPE and the fraction of businesses that as supply-side frictions subsided during the second
receiving PPP in the ﬁrst round is driven not by differ- round of the program, the relation between PPPE and the
ences in demand for PPP loans across regions but rather by fraction of businesses receiving PPP ﬂattened, which in-
their exposure to banks that underperformed. Otherwise, dicates that differences in demand for PPP funds were
this positive association would not necessarily disappear unlikely to explain the positive relation during the ﬁrst
over time. The pattern suggests either that underperform- round.
ing local banks improved their performance in deploying A potential explanation for the gradual weakening of
PPP over time or that small businesses in areas where lo- the relation between local PPPE and the fraction of busi-
cal banks underperformed were able to obtain funds from nesses receiving PPP is that non-local banks and nonbanks
other non-local lenders. stepped in to substitute for underperforming local banks.
We further probe the relation between local PPPE and To investigate this possibility, we decompose the total frac-
the allocation of PPP funds in Table 4. There, we assess the tion of establishments receiving PPP in each ZIP and indus-
association between ZIP PPPE or predicted PPPE and the try into the fraction of establishments receiving loans from
fraction of businesses receiving PPP in each ZIP-by-industry local banks (deﬁned as banks with a branch within 10
group after conditioning on state-by-industry ﬁxed effects. miles of a ZIP code centroid), non-local banks (deﬁned as
In each panel, the top row shows the relationship be- all banks with branches that are farther than 10 miles from
tween PPPE and the fraction of businesses receiving PPP, the ZIP), credit unions, Fintechs, and all other nonbanks
while the bottom row shows the same relationship replac- participants. Fig. 5 shows the average fraction of establish-
ing PPPE with predicted PPPE. Again, both panels show ments receiving PPP during round one, round two, and the
broadly similar results. Thus, we evaluate whether busi- entire program by source of PPP funding. On average, ap-
nesses within the same state and industry had different proximately 20% of all establishments in a ZIP were able to
access to PPP loans because they were located in ZIP codes obtain funding during the ﬁrst round, and local banks ac-
whose nearest banks performed relatively well compared counted for most of these loans. Fintech lenders and non-
to businesses in the same state and industry but in ZIP banks participated very little during the ﬁrst round. During
codes whose banks underperformed. the second round, local banks still accounted for the ma-
Column (1) of Table 4, Panel A, further supports the jority of disbursed loans, but Fintech lenders and especially
idea that local exposure to banks that overperformed in non-local banks participated to a much larger extent. This
the PPP had a positive impact on the ability of busi- pattern is consistent with Fintech institutions substituting
nesses to obtain PPP funds during the ﬁrst round. Even for local banks in the area. Over the entire program, lo-
within a given state and industry, being in the same ZIP cal banks accounted for more than two-thirds of all loans,
or within 10 miles of banks that overperformed in the while Fintechs and other non-banks institutions accounted
ﬁrst round was associated with a signiﬁcantly higher share for ﬁve percent of loans.27
of businesses receiving PPP during the ﬁrst round. We Next, we evaluate whether the presence of non-local
ﬁnd similar conclusions when we measure local ZIP ex- banks and Fintechs mattered most in areas that were ex-
posure to banks that were constrained processing PPP ap- posed to local banks that underperformed in the PPP. Un-
plications using our predicted PPPE measure.26 In column surprisingly, in column (2) of Table 4, Panel A, we show
(1) of Panel B, we assess whether this impact persisted that local PPPE is associated with a greater fraction of es-
tablishments receiving loans from local banks in the ﬁrst
round of the program. Columns (3), (4), and (6) show that
25
In this ﬁgure, we measure PPP loans relative to eligible establish- ZIP PPPE is unrelated with the fraction of establishments
ments, which equals all establishments in a ZIP less an estimate of the
share of establishments with more than 500 employees (which are not
receiving loans from non-local banks, credit unions, and
eligible for PPP) plus an estimate of the number of proprietorships likely
to apply for PPP.
26
In Appendix B, we show that our results are robust to including
27
county-by-industry ﬁxed effects. Thus, we ﬁnd a positive relationship be- Lenders that were not classiﬁed as depository institutions were clas-
tween ZIP PPPE and the fraction of businesses receiving PPP even when siﬁed between community lenders, credit unions, and other businesses
we compare businesses that are located within the same county and in- manually. We classiﬁed the following lenders as Fintech companies: Kab-
dustry and thus are even more likely to be exposed to similar external bage, BSD Capital, Lendistry, Flagship, Marketplace, Fund-Ex Solutions,
conditions. Having said that, we use state-by-industry ﬁxed effects in our Fundbox, Fountainhead, Intuit, Itria, MBE, Mountain Bizcapital, Readycap
analysis of employment impacts because the Homebase data does not and Newtek. Some of these lenders, including Kabbage, associated with
cover the full set of counties and industries. This limitation substantially banks in the ﬁrst round because they could not yet operate on a stan-
reduces the amount of variation available for estimation within these nar- dalone basis due to program rules. Prior to the eligibility of Fintechs, we
row cells, preventing us from drawing strong inference on employment count these as non-local banks and thus some substitution between local
impacts when relying only on this variation. and non-local banks could come from collaboration with Fintechs.

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Table 4
ZIP PPPE in Round 1 and PPP Reallocation across Funding Sources. Table 4 shows the correlation between PPPE and the fraction of eligible establishments
receiving PPP loans from different sources in the ﬁrst and second rounds of the program. The left-hand-side variable in column (1) is the fraction of
eligible establishments within a ZIP and 2-digit NAICS industry that received PPP in the ﬁrst round in Panel A and in both rounds in Panel B. Left-hand-
side variables in other columns represent a decomposition of the dependent variable in column (1) into the fraction of establishments within a ZIP and
2-digit NAICS industry that received PPP from local banks, non-local banks, credit unions, FinTech companies, and other nonbanks. ZIP PPPE (Round 1)
is the weighted average of bank PPPE during the ﬁrst round at the ZIP level. The weights are deﬁned by the share of the number of branches of each
bank within 10 miles of the center of the respective ZIP. ZIP PPPE is standardized to permit coeﬃcients to be interpreted as the effect of a one-standard-
deviation increase in ZIP PPPE and observations are weighted by the number of eligible establishments in each zip-industry pair. Predicted PPPE is the
weighted average of predicted bank PPPE during the ﬁrst round at the ZIP level. The predicted values of bank PPPE are obtained from estimating the
empirical speciﬁcation of column (8) of Table 2. The weights are deﬁned by the share of the number of branches of each bank in the zip code or within
10 miles of the center of the respective ZIP. Eligible establishment counts equal all establishments in a ZIP less an estimate of the share of establishments
with more than 500 employees (which are not eligible for PPP) plus an estimate of the number of proprietorships likely to apply for PPP. All regressions
include state-by-NAICS ﬁxed effects. Standard errors are presented in parentheses, and are clustered at the state level. ∗ ∗ ∗ , ∗ ∗ , and ∗ , represent statistical
signiﬁcance at 1%, 5%, and 10% levels, respectively.

Panel A: Allocation in Round 1

(1) (2) (3) (4) (5) (6)

PPP Loans Relative to All Establishments by Lender Source

PPP/Est (%) Local Banks Non-Local Banks Credit Unions FinTech Nonbanks
∗∗∗ ∗∗∗ ∗∗∗
Zip PPPE (Round #1) 5.458 5.401 0.162 0.152 -0.204 -0.007
(0.736) (0.581) (0.117) (0.109) (0.021) (0.020)

Observations 250078 250678 251344 251468 251488 251435
Adjusted R2 0.408 0.390 0.126 0.156 0.294 0.045
State×Industry FE Yes Yes Yes Yes Yes Yes

PPP/Est (%) Local Banks Non-Local Banks Credit Unions FinTech Nonbanks

Predicted PPPE 2.837∗ ∗ ∗ 2.961∗ ∗ ∗ -0.085 0.054 -0.073∗ ∗ ∗ 0.003
(0.981) (0.866) (0.149) (0.093) (0.024) (0.017)

Observations 250078 250678 251344 251468 251488 251435
Adjusted R2 0.380 0.357 0.126 0.155 0.290 0.045
State×Industry FE Yes Yes Yes Yes Yes Yes

Panel B: Allocation in Round 1 and 2

(1) (2) (3) (4) (5) (6)

PPP Loans Relative to All Establishments by Lender Source

PPP/Est (%) Local Banks Non-Local Banks Credit Unions FinTech Nonbanks

Zip PPPE (Round #1) -1.580∗ ∗ ∗ 1.224∗ ∗ ∗ -1.942∗ ∗ ∗ 0.310 -1.480∗ ∗ ∗ -0.139∗
(0.345) (0.350) (0.271) (0.336) (0.191) (0.080)

Observations 234128 244928 250263 251342 251377 251387
Adjusted R2 0.359 0.324 0.199 0.222 0.231 0.088
State×Industry FE Yes Yes Yes Yes Yes Yes

PPP/Est (%) Local Banks Non-Local Banks Credit Unions FinTech Nonbanks

Predicted PPPE -0.660 0.932∗ -1.095∗ ∗ ∗ 0.031 -0.751∗ ∗ ∗ -0.040
(0.453) (0.516) (0.391) (0.287) (0.262) (0.041)

Observations 234128 244928 250263 251342 251377 251387
Adjusted R2 0.358 0.323 0.193 0.221 0.213 0.087
State×Industry FE Yes Yes Yes Yes Yes Yes

nonbank lenders in the ﬁrst round. Column (5) shows a ing the second round of the PPP program. In column
negative relation between local bank performance and the (2), local PPPE remains an important determinant of the
fraction of local establishments served by Fintechs, sug- fraction of loans from local banks, though the relation-
gesting that these institutions played a greater role in PPP ship is somewhat weaker. This weaker relationship possi-
lending in areas with worse local bank performance. De- bly results from improved performance of low-PPPE banks
spite the statistical signiﬁcance of the effects of column during the second round. Consistent with the ﬁndings in
(5), their economic magnitude is relatively small, indi- Erel and Liebersohn (2020), we ﬁnd in columns (3), (4), (5),
cating these substitute lenders were unable to offset the and (6) that other ﬁnancial institutions such as non-local
dislocations from underperforming local banks during the banks and Fintechs substitute for underperforming local
ﬁrst round. banks. Non-local banks are the most important source of
In columns (2) through (6) of Table 4, Panel B, we ex- substitute funds. Fintechs are less important but still quite
amine if these non-local sources of funding had an eco- elastic to the effect of weak local bank performance. By the
nomically larger role in substituting for local banks dur- end of the program, the total effect of substitute lenders is

740
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Fig. 5. Share of Establishments Receiving PPP by Lender Type. Figure 5 shows the number of PPP loans broken down by lender type and funding round,
scaled by the total number of establishments. Data come from the SBA, FDIC Summary of Deposits, and Census.

large enough to fully offset the weak performance of local distortions during the second round, we ﬁnd that the rela-
banks in low PPPE areas.28 tionship between the share of business shutdowns in the
week of March 22nd–March 28th and the share of busi-
nesses receiving PPP weakens substantially when we con-
4.5. Are PPP allocations targeted to the hardest hit regions?
sider the share of businesses receiving PPP during both
rounds. In Panel B, we repeat the analysis using the de-
Were PPP funds disbursed to geographic areas that
cline in hours worked between January and the week of
were initially most affected by the pandemic? Given that
March 22nd–March 28th. An analogous relationship holds,
one of the policy goals of the program was to inject
with regions receiving more PPP funding during the ﬁrst
liquidity into small businesses and prevent unnecessary
round displaying smaller shocks in terms of the initial de-
bankruptcies, we examine whether funds ﬂowed to dis-
cline in hours worked and with this relationship becoming
tressed areas with more pre-policy economic dislocation
weaker or even nonexistent when we consider PPP fund-
and disease spread. In addition, we ask whether the signif-
ing over the two rounds. In Panel C, we repeat the analysis
icant heterogeneity in bank performance and exposure to
using the decline in the number of employees. The results
bank performance across regions played an important role
mirror those in Panels A and B; regions receiving more PPP
in the targeting of the program.
funding during the ﬁrst round see a smaller reduction in
Fig. 6 partitions the distribution of ZIP codes according
the number of employees prior to the PPP. There is little
to the ratio of PPP loans in the ﬁrst round to the num-
relationship in the second round.
ber of establishments in the ZIP code. We then compare
In Appendix D, we further conﬁrm our ﬁndings us-
areas with high and low PPP allocations in terms of em-
ing the Homebase data with other levels of aggregation
ployment outcomes prior to any funds being distributed.
and using other data sources—we ﬁnd no consistent rela-
In Panel A, we observe a negative relationship between the
tionship between PPP allocation and bank exposure with
share of business shutdowns in the week of March 22nd–
UI claims or small business revenues. We also explore
March 28th and the share of businesses receiving PPP in
whether funds initially ﬂowed to areas with early pan-
round one.29 Consistent with the broad deﬁnition of eligi-
demic outbreaks. There is a slight negative correlation
bility of the program and with a decline of the supply-side
between PPP receipt and COVID-19 conﬁrmed cases and
deaths at the state level. There is little correlation between
28
In Appendix B, we use a proprietary dataset obtained through a mem-
the magnitude of social distancing at the state level and
ber bank of the Community Development Bankers Association (CDBA) and PPP allocations. The totality of the evidence suggests that
we ﬁnd that the PPP loans issued by that member bank to new clients are there was little targeting of funds in the ﬁrst round to ge-
late relative to those from existing clients and these new clients come ographic areas that were harder hit by the pandemic and,
predominantly from regions served by banks with low-PPPE performance
if anything, areas hit harder by the virus and subsequent
relative to the PPPE of the regions where the bank and its existing clients
were located. These results further indicate that exposure to banks with economic impacts initially received smaller allocations.
low PPPE performance forced small businesses to seek PPP funding else- This interpretation remains true when considering both
where. rounds of funding, as the relationship between shock
29
Following Bartik et al. (2020a), we deﬁne a business shutdown as severity and PPP funding turns less negative without turn-
businesses that report zero hours worked during a week using the data
ing positive. Our ﬁndings are also consistent with the
from HomeBase.

741
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Fig. 6. Targeting of PPP Allocation (First Round and Overall). Fig. 6 stratiﬁes all businesses in Homebase in 10 bins based on the fraction of establishments
in their ZIP code receiving PPP during the ﬁrst round and during both rounds combined. Panel A plots for each bin the share of Homebase businesses that
shut down in the week of March 22nd–March 28th. Panel B plots for each bin the average decline in hours worked in the week of March 22nd–March
28th relative to a baseline of the average weekly hours worked in the last two weeks of January. Panel C plots for each bin the average decline in the
number of employees in the week of March 22nd–March 28th relative to a baseline of the average number of employees in the last two weeks of January.
Data are from SBA, Homebase, and County Business Patterns.

742
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

broad eligibility criteria for PPP loans—most ﬁrms below and its timing. With the second round of funds, which be-
the size threshold could apply for funding—and the ab- gan on April 27th, PPP funding limits were no longer bind-
sence of conditionality in program generosity—loan for- ing and the gap between high and low PPPE exposure re-
giveness did not depend on shock severity. The argument gions mostly closed. Thus, as we move to study the pro-
in Barrios et al. (2020) that ﬁrm payroll closely predicted gram later in May and through the end of August, we will
PPP loan receipt accords with this view. Nevertheless, our interpret the research design as assigning some ﬁrms fund-
bank-level results also point to an important loan supply ing with a delay, instead of as assigning some ﬁrms no
factor distorting the distribution of PPP loans, especially funding at all.
during the program’s initial rollout. In our main analysis, we present reduced form regres-
sions of employment and local economic outcomes on
5. Employment impacts and local economic activity PPPE and predicted PPPE while allowing for separate treat-
ment effects by week or month. Given the rapid nature
5.1. Research design and size of the economic shock, we highlight two impor-
tant considerations when analyzing data from this time
Did banks’ unequal ability and willingness to quickly period. First, our targeting analysis shows that regions re-
process PPP applications have any impact in explaining the ceiving more PPP funding were less hard hit by the initial
employment effects of the PPP? Our results on PPP per- shock, in part due to the banking channel we emphasize.
formance differences across banks motivate two comple- Thus, it is important to properly condition on this non-
mentary research designs for evaluating the PPP. The ba- random assignment of PPP funding. If one does not break
sic idea is to use differences in local area PPP exposure out the data ﬁnely enough or condition properly for tar-
(PPPE), as well as pre-determined supply-side variation in geting differences—for example, by treating the last weeks
PPPE (predicted PPPE), to partition geographies and com- of March as a pre-period benchmark—then one might de-
pare the evolution of local outcomes for high versus low tect a spurious effect of the program. This issue is very
PPPE regions. By exploiting differential exposure to banks clear when we examine week-by-week outcomes around
that performed poorly in distributing PPP funding during the policy window.
the ﬁrst round of the program, we can isolate the effect To account for these targeting differences, we estimate
of the PPP from other differences across regions that may the effects of the program by comparing weeks in the
drive differences in PPP loan demand. As described above, post-PPP period to the two weeks in the post-lockdown,
we map bank level aggregates for PPP lending from the pre-PPP period. We also include time-varying controls and
SBA data onto local geographies using measures of local state-by-time-by-industry ﬁxed effects to estimate treat-
bank branch presence. The research design is akin to a Bar- ment effects under weaker versions of the Bartik assump-
tik instrument and therefore relies on the assumption that tion. Controls include the social distance index, COVID
pre-policy bank branch shares are not correlated with the cases per capita and deaths per capita measured as of
various outcomes we study, conditional on observables.30 week 9, all interacted with indicator variables for the
We focus our analysis on the time period between the months of April, May, June, July, and August. We also in-
third week of January and the end of the program in clude bank controls for the average tier-1 capital and core
the last week of August to study the short- and medium- deposit ratios of all banks within a 10-mile radius of the
term effects of the PPP in the immediate aftermath of the ZIP code, weighted by the number of banks’ branches
pandemic when the injection of liquidity was thought to within a 10-mile radius of the ZIP code. Once we adjust
matter the most for sustaining employment. Starting the for targeting differences, including these more restrictive
sample period in January allows us to establish a base- controls has little effect on our estimates.
line period prior to the pandemic, thereby controlling for A second consideration is that research designs that ex-
time-invariant determinants of economic activity within ploit differences in PPP receipt or application without an
the same location. instrument for loan supply or eligibility will likely over-
The PPP began accepting loans on April 3rd and all of state the impact of the program. Demand for PPP loans
the initial funds were exhausted by April 16th. During this is likely correlated with omitted ﬁrm-level factors, such as
period, banks played a key role in allocating limited funds, whether the ﬁrm anticipates being able to use the funds
creating the variation we use to identify the effects of the during the forgiveness window. Our PPPE and predicted
program. We exploit the fact that ﬁrms are located in re- PPPE instruments attempt to isolate loan supply drivers in-
gions that vary in their exposure to bank performance, dependent of loan demand.
which mediates both the level of PPP loan disbursement

5.2. Small business employment
30
Appendix G evaluates the research design using diagnostic Bartik tests
following Goldsmith-Pinkham et al. (2020). The diagnostics provide some
intuition about the sources of identiﬁcation. First, our estimates are not A signiﬁcant portion of the policy and media interest
driven by just one or two banks, or even by the top-4 banks alone. Sec- in the PPP concerned the program’s potential employment
ond, inﬂuential banks tend to be either large or mid-sized banks and effects. Previous work has shown that credit market dis-
those with PPPE pointing to substantial over- or underperformance. Third, ruptions can have large effects on employment (Chodorow-
more of the identifying variation comes from banks with positive Rotem-
berg weights, which enables the Bartik estimator to be interpreted more
Reich, 2014), which may have in part motivated the quick
easily as a LATE. Finally, bank-branch shares are only weakly correlated policy response. We examine several employment out-
with local observables, supporting the key identiﬁcation assumption. comes, including business shutdowns (i.e., hours worked

743
J. Granja, C. Makridis, C. Yannelis et al.

reduced to zero during the entire week), declines in hours
worked, and declines in the number of employees.

Fig. 7 presents simple difference-in-difference graphs
for each of our Homebase employment outcomes. We di-
vide all firms in the sample based on whether they are lo-
cated in regions with above- or below-median PPPE or pre-
dicted PPPE. We take advantage of the granularity in the
Homebase data and conduct our analysis at the ZIP level.
We use vertical markers to demarcate the post-lockdown,
pre-PPP period; the post-PPP launch; when the first round
of PPP funds are exhausted and when the second round
of PPP funding begins. Predicted PPPE is determined us-
ing the supply-side factors in Table 2: wages over wages
plus data expenses, pre-existing SBA lending relationships,
and enforcement actions. Panel A shows business shut-
downs, Panel B shows hours worked, and Panel C shows
the change in the number of employees. Results using both
PPPE measures point to very similar patterns.

Prior to the initial lockdown orders, employment out-
comes in high- and low-PPPE areas evolve very similarly,
even in the absence of controls, suggesting that in nor-
mal times these areas were following similar trends. We
then see a dramatic decline in each employment outcome
starting in the week prior to the lockdowns. Consistent
with our targeting results, this decline is modestly larger
for regions with low PPPE. The difference in employment
declines is somewhat smaller when we split the sample
into high- and low-predicted PPPE ZIPs, which indicates
that the predicted PPPE measure is less correlated with
geographic differences in targeting of the program. Impor-
tantly, during the first round of PPP, the gap between high
and low PPPE areas does not widen further, indicating lit-
tle incremental impact of PPP during this time. The gap
for the ratio of hours worked and for the change in the
number of employees widens gradually during May and
June, which suggests intensive-margin employment effects,
while the gap for shutdowns changes little.

Fig. 8 plots coefficients and standard errors for regres-
sions of differences in employment outcomes on exposure
to PPPE and predicted PPPE. We estimate weekly regres-
sions of the form:

AYijne = Msn + BPPPE; + VXijne + €ijne

where Ayjjn¢ is the difference between the Homebase out-
comes Yjjn¢ (business shutdown, hours decline, and em-
ployee counts) of a firm i in each week relative to the aver-
age value in the two weeks prior to the PPP launch; PPPE;
is either PPPE or predicted PPPE in ZIP j; asn are state-
by-industry fixed effects; and Xjj,; are additional control
variables. The plots in the top panels use our main PPPE
measure as the variable of interest, while the bottom pan-
els estimate the local projections using the predicted PPPE
variable as the main variable of interest. Panel A, B, and
C plot estimates where the outcome variable is the differ-
ence in business shutdowns, the decline in hours worked,
and the change in the number of employees, respectively.

The coefficients capture the effect of PPP exposure on
the outcome of interest under the identifying assumption
that the firms and areas differentially exposed would have
trended similarly in the absence of the PPP after condi-
tioning on covariates. Given the fast-moving employment

744

Journal of Financial Economics 145 (2022) 725-761

losses and differential state policies, the choice of base-
line and fixed effects are particularly important. We ac-
count for differential targeting by using as a baseline the
two weeks prior to PPP funds being disbursed, which is
consistent with the aggregate time series in Fig. 7. The
weekly regressions combined with state-by-industry fixed
effects imply that we are comparing trajectories for firms
within state-by-industry groups and allowing general time
trends within these groups. Focusing on within-state es-
timates is particularly important because many lockdown
and reopening policy decisions occur at the state level, and
there is some evidence that state shutdown orders partly
influenced the decline in economic activity (Goolsbee and
Syverson, 2020).

For both PPPE measures, the results align with the raw
differences across high and low PPPE regions in Fig. 7.
When using predicted PPPE, we see weaker evidence of
targeting as the gap opens following the launch of the PPP.
We see little effect on business shutdowns until the end of
the sample period. Beginning in May, there are statistically
significant positive effects on hours worked and the num-
ber of employees, which remain stable through August.

Table 5 presents our regression estimates, in which we
pool the weekly effects into months. We estimate the fol-
lowing specification:

+ B21[May] = PPPE;

+ B31[June] x PPPE;

+ Ba4llJuly] x PPPE;

+ Bsl[August] x PPPE; + yXj + €isjnt

(1)

where Ej; jn¢ is an outcome (business shutdowns, the de-
cline in hours worked, or the number of employees) for
firm i in state s, ZIP j, and industry n in week t. The out-
come variable for each establishment is measured in that
week relative to the hours worked in that same estab-
lishment during the two weeks prior to the PPP launch.
The term a; captures firm fixed effects, dsn¢ are state-by-
industry-by-week fixed effects, PPPE; is ZIP PPPE or pre-
dicted PPPE, and éjsjn¢ is an error term. We also include in-
teractions between the social distance index, COVID cases
and deaths per capita measured as of week 9, all inter-
acted with indicator variables for April, May, June, July, and
August. These controls capture time-varying effects of the
initial severity of the pandemic at the local level. We fur-
ther include bank controls for the average tier-1 capital
and core deposit ratios of all banks within a 10-mile ra-
dius of the ZIP code where the firm is located, weighted
by the number of banks’ branches within a 10-mile radius
of the ZIP code.

The coefficients 6;, 62, 63, 64, and Bs capture the dif-
ferential effect of PPP exposure on the outcome of inter-
est in each month relative to the two weeks prior to the
launch of PPP. The coefficient 6; captures the average ef-
fect of exposure to better bank PPP performance after the
initial rollout of the PPP, when most regions remained un-
der some form of shelter-in-place order. The coefficient 6
captures effects in May, as many regions began to lift re-
strictions. The coefficients 63, 64, and Bs capture medium-
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Fig. 7. PPPE and Homebase Employment Outcomes. Fig. 7 shows the ratio of hours worked over time, the percent of businesses shut down, and the ratio
of number of employees splitting the sample into regions with above- versus below-median PPPE and above versus below-median predicted PPPE. Data
are from SBA, Homebase, County Business Patterns.

745
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725-761

anel C. Change in Nbr. Employees

i hoe oe
ba, a, eens Py,
94 gy
+ 5:0, oy My ee bsg, fm, eH
ao} 55, tog "50, ta
vo Fon ing Fey ing
vy 2p, Hoy Pn
ray Py ee, a
Gy ay ‘Imp We,
io) bay, ring po-*e-H4 8p, ae,
| etn, oy tle L Wing Oy
Bang ey ats aceite Bing ey
, o
wn b ay, Pigg, bo-*--4 Fin ian,
re 1 mg H--e--4 tn he
Pam, Sy aT ee [5 4
3 Pu, ns vm bean, id
Ce, en. Pte,
“2 OH "2m,
a Pen ep,
M rn,
is Pe ag be ag
& ie in, Pa, Ls, an, ; ey
ls im,
‘pee, tog ea,
o a L “i oy
Ong, W, ey, hay, co
& Letty, nes been
oO <1 4 %. Ye, i
toe 8m iy, MH
— 7
vo
I —— 4m dd

a cn — wf a
eoa-fe---4 0 ba ® rte 4 beg ery.

Gg org eIey

tte 4 bsg tO,

° gg ley

tLe 4 18, en, PH

, 265 toy

oe-4 | coy "ing,

an eto,

H-e-A [2 m, ion

does Fein. “orca

Chinn my
if-e 5 [Hing

H-*-—4 bin, >,

"ey oy

Panel A. Business Shutdowns

zo" 0 a 0 z0 0 ay
qUaIOIYeOD oy (Addd Peyoipeid) JU!O1ye0D, ey

Fig. 8. PPPE and Homebase Post-PPP Outcomes (Local Projections). Fig. 8 plots coefficients and standard errors of regressions investigating the impact of
exposure to PPPE (top row) and predicted PPPE (bottom row) on employment and firm outcomes, defined as the difference between these outcomes in
each week relative to their average in the two weeks prior to program launch (weeks 10 and 11). Panel A plots the coefficients 8 and standard errors of
week-by-week regressions of AShutdownjjn = Osn + BPPPE; + UXijn + €ijn, Where AShutdown,j, is the difference between the shutdown indicator of firm i
in each week and the average shutdown indicator for that firm during the two weeks prior to program launch, PPPE; is the average exposure of the ZIP j to
bank PPPE, as, are state-by-industry fixed effects and Xjj, are additional control variables. Panel B plots estimates from similar week-by-week regressions
that use the change in the decline in hours worked relative to January as the dependent variable. Panel C plots estimates from similar week-by-week
regressions that use the change in the decline in number of firm employees relative to January as the dependent variable. Data are from Call Reports, SBA,
Homebase, and County Business Patterns.

746
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725-761

Table 5

PPP Exposure and Homebase Employment Outcomes. Table 5 reports the results of OLS regressions examining the relation between exposure to PPPE
during the first round and the difference between a firm’s average employment outcomes in the two weeks prior to the launch of PPP and the firm’s
outcomes in each of the following weeks. A Bus. Shutdown, is the difference between the firm’s shutdown status in a week and its average shutdown
status in weeks 10 and 11, where shutdown status takes a value of one if the business reported zero hours worked over the entire week. A Hours Worked,
is the difference in the ratio of hours worked in each establishment in a week and the average ratio of hours worked in that establishment in weeks
10 and 11. The ratio of hours worked in each establishment is measured as the hours worked in that week relative to the hours worked in that same
establishment during the last two weeks of January. A Nbr. Employees, is the difference in the ratio of the number of employees in each establishment in
a week and the average ratio of number of employees in that establishment in weeks 10 and 11. The ratio of number of employees in each establishment
is measured as the number of distinct employees that worked in the establishment in that week relative to the number of distinct employees working in
that same establishment during the last two weeks of January. Zip PPPE (Round 1) is the weighted average of bank PPPE during the first round at the ZIP
level. The weights are defined by the share of the number of branches of each bank in the zip code or within 10 miles of the center of the respective ZIP.
Predicted PPPE is the weighted average of predicted bank PPPE during the first round at the ZIP level. The predicted values of bank PPPE are obtained from
estimating the empirical specification of column (8) of Table 2. The weights are defined by the share of the number of branches of each bank in the zip
code or within 10 miles of the center of the respective ZIP. I(Month=‘M’), where M = {April, May, June, July, August} are indicator variables for the weeks
that span those respective months. Other control variables include interactions between the median household income, social distance index, COVID cases
per capita and deaths per capita measured as of week 9 interacted with the indicator variables for April, May, June, July, and August and controls for the
average tier 1 capital and core deposit ratios of all banks within the zip code or within a 10 miles radius of the zip code also interacted with the indicator
variables for April, May, June, July, and August. Standard errors are clustered at the state level. ***, **, and *, represent statistical significance at 1%, 5%, and
10% levels, respectively.

(1) (2) (3) (4) (5) (6)
A Bus. Shutdown A Hours Worked A Nbr. Employees
Zip PPPE (Round #1) x I(Month=April) 0.002 0.002 0.002 0.003 0.001 0.003
(0.004) (0.003) (0.003) (0.002) (0.003) (0.002)
Zip PPPE (Round #1) x I(Month=May) -0.000 -0.003 0.022*** 0.020"** 0.019*** 0.020"**
(0.004) (0.004) (0.004) (0.004) (0.004) (0.005)
Zip PPPE (Round #1) x I(Month=June) 0.005 -0.003 0.034*** 0.033*** 0.030*** 0.032***
(0.005) (0.005) (0.006) (0.006) (0.006) (0.007)
Zip PPPE (Round #1) x I(Month=July) 0.011** -0.001 0.029"** 0.032*** 0.026*** 0.033***
(0.005) (0.006) (0.008) (0.008) (0.008) (0.009)
Zip PPPE (Round #1) x I(Month=August) 0.011* -0.001 0.029"** 0.031*** 0.024** 0.031***
(0.005) (0.006) (0.008) (0.008) (0.009) (0.009)
Observations 819834 819834 819834 819834 819834 819834
Adjusted R? 0.058 0.602 0.134 0.629 0.110 0.571
State x Industry x Week Fixed Effects Yes Yes Yes Yes Yes Yes
Other Control Variables No Yes No Yes No Yes
Firm Fixed Effects No Yes No Yes No Yes
A Bus. Shutdown A Hours Worked A Nbr. Employees
Predicted PPPE x I(Month=April) -0.000 0.000 -0.001 -0.001 -0.000 0.000
(0.003) (0.003) (0.002) (0.002) (0.002) (0.002)
Predicted PPPE x I(Month=May) -0.005 -0.006** 0.012*** 0.009*** 0.010*** 0.008**
(0.003) (0.003) (0.004) (0.003) (0.004) (0.003)
Predicted PPPE x I(Month=June) -0.003 -0.007* 0.022*** 0.019*** 0.019*** 0.017***
(0.004) (0.004) (0.005) (0.005) (0.006) (0.006)
Predicted PPPE x I(Month=July) 0.000 -0.005 0.019"** 0.017*** 0.013* 0.014**
(0.003) (0.004) (0.005) (0.004) (0.007) (0.007)
Predicted PPPE x I(Month=August) 0.001 -0.005 0.017*** 0.016"** 0.011 0.012*
(0.004) (0.004) (0.005) (0.004) (0.007) (0.007)
Observations 819834 819834 819834 819834 819834 819834
Adjusted R? 0.058 0.602 0.133 0.629 0.110 0.571
State x Industry x Week Fixed Effects Yes Yes Yes Yes Yes Yes
Other Control Variables No Yes No Yes No Yes
Firm Fixed Effects No Yes No Yes No Yes
term effects in June, July, and August after state reopenings The table confirms the finding of no statistically or eco-
continued. nomically significant relationship between PPP bank expo-
In the first two columns of Table 5, the outcome of in- sure and these employment outcomes in April, the initial
terest is business shutdowns, in the following two columns month of the PPP. Moreover, our least squares estimates
it is the decline in hours worked, and in the final pair are not simply statistically insignificant with large confi-
of columns it is the number of employees. For each pair dence intervals; rather, they are precise zeros. In May and
of columns, the first column includes state-by-industry- June, we continue to find precise zero effects for business
by-week fixed effects, while the second column adds firm shutdowns, and either no or marginally significant positive
fixed effects and additional control variables. The top panel effects in later months when using PPPE. Using predicted
shows estimates of Eq. (1) using PPPE as the treatment, PPPE, there is a very small relationship with shutdowns in
while the bottom panel uses predicted PPPE as the treat- May and June which fades out by July. For intensive mar-
ment. gin employment, the decline in hours worked measure in-

747
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

creases for ﬁrms with higher PPP exposure in May and Our results are largely consistent with some contem-
June, and this effect remains signiﬁcant through August. poraneous evidence from other researchers using different
The effect sizes are small—approximately two percentage data sets and research designs. Autor et al. (2020) (hence-
points in May and three percentage points thereafter for forth ACCGLMPRVY) use payroll data from ADP, a large
a standard-deviation increase in PPPE—but highly statisti- payroll processor, and also use the 500 employee thresh-
cally signiﬁcant. Effects on the number of employees are old design to estimate employment effects. They ﬁnd that
quite similar to those for the number of hours worked. The the PPP boosted employment at eligible ﬁrms by 2–4.5%.
coeﬃcient patterns are also quite similar between the top Chetty et al. (2020) use high frequency employment data
and the bottom panel suggesting that both PPPE and pre- from several payroll processors for small businesses and
dicted PPPE capture similar variation. In other words, PPPE study the evolution of employment outcomes for ﬁrms
does not appear to be driven by demand to a great extent above and below the 500 employee PPP eligibility thresh-
relative to predicted PPPE. old. They ﬁnd statistically insigniﬁcant effects on employ-
As another way of interpreting our magnitudes, con- ment with conﬁdence intervals that permit modest effect
sider the following comparison. The difference between sizes. Hubbard and Strain (2020) use Dun & Bradstreet data
PPPE for top versus bottom quartile ZIP codes is 0.44. to implement the threshold design. They present some
This difference implies an increase in the share of estab- speciﬁcations that yield larger estimates, but the overall
lishments receiving PPP funding of 8.4 percentage points, takeaway from their analysis appears in line with these
which is large relative to the mean level of 22%.31 Us- other threshold designs.
ing the reduced form estimates for April in Table 5, col- Relative to this approach, our research design has a
umn (2), this change in funding implies an increase in the few beneﬁts. First, it is not local to ﬁrms around the
probability of ﬁrm shutdown of 0.6 percentage points (= 500 employee threshold; most PPP borrowers are consider-
0.44 × 0.002 × (1/0.16 )), where 0.16 is one standard devi- ably smaller. Second, the threshold design requires smaller
ation of PPPE. The lower bound of the 95% conﬁdence in- ﬁrms and larger ﬁrms to trend similarly around the reform,
terval is well below a one percentage point effect. Anal- which is a strong assumption if smaller ﬁrms are more
ogous calculations for the other outcomes give similarly vulnerable to shocks and because the PPP coincided with
small effect sizes. The effect sizes are marginally smaller other programs operated by the Federal Reserve to help
when using predicted PPPE as an instrument rather than larger ﬁrms. Third, we use our design in the next section to
PPPE, though the conﬁdence intervals overlap. Thus, rela- study impacts on aggregate local labor market and eco-
tive to the aggregate patterns in Fig. 7—a 40 percentage nomic outcomes, which is not feasible with the threshold
point increase in the probability of ﬁrm shutdown and 60 design. Nevertheless, it is informative that similar results
percentage point reductions in the ratio of hours worked emerge from different data sets and research designs.33
and the number of employees relative to January—we can Several other studies use differences in the timing of
reject modest effect sizes during this period. PPP receipt to examine the program’s employment ef-
As we move into May and June, the results for busi- fects, while also exploiting differences in timing due to
ness shutdowns do not change. However, the effect sizes pre-existing variation in bank lending relationships. Li and
for the decline in hours worked increase. In May, the point Strahan (2020) ﬁnd modest employment effects of the
estimate of 0.020 implies an increase in hours worked of program, as we do, while Faulkender et al. (2020) and
5.5 percentage points (= 0.44 × 0.020 × (1/0.16 )) with a Doniger and Kay (2021) ﬁnd substantially larger employ-
95% conﬁdence upper bound of 7.7 percentage points (= ment effects. While the conceptual approach in these pa-
0.44 × (0.020 + 1.96 × 0.004 ) × (1/0.16 )). The analogous pers is similar to ours, a key source of difference is the
estimates for June are 9.4 and 12.5 percentage points, re- extent to which the research design accounts for nonran-
spectively, which stabilize through August. Estimates for dom program targeting, which we show is quantitatively
the number of employees are nearly identical to those for important. Bartik et al. (2020b) also ﬁnd signiﬁcantly lower
the hours worked outcome. self-reported survival probabilities for ﬁrms whose primary
Because the second round of funds did not reach ﬁrms banks were in the top four, though the outcome and sam-
until late in May, our research design can be interpreted ple of very small ﬁrms in this study make it diﬃcult to
as comparing ﬁrms that did receive funds to those that did compare their results to ours.
not for April and May. In June, the research design is bet-
ter interpreted as reﬂecting differences between early and
late recipients. Thus, our estimates may be conservative re-
garding the overall employment effects of the program by ment being closed for all weeks from the beginning of the PPP through
this point in time. On the other hand, if many ﬁrms that the end of August. The results suggest a non-trivial impact of PPP on ﬁrms
did not receive funds early decided to close permanently, over the medium run, consistent with the idea that some ﬁrms that did
not receive funds early enough decided to close permanently.
then our estimates for June can be more easily compared 33
Another reason we may ﬁnd smaller effects than ACCGLMPRVY is that
to those in April and May.32 our data measure hours worked while their data measure payroll. If ﬁrms
partly deploy PPP to compensate furloughed workers who remain func-
tionally unemployed, then this difference in measurement could account
31
This calculation comes from 0.44 × 0.19, which is the coeﬃcient of for some of the gap between our estimates. Appendix F presents results
PPP per establishment as of the end of round one on PPPE in a ZIP-level using the Census Household Pulse Survey data that lean against this inter-
regression with state ﬁxed effects. pretation. A relatively small share of households report receiving any pay-
32
Appendix F uses Homebase data to study the relationship between ment for time not working in the previous week. Importantly, the share of
PPPE and a measure of “permanent” shutdowns, deﬁned as the establish- households reporting receiving no pay is not associated with state PPPE.

748
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725-761

Table 6

PPP Exposure and Local Labor Market and Economic Effects. Table 6 reports the results of OLS regressions examining the relation between exposure to PPPE
during the first round and county-level unemployment filings, small business revenue from Womply, and employment growth from Opportunity Insights. A
UI Claims is the difference between the county unemployment filings during a week and the average unemployment filings in the county in weeks 10 and
11. A Small Business Revenue is the difference between the county aggregate change in small business revenue relative to January and the average change
in small business revenue in weeks 10 and 11 relative to January. Aggregate change in small business revenue is from Womply. A OI Emp. is the difference
between county employment growth relative to January in a week and the average county employment growth relative to January in weeks 10 and 11.
The county-level employment data come from Opportunity Insights. County PPPE is the weighted county average of the bank PPPE at the end of the first
round, weighted by the share of the number of branches of each bank in each county. County Predicted PPPE is the weighted county average of predicted
bank PPPE at the end of the first round. The predicted values of PPPE are obtained from estimating the empirical specification of column (8) of Table 2.
The weights are defined by the share of the number of branches of each bank in the county. I(Month=‘M’), where M = {April, May, June, July, August} are
indicator variables for the weeks that span those respective months. Other control variables include interactions between the median household income,
social distance index, COVID cases per capita and deaths per capita measured as of week 9 interacted with the indicator variables for April, May, June, July,
and August and controls for the average tier 1 capital and core deposit ratios of all banks within the county also interacted with the indicator variables
for April, May, June, July, and August. Appendix Table B.1 shows summary statistics. Standard errors are clustered at the state level. ***, **, and *, represent
statistical significance at 1%, 5%, and 10% levels, respectively.

(1) (2) (3) (4) (5) (6)

A UI claims A Small Bus. Rev. A OI Emp.
County PPPE x I(Month=April) -0.111 -0.114** 0.013*** 0.001 -0.001 -0.000
(0.071) (0.056) (0.004) (0.004) (0.002) (0.003)
County PPPE x I(Month=May) -0.151* -0.158** 0.028*** 0.007 0.009*** 0.007***
(0.086) (0.073) (0.005) (0.007) (0.003) (0.003)
County PPPE x I(Month=June) -0.104 -0.119 0.003 -0.011 0.016** 0.011***
(0.082) (0.074) (0.006) (0.008) (0.006) (0.003)
County PPPE x I(Month=July) -0.073 -0.116 -0.012** -0.022** 0.020** 0.014***
(0.099) (0.075) (0.005) (0.009) (0.008) (0.003)
County PPPE x I(Month=August) -0.066 -0.084 -0.014*** -0.021*** 0.020** 0.013***
(0.106) (0.073) (0.005) (0.007) (0.009) (0.004)
Observations 46092 45533 43930 43863 17112 17112
Adjusted R? 0.745 0.950 0.491 0.735 0.697 0.879
State x Week Fixed Effects Yes Yes Yes Yes Yes Yes
Other Control Variables No Yes No Yes No Yes
County Fixed Effects No Yes No Yes No Yes
A UI claims A Small Bus. Rev. A OI Emp.
County Predicted PPPE x I(Month=April) -0.084 -0.059 0.011*** 0.002 -0.001 -0.000
(0.084) (0.057) (0.003) (0.003) (0.003) (0.003)
County Predicted PPPE x I(Month=May) -0.124 -0.098 0.025*** 0.008 0.007 0.002
(0.100) (0.073) (0.008) (0.007) (0.006) (0.004)
County Predicted PPPE x I(Month=June) -0.103 -0.090 0.013 0.004 0.015 0.006
(0.094) (0.075) (0.009) (0.009) (0.010) (0.004)
County Predicted PPPE x I(Month=July) -0.064 -0.097 -0.002 -0.004 0.018 0.008
(0.125) (0.080) (0.006) (0.006) (0.014) (0.005)
County Predicted PPPE x I(Month=August) -0.016 -0.037 -0.001 -0.002 0.019 0.008
(0.142) (0.080) (0.006) (0.005) (0.015) (0.006)
Observations 46092 45533 43886 43863 17112 17112
Adjusted R? 0.744 0.950 0.489 0.734 0.688 0.878
State x Week Fixed Effects Yes Yes Yes Yes Yes Yes
Other Control Variables No Yes No Yes No Yes
County Fixed Effects No Yes No Yes No Yes

tial lockdown orders, UI claims surge and small business
revenues and OJ employment rates decline in both groups.

5.3. Local labor market and economic activity

Figs. 9 and 10 and Table 6 present results using broader
measures of employment outcomes: initial unemployment
insurance (UI) claims, small business revenue, and employ-
ment data from Opportunity Insights (OI). We focus on
county-level outcomes because that is the finest level of
aggregation for which these data are available.

Fig. 9 splits the counties in the sample in two groups
based on their PPPE and predicted PPPE measures and
plots the evolution over time of average employment out-
comes. The plots suggest that, prior to lockdown orders,
average UI claims are relatively low, and UI claims, small
business revenues, and OI employment rates all trend sim-
ilarly across both groups during the period. After the ini-

749

The high-PPPE group sees somewhat lower UI claims in
May, and small business revenues and OI employment
rates recover faster for this group relative to the low-PPPE
group from mid-April until the end of May. These differ-
ences subsequently fade. The graphs also point to the im-
portance of targeting differences across groups, as high-
PPPE areas appear to be differentially hit prior to the PPP’s
rollout.

Fig. 10 provides further graphical evidence of the im-
pact of PPP on these outcomes. The figure repeats the lo-
cal projection analysis, replacing the main outcomes with
the difference in UI claims, decline in small business rev-
enue, and change in Ol employment rates. We observe lit-
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Fig. 9. PPPE and Alternative Outcome Variables. Fig. 9 shows the evolution of the ratio of weekly initial unemployment ﬁling claims at the county level
and total county employment (Panel A), the change in aggregate small business revenue at the county level relative to January (Panel B), and the ratio of
county employment relative to January (Panel C). We exclude California counties from the time series of Panel A due to a large outlier in UI claims that
is likely due to a backlog in UI claims processing in that state. In the appendix, we include the plot that includes Californian counties. Data are from Call
Reports, SBA, County Business Patterns, State Labor Departments, Opportunity Insights website, and Womply.

750
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725-761

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Fig. 10. PPPE and Alternative Outcome Variables (Local Projections). Fig. 10 plots coefficients and standard errors of regressions investigating the impact
of exposure to PPPE (top row) and predicted PPPE (bottom row) on employment and firm outcomes, defined as the difference between these outcomes in
each week relative to their average in the two weeks prior to program launch (weeks 10 and 11). Panel A plots the coefficients 6 and standard errors of
week-by-week regressions of AUI. = sn + BPPPE, + TX + €c, where AUI, is the difference between the UI claims of county c in each week of the sample
and the average UI claims for that county during the two weeks prior to program launch, PPPE, is the average exposure of the county to bank PPPE, as;
are state fixed effects and X, are additional control variables. Panel B plots estimates from similar week-by-week regressions that use the change in weekly
small business revenue relative to January as the dependent variable. Panel C plots estimates from similar week-by-week regressions that use the change
in weekly employment outcomes relative to January as the dependent variable. Data are from Call Reports, SBA, Womply, and Opportunity Insights.

751
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

tle discernible impact on UI claims. The small business rev- We emphasize two takeaways. First, the ﬁrst stage co-
enues analysis suggests a positive impact of PPP initially, eﬃcient for PPPE is marginally stronger than for predicted
which levels off in the subsequent months. The OI data PPPE (see also Fig. 4, discussed in Section 4.4). Accounting
suggest a pattern similar to our Homebase analysis, albeit for this difference brings estimated impacts of PPP loans
with slightly smaller magnitudes. on employment to statistical equivalence within each sam-
Table 6 repeats the analysis of Table 5 for these out- ple. If anything, the IV coeﬃcients for predicted PPPE are
comes. We ﬁnd a small statistically signiﬁcant effect on slightly larger than for PPPE; we interpret this fact as sug-
UI claims in April and May when using PPPE, which dis- gesting that omitted upward-biasing demand factors are
sipates by June. Effects are insigniﬁcant when using pre- unlikely to confound our PPPE-based estimates.
dicted PPPE. Following the calculations above, the 95% The second takeaway is that reweighting the Homebase
lower bound estimated effect for the month of May is - sample can reconcile the seemingly disparate estimates be-
13.2 basis points (= 0.44 × (−0.158 − 1.96 × 0.073 )). The tween OI and Homebase. Whereas the coeﬃcient for the
middle columns show the relationship between small busi- unweighted Homebase sample is statistically and econom-
ness revenue and PPPE or predicted PPPE. We ﬁnd a posi- ically greater than the OI coeﬃcient at the 95% level, the
tive relationship between PPP exposure and small business reweighted Homebase coeﬃcient falls by approximately
revenue, which is statistically signiﬁcant in a few speciﬁ- one-third.35 In this speciﬁcation, bootstrapped conﬁdence
cations in April and May, but levels off and even becomes intervals for the difference between the OI and Home-
negative in subsequent months. One possible explanation base estimates are statistically insigniﬁcant in Panel A and
is that access to liquidity through the PPP allowed ﬁrms to barely reject zero in Panel B. As discussed in Section 6,
avoid engaging in high-risk practices to generate revenue. given that Homebase includes smaller ﬁrms that are more
For example, restaurants may have been able to close and likely to show larger responses, allowing for heterogeneous
focus on food delivery as opposed to resuming in-person impacts by ﬁrm size would further narrow the modest re-
dining when allowed. Early PPP recipients may also have maining gap between these estimates.
felt less urgency to make investments to reopen immedi- Overall, no speciﬁcation or outcome variable suggests
ately, instead electing to defer operations until more un- large changes in employment across ZIPs or counties based
certainty resolved. The last two columns present regres- on either PPPE measure, despite the large differences in
sions of employment growth in OI on county-level PPPE program access predicted by these measures. Once we ac-
and predicted PPPE. The estimates suggest small effects in count for differences in ﬁrst stage strength across instru-
April that rise modestly in May and June. ments and industry representation across data samples, all
The results using predicted PPPE, shown in the bottom speciﬁcations paint a consistent picture of modest, positive
panel, point to statistically insigniﬁcant effects of the PPP employment impacts.
on UI or employment, and small effects on small business
revenues in early months that dissipate by June. However, 5.4. Matched sample analysis
the point estimates are similar and the conﬁdence intervals
are large enough that we cannot rule out the reduced form We complement our regional estimates with a sample
effects from the PPPE instrument. of 10,694 ﬁrms, for which we are able to match PPP loan
Table 7 presents a formal analysis that reconciles es- information to payroll information from Homebase. In this
timated employment effects across the Homebase and OI analysis, we have a smaller sample of ﬁrms, but we can
samples and when comparing the PPPE to predicted PPPE also directly measure if and when each individual ﬁrm ob-
estimates. We estimate IV regressions for each sample and tained a PPP loan. We use the individual matched data and
instrument, focusing in Panel A on the local projection es- variation in the timing of when ﬁrms received PPP loans
timate in week 23 (June 21–27), the week with the largest to examine the impact of PPP receipt on ﬁrms’ employ-
coeﬃcient in the Homebase sample. Panel B presents esti- ment outcomes. We ask whether differences in timing ma-
mates for all weeks pooled together. The Homebase data terially affected short-term employment outcomes of ﬁrms
is not representive of the broader PPP-eligible economy, that received loans earlier versus later. Because the tim-
especially in terms of industry composition. We therefore ing of loan receipt may reﬂect differences in loan demand
also present a reweighted Homebase analysis.34 Following across ﬁrms, we also instrument for the timing of receipt
DiNardo et al. (1996), we reweight observations to match using PPPE and predicted PPPE. This alternative strategy
the less-than-500-worker-establishment-count distribution provides a useful way to assess the robustness of our main
across industries in the Census SUSB data. Concretely, this results.
reweighting downweights bars and restaurants relative to Fig. 11 shows the evolution of business shutdowns
other industries. (Panel A), change in hours worked (Panel B), and the
change in employee counts over time (Panel C) for early
and late recipients of PPP funds. Early recipients are de-
ﬁned as those ﬁrms that receive a loan in the week ending
34
The Homebase industry categories are coarsely deﬁned and do not on April 11th or earlier and late recipients are ﬁrms that
have a one-to-one mapping with NAICS industry categories. Thus, each
Homebase category can potentially span multiple two-digit NAICS in-
35
dustries. We use the self-reported industry category of each PPP appli- Appendix F shows that the estimated effects of the program in the
cant recorded in their PPP applications to create a mapping between the Homebase sample are generally stronger for the Food & Drink and Retail
Homebase industry for our matched sample and two-digit NAICS indus- industries, which are disproportionately represented in Homebase relative
tries and apply this mapping to the full Homebase sample. to the Census or OI.

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Table 7
Reconciling Estimates across Samples and Exposure Measures. Table 7 presents employment estimates across the Homebase and OI samples and compares
estimates using the PPPE and predicted PPPE instruments. We estimate IV regressions for each sample and instrument, focusing on the local projection
estimates in week 23 (June 21–27), the week with the largest coeﬃcient in the Homebase sample, and pooled across all weeks. The endogenous variable
is the fraction of establishments in an area that received PPP as of the end of the ﬁrst round. We also present an industry-reweighted Homebase analysis.
The Homebase industry categories are coarsely deﬁned and do not have a one-to-one mapping with NAICS industry categories. Thus, each Homebase
category can potentially span multiple two-industry NAICS industries. We use the self-reported industry category of each PPP applicant recorded in their
PPP applications to create a mapping between the Homebase industry and the two-digit NAICS industries. Following DiNardo et al. (1996), we then reweight
observations to match the less-than-500-worker-establishment-count distribution across industries in the Census SUSB data. Concretely, this reweighting
downweights bars and restaurants relative to other industries. All speciﬁcations include state (OI) or state-by-industry (Homebase) ﬁxed effects and pre-
policy controls. Statistical tests within a sample are computed via simultaneous GMM with standard errors clustered at the state level. Conﬁdence intervals
report the difference in coeﬃcients across samples, computed using bootstrapped coeﬃcient distributions. ∗ ∗ ∗ , ∗ ∗ , and ∗ , represent statistical signiﬁcance at
1%, 5%, and 10% levels, respectively.

Panel A. Peak Employment Effect (June 21–27)

(1) (2) (3) (4) (5) (6)
Homebase, No Wt Opportunity Insights Homebase, Indy Wt

2SLS Coeﬃcient 0.834∗ ∗ ∗ 1.354∗ ∗ ∗ 0.324∗ ∗ ∗ 0.594∗ ∗ 0.550∗ ∗ 1.565∗ ∗ ∗
(0.180) (0.511) (0.081) (0.254) (0.240) (0.568)
First Stage Coeﬃcient 0.261∗ ∗ ∗ 0.229∗ ∗ ∗ 0.310∗ ∗ ∗ 0.259∗ ∗ ∗ 0.269∗ ∗ ∗ 0.228∗ ∗ ∗
(0.021) (0.047) (0.028) (0.095) (0.022) (0.047)

Instrument PPPE Predicted PPPE PPPE Predicted PPPE PPPE Predicted PPPE
Geography ZIP ZIP County County ZIP ZIP
N 35645 35645 742 742 35645 35645
F-Statistic 146.8 23.3 120.6 7.5 144.8 24.1

P-value vs PPPE - 0.297 - 0.595 - 0.080
95% CI HBNoWt - OI - - [0.280, 0.849] [-3.553, 3.720] - -
95% CI HBWt - OI - - - - [-0.087, 0.640] [-3.052, 3.880]

Panel B. Average Employment Effect (April–August)

(1) (2) (3) (4) (5) (6)
Homebase, No Wt Opportunity Insights Homebase, Indy Wt

2SLS Coeﬃcient 0.524∗ ∗ ∗ 0.653∗ ∗ ∗ 0.229∗ ∗ ∗ 0.353∗ ∗ 0.308∗ 0.655∗ ∗
(0.134) (0.244) (0.053) (0.145) (0.162) (0.286)
First Stage Coeﬃcient 0.261∗ ∗ ∗ 0.229∗ ∗ ∗ 0.301∗ ∗ ∗ 0.237∗ ∗ 0.268∗ ∗ ∗ 0.228∗ ∗ ∗
(0.022) (0.047) (0.027) (0.093) (0.022) (0.047)

Instrument PPPE Predicted PPPE PPPE Predicted PPPE PPPE Predicted PPPE
Geography ZIP ZIP County County ZIP ZIP
N 820616 820616 17135 17135 820616 820616
F-Statistic 146.8 23.4 124.9 6.4 144.3 24.0

P-value vs PPPE - 0.615 - 0.616 - 0.223
95% CI HBNoWt - OI - - [0.251, 0.417] [-0.242, 0.522] - -
95% CI HBWt - OI - - - - [0.024, 0.204] [-0.282, 0.534]

Fig. 11. PPPE and Post-PPP Outcomes (Matched Sample Analysis). Fig. 11 investigates business shutdowns, changes in the ratio of hours worked, and
changes in the number of employees for ﬁrms in the Homebase sample that are name-matched to the PPP data set from SBA. We compare ﬁrms that
received PPP approval in week 12 or earlier to those that received PPP approval in week 16 or later. Data is from Call Reports, SBA, and Homebase.

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J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725-761

Table 8

Homebase Employment and PPP Loan Timing (Matched Sample). Table 8 presents the results from the individual matched sample. The left-hand-side
variable in Panel A, A Shutdown, is the difference between each matched firm’s shutdown status in week 16 (May 3rd to May 9th) and its average
shutdown status in weeks 10 and 11. Shutdown is an indicator variable that takes the value of one if the business reported zero hours worked over the
entire week. A Hours Worked is the change between the average number of hours worked at each establishment in the last two weeks prior to the launch
of PPP and the number of worked at each establishment in week 16 (May 3rd to May 9th). A Nbr. Employees is the change between the average number of
employees working for each establishment in the last two weeks prior to the launch of PPP and the number of employees working for each establishment
in week 16 (May 3rd to May 9th). Week of PPP Loan is a variable representing the week in which the firm received PPP loan approval. Standard errors are
clustered at the state level. ***, **, and *, represent statistical significance at 1%, 5%, and 10% levels, respectively.

Panel A. Business Shutdowns

(1) (2) (3) (4) (5) (6)
A Shutdown
OLS IV IV
Week of PPP loan 0.007*** 0.007*** 0.012 0.014 0.026** 0.061*
(0.002) (0.002) (0.009) (0.019) (0.012) (0.032)
Observations 10694 10024 10556 9891 10556 9891
F-Stat 186.060 51.073 28.033 4.982
Industry Fixed Effects Yes No Yes No Yes No
State xInd Fixed Effects No Yes No Yes No Yes
Instrument - - PPPE Zip Predicted PPPE

Panel B. Ratio Hours Worked

(1) (2) (3) (4) (5) (6)
A Hours Worked

OLS IV IV

Week of PPP loan -0.012*** -0.011*** -0.057*** -0.059*** -0.046*** -0.076

(0.001) (0.001) (0.006) (0.018) (0.013) (0.046)
Observations 10694 10024 10556 9891 10556 9891
F-Stat 186.060 51.073 28.033 4.982
Industry Fixed Effects Yes No Yes No Yes No
StatexInd Fixed Effects No Yes No Yes No Yes
Instrument - - PPPE Zip Predicted PPPE

Panel C. Ratio Nbr. Employees

(1) (2) (3) (4) (5) (6)
A Nbr. Employees

OLS IV IV
Week of PPP loan -0.011*** -0.010*** -0.047*** -0.047*** -0.040*** -0.053
(0.001) (0.001) (0.006) (0.017) (0.011) (0.039)
Observations 10694 10024 10556 9891 10556 9891
F-Stat 186.060 51.073 28.033 4.982
Industry Fixed Effects Yes No Yes No Yes No
StatexInd Fixed Effects No Yes No Yes No Yes
Instrument - - PPPE Zip Predicted PPPE
receive a loan in the week beginning May 3rd or later. For 9th, the final week before the second round of PPP loans
all three outcomes, we see a gap open up prior to PPP loan was disbursed. Therefore, the regression is measuring em-
disbursement, which may reflect a combination of our tar- ployment effects using first round recipients as a “treat-
geting results and differences in loan demand, consistent ment” group and second round recipients—who have not
with prior results suggesting that early recipients were big- yet received their loans—as a “control” group.
ger and less constrained firms (Balyuk et al., 2020; Doniger We estimate the following specification:

and Kay, 2021). Following PPP disbursement, the gap grows
over time. The raw data is suggestive of earlier PPP receipt
leading to higher employment and business survival rates.

AYisj = sn + ¢WeekPPP, + 5s

where Ayj;; is the difference between the outcomes Yj;
To address the concern that difference in timing may (shutdown, hours worked, number of employees) of firm i

be driven by demand, we instrument using PPPE and pre- in the week beginning on May 3rd, and the average out-

dicted PPPE. Table 8 presents results from the individual come for the same firm during the two weeks prior to the

matched sample exploring the timing of PPP receipt, re- launch of PPP. Using the two weeks prior to the launch of

gressing outcomes on the week in which a firm received PPP as a benchmark is particularly important in this anal-

PPP. We focus on outcomes in the week of May 3rd to May ysis given the substantial gap that opens between the av-
erage employment outcomes for these groups prior to the

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J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

PPP launch. W eekP P Pi is the week in which a ﬁrm received the policy shown by the bottom group is set to zero and
a PPP loan, and thus ζ captures the effect of receiving a removed from the effect computed for other groups.37
PPP loan one week later. The term αsn represents industry- PPPE for the bottom group is −0.30 and increases to
or state-by-industry ﬁxed effects. The ﬁrst two columns 0.41 for the highest group. Thus, for exposure group g, the
show OLS estimates, with columns (1) and (2) including aggregate increase in employment induced by the program
industry and state-by-industry ﬁxed effects, respectively. is:
Columns (3) and (4) show IV estimates, instrumenting the
week in which a ﬁrm received PPP with PPPE measured at
Yg = βt × (eg − (−0.30 )) × Yg,pre , (2)
the ZIP level. The ﬁnal two columns show IV estimates, in- where βt is our reduced form estimate on PPPE, eg is the
strumenting the week in which a ﬁrm received PPP with weighted-average program exposure where the weights
predicted PPPE, again measured at the ZIP level. are estimated eligible employment in each geography, and
The results in Table 8 are largely consistent with our Yg,pre is within-sample pre-program employment. A less
bank exposure results, suggesting modest short-term ef- conservative approach aggregates estimates relative to a
fects of the PPP. In the top panel the outcome is busi- no-exposure baseline, which equals −0.5. We also report
ness shutdowns, in the middle panel it is hours worked, estimates based on the predicted PPPE exposure measure
and in the bottom panel it is the number of employ- and from either the Homebase or OI samples, which rep-
ees. In all regressions, the magnitudes of the OLS coef- resent different levels of local labor market aggregation.
ﬁcients are smaller than magnitudes of the IV estimates. We estimate reduced form regressions for each week
One interpretation of this fact is that larger ﬁrms that from the beginning of the program through the end of Au-
were less credit-constrained had earlier access to the pro- gust. For local labor market data, we focus on the OI em-
gram, which would underscore the importance of instru- ployment measure. For Homebase data, we focus on the
menting for the timing of PPP receipt. In the case of col- number of employees measure and the reweighted sample
umn (6) in all panels, the inclusion of state-by-industry from Section 5.3 that balances the industry composition
ﬁxed effects weakens the ﬁrst stage of the IV consider- of Homebase. The reduced form regressions correspond to
ably, which might explain the relatively larger magnitudes the IV speciﬁcations in Table 7, Panel A, columns (3) and
of the coeﬃcients and imprecision of those estimates. As a (5), respectively. We report week-speciﬁc estimates from
result, we do not draw strong conclusions from this spec- different phases of the program and a cumulative estimate
iﬁcation, though the results remain broadly consistent if that averages weekly estimates from the beginning of the
noisier. program through August.
Panel A suggests marginally signiﬁcant effects on busi- Table 9 presents the estimates. Using the PPPE design
ness shutdowns in the IV speciﬁcation, and that obtaining and reweighted Homebase sample, we estimate the PPP in-
a PPP loan one week earlier leads to a decrease in shut- creased employment during the lockdown period by 1.57
downs of between 1.4 and 2.6 percentage points. In Panel million in week 15, or 2.2% of pre-program employment.
B, we ﬁnd that obtaining a PPP loan one week earlier leads This effect rises during the reopening period to 3.55 mil-
to an increase in hours worked of between 4.6 and 5.9 per- lion (5.1%) in week 22 and then falls later in the program
centage points for a ﬁrm receiving a PPP loan a week ear- to 2.71 million (3.9%) in week 29. The cumulative impact
lier. Panel C points to similar effects on the number of em- over the program’s ﬁrst ﬁve months is 2.02 million (2.9%).
ployees, with obtaining a PPP loan one week earlier lead- Estimates based on predicted PPPE give nearly identical re-
ing to an increase in the number of employees of between sults.
4.0 and 4.7 percentage points for a ﬁrm receiving a PPP Note this is a lower-bound estimate if the lowest expo-
loan a week earlier.36 sure ZIP also responds to the program. When we aggregate
relative to a no-exposure baseline, we estimate an increase
6. Aggregate impacts that ranges between 3.28 and 5.43 million (4.7–7.8%). Aver-
aging the more conservative and more aggressive estimates
Our approach to aggregation follows Mian and yields an estimated range of 3.8–5.4%.
Suﬁ (2012) and Berger et al. (2020). We estimate the Estimates based on the OI sample are quite similar in
total employment gains caused by the program in its ﬁrst terms of cumulative magnitudes, ranging between 1.77 and
ﬁve months, exploiting only differences in cross-sectional 4.52 million. However, the dynamics in the OI data suggest
exposure and using the group receiving the smallest shock a smaller effect during the lockdown period that rises dur-
as a counterfactual. We choose the bottom 1% of geogra- ing the reopening period before leveling off.38 Averaging
phies (ZIP or county) as the counterfactual group and
compute the effect of the policy for other groups relative 37
As is the case for any aggregate estimates that rely on cross-sectional
to this group. By construction, any time-series effect of identiﬁcation net of time ﬁxed effects, we cannot observe a counterfac-
tual that measures general equilibrium effects. This is another reason why
producing estimates with different assumed counterfactuals can inform
36 the range of plausible aggregate impacts, in addition to demonstrating the
Appendix F shows the coeﬃcients of week-by-week regressions that
repeat the OLS and IV speciﬁcations of columns (1) and (3) of Table 8 for degree of sensitivity of results to different assumptions.
38
every week in the sample. Similar to our regional analyzes, the dynamics Table 9 also reports a speciﬁcation that accounts for ﬁrm size hetero-
indicate that gaps in the number of employees and hours work persist geneity by assuming treatment effects for larger ﬁrms that are half the
until August. Again, we caution that the OLS estimator will be biased if size of the ﬁrms in Homebase. We assume these ﬁrms account for one-
ﬁrms that obtained loans earlier are fundamentally different from ﬁrms third of eligible employment. The Homebase sample comprises mainly
that received PPP loans later. small ﬁrms with median pre-program employment of 27 and mean pre-

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J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Table 9
Aggregate Effects under Alternative Estimation Methods. Table 9 summarizes our estimates of the aggregate effect of the PPP program. The aggregate effect
is presented based on different analysis samples and aggregation assumptions. We present estimates based on the ZIP-level estimates from Homebase
employment data, reweighted to balance the industry composition of the Homebase data, and based on the county-level estimates from OI employment
data. For Homebase, we include a speciﬁcation that accounts for ﬁrm size heterogeneity by assuming treatment effects for larger ﬁrms that are half the size
of the ﬁrms in Homebase. We assume these ﬁrms account for one-third of eligible employment. We report week-speciﬁc estimates from different phases
of the program (lockdown, reopening, reopened) and a cumulative estimate that averages weekly estimates from the beginning of the program through
August. Percent impacts in parentheses are computed relative to the eligible population of 70 million.

(1) (2) (3) (4) (5)
Estimation Window Week 15, Week 22, Week 29, Cumulative through August, Millions
Millions (%) Millions (%) Millions (%) (%)

Homebase, Industry Weights
A. Relative to Bottom 1% 1.57 (2.2%) 3.55 (5.1%) 2.71 (3.9%) 2.02 (2.9%) 2.11 (3.0%)
B. Relative to Zero 2.55 (3.6%) 5.76 (8.2%) 4.40 (6.3%) 3.28 (4.7%) 5.43 (7.8%)
C. Average of A and B 2.06 (2.9%) 4.66 (6.7%) 3.56 (5.1%) 2.65 (3.8%) 3.77 (5.4%)
D. C with Firm Size 1.72 (2.5%) 3.88 (5.5%) 2.96 (4.2%) 2.21 (3.2%) 3.14 (4.5%)
Heterogeneity
Opportunity Insights
A. Relative to Bottom 1% 0.72 (1.0%) 1.80 (2.6%) 2.16 (3.1%) 1.97 (2.8%) 1.77 (2.5%)
B. Relative to Zero 0.99 (1.4%) 2.49 (3.6%) 2.98 (4.3%) 4.52 (6.5%) 4.18 (6.0%)
C. Average of A and B 0.86 (1.2%) 2.15 (3.1%) 2.57 (3.7%) 3.25 (4.6%) 2.98 (4.3%)
Combined Estimates
A. Average of HB.D and OI.C 1.29 (1.8%) 3.01 (4.3%) 2.77 (4.0%) 2.73 (3.9%) 3.06 (4.4%)

Exposure Measure PPPE PPPE PPPE PPPE Predicted PPPE

estimates from Homebase and OI yields a combined em- June 2021 are 1.98 million worker years of employment at
ployment impact of approximately 3 million workers, or 4% a cost of $258,0 0 0 per worker-year retained.
of pre-program employment, with peak employment im- We do ﬁnd an increasing treatment effect over the
pacts perhaps 1 to 2 percentage points higher. course of the program’s ﬁrst few months, whereas AC-
When considered relative to the scale of the PPP pro- CGLMPRVY ﬁnd an immediate response that appears more
gram, the employment effects we estimate are fairly mod- stable over time. While we do not want to overstate
est. The program disbursed $525 billion in total loans, these differences, they may reﬂect the fact that our es-
which implies a cost-per-job-year of $175,0 0 0 under the timates feature smaller ﬁrms who may be more respon-
assumption that all the induced jobs persist for a year.39 sive to stimulus policy (Zwick and Mahon, 2017; ACCGLM-
Incorporating the saved funds from lower unemployment PRVY22) and who may have been less able to increase em-
insurance claims (roughly $5–10K per worker) only mod- ployment while shelter-in-place orders remained in force.
estly alters this calculation. Firms applying for PPP loans These ﬁrms are more representative of the overall popu-
reported 51 million jobs in total supported by the program. lation of PPP recipients, so our results might be especially
When combined with our estimates, an implication is that informative about the program’s overall impact during this
more than 90% of these supported jobs were inframarginal. time.
If wages for inframarginal workers did not adjust, then the
bulk of the program’s economic beneﬁts appear to accrue 7. Interpretation and mechanisms
to other stakeholders, including owners, landlords, lenders,
suppliers, customers, and possibly future workers. 7.1. Potential channels
Relative to ACCGLMPRVY, our estimates are quite simi-
lar. Our aggregate estimates are remarkably consistent with The primary focus of our paper is to evaluate the PPP
a recent paper by Autor et al. (2022) (henceforth ACCGLM- and the role of banks in driving the policy response we
PRVY22) who, building on ACCGLMPRVY, ﬁnd the PPP in- identify. We ﬁnd limited evidence that PPP funding has
creased employment by about 3 million jobs per week in signiﬁcant effects on employment or local economic activ-
the second quarter of 2020. Their overall estimates through ity during the ﬁrst month of the program. In the subse-
quent months, we ﬁnd more evidence of employment ef-
fects on the intensive margin, but can still rule out large
program employment of 37 and very few ﬁrms with more than 100 em- employment effects of the program. Thus, while differ-
ployees. This approach follows logic in Autor et al. (2022), who consider
ences in bank performance lead to distortions in access to
aggregation based on evidence that ﬁrms away from the 500 worker dis-
continuity display larger treatment effects. Even after accounting for ﬁrm the program, these differences appear relatively unimpor-
size heterogeneity, the Homebase and OI estimates remain close. tant for employment, given the small overall employment
39
If half of the induced jobs persisted for 12 months, the estimate effects we estimate. If ﬁrms did not primarily maintain or
would be $246,0 0 0; if they all ended in August, the estimate would be increase employment, what did they do with PPP funds
$414,0 0 0. Finally, some of the PPP loans will be reimbursed, which re-
duces the overall cost of the program. Given the research design limits
and how might the funds ultimately affect employment?
our ability to explore longer run impacts, we leave to future work to pro- There are several non-mutually exclusive channels
vide more comprehensive cost-per-job-year estimates. through which businesses may have absorbed the funds

756
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

without immediate employment effects. First, program el- 7.2. Fixed payments and precautionary savings
igibility was deﬁned broadly, so many less affected ﬁrms
likely received funds and continued as they would have To explore the effects of PPP on non-employment ﬁ-
in the absence of the funds. In these cases, the program’s nancial outcomes, we use information from the ﬁrst phase
beneﬁts accrue to the ﬁrm’s owners.40 of the Census Small Business Pulse Survey measuring the
Second, ﬁrms retained signiﬁcant ﬂexibility in how they effect of changing business conditions during the Coron-
could use the funds over time, and they may have used avirus pandemic on US small businesses. The ﬁrst phase
funds initially to strengthen balance sheets and for non- of the survey was conducted weekly from April to June
employment related expenses. Financial frictions can am- 2020.42 In the top two panels of Table 10, we exam-
plify precautionary savings motives, which imply ambigu- ine whether receipt of PPP allowed ﬁrms to avoid be-
ous impacts on employment. While funds may have gone coming delinquent on scheduled payments (either loan or
to distressed ﬁrms, they may still choose to downsize non-loan). We estimate regressions of the relationship be-
and cut employees in the face of uncertainty. For exam- tween PPP fund allocation and the percentage of ﬁrms re-
ple, ﬁrms were uncertain about the duration of the pan- porting missing payments at the state-industry level.43 In
demic and future revenue streams, and likely wanted to light of our targeting results, these regressions add controls
hold cash to survive a longer duration crisis. Such motives for pre-PPP measures of crisis severity, including the pre-
are consistent with Almeida et al. (2004) and Riddick and PPP decline in hours worked from Homebase, the pre-PPP
Whited (2009) who ﬁnd that uncertainty increases ﬁrms’s counts of COVID cases and deaths per capita, and the pre-
precautionary motives to hold cash, particularly when ex- PPP social distancing index.
ternal ﬁnancing is diﬃcult to obtain. In the top panel of Table 10, column (1) indicates that
Third, some ﬁrms may have increased employment an increase in the share of ﬁrms reporting receiving PPP
or called back workers, though they account for a rela- is not signiﬁcantly associated with a decline in the per-
tively small share of total recipients. The primary chan- centage of ﬁrms missing loan payments. This result, how-
nel through which the PPP could affect employment is ever, could indicate that areas and industries with a lower
through ﬁnancial frictions. Firms may temporarily need liq- percentage of businesses receiving PPP had a larger frac-
uidity during the downturn to cover cash shortfalls, either tion of businesses that were uninterested or unable to ap-
due to a loss in demand or lockdown policies. These ﬁrms ply for funds. To address this issue, we use state PPPE
may be unable to access credit, for example, due to clas- and predicted PPPE to capture geographic differences in ac-
sic asymmetric information effects where lenders are un- cess to the supply of PPP funds resulting from differences
able to separate ﬁrms that will survive from those that fail across regions in their exposure to bank PPP performance.
(Stiglitz and Weiss, 1981). In this case, credit supply can be These differences are plausibly unrelated to demand fac-
ineﬃciently low. PPP guarantees would make lenders will- tors and therefore less likely to be confounded by them. In
ing to extend credit, enabling liquidity-constrained ﬁrms to columns (2) and (4), we focus on the relation between the
survive, raising employment, and potentially increasing ag- percentage of ﬁrms receiving PPPE and state PPPE or pre-
gregate welfare by shifting credit supply toward eﬃcient dicted PPPE. Both IVs generate similar results. The relation-
levels.41 ship is strong, with F-statistics of 115 and 67 when using
Finally, related to the ﬁrst channel, banks may substi- state PPPE or predicted PPPE as instruments, respectively.
tute more generous PPP loans for other lending that would In columns (3) and (5), we present results of an IV strategy
have happened otherwise (Gale, 1991). Such crowd-out of whereby we instrument for the percentage of ﬁrms receiv-
private ﬁnancing is also consistent with small employment ing PPP using state PPPE and predicted PPPE. Using this
effects. Relatedly, business stealing spillovers between eli- strategy, we ﬁnd that a ten percentage point increase in
gible and ineligible employers could account for low em- ﬁrms receiving PPP is associated with a 1.7 to 1.8 percent-
ployment effects at the labor market level. age point decline in missing loan payments.
In the middle panel of Table 10, we ﬁnd that a ten per-
centage point increase in the share of ﬁrms receiving PPP
is associated with an even larger effect on missed non-
loan payments. This result reﬂects the fact that many small
businesses do not necessarily have loans. Instead, their pri-
40
mary ﬁxed obligations are rent payments, utilities, supplier
Drawing on data from a large survey of business owners on Face-
book, Alekseev et al. (2020) ﬁnd that 30% to 40% of small businesses did
not experience sales declines in the ﬁrst month of the crisis. Among the
42
businesses that did experience declines, the severity of the decline varies We do not use the second phase of the survey, which began in Au-
widely from declines of 10 to 20% to nearly complete shutdowns. More- gust 2020 and ended in October 2020, because it falls outside the sample
over, only half of ﬁrms surveyed reported struggling to pay obligated ex- period of our analysis. Note that the sample size changes across variables,
penses (though presumably this share increased over time). Additionally as the Census does not report for some state-industry observations, likely
Griﬃn et al. (2021) ﬁnd evidence of signiﬁcant fraud, with many loans due to censoring.
going to ineligible or even non-existent ﬁrms. These loans are unlikely to 43
Unfortunately, the Pulse survey does not separate non-loan scheduled
generate large employment effects. payments into payroll versus non-payroll components. However, it does
41
Programs like the PPP can also increase employment through a sub- focus on “required” payments, which ﬁrms may interpret as referring to
sidy channel, by reducing the cost of capital for ﬁrms and possibly at- payments for past labor rather than discretionary payments based on re-
tracting excessively risky borrowers. This channel can affect employment taining workers going forward. Results for this measure should be inter-
even in the absence of ﬁnancial frictions. In these cases, the welfare ben- preted with some uncertainty about respondents’ interpretation of the
eﬁts of subsidized credit are less clear. question.

757
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

Table 10
PPP Receipt, Missed Payments, and Cash-on-Hand (Census Pulse Survey). Table 10 reports the results of OLS and IV regressions examining the relation
between the geographic allocation of PPP funds during the ﬁrst round and outcomes from the Census Small Business Pulse Survey. Survey outcomes cover
the nine weeks from April 26th through June 27th. The left-hand-side variable in the top panel is the percentage of ﬁrms reporting a missed scheduled
loan payment. The left-hand-side variable in the middle panel is the percentage of ﬁrms reporting a missed other scheduled payment such as rent, utilities,
and payroll. The left-hand-side variable in the bottom panel is the fraction of businesses with cash on hand to sustain operations for three months or more.
% PPP Received is the percentage of businesses reporting having received PPP funds in a state-by-industry group. State PPPE is the weighted state average
of bank PPPE at the end of the ﬁrst round, where the weights are given by the share of the number of branches of each bank in each state. State Predicted
PPPE is the weighted state average of predicted bank PPPE at the end of the ﬁrst round. The predicted values of bank PPPE are obtained from the empirical
speciﬁcation of column (8) of Table 2. The weights are deﬁned by the share of the number of branches of each bank in the state. Regressions include
controls for: Pre-PPP Decline Hours Worked, which equals the average decline in hours worked in each state between January and the last week of March;
Pre-PPP State Covid-19 Cases (per capita) and Pre-PPP State Covid-19 Deaths (per capita) at the state level; and Pre-PPP State Social Distancing Index, which is
the change in average distance traveled in the state until the end of March using individuals’ GPS signals. All speciﬁcations include industry×week ﬁxed
effects. Standard errors are clustered at the state level. ∗ ∗ ∗ , ∗ ∗ , and ∗ , represent statistical signiﬁcance at 1%, 5%, and 10% levels, respectively.

(1) (2) (3) (4) (5)
OLS IV 1st Stage IV 2nd Stage IV 1st Stage IV 2nd Stage

LHS Variable % Miss Loan Pmt % PPP Rec. % Miss Loan Pmt % PPP Rec. % Miss Loan Pmt
∗∗∗
% PPP Received -0.013 -0.166 -0.184∗ ∗ ∗
(0.011) (0.035) (0.039)
State PPPE 31.238∗ ∗ ∗
(2.910)
State Predicted PPPE 62.610∗ ∗ ∗
(7.630)

Observations 3659 3659 3659 3659 3659
Adjusted R2 0.518 0.614 -0.119 0.601 -0.147
FStat 115.265 67.343

LHS Variable % Miss Schd Pmt % PPP Rec. % Miss Schd Pmt % PPP Rec. % Miss Schd Pmt

% PPP Received -0.082∗ ∗ ∗ -0.492∗ ∗ ∗ -0.492∗ ∗ ∗
(0.018) (0.066) (0.063)
State PPPE 31.014∗ ∗ ∗
(2.880)
State Predicted PPPE 62.154∗ ∗ ∗
(7.447)

Observations 3612 3612 3612 3612 3612
Adjusted R2 0.646 0.619 -0.128 0.606 -0.128
FStat 115.934 69.656

LHS Variable % Cash 3 mths % PPP Rec. % Cash 3 mths % PPP Rec. % Cash 3 mths

% PPP Received 0.009 0.380∗ ∗ 0.316∗ ∗
(0.030) (0.143) (0.149)
State PPPE 26.992∗ ∗ ∗
(2.961)
State Predicted PPPE 58.403∗ ∗ ∗
(6.815)

Observations 1445 1445 1445 1445 1445
Adjusted R2 0.603 0.774 -0.270 0.767 -0.200
FStat 83.103 73.435

Controls Yes Yes Yes Yes Yes
Industry×Week Fixed Effects Yes Yes Yes Yes Yes

payments, and ﬁxed employment-related expenses. Again percentage of ﬁrms in that state-by-industry group that re-
the two IVs generate very similar results. The results of ported receiving PPP. However, when we examine the same
the IV strategy in columns (3) and (5) suggest that a ten relation using instead the state PPPE or predicted PPPE
percentage point increase in ﬁrms receiving PPP is associ- variables, which better isolate access to the supply of PPP
ated with a 4.9 (s.e. = 0.7) percentage point decline in the funds, access to PPP is economically and signiﬁcantly re-
number of ﬁrms reporting missing any type of scheduled lated to the share of ﬁrms reporting signiﬁcant liquidity.
payments. In the IV regression, which uses state PPPE and predicted
The Census survey data also reveal that the PPP funds PPPE to instrument for the share of ﬁrms receiving PPP, a
increased ﬁrms’ cash on hand. This exercise also offers ten percentage point increase in the share of ﬁrms receiv-
a useful sanity check of the informativeness of the sur- ing PPP is associated with a 3.2 to 3.8 percentage point in-
vey data. Similar to results on missed loan payments, the crease in the share of ﬁrms reporting at least three months
coeﬃcients reported in column (1) of the bottom panel of cash to cover business operations.
of Table 10 do not indicate an economically or statisti- Overall, these results are consistent with the idea that
cally signiﬁcant relation between cash-on-hand and the the PPP provided ﬁrms with an important liquidity cushion

758
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

that they used to navigate the initial months of the pan- many workers saw UI replacement rates above their usual
demic. These results also align with our evidence that the salaries due to an additional $600 a week in federal ben-
PPP did not immediately induce employment responses eﬁts (Ganong et al., 2020). Some commentators and me-
and only modestly increased employment in the months dia reports suggested that this beneﬁt led to diﬃculties
following PPP receipt.44 Many businesses may have re- for ﬁrms in recalling workers, which could have attenuated
tained the PPP funds in bank accounts as precautionary the employment effects of the PPP.45 While recent work
savings until they were ready to resume activities, per- such as Altonji et al. (2020) suggest a muted effect of UI
haps when demand for their goods and services return extensions on unemployment levels and the speed of re-
to normal or when relaxed shelter-in-place orders permit turning to work, we consider this possibility by exploiting
them to reopen for business. Generally, the results are not state variation in UI replacement rates.
consistent with the idea that the PPP served as a large- We explore whether UI generosity attenuated the em-
scale alternative to unemployment insurance for delivering ployment effects of PPP lending by splitting our sample by
funds directly to affected workers. the generosity of state UI beneﬁts. In Appendix F, we re-
peat our analyzes of Tables 5 and 6 with the sample di-
7.3. Crowd-out and business stealing vided between states with above- or below-median UI re-
placement rates. The results do not support the hypothe-
One potential mechanism explaining the small employ- sis that the responses are greater in states with less gener-
ment effects of the program is crowd-out. The risk of gov- ous UI. For employment, UI ﬁlings, and small business rev-
ernment loan programs crowding out private lending has enues, effect sizes are either similar or greater in high ben-
long been a concern for loan guarantee programs (e.g., eﬁt states. It is important to note that, even in states with
Gale, 1991). In the counterfactual, PPP loans may have less generous UI systems, replacement rates were histori-
been made under standard commercial loan programs. In cally high for lower income workers and thus we may be
the presence of substantial crowd-out, the program would unable to capture the effects of a counterfactual without
have little effect on employment and other ﬁrm outcomes. elevated UI beneﬁts.
While we ﬁnd some evidence of crowd-out, the results
suggest that magnitudes are small and private lending 8. Conclusion
would not have fully offset PPP lending. The results are
presented in Appendix E. This ﬁnding is plausible because This paper studies a large and novel small business sup-
loans to replace lost revenue would be unlikely to pass a port program that was part of the initial crisis response
private loan underwriting test. package, the Paycheck Protection Program (PPP). We focus
Another possibility is that eligible ﬁrms might expand on the role that banks played in intermediating PPP funds,
at the expense of local competitors. Such business stealing the impact of bank performance on program targeting, and
spillovers could account for low employment effects at the the overall short- and medium-term employment and local
labor market level. Alternatively, the program might have economic effects of the program.
positive local demand effects, for instance, on the suppli- We consider three dimensions of program targeting.
ers of treated ﬁrms. Given the scale and severity of the First, did the funds ﬂow to where the economic shock was
labor market disruption due to the pandemic, traditional greatest? Second, given the PPP used the banking system
measures of labor market tightness are unlikely to be use- as a conduit to access ﬁrms, we ask what role did the
ful. However, we can ask whether regions with a larger banks play in mediating policy targeting? Third, why did
share of employment in PPP-eligible establishments exhibit some banks systematically under- or overperform in dis-
different effects relative to those with fewer eligible es- bursing PPP loans relative to their share of the small busi-
tablishments. Appendix F presents split sample analyses ness loan market? We ﬁnd little evidence that funds were
estimating employment effects for regions based on the targeted toward geographic regions more severely affected
share of establishments that would be eligible for funds. by the pandemic. If anything, the opposite is true and
Employment effects are generally similar or greater in re- funds were targeted toward areas less severely affected by
gions where a larger share of establishments are eligible the virus, at least initially. Bank heterogeneity played an
for funds, inconsistent with a business stealing effect and important role in mediating funds, affecting who received
possibly consistent with the presence of some local de- funds and when their applications were ultimately pro-
mand effects. cessed. Ex ante bank characteristics, including greater la-
bor capacity to process loans, pre-existing SBA relation-
7.4. UI expansion ships, and active enforcement actions against banks, pre-
dict banks’ relative performance in disbursing PPP loans.
One possible reason why the observed employment Regions with higher exposure to banks that performed
effects were so small is that historically high levels of well saw higher levels of PPP lending and received funds
UI made it diﬃcult for ﬁrms to recall workers. Indeed,
45
For example, the Wall Street Journal article “Businesses Struggle to
44
Appendix F provides additional evidence that exposure to PPPE is as- Lure Workers Away From Unemployment” on May 8th (https://www.wsj.
sociated with fewer permanent shutdowns in the Homebase sample. This com/articles/businesses- struggle- to- lure- workers- away- from- unemploy
evidence is consistent with the idea that despite modest employment ef- ment-11588930202?mod=ﬂipboard) suggested that “Businesses looking
fects, the program may have prevented ﬁrms from closing and this effect for a quick return to normal are running into a big hitch: Workers on
could manifest in stronger employment outcomes in the long- run. unemployment beneﬁts are reluctant to give them up.”

759
J. Granja, C. Makridis, C. Yannelis et al. Journal of Financial Economics 145 (2022) 725–761

more quickly.46 Limited targeting in terms of who was el- Sunderam, and Luigi Zingales for comments. Livia Am-
igible likely also led to many inframarginal ﬁrms receiving ato, Laurence O’Brien, Igor Kuznetsov, and Zirui Song pro-
funds and to a low correlation between regional PPP fund- vided excellent research assistance. João Granja gratefully
ing and shock severity. acknowledges support from the Jane and Basil Vasiliou Fac-
Using a number of data sources and exploiting lender ulty Scholarship and from the Booth School of Business
heterogeneity in disbursement of PPP funds, we ﬁnd ev- at the University of Chicago. Yannelis and Zwick gratefully
idence that the PPP had only a small effect on employ- acknowledge ﬁnancial support from the Booth School of
ment in the months following the initial rollout. Our es- Business at the University of Chicago. Zwick has provided
timates are precise enough to rule out large employment compensated expert testimony on behalf of a PPP loan ser-
effects in the short-term. It appears likely that many rel- vicer. We are grateful to the Small Business Administration,
atively healthy ﬁrms received funds and continued with Homebase, Womply, and Opportunity Insights for data, and
their business as usual. At the same time, the program may to the CDBA, ACAP, US Treasury, and the House Select Sub-
have played an important role in promoting ﬁnancial sta- committee on the Coronavirus Crisis for helping us under-
bility. Firms with greater exposure to the PPP hold more stand the institutional background.
cash on hand, and are more likely to make loan and other
scheduled payments. Supplementary material
Measuring the relative importance of these responses
is critical for evaluating the social insurance value of the Supplementary material associated with this article can
PPP and similar policies, and designing them effectively. be found, in the online version, at doi:10.1016/j.jﬁneco.
Because policymakers often rely on banks to deploy credit 2022.05.006.
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