Political Borders and Bank Lending

in Post-Crisis America

Matthieu Chavaz and Andrew K. Rose1

Updated: November 28, 2017

Abstract

We study political influences on private banks receiving government funds. Using spatial discontinuities associated with congressional district borders, we show that recipient banks of the 2008 TARP program increased mortgage and small business lending by 23-60% more in census tracts located just inside their home-representative’s district than just outside. The effect is stronger when the representative voted for TARP, is politically powerful, close to the financial industry, and when the bank is important in the district. These findings suggest that obtaining public funds subjects firms to political influences, which affects the allocation of corporate investment across political constituencies. Keywords: empirical; data; panel; fixed; effect; county; district; congress; policy; mortgage. JEL Classification: F36, G28 Chavaz: Bank of England, Threadneedle Street, London UK EC2R 8AH; +44 (77) 8741-8688; matthieu.chavaz@bankofengland.co.uk; http://matthieuchavaz.wix.com/home Rose: Haas School of Business, Berkeley CA USA 94720-1900; +1 (510) 642-6609; arose@haas.berkeley.edu; http://faculty.haas.berkeley.edu/arose

                                                            1 Chavaz is Senior Economist, Bank of England; Rose is Rocca Professor of International Business, ABFER Senior Fellow, CEPR Research Fellow, and NBER Research Associate. This paper grew out of conversations and work with Tomasz Wieladek, to whom we owe a considerable debt. For comments, we thank: Sumit Agarwal; Pat Akey; Saleem Bahaj; Allen Berger; Aaron Bodoh-Creed; Craig Brown; Victor Couture; Claudia Custodio; Lucas Davis; Ran Duchin; Paul Gertler; Brett Green; Rainer Haselmann; Zsuzsa Huszar; Rustom Irani; Rajkamal Iyer; Ravi Jain; Sebnem Kalemli-Ozcan; Ross Levine; Elena Loutskina; Frederic Malherbe; Hamid Mehran; Andrea Polo; Wenlan Qian; Veronica Rappaport; David Reeb; Richard Rosen; Yona Rubinstein; Farzad Saidi; Amit Seru; David Sraer; Johan Sulaeman; John Sutton; Hans-Joachim Voth; Bernie Yeung; and seminar participants at Bank of England, BoE-EBRD MoFir workshop, Barcelona Graduate School of Economics Summer Forum, Berkeley-Haas, CEPR Swiss Winter Financial Intermediation conference, Chicago Booth Political Economy of Finance conference, Chicago Financial Institutions conference, Financial Intermediation Research Society conference, Halle Institute for Economic Research, London School of Economics, and NUS Business School. All opinions expressed in this paper are those of the authors, not the Bank of England.

   

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Private firms can receive substantial public funds in the form of procurements, subsidies

or outright bailouts. The role of political connections in the allocation of these funds has

attracted substantial attention.2 This paper explores a related but different question: do political

influences affect the behavior of private firms that benefit from public funds? Government

funding can be critical for firms and the wider economy, particularly financial bailouts during

crises. Because they mobilize substantial taxpayer money, these programs generate substantial

political and media controversy. Yet, there is little evidence of how the political forces that

create the programs consequently affect the economic behavior of recipients of the same

programs. The objective of this paper is to show how a substantive public intervention in an

important market changes the investment decisions of beneficiary firms across political districts,

and, in particular, how this response likely reflects political influences.

Public funding programs provide scope to politicians to influence the availability and

terms of funds to firms they are connected to. Our main hypothesis is that beneficiary firms, in

return, increase investment in these politicians’ constituencies. We exploit a large American

government intervention, the injection of $209 billion capital into 709 banks under the 2008

Troubled Asset Relief Program (TARP). This program was exceptionally large and played a

prominent role in the financial crisis. It also illustrates the impact of one particular type of

political connections – those based on geographical proximity. Specifically, Congressional

representatives helped applicant banks headquartered in their constituencies to gain access to the

program.3 This leads to our question: did beneficiaries, in return, increase lending in these

politicians’ constituency? Since politicians tend to help firms located in their constituency more

generally, firms should have an incentive to be responsive to local politicians, particularly in a

                                                            2 Amore and Bennedsen (2013), Cingano et al. (2013), Cohen et al. (2011), Goldman et al. (2013), and Schoenherr (2017) show evidence of political influences on the allocation of public procurements. Johnson and Mitton (2003), Brown and Dinc (2005), Duchin and Sosyura (2012), Behn et al. (2014), and Liu and Ngo (2014) document political influences on government bailouts. 3 www.wsj.com/articles/SB123258284337504295

   

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context of regulatory overhaul.4,5 We find a strong positive answer: TARP recipients’ mortgage

and small business lending growth increases by 23% to 60% more inside the district of their

“home” Congress representative. Lending in areas immediately outside of the home district fell,

whereas lending inside the home districts remained flat or increased.

The American political and banking system provides an ideal empirical laboratory to test

whether banks respond to local political influences. The borders of the (435) American

congressional district border create spatial discontinuities between small contiguous areas which

are subject to the same political and regulatory circumstances, but part of different political

constituencies. US regulators provide comprehensive mortgage and (to a lesser extent) small

business data broken down by firm, time, and space, including detailed borrower characteristics.

Since most banks are active in multiple districts, we can compare bank lending in small

geographical units belonging to different congressional districts, while controlling for other (non-

political) determinants of lending, like credit demand or neighborhood affluence. Finally, the

relative transparency of the American legislative process provides data for politicians’ votes on

crucial issues like the TARP, and political contributions from the financial industry.

Our main test uses a 2006-2010 annual panel of bank-county-level mortgage lending

growth collected from Home Mortgage Disclosure Act (HMDA) data in a difference-in-

difference-in-difference set-up. Given our hypothesis, we ask whether the mortgage growth of

                                                            4 Faccio and Parsley (2009), Cooper et al. (2010), Cohen et al. (2013), Kim et al. (2013), Kostovertsky (2015). Politicians might help firms located inside their constituency because of common interests in local economic activity, and personal or financial ties (Amore and Bennedsen 2013; Tahoun, 2014; Cohen and Malloy, 2014). In addition to geography-based relations, firms can also connect with politicians through lobbying or donations. We do not investigate such connections. One advantage of focusing on geographical connections is that – conditional on the pre-determined headquarter location decision – they do not result from an active decision and can thus be treated as exogenous (Kim et al., 2013; Kostovertsky, 2015). If anything, the existence of other forms of connection would lead us to overestimate “true” connections, creating a negative bias against our results (Faccio and Parsley, 2009). 5 The case of Huntington Bank helps to illustrate our hypothesis. The bank is based in Columbus Ohio, but operated in a number of American states. In 2008, it received $1.4 billion in TARP funds, along with several other Ohio lenders. The Wall Street Journal reported that these injections followed the intervention of an Ohio “congressional delegation”. Six months later, Huntington announced that it would lend $1 billion to small businesses in Ohio through a partnership with the state government. Free Enterprise noted that “Many small businesses have waited for such initiatives from banks like Huntington that received TARP money”. http://blogs.findlaw.com/free_enterprise/2009/05/public-private-partnership-in-ohio-to-offer-1-billion-in-small-business-loans.html

   

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TARP recipients (compared to other banks) in a given county and year is higher after the TARP

(as opposed to before) if the county lies in the district of the recipient’s home representative (not

elsewhere).

The main challenge is that participation in TARP could be correlated with

characteristics of participants’ home district after TARP, besides those associated with political

considerations. For instance, participants might receive more credit demand or may be more

reluctant to cut lending in familiar areas close to their headquarters (“home bias”). Our baseline

approach mitigates these concerns in three complementary ways. First, we saturate the model

with county-year and bank-home fixed effects. Second, we focus on mortgages originated in

neighborhoods (census tracts) located immediately next to an intrastate congressional district

border. Third, we use Instrumental Variable (IV) estimators based on banks’ pre-crisis

regulatory or political connections, as well as propensity score matching (PSM) estimators based

on banks’ pre-crisis probability to enter TARP (Li, 2013; Duchin and Sosyura, 2014). Our result

is comparable in statistical and economic significance in all three approaches.

We pursue several alternative strategies to demonstrate that this “home-district effect”

does not result from non-political mechanisms. Our effect is insensitive to dropping heavily

gerrymandered districts. Also, controlling for several possible manifestations of a post-crisis

home bias does not change our conclusions. Specifically, our key result is robust to controlling

for a “flight” of TARP participants towards areas geographically closer to their headquarters,

richer counties, bigger counties, or urban counties in which they may possess superior

information. All this suggests that the home-district effect is driven by political borders between

congressional districts, not by home bias. Controlling explicitly for the possibility that TARP

recipients might receive more credit demand in their home district through county-year-TARP

fixed effects does not change our results either. Finally, more specific heterogeneities between

   

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TARP and non-TARP banks (like capitalization) and home-district and non-home district

counties (like affluence, loan risk, loan size or ethnic make-up) do not explain our results.

We find a similar home-district effect using disaggregated data (to remove any credit

demand effect); an individual mortgage application is 3 to 4% more likely to be accepted if it is

submitted to a TARP bank and the borrower is located inside the bank’s home-representative

district. We also find the home-district effect in a wholly different dataset of small business

lending. In contrast, the effect disappears when we falsify the timing of the TARP.

In the final part of the paper, we strengthen our interpretation by investigating the

variation of our result across time, policy beneficiaries, and politicians, and its aggregate impact

for district lending conditions, electoral outcomes, and bank portfolio quality.

Overall, our findings suggest that the home-district effect is concentrated in periods,

banks, and congressional representatives where there is the greatest scope for political

interference and the most mutually valuable connection between the bank and its home

representative. First, the timing of the home-district effect coincides with periods during which

politicians have the greatest latitude to interfere in the allocation process, namely before the

Treasury steps in to reduce lobbying in favor of TARP applicants. Interestingly, the home-

district is reversed when a participant exits the program, or when its home representative at the

start of the program is no longer in office. When this happens, the recipients decrease lending

growth inside their home district, and increase it elsewhere.

Second, the home-district effect is higher for banks where political interference is more

likely or more valuable. Specifically, the effect is higher for those banks whose organizational

structure allowed them to apply during the first round of TARP disbursement, presumably the

period of maximal political interference. The effect is also higher for banks less likely to be

accepted by regulators (due to high liquidity risk).

   

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Third, the home-district effect is concentrated among politicians who might be more

willing or able to help banks, either in the specific context of TARP applications or in the

broader context of regulatory overhaul in Congress. We find that the home-district effect only

holds if the representative supported the (tightly contested) TARP bill in Congress. The home-

district effect is also stronger if he/she was a member of a House committee used for TARP-

related legislation. The effect also increases with the amount of pre-crisis campaign

contributions the politician received from the financial industry. Finally, the effect rises with the

importance of the bank in the representative’s district: the higher the recipients’ pre-crisis

mortgage market share in the politician’s constituency, the higher the home-district effect.

Together, our results indicate that banks are particularly responsive to political influences

(or the threat thereof) when the connection with the home representative has reciprocal benefits,

whether realized or potential. This leads us to conclude that the home-district effect is political.

In an appendix, we aggregate data by districts and banks and provide three results

consistent with this conclusion. First, we show that districts with a larger presence of TARP

participants headquartered locally see a larger increase in total mortgage originations and

application acceptation after TARP. Second, improved lending conditions are empirically

associated with a better performance of the district’s incumbent’s candidate in the 2010 midterm

House of Representatives election. Third, TARP participants with a higher share of home-

district loans see a larger increase in non-performing loans two years after the onset of the

TARP. While indicative rather than definitive, these results support the notions that the home-

district effect matters for aggregate lending and political outcomes across districts, and entails a

cost to affected banks.

   

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1. Context in the Literature

The key contribution of this paper is to document evidence of political forces affecting

investment decisions by private firms that are beneficiaries of government funds.

Our findings provide a counterpoint to extensive evidence that firms derive important

benefits from political connections, like support for relevant legislation (Kroszner and Strahan,

1999; Mian et al., 2012; Cohen et al., 2013) and procurement contracts (Goldman et al., 2013;

Amore and Bennedsen, 2013; Cingano et al., 2013; Cohen et al., 2011; Tahoun, 2014;

Schoenherr, 2017). Bailouts are an important case in point. Connected banks are more likely to

get bailed out in developing and advanced countries (Johnson and Mitton 2003; Brown and Dinc,

2005; Behn et al., 2014; Duchin and Sosyura, 2012; Liu and Ngo, 2014); this is one reason why

political connections boost firm value (Faccio et al., 2006), as shown by Fisman (2001) and

Faccio (2005).

These papers study political influences on access to government funds. Our work focuses

on the “flip side”: we show that banks receiving public funds re-allocate lending across political

constituencies in a way consistent with informal political influences. Bertrand et al. (2007) find

only weak evidence for the related hypothesis that private French firms carrying out politically

motivated investments in key constituencies receive more government subsidies in return.

Our findings also contribute to understanding the effect of large-scale government

intervention into private firms. Black and Hazelwood (2013) and Duchin and Sosyura (2014)

show that TARP banks become riskier; this suggests that access to public funds creates moral

hazard. Our paper highlights a different effect: receiving public funds subjects beneficiaries to

political influences, and this affects the allocation of corporate investment across constituencies.

This uneven allocation might help explaining why the bank-level effect of TARP on lending is

modest (Li, 2013). While many studies discuss the possibility of political influences on TARP

   

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participants (e.g. Veronesi and Zingales, 2010), ours is the first to explicitly investigate whether

and how these influences affect the geographic allocation of credit.6

Our paper also complements extensive evidence of politically motivated bank lending in

emerging markets and Italy (Sapienza, 2004; Khwaja and Mian, 2005; Dinc, 2005; Claessens et

al., 2008; Cole, 2009; Carvalho, 2014). This evidence always draws from government-owned

banks. Since politicians have formal powers like board appointments on these banks, these

findings could reflect formal lending mandates rather than an informal “quid pro quo”.7 Our set-

up allows us to focus on the latter mechanism, as government-owned banks do not exist in the

United States and Congress explicitly ruled out lending mandates on TARP participants.

Our results echo two recent findings: consumer credit falls in the districts of Senate

committee leaders (Akey et al., 2016), and post-crises foreclosures are delayed in the districts of

House financial services committee members (Agarwal et al., 2016). We study a different

outcome (mortgage and small business lending) and mechanism: political influences specific to

beneficiaries of public funds. This effect varies with both politicians’ ability to help firms (as

proxied by power in Congress), and on their willingness to do so (as proxied by votes and the

bank’s importance in the politician’s district). This helps understanding why the value of

geographic political connections is not conditional on committee assignments (Faccio et al.,

2006; Faccio and Parsley, 2009; Cooper et al., 2010; Kim et al., 2012), and why financial

industry donations to politicians outside banking committees are substantial.8

                                                            6 Calomiris and Kahn (2015) survey studies of the TARP. Akin et al. (2016) explore insider trading related to the TARP. 7 Unlike the other papers, Claessens et al. (2008) do not specifically focus on state-owned banks. But they note that their results could be explained in part by the prevalence of state-owned banks in Brazil. 8 Twelve of the twenty 110th Congress House representatives with the highest financial industry contributions were not members of the House banking committee. Mian et al. (2010) data shows that the average non-member receives 154,445 $ against 348,568 for members. In addition to committee membership, politicians power depends on ruling-party membership (Kim et al., 2012), seniority (Roberts, 1990), relationship length (Cooper et al., 2010), and the ability to enter logrolling deals (Stratmann, 1992).

   

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Finally, our results speak to a broad literature in international trade and finance on the

home bias and the border effect, and on the reasons why these effects increase after crises

(Giannetti and Laeven, 2012; Rose and Wieladek, 2014).9 One challenge is that areas separated

by international borders – and many intra-national borders – differ in many dimensions, like

regulatory, fiscal and monetary policy, and opacity. We study close and small areas where these

differences can be controlled for; we can thus focus on the political dimension of borders.

2. The TARP and Political Influences

2.1. The TARP

The Troubled Assets Relief Program (TARP), a plan to purchase illiquid mortgage-

backed (“toxic”) securities from banks, was submitted to Congress on 20th September 2008 as

part of the Emergency Economic Stabilization Act (EESA). The bill initially failed to pass

through the House of Representatives on September 29th; after a stock market collapse that day,

it was reconsidered and obtained a bipartisan majority less than a week later, on October 3rd.

Shortly thereafter, the Treasury announced its intention to use TARP funds primarily to purchase

equity shares in banks. Since this Capital Purchase Program (CPP) mobilized the largest share of

funds initially earmarked for the TARP, we refer to CPP and TARP interchangeably.

As of March 2016, $209.1 bn of CPP funds had been used to buy preferred equity in 709

different banks or bank-holding-companies. This started with a forced injection of $125 bn into

nine major American banks on 14th October. Participation was then opened to all domestic

regulated deposit-takers on a voluntary basis, subject to a three-step application process. First,

applications were submitted to and reviewed by the applicant’s local regulator (e.g. a state

branch of the FDIC). Second, this initial review was screened by the applicant’s national

                                                            9 See e.g. Cooper (2013) for a survey.

   

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regulator (e.g., the FDIC’s Washington headquarters). Finally, the Treasury made one last

review. Criteria included measures of applicants’ financial health such as capitalization,

liquidity, and local concentration. Once in the program, recipients were subject to a mandatory

5% annual dividend payable to the Treasury.

2.2. Sources of Political Influences

The beginnings of the TARP were marked by contentious and widely publicized

discussions around the program’s perceived failure to boost lending to “Main Street.” TARP

recipients and congressional supporters were vilified at both Tea Party and Occupy Wall Street

rallies.10 The TARP “stigma” had concrete repercussions; Ng et al. (2011) find that the media

coverage of TARP recipients was mostly negative, which depressed their stock returns.

The public authorities had no formal way to appease such outrage by encouraging

participants to lend. The Treasury bought non-voting shares (warrants) from banks, and CPP

contracts initially did not contain any covenants on lending, nor on the disclosure of usage of

funds. Oversight bodies, both public (e.g. the US Government Accounting Office) and private

tried to fill this gap by monitoring recipients’ behavior. For instance, a 2010 report by the

Woodstock Institute pointed to a decline in mortgage lending by the largest TARP recipients to

underserved communities in major American cities.11

However, Congress retained a key source of leverage on participants via a provision to

modify ongoing CPP contracts unilaterally. Congress made use of this provision in 2009 to force

participants to obtain the Treasury’s approval for executive compensation and CPP repayment

plans, motivating the largest American banks to exit the TARP quickly (Bayazitova and

Shivdasani, 2011; Wilson and Wu, 2012). Congress also discussed imposing conditions on

                                                            10 The Tea Party ‘backlash’ was triggered by the launch of the HAMP, a follow-up program to TARP. https://en.wikipedia.org/wiki/Tea_Party_movement. 11 http://www.woodstockinst.org/sites/default/files/attachments/payingmore4_may2010_collaboration_0.pdf.

   

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lending, prompting some industry observers to “fear that the TARP will become a vehicle by

which Congress will impose credit allocation policies on TARP investees.”12 This suggests that

Congress retained important leverage on recipients even once the funds had been distributed.

While Congress renounced imposing formal lending mandates, it retained informal ways

to encourage lending. Politicians could single out TARP recipients “guilty” of insufficient

lending.13 For instance, the chairman of the March 2009 hearing “Is TARP working for Main

Street?” invited a deli-owner from his district to testify about the refusal of a TARP recipient to

roll over his loan. In his statement, the chairman acknowledged that such hearings could lead

“critics of Congress” to “argue that we are setting out to force banks to lend or encouraging

banks to make bad loans.”14 TARP architect Henry Paulson himself acknowledged that “banks

rushed to repay because of the associated restrictions on pay levels and the political atmosphere,”

pointing in particular to “calls for mandatory lending” from Congress in 2008; “as soon as we

announced it (…) people were saying, ‘Make them lend. Why aren’t they lending more?’ …

And so I think what happened was then some banks were reticent to take the capital.”15

Anecdotal evidence suggests that recipients were responsive to political circumstances,

and could use evidence of lending in key areas to counter criticisms. Confronted by an Ohio

congresswoman about foreclosures in her district, TARP recipient J.P. Morgan communicated

that “the company lent more than $16 billion to more than 3.5 million Ohio consumers last year

and provided $3.8 billion in loans to more than 70,000 companies in the state.”16 A couple days

                                                            12 https://www.gpo.gov/fdsys/pkg/CHRG-111hhrg48862/html/CHRG-111hhrg48862.htm. 13 In December 2008, the Chicago firm Republic Windows & Doors shut its doors, laying off 300 employees, after failing to renegotiate an important loan with Bank of America. Speaking at a worker’s sit-in, TARP supporter Illinois Senator Dick Durbin said: “We are going to sit down with my friends in the Senate and talk about ways to reach out to the bank, which is receiving funds from the $700 Troubled Assets Relief Program”; http://www.findingdulcinea.com/news/business/2008/December/Factory-Closure-Leads-to-Worker-Sit-in--Calls-for-Bank-of-America-Boycott-.html 14 The Chairman contended that he was “not interested in encouraging banks to made bad loans” but that “even under [stricter lending] standards there are thousands of businesses across the country that can qualify for loans.” https://www.gpo.gov/fdsys/pkg/CHRG-111hhrg48862/html/CHRG-111hhrg48862.htm. 15 https://www.ft.com/content/3379543e-5913-11df-90da-00144feab49a. 16 http://www.wsj.com/articles/SB10001424052748703416204575145743093039972.

   

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ahead of his testimony before Congress, the CEO of (TARP recipient) MidSouth Bank

announced to local TV channel KPLC that his bank “is extending its popular Town Hall-style

meeting series” at its headquarters and branches. ‘The series was a big success in that it helped

us get the message out that we are looking for qualified borrowers …’.”17 Tennessee-based

consultancy Financial Marketing Solutions offered advice on “how to communicate acceptance

of TARP money”, recommending that banks “promote … TARP-driven opportunities to lend

more to the community, sparking new growth and economic activity”, rather than “defending the

media accusation that banks are hoarding the TARP money to cover losses.”18

It seems clear that anecdotal evidence suggests that TARP recipients were both exposed

and potentially responsive to political forces in their lending decisions, especially from TARP

supporters in Congress, and that this exposure could differ across constituencies.19

The TARP remained a contentious issue for both representatives and recipients through at

least the 2010 mid-term elections.20 Official efforts to boost the impact of the TARP on lending

resulted in a number of follow-up programs designed to increase mortgage refinancing (HAMP),

small business credit (SBLF), or lending to underserved communities (CDFCI). This further

suggests that political considerations may have remained relevant to TARP participants for

several years even after they first received TARP money. Still, the point of this research is to

provide rigorous statistical evidence of political effects on lending; we now turn to that task.

                                                            17 http://www.kplctv.com/story/9973030/midsouth-bank-extends-town-hall-meeting-schedule. 18 http://www.fms4banks.com/blog/2009/01/23/how-to-communicate-the-acceptance-of-tarp-money. 19 It is easy to find contemporary informal evidence of political interference with the TARP process. For instance, Barney Frank’s intervention on behalf of OneUnited Bank was covered by the Wall Street Journal, January 22, 2009. Governor Mark Sanford is quoted as saying “It’s total arbitrary … If you’ve got the right lobbyists and the right representatives connected to Washington … you get the golden tap on the shoulder …” (in The Daily Kos, January 23, 2009). The New York Times discussed the loosening rules on bank aid on Oct 31, 2008. 20 www.nytimes.com/2010/07/11/us/politics/11tarp.html.

   

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3. Methodology and Data

We are interested in whether political considerations matter for credit decisions of banks

which received TARP capital injections. In particular, we seek to determine if these banks lent

more inside the congressional district of the political representative where the bank is

headquartered – the “home district” – than outside.

We choose counties to delineate local banking markets following much of the literature.21

Accordingly, our dependent variable of interest is the lending growth for a given bank in a

particular county for a single year. One complication is that counties in urban areas often span

multiple districts (e.g., in Los Angeles County). Since we are interested in separating home-

district lending from other lending, we further split any multi-district county into districts.

Figure 1 illustrates this strategy for the state of Oklahoma (OK). The thick (black) lines

delineate the five OK congressional districts in the 110th Congress, identified by their number

(inside red circles). Thinner (gray) lines delineate the 77 OK counties. The rural Caddo County

(southwest of Oklahoma City; population 29,600) belongs entirely to the 3rd district. In contrast,

the urban Oklahoma County (around Oklahoma City; population 718,633) spans the 4th and 5th

districts. In the latter case, we split a bank’s annual lending into loans made in the a) 4th and b)

5th districts.22 In what follows, we refer to these as “county-years” for convenience.

                                                            21 See for instance Gilje et al. (2016). The contours of local banking markets do not generally coincide with congressional district borders. Mortgage lending data for 2005 (sources are discussed in the following section) indicates that the median/average American bank originate mortgages in 5/11.2 congressional districts, respectively. The 10th percentile bank lends in two districts, suggesting that even small banks operate in more than one congressional district. The disconnect between banking markets and districts seems obvious, since district maps are not primarily drawn based on economic or socio-economic homogeneity, but rather on intrinsically political criteria, starting with the need for each district to contain a similar number of people. Further, the allocation of congressional districts to states is changed every decade and district maps are regularly re-drawn; consequently, the shapes of some districts change in the absence of economic changes. 22 In our baseline sample, we use only loans within a given county which are made in census tracts adjacent to an intrastate district border; more on this below.

   

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3.1. Empirical Model

We employ a difference-in-difference-in-difference strategy; we examine credit growth

of TARP recipients (as opposed to non-recipients), after the TARP (as opposed to before), in

counties inside a bank’s home district (as opposed to outside). Our empirical model is:

ΔLoani,c,t = βTTARPi,t + βTHTARPi,t∙Homei,c + δXi,t + ζZi,c,t + {ηc,t} + {θi,c} + εi,c,t (1)

where:

ΔLoani,c,t is the first difference in the natural logarithm of aggregate mortgage lending

originated by bank i in county c (or county-district c in multiple-district counties), in year t,

TARPi,t is a dummy variable which is one if i had received CPP capital by time t, and zero

otherwise,

Homei,c is a dummy variable which is one if county c is part of the congressional district in

which bank i is headquartered (using districts from the 110th congress), and zero otherwise,23

δ and ζ are nuisance coefficients,

X is a vector of bank controls similar to Duchin and Sosyura (2014), which includes one-year

lags of: size (log total assets, hereafter “TA”); tier-1 capital (%TA); cash (%TA); charge-offs

(% total loans); non-performing loans (% total loans); repossessed real estate (% TA);

deposits (%TA); (log) bank age; return on equity; and exposure to local shocks (average

change in Philadelphia Fed yearly state-level economic activity index, weighted by bank’s

branch presence in a state),

Z is a vector of borrower controls, which includes weighted average characteristic in a

county-year (using loan size as weight) of: loan-to-income ratio; log income; log loan size;

dummy for ethnic minority (non-Caucasian); dummy for gender (non-male); and median

family income in borrower’s census tract,

                                                            23 Note that Homei,c does not appear in level in the model since it is captured by the bank-home fixed effect.

   

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{ηc,t} and {θi,c} are comprehensive sets of county-year and bank-home (district) fixed

effects, respectively, and

εi,c,t is a (hopefully) well-behaved residual, to represent all other determinants of loan growth.

The main coefficient of interest is βTH. The parameter captures the differential effect of

the TARP for mortgage growth in counties inside the bank’s home district. βT measures the

effect of TARP on mortgage growth in non-home district counties. We interpret robust

indications of a positive significant βTH to be evidence of a “home-district effect” associated with

political influences.

We begin by looking for such influences in all districts and thus for all representatives.

This is a conservative approach since some representatives are clearly more able and/or more

willing than others to cater to participants’ interest, for instance vis-à-vis the bank regulators

administering the TARP. Later on, we explore how the home-district effect varies with proxies

for the ability or inclination of a representative to help participants, like votes on key issues,

power in Congress or contributions received from the financial industry.

3.2. Estimation

We estimate (1) with four different techniques, clustering the standard errors by bank.

The main econometric challenge is that participation in the TARP could be correlated with post-

TARP characteristics of the participants’ home district, besides those linked to political effects.

For instance, a bank anticipating high credit demand in its home district could be more prone to

apply to the TARP, and to be accepted by the regulator. Alternatively, TARP banks could be

financially weaker, and may choose to cut lending first in distant areas while maintaining lending

in areas close to its headquarters where it has a comparative advantage in identifying profitable

   

15  

investments (“home bias”).24 We address this challenge in three complementary ways: a) fixed

effects, b) a sample selection highlighting spatial discontinuities associated with political borders

and c) instrumental variables (we also pursue this issue further below in different ways).

We remove considerable unobserved heterogeneity via the two sets of fixed effects in (1).

The county-year fixed effects {ηc,t} control for credit demand and economic activity in a given

county-year.25 The bank-home fixed effects {θi,c} control for time-invariant heterogeneity

across banks and the way they behave in home and non-home-district counties, for instance

because of superior local knowledge.

3.3. Spatial Discontinuity

We further attenuate unobservable heterogeneity between home and non-home lenders

and counties by measuring ΔLoani,c,t using only loans inside a given county c (or district in a

multi-district county) that are originated in census tracts immediately adjacent to an intrastate

congressional district border. We can do so since our data reports the location of a borrower at

the level of the census tract, a small unit designed to contain a socio-economically homogeneous

population of about 7,000 individuals.

Of 77 Oklahoma counties, only 33 contain census tracts adjacent to an intrastate district

border (these counties are shaded in Figure 1); we drop the other 44 counties. Within the

remaining 33 counties, we then focus on census tracts next to district borders. The mean/median

OK county has 12.9/5 census tracts; rural counties have only few tracts, but urban counties have

                                                            24 Banks behave differently in markets closer to their headquarters since geographical proximity attenuates informational asymmetries (Petersen and Rajan, 2002), particularly so after downturns (Giannetti and Laeven, 2014; Chavaz, 2016). 25 Our home-district effect estimate could be biased upwards if TARP recipients receive more unsolicited applications in their home district. It is unclear whether or not unsolicited prospective borrowers might prefer to apply with a TARP recipient rather than with other lenders. Applicants might perceive TARP banks to have higher lending capacity due to lower funding costs, but applicants might also be wary of the stigma attached to TARP participation, perceiving it as a signal of underlying weakness (Berger and Roman, 2015). Either way, it seems implausible to us that this perception would prevail only a) inside the bank’s home district and not elsewhere, and b) for borrowers with higher unobservable quality. For robustness, we check for the possibility that TARP recipients received more unsolicited applications via county-year-TARP fixed effects.

   

16  

many. Keeping only “frontier” census tracts allows us to increase the sharpness of

discontinuities (particularly in urban areas). This strategy is illustrated in the close-up map of the

Oklahoma County in Figure 2. The thick (black) lines again delineate districts, while thin (gray)

lines separate census tracts. Out of the 227 tracts in Oklahoma County, we only keep loans from

the 33 census tracts adjacent to district borders (shaded in Figure 2).

The goal of zooming onto “frontier” tracts is to make Homei,c irrelevant for non-political

reasons, like home bias. A bank headquartered in downtown Oklahoma City (in the 5th OK

district) might have superior information on future lending opportunities in the average

Oklahoma County tract, compared with “outsider” banks or counties. But it is less plausible that

this advantage also characterizes Oklahoma County tracts immediately next to the 5th district

border, especially by way of comparison with tracts immediately on the other side of the same

border. This restriction – combined with fixed effects and instrumental variables (see below) –

reduces the danger of our results being tainted by bank home-bias, and makes us comfortable

with assuming that unobserved home-district characteristics (such as expected local demand or

knowledge) cannot explain selection into TARP, and post-TARP lending growth. Since we

exclude areas contiguous to any district border which coincides with a state border, we also

attenuate differences due to bank regulation and supervision or the broader institutional

framework.

The drawback of the strategy is that it removes much of the data. Appendix A1 provides

further detail on this issue. In particular, we show that our approach does not seem to create

selection bias. We also show below that we obtain similar results using all census tracts,

suggesting that that our discontinuity approach adds safety to our identification strategy but is

not strictly necessary for our results.

   

17  

3.4. Instrumental Variable Strategy

A third way to reduce concerns that participation in the TARP is correlated with post-

TARP district-level heterogeneity is to instrument for a bank’s TARP participation using pre-

determined bank characteristics. We follow Li (2013) and Duchin and Sosyura (2014) by

predicting TARP participation using connections with influential regulators and Congress

members. We first estimate a cross-sectional probit model of bank’s i participation in TARP:

TARPi = λConnectionsi + ψXi + ξi (2)

where

Connectionsi is a measure of connections for bank i. We use two measures of connections:

1. Fed director is one if an executive director of bank i served on the Federal Reserve’s

Board of Governors or the board of a regional Fed,

2. Subcommittee member is one for bank i if its home-district representative served on

the Financial Institutions and Consumer Credit Sub-Committee of the 111th Congress,

X are control variables, taken from equation (1), using 2008q3 values,

λ and ψ are coefficients to be estimated for instrument generation, and

ξ is a well-behaved residual. 26

After estimating (2), we retrieve the fitted values and interact them with a dummy

variable (unity post 2007, zero before) to create a time-varying instrument. That is, we form (

Connectionsi + Xi)∙It where It is one after 2007 and zero otherwise. We call this instrument

                                                            26 Fed director and Subcommittee member is 1 for 1% and 8.4% of 6,251 banks included in that regression, respectively.

   

18  

TARP. To estimate βTH we follow the same procedure, but interact the IV additionally with our

home-district dummy variable, which we call TARP ∙ Home.27

Coefficient estimates from the first stages are presented in Table A2; it is immediately

obvious that ours are not weak instruments, satisfying the first requirement for a suitable

instrument. A second condition is that TARP ∙ Home affect ΔLoani,c,t only via its impact on

TARPi,t∙Homei,c rather than via factors excluded from model (1). In other words, TARP ∙ Home

should be uncorrelated with εi,c,t. Duchin and Sosyura (2014) show that committee memberships

are largely exogenous to bank lending behavior since they are allocated on the basis of federal

political outcomes and rotate regularly. It would take an even stronger assumption for the

exclusion restriction to be violated in our case given our difference-in-difference-in-difference

approach and extensive set of fixed effects: congressional sub-committee membership or Fed

directorship would have to be correlated with credit demand faced by TARP recipients only, only

in their home-district, and only after TARP, which seems implausible.

3.5. Propensity Score Matching

A final challenge is that participation in TARP could proxy for other bank characteristics

which could affect post-crisis home lending. For instance, financially weak banks could be more

likely to participate and to retreat home after the crisis, irrespective of TARP. Following again

Duchin and Sosyura (2014), we match samples consisting of a) all TARP recipients and b) their

closest non-recipient counterpart. To match recipients and non-recipients, we estimate a probit

model of TARP participation similar to (2), but without the political variables.28 We then match

                                                            27 One caveat: we lack information on bank applications to the TARP. Duchin and Sosyura (2012, 2014) have collected application information from banks’ annual reports or other communications. However, this information is only available for public banks, which are a minority in our sample. Duchin and Sosyura (2012) find that 80.2% of eligible banks applied, and that pre-existing connections do not correlate with application decision. 28 We also add a dummy for whether a bank is part of a Bank Holding Company [BHC] or not. We refer to BHCs informally as banks in the text below.

   

19  

each recipient to a non-recipient using predicted participation probabilities, delivering propensity

score matching estimates of our key coefficients.

3.6. Data and Sample

We focus on the mortgage market, for two reasons. First, its intrinsic importance,

especially for the 2007-09 financial crisis which probably originated in the American housing

market. Second, the relevant dataset is of high quality and covers the majority of the American

market. All financial institutions are required to report their mortgage origination activity to the

FFIEC under the 1975 Home Mortgage Disclosure Act (HMDA) on a mandatory annual basis,

minimizing the selection bias present, for instance, in small business lending data.29 Crucially,

the dataset provides detailed borrower location information, a key requirement for our strategy.

We focus on data for the 2006-2010 period.30 From the raw dataset, we discard

applications received by non-commercial bank lenders (credit unions, thrifts, subprime

specialists, etc.), applications with incomplete location or income information, applications in

overseas territories, and applications for unusual products (multi-family dwellings and loans

guaranteed by the Veterans Administration or the Farm Service Agency). This leaves us with

44.8 million mortgage applications.

For each entry, HMDA reports whether the application was accepted, the identity of the

bank, loan-, borrower- and borrower-census-tract characteristics, including loan size, income,

race, and sex. The borrower location is reported at the level of the census tract. We use this

information to discard loans made in tracts not contiguous to an intrastate congressional district

                                                            29 The only HMDA reporting exemption is for banks under a size threshold (e.g. $36 mn in 2007) and banks without a branch in a Metropolitan Statistical Area (MSA). This means that the data covers the vast majority of mortgage lending, excepted in a few rural areas. Data can be downloaded from the FFIEC website (https://www.ffiec.gov/hmda/hmdaproducts.htm). The coverage is less comprehensive in the small and medium enterprise (SME) lending dataset stemming from the Community Reinvestment Act (CRA). We use this dataset as a robustness check below. 30 We use a relatively short window (2006-2010) for the baseline estimation to diminish the problem of banks exiting TARP. To check the importance of the window, we experiment with alternatives later on.

   

20  

border (see above). We used Census Bureau maps for the 110th congress to map census tracts

into districts, and a relationship file from Brown University to identify contiguous tracts.31

Finally, we aggregate the data by bank-county-year (or bank-county-district year in multiple-

district counties). The final dataset spans 8,708 county-year and 5,272 bank-home combinations.

Since the majority of TARP recipients were bank-holding companies (BHCs) rather than

banks, we aggregate lending data to the BHC level, and refer to “banks” for convenience in what

follows.32 We typically do not include data for the nineteen biggest US banks, those which

participated in the Fed’s 2009 SCAP stress test; since they were forced to participate in the

TARP, there is no way to separate the effect of TARP from the effect of being a systemically

important bank.33 We also drop foreign-owned banks ineligible for the TARP, and banks for

which we cannot find the end-2007 headquarter in Call Reports.

We add data on TARP recipients taken from the US Treasury’s website and merge it with

HMDA data using the recipient’s name.34,35 The data indicates the size and timing of capital

injections, as well as the dates of the initiation and completion of repayment, if applicable. 672

distinct firms (mostly banks) participated in TARP; 204 entered the program in 2008, and

another 468 in 2009. We observe 444 of the 672 participants in our full bank-county-year

mortgage lending.36 The FDIC’s Call Reports database provides us with bank-year controls and

the unique regulatory identifier of a bank and its parent BHC. We aggregate all these controls to

                                                            31 See http://www.s4.brown.edu/us2010/Researcher/Pooling.htm. A limited number of tracts can be attributed to more than one district; we drop loans granted in these tracts. 32 We map the bank identifier provided in HMDA into a BHC identifier using the Regulatory High Holder identifier provided in bank Call Reports. For banks unaffiliated to a BHC, we aggregate data at the bank level. 33 Duchin and Sosyura (2014). We check for the importance of this exclusion below by including these banks in a sensitivity check. 34 See treasury.gov/initiatives/financial-stability/reports/Pages/default.aspx. 35 We thank Anya Kleymenova for kindly sharing her merging file. 36 We do not observe the remaining 228 participants for a variety of reasons: some participants do not do mortgage lending at all (e.g. American Express); others are too small or too little present in urban areas to be covered in HMDA; some participants are missing data (e.g., 2007 headquarter location); some are removed because of the filters we apply (e.g. dropping the top-19 banks like Bank of America). 383 of these 444 participants remain in the final benchmark sample once we filter out loans in non-contiguous tracts.

   

21  

the BHC-year level. The BHC-level Call Reports provide us with the BHC’s headquarters

location.37 We use the end-2007 bank headquarters location, to rule out strategic relocation after

the crisis. We again map the headquarter location into districts using Census Bureau maps.38

We merge HMDA and Call Reports data using the regulatory identifier provided by HMDA.

Finally, we find data from the House of Congress website on congressional

representatives, membership in key committees, and voting behavior for TARP-related roll calls.

Data from service on Federal Reserve Bank boards are from Li (2013).39

3.7. Summary Statistics and Parallel Trends Assumption

Appendix A2 provides descriptive statistics and discusses the timing of the shock as well

as the validity of the parallel trends assumptions. Average home and non-home lending trends

are roughly comparable for participants and other banks before TARP. After TARP, participants

cut non-home lending drastically whereas home lending remains comparable for the two groups.

This effect is reversed in 2010, when most participants have exited the program. While

necessarily informal, we find this result interesting; it proves to be consistent with our more

rigorous statistical work. We now turn to the latter to confirm the “home-district” effect using

our regression framework.

                                                            37 Bank- and BHC-level Call Reports can be downloaded from the Federal Reserve Bank of Chicago website (https://www.chicagofed.org/banking/financial-institution-reports/commercial-bank-data and https://www.chicagofed.org/banking/financial-institution-reports/bhc-data, respectively). 38 In single-district counties, we map bank headquarters into districts using the Census Bureau relationship file. For banks with headquarters located in counties with multiple districts, we either use the headquarters’ zip code and combine it with a ZCTA-District and ZIP-ZCTA relationship file from the Census Bureau, or headquarters’ geographical coordinates (from Summary of Deposits) mapped into districts using our own geo-coding routine. We drop the few banks whose headquarters can be attributed to multiple districts. 39 We thank Lei Li for kindly sharing the data for his instrument.

   

22  

4. Main Results

4.1. Benchmark Estimates

Our benchmark results are presented in Table 1, which tabulates estimates from OLS

(column 1), both sets of instrumental variables (IV, in columns 2-3), and propensity score

matching (PSM, in column 4). We tabulate the {β} coefficients of interest: the effect of TARP

on mortgage-loan growth outside the home-district, and whether this effect differs significantly

between areas inside and outside the home-district (other estimates are available online).

The effect of the TARP on mortgage lending outside the home-district, tabulated in the

second row, is mixed. In particular, the coefficient tabulated on the bottom row, βT, is

statistically insignificant and small for OLS and PSM estimators, negative and significant for

both IV estimators. In other words, banks that received TARP funds either maintained or cut

lending for areas outside their home-district. Still, our main interest is in the top row, which

tabulates estimates of the home-district effect, βTH, on loan origination.40 In contrast with the

small or negative effect of the TARP outside the home-district, the parameter for TARP x Home

indicates that the effect of TARP inside the home district is highly significant, both statistically

and economically. Our OLS estimates indicate that mortgage lending grows (exp(.22)-1≈) 25%

more in home districts; the PSM estimate is comparable. IV estimates suggest an even larger

effect, indicating that the TARP leads to around (exp(.47)-1≈) 60% more lending in the home

district. The fact that IV estimates are larger than the OLS/PSM estimates is consistent with IV

measuring the local treatment effect of receiving TARP funds as soon as the possibility opens up

(results in section 5 show that early recipients are more prone to political influences), and partly

                                                            40 The coefficient measures whether more loans are originated within the home-district of the bank, ceteris paribus; because some of these loans will be securitized, agents outside the home district will eventually hold some of the mortgages. It is unclear whether this would be of relevance to the relevant politicians.

   

23  

thanks to political connections. All four (OLS, IV, and PSM) estimates are statistically different

from zero at the 1% level.

The average home-district lending growth of TARP participants can be gauged by adding

the parameter estimates for TARP and TARP x Home. This sum ranges from 0.06 (second IV

regression) to 0.17 (OLS regression). But the t-test p-values reported at the bottom of Table 1

show that these sums are different from zero in the OLS regression only. In other words, TARP

participants do not necessarily boost lending inside their home district; instead, they seem to

shield home-district counties from the lending cuts they impose elsewhere. This interpretation

coincides with the visual reading of lending trends in Figure A1 (see section 3.7).

4.2. Sensitivity Analysis

Table 2 reports sensitivity analysis for the key coefficient, βTH, the estimate of the home-

district effect. We consider seventeen perturbations to our benchmark methodology, and tabulate

OLS, IV, and PSM estimates in Panel A of Table 2; our default estimates from Table 1 are

recorded on top to facilitate comparison.

First, we consider slightly different regressands. We successively and separately

eliminate: loans purchased by Government-Sponsored Enterprises, loans guaranteed by the FHA,

and refinance loans. The home-district effect remains positive and statistically significant

throughout these perturbations. We then try shorter (2006-2009) and longer (2005-2012) sample

periods. We obtain similar results, though they are economically smaller for the larger window.

Our next checks involve exploring alternative sets of banks and geographies. First, we

include all loans, instead of only those made in tracts contiguous to district borders; this

marginally reduces the economic magnitude of our estimates. We then successively: a) add back

the largest (nineteen) American banks (those who participated in the 2009 stress test), b) drop the

   

24  

top-30 banks (the 2014 CCAR participants) and c) drop all banks headquartered in New York

City. Our results are economically and statistically somewhat smaller, but still significantly

different from zero at the 5% level; our results are not driven by “mega-banks”.

We then check the importance of controls. To account for changes in the observable

quality of applicants across different banks and counties, we replace bank-county-year borrower

controls by comparable bank-county-year applicant controls. This does not materially change

results. Dropping all the bank controls also has little effect on our results. We then explore an

alternative definition of Home, which is unity not only in a BHC’s home district, but also in any

of its subsidiaries’ home districts.41 The resulting home-district effect is essentially unchanged.

Another issue to consider is the importance of outliers; we pursue this in two different

ways. First, we winsorize all variables at the 1% level. Alternatively, we drop outliers, defined

as observations with residuals lying more than two standard deviations from the mean. Our

results remain statistically solid through these checks, but the economic magnitude falls by

around a quarter in the second perturbation. This suggests that our headline economic estimates

are somewhat inflated by observations with extreme lending growth. We then experiment with

standard errors, using state-level clustering. We obtain smaller standard errors, confirming that

bank-clustering is more conservative. Finally, we replace bank-home fixed effects with bank-

county fixed effects; this is of little consequence.42 To summarize our sensitivity analysis: the

home-district effect does not depend on minor features of our sample and model specification.

4.3. Alternative explanations

                                                            41 Our baseline set-up assumes that BHCs (or banks in the case of independent banks) are connected to the representative for the district in which the BHC is headquartered; this alternative definition accounts for the possibility that political connections also exist between BHCs and representatives of the districts in which subsidiaries are headquartered. We make this assumption to conform to the facts that a) TARP funds were granted at the BHC level, and b) connections between a BHC and its home-district representative predict participation in the TARP (Duchin and Sosyura, 2012).

42 The same is true of using bank-district fixed effects, as we did in earlier versions of the paper.

   

25  

Our next set of tests addresses four alternative explanations for the home-district effect:

gerrymandering, credit demand, home bias, and other differences between banks and their

borrowers. Our results are reported in Panel B of Table 2. We first drop all loans granted in the

40 most gerrymandered districts, as identified by Mackenzie (2009) based on their

geographically abnormal shapes. The results change little; gerrymandered districts are not the

source of our finding. 43

Second, we replace county-year with TARP-county-year fixed effects, again finding

comparable results. This suggests that the home-district effect cannot be explained by changes

in average credit demand faced by TARP recipients in their home-district (the application-level

evidence below demonstrates this more directly).

Third, we control for several possible manifestations of home bias. We start by adding a

control Crisis x Home, where Crisis is unity after 2008, and zero otherwise. This allows us to

capture any general retrenchment towards the home district, for instance if banks seek to

strengthen their connection with the home-district representative in a context of impending

regulatory overhaul, irrespective of participation in TARP. The OLS/PSM estimates are

unaffected, and the IV estimates are higher. This suggests that the home-district effect operates

over and above any crisis-induced extra home bias effect.44

Our results could also reflect a home bias specific to TARP participants. TARP banks

might be weaker and thus more prone to cut lending. In turn, weak banks might want to cut

lending first in those markets in which they do not have superior information, like distant

                                                            43 Gerrymandering could bias our results upwards if it increases the sharpness of the discontinuity between politically heterogeneous but economically similar areas. Alternatively, gerrymandering could bias our results downwards if abnormal district shapes make it unlikely that a bank only maintains relationships with the representative of its home district. We have also checked that the home-district effect is not statistically different for the most gerrymandered districts. 44 If we substitute 2007 for 2008, the IV estimates remain essentially unchanged, but the OLS and PSM estimates fall to 0.16 (0.09) and 0.16 (0.07) respectively.

   

26  

counties (Landier et al., 2007; Giannetti and Laeven, 2012) or quantitatively less important

counties. This could bias our results if these “core” counties also lie within banks’ home district.

We explore this TARP-specific home-bias in three ways. First, we add a control “Close

to Headquarter” which is one if the distance between a given county and the county where the

bank is headquartered is smaller or equal to the 5th percentile for a given bank-year, and zero

otherwise.45 We then interact this control with TARP. The economic size of the home-district

effect diminishes somewhat, but our key conclusion is unchanged. Second, we add a dummy

“Home County” – unity in the county where a bank is headquartered, and 0 elsewhere. Unlike

congressional districts, counties do not delineate areas with obvious differential exposure to

federal politics. Thus, TARP recipients should not face any political incentive to increase

lending in their home county, other than because of its overlap with the home district. But if our

results are driven by distance rather than by political factors, the home-county border could

matter. In that case, adding this control should reduce the size of the home-district effect. The

results suggest otherwise; the economic magnitude of TARP x Home changes little.

Banks might be headquartered in richer, urban areas; markets close to headquarters might

also account for a bigger share of the bank’s business. So yet another form of home bias is that

weak banks could cut lending more in poorer, rural or smaller markets, and less in richer, urban

or bigger markets they know better. We thus first control for “Rich County” (and its interaction

with TARP) – unity if county borrower income is above the bank-year median, and zero

otherwise. We then control for “County Importance” – the percentage of a bank’s total lending

in a given county before TARP (2006-2007), and interact it with TARP. Adding these two

controls separately does not change our results.46 We then run the baseline regression separately

                                                            45 Results are unchanged when we use the 10th, 15th, 20th and 25th percentile instead. 46 We find comparable (unreported) results when alternatively controlling for the market share of a bank in a given county before TARP (2006-2007), and its interaction with TARP. This indicates that our main result is not explained by a “flight” of TARP banks towards markets where they have a dominant position.

   

27  

for a) rural counties (counties in a single district) and b) urban counties (counties spanning

multiple districts). The home-district effect remains significant in both samples, with only minor

differences in statistical and economic significance.

Together, these tests indicate that the home-district effect is not explained by home-

district credit demand, or by a reluctance to cut lending in closer, richer or bigger markets.

One final challenge is that TARP and non-TARP banks could differ along finer

dimensions than their overall propensity to participate (as controlled for in our baseline PSM),

for instance their capitalization; home and non-home districts could also differ along other

dimensions than political ones, for instance their affluence. Given our difference-in-difference-

in-difference approach, both these challenges should hold at the same time to bias our results. In

Appendix A3, we confirm that our main result is similar when matching participants and non-

participants based on every individual bank and borrower characteristics in our sample, and

when adding a range of additional TARP x County characteristic controls.

4.4. Placebo Test

We also add a placebo test, in which we falsify the timing of the shock. We assume that

the TARP recipients receive an equity injection three years before the actual date; we then

estimate the baseline regression for the 2003-2007 period. The home-district coefficient is

economically and statistically insignificant for all estimators; this suggests that our main result is

not driven by different pre-shock trends across recipients and non-recipients.47

4.5. Application-level Evidence

                                                            47 We reached a qualitatively similar conclusion in the 2016 NBER working paper version of this study, but we had found different coefficients as a result of inadvertently leaving the top-19 banks inside the sample.

   

28  

As a final check on our identification strategy, we exploit our mortgage data at the most

disaggregated level, that of the individual mortgage application. We estimate the model:

Acceptedi,a,c,t = βTTARPi,t + βTHTARPi,t∙Homei,c + δXi,t + ζZi,a,c,t + {ηc,t} + {θi,c} + εi,a,c,t (3)

where:

Acceptedi,a,c,t is 1 if bank i accepts application a in census tract c and year t, and 0 otherwise,

Bank controls, borrower controls and the bank-home fixed effect θi,c are similar to the

baseline model,48 and

The location-time fixed effects are discussed below.

The application-level analysis gives a distorted picture of the average home-district

effect, since it a) overweighs large banks and areas and b) only captures changes in acceptance

rates, not lending volume. If a TARP recipient aggressively solicited applications (in line with

anecdotal evidence in section 2) or used its funding advantage to outbid its competitors without

increasing risk-taking, this model would not capture it.

However, this approach has two benefits. First, we can estimate the differential effect of

the TARP a) within a given neighborhood and year (via census tract-year fixed effects) and b)

across a pair of neighborhoods located on either side of an intrastate district border (via census

tract pair-year fixed effects). Second, since it models a mortgage supply decision conditional on

a given mortgage demand, this approach removes unobservable individual demand-side effects.

Together, these can help us gauge the robustness of our identification strategy.

We use two alternative sets of fixed effects. First, we replace the county-year fixed

effects (used in the baseline model) with census tract-year fixed effects (henceforth, “within-tract

                                                            48 A minor difference is that borrower controls appear at the borrower level rather than as a bank-county-year average as in the baseline regression. Specifically, Z includes: loan-to-income, log loan size, log income, and binary variables for borrowers that are black, Latino and non-male. We do not include the tract-level borrower controls used in the baseline regression since they are picked up by the tract-year fixed effects.

   

29  

model”). This controls for credit demand and unobservable borrower quality in a neighborhood,

period by period. Combined with the alternative dependent variable, this approach is the most

conservative way to control for demand factors feasible using HMDA data.

Second, we retain tract-year fixed effects, but replace the bank-home fixed effects (of the

baseline set-up) with bank-census pair fixed effects (henceforth, “across census pairs model”).

This allows us to control for unobserved heterogeneity in the way a given bank behaves on

average within a pair of two census tracts located on either side of an intrastate district border.49

Given the extensive potential number of observations and fixed effects, we drop loans

which play no role in our baseline results according to our robustness checks (see Table 2),

namely loan purchased by GSEs, loans guaranteed by the FHA and refinance loans.50 We do not

report IV estimates since they often fail to converge, given the large number of fixed effects.51

The results in Table 3 indicate a positive and strongly significant coefficient for TARP x

Home. This is true for both OLS and PSM estimates, and for both models (within census and

across census pairs). For instance, the OLS estimate of the within-tract model (column 1)

indicates that, controlling for his/her characteristics, an applicant’s chance to be accepted is 4%

higher if he/she applies with a TARP recipient, and his/her house is located in the bank’s home

district. We find comparable estimates in the other three columns. In contrast, the coefficient

for TARP is always negative but statistically insignificant, indicating that borrowers are treated

insignificantly different outside a TARP bank’s home district. We conclude that at least a

                                                            49 Since they vary in size and shape, a majority of census tract can be paired with multiple census tracts on the other side of the border (2.3 on average). Thus, a given observation must be included several times in some cases for this model to be identified; specifically, applications must appear once for each possible pair they can be attributed to. For instance, an application from a tract that can be matched to three different tracts on the other side of the border must be included three times in the dataset. 50 This also allows us to focus on applications for which banks have the greatest margin of discretion. In particular, GSE loans are typically underwritten automatically using the GSEs’ own software and standardized data, leaving little discretion for alternative considerations (such as political ones) to be factored into screening decisions. Refinancing loans also leave less discretion to banks, since the ability to observe the applicant’s payment history reduces contracting frictions (Gilje et al., 2016). 51 Since non-linear models are biased in the presence of high-dimensional fixed effects, we estimate the application-level model via OLS despite the binary dependent variable (Puri et al., 2011; Duchin and Sosyura, 2014).

   

30  

portion of the home-district effect can be ascribed to TARP recipients’ willingness to accept

applications from their home district disproportionately.

4.6. External Validity: Small Business Lending

Our focus on the mortgage market is partly motivated by data considerations. The

HMDA is the only comprehensive database containing precise information on the geographic

location of borrowers. In principle however, there is no reason why the home-district effect

should not hold for other markets, such as those for commercial and industrial lending. Banks

are the single most important source of credit for small firms, and recipients’ small business

lending was an important focal point of TARP surveillance bodies such as the Congressional

Oversight Panel, as well as media discussions around credit supply after the crisis and TARP.52

Such concerns may well have opened the door to political influences similar to those at work in

the case of mortgage lending.

Accordingly, we investigate the home-district effect in the small business lending market.

We use a panel of small business loans for the 2006-2010 period collected under the auspices of

the Community Reinvestment Act (CRA). The CRA dataset has two main disadvantages

compared with the HMDA database. First, although a majority of American banks file CRA

reports, participation is voluntary. Second, the publicly-accessible version of CRA aggregates

lending to the bank-county-year level, where HMDA reports application-level data. This has

two implications for our methodology. First, one cannot explicitly control for borrower

characteristics (the vector Z), at least beyond those captured by a county-year fixed effect.

Second, we cannot zoom onto loans within a given county granted in census tracts contiguous to

district borders. Instead, we focus on counties which are contiguous to congressional district

borders, within the same state. Note that since urban counties often have multiple districts, this                                                             52 See e.g. Congressional Oversight Panel (2010), “The Small Business Credit Crunch and the Impact of the TARP”. Available for download from www.gpo.gov.

   

31  

implies that the sample in this regression is biased towards rural areas. With those exceptions,

our empirical model is the same as that of our baseline model (1).

Table 4 reports OLS, IV, and PSM results for small business lending analogous to those

of Table 1. We find similar results to the mortgage regressions. The coefficient for the home-

district effect ranges from 0.21 (PSM) to 0.48 (IV). As expected from the poorer data quality

and identification, the precision of the effect is lower than with mortgages. The OLS estimate is

significantly different from zero only at the 10% level, though the others are significant at the

5% level. The TARP coefficient is never significantly different from zero in any of the

equations. In other words, the TARP has no significantly discernable effect on small business

lending except inside the recipients’ home-representative congressional district.

These results provide an independent check for our mortgage results; the fact that we find

qualitatively and quantitatively similar results with a different dataset suggests that the home-

district effect is robust to idiosyncrasies associated with the mortgage market or HMDA data.

5. Variation across time, banks, and politicians, and aggregate and electoral effects

We have established the existence of a “home-district” effect; recipients of public capital

injections have higher lending growth inside their home-representative’s congressional district

than outside. That is, the nature of mortgage and small business lending by TARP recipients

appears to have been influenced by political considerations. In this section, we provide

additional evidence to supplement and strengthen our interpretation.

The political economy literature and anecdotal evidence surveyed in section 2 suggest

two possible reasons for our findings. First, recipients might want to (or be compelled to)

reciprocate a “favor” provided by their home representative. This can include direct help in

entering or exiting the program, as well as other congressional actions before and after the

   

32  

inception of funds which are particularly beneficial to a participant.53 Second, recipients might

seek to preempt political interference. Access to public funds attracts political and media

scrutiny on banks. Evidence in section 2 suggests that a) politicians could use platforms like

Congressional hearings to pressure participants, and b) participants could use evidence of

lending in key areas to counter (or pre-empt) criticisms on their lending behavior.  

These mechanisms are neither observable, nor mutually exclusive; we thus do not attempt

to disentangle them.54 Instead, we explore predictions consistent with either channel.

Specifically, our key interest is to test whether the home-district effect is stronger in periods,

banks and politicians where the scope or motive for political intervention and/or the incentive of

the bank to be responsive to political influences (or the threat thereof) is higher. Panel C in

Table A3 reports summary statistics for the proxies used to test these predictions.

5.1. Timing

We start by investigating whether the timing of the home-district effect coincides with

periods during which politicians have the greatest scope to intervene, and banks are most liable

or vulnerable to interference. We explore two proxies. First, political influences should be

stronger around the capital injection time. We thus create three separate dummies TARPt,

TARPt+1 and TARPt+2 , which are, respectively, unity during the year the bank enters the TARP,

one year after, and two years after, and zero otherwise. We then interact these dummies with

Home. We find that TARPt x Home and TARPt+1 x Home are significant at 1% confidence level

and of comparable economic size. (The sum of these two coefficients is reported in column 1 of

                                                            53 For instance, the Washington Post reports that “Rep. Barney Frank (D-Mass.) … wrote language into the bailout bill that effectively directed the Treasury to give special consideration to [Massachusetts bank] OneUnited, and he followed up with a call to Treasury. The bank got $12 million.” http://www.washingtonpost.com/wp-dyn/content/article/2009/07/01/ AR2009070103694.html 54 It would be conceptually useful to distinguish between them since the second mechanism suggests that political influences can bind even without explicit politician interference. But given their substantial observational overlap, we do not believe to have sufficiently precise data to cleanly separate these two arguments in the data.

   

33  

Table 5). But TARPt+2 is insignificant. Consistent with intuition, the home-district effect is thus

concentrated around the injection date.

Second, political influences should be stronger as long as the bank holds TARP funds,

and its home representative at the start of the program is in office. We thus create a dummy

“Exit” (and its interaction with Home) – unity if a bank has repaid TARP funds, or its 2008

home representative is no longer in office after the November 2008 elections, and zero

otherwise. The results tabulated in column 2 of Table 5 show that the home-district effect

reverses once the recipient’s relationship ceases to either the TARP or the bank’s original home

representative. TARP x Home x Exit is negative and significant; this suggests that TARP

recipients decrease home-district credit growth when this relationship ceases.55

5.2. Bank characteristics

We have established that the timing of the home-district effect coincides with periods of

greatest possibility of political influence. We now explore whether the effect is also stronger for

those banks with more scope for such influence, or a bigger incentive to respond to it.

We consider two proxies. First, anecdotal evidence suggests that applicant banks helped

by politicians access TARP during the first round of the distribution of CCP funds. The Wall

Street Journal first reports about political interference on 22 January 2009; five days later,

Treasury Secretary Geithner announces rules to prevent lobbying on behalf of applicants. This

should restrict the scope for political interference during the two next application rounds.56 

                                                            55 In contrast, TARP x Exit is positive and significant; recipients increase lending growth out of their home district once they are no longer liable. This reversal is only partial. The decrease in home-district credit growth when the relationship to TARP or the initial representative terminates is -0.12 (≈0.40+0.28), against +0.28 when the relationship is still going on. 56 http://www.nytimes.com/2009/01/28/business/economy/28lobby.html. The first application window opened from October 14 to November 14, 2008. In January 14, application was opened again for a month to qualifying S-corporations. Finally, a third application window was opened on 13 May, 2009 for banks with total assets below 500 Million (Millon Cornett et al., 2013).

   

34  

To explore application timing while avoiding endogeneity issues, we exploit two aspects

of bank organizational structure. Specifically, the first application round was opened only to

public banks. One reason is that many privately held banks are organized as “Corporation S”, a

type of firms which can only have one class of shareholders. The Treasury was thus initially

unable to purchase preferred stock in these banks as foreseen by the terms of the TARP. We

thus construct a dummy “Eligible for 1st round” – unity if a bank is a) publicly traded and b) not

a Corporation S, and zero otherwise. The results tabulated in column 3 of Table 5 show that the

interaction of Eligible and TARP x Home is positive and significant. In other words, the home-

district effect is higher for potential first-round recipients, in line with our intuition.  

Our second proxy explores the role of bank risk. The TARP was not intended as a

bailout of unhealthy banks. Bayazitova and Shivdasani (2012) and Duchin and Sosyura (2012)

confirm that riskier applicants were less likely to be accepted. Specifically, the finding common

to both studies is that banks with greater funding risk are less likely to be accepted. We thus

create a proxy “Deposit-to-asset ratio” measured as the share of bank total assets in the form of

deposits in 2008q3. The results in column 4 show that the interaction of Deposit-to-asset ratio

and TARP x Home is negative and significant. This suggests that participants that were less

likely to be accepted are more subject or responsive to political influences or the threat thereof.57  

5.3. Politician characteristics

We have established that the home-district effect coincides with the periods and banks

most susceptible to political interference. We now explore whether the effect also changes with

proxies for politicians willingness and ability to help banks as part of TARP, or more generally. 

                                                            57 We find qualitatively similar results when using the share of undrawn lending commitments to total assets as alternative measure of liquidity risk (Millon Cornett et al., 2013). Bayazitova and Shivdasani (2012) and Duchin and Sosyura (2012) also investigate the role of solvency risk as measured by bank capitalisation, but do not find any significant effect on acceptation. In unreported results, we similarly find that pre-TARP capitalisation does not change the home-district effect.

   

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We consider three proxies of the willingness of politicians to help banks. We begin by

investigating the role of TARP votes in Congress. Most representatives featured in anecdotal

evidence in section 2 were TARP supporters. We assume that intervening in favor of applicants

or pressurizing participants to lend is less costly for TARP supporters. More broadly, the TARP

vote provides an indicator of revealed preferences to help banks, as it was largely determined by

a representative’s proximity to the financial industry (Mian et al., 2010).58 Finally, the TARP

vote was tight; individual politicians seeking to help firms can thus make a difference (Cohen

and Malloy, 2014).59

Accordingly, we re-estimate baseline model (1), additionally controlling for the dummy

“TARP supporter” – one for banks whose home representative supported the TARP, and zero

otherwise. Our main coefficient of interest is the term TARP x Home x TARP supporter; this

captures how the home-district effect changes with the vote. Column 5 in Table 5 shows that the

home-district effect increases significantly with a ‘yes’ vote. Specifically, the home-district

effect is 0.34 (≈0.38-0.04) for ‘yes’-vote banks, against -0.04 for ‘no’-vote banks. In other

words, political considerations seem to only influence recipients’ lending if its representative’s

vote aligns with bank special interests.60

As a second proxy for politicians’ willingness to help banks, we consider contributions

received from the financial industry. Politicians receiving more contributions are more prone to

cater to banks’ special interests in Congress, and thus represent a potentially more valuable

connection in a context of crisis and regulatory overhaul. Accordingly, we use Mian et al.

                                                            58 In contrast, the TARP vote does not correlate with mortgage defaults in the representative’s district. 59 The Emergency Economic Stabilization Act (EESA), the legislation that created the TARP, was voted down 205-228 on Sept 29, 2008 before being voted through 263-171 on Oct 3, 2008. We focus on the latter vote in the tests below. 60 We also tested whether the home-district effect is stronger if the representative had voted for the 2008 American Housing Rescue and Foreclosure Prevention Act (AHRFPA), a federal program supporting mortgage renegotiations and GSEs. Unlike the EESA, the AHRFPA targeted constituent interests (those of underwater mortgagors), rather than those of the financial industry (Mian et al., 2010). In unreported results, we found that TARP x Home x AHRFPA supporter is statistically insignificant. The home-district effect thus does not seem to vary with votes on objects benefiting constituent interests rather than those of banks.

   

36  

(2010)’s database to construct a variable “Financial contributions” which corresponds to the

(log) amount received by a bank’s representative up to November 2008 from a Political Action

Committee affiliated to the financial industry, as measured by the Center for Responsive

Politics.61 The interaction of Financial contributions with TARP x Home captures whether the

home-district effect increases with the home-representative’s connection to the financial

industry. Our result is tabulated in column 6 of Table 5. Consistent with our intuition, we find

that the triple interaction term of interest is positive and significant at the 5% confidence level.62

Third, a politician’s willingness to help a bank should also increase with the importance

of the bank for its district. Cohen et al. (2013) show that politicians are more prone to cater to a

firm’s interests if it can have a sizable impact on economic activity in his/her district. We thus

create a variable “District market share” which is the bank’s share of mortgage origination in its

home district before TARP (2006-2007). The results in column 7 of Table 5 confirm our prior:

the home-district effect increases significantly with the home-district market share. Specifically,

the estimate for the TARP x Home x District market share interaction (2.03) suggests that the

home-district effect is 0.23 for a bank with an average market share (9%) and increases to 0.52

when the market share increases by one standard deviation (14%).

Finally, we explore the ability of politicians to help or pressure firms. To do so, we

consider membership in key committees (Duchin and Sosyura, 2012; Agarwal et al., 2016; Akey

et al., 2016). Powerful politicians have more sway in Congress and, presumably, over

government. They were thus in a good position to help applicants at the start of the program, and

to influence key legislation affecting the terms of TARP after it had been launched. Table A6

shows that one committee of the 110th Congress worked on bills related to TARP, and another

                                                            61 We remove banks whose representative was not re-elected in 2008 from the sample for this regression since we do not have contributions data for newly elected representatives. We do the same for the TARP supporter test for a similar reason. 62 We find comparable economic and statistical significance when running this regression in a subsample of banks whose representative supported the TARP. Political contributions thus matter independently of their effect on the TARP vote.

   

37  

three in the 111th Congress. We thus create a dummy “Powerful politician” which is one for a

bank whose home representative sat on one of these committees during the corresponding period.

Column 8 in Table 5 shows that the interaction of this dummy with TARP x Home is positive

and significant. Specifically, the home-district effect is 0.39 (≈0.31+0.08) for participants with a

powerful home representative, against 0.09 for other participants. Political considerations thus

seem substantially stronger for banks connected to a powerful politician.63

Together, these results reinforce the interpretation that political influences (or the threat

thereof) influence lending decisions in periods, banks and politicians where the scope or motive

for political interference and the incentive on the part of the bank to respond to them or pre-empt

them is higher. The evidence presented in this section is supplemental, not definitive. Still, it is

consistent with the notion of a reciprocal political channel that steers mortgage growth after the

TARP towards areas within the district borders of the bank’s congressional representative.

5.4. Aggregate and electoral effects

Thus far, our tests use only parts of the available data, split across counties and banks for

cleaner identification; this raises a question of whether the home-district effect matters in the

aggregate for politicians, their constituents and TARP participants, as our interpretation

implicitly suggests. In the appendix section A4, we provide three results supportive of this

notion. First, districts in which locally headquartered TARP participants have a 10% higher

market share experience 4.2% higher growth in total lending after TARP. Second, improved

lending conditions go along with improved electoral prospects for incumbents during the 2010

House of Representatives elections, with a magnitude close to the effect of higher federal

spending in a district for incumbent vote percentage (Levitt and Snyder, 1997). Finally, TARP

                                                            63 Politicians’ attempt to join key 111th Congress committees could be correlated with banks in their home district participating in TARP. To rule out this possibility, we re-estimated this regression assuming that Powerful representative is 1 only for a representative who already sits in a key committee in the 110th Congress. We find similar results (available upon request).

   

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participants with a higher share of home-district mortgages in their overall loan portfolio

experience more non-performing loans after TARP. Aggregating data necessarily reduces

statistical power and identification precision, so we interpret magnitudes with caution. But at

face value, these results support the hypothesis that the home-district effect matters in aggregate

for politicians, constituents, and banks.

6. Conclusion

Government-funded programs are necessarily shaped and approved by parliaments, and

allocated discretionarily by public bodies. This leaves scope to politicians to influence the

availability and terms of funds to firms they are connected to. In this paper, we have examined

the consequences of a large political intervention for the allocation of corporate investment

across political constituencies. We have documented the existence of a “home-district effect”;

banks that received capital from the Troubled Asset Relief Program (TARP) lent 23%-60% more

in their home-representative’s congressional district than elsewhere. We have also provided

evidence that suggests that this higher lending improved the electoral prospects of incumbents

while also reducing the quality of banks’ mortgage portfolios.

The key contribution of these findings is to document evidence that investment decisions

by beneficiaries of government funds are subject to political influences. Our findings also show

that political forces matter despite the maturity of the American political and financial systems

and the absence of formal channels for politicians to influence bank lending decisions.64 Of

course, we do not know whether our result is general, or an idiosyncratic result of an exceptional

                                                            64 Members of key Congress committees obtain bank loans at preferential terms (Tahoun and Vasvari, 2016). Collusion between politicians and local banks have contributed to the long-standing regional fragmentation of the American banking system (Kroszner and Strahan, 1999), and to limits on access to credit in early 20th Century America (Rajan and Ramcharan, 2011).

   

39  

financial intervention during a financial crisis. Other government funding programs like

procurement contracts may constitute insightful laboratories for further research.

From a policy perspective, our results bear on discussions around newly created cross-

border bank funding and resolution arrangements such as the European Stability Mechanism

(ESM). Our results suggest that conflicting local interests may steer the impact of bailout

programs, even in areas as politically and financially integrated as the United States. This

suggests that international mechanisms may find it even more difficult to mute conflicting

national interests over bailouts and the associated impact on credit supply.

Our study also adds to the debate concerning the causes of the credit fragmentation that

followed the global financial crisis (e.g., Giannetti and Laeven, 2012). We do not explicitly

search for evidence of aggregate post-crisis financial fragmentation in the United States.

Nevertheless, our results are consistent with the hypothesis that financial fragmentation can

result from “financial protectionism,” that is, a distortion of credit flows towards the local

economy after large government intervention in the financial sector (Rose and Wieladek, 2014).

   

40  

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TABLE 1: Baseline Estimates of Home-district Effect: Effect of TARP participation on home-district mortgage lending

(1) (2) (3) (4) OLS IV (1) IV (2) Propensity

Score Matching

Stage 0 instrument: Fed director Subcommittee member

TARP x Home (βT) 0.22** 0.47** 0.46** 0.21** (0.07) (0.14) (0.13) (0.06) TARP (βTH) -0.05 -0.38** -0.39** -0.13 (0.09) (0.15) (0.16) (0.07) Observations 93,671 93,671 93,671 44,553 Adjusted R2 0.40 0.39 0.39 0.44 Kleibergen-Paap statistic 42.07 37.23 TARP x Home + TARP 0.18 0.09 0.06 0.09 (p-value) (0.00) (0.51) (0.65) (0.135)

Coefficients, with standard errors (clustered by bank-holding company) in parentheses; one (two) asterisk(s) indicates significantly different from zero at .05 (.01) level. Regressand is first difference in log mortgage lending for bank-county-year. Columns correspond to different estimators. Annual American data 2006-2010, for all loans given to census tracts adjacent to a within-state congressional district border. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants. TARP is one if bank participates in TARP, zero otherwise; Home is one if county is inside congressional district for bank headquarters. Bank-year controls included but not recorded: log total assets; tier-1 capital (%Total Assets); cash (%TA); charge-offs(%TA); non-performing loans(%TA); repossessed real estate(%TA); deposits(%TA); (log) bank age; return on equity; and exposure to local shocks. Bank-county-borrower controls included but not recorded: log income; loan-to-income; log loan size; non-white dummy; non-male dummy; tract median income. Bank-home and county-year fixed effects included but not recorded.

   

45  

TABLE 2: Sensitivity analysis for TARP x Home (βTH)

OLS IV (1) IV (2) PSM Obs. Instrument: Fed director Subcom.

member

Default 0.22** 0.47** 0.46** 0.21** 93,671

(0.07) (0.14) (0.13) (0.06)

Panel A: Sample and model specification

Drop GSE-purchased 0.19** 0.39** 0.37** 0.19** 84,406 Loans (0.07) (0.13) (0.13) (0.06)

Drop FHA- 0.23** 0.49** 0.47** 0.22** 90,931 guaranteed Loans (0.08) (0.14) (0.14) (0.07)

Drop refinance 0.25** 0.30* 0.27* 0.20** 65,793 Loans (0.09) (0.12) (0.12) (0.07) 2006-2009 0.27** 0.62** 0.60** 0.24** 73,354 (0.08) (0.16) (0.15) (0.07) 2005-2012 0.15* 0.40** 0.40** 0.14** 130,033 (0.06) (0.11) (0.11) (0.04)

Keep loans in all census tracts

0.21** 0.52** 0.49** 0.17** 220,192 (0.07) (0.15) (0.15) (0.06)

Keep all banks

0.16* 0.26* 0.26* 0.21** 133,629 (0.08) (0.10) (0.10) (0.06)

Drop top-30 banks 0.19* 0.62** 0.61** 0.14* 82,165 (0.08) (0.23) (0.23) (0.05)

Drop New York City-headquartered banks

0.15* 0.50** 0.48** 0.12* 82,962 (0.07) (0.19) (0.18) (0.05)

Applicant Controls

0.21** 0.46** 0.44** 0.21** 93,671 (0.08) (0.14) (0.13) (0.07)

No Bank Controls

0.28* 0.43** 0.42** 0.30** 93,671 (0.12) (0.14) (0.13) (0.11)

Home also subsidiary headquarter

0.24** 0.53** 0.51** 0.19** 93,671 (0.08) (0.15) (0.14) (0.06)

1% Winsorizing

0.21** 0.45** 0.43** 0.21** 93,671 (0.07) (0.13) (0.12) (0.06)

Drop >2 Std Err Residuals

0.16** 0.32** 0.31** 0.15** 89,286 (0.06) (0.10) (0.10) (0.05)

   

   

46  

Table 2 (continued)

State 0.22** 0.47** 0.46** 0.21** 93,671 clustering (0.04) (0.08) (0.08) (0.04)

Bank-County fixed effect

0.24* 0.47** 0.46** 0.23** 93,671 (0.10) (0.14) (0.14) (0.08)

Panel B: Alternative explanations

Drop gerrymandered districts

0.22** 0.49** 0.48** 0.22** 88,388 (0.08) (0.14) (0.14) (0.07)

County-Year-TARP fixed effects

0.17** 0.75** 0.74** 0.20** 93,671 (0.06) (0.28) (0.28) (0.07)

Control for Post-2008 x Home

0.24** 0.72** 0.70** 0.23** 93,671 (0.08) (0.20) (0.20) (0.09)

Control for TARP x Close to Headquarter

0.18** 0.38** 0.36** 0.17** 93,671 (0.07) (0.13) (0.12) (0.06)

Control for TARP x Home-County

0.20** 0.42** 0.41** 0.20** 93,671 (0.09) (0.12) (0.12) (.08)

Control for TARP x County Importance

0.25** 0.40** 0.40** 0.24** 72,928 (0.06) (0.13) (0.13) (0.05)

Control for TARP x Rich County

0.22** 0.45** 0.43** 0.21** 93,671 (0.07) (0.13) (0.13) (0.06)

Rural (single-district) counties only

0.19* 0.51** 0.49** 0.19* 53,959 (0.08) (0.15) (0.15) (0.08)

Urban (multiple-district) counties only

0.25** 0.39** 0.38* 0.23** 39,712 (0.09) (0.15) (0.15) (0.08)

Panel C: Placebo test

Placebo -0.03 -0.05 -0.07 0.09 74,888 (wrong timing) (0.08) (0.09) (0.10) (.10)

Coefficients, with standard errors (clustered by bank-holding company) in parentheses; one (two) asterisk(s) indicates significantly different from zero at .05 (.01) level. Regressand is first difference in log mortgage lending for bank-county-year. Columns correspond to estimators; rows correspond to perturbations of benchmark methodology. “Obs.” is the number of observations in the OLS regression. American data 2006-2010 unless marked, for all loans given to census tracts adjacent to a within-state congressional district border. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants. TARP is one if bank participates in TARP, zero otherwise; Home is one if county is inside congressional district for bank headquarters. Bank-year controls included but not recorded: TARP dummy; log total assets; tier-1 capital (%Total Assets); cash (%TA); charge-offs(%TA); non-performing loans (%TA); repossessed real estate(%TA); deposits(%TA); (log) bank age; return on equity; and exposure to local shocks. Bank-county-borrower controls included but not recorded: log income; log loan size; loan-to-income non-white dummy; non-male dummy; tract median income. Bank-home and county-year fixed effects included but not recorded.

   

47  

TABLE 3: Application-level evidence for the home-district effect of TARP participation on mortgage lending (1) (2) (1) (2) OLS Propensity

Score Matching

OLS Propensity Score

Matching Model: Within census tracts Across census pairs TARP x Home 0.04** 0.04** 0.03** 0.03** (0.01) (0.01) (0.01) (0.01) TARP -0.03 -0.01 -0.02 -0.01 (0.02) (0.02) (0.01) (0.02) Fixed effects: Tract-Year Yes Yes Yes Yes Bank-Home Yes Yes Bank-Pair Yes Yes Observations 767,397 439,774 1,632,856 927,653 Adjusted R2 0.23 0.26 0.33 0.33

Coefficients, with standard errors (clustered by bank-holding company) in parentheses; one (two) asterisk(s) indicates significantly different from zero at .05 (.01) level. Regressand is one if mortgage application accepted, zero otherwise. Annual American data 2006-2010, for all loan applications received in counties adjacent to a within-state congressional district border, except loans sold to GSEs, loans guaranteed by the FHA and refinancing loans. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants. TARP is one if bank participates in TARP, zero otherwise; Home is one if county is inside congressional district for bank headquarters. Bank-year controls included but not recorded: log total assets; tier-1 capital (%Total Assets); cash (%TA); charge-offs(%TA); non-performing loans(%TA); repossessed real estate(%TA); deposits(%TA); (log) bank age; return on equity; and exposure to local shocks. Applicant controls included but not recorded: log income; loan-to-income; log loan size; Latino dummy; black dummy; non-male dummy.

   

48  

TABLE 4: Home-district effect of TARP participation on small business lending

(1) (2) (3) (4) OLS IV (1) IV (2) Propensity

Score Matching

Stage 0 instrument: Fed director Subcommittee member

TARP x Home 0.26 0.48* 0.50* 0.21* (0.14) (0.21) (0.22) (0.10) TARP 0.05 -0.34 -0.27 0.03 (0.16) (0.21) (0.22) (0.09) Observations 43,019 42,896 42,896 25,868 Adjusted R2 0.25 0.03 0.03 0.28

Coefficients, with standard errors (clustered by bank-holding company) in parentheses; one (two) asterisk(s) indicates significantly different from zero at .05 (.01) level. Regressand is small business lending (log) growth. Annual American data 2006-2010, includes all loans given out in counties adjacent to a within-state congressional district border. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants. TARP is one if bank participates in TARP, zero otherwise; Home is one if county is inside congressional district for bank headquarters. Bank-year controls included but not recorded: log total assets; tier-1 capital (%Total Assets); cash (%TA); charge-offs(%TA); non-performing loans(%TA); repossessed real estate(%TA); deposits(%TA); (log) bank age; return on equity; and exposure to local shocks. Bank-home and county-year fixed effects included but not recorded.

   

49  

TABLE 5: Variation of the “Home-district” effect across time, banks, and politicians

Coefficients, with standard errors (clustered by bank-holding company) in parentheses; one (two) asterisk(s) indicates significantly different from zero at .05 (.01) level. Regressand is first difference in log mortgage lending for bank-county-year; each column represents a different regression. Annual American data 2006-2010, for all loans given to census tracts adjacent to a within-state congressional district border. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants. TARP is one if bank participates in TARP, zero otherwise; Home is one if county is inside congressional district for bank headquarters. In column 1 (Around injection), TARP is the sum of the coefficients for TARPt (1 the year the bank receives TARP, 0 otherwise) and TARPt+1 (1 the year after the bank receives TARP, 0 otherwise), and TARP x Home is the sum of TARPt x Home and TARPt+1 x Home; TARPt+2 and TARPt+2 x Home included but not reported. Exit is 1 if the bank’s representative was not re-elected in the November 2008 congressional election or if the bank has reimbursed TARP funds, and 0 otherwise. Eligible for 1st round is 1 if the bank is a public, non-Corporation S bank, and 0 otherwise. Deposit-to-asset ratio is the bank’s deposit funding as percentage of total assets as of 2008q3. TARP supporter is 1 if a bank’s home representative voted in favor of EESA in Congress (October 2nd 2008 roll call), and 0 otherwise. Financial contributions is log contributions made by financial industry to 110th Congress home representative (up to November 2008). District market share is the bank’s share of total mortgage lending in its home district in 2006-2007. Powerful politician is 1 in 2008 if a bank’s home representative is member of the 110th Congress House financial committee; 1 after 2008 if the representative is member of 111th Congress House financial, ways and means, judicial or oversight and government reform committees; and 0 otherwise. Bank-year controls included but not recorded: log total assets; tier-1 capital (%Total Assets); cash (%TA); charge-offs(%TA); non-performing loans(%TA); repossessed real estate(%TA); deposits(%TA); (log) bank age; return on equity; and exposure to local shocks. Bank-county-borrower controls included but not recorded: log income; loan-to-income; log loan size; non-white dummy; non-male dummy; tract median income. Bank-home and county-year fixed effects included but not recorded.

(1) (2) (3) (4) (5) (6) (7) (8) Timing Bank characteristics Politician characteristics Interaction: Around

injection Exit Eligible

for 1st round

Deposit-to-asset

ratio

TARP supporter

Financial Contributions

District market share

Powerful Politician

TARP x Home 0.63** 0.28** 0.03 1.80* -0.04 -0.65* 0.05 0.08 (0.22) (0.08) (0.07) (0.82) (0.09) (0.33) (0.07) (0.05) TARP -.39 -0.12 0.06 -1.38** 0.25* 1.08** 0.06 0.07 (0.24) (0.09) (0.08) (0.50) (0.12) (0.33) (0.08) (0.07) TARP x Home x Interaction

-0.40* 0.32* -2.34* 0.38* 0.08* 2.03** 0.31* (0.16) (0.14) (1.10) (0.16) (0.03) (0.75) (0.14)

TARP x Interaction 0.49** -0.15 2.04** -0.41** -0.010** -0.78** -0.26* (0.15) (0.10) (0.71) (0.15) (0.03) (0.15) (0.12)

Observations 93,671 93,671 93,671 93,671 82,984 82,774 86,723 93,671 Adjusted R2 0.39 0.39 0.39 0.39 0.40 0.40 0.39 0.39

   

50  

FIGURE 1: Oklahoma State county and congressional district borders. Thick black lines delineate 110th Congress district borders; thin gray lines delineate county borders. Colored counties contain census tracts contiguous to an intrastate congressional district border. Each color corresponds to a different congressional district; circled numbers indicate district identifiers. Oklahoma County is highlighted in red (see Figure 2 below for a detailed view). Authors’ illustration based on an original map from the Census Bureau.

   

51  

FIGURE 2: Oklahoma County census tracts. The top panel shows all the 2000 census tracts of Oklahoma County. Thin red or gray lines delineate census tract borders. Thick black lines delineate 110th Congress district borders. Colored census tracts are contiguous to an intrastate congressional district border. Each color corresponds to a different district; circled numbers indicate district identifiers. The bottom panel shows the location of Oklahoma County (in red) in the State of Oklahoma. Thin gray lines indicate county borders; thick black lines indicate 110th Congressional district borders. Authors’ illustration based on original maps from the Census Bureau.

   

52  

Appendix A1: Impact of Discontinuity Strategy on the Sample

The key idea of the discontinuity component of our identification strategy is to

include in the benchmark sample only mortgages given in census tracts adjacent to an

intrastate congressional district border. This section discusses how this approach changes the

sample compared to the full sample obtained when using all data.

Panel A in Table A1 shows that 12,007 of the 65,310 American census tracts are

contiguous to an intrastate district border; 81.6% of tracts are thus left out of the benchmark

sample. But since we collapse data by bank-county-year, the loss of observations compared

to the sample obtain when collapsing the full sample is proportionately smaller.65 Panel B of

Table A1 illustrates this fact; the benchmark has 93,671 bank-county-year observations,

against 219,072 for the full sample.

The difference between the two samples reflects two sources of data loss. First, we

drop data from all counties that have no contiguous tract whatsoever, such as the non-shaded

Oklahoma counties in Figure 1. Only 2,141 of 3,636 American counties (59%) contain at

least one contiguous tract and are thus included in the benchmark sample.66 The other

counties are left out of the benchmark sample.

Second, for those counties that are included in the benchmark sample, we lose data

from all non-contiguous tracts within that county; see for instance the non-shaded Oklahoma

City county tracts in Figure 2. For the mean bank-county-year observation, 52% of the

lending volume comes from contiguous tracts and is thus taken into account when we

compute annual bank-county mortgage growth. The other (48%) loans are not taken into

account in the benchmark sample. This loss of data makes it less likely that there are two

                                                            65 A hypothetical county with 100 tracts would be included in the benchmark sample even if only one of its tracts is a contiguous one. However, the benchmark sample would use only around 1% of the lending volume in that county to compute bank-county-year mortgage growth, whereas the full sample would use 100% of it. 66 The total number of counties in our sample is higher than the official number of counties (3,143) since we split multiple-district counties into district-counties.

   

53  

consecutive non-zero lending for a given bank-county-year combination, and that the latter is

thus included in the benchmark sample.

Does the discontinuity approach create a selection bias and undermines the external

validity of our results? Panel C in Table A1 reports summary statistics for the bank-county

variables in the benchmark and full samples. Annual mortgage growth is not statistically

different across the two samples; lending dynamics in the baseline sample are thus

representative of those of the full sample. Borrower controls are statistically different across

the two samples, but differences seem economically small. For instance, 6% of loans go to

non-white borrowers in the benchmark sample, against 6.3% in the full sample.67 Robustness

checks discussed in section 5 confirm that we obtain quantitatively similar results when using

the full sample.

                                                            67 This possibly reflects the fact that rural counties are less likely to contain contiguous tracts and thus to be included.

   

54  

Table A1: Comparing the Benchmark Discontinuity (contiguous census tracts only) and Full Samples (all census tracts)

(1) (2) (3) (4)

Panel A: Total number of U.S. census tracts

All tracts Contiguous tracts

Number of census tracts 65,310 12,007

Panel B: Sample characteristics

All tracts Contiguous tracts

Number of bank-county observations 219,072 93,671

Number of banks 3,395 2,699

Number of counties 3,636 2,141

% included loan volume (mean year-county-bank obs.)

100% 52.0%

Panel C: Bank-county mean characteristics

All tracts Contiguous tracts Diff t-test

Δ (log) mortgage lending 0.018 0.015 0.004 -0.004

(Log) borrower income 4.511 4.475 0.036 0.046**

(Log) loan size 4.949 4.935 0.014 0.083**

Borrower tract (log) median income 4.646 4.683 -0.037 0.002**

Borrower loan-to-income 2.081 2.099 -0.018 0.066**

Non-male dummy 0.193 0.192 0.001 -0.000

Non-white dummy 0.063 0.060 0.003 0.002** Panel A reports the total number of 2000 US Census tracts (column 1), and the number of these tracts contiguous to an intrastate 110th Congress district border (column 2). Panel B reports key characteristics of the benchmark sample (containing only loans in contiguous tracts) and full samples (containing loans in all tracts). Annual American data 2006-2010. Panel C reports the average of bank-county-year variable in the benchmark sample (column 1) and full sample (column 2); column 3 reports the difference between these means. Column 4 reports the paired t-test for mean difference between the value of a variable in the benchmark sample and the corresponding observation in the full sample; one (two) asterisk(s) indicates mean equality can be rejected at .05 (.01) significance level. Raw (loan-level) data are aggregated by year and county (district for multiple-district counties) in the two samples. Both samples cover all HMDA-reporting commercial banks active as of 2007Q4 are included except the 2009 stress test participants.

   

55  

Table A2: Instrumental Variable Estimation

(1) (2) (3) (4) (5) (6) IV (1) IV (2) IV Stage: Stage 0 Stage 1 Stage 0 Stage 1 Dependent variable:

I(TARP) TARP TARP x Home

I(TARP) TARP TARP x Home

Stage 0 instrument:

Fed director 0.72** (0.18)

Subcommittee member

0.30** (0.07)

Stage 1 instruments:

(1) 0.76** -0.013 (0.17) (0.08) Home x (1)

-0.066 1.08** (0.03) (0.07)

(2) 0.74** -0.01 (0.19) (-1.84) Home x (2)

-0.09** 1.08** (0.03) (0.08)

Observations 6251 92,790 92,790 6251 92,790 92,790 Adjusted R2 0.81 0.44 0.799 0.432 F-test: + x Home=0 (p-value)

0.0 0.0 0.0 0.0

This table reports results of the stage-0 (columns 1 and 4) and stage-1 (columns (2-3 and 5-6) of the three-stage least square model whose stage 2 is presented in Table 1 (columns 2-3). Stage-0 is a cross-sectional bank-level probit regression of participation in TARP conditional on an exogenous instrument and bank controls (2008 values). I(TARP) is 1 if bank b is a TARP recipient. Fed director is 1 if a member of b’s board is or was a member of a Federal Reserve Bank, and 0 otherwise. Subcommittee member is 1 if b’s home district representative is member of the House Subcommittee on Financial Institutions and Consumer Credit of the 111th Congress, and 0 otherwise. Robust, non-clustered standard errors in parentheses (* p<0.05, ** p<.01). Stage 1 is the usual first stage of a 2SLS model. It regresses the bank-county-year-level endogenous variables TARP and TARP x Home against instruments obtained from Stage 0. Specifically, is the fitted value of TARP participation obtained from Stage 0 after 2008, and 0 otherwise. Home x is the fitted value of TARP participation obtained from Stage 0 after 2008 and if county c is inside b’s home congressional district, and 0 otherwise. The sample covers the 2006-2010 period, and includes all loans given out in census tracts adjacent to a within-state congressional district border. All US commercial banks active as of 2008q3 are included. Regressions also include bank-year controls as of 2008q3 (log total assets, tier-1 capital, cash, charge-offs, non-performing loans, repossessed real estate, deposits, (log) bank age, return on equity and exposure to local shocks) and bank-county-borrower controls (log income, non-white dummy, non-male dummy, tract median income), as well as bank-district and county-year fixed effects. Standard errors clustered by Bank-Holding Company in parentheses (* p<0.05, ** p<.01).

   

56  

Appendix A2: Summary Descriptive Statistics and Parallel Trends

Table A3 provides summary statistics for the benchmark sample. (Log) mortgage

lending grows by 1.5% for the average bank-county-year. 22% of these observations concern

banks in their home district; 21% capture banks in the TARP program, around 10% of which

concern home-district lending.

Our main interest is to estimate whether TARP participants’ lending growth is higher

in their home district vs. elsewhere, compared to non-participants. Figure A1 provides

suggestive visual evidence for this “home-district effect”; it plots average bank-county annual

mortgage growth for participants vs. other banks in counties outside their home districts

(panel A) and inside it (panel B). The most striking pattern is that TARP participants

substantially cut lending outside the home district during TARP years (2008-2009) while

non-participants increase lending. Meanwhile, home-district lending seems much less

affected: participants and non-participants both keep on increasing lending during the TARP

years. Trends for both groups seem to converge at the end of the sample (2010).

Section 5 in the main text confirms the existence of a significant “home-district

effect” in a regression analysis; we interpret this effect as a consequence of participation in

TARP. For this inference to be valid, participants’ home- and non-home district lending

growth should have followed a trend similar to non-participants absent TARP. Panel A in

Figure A1 shows that this parallel trends assumption is satisfied for non-home district

lending: trends before TARP (2006-2007) are almost indistinguishable outside the home

district. Trends seem roughly comparable in the home district as well (panel B). However

we cannot rule out that these trends are statistically different on the basis of this graph only.

Of course, the plots of Figure A1 are simple averages, not controlling for any of the

many influences on mortgage lending that vary by area, bank, and time. Still, three tests

suggest that our finding is attributable to TARP, not differential trends in lending growth.

   

57  

First, future participation in TARP does not have any significant effect in the pre-TARP

period (see section 5). Second, baseline results do not change when we match participants

with non-participants based on their pre-TARP home-lending growth trend (see Appendix

A3). Finally, a robustness check in section 5 suggests that the home-district effect is reversed

once participants exit the program.

Figure A1 suggests another possible caveat of our experiment. Panel A shows that in

2008, non-home lending trend changes for non-participants as well. This suggests that

developments parallel to TARP might have changed all banks’ incentives to lend outside of

their home district. In the main text, we conjecture that this reflects a general crisis-time

retrenchment away from arm’s length lending following the collapse of non-agency

securitization markets. A robustness check in section 5 shows that controlling for this effect

does not change our estimate of the home-district effect.

   

58  

Table A3: Summary Statistics for the Benchmark Sample

(1) (2)

Mean Std. Dev.

Panel A: Bank-year variables

TARP 0.212 0.41(Log) total assets 14.10 2.76Tier-1 capital (% Total assets) 0.08 0.03Cash (% Total assets) 0.02 0.02Charge-offs (% Total assets) 0.01 0.01Repossessed real estate (% Total assets) 0.00 0.01Deposits (% Total assets) 0.73 0.14Non-performing loans (% Total assets) 0.02 0.02(Log) bank age 66.55 42.33Return on equity 0.06 0.15Exposure to local shocks -0.16 1.62

Panel B: Bank-county-year variables

Δ (log) mortgage lending 0.015 1.12Home 0.22 0.41TARP x Home 0.020 0.14Borrower loan-to-income 2.10 1.07(Log) borrower income 4.48 0.61(Log) loan size 4.94 0.82Borrower tract (log) median income 4.68 0.27Non-white dummy 0.06 0.18Non-male dummy 0.19 0.26

   Panel C: Additional bank-level variables

Exit 0.13 0.34Eligible for 1st round 0.39 0.49Deposit-to-asset ratio 0.72 0.14TARP supporter 0.63 0.48Financial contributions 11.99 0.98District market share 0.09 0.14Powerful politician 0.35 0.48

This table reports the mean (column 1) and standard deviation (column 2) of variables of the main regression model (1) for all observations included in the benchmark sample. Annual American data 2006-2010, for all loans given to census tracts adjacent to a within-state congressional district border. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants. TARP is one if bank participates in TARP, zero otherwise; Home is one if county is inside congressional district for bank headquarters. See section 4 (bank-year and bank-county-year variables) and section 6 (additional bank-level variables) for other variable definitions.

   

59  

Figure A1: Mean Annual Bank-County Mortgage Lending Growth

This figure plots the average yearly bank-county mortgage lending growth in counties outside a bank’s home district (Panel A) and counties inside a bank’s home district (Panel B), for TARP participants (black lines) and non-participants (grey lines). Annual American data 2006-2010, for all loans given to census tracts adjacent to a within-state congressional district border. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants. TARP is one if bank participates in TARP, zero otherwise; Home is one if county is inside congressional district for bank headquarters.

Panel A: Non-home district lending

Panel B: Home-district lending

‐30%

‐20%

‐10%

0%

10%

20%

30%

40%

2006 2007 2008 2009 2010

Non‐TARP TARP

‐30%

‐20%

‐10%

0%

10%

20%

30%

40%

2006 2007 2008 2009 2010

Non‐TARP TARP

   

60  

Appendix A3: Heterogeneity between banks and districts

Our main test compares TARP and non-TARP banks’ lending growth inside and

outside their home-district counties. This difference-in-difference-in-difference approach

diminishes the possibility that our main result is biased because TARP and non-TARP banks

or home-district and non-home district counties are heterogeneous in other dimensions than

their susceptibility to political influences after TARP. This section provides additional

evidence in support of this claim.

Heterogeneity between banks

We first investigate differences between TARP and non-TARP banks. In the paper,

we explore these heterogeneities through the baseline propensity-score matching exercise

(column 4 in Tables 1 and 2). This exercise matches participants and non-participants based

on a combination of pre-TARP bank-level characteristics, as captured by their propensity to

participate. Still, recipients and non-recipients could differ along individual pre-TARP

characteristics. For instance low-capital banks could be more prone to participate and to face

political pressure irrespective of participation.

We thus successively match participants and non-participants based on every control

variable in our baseline model as measured before TARP (2007).68 In addition to these

variables, we match banks based on (i) the trend in home-district lending growth (measured

as the difference between mean 2007 and 2006 mortgage growth) and (ii) their volume of

home-district lending as percentage of total lending. The former matching controls for

possible differences in pre-TARP home-district growth trend suggested by visual inspection

of parallel trends (Figure A1). The latter matching controls for the possibility that TARP

banks are larger and thus less dependent on their home-district markets.

                                                            68 The methodology largely follows Cohn and Wardlaw (2016).

   

61  

Table A4 reports the results of this analysis. Columns 1 to 3 suggest that matching

successfully erase differences across participants and non-participants in all dimensions but

size and age. However, the remaining difference in these two cases looks economically

negligible. Columns 4 and 5 report the size and standard error of the main coefficient of

interest TARP x Home as obtained when running the baseline regression using the respective

matched samples. The economic magnitude and statistical significance of the parameter are

stable and very similar to the baseline result in all cases. This suggests that differences in

observable bank-level and bank-home-district characteristics across recipients and non-

recipients do not explain our baseline results.

Heterogeneity between districts

We then investigate differences between home-district and non-home district

counties. Banks may tend to be headquartered in downtown areas. These areas can either be

more affluent or more deprived than contiguous areas, depending on the city. However, these

heterogeneities should only bias our results if they are specific to TARP participants while

they are on the program, because of our difference-in-difference-in-difference approach.69

We explore several variants of this hypothesis in Table A5. Specifically, we repeat

the baseline regression (1) while controlling for an additional county characteristic and its

interaction with TARP. We consider six different characteristics, all measured as county

averages in 2006-2007. Colum 1 reports the parameter estimate for TARP x Home when

each of these additional variables is controlled for. The parameter estimate barely changes at

all across all six regressions. This confirms that our approach is not sensitive to non-political

heterogeneities across districts.70

                                                            69 For instance, TARP banks could be more prone to “fly” once on the program if they are headquartered in affluent areas and surrounded by deprived suburbs. 70 We reach a similar conclusion when alternatively coding the county characteristic as a dummy – one if above median for a given bank, 0 otherwise.

   

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Table A4: Additional Sensitivity Analysis for TARP x Home (βTH) – Pre-TARP Characteristic-by-Characteristic Matching

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

TARP Non-TARP

t-test βTH Std Obs

Panel A: Matching by bank characteristics

(Log) total assets 13.035 13.003 0.065 0.22** (0.07) 46,409

Tier-1 capital 0.085 0.085 0.319 0.20** (0.07) 42,538

Cash 0.015 0.015 0.062 0.20** (0.07) 42,877

Charge-offs 0.002 0.002 0.506 0.21** (0.06) 42,768

Repossessed real estate 0.001 0.001 0.683 0.19** (0.07) 39,835

Deposits 0.799 0.799 0.555 0.19** (0.07) 43,334

Non-performing loans 0.006 0.006 0.383 0.22** (0.06) 40,182

(Log) bank age 61.665 61.636 0.000 0.20** (0.06) 38,418

Return on equity 0.107 0.107 0.792 0.20** (0.07) 41,768

Exposure to local shocks 0.392 0.393 0.123 0.18** (0.07) 38,954

Panel B: Matching by bank-home district characteristics

Δ (log) mortgage lending trend

-0.079 -0.080 0.352 0.20** (0.07) 41,218

% Home-district lending 0.436 0.436 0.845 0.18* (0.07) 48,551

Borrower loan-to-income 2.033 2.033 0.517 0.19** (0.07) 42,556

Borrower (log) income 4.549 4.550 0.146 0.21** (0.07) 42,620

(Log) loan size 4.962 4.960 0.323 0.21** (0.07) 42,509Borrower tract (log) median income

4.680 4.679 0.267 0.20** (0.07) 41,554

Non-white dummy 0.054 0.054 0.284 0.19** (0.06) 39,049

Non-male dummy 0.185 0.185 0.331 0.19** (0.06) 42,385

This table compares the mean value of bank-level (panel A) and bank-home-district-level (panel B) variables before TARP (2007) in different matched samples. Each row corresponds to a different sample of TARP and non-TARP recipients matched based on the respective characteristic. Columns 1 and 2 report the mean characteristic for future TARP recipients and non-recipients, respectively. Column 3 reports the p-value of a paired t-test of characteristics equality across the two groups. Columns 4 and 5 report the parameter estimate and standard error (clustered by bank-holding company) for the TARP x Home coefficient obtained when regressing the main model (1) in the respective matched sample, respectively; one (two) asterisk(s) indicates significantly different from zero at .05 (.01) level. Column 6 reports the total number of bank-county-year observation in the respective sample. American data 2006-2010 for all loans given to census tracts adjacent to a within-state congressional district border. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants.

   

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Table A5: Additional Sensitivity Analysis for TARP x Home (βTH) – Additional TARP x County characteristic controls

(1) (2)

βTH Std

Controlling for interaction between TARP and:

Borrower loan-to-income (county average) 0.22** (0.07)

Borrower (log) income (county average) 0.21** (0.07)

(Log) loan size (county average) 0.21** (0.07)

Borrower tract (log) median income (county average) 0.22** (0.08)

Non-white dummy (county average) 0.22** (0.06)

Non-male dummy (county average) 0.22** (0.06)

Coefficients, with standard errors (clustered by bank-holding company) in parentheses; one (two) asterisk(s) indicates significantly different from zero at .05 (.01) level. Regressand is first difference in log mortgage lending for bank-county-year. Columns 1 and 2 report the parameter estimate and standard error (clustered by bank-holding company) for TARP x Home (βTH) obtained using the baseline regression (1) and additionally including a County characteristic control and its interaction with TARP. Rows correspond to different county characteristics. County characteristics are calculated as mean of the corresponding variable in a given county in 2006-2007. American data 2006-2010 for all loans given to census tracts adjacent to a within-state congressional district border. All HMDA-reporting commercial banks active as of 2007q4 are included except the 2009 stress test participants. TARP is one if bank participates in TARP, zero otherwise; Home is one if county is inside congressional district for bank headquarters. Bank-year controls included but not recorded: TARP dummy; log total assets; tier-1 capital (%Total Assets); cash (%TA); charge-offs(%TA); non-performing loans (%TA); repossessed real estate(%TA); deposits(%TA); (log) bank age; return on equity; and exposure to local shocks. Bank-county-borrower controls included but not recorded: log income; log loan size; loan-to-income non-white dummy; non-male dummy; tract median income; county characteristic; county characteristic x TARP; county characteristic x TARP fixed (1 if a bank is or will be on TARP, 0 otherwise). Bank-home and county-year fixed effects included but not recorded.

   

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Table A6: House of Representatives Bills Relevant for TARP Participants

House committees:

Con-gress Act Name

Financial Services Judiciary

Oversight and

Government Reform

Ways and means

110 Special Inspector General for the TARP (HR 3731)

x

111 Special Inspector General for the TARP (HR 383)

x x

111 TARP Reform and Accountability (HR 384)

x x

x

111 To amend the EESA of 2008 to provide for additional monitoring and accountability of the TARP (HR 1242)

x

111 To amend the executive compensation provisions of the EESA of 2008 to prohibit unreasonable and excessive compensation and compensation not based on performance standards (HR 1664)

x

111 SIG TARP Small Business Awareness (HR 3179)

x

111 TARP Executive Disclosure Act (HR 3436)

x x x

This table lists all the bills submitted to the 110th or 111th House Representative whose title features the words “TARP” or “EESA”, were submitted after the passage of EESA and that have been referred to at least one House committee. Compiled by the authors using Congress archives (http://www.congress.gov).    

   

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Appendix A4: Aggregate and electoral effects

We have established that TARP recipients increase lending in their home Congress

representative’s district. Our interpretation is that representatives seek to encourage lending

in their district, and TARP recipients respond to local political influences (or the threat

thereof). However, our tests do not show either that aggregate district lending increases, or

that congressional representatives benefit from any higher lending.71 In addition, we have

linked the home-district effect to the characteristics but not the benefits of the incumbent, for

instance in subsequent elections.72

We seek to fill these two gaps simultaneously using a two-stage least squares cross-

sectional regression. The first stage relates aggregate lending growth in a district after TARP

to this district’s total exposure to the home-district effect. Formally, we estimate:

∆ ∙ % ∩ ,

where ∆ is the 2006-2007 to 2008-2009 change in total log mortgage

origination volume in a district (thus including non-frontier areas and all banks). The

explanatory variable of interest % ∩ is the share of mortgages originated by

TARP participants headquartered in the district, measured before the TARP (that is, in 2006-

2007) to avoid reverse causality. This variable captures the prior that districts with a larger

presence of locally headquartered TARP banks stand to gain more from the home-district

effect than other districts.

Stage 2 relates district lending growth to the incumbent’s 2010 electoral performance:

∙ ∆ ,

                                                            71 This is because we split lending by counties and banks, and exclude both non-“frontier” areas and large banks. This sharpens identification, but delivers a partial view of total district lending, the likely relevant outcome for the politician. 72 A large theoretical and empirical literature shows that economic conditions influence electoral outcomes, including those of American midterm Congress elections (Lewis-Beck and Stegmaier (2000) and references therein). Most studies concentrate on changes in local income. But Antoniades and Calomiris (2016) show that voters in a county “punish” the incumbent presidential candidate if local credit supply declines, even controlling for county income.

   

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where the regressand is Win – 1 if the incumbent wins the 2010 House of Representatives

midterm election, and 0 otherwise, and % ∩ is used as an instrumental

variable for ∆ .73

% ∩ is pre-determined, but still might be correlated with a number

of determinants of lending growth and electoral outcomes; failing to control for these could

lead to a violation of the exclusion restriction. We thus control for characteristics of the

districts’ borrowers, incumbent candidate and electoral competition.74,75 We also include

state fixed effects to control for state-wide shifts in economic conditions or political

preferences. The two equations are estimated on the cross-section of 392 incumbent

congressional representatives who ran for re-election in 2010.76

Table A7 reports the estimation results. Districts more exposed to the home-district

effect experience higher aggregate lending. The coefficients of the first-stage in column 1

indicate that when % ∩ increases by 10%, total post-TARP lending is 4.2%

higher, an economically and statistically significant amount.77 Reassuringly, the second-

stage results show that higher post-TARP lending in the district is associated with a higher

probability that the incumbent wins the 2010 midterm election, when using either total post-

TARP lending growth (column 3) or acceptation rate (column 4) as endogenous variable of

interest. We also find that quantitatively, a one-standard deviation lending increase (+28%,

or $560 million for the average district) is associated with a 10 percentage points higher vote

percentage for the incumbent (results are available upon request). This is a large number; it

                                                            73 We estimate a linear probability model despite the dummy regressand due to the presence of fixed effects. 74 We include pre-TARP mean values of all borrower controls included in the main regressions, as well as the post-TARP change in two district-level outcomes available through HMDA – average borrower income and loan size. 75 We include incumbent log number of terms served and party (Republican dummy), and a 2006-2008 representative Republican dummy. Many incumbents are uncontested, and electoral competition might affect politicians’ incentives to cater to constituents’ needs (Levitt and Snyder, 1997). So we control for the 2006 and 2008 winning margin and the 2008 and 2010 log number of candidates. %(TARP ∩ Home)d might affect electoral outcomes through its effect on local labour markets in the banking sector, so we also include the share of employees by the financial industry. Finally, we include the market share of locally headquartered banks to control for the effect of small banks presence on post-crisis lending (DeYoung et al. 2015). 76 We obtain qualitatively similar stage-1 results when using all districts. 77 Alternatively, column 2 shows that the mortgage application acceptation rate rises by a comparably large 0.7 percent.

   

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is also close to Levitt and Snyder (1997), who find that $50 million more federal spending in

a district increases incumbent’s performance by 2 percentage points.

In contrast to our main regression results, these tests seek to maximise

representativeness, which comes at the cost of lower precision. While magnitudes should

thus be interpreted with caution, the results qualitatively support the notion that the home-

district effect matters for district lending conditions and political outcomes.

A related question is whether the home-district effect imposes any cost to TARP

participants. Our findings that participants increase lending and application acceptations

conditional on borrower credit risk suggest looser underwriting standards in the home

district.78 To test this we estimate the cross-sectional regression:

∆% ∙ % ,

where ∆% is the change in bank non-performing loan

percentage between the pre-TARP (2006q4-2007q4) and 2010q4, when changes in lending

standards might start appearing on balance sheets. Our explanatory variable of interest is

% , the interaction of a TARP dummy with the bank’s share of home-

district lending before TARP (2006-2007). This captures the notion that participants with a

larger portion of overall lending in their home district are more affected by a relaxation of

home-district underwriting standards compared to other banks.79 The results, reported in

column 5, suggest that a 10% increase in TARP-Home is associated with 0.2 percentage

points higher share of non-performing loan. This effect is quantitatively modest from the

bank’s overall balance sheet point of view, but relatively large compared to the average

change in non-performing loans over the period (+2.8 percentage points).

                                                            78 Alternatively, TARP participants might also be able to expand home-district lending by passing on the lower funding costs they might enjoy through TARP (Berger and Roman, 2015) to home-district borrowers. 79 In addition to the components of this interaction, we include the bank and borrower controls used in the main regression (all measured as pre-TARP mean), as well as state fixed effects.

   

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TABLE A7 – Aggregate and electoral effects

(1) (2) (3) (4) (5) District-level effect Bank-level effect

Model: IV Stage 1 IV Stage 2 OLS

Dependent variable:

Δ Mortgage volume

Δ% Accepted

applications

Yes if incumbent wins 2010 midterm

Δ% Non-performing loans

%(TARP ∩ Home)d

0.42** 0.06** (0.16) (0.02)

Δ Mortgage volume

1.87* (0.92)

Δ % Accepted applications

12.32* (5.47)

%(TARP x Home)i 0.02* (0.01)

State fixed effects Yes Yes Yes Yes Yes Borrower controls Yes Yes Yes Yes Yes Election controls Yes Yes Yes Yes Bank controls Yes

Observations 392 392 392 392 2,374

R2 0.76 0.67 0.13 0.19 0.26 Coefficients, with robust standard errors in parentheses; one (two) asterisk(s) indicates significantly different from zero at .05 (.01) level. Regressands are: 2006-2007 to 2008-2009 change in log mortgage origination volume for a district (column 1); 2006-2007 to 2008-2009 change in accepted mortgage applications (% total) for a district (column 2); 1 if incumbent candidate wins 2010 midterm House of Representatives election, 0 otherwise (columns 3-4); 2006q4-2007q4 mean to 2010q4 change in non-performing loans (% total loans) for a bank (column 5). %(TARP ∩ Home)d is 2006-2007 mortgage volume originated by TARP participants headquartered in the district (%district total). %(TARP x Home)i is 2006-2007 home-district mortgage volume (% bank total) for TARP participants, 0 for other banks. Borrower controls included but not recorded are 2006-2007 district (columns 1-4) or bank (column 5) average of: log income; loan-to-income; log loan size; non-white dummy; non-male dummy; tract median income. Election controls included but not recorded are: 2006 and 2008 winner vote margin; 2008 and 2010 log general election candidates number; 2006-2008 representative Republican dummy; 2010 incumbent Republican dummy, log terms served, and 2008 general election vote %; financial industry employees (% total employees). Bank controls included but not recorded are 2006q4-2007q4 mean of: home-district mortgages (%total mortgages); TARP dummy (1 if bank is future recipient, 0 otherwise); non-performing loans (%Total Loans); log total assets; tier-1 capital (%Total Assets); cash (%TA); charge-offs(%TA); non-performing loans (%TA); repossessed real estate(%TA); deposits(%TA); (log) bank age; return on equity; and exposure to local shocks. Districts where the incumbent candidate does not run in 2010 are excluded from columns 1-4. Annual American data for all loans. All HMDA- and Call Reports-reporting commercial banks active as of 2007q4 are included.