Essays in Real Estate and Finance
by
Carl J. Liebersohn
B.A., Mathematics and Economics
Amherst College, 2009
S.M., Management Research
Massachusetts Institute of Technology, 2018
Submitted to the Sloan School of Management
in partial fulfillment of the requirements for the degree of
DOCTOR OF PHILOSOPHY IN MANAGEMENT
at the
MASSACHUSETTS INSTITUTE OF TECHNOLOGY
September 2018
@ Massachusetts Institute of Technology 2018. All rights reserved.
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loan School of Management
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Antoinette Schoar
Michael M. Koerner (1949) Professor of Entrepreneurship
Signature redacted Thesis Supervisor
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MASSACH S NCatherine Tucker
Sloan Distinguished Professor of Management
SEP 272 018 Professor of Marketing
Chair, MIT Sloan PhD Program
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Essays in Real Estate and Finance
by
Carl J. Liebersohn
Submitted to the Sloan School of Management
on August 10, 2018, in partial fulfillment of the
requirements for the degree of
DOCTOR OF PHILOSOPHY IN MANAGEMENT
Abstract
This dissertation consists of three chapters on topics related to real estate and fi-
nance. The first chapter studies the effects of bank competition on bank risk-taking
and lending. Using a quasi-experimental design that exploits the exogenous appli-
cation of bank antitrust laws following bank mergers, I show that bank competition
leads to more loans going to larger and safer borrowers. The second chapter shows
that housing demand shocks from 2000-2006 are highly correlated the elasticity of
housing supply in different regions, and explores the implications of this for research
on the effects of housing prices. The third chapter, written with Gregory Howard,
proposes a new channel for changes in aggregate housing prices. We show empiri-
cally and theoretically that increased demand for housing in inelastic areas led to
higher aggregate housing prices from 2000-2006, and quantify the magnitude of this
channel.
Thesis Supervisor: Antoinette Schoar
Title: Michael M. Koerner (1949) Professor of Entrepreneurship
3

Acknowledgments
I am grateful to the members of my thesis committee for the patience, guidance, and
support: Antoinette Schoar (chair), Jonathan Parker, and Jim Poterba. Thanks also
to Nittai Bergman, Ricardo Correa, Xavier Giroud, Nancy Rose, Adrien Verdelhan,
Daniel Green, Asaf Bernstein, Kirill Borusyak, Greg Howard, Peter Hull, Vikram
Jambulapati, Rachael Meager, and Teju Velayudhan, as well as to seminar partici-
pants at MIT, the Federal Reserve Board, and the Banco Central do Brasil for their
helpful comments and suggestions. I gratefully acknowledge the financial support of
the Becker Friedman Institute Macro-Financial Modeling Initiative. This dissertation
would not have been possible without the constant support and guidance of my wife
Teju, of my parents, and of my brother Ben.
5
6
Chapter 1
How Does Competition Affect Bank
Lending? Quasi-Experimental Evidence
from Bank Mergers
This chapter studies the effects of bank competition on commercial lending. I find that
greater competition causes a change in the quantity and composition of businesses receiving
loans, with more loans going to larger and safer borrowers. To identify exogenous changes in
bank competition, I exploit discontinuitiesi n the application of bank antitrust rules governing
mergers. In markets that fall narrowly below regulatory cutoffs, competition declines due to
bank mergers. In markets above cutoffs, forced branch divestitures keep competition constant
even though mergers occur. Using a difference-in-differences methodology comparing these
types of markets, I estimate that antitrust rules cause the Herfindahl Index to fall in relative
terms by 180 points and, consistent with greater competition, deposit rates to rise by 0.13
percentage points. Using loan-level data from commercial mortgages, I show that this change
in competition is associated with a 5 percent increase in the likelihood that borrowers take a
loan from a local bank and an increase in the average borrower size of 10 percent without a
change in the average loan-to-value ratio. For banks not directly involved in a merger, lending
to large borrowers increases and the nonperforming loan ratio falls by 0.38 percentage points.
Overall, my findings support a model in which competition improves the efficiency and quality
of bank lending.
7
1.1 Introduction
How does competition affect banks' provision of financing? This question, which has broad
relevance for credit markets and firms' access to capital, has become increasingly salient as the
banking sector in the United States has consolidated. Since 1994, the number of commercial
banks has declined by fifty percent from about 10,000 to 5,000. This consolidation has led to
an unprecedented increase in bank concentration at the local level. It is therefore important
to understand what effect competition has on the quantity and composition of credit available
to businesses. This paper empirically investigates the effect of bank competition on credit
supply, risk, and composition.
Theoretical predictions about the effect of competition on lending depend on assumptions
about the role banks play in credit allocation. Petersen and Rajan (1995) emphasizes banks'
ability to form long-term relationships with borrowers, arguing that monopolists may lend
more than competitive banks because monopolists can smooth profits over the course of
their lending relationships. Alternatively, Jayaratne and Strahan (1996) and Bertrand et
al. (2007) study banks' ability to allocate capital and argue that greater competition may
improve the efficiency of bank lending, possible leading to more and more effective lending.
Finally, in Keeley (1990) and Allen and Gale (2004), banks choose borrowers as they would
choose a portfolio of risky assets; competition induces a shift toward riskier borrowers as
lower profits reduce the downside risk from bank bankruptcy.
This paper empirically evaluates theories of banking by studying how loan risks and
volumes change following mergers whose competitive impact is exogenously restricted by
antitrust regulation. I find that, for incumbent banks not involved in a merger, competition
increases credit supply and decreases loan risks. These findings are most consistent with
models in which competition increases the efficiency of the banking system by reducing
market power.
The source of empirical variation is a quantitative cutoff rule used by U.S. antitrust
authorities to determine the approval of bank mergers, which discontinuously changes the
8
probablility that regulators intervene in a market. This results in some markets where
mergers proceed as planned and others where regulators exogenously restrict consolidation.
When banks plan to merge, regulators decide whether to intervene based on how the merger
would change the Herfindahl Index (HHI) of bank deposits in any market where both the
absorbing and acquired bank have branches.1 Therefore, the same proposed merger might
induce intervention in some banking markets but not others. I show that the rule does
not influence the banks' decision to merge, but it does mitigate the anti-competitive effects
of mergers in the markets where regulators intervene. Regulators require merging banks to
divest branches in any market where the HHI would rise by at least 200 points to a level above
1800. If the HHI would rise to a level below 1800, there is no such requirement. I exploit
the heterogeneous application of antitrust rules above and below the 1800 HHI cutoff using
a difference-in-differences design that compares banking markets whose HHI falls within a
500-point range of 1800. These effects are robust to using alternative HHI ranges above and
below the cutoff.
The difference-in-differences estimates show that antitrust enforcement has a dramatic
effect on the level of competition, which I then use to study the effect of competition on
bank lending by banks uninvolved in the mergers. In markets with a predicted HHI from
1300-1800, mergers cause the HHI to increase by about 363 points on average. Due to
enforcement, the HHI increases by 180 points less in markets in the predicted 1800-2300
region. For comparison, a 180-point change in HHI would be approximately equivalent to
a change from eight to seven equally-sized banks. Price-based measures also show that this
antitrust rule affects bank competition. The 180-point HHI decrease is associated with an
increase in 3-month certificate of deposit (CD) spreads of 0.10 percentage points and an
increase in 3-year CD spreads of 0.21 percentage points, both of which are consistent with
increased competition and large compared to median annual percentage yields of 1.14% and
The Herfindahl Index is a measure of market concentration widely used in competition research and
policy. Throughout this article, I use the definition of "banking market" used by bank regulators in the
United States. Markets typically correspond to MSAs or non-MSA counties. The HHI for banks is measured
using deposits data from the FDIC Summary of Deposits Database.
9
2.90%.
Having established that antitrust laws affect the level of competition in local banking
markets, I investigate the effect of competition on bank lending. I investigate three em-
pirical effects of competition that distinguish theories of banking. First, whether greater
competition increases or decreases total bank lending. Second, how competition changes the
composition of borrowers receiving loans. Third, how competition affects loan delinquency
rates.
I evaluate these predictions using bank-level balance sheet data as well as loan-level mi-
crodata on commercial real estate (CRE) lending. Because CRE lending relies on banking
relationships that are established over time and are therefore a real-world analogue to the
type of loans studied by banking theory, CRE is an ideal setting to study theories of compe-
tition. Furthermore, CRE loans are the largest single source of financing for small businesses
in the United States, according to the Survey of Small Business Finances. To isolate the
effects on bank competition, the sample is limited to include only incumbent banks in each
banking market, without the banks that are themselves merging. There are three main
findings.
First, I find that greater competition is associated with an increase in bank lending,
but only to larger businesses within the small business portfolio.2 At the bank level, small
business CRE lending increases relative to banks' total CRE lending, but only for small
business CRE loans with a value of $250,000-$1,000,000. In the loan-level data, estimates
indicate a 40% increase in loan origination at the market level for loans with collateral above
the median value of $243,000, due to a combination of new lending and refinancing. In
contrast, I estimate a small, positive, and not statistically significant effect on smaller loans
in both loan- and bank-level data.
Second, the increase in lending for large borrowers changes the composition of borrowers
2 "Small business lending" in the bank-level data refers to loans with value less than $1,000,000. Within
this loan range, a "large borrower" is one that borrows between $250,000-$1,000,000 and a "small borrower"
is one that borrows less than $250,000.
10
receiving loans. Deeds records estimates show that, following mergers where antitrust law
is applied, CRE loan sizes increase by 10 percent relative to mergers where laws are not
applied. Average borrower collateral values and property prices increase, indicating a change
in borrower composition, while loan-to-value (LTV) ratios change very little. Borrowers
are five percent more likely to borrow from nearby banks located in the same market and
the increase in loan size I estimate is driven entirely by local lenders. I show that large
borrowers are generally less dependent on nearby banks for financing, so a straightforward
interpretation of these findings is that greater competition in a local market attracts large
borrowers who would otherwise borrow elsewhere.
The third finding is that greater competition is associated with less risky bank lending.
In markets where the HHI falls by 180 points because of bank regulation, banks have a
0.36 percentage point overall lower non-performing loan ratio and a 0.34 percentage point
lower non-performing loan ratio for commercial real estate loans. Using microdata from
commercial mortgage-backed securities, I show that, in general, large CRE borrowers default
at significantly lower rates than small ones. Therefore, when the composition of borrowers
changes from smaller to larger borrowers, it is natural that the rate of delinquency should
fall as well.
The estimated effect of competition on bank capital structure, including leverage, regu-
latory capital, and deposit reliance, is small in magnitude and not statistically significant.
Because the bank sample only includes local banks, the 180-point change in HHI is a signifi-
cant change in competition. Therefore, these estimates are less consistent with the hypothesis
that greater competition causes banks to adopt a riskier capital structure.
The identifying assumption for these estimates is that incumbent banks would not re-
spond differently to mergers with antitrust intervention if it were not for the interventions
themselves. This assumption is strongly supported by the data: The incumbent banks I
study are observably similar in markets with and without intervention. Three facts provide
further evidence for this. First, I show that mergers are not self-selected on the basis of
11
whether antitrust rules will be applied (if they were, mergers that occur despite anticipated
antitrust intervention might be unusual in some way).' In particular, there is no bunching of
mergers below the 1800 cutoff, as one would expect if banks were merging selectively. Second,
I show that mergers do not have a direct effect on the measured size and branch network of
the incumbent banks. Third, I do not estimate an effect in a placebo sample which uses the
HHI=1800 cutoff but restricts mergers to those where the HHI increases by fewer than 200
points and are therefore unaffected by antitrust law. A variety of other placebo tests and
control variables provide further support for my identification.
What do the results imply for theories of banking? The empirical results support the
theory that competition increases lending and improves the effectiveness of the financial
system. This theory emphasizes the role of banks as efficient allocators of capital that have
a special ability to determine which investments are the most profitable. By contrast, in
the model proposed by Petersen and Rajan (1995), monopolistic banks know that they
can recover losses incurred by lending to unknown borrowers using the rents they earn from
borrowers who turn out to be successful. This model predicts that competition decreases the
total amount of bank financing, but the empirical results are less supportive of this prediction.
The empirical results also do not support the hypothesis that competition increases risky
lending. This theory, which is known as the Charter Value Hypothesis, holds that deposit
insurance incentivizes banks to make risky bets with depositors' money, but the incentive
for risk-taking is lower for monopolistic banks who would lose their rents in bankruptcy
(Keeley, 1990; Allen and Gale, 2004). Instead, the results support the class of models in
which competition is efficiency-enhancing.
This result is important because it suggests a possible downside to the increase in bank
concentration that has occurred over the past twenty years. The findings therefore contribute
to a debate on the effects of rising concentration that has occurred in the United States more
generally (Gutierrez and Philippon, 2016; Grullon et al., 2017). The estimates shown here
3 This is not surprising, as bank mergers typically involve a large number of markets, and antitrust action
in a handful of markets is unlikely to derail a merger altogether.
12
indicate that the rise in bank concentration may have negative effects on commercial lending.
The results also have implications for bank antitrust regulation. Bank regulators are
uncertain about whether competition has positive or negative effects (Group of Ten, 2001;
Beck, 2008). Theoretically, different effects may dominate in different settings and at dif-
ferent levels of competition but what is most relevant for bank regulators is the change in
bank behavior that is induced by antitrust laws. Therefore, my results do not prove that
competition never has a "dark side", but they provide evidence against a dark side at the
most relevant policy margins.
The paper proceeds as follows. Section 1.2 reviews related literature. Section 1.3 presents
a stylized framework used to analyze the empirical estimates. Section 1.4 describes the
institutional setting, including a summary of the bank antitrust process in the United States
and details on the quantitative screening process. Section 1.5 describes the main data sources
and presents summary statistics. Section 1.6 describes the main difference-in-differences
strategy used to identify the effects of bank competition. Section 1.7 provides evidence
for the effectiveness of antitrust law enforcement, Section 1.8 presents the main empirical
estimates, and Section 1.9 concludes.
1.2 Literature Review
Empirical research on bank competition has studied the effects of bank competition on both
banks and on borrowers. This paper contributes to both empirical literatures.
The most closely related research to this paper studies the effects of bank competition
on lending to small businesses. Jayaratne and Strahan (1996) and Jayaratne and Strahan
(1998) show that states relaxing branch restrictions had greater credit provision and econo-
mic growth as a result. Related research by Rice and Strahan (2010) shows that restrictions
on branch expansion raised interest rates and reduced credit supply without a change in
borrowing amounts. Other papers examining the effects of branching restrictions include
13
Jiang et al. (2017), Black and Strahan (2002), Cetorelli and Strahan (2006), and Goetz et al.
(2016). Overall, these research show that relaxing restrictions leads to positive financial and
real outcomes for firms. Relatedly, a number of papers study the cross-sectional relations-
hip between competition and lending-related variables, including Elsas (2005), Degryse and
Ongena (2007) and Love et al. (2015). Finally, Bertrand et al. (2007) studies the effects of
the liberalization of the French banking system on business lending and real firm outcomes.
Two innovations set this paper apart from the literature on branching restrictions. First,
this paper studies competition per se, rather than changes in management that may result
from a changing market structure. Strahan (2003) and Jayaratne and Strahan (1998) show
that removing branch restrictions affected credit supply partly because this change allowed
well-managed banks to take over poorly-managed ones, thus increasing the quality of bank
management. In contrast, this paper studies changes to competition induced by a change
in the number of competitors rather than bank management, which more directly tests the
implications of theories of bank competition.4 Second, this paper is unusual in its use of
loan-level data. Together, these differences make it possible to test theories of competition
that focus on the number of competitors in a banking market.
The findings in this paper are also related to research on the effects of competition on bank
risk-taking. A number of papers in this area focus on testing the Charter Value Hypothesis
(CVH), which predicts greater competition causes more bank risk-taking because of a decline
in charter value. Overall, the results of this extensive literature have been mixed.5 The mixed
findings may be due to theoretical ambiguity, difficulty in measuring bank risk-taking, or the
difficulty of identifying exogenous changes to market structure.
Finally, my estimates complement the findings of Williams (2017) and Nguyen (2016),
4 Strahan (2003) shows that interstate branching restrictions have no effect the Herfindahl Index, which
is one of the main measures that antitrust regulators target and which I study. By contrast, I show that
the size and ownership structure of incumbent banks do not change as a result of antitrust law enforcement,
ensuring that the causal channel is different from the one studied by research on branching restrictions.
'Pro-CVH: Keeley (1990); Demsetz et al. (1996); Beck et al. (2006); Dick (2006); Yeyati and Micco (2007);
Ariss (2010); Jimenez et al. (2013); Beck et al. (2013) Anti-CHV: Nicolo (2001); Boyd and De Nicolo (2005);
De Nicolo and Loukoianova (2007); Schaeck et al. (2009). Mixed: Berger et al. (2009).
14
which, rather than studying market-level competitive dynamics, focus on the effect of mergers
on the merging banks themselves. Williams (2017) compares the effect of monetary policy
on divested branches to its effect on non-divested branches by the same banks in the same
banking market, finding that branches purchased by small banks become more sensitive
to monetary policy. Nguyen (2016) shows that branch closings following mergers reduce
credit provision for businesses located near the closed branches. Bank mergers are also
important to this study, but rather than investigating the effect of mergers within a banking
market, I study the effects of antitrust laws across banking markets, comparing markets
where antitrust laws apply to markets where they do not apply. In order to study competition
as a market-wide phenomenon, data on incumbent banks (rather than the banks that are
actually involved in a merger) best demonstrates the effect of competition.
1.3 Theoretical Framework
The literature discussed in the previous section discusses many possible ways that banks
may respond to competition. Rather than test all possible channels, I will focus on three
of the main theoretical mechanisms drawn from theoretical research. First, monopolists do
not take prices as given, so one would expect monopolists to lend less than competitive
banks. I call this the market power mechanism. Second, when projects require repeated
investments and are initially unprofitable, monopolists might make early-stage investments
that competitive banks will not. The rents earned on late-stage loans subsidize early and
possibly unprofitable investments. This mechanism, which leads monopolists to lend more
than competitive banks, is the long term project mechanism studied by Petersen and Rajan
(1995) and Boot and Thakor (2000). Third, monopolists may take fewer risks because the
rents are a valuable asset that are lost in bankruptcy. Research on this theory refers to this
as the Charter Value Hypothesis. It predicts that monopolists make less risky loans than
competitive banks do.
15
Appendix 1.13.1 presents a simplified mathematical model which encompasses the three
mechanisms. Below, I describe the main assumptions and logic behind each mechanism.
Market Power Mechanism
The market power mechanism predicts that monopolistic banks will use their market
power to lend less at a higher price because they are not price-takers (as competitive banks
are). This mechanism underlies the " Structure-Conduct-Performance" paradigm that was
once dominant in theoretical research on bank competition. For any particular type of loan or
financial product, the effects of this mechanism may depend on a variety of factors, including
market contestability, lenders' ability to price discriminate, and borrowers' search costs. For
example, borrowers with easily-valued collateral may be able to search for financing more
easily outside of their local banking market, causing them to have a high elasticity of loan
demand. An increase in local market power may drive these borrowers to find loans elsewhere
if local banks are not able to price discriminate.
Long-Term Project Mechanism
The Long-Term Project Mechanism emphasizes banks' ability to maintain relationships
with borrowers. Unknown borrowers with little collateral may be initially unprofitable to
lend to because banks do not know whether they are good or bad credit risks, but by
borrowing repeatedly and repaying their debts, borrowers may be able to establish a good
reputation. Monopolistic banks can earn rents on their loans to reputable borrowers which
they use to subsidize the unprofitable early stages of their lending relationships knowing they
might be able to earn profits at a later stage. Because competitive banks' rents are limited,
they may not want to lend to unknown borrowers, as there is no way for their relationships
to eventually become profitable. As with the Market Power Mechanism, the effects of this
channel depend on borrowers' collateral availability and search costs.
Charter Value Hypothesis
Because competitive banks earn lower rents on their loans than monopolistic banks do,
they have less to lose in bankruptcy. Investments or strategic choices that run the risk of
16
causing bankruptcy (but are otherwise profitable) are therefore more attractive to compe-
titive banks than to monopolistic banks. This causes competitive banks to take more such
risks than monopolistic banks. These risks may be in the form of risky loans, a risky capital
structure, risky derivatives trades - anything that causes bankruptcy with some probability.
The payoffs from the risky bets either do not depend on the degree of competition or are
less affected by it than the profits from the "normal" investments which the banks would
otherwise make.
Empirical Predictions
These mechanisms yield several empirical predictions. I divide them into predictions for the
total amount of bank lending, the composition of borrowers receiving loans, and the riskiness
of bank capital structure.
Total Lending
The effect of competition on total lending depends on which mechanism dominates. The
long-term project mechanism predicts that monopolists do more overall lending, particularly
for projects that require a high initial investment. By contrast, the market power mechanism
predicts that competitive banks do less lending, in which case marginal borrowers may be
those who have easy access to outside sources of finance.
Borrower Composition
The long-term project mechanism predicts that the composition of loans should shift
towards larger, better-etablished borrowers. Newer and smaller borrowers are the most
likely to need early-stage investments from banks (Petersen and Rajan, 1995). This also
implies a shift towards less risky lending as better-established firms are less likely to become
delinquent. The market power mechanisms predicts less borrowing and higher interest rates.
If banks cannot perfectly price discriminate, borrowers with the greatest access to outside
sources of finance, such as those with the best collateral or reputation, can go outside the
local market when competition is low. Finally, the Charter Value Hypothesis predicts that
17
competitive banks take more risks. In some formulations of this mechanism, such as the one
modeled by Allen and Gale (2004), this means a higher share of risky borrowers.
Bank Capital Structure
The Charter Value Hypothesis predicts that greater competition causes banks to take
actions that increase their risk of bankruptcy. They could plausibly do this by lending to
riskier borrowers or by adopting a riskier capital structure, such as one more prone to bank
runs or with a smaller equity buffer. Neither the long-term project mechanism nor the
market power mechanism predict changes in bank capital structure.
Table 1.1 summarizes the three mechanisms' main predictions.
1.4 Institutional Setting
U.S. banks that wish merge must receive the approval of the bank regulator in charge of the
acquiring bank. Regulators take many laws and regulations into account when they evaluate
mergers. Some of those laws govern the antitrust implications of bank mergers.' To make
their antitrust-related decisions, both bank regulators and the Department of Justice (DOJ)
perform a quantitative screening of each market where both the acquiring bank and the
bank being acquired have branches. The screening relies on a formal quantitative analysis
of changes to the Herfindahl-Hirschman Index (HHI) due to the merger. When banking
markets involved in a merger violate the quantitative screening, regulators generally do not
block the merger altogether. Rather, they require antitrust remedies to be applied to the
violating banking markets. Merging banks often have branches in many of the same banking
markets, but only the banking markets violating the quantitative screening are affected; the
merger can take place as planned in all other banking markets.
Regulators screen banking markets for antitrust concerns in three steps:
6 The laws governing antitrust are the Sherman and Clayton Antitrust acts. "Regulators" here means the
Federal Reserve, FDIC, OCC, or the NCUA. Typically we think of antitrust enforcement as a matter for the
court system, but administrative law allows bank regulators to make most antitrust decisions. Only when
the U.S. Department of Justice (DOJ) disagrees with bank regulators, which happens in a minority of cases,
do courts get involved.
18
1. They calculate the HHI of bank deposit concentration in each market where both
banks have branches. 7 The HHI is defined as the sum of squared deposit market
shares, multiplied by 10,000. Market shares are measured using branch deposit data
from the FDIC Summary of Deposits Database. The HHI ranges from 0, for perfectly
competitive markets, to 10,000 for markets with one firm.
2. They calculate the resulting HHI in each market if the merger went through as planned.
3. Markets where the HHI would increase by at least 200 points (AHHI > 200) to a level
above HHI = 1800 are flagged for further review and antitrust remedies are required
in these markets.
While the screening cutoffs (AHHI = 200 and HHI = 1800) are important, they are not
binding for bank regulators. These and other the guidelines may be waived, for example, if
there is "evidence that the merging parties do not significantly compete with one another"
or "evidence that rapid economic change has resulted in an outdated geographic market,"
according to reports published by the FDIC. Regulators also commonly allow mergers to
go through in markets violating the screening when they believe the bank being acquired
could not survive without being acquired. Moreover, they may require remedies even when
the quantitative screening is not violated, for example because of concerns about a mer-
ger's effects on community lending or financial stability. Finally, antitrust screening was
partially suspended during the financial crisis. I exclude mergers taking place in 2007-2008
from the sample throughout this paper. Despite this regulatory discretion in the applica-
tion of antitrust rules, Section 1.7 will show that the likelihood of branch divestiture rises
discontinuously at the HHI=1800 cutoff.
7 Regional Federal Reserve Banks define the geographic banking markets which other regulators use as
well; in urban areas, markets typically coincide with MSAs, and in rural areas, they may be single counties.
However, there is widespread discussion in the legal and economic literature about the right definition of a
banking "market." While there is evidence that banking is a local phenomenon (Petersen and Rajan, 1994),
some authors have argued that innovations to the banking industry have enabled banks to compete effectively
over large areas (Pekarek and Huth, 2008) and others that banks compete in a highly localized way Nguyen
(2016). In order to exploit regulatory cutoffs, I use the Federal Reserve definitions for the antitrust analysis.
19
Regulators do not block bank mergers altogether when a banking market fails the HHI
screening. Instead, they require the merging banks to sell some of their branches to a
third-party bank with no prior presence in the offending market. This is known as branch
divestiture. The purpose of branch divestiture is to maintain a high level of competition in
banking markets that would otherwise become non-competitive due to a merger. The details
of which branches are divested and to whom they are sold are negotiated between regulators
and banks, but regulators generally require that the former branches of the absorbed bank
are the ones divested.
Regulators monitor the divestiture process to ensure that divested branches remain com-
petitive after they are sold. To keep banks from sabotaging their divested branches, banks
must bundle together each customer's complete bank services, including loans, deposits, cre-
dit cards, and so on, and all of these must be divested together or kept together. Potential
buyers of divested branches must also prove that they are sufficiently large and experienced
before they are allowed to buy the branches.8 Finally, regulators monitor divested branches
for several years to ensure that the level of competition stays high in the banking market. Pil-
loff (2002) and Burke (1998) provide empirical evidence that the branch divestiture process
works well and divested branches remain competitive.
1.5 Data Sources and Summary Statistics
This section describes summary statistics for the sample used to identify the effects of bank
competition. The data comes from several sources, including the FDIC Summary of Deposits
Database, Call reports, RateWatch survey data on certificate of deposit (CD) rates, loan data
from commercial mortgage-backed securities (CMBS), deeds records, and the 2003 Survey
of Small Business Finances (SSBF).
8Regulators also carefully negotiate which branches are spun off to minimize disruption. Most often,
the branches being spun off belong to the bank being acquired, to prevent customers from re-opening their
accounts at a different branch of their old bank. Regulators may also accept a divestiture of branches by the
acquiring bank, but they rarely involve a mix of the two (Pilloff, 2002; Burke, 1998).
20
This paper will exploit the HHI = 1800 cutoff rule as the basis for its empirical variation.
As I will show in Section 1.6, banking markets whose HHI falls narrowly above the cutoff
have a far greater chance of failing regulators' quantitative screening than markets narrowly
below the cutoff. The main empirical specification will study only those banking markets
where the HHI rose by at least 200 points and was predicted to fall within 500 points of
1800. That is, markets involved in mergers where the HHI was between 1300 and 1800. This
includes 200 banking markets involved in 348 mergers. (Not all data sources are available for
the full set of mergers and markets, however.) I estimate the effects of competition on bank
behavior in data from the FDIC Summary of Deposits Database, using bank call reports,
and using loan-level microdata from deeds records. For these three datasets, the summary
statistics shown here are only for the sample of banking markets used in the main regression
specifications.
1.5.1 Merger and Branch Summary Statistics
I use the FDIC Summary of Deposits (SOD) database to investigate bank mergers. For
each banking market involved in a merger where both the surviving and purchased bank
have branches, I calculate: 1) The HHI immediately before the merger takes place, or the
pre-merger HHI; 2) The HHI that would result if the merger went through as planned and
no local branches were divested, the predicted HHI; 3) The difference between these, the
predicted change in HHI due bank mergers. The Federal Reserve Bank of St. Louis provides
a free online tool, CASSIDI, which performs these calculations for all bank branches that
are currently in place. I verify the accuracy of my calculations by showing that they are the
same as those calculated by the CASSIDI tool when applied to current branches.
Table 1.2 shows summary statistics for the sample of banking markets involved in bank
mergers where the change in HHI is at least 200 points. For each banking market, I combine
branching data from the SOD with market-level population and income averages from the
U.S. Census Bureau and the Quarterly Census of Employment and Wages (QCEW). The
21
banking markets in the sample are medium-sized towns: The population is 218,200 people,
and median house price growth is 3.6%, which is below the national average during this
sample period. The average banking market HHI is 1996, equal to about five equally-
sized banks. The average number of banks is 19, however, which means that deposits are
concentrated in a handful of large banks, but there are many small banks as well, each having
small market shares. Finally, the median bank in these banking markets has, on average,
116 branches, indicating a large presence for major national and regional banks.
1.5.2 Deposit Rates
Data on retail deposit rates is provided by the firm RateWatch. This dataset includes
branch-level retail deposit rates nationally. Banks hire RateWatch to conduct surveys of
their competitors' interest rates in order to compete effectively.
Because interest rate data is collected at the request of banks, coverage varies by market
and by year. However, it is nearly comprehensive for the entire urban U.S. beginning in 2000.
I use exclusively deposit rates data for $10,000 CDs, which I match to the closest-maturity
T-Bill rates to calculate spreads. I calculate the average of these across all rate-setting
branches in the market to calculate the market-by-maturity average spread. Overall market-
level spreads are the average of each of the maturities.
RateWatch deposit rate data is widely used to investigate the effects of competition, for
example by Drechsler et al. (2017) and Azar et al. (2016).
1.5.3 Bank Cross-Sectional Statistics
Bank-level data comes from publicly-available Call reports. I select a sample of local banks
with at least half of their deposits located in a single banking market. There are two reasons
to focus on local banks. First, the variation in bank competition I use is regional, so to
estimate its effects I must identify banks within a particular region. Second, the Charter
Value Hypothesis models the effects of competition which affect a bank's entire operations.
22
This is most relevant for local banks.
I divide bank variables into three groups: Bank scale, capital structure, and lending
behavior.
" Bank scale: Total assets and total bank lending.
" Capital structure: Tier 1 Capital Ratio, Equity/Total Assets, and Deposits/Total As-
sets. A bank has a riskier capital structure when any of these ratios is lower.
" Lending behavior: The non-performing loan ratio (NPL) and loan loss reserves (LLR)
measure the riskiness of the loans. The NPL ratio is the fraction of all loans that are
90+ days delinquent, an ex post measure of bank risk-taking. Loan Loss Reserves, also
measured as a fraction of total loans, are held in case of future non-performance and
so are an ex ante measure of risk taking. I measure small business lending using data
by loan size. Interest and total earnings measure incumbent banks' size.
Summary statistics of bank characteristics for pre-merger years are shown in Table 1.3. The
sample used in this paper encompasses banks with at least half of their deposits located in a
banking market. The average bank has $531mn in loans and $921mn in total assets, although
the medians are only $28mn and $45mn respectively, indicating a right-skewed distribution
of bank characteristics by market. In this sample, banks have a loan loss reserve ratio of
1.5% and an NPL ratios of 0.8% on average. They have an equity/assets ratio of 10% and
a slightly higher Tier-1 Capital/Risk-Weighted Asset Ratio of 15%. Because these are local
banks, they are heavily deposit-reliant, with a deposit/assets ratio of 84% on average.
Further details about bank sample selection and variable construction are available in
Appendix 1.13.2.
1.5.4 Commercial Mortgage Statistics
I study the effects of bank competition on CRE lending using data on commercial mortgages.
There are two main sources of loan-level data: Deeds records from CoreLogic and CMBS
23
data provided by Trepp.
Companies that sell or mortgage their property generally record their transactions by
filing deeds records with their county recorder. In most states, this is required by law. Even
when not required by law, lenders typically require official recording. This both provides
official documentation of land ownership and allows potential lenders to keep track of bor-
rowers' existing debts. Once recorded, deeds transactions are available to the public, but
collecting this data often requires a visit to the County Recorders office for every county of
interest. I use data hand-collected by the company CoreLogic, which has a national staff
that visits county recorders offices for every U.S. county. The CoreLogic data is widely used
in research on residential real estate, but it is just as valuable for tracking CRE. Geographic
coverage is spotty in the 1990s but becomes nearly comprehensive by 2000.
The available sample includes deeds records from banking markets where mergers take
place in which the predicted HHI is 1800-2800 and the change in HHI is at least 200 points.
This sample includes 63,783 properties in 179 counties which are part of 109 banking markets.
Included are years 1994-2015, or whatever years are available for each market.
Deeds records are available at the transaction level. The key variables are property price
(if a sale occurs), mortgage amount and lender (if a mortgage exists), deed type, property
location, and owner name and address. I focus on mortgage transactions and drop sales with
no mortgage. Because many mortgages are used to roll over or refinance existing debt and
therefore do not correspond to a sale, I extrapolate prices from previous or future sales to
estimate property values and LTV ratios when prices are not available. (Details on this are
available in Appendix 1.13.2.)
My empirical variation affects the degree of bank competition in a single banking market.
Therefore it is important to distinguish between mortgages from local banks, that are directly
affected by competition, and mortgages from non-local banks, which are only indirectly
affected. To distinguish local from non-local mortgages, I create an indicator variable equal
to 1 if the borrower and the lender are located in the same city.
24
Table 1.4 shows summary statistics of the deeds records sample. The median mortgage
has a value of $190,000 on a property with value $243,000, leading to an LTV of 80%.
However, these variables are right-skewed, leading to an averages that are much larger than
the medians. Furthermore, in the sample, 61% of mortgages include a price and so are likely
part of a property sale. In 31% of cases, the address for the lending bank lists the same
city as the property owner mailing address. Only 1.1% of the mortgages are for construction
loans.
Detailed loan-level data on securitized mortgage loans comes from a database provided by
Trepp. This database covers the near-universe of the securitized mortgage market, including
data from 1998-2015. The sample used here includes all commercial property mortgages
for either offices or retail space (i.e., excluding multifamily residential and less common
property types such as hotels, storage units, mixed-use, etc.) Summary statistics for this
database are shown in Table 1.16. CMBS loans are larger than bank portfolio loans, with
an average amount of $15mn. They also tend to be issued in properties located in the
largest U.S. cities and during times with high demand for securitized products, such as
2004-2006. Because CMBS loans are common only in a small number of cities, this data
is more useful for understanding loan attributes than for estimating the effect of regional
changes in competition.
To understand how different types of borrowers use commercial mortgages, I use data from
the 2003 Survey of Small Business Finances. This data comes from a survey of 4,240 small
businesses conducted by the Federal Reserve Board from 2003-2005. It contains detailed
data on financing and borrower/lender characteristics. Summary statistics are shown in
Table 1.17 for the 697 businesses in this survey with a mortgage. The average small business
with a mortgage has 13 employees, $1.18m in assets, and $795,000 in debt, of which $583,000
is the mortgage. The median distance from its primary bank is 1 mile, with 85% having
their primary bank within 10 miles and 96% within 25 miles. Regional identifiers are not
available in this data, so I use it to study cross-sectional borrower characteristics rather than
25
estimating difference-in-differences specifications.
1.6 Empirical Strategy
This paper's empirical variation exploits the heterogenous application of antitrust laws in
banking markets above and below the 1800 HHI cutoff. Regulators do not require branch
divestiture in banking markets where the predicted HHI rises by at least 200 points to a
level below 1800. When the predicted HHI rises by at least 200 points to a level above 1800,
however, regulators do require branch divestitures. This means that mergers in very similar
banking markets can have very different effects on the level of bank competition, depending
on which side of the HHI cutoff their HHI falls. To evaluate the effects of bank competition,
I compare the change in competition and bank behavior in markets above and below the
HHI=1800 cutoff.
This section describes the estimation strategy I use to exploit the 1800 HHI policy cutoff
as well as the assumptions required for this to be a valid source of identifying variation. It
also provides empirical evidence that supports the assumptions.
1.6.1 Difference-in-Differences Design
Figure 1-1 shows the predicted HHI and predicted change in HHI for every banking market
involved in a merger where both the acquiring and absorbed bank had branches between
1994 and 2015. Banking markets that are part of more than one such merger appear once
for each merger. The upper-right quadrant of the figure shows branches where the predicted
change in HHI is at least 200 points and the predicted post-merger HHI level is at least 1800.
The mergers taking place in these markets are flagged in the quantitative antitrust screening
used by bank regulators, which in generally causes regulators to require branch divestitures.
I limit my analysis to markets within a 500-point range of 1800 in order to control for the
fact that markets far above or below the 1800 cutoff may be very different from each other,
26
and these differences could cause banks in these markets to react to mergers differently for
reasons that have nothing to do with regulator intervention. 9 Hence the treatment group
is defined as markets involved in mergers, where the predicted HHI increase is at least 200
points and the predicted HHI level is within only a 500-point range of the 1800 cutoff, i.e.
1800-2300. Likewise, the control group is defined as markets involved in mergers where the
predicted HHI increase is at least 200 points but the predicted post-merger HHI level is
1300-1800. The treatment and control groups are marked in Figure 1-1.1o
The main identification strategy used in this paper is a two-way fixed effects, difference-
in-differences style estimator which compares treated and untreated banking markets before
and after mergers occur. Equation 1.1 is the main regression specification.
Yt = 31POSTt + 02 ANTITRUST x POSTit + +yt  6 + /3 xzt+ Fit (1.1)
The main control variables include: Market fixed effects (6i), which control for time-
invariant heterogeneity in market characteristics; and year fixed effects (-yt), which control
for national changes in bank lending that may be correlated with the timing of bank mergers.
Since markets may appear more than once if they are involved in multiple bank mergers, each
market has a different fixed effect each time it appears." The main dependent variables are
measures of bank competition and bank lending behavior. An ANTITRUST main effect is
unnecessary because it is banking market-specific and therefore is collinear with the market
fixed effects 6i. For robustness checks, I also include time-varying market-level controls Xit.
Standard errors are clustered by banking market.
The coefficient on #2 estimates the difference in post-merger behavior between treated
and control markets due to the heterogeneous application of antitrust law. The interaction
term ANTITRUST, x POSTi is equal to one only in years following mergers in treated
9Hertzberg et al. (2011) and Mello (2017) use similar strategies to exploit interventions that are applied
with fuzzy cutoff rules.
10Figure 1-7 shows a map of the treatment and control markets; they are evenly distributed throughout
the country and tend to be small- to medium-sized cities.
"Monte Carlo simulations show that this yields unbiased estimates of the coefficient of interest.
27
markets (where intervention is required). I refer to markets where ANTITRUST = 1 as
"treated" markets. Because bank regulators typically do not announce when they intervene in
banking markets, 12 is an intent-to-treat (ITT) effect which measures the difference between
markets where divestitures are required by antitrust rules and markets where they are not
required.
The coefficient on POSTt, i1, estimates the change in the independent variable from the
pre-merger period to the post-merger period, for markets where no intervention is required
and branches may be combined. POSTit is equal to 1 in all years following official merger
announcements and equal to 0 in years prior to announcements (the year of the official merger
announcement is dropped). This value of this coefficient includes two combined effects. The
first is the effect of the merger itself, which reduces the level of competition in each banking
market. The second is changes in market-level bank behavior relative to other markets at
that time, which coincide with the timing of the merger and may cause mergers to occur.
The main dependent variables measure total bank lending, borrower composition, and
bank risk-taking. The first set of dependent variables measure total lending. The total
lending measures I study in Call Reports are total bank lending and small business lending.
To measure small business lending separately, I use the "Loans to Small Businesses and Small
Farms" variables scaled by overall bank lending. In loan-level deeds data, I simply study the
total volume and number of loans originated in each year, which includes both refinancing
and new originations. In both datasets, I separately study lending by borrower size. Call
reports define borrower size using loan amount buckets of $0-$100,000, $100,000-$250,000
and $250,000-$lmn, and in deeds records I study loans to borrowers with collateral above
and below the median value of $243,000. Borrower size is important to study because it is
closely linked to banking theory. Petersen and Rajan (1994) argue that the long-term project
mechanism is most relevant for the very smallest and newest firms because banks must make
the greatest effort to learn about them. Confirming the results in Petersen and Rajan (1994)
and Berger et al. (2005), Table 1.18 shows that more established small businesses have more
28
impersonal relationships with their mortgage lenders and are more likely to borrow from
a distant lender, suggesting that large borrowers have easier access to outside sources of
finance.
The second set of dependent variables measure borrower composition. I estimate the
effect of competition on average borrower size as well as whether borrowers and lenders are
located in the same city. Both of these variables are in deeds records.
The third set of dependent variables measure bank risk. I study loan risks and capital
structure risks separately. Call reports contain data on non-performing loans (NPLs) by loan
type, which are a measure of ex post risk, as well as loan loss reserves, which are a measure
of ex ante risk. Deeds data does not contain delinqucncy information, but I measure loan-
to-value ratios which are closely related to risk. I also note that risk and borrower size are
closely related, as large borrowers are less delinquent in CMBS records (Table 1.19). To
study capital structure risks, I use bank-level data on leverage, deposit reliance and Tier 1
Capital Ratio.
1.6.2 Identifying Assumptions
Differences in competition across banking markets may be correlated with differences in
investment opportunities and borrower characteristics, biasing typical estimates of the rela-
tionship between competition and lending.1 2 Because of the difference-in-differences design,
the identifying assumption in this study is weaker than what is typically needed: I need only
assume that incumbent banks' response to a merger of their competitors would be the same
in treatment and control markets.
As antitrust intervention is determined by a plausibly exogenous regulatory cutoff, the
identifying assumption - that treatment and control banks would react similarly to the
merger of one of their competitors - is highly plausible. The next section will provide three
further pieces of evidence to support it: First, I show that mergers are not self-selected in
12For example, banks may choose to enter banking markets where they believe investment opportunities
will increase, leading to a spurious positive correlation between lending and competition.
29
anticipation of antitrust enforcement. Second, the estimates are not due to spurious ex ante
differences in bank or market characteristics. Third, there is no direct affect of competition
on the structure of banks in the sample.
Bank mergers are not self-selected in anticipation of antitrust enforcement
If banks decide not to merge because they know that regulators will require branch dives-
titures in some of their markets, then the mergers that occur in spite of this might be a
select sample, which could cause a sample selection bias. I provide three pieces of evidence
to argue that this is not the case
First, bank markets typically involve multiple banking markets. The acquiring and ab-
sorbed banks also generally share branches in many banking markets, and antitrust remedies
are generally acquired in no more than a few of these. Therefore, as long as violating bank
markets are not pivotal for banks' merger decisions, it is plausible that this assumption is
satisfied. Further, the main regression results are very similar in a sample of bank mergers
where the absorbing and acquired banks both have branches in multiple banking markets.
Second, there is no evidence that bank mergers are avoided when they might cause
potential antitrust violations. Figure 1-4 shows the density of predicted HHIs in banking
markets where mergers occur, limited to a sample where the HHI increase is at least 200
points. If mergers were being avoided because of anticipated antitrust violation, one would
expect to see fewer mergers just above the 1800 threshold, but this is not the case.
Third, if banks were failing to merge to avoid antitrust rules, they might manipulate the
HHI in order to avoid the cutoff. The easiest way to do this would be to reduce their deposits
in order to decrease a market's HHI. Figure 1-8 shows bank deposits for branches near the
threshold and further away, but there is no trend in deposits around the time of mergers in
either group.
30
No effect in placebo tests of markets with similar characteristics
Banking markets where antitrust is applied have a higher ex ante HHI than markets where
antitrust law is not applied. The difference in HHI is small, as I study mergers in a narrow
range of 1800, but a potential concern is that the differential effect of bank mergers is a
direct effect of the difference in ex ante HHI in itself. To alleviate this concern, throughout
the paper I re-estimate the specifications in a placebo sample of bank mergers where the HHI
increase is below 200 points. These banking markets have a differential ex ante HHI level
just as the main sample does, but are unaffected by antitrust law because the HHI increase
is smaller. If ex ante differences in HHI levels had a direct effect on merger responses, one
would expect to estimate an effect of mergers in this placebo sample. I perform further
placebo tests using the sample of bank mergers where the HHI increase is above 200 points
but the antitrust "cutoff" is set to a placebo value different from the true cutoff.
Table 1.22 estimates the difference in several key variables between treated and untreated
markets in the pre-treatment period for several of the most important bank-level variables
I study. Of the six variables, only one is statistically significantly different between these
groups, at the 10% level.13
As further evidence, I include as control variables the interaction between ex ante bank
and market characteristics and the POST indicator. The inclusion of these controls does
not change estimates. These robustness checks reduce the likelihood that the results could
be driven by heterogeneous local bank characteristics.
Competition does not affect structure of incumbent banks
Previous research has shown that bank scale and structure affect lending behavior (Williams,
2017; Berger et al., 2005). If incumbent banks' size or structure changed in response to
changing competition in a way that was different in treatment and control markets, the main
13Pre-treatment balance between treatment and control markets is not an identifying assumption in this
setting, but balance on pre-treatment levels increases the plausability of parallel trends as well.
31
results could be due to changing bank size rather than changing competition. However, Table
1.20 shows that the incumbent bank size and branch network do not change as a result of
changing competition. As an additional robustness check, I control for time-varying average
bank characteristics at the market level.
1.7 Evidence That Antitrust Laws Are Applied Properly
The empirical design relies on the correct application of antitrust rules. This section provides
evidence that antitrust rules indeed affect bank competition, as they are intended to. It first
examines the number of branch spinoffs in markets above and below the 1800 cutoff, and
then shows how this affects the market-level HHI.
1.7.1 Branch Spinoffs Following Mergers
Figure 1-5 shows the fraction of bank branches spun off by merging banks in markets both
above and below the HHI=1800 cutoff, and above the AHHI > 200 cutoff. The figure me-
asures branches sold to competitors by merging banks within three years of bank mergers.
In markets where the predicted HHI is below 1800, about 2% of branches are sold to compe-
titors, whereas in markets above the 1800 cutoff, 7%-10% are. This indicates that antitrust
rules on average affect about 5% of merging bank branches. The 2% of branches sold to
competitors below the 1800 cutoff may be because regulators require antitrust remedies even
though the market passes the quantitative screening. They may also reflect normal bank
behavior, as the changes in ownership are not necessarily caused by regulatory requirements.
The 7%-10% of branches that are spun off above HHI=1800 are only required to be enough
for banking market concentration to return to HHI=1800. Mergers that lead to a higher HHI
level require more branches to be divested to restore the level of competition to what it was
before. Appendix Figure 1-10 replicates Figure 1-5, limited to markets where the predicted
change in HHI is below 200 points - a placebo test. There is no discontinuity across the
32
1800 cutoff for this sample.
The timing of branch spinoffs is shown in Figure 1-9. Spinoffs do not always happen in
the year of bank mergers but may happen over the course of several years - as many as five
years post-merger. Regulators allow banks to spend several years searching for a well-run
buyer who will pay a fair price for the divested branches. This means that the difference in
competition between the treatment and control markets can take several years to emerge.
A fraction of banks below the official cutoff are sold, either because banks decide they are
no longer needed post-merger or because regulators intervene in these mergers despite not
being required to do so under official screening criteria.
To ensure that branch divestitures lead to greater competition, regulators require that
acquiring banks be large and well-run - and do not have a prior local presence. Prior to
mergers, these banks have almost no branches in the market where intervention occurs, but
the banks have a large branch network elsewhere. Following mergers, they own a substantial
number of branches in the market with intervention.
1.7.2 Effect of Intervention on HHI
Estimates indicate that the rules are effective at lowering bank concentration. Table 1.11
shows the average effect of antitrust rules on the HHI, estimated using Equation 1.1. In non-
intervention markets, the HHI increases by 363 points following mergers with no antitrust
intervention, but it increases by 180 points less less in markets where antitrust law applies.
Estimates are similar using year fixed effects. Tables 1.13, 1.14 and 1.15 show that there is
no estimated difference between treatment and control markets when using placebo cutoffs.
Figure 1-2 is an event study graph showing how the HHI changes year-by-year before and
after mergers occur. Prior to mergers, the HHI moves in parallel in treatment and control
markets. Following mergers, the HHI initially rises in both groups, before declining to below
its pre-merger level in treated markets, as the treated bank divests branches.
33
1.7.3 Effect of Intervention on Certificate of Deposit Rates
Price-based measures of competition are better than concentration-based measures such as
the HHI. This is because price-based measures take into account market contestability and
actual competitive behavior (Berger et al., 2004). Table 1.6 shows estimates of the treatment
on certificate of deposit (CD) rates at incumbent bank branches. Placebo event studies and
estimates show anomalous behavior in the years immediately around merger announcements,
possibly due to the disruptive effects of mergers on data collection. Therefore I exclude data
collected within 3 years of mergers in estimates of Equation 1.1.14
Estimates suggest that required antitrust rule application is associated with 10-18 basis
point (0.1 to 0.18 percentage point) change in CD spreads. The effects are larger for longer
maturity CDs. This is not just an artifact of their higher rates, as estimates are larger in
percentage terms as well.'
Figure 1-3 is an event study graph showing the difference between treated and untreated
banking markets around the time of mergers. CD rates rise significantly relative to what
they were pre-merger in treated markets and stay elevated indefinitely even though the
HHI does not fall in these markets and even rises immediately following mergers. Antitrust
remedies may actually raise the level of competition in treated markets compared to their
pre-treatment degree of competition. This is because regulators replace a generally small
(and recently acquired) bank with a new outside competitor. Regulators also ensure that
the bank which acquires divested branches is competitive and well-run.
14Estimates are noisier but similar including these years.
15A plausible explanation for this is that competition has greater effect on longer-dated CDs because they
have a greater demand elasticity, as it is more worthwhile for consumers to spend time finding a better rate
when their money is tied up longer.
34
1.8 Empirical Estimates: Effect of Competition on Len-
ding
This section presents estimates of the effect of competition on bank balance sheets and loan
market characteristics. Combining loan- and bank-level estimates with cross-sectional facts
about CRE loans, a unified picture emerges about the effect of competition on business
lending which largely supports the predictions of the market power mechanism.
1.8.1 Overall Small Business Lending
In both bank-level and loan-level data, greater competition leads to more lending for small
businesses, but only for the largest borrowers within this category. Table 1.7 estimates
the effect of competition on small business CRE lending as a fraction of banks' total CRE
lending. For loans below a value of $250,000, I estimate no effect of competition on small
business lending. However, for loans from $250,000-$1,000,000, competition increases total
lending by of 3% of banks' total CRE lending, an affect which is statistically significant at
the 1% level. As I estimate an increase in lending for these borrowers, and no decrease for the
smallest borrowers, the estimates are most consistent with the market power mechanism. 16
Small business lending estimates from Call reports are scaled by banks' overall lending in
order to increase precision, as bank lending is noisily measured when left unscaled. Therefore,
I confirm the bank-level estimates using deeds records aggregated to the banking market
level. Results are shown in Table 1.8 and are consistent with the bank-level estimates. The
dependent variable in this table is total CRE loan origination volume for banking markets
and years with at least 30 transactions. I estimate that competition is associated with an
increase in CRE originations, both in terms of the number of loans and the loan volume.
Consistent with the Call Report estimates, I find a large and statistically significant effect
of competition on loans of above-median size but not for loans below median size. This is
16 Placebo checks are shown in Tables 1.32, 1.33 and 1.34. Estimates for C&I lending, which show no
statistically significant effect, are shown in Table 1.31.
35
driven by an increase in the number of loans, rather than large loans, as the effect on loan
count and loan volume are of a similar magnitude. While an estimated effect of 0.3-0.4 may
seem large (approximately 30%-40%), these estimates this do not mean that the amount of
borrowing or number of purchases increases by 0.3-0.4 log points, as the mortgages could
be used to refinance existing debt or to make property purchases that would otherwise be
financed in some other way or purchased in cash.1 7
Thus the first result is that estimates from both bank call reports and loan-level deeds
records imply that competition increases lending to small businesses. This is true even as
overall bank assets and liabilities, shown in Table 1.12, do not change in a statistically
significant way. In both datasets, I estimate a statistically significant and large effect for
the largest CRE borrowers, and positive but small and not statistically significant effect for
the smallest borrowers. These estimates support the market power mechanism, as an overall
increase in lending is one of this mechanism's main predictions. By contrast, they are less
consistent with the long-term lending mechanism, which would imply a decrease in bank
lending due to competition.
1.8.2 Borrower Composition
The second result is that greater competition is associated with an increase in the average
CRE borrower size, consistent with the overall increase in lending I find for large borrowers
(and providing further support for the market power mechanism). Tables 1.9 and 1.10 show
estimates of the effect of competition on borrower characteristics in deeds data. Greater com-
petition is associated with an increase in the average borrower size (measured by collateral
value) of 10%, shown in Column 2 of Table 1.9. These borrowers receive larger mortgages,
with little change in LTV ratios (Column 3). Businesses also borrow more locally, as the
fraction of borrowers whose lender is located in the same city increases by 5% (Column 4).18
17Since the sample of deeds records available only includes those where AHHI > 200 and 1300 < HHI <
2300, placebo checks are not possible in deeds data.
18Data is available to me only for the set of markets where the main treatment variable is defined, so it is
not possible to do placebo checks using alternative HHI cutoffs.
36
Further, I estimate a tight link between the increase in local borrowing and the increased
borrower size. Table 1.10 partitions the sample into above- and below-median sized loans
(Columns 2 and 3), and loans originated by lenders from other cities versus the same city
(Columns 4 and 5). These estimates show that it is mainly the the larger borrowers who
are switching to local banks, and similarly, it is the local banks whose average borrower
size increases. It is not surprising that the effects of competition are greatest for larger
borrowers, as they are generally more likely to borrow from far away and may have an easier
time switching lenders because they are less reliant on close relationships with banks. The
finding that borrowers switch from distant to nearby finding is thus a direct theoretical
implication of the market power channel.
1.8.3 Bank Risk and Capital Structure
The third result is that that competition is associated with lower loan risks at the bank level,
as measured by NPLs, and no change in capital structure, shown in Table 1.11. In treated
markets, the non-performing loan ratio declines by 0.38 percentage points for all loans and
by 0.34 points for real estate loans. I do not estimate an effect on NPLs for C&I lending.
The loan loss reserve ratio declines by 0.04 percentage relative to untreated markets, but this
change is not statistically significant. The smaller decline in loan loss reserves may indicate
that banks were not aware that their lending was becoming more risky, although due to noise
in the estimates I cannot reject a large negative effect. These findings are consistent with
the market power channel, with the long-term lending channel, or with Boyd and De Nicolo
(2005). Finally, table 1.29 splits banks into those above and below the median size by total
lending. The estimated effect on loan risks is larger for banks above the median size. As
small banks are more relationship-dependent than large banks, this finding suggests that the
decrease in risk was not due to changes in the nature of bank relationships. CMBS records
show that large borrowers become delinquent less often than small borrowers do, implying
that the increase in borrower size may be the reason that the non-performing loan ratio falls.
37
Competition is associated with no statistically significant change in overall bank size
or capital structure, shown in Table 1.12. The estimated effect of competition on banks'
capital structure is near zero and precisely estimated, capital structure is measured as the
ratio of equity to total assets, deposits to total assets, or the ratio of Tier 1 Capital to Risk-
Weighted Assets. The effect of competition on bank size is also not statistically significant
but is measured with more noise and is roughly -7%.
Comparing these results to the empirical predictions described in Section 1.3 shows that
the evidence is most in line with the predictions of the market power channel. Contrary
to the predictions of the Charter Value Hypothesis, bank-level estimates show that greater
competition is associated with less risky lending and no change to bank capital structure.
The long-term lending channel predicts a shift towards'larger borrowers, as I find, but also
predicts a decrease in lending to the smallest borrowers, which I do not find.
1.8.4 Discussion
Why does this paper not find evidence in support of the Charter Value Hypothesis or re-
lationship lending mechanism, when the results from many previous papers have supported
these theories? There are three possible reasons why the results in this paper differ from the
findings in previous studies. First, much of the previous evidence has been based on cross-
sectional estimates of the relationship between bank behavior and competition across markets
or countries, whereas this paper studies a source of exogenous variation from economic po-
licy. There are both advantages and disadvantages to using exogenous policy variation. The
main advantage is that it deals with concerns about the endogeneity of bank mergers. The
main disadvantage is that the effects estimated in this paper apply to the particular margin
of bank competition that is determined by antitrust laws. Variation in bank competition
on other margins might have different effects. For example, risk shifting incentives may be
particularly strong for banks near bankruptcy, so increases in competition may induce these
banks to make riskier loans when it has no such effect in general. Nonetheless, the results in
38
this paper are still highly relevant as antitrust law is an important margin for policy-making
and the estimates may be more generally applicable than results from banks in extreme
circumstances.
The second reason for possible differences is that other models may be more relevant
for types of financing that this paper does not study. For example, the loan-level estimates
presented here come exclusively from CRE loans. However, it could be that, because CRE
loans are collateralized, relationship lending motives are less important in this sector than
for loans with less collateral. The null results I estimate for the effects of competition on C&I
lending, for example, may be because the positive competitive effects of the market power
mechanism and the negative competitive effects of the long-term project mechanism cancel
each other out in the market for C&I lending. As CRE loans are the single largest source
of financing for small businesses, and the estimates from bank balance sheets include a wide
range of banking products, however, the estimates in this paper are economically relevant.
The third major difference between the methods in this paper and previous studies is
that, in the language of Berger et al. (1999), I focus on the "external" effects of bank mer-
gers, rather than the "internal" effects. The internal effects of bank mergers are those that
affect the merging bank itself whereas the external effects are those that affect competitor
banks through changing market structure. As an example of research that studies the in-
ternal effects of bank mergers, a substantial literature has studied how statewide branching
deregulation in the United States affected financing, growth and economic activity (e.g., Jay-
aratne and Strahan, 1998; Demsetz et al., 1996; Rice and Strahan, 2010). A second example
is Williams (2017), which studies the internal effects of bank mergers on banks' responses to
monetary policy. These papers address a different set of models from the ones studied here,
and therefore yield complementary but different results. Estimates of external effects of bank
mergers address theory about the effects of bank competition on bank behavior rather than
theory about the effects of bank size or management.
39
1.9 Conclusion
This paper investigates the effects of competition on small business lending using a new
source of exogenous variation in the competitive impact of bank mergers. The estimates show
that greater bank competition is associated with more lending to above-median-sized small
businesses and decreased risk at the bank level. However, the effects of greater competition
are unevenly distributed. In both bank- and loan-level data, I find that lending increases
for the largest borrowers and has no effect on the smallest. This does not mean that small
borrowers do not benefit, however, as they may be paying lower interest rates for the same
loans. Part of the increase in lending to large borrowers is because they switch from borrowing
outside of the local market to borrowing from local banks.
These results emphasize the role of banks as specialists in the efficient allocation of
capital to the economy whose effectiveness is improved when competition rises. My results
provide less support for models that emphasize banks' ability to maintain long-term lending
relationships or that model banks as entities optimizing their loans along a risk-reward
frontier. Further, the class of models I support imply a "light side" rather than a "dark side"
to bank competition.
The increase in bank concentration since the passage of the 1994 Riegle-Neal Act has
mirrored a rise in concentration across all U.S. industries. The estimates in this paper
suggest that rising bank concentration is a concern from the perspective of efficient capital
allocation. However, the estimates also imply that antitrust rules may be a valuable policy
tool for increasing bank competition.
40
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45
1.10 Figures
Figure 1-1: Predicted HHI and predicted AHHI in all markets
Predicted ex post HHI and predicted change in HHI for every commercial bank or bank
holding company merger in the United States, 1994-2015. Source: Author's calculations
using FDIC Summary of Deposits Database.
0
0n
* I
* . .1
0:C
.1
0 . I.
- . I.
40 I.
00 I -~
t I
a. I.
.v-*s ,~;.
. 1* . . Treated
)
.~ ~*
Non-Treated
%*
0
r-4
0 -
O0 200 400 600 800
Change in HHI
Each point is a combination of one market and one market. Data from merger simulatior
result of 5614 mergers. Calculations from FDIC SOD data, 1994-2006 2009-2015.
46
Figure 1-2: HHI Event Study Graph
Event study graph of deposit rates. TREAT=1 are defined as mergers with a predicted HHI increase of at
least 200 points and a predicted HHI level of 1800-2300. TREAT=0 are defined as mergers with a predicted
HHI increase of at least 200 points and a predicted HHI level of 1300-1800. Lines created using event study
regression estimates from a specification of the form Rate = Zte [-4,8] fgjx TREAT x IEventTime=t + 3 eit
where event-times less than t < -4 are coded as -4 and event-times above t > 8 are coded as t = 8. Source:
FDIC Summary of Deposits Database.
4I-J
0
4I-J
>0
.C:
W
Cn
U
C0
0
- - - - - - - - - -
-3 -2 -1 0 1 2 3 4 5 6 7
Years relative to merger announcement
TREAT=1 (HHI >1800) _ ___ TREAT=O (HHI <1800
(Intervention) (No Intervention) I
Each observation is a market in a particular year. SE's clustered by market. Limited to
mkts with AHHI>200. Source: FDIC SOD, 1994-2006 and 2009-2015.
47
Figure 1-3: CD Rate Event Study
Event study graph of deposit rates. TREAT=1 are defined as mergers with a predicted HHI increase of at
least 200 points and a predicted HHI level of 1800-2300. TREAT=0 are defined as mergers with a predicted
HHI increase of at least 200 points and a predicted HHI level of 1300-1800. Lines created using event study
regression estimates from a specification of the form Rate = &C [-4,8] fgt x TREAT X IEventTime=t 8 + Eit
where event-times less than t < -4 are coded as -4 and event-times above t > 8 are coded as t = 8. Source:
RateWatch.
0.
.a n
0
4-111
00
41-J
L
- - -N
CN
C- 0
fa- Yeroeaiv omre anucmn
TRA= (HH > 
U -3 IN0 -2 TRET= -1 (H I<800 1 2 3 4 5 6 7
Years relative to merger announcement
____TREAT=1 (HHI >1800) ____TREAT=0 (HHI<1800'
(Intervention) (No Intervention)
Each observation is a market in a particular year. 
mkts SE's clustered with AHHI>200. by market. Source: Limited Author's tocalculations from Ratewatch.
48
Figure 1-4: Density of HHI around HHI=1800 cutoff for realized mergers
Predicted ex post HHI for bank mergers with a predicted HHI increase of at least 200 points. Mergers are
those with merger dates from 1994-2015. Source: FDIC Summary of Deposits Database.
0~
C
L_
U-
1000 1500 2000 2500 3000
Predicted post-merger HHI
49
Figure 1-5: Density of HHI around HHI=1800 cutoff for realized mergers
Fraction of branches spun off within two years of bank mergers, by predicted HHI for mergers with a predicted
HHI increase of at least 200 points. Mergers are those with merger dates from 1994-2015. Source: FDIC
Summary of Deposits Database.
0 q
C
=3
-ce
CL
C
L.
0
4j-
U
LL - - E
0) _J
<800 1300-1800 2300-2800
800-1300 1800-2300 >2800
Post-Merger HHI, AHHI>200
50
1.11 Tables
Table 1.1: Empirical Predictions from Banking Theory
This table shows the main empirical predictions from theories of bank competition. See Section 1.3 for more
details.
Effect of competition Long-Term Market Charter
Project Power Value
Mechanism Mechanism Hypothesis
Total Lending Lower, esp. Higher, esp.
borrowers borrowers
with high with outside
initial options
investments
Borrower Composition Older, larger, Older, larger, Riskier
safer safer
Capital Structure Risker; run-
or
bankruptcy-
prone
51
Table 1.2: Banking Market Summary Statistics
Summary statistics of banking markets involved in mergers, that caused a predicted HHI increase of at least
200 points and a predicted HHI level of 1300-1800. Sources: U.S. Census Bureau (population), IRS Statistics
of Income (Wages and AGI), FDIC Summary of Deposits (bank statistics).
(1) (2) (3) (4) (5)
VARIABLES mean sd p1O p50 p90
Population (th) 218.2 370.4 23.50 107.7 462.0
Wages/Capita (th) 12.63 2.628 9.262 12.48 15.57
AGI/capita (th) 17.61 3.722 12.89 17.58 21.74
House Price Growth 3.569 2.153 0.865 3.647 5.976
Weighted HHI 1,996 849.1 1,343 1,739 2,832
Avg Branch Deposits 3,128 6,810 182.4 957.1 6,956
# Banks 19.20 19.06 8 13.85 34.17
Median Bank # branches 115.5 144.2 4.132 61.08 306.1
52
Table 1.3: Bank Summary Statistics
Summary statistics of average bank-level variables for banks located in main sample of banking
markets.The main sample of banking markets is defined as markets involved in mergers that caused a
predicted HHI increase of at least 200 points and a predicted HHI level of 1300-1800. Averages are taken at
the banking market level, and statistics are shown across banking markets for the years prior to bank
mergers. Includes data from 2,130 banks. Sources: Call Reports.
(1) (2) (3) (4) (5)
VARIABLES mean sd p10 p50 p90
CRE Ln <100k (mn) 2.28 5.27 0.00 0.93 4.96
CRE Ln 100k-250k (mn) 5.45 14.50 0.03 2.36 10.90
CRE Ln 250k-lmn (mn) 17.91 55.45 0.00 7.20 35.53
Loans (mn) 530.54 5,098.97 27.52 78.03 528.95
Assets (mn) 921.45 10,406.32 45.16 121.53 811.82
Loan Int. Inc. 19,434.96 181,936.67 1,131.85 3,025.62 19,986.42
1OOxLn Loss Reserves/Lns 1.46 0.55 0.86 1.35 2.22
100xNPLs/Lns 0.84 0.65 0.13 0.69 1.75
Equity/Assets 0.10 0.03 0.07 0.09 0.14
TI Cap Ratio 0.15 0.05 0.10 0.14 0.22
Deposits/Assets 0.84 0.07 0.74 0.85 0.90
53
Table 1.4: Deeds Records Summary Statistics
Summary statistics of business data for the 63,783 deeds records available in banking markets where mergers
occur, for mergers where the HHI increase is at least 200 points and the predicted HHI value is 1300-2300.
This corresponds to in 179 counties in 109 banking markets. Mortgages are weighted so that all banking
markets receive equal weight in the statistics. "Sale" is an indicator equal to 1 if a property price is recorded
that corresponds to the mortage. Properties with Sale=0 do not have a property price listed, so prices are
instead extrapolated using historical or future sales for the same property. Source: CoreLogic.
(1) (2) (3) (4) (5)
VARIABLES mean sd p1O p50 p90
Mortgage Amt (th) 1,311 20,891 44 190 1,150
Property Price (th) 742 3,798 63 243 1,350
LTV 3.8 313 .31 .8 1.7
Same City .31 .46 0 0 1
Sale .61 .49 0 1 1
New Construction .011 .11 0 0 0
54
Table 1.5: Rules lower HHI in short-and long-run
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank competi-
tion on market-level HHI. HHI is calculated as the sum of squared deposit market shares by bank, multiplied
by 10,000. TREAT is equal to 1 only for banks in banking markets where a merger leads to a predicted HHI
increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in banking markets
where a merger leads to a predicted HHI increase of at least 200 points to a level 1300-1800. POST=1 in
years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank mergers is
dropped. Standard errors clustered by banking market. Source: FDIC summary of Deposits database.
(1) (2) (3) (4)
VARIABLES HHI HHI Log(HHI) Log(HHI)
POST 362.8*** 344.3*** 0.183*** 0.178***
(55.90) (55.34) (0.0219) (0.0205)
t>=5 117.5** 0.0174
(58.63) (0.0227)
POSTxTREAT -179.6** -147.8** -0.0778** -0.0682**
(71.92) (59.81) (0.0313) (0.0264)
t>=5 X TREAT -68.08 -0.0185
(63.64) (0.0285)
Observations 5,635 5,635 5,635 5,635
R-squared 0.693 0.695 0.730 0.730
Market FE X X X X
Year FE X X X X
Clusters 207 207 207 207
55
Table 1.6: Difference in Differences results with $10k CD spreads by maturity
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank com-
petition on market-level CD spreads. Spreads calculated as difference between rate and nearest-maturity
constant-maturity Treasury rate. CD spreads of banks involved in each bank merger is dropped. TREAT is
equal to 1 only for banks in banking markets where a merger leads to a predicted HHI increase of at least 200
points to a level 1800-2300. TREAT is equal to 0 only for banks in banking markets where a merger leads
to a predicted HHI increase of at least 200 points to a level 1300-1800. POST=1 in years following bank
mergers, POST=0 in years prior to bank mergers. Limited to market-year combinations with at least CD
spread observations available. Observations within 3 years of relevant bank mergers are dropped. Standard
errors clustered by banking market. Source: Ratew
(1) (2) (3) (4) (5) (6)
Avg
VARIABLES 3M-3Y CD 3M CD 6M CD 1Y CD 2Y CD 3Y
POST -4.168 0.612 -2.832 -3.612 -5.596 -14.76***
(3.952) (4.570) (3.845) (4.149) (4.465) (4.592)
POSTxTREAT 13.02** 9.777* 12.82** 12.18** 13.58** 20.72***
(5.620) (5.351) (5.630) (5.568) (6.259) (7.180)
Observations 2,580 2,514 2,563 2,572 2,649 2,598
R-squared 0.906 0.918 0.907 0.887 0.873 0.858
Market FE X X X X X X
Year FE X X X X X X
Clusters 185 184 184 184 187 186
56
Table 1.7: Effect of Competition on Small CRE Loans
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a single
banking market and total loans of at least $20mn. Estimates weighted by bank loan market share within
banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at least four
local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a predicted
HHI increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banking markets
where a merger leads to a predicted HHI increase of at least 200 points to a level 1300-1800. POST=1 in
years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank mergers is
dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3)
Frac. CRE Lns Frac. CRE Lns Frac. CRE Lns
VARIABLES <100k 100k-250k 250k-lmn
POST 0.00201 -0.000446 -0.0314**
(0.00512) (0.00895) (0.0150)
POSTxTREAT 0.00812 0.00182 0.0311*
(0.00617) (0.0106) (0.0171)
Observations 18,213 18,664 18,645
R-squared 0.536 0.413 0.186
Market FE X X X
Year FE X X X
Clusters 98 98 98
57
Table 1.8: Effect of Competition on Loan Volume, Deeds Records
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank competi-
tion on aggregated CRE loan counts from deeds records. Limited to sample of office or commercial property
CRE loans and banking markets with at least 30 transactions. See Appendix 1.13.2 for more details on
data set construction. Each observation represents one market in one merger. TREAT is equal to 1 only
for banks in banking markets where a merger leads to a predicted HHI increase of at least 200 points to a
level 1800-2300. TREAT is equal to 0 only for banking markets where a merger leads to a predicted HHI
increase of at least 200 points to a level 1300-1800. POST=1 in years following bank mergers, POST=0 in
years prior to bank mergers, and the year of bank mergers is dropped. Standard errors clustered by banking
market. Source: CoreLogic.
(1) (2) (3) (4) (5) (6)
Loan Vol Loan Vol Loan Vol Loan Count Loan Count Loan Count
VARIABLES All > Median Size <Median Size All > Median Size <Median Size
POST -0.130 -0.147** 0.0628 -0.0349 -0.0644 0.0954
(0.102) (0.0726) (0.112) (0.0746) (0.0701) (0.103)
POSTxTREAT 0.372 0.404** 0.237 0.246 0.345* 0.239
(0.246) (0.190) (0.244) (0.221) (0.206) (0.235)
Observations 1,527 1,525 1,527 1,527 1,525 1,527
R-squared 0.784 0.880 0.801 0.882 0.894 0.832
58
Table 1.9: Effect of Competition on Loan Characteristics, Deeds Records
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on loan-level variables from deeds records. Limited to sample of office or commercial property CRE
loans. See Appendix 1.13.2 for more details on data set construction. Estimates weighted by inverse number
of loans by market, ensuring all markets are weighted equally. TREAT is equal to 1 only for banks in ban-
king markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1800-2300.
TREAT is equal to 0 only for banking markets where a merger leads to a predicted HHI increase of at least
200 points to a level 1300-1800. POST=1 in years following bank mergers, POST=0 in years prior to bank
mergers, and the year of bank mergers is dropped. Standard errors clustered by banking market. Source:
CoreLogic.
(1) (2) (3) (4) (5)
VARIABLES Log(Mtg Amt) Log(Prop. Value) Log(LTV) Same City Purchase Mtg
POST -0.0573** -0.0595** -0.00478 -0.00599 -0.00386
(0.0261) (0.0288) (0.0153) (0.0134) (0.0200)
POSTxTREAT 0.0872* 0.101* -0.00432 0.0456** 0.113***
(0.0518) (0.0562) (0.0216) (0.0201) (0.0404)
Observations 421,245 421,245 421,245 346,872 421,245
R-squared 0.111 0.171 0.041 0.089 0.090
Market FE X X X X X
Year FE X X X X X
Clusters 145 145 145 139 145
59
Table 1.10: Effect of Competition on Loan Characteristics, Deeds Records by Type
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on loan-level variables from deeds records. Limited to sample of office or commercial property CRE
loans. See Appendix 1.13.2 for more details on data set construction. Estimates weighted by inverse number
of loans by market, ensuring all markets are weighted equally. TREAT is equal to 1 only for banks in banking
markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1800-2300. TREAT
is equal to 0 only banking markets where a merger leads to a predicted HHI increase of at least 200 points
to a level 1300-1800. POST=1 in years following bank mergers, POST=0 in years prior to bank mergers,
and the year of bank mergers is dropped. Standard errors clustered by banking market. Source: CoreLogic.
(1) (2) (3) (4) (5)
Same City Same City Same City Log Size Log Size
VARIABLES All <Median Size >Median Size Same City Not Same City
POST -0.00708 -0.00598 -0.00668 -0.0594 -0.0336
(0.0124) (0.0147) (0.0152) (0.0410) (0.0374)
POSTxTREAT 0.0443** 0.0301 0.0694** 0.174*** 0.00278
(0.0194) (0.0225) (0.0336) (0.0655) (0.0839)
Observations 344,808 166,034 178,773 194,259 249,554
R-squared 0.075 0.087 0.073 0.173 0.165
Clusters 141 138 137 141 141
60
Table 1.11: Effect of Competition on Bank Loans
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank com-
petition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a
single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1300-1800.
POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4) (5)
NPLs/Lns NPLs/Lns
VARIABLES Log(Lns) NPLs/Lns (RE) (CI) LLRs/Lns
POST 0.129 -0.0132 0.00207 0.0749 -0.0685
(0.122) (0.124) (0.124) (0.0585) (0.0631)
POSTxTREAT -0.0897 -0.377** -0.335** -0.0485 -0.0454
(0.188) (0.159) (0.145) (0.0725) (0.0990)
Observations 21,516 20,879 20,619 20,481 21,516
R-squared 0.422 0.317 0.483 0.451 0.242
Market FE X X X X X
Year FE X X X X X
Clusters 100 100 100 100 100
61
Table 1.12: Effect of Competition on Bank Assets and Liabilities
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank com-
petition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a
single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1300-1800.
POST=1 in years following bank mergers, POST=O in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4)
VARIABLES Eqty/Asst T1CR/RWA Log(Asst) Deposits/Assets
POST 0.000279 -0.00312 0.107 -0.000580
(0.00238) (0.00402) (0.119) (0.0105)
POSTxTREAT -0.00166 -0.00442 -0.0702 -0.00574
(0.00285) (0.00472) (0.183) (0.0158)
Observations 21,516 17,599 21,516 21,516
R-squared 0.131 0.179 0.418 0.212
Market FE X X X X
Year FE X X X X
Clusters 100 94 100 100
62
1.12 Supplementary Figures
Figure 1-6: HHI by Market; Total Commercial Banks
Total number of commercial banks in the United States and average market-level HHI. Average is weighted
by bank deposits. Source: Commercial banks retrieved from FRED, Federal Reserve Bank of St. Louis.
HHI calculated from FDIC Summary of Deposits Database.
0
0D
0
r-4 LA
N
N
N C)
N
N
N
E) 0 N 5oE
0
.V C:)U
MU) N
N 0 0
N
-0 : N N
N
N
N
D0~ N N 0
N
N
N
N
N 0
-0
0d
1995 2000 2005 2010 2015
Year
Avg. Market HHI ---- - # Banks
63
Figure 1-7: Map of Treated vs Untreated
Map of banking markets that appear as treated or untreated following bank mergers 1994-2015. Treated is
defined as a predicted HHI increase of at least 200 points to a level 1800-2300. Untreated is defined as a
predicted HHI increase of at least 200 points to a level 1300-1800. Markets with bank mergers but with no
HHI increase in these ranges do not appear.
Treated
E Sometimes Treat
D Untreated
El Neither
64
Figure 1-8: Deposits constant, near and away from cutoff
Bank branch average log deposits around the time of bank mergers with an HHI increase of at least 200
points. Limited to branches of merging banks. Mergers split by the predicted ex post HHI. Source: FDIC
Summary of Deposits.
Deposits flows for Near-Cutoff vs Far Mergers
I-.
6
I I
. - a
0
CL I I
VL
0
U
L..
T_
m
6
-5 -4 -3 -2 -1 2 3 4 5
Time relative to merger
-1---- HHI<1600 or HHI>2000 -*- 1600<HHI<200
Data source: FDIC Summary of Deposits; Chicago Fed Mergers data
65
Figure 1-9: Spinoffs over Time
Branch spinoffs for merging banks around the time of bank mergers. Spinoffs are defined as branches whose
ownership changes from one bank to another. Calculated using the sample of bank branches that exist in
time t=-1 year relative to mergers. Source: FDIC Summary of Deposits.
Branch Spinoffs by Merging Bank
Ln
0-
.C
L.
/\
- - - - - - - - -- -- - =
I I I |11
-3 -2 -1 0 2 3 4 5 6 7
Year relative to merger
- - - - - Post-Merger HHI<1800 --- Post-Merger HHI>180
Source: FDIC Summary of deposits. Conditions on branch existing and owned by merging
in t=-1.
66
Figure 1-10: Branch spinoff likelihood, mkts with AHHI < 200
Binscatter plot showing the fraction of branches spun off for bank mergers with a predicted HHI increase of
below 200 points. X axis shows the predicted HHI change. Y axis shows the realized fraction of branches
that are spun off within each bin of the X variable. Source: FDIC Summary of Deposits.
0
0
Prob. of Spinoff, 0
Prob. of Spinoff, HHI>1800
U HHI<J800
MC4 0 * .0 *1
U.0 .0 00 S 0
LL.
0
0
5D
00 1000 1500 2000 2500 3d00
Change in HHI due to merger
Fraction of branches spun off is measured in each market for each merger. Markets are c
by ventiles of HHI growth due to merger; each point represents one ventile. Data from 1
2009-2015. Limited to mergers with AHHI<200. Source: Author's calculations from FDIC!
67
1.13 Supplementary Tables
Table 1.13: HHI Placebo at HHI=1300
Placebo difference in differences regression estimates of Equation 1.1, estimating the effect of required bank
competition on market-level HHI. HHI is calculated as the sum of squared deposit market shares by bank,
multiplied by 10,000. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 1300-1800. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1800-2300.
POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: FDIC summary of Deposits
database.
(1) (2) (3) (4)
VARIABLES HHI HHI Log(HHI) Log(HHI)
POST 402.0*** 419.6*** 0.163*** 0.163***
(99.43) (101.0) (0.0331) (0.0331)
t>=5 67.20 0.00801
(85.61) (0.0259)
POSTxTREAT -111.6 -143.0 -0.0380 -0.0394
(100.3) (99.40) (0.0375) (0.0374)
t>=5 X TREAT 54.28 0.00244
(72.06) (0.0275)
Observations 4,094 4,094 4,094 4,094
R-squared 0.697 0.698 0.752 0.752
Market FE X X X X
Year FE X X X X
Clusters 160 160 160 160
68
69
Table 1.14: HHI Placebo at HHI=2800
Placebo difference in differences regression estimates of Equation 1.1, estimating the effect of required bank
competition on market-level HHI. HHI is calculated as the sum of squared deposit market shares by bank,
multiplied by 10,000. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 2300-2800.
POST=1 in years following bank mergers, POST=O in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: FDIC summary of Deposits
database.
(1) (2) (3) (4)
VARIABLES HHI HHI Log(HHI) Log(HHI)
POST 266.6*** 251.6*** 0.166*** 0.161***
(37.14) (35.18) (0.0204) (0.0195)
t>=5 42.66 0.00425
(51.61) (0.0236)
POSTxTREAT 66.02 138.2 0.0277 0.0545
(89.83) (122.8) (0.0486) (0.0570)
t>=5 X TREAT -135.0 -0.0496
(108.1) (0.0513)
Observations 3,680 3,680 3,680 3,680
R-squared 0.581 0.582 0.616 0.617
Market FE X X X X
Year FE X X X X
Clusters 135 135 135 135
70
Table 1.15: HHI Placebo, 10 < AHHI < 200
Placebo difference in differences regression estimates of Equation 1.1, estimating the effect of required bank
competition on market-level HHI. HHI is calculated as the sum of squared deposit market shares by bank,
multiplied by 10,000. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of less than 200 points to a level 1300-1800. TREAT is equal to 0 only for banks
in banking markets where a merger leads to a predicted HHI increase of less than 200 points to a level
1800-2300. POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the
year of bank mergers is dropped. Standard errors clustered by banking market. Source: FDIC summary of
Deposits database.
(1) (2) (3) (4)
VARIABLES HHI HHI Log(HHI) Log(HHI)
POST 77.89 48.27 0.0406** 0.0283
(52.10) (44.77) (0.0206) (0.0176)
t>=5 85.93 0.0219
(62.62) (0.0249)
POSTxTREAT -49.21 -9.931 -0.0198 -0.00301
(66.65) (49.17) (0.0265) (0.0201)
t>=5 X TREAT -66.64 -0.0292
(69.55) (0.0284)
Observations 14,674 14,674 14,674 14,674
R-squared 0.620 0.620 0.684 0.685
Market FE X X X X
Year FE X X X X
Clusters 345 345 345 345
71
Table 1.16: Borrower Characteristics in CMBS Records
Summary statistics of loan-level securitized mortgage characteristics. Data is from 30,776 loans from offices
and retail buildings. Source: Trepp.
(1) (2) (3) (4) (5)
VARIABLES mean sd p10 p50 p90
Term (Months) 117 40 60 120 120
Loan Amt (th) 14,558 37,668 1,500 5,400 28,600
LTV 68 12 52 71 79
Occupancy 95 7 86 99 100
Interest Spread 1.7 .76 .91 1.6 2.7
72
Table 1.17: Borrower Characteristics in the SSBF
Summary statistics of business data for the 697 firms in the 2003 Survey of Small Business Finances that
report having a mortgage. Observations include all implicates and are weighted by Final Weight. Missing
data is dropped casewise.
(1) (2) (3) (4) (5)
VARIABLES mean sd plO p50 p90
D&B Credit Score 3.5 1.5 1 4 5
Total employees 13 30 2 5 24
Dist to Primary Bank 12 66 1 1 15
Total Assets 1,181,876 5,063,634 22,697 249,000 2,106,616
Impersonal Rel. .67 1.7 0 0 4
Total Mortgage 582,904 4,016,602 20,000 108,000 711,659
Total Debt 795,140 4,720,999 40,000 199,000 1,222,000
73
Table 1.18: Cross-Sectional Characteristics in SSBF
Regression estimates for the 697 firms in the 2003 Survey of Small Business Finances that report having a
mortgage. Robust standard errors. Observations include all implicates and are weighted by Final Weight.
Missing data is dropped casewise.
(1) (2) (3) (4) (5) (6)
VARIABLES Log Rel. Mnths Log Dist Impersonal Log Rel. Mnths Log Dist Impersonal
Log Mortgage -0.00183 0.0609* 0.119**
(0.0301) (0.0321) (0.0590)
Log Assets 0.0765*** 0.0396 0.0765
(0.0281) (0.0258) (0.0480)
Constant 4.388*** 0.574 -0.726 3.420*** 0.802** -0.268
(0.362) (0.382) (0.692) (0.358) (0.325) (0.597)
Observations 697 697 697 694 694 694
R-squared 0.000 0.009 0.012 0.019 0.005 0.006
74
Table 1.19: Cross-Sectional Characteristics of Large CMBS Loans
Cross-sectional regression estimates for CMBS loans. Includes full sample of available CMBS loans originated
from 1998-2015. "Days Dlq, 3 yrs" refers to the number of days that a loan is in delinquency within three
years of loan origination. Int. rate is the original interest rate paid on loans. Property value is calculated by
multiplying the original loan balance by the origination LTV. DSCR is the debt service-cashlflow coverage
ratio. Source: Trepp. Robust standard errors.
(1) (2) (3) (4) (5)
Mths Dlq Mths Dlq
VARIABLES 3 yrs 3 yrs Int. Rate Int. Rate Int. Rate
Log Prop. Val -0.000679*** -0.00143*** -0.483*** -0.574*** -0.408***
(7.5le-05) (9.56e-05) (0.00308) (0.00327) (0.00304)
LTV 0.000198*** 0.0209*** 0.0175***
(8.08e-06) (0.000328) (0.000337)
DSCR -0.0640***
I (0.00215)
Mths Dlq, 3 yrs 1.896***
(0.138)
Mths Dlq, 2 yrs 0.0225
(0.229)
Constant 0.0144*** 0.0124*** 13.33*** 13.30*** 10.82***
(0.00115) (0.00110) (0.0467) (0.0443) (0.0453)
Observations 132,702 132,702 131,703 131,703 99,526
R-squared 0.001 0.005 0.194 0.225 0.164
75
Table 1.20: Bank Size and Small Business Lending
Estimates of the relationship between log(total bank lending) and the composition of bank loans. Sample
includes universe of U.S. commercial banks with assets above $20,000,000 from 1994-2015. Estimates are
unweighted. Sources: Call Reports.
(1) (2) (3) (4) (5) (6)
Frac CRE Frac CRE Frac CRE Frac CI Frac CI Frac CI
VARIABLES <100k 100k-250k 250k-lmn <100k 100k-250k 150k-lmn
Log(Tot Loans) -0.03*** -0.04*** -0.05*** -0.05*** -0.03*** -0.03***
(0.00) (0.00) (0.00) (0.00) (0.00) (0.00)
Constant 0.49*** 0.61*** 0.93*** 0.87*** 0.51*** 0.62***
(0.01) (0.01) (0.01) (0.01) (0.01) (0.01)
Observations 155,044 157,129 156,309 156,496 154,446 150,858
R-squared 0.11 0.15 0.12 0.11 0.14 0.06
76
Table 1.21: Effect of Mergers on Incumbent Bank Size
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on bank-level variables measuring bank size. Limited to incumbent banks not taking part in bank
mergers. TREAT is equal to 1 only for banks in banking markets where a merger leads to a predicted HHI
increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in banking markets
where a merger leads to a predicted HHI increase of at least 200 points to a level 1300-1800. POST=1 in
years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank mergers is
dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4)
VARIABLES Mkt Branches Mkt Banks Avg # Branches HMDA DTI
POST -0.0131** -0.0344* 0.139 0.00136
(0.00548) (0.0207) (0.110) (0.0201)
POSTxTREAT 0.00272 0.0192 0.0675 0.00836
(0.00623) (0.0311) (0.141) (0.0229)
Observations 4,928 4,928 4,928 4,685
R-squared 0.990 0.961 0.871 0.847
Market FE X X X X
Year FE X X X X
Clusters 193 193 193 192
77
Table 1.22: Bank Characteristics in Treated vs Untreated Markets
Balance table estimating the effect of treatment on bank balance sheet variables limited to markets and
mergers where POST=0. Limited to sample of banks with more than 50% of SOD deposits in a single
banking market and total loans of at least $20mn. Estimates weighted by bank loan market share within
banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at least four
local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a predicted
HHI increase of at least 200 points to a level 1300-1800. TREAT is equal to 0 only for banks in banking
markets where a merger leads to a predicted HHI increase of at least 200 points to a level 800-1300. POST=1
in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank mergers is
dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4) (5) (6)
CRE/Lns CRE/Lns CRE/Lns
VARIABLES LLRs/Lns NPLs/Lns <100k 100k-250k 250k-lmn Log(Lns)
TREAT 0.0269 0.139* 0.00301 0.0138 -0.0226 -0.213
(0.0580) (0.0817) (0.00919) (0.0120) (0.0150) (0.184)
Observations 6,460 6,441 5,241 5,263 5,195 6,460
R-squared 0.047 0.048 0.077 0.040 0.038 0.026
Year FE X X X X X X
Robust standard errors in parentheses
*** p<0.01, ** p<0.0 5 , * p<0.1
78
Table 1.23: Effect of Competition on Bank Assets and Liabilities: Placebo, HHI=1300
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a single
banking market and total loans of at least $20mn. Estimates weighted by bank loan market share within
banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at least four
local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a predicted
HHI increase of at least 200 points to a level 1300-1800. TREAT is equal to 0 only for banks in banking
markets where a merger leads to a predicted HHI increase of at least 200 points to a level 800-1300. POST=1
in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank mergers is
dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4)
VARIABLES Eqty/Asst T1CR/RWA Log(Asst) Deposits/Assets
POST -0.00465 -0.0129*** 0.292* -0.0163
(0.00312) (0.00424) (0.154) (0.0171)
POSTxTREAT -0.000283 0.000323 -0.300 0.0191
(0.00290) (0.00846) (0.317) (0.0120)
Observations 11,857 9,506 11,857 11,857
R-squared 0.154 0.234 0.499 0.266
Market FE X X X X
Year FE X X X X
Clusters 62 56 62 62
79
Table 1.24: Effect of Competition on Bank Assets and Liabilities: Placebo, HHI=2300
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank com-
petition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a
single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 2300-2800. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1800-2300.
POST=1 in years following bank mergers, POST=O in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4)
VARIABLES Eqty/Asst T1CR/RWA Log(Asst) Deposits/Assets
POST 0.000161 -0.00293 0.0279 0.00924
(0.00252) (0.00429) (0.114) (0.0109)
POSTxTREAT -0.00250 -0.00712 0.292* -0.0246*
(0.00309) (0.00615) (0.150) (0.0144)
Observations 18,394 15,047 18,394 18,394
R-squared 0.129 0.159 0.456 0.213
Market FE X X X X
Year FE X X X X
Clusters 74 73 74 74
80
Table 1.25: Effect of Competition on Bank Assets and Liabilities: 10 < AHHI < 200
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a single
banking market and total loans of at least $20mn. Estimates weighted by bank loan market share within
banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at least four
local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a predicted
HHI increase of between 10 and 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at between 10 and 200 points to a level
1300-1800. POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year
of bank mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4)
VARIABLES Eqty/Asst T1CR/RWA Log(Asst) Deposits/Assets
POST -0.00152 -0.000635 -0.0262 0.00248
(0.000966) (0.00189) (0.0433) (0.00394)
POSTxTREAT 0.00123 -0.00227 -0.185 0.00981
(0.00198) (0.00392) (0.164) (0.0129)
Observations 708,367 563,266 708,367 708,367
R-squared 0.146 0.158 0.487 0.272
Market FE X X X X
Year FE X X X X
Clusters 288 273 288 288
81
Table 1.26: Effect of Competition on Bank Lending: Placebo, HHI=1300
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a single
banking market and total loans of at least $20mn. Estimates weighted by bank loan market share within
banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at least four
local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a predicted
HHI increase of at least 200 points to a level 1300-1800. TREAT is equal to 0 only for banks in banking
markets where a merger leads to a predicted HHI increase of at least 200 points to a level 800-1300. POST=1
in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank mergers is
dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4) (5)
NPLs/Lns NPLs/Lns
VARIABLES Log(Lns) NPLs/Lns (RE) (CI) LLRs/Lns
POST 0.299* -0.145 -0.169 -0.00376 -0.0908
(0.153) (0.156) (0.149) (0.0705) (0.131)
POSTxTREAT -0.275 -0.252 0.00129 -0.223 -0.144
(0.316) (0.328) (0.198) (0.146) (0.223)
Observations 11,857 11,702 11,603 11,119 11,857
R-squared 0.500 0.240 0.425 0.469 0.244
Market FE X X X X X
Year FE X X X X X
Clusters 62 62 62 62 62
82
Table 1.27: Effect of Competition on Bank Lending: Placebo, HHI=2300
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank com-
petition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a
single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 2300-2800. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1800-2300.
POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4) (5)
NPLs/Lns NPLs/Lns
VARIABLES Log(Lns) NPLs/Lns (RE) (CI) LLRs/Lns
POST 0.0474 0.00838 0.0261 0.0911 -0.00325
(0.118) (0.130) (0.128) (0.0655) (0.0677)
POSTxTREAT 0.257* -0.353* -0.261* -0.308*** -0.0306
(0.152) (0.187) (0.151) (0.0911) (0.0811)
Observations 18,394 17,832 17,608 17,346 18,394
R-squared 0.458 0.320 0.494 0.456 0.220
Market FE X X X X X
Year FE X X X X X
Clusters 74 74 74 74 74
83
Table 1.28: Effect of Competition on Bank Lending: 10 < AHHI < 200
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a single
banking market and total loans of at least $20mn. Estimates weighted by bank loan market share within
banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at least four
local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a predicted
HHI increase of between 10 and 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at between 10 and 200 points to a level
1300-1800. POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year
of bank mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4) (5)
NPLs/Lns NPLs/Lns
VARIABLES Log(Lns) NPLs/Lns (RE) (CI) LLRs/Lns
POST -0.0225 0.0694 0.0545 -0.0261 0.0161
(0.0422) (0.0442) (0.0598) (0.0226) (0.0308)
POSTxTREAT -0.172 0.0465 -0.0285 0.0247 0.0752
(0.161) (0.0889) (0.0881) (0.0541) (0.0737)
Observations 708,367 692,744 683,227 654,981 708,367
R-squared 0.484 0.285 0.458 0.409 0.223
Market FE X X X X X
Year FE X X X X X
Clusters 288 288 288 288 288
84
Table 1.29: Effect of Competition on Bank Loans by Bank Size
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank com-
petition on bank-level variables. Limited to sample of banks with more than 50% of SOD deposits in a
single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1300-1800.
POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Estimates split by median banks size of
$86mn, where median bank size is calculated using pre-merger total lending. Source: Call reports.
(1) (2) (3) (4) (5) (6)
Small Small Small Large Large Large
VARIABLES Log(Lns) NPLs/Lns LLRs/Lns Log(Lns) NPLs/Lns LLRs/Lns
POST 0.124 -0.155 -0.165 0.201 -0.0251 -0.0545
(0.117) (0.196) (0.103) (0.132) (0.133) (0.0706)
POSTxTREAT 0.115 -0.173 -0.0326 -0.182 -0.450*** -0.0676
(0.151) (0.239) (0.162) (0.209) (0.169) (0.0978)
Observations 6,869 6,712 6,869 14,640 14,160 14,640
R-squared 0.579 0.326 0.380 0.451 0.358 0.256
Market FE X X X X X X
Year FE X X X X X X
Clusters 85 85 85 99 99 99
85
Table 1.30: Effect of Competition on Bank Lending: Bank Controls
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank com-
petition on bank level variables, with added controls. Limited to sample of banks with more than 50% of
SOD deposits in a single banking market and total loans of at least $20mn. Estimates weighted by bank
loan market share within banking market (loans/(loans of all banks in market)). Sample limited to banking
markets with at least four local banks. TREAT is equal to 1 only for banks in banking markets where a
merger leads to a predicted HHI increase of at least 200 points to a level 1800-2300. TREAT is equal to 0
only for banks in banking markets where a merger leads to a predicted HHI increase of at least 200 points to a
level 1300-1800. POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the
year of bank mergers is dropped. Controls are the log number of branches per banking market, the average
bank size (where bank size is the log total number of branches), bank ex ante log assets fully interacted
with POST, bank ex ante total lending fully interacted with POST, and bank ex ante equity/assets fully
interacted with POST. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3) (4) (5)
NPLs/Lns NPLs/Lns
VARIABLES Log(Lns) NPLs/Lns (RE) (CI) LLRs/Lns
POST 1.867*** 0.193 -0.201 -0.525 0.976**
(0.546) (0.654) (0.713) (0.404) (0.453)
POSTxTREAT -0.123 -0.348* -0.426*** -0.0173 -0.0606
(0.0755) (0.177) (0.153) (0.0757) (0.0966)
Log # Branches in Mkt 0.751** 0.744 0.797 0.161 0.446*
(0.315) (0.538) (0.510) (0.272) (0.266)
Avg Log # Branches per Bank 9.09e-05 7.93e-05 1.42e-05 7.77e-05** 0.000154*
(7.11e-05) (0.000149) (0.000160) (3.55e-05) (7.82e-05)
Observations 13,758 13,471 13,344 13,128 13,758
R-squared 0.832 0.395 0.533 0.492 0.339
Market FE X X X X X
Year FE X X X X X
Clusters 94 94 94 93 94
86
Table 1.31: Effect of Competition on Small Bank C&I Loans
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on C&I lending by loan size. Limited to sample of banks with more than 50% of SOD deposits in
a single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1300-1800.
POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3)
Frac. CI Lns Frac. CI Lns Frac. CI Lns
VARIABLES <100k 100k-250k 150k-lmn
POST 0.0113 -0.00743 -0.00779
(0.0145) (0.00683) (0.00931)
POSTxTREAT 0.0144 0.00795 0.00160
(0.0229) (0.0115) (0.0200)
Observations 18,261 17,897 17,414
R-squared 0.316 0.180 0.163
Market FE X X X
Year FE X X X
Clusters 98 98 98
87
Table 1.32: Effect of Competition on Small Bank CRE Loans: Placebo Estimates at
HHI=1300
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on CRE lending by loan size. Limited to sample of banks with more than 50% of SOD deposits in
a single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHIl increase of at least 200 points to a level 2300-2800. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 2300-2800.
POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3)
Frac. CRE Lns Frac. CRE Lns Frac. CRE Lns
VARIABLES <100k 100k-250k 250k-lmn
POST -0.00324 -0.0129 -0.0130
(0.00719) (0.0133) (0.0182)
POSTxTREAT 0.00427 0.0120 0.0144
(0.0115) (0.0145) (0.0268)
Observations 9,921 10,083 10,054
R-squared 0.570 0.402 0.145
Market FE X X X
Year FE X X X
Clusters 60 60 60
88
Table 1.33: Effect of Competition on Small Bank CRE Loans: Placebo Estimates at
HHI=2300
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on CRE lending by loan size. Limited to sample of banks with more than 50% of SOD deposits in
a single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase of at least 200 points to a level 1800-2300. TREAT is equal to 0 only for banks in
banking markets where a merger leads to a predicted HHI increase of at least 200 points to a level 1300-1800.
POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year of bank
mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3)
Frac. CRE Lns Frac. CRE Lns Frac. CRE Lns
VARIABLES <100k 100k-250k 250k-lmn
POST 0.00106 -0.00211 -0.0180
(0.00496) (0.00855) (0.0169)
POSTxTREAT -0.00282 0.00799 -0.0177
(0.00771) (0.0138) (0.0189)
Observations 15,312 15,658 15,573
R-squared 0.513 0.416 0.222
Market FE X X X
Year FE X X X
Clusters 74 74 74
89
Table 1.34: Effect of Competition on Small Bank CRE Loans: 10 < AHHI < 200
Difference-in-differences regression estimates of Equation 1.1, estimating the effect of required bank compe-
tition on CRE lending by loan size. Limited to sample of banks with more than 50% of SOD deposits in
a single banking market and total loans of at least $20mn. Estimates weighted by bank loan market share
within banking market (loans/(loans of all banks in market)). Sample limited to banking markets with at
least four local banks. TREAT is equal to 1 only for banks in banking markets where a merger leads to a
predicted HHI increase between 10 and 200 points to a level 1800-2300. TREAT is equal to 0 only for banks
in banking markets where a merger leads to a predicted HHI increase of between 10 and 200 points to a level
1300-1800. POST=1 in years following bank mergers, POST=0 in years prior to bank mergers, and the year
of bank mergers is dropped. Standard errors clustered by banking market. Source: Call reports.
(1) (2) (3)
Frac. CRE Lns Frac. CRE Lns Frac. CRE Lns
VARIABLES <100k 100k-250k 250k-lmn
POST 0.00192 0.00146 -0.00186
(0.00212) (0.00263) (0.00636)
POSTxTREAT -0.00707 -0.00279 0.00850
(0.00665) (0.00726) (0.0161)
Observations 584,893 612,496 618,737
R-squared 0.532 0.421 0.242
Market FE X X X
Year FE X X X
Clusters 286 285 285
90
Table 1.35: Effect of Competition on CMBS Loans
Difference-in-differences estimates for CMBS loans, estimating effect of required antitrust interventions on
CMBS loan characteristics in local banking market. "Dlq 3 yrs" refers to the number of months a loan
is delinquent within three years of origination. Estimates of Equation 1.1. Variables measured at time of
securitization. Limited to sample of loans backed by retail or office properties. Source: Trepp. Standard
errors bootstrapped and clustered by banking market.
(1) (2) (3) (4) (5) (6) (7)
Dlq
VARIABLES Rate Spread LTV Occupancy Log(Loan) Term (mths) 3 yrs (mean) Rate
POST 0.0226 0.312 0.0790 -0.0583 -4.559 0.0228 0.0226
(0.0365) (0.721) (0.362) (0.0680) (3.459) (0.0199) (0.0340)
POSTxTREAT -0.0753* 0.879 0.238 0.293** 2.751 0.00202 -0.0753*
(0.0434) (0.722) (0.544) (0.117) (5.485) (0.0326) (0.0400)
Observations 335 333 333 333 335 335 335
R-squared 0.936 0.614 0.591 0.752 0.773 0.747 0.984
Markets 45 44 44 44 45 45 45
91
1.13.1 Model of Bank Lending
Setting
Banks' investment options in this setting are a simplified version of banks' choices in the
models described by Keeley (1990), Petersen and Rajan (1995), Allen and Gale (2004) and
Tirole (2010). I adopt the three key features of these models and show how they interact
with each other: First, banks have the option to make repeated loans to the same borrowers.
Second, some borrowers have outside financing options which may include borrowing in a
different market or using other types of financing. Third, banks can make choices that could
cause them to go bankrupt.
Banks have two non-mutually exclusive investment options: (a) standard lending projects
where the net profits to the bank is endogenously determined, and (b) a bet-the-bank project
where the net payoff is exogenous even for the monopolist. The standard lending projects
require multi-stage investment of the sort analyzed in theories of relationship lending; For
these projects, a unit mass of entrepreneurs approach the bank with projects that require
investment 11 in their first stage. Entrepreneurs' first-stage investments have unit payoff
if they are successful, which occurs with probability p, and zero payoff otherwise. If the
projects are funded, entrepreneurs may raise funds I2 < 11 which they invest in the project's
second stage, which again pays off with probability p and has unit payoff if successful.19
To create a downward-sloping demand curve, I suppose that with probability a, entre-
preneurs receive a take-it-or-leave-it outside financing offer in the first period that provides
financing for both periods (whether the offer occurs is not observable to the banks). The
outside financing offer gives investment 11 and 12 in each period in return for payment r in
each period where 1 jf2 < r < 1. Entrepreneurs repay banks only from the project payoff.
The bet-the-bank project pays off with probability pR and has zero investment cost. 2 0 If
19An interpretation of this is that screening is required in period 1 so that I, = 12 + c with c > 0.
200ne can think of this as the sort of risky choice that led some banks to fail in the 2008 financial crisis or
the Savings and Loan Crisis of the 1980s. In particular, it could be any choice of asset or liability structure
that runs a risk of catastrophic failure.
92
it pays off, it has unit payoff. If it is undertaken but fails, the bank goes bankrupt, earning
no profits from either this investment or from the standard lending projects.
Banks may either be monopolists or competitive; both cases are analyzed separately
below. Free entry ensures that the payoff competitive banks demand from lending to entre-
preneurs is such that banks' profits are zero in expectation. On the other hand, monopolists
demand the payoff from entrepreneurs that maximizes their payoffs, limited only by the fact
that entrepreneurs may accept an outside offer if it gives a better price and that entrepre-
neurs cannot repay more than they earn. In both cases, banks invest only in weakly positive
net present value (NPV) projects.
Competitive Banking Market
The zero profit condition implies that the payoff competitive banks require from successful
projects in the first period is 1/p and the payoff they require from successful standard lending
projects in the second time period is _2/p. Because each project's payoff is assumed to be 1
if successful, only projects where 11 < p will be funded. Otherwise, the bank will receive a
return less than I/p . If a project is not funded in the first period, there is no second period
investment opportunity. Therefore '2 < I by assumption; if a project is funded in period 1 ,
it will also be funded in period 2. So competitive banks either choose to fund the project in
both periods (if I1 < p) or not at all (if 1 > p). The outside financing opportunity with cost
r is more expensive than the average competitive rate offered by banks 1'12 by assumption,
and therefore borrowers will take local bank financing whenever it is offered.
Competitive banks will always invest in the bet-the-bank project since their expected
return is pR and they do not risk losing any profits from the standard lending projects
because of the zero-profit condition.
Monopolistic Banking Market
Monopolists lend whenever 2p - (I1 + 12) > 0 because they can capture the rents from
both periods. Since I2 < '1, there is a range of projects where p satisfies '1 > p > 11'2
where monopolists will lend but competitive banks will not. The fact that there is a wider
93
range of projects where monopolists lend (as opposed to entrepreneurs) captures the central
insight of the long-term project mechanism described by Petersen and Rajan (1995). The key
insight is that projects may require high initial investments - for example, due to screening
costs - which monopolists can recapture if they continue to lend to the same borrowers.
Because borrowers are stuck going to the same bank in both periods, monopolistic banks
have what amounts to an equity stake in projects.
Suppose now that p > I1+ 2 so monopolists can lend profitably. If monopolists demand a
payoff of between r and 1, their offer will be accepted by the 1- a borrowers who do not have
the outside option. If they demand a payoff between 0 and r, their offer will be accepted
by all borrowers. Therefore, to maximize their profits, monopolists will demand a payoff
of either 1 or r from successful projects. Demanding 1 is optimal whenever the expected
profits from lending at rate 1 to 1 - a of the borrowers and earning profits 2p - (I1 + 12) on
each is greater than the expected profits from lending at rate r to all borrowers and earning
profits 2pr - (I1 + 12) on each. In other words, demanding a payoff of 1 is optimal whenever
(1 - a) (2p - (I1 + 12)) > 2pr - (11 + 12), or equivalently, whenever a < 1 _ 22ppr-(-I(1I+1I 22) . This
means that for sufficiently small a, monopolistic lenders do not mind losing the borrowers
with the outside option. The loss of these borrowers exemplifies the market power mechanism
as market power can lead to less lending at higher prices.
A monopolist's decision to invest in the bet-the-bank project depends on the profits from
standard lending. Let x be the profits monopolists make from lending - either (1 - a) (2p -
11-12) or 2pr--i1I2, whichever is greater. Then the bet-the-bank project is worth investing
in whenever pR (x + 1)> x or equivalently x < 4j- . Intuitively, profitable investments can
dissuade banks from taking risks that put the whole company's profits at stake if the whole
company's profits are high enough. This is the key insight of the Charter Value Hypothesis.
In summary, monopolistic banks will either invest in the bet-the-bank project or not,
and will either require r or the full unit return from standard lending projects. The choices
they make depend on the parameter values. Compared to competitive banks, monopolists
94
are less likely to invest in the bet-the-bank project and may do either more or less standard
lending in total. They are likely to lend more often if first-period investment costs are high
enough to prevent competitive banks from making such loans, and they lend less often if
it is worthwhile for them to charge interest rates high enough that some borrowers find it
optimal to find financing elsewhere.
1.13.2 Data Construction
Call Reports Variables
Sample Selection
The following sample selection is used for local banks:
" Banks are matched to FDIC SOD data. Banks are selected if more than 50% of their
deposits are located in a single banking market.
" Banks must have at least $10mn in total assets.
* Regression sample requires there to be at least four commercial banks satisfying these
criteria in each year.
* Bank-year observations are removed if the bank is part of any merger within two years.
" Variables are Winsorized at the 5% level. Non-performing loan measures are dropped
if they are above 10.
Variable Definitions
Not all variables are available for all years. Variables are defined as follows:
" Log Assets - Log(RCFD2170)
" Log Lending - Log(RCFD2122)
95
* Equity/Assets - RCFD3210/RCFD2170
" Tier 1 Capital / Risk-Weighted Assets - RCFD8274/RCFDA223
* Non-Performing Loans (NPL) / Total Loans - (RCFD1407+RCFD1403)/RCFD2122
" Loan Loss Reserves (LLR) / Total Loans - RCFD3123/RCFD2122
* Non-Performing Loans (Real Estate) / Real Estate Loans -
(RCFD1247+RCFD1250+RCON1212+RCFD1246+RCFD1249
+RCON1211)/RCFD1410
* Non-Performing Loans (C&I) / C&I Loans -
(RCON1222+RCON1251+RCON1254+ RCON1224+RCON1253
+RCON1256)/RCFD1766
* Total C&I Lending: RCFD1766
" C&I Lending <$100k, $100k-$250k, $250k-$lmn respectively: RCON5571, RCON5573,
RCON5575
These variables are only defined for banks that do nonzero total lending for these types
of loans.
" Total CRE Lending - RCON1480
" CRE Lending <$100k, $100k-$250k, $250k-$lmn respectively: RCON5565, RCON5567,
RCON5569
These variables are only defined for banks that do nonzero total lending for these types
of loans.
" Loan interest income - RIAD4010
96
Deeds Records
Sample Selection
* The purchased data sample only includes commercial properties, either retail or office.
The sample is the sample of properties available in counties that partially or wholly
overlap a banking market where the treatment variable is either 0 or 1, i.e., in which
a merger took place from 1994-2015 in which the predicted HHI change was at least
200 points and the predicted HHI level was 1300-2800.
* I drop multi-market sales.
" In regression estimates I weight properties by the inverse number of properties per
banking market and year so that weights total to 1 within banking market-year pairs.
I require a minimum of 10 sales per banking market for use in sample estimates.
Variables
" Reported property prices are used only for properties that are coded as arms-length
transactions and resales and either grant deeds or quitclaim deeds, excluding inter-
family sales. For properties without a price, prices are filled in as follows. First, a
state-level price index is created by estimating a specification of the following form:
Log(Priceit) = Pt x Pricet + 3iPropertyi
where i indexes prices, s indexes states and t indexes years. The Pt coefficients create
a state-specific price index. For a property sold at time t' and time t, where the
log price is available at time t, pit but no price is available at time t', I estimate
pit = pit + Pt - Pset. If a price is available at two dates, one before time t' and after
time t', I take the average of both prices estimated in this way.
" Lenders and borrowers are in the same city if the borrower mailing address city matches
97
the lender address city.
" The LTV ratio is calculated as the loan amount divided by the property price.
" The mortgage amount is as reported.
" Prices and mortgage amounts are Winsorized at 5%.
98
Chapter 2
Housing Demand, Regional House
Prices and Consumption
This chapter provides a new explanation for regional variation in the 2000-2012 housing
and consumption boom and bust. Cities with a greater share of growing industries experien-
ced larger housing demand shocks, larger house price increases from 2000-2006 and greater
price declines from 2007-2012. Consistent with theory, price effects were strongeri n housing-
supply inelastic cities. City-level differences in housing demand are correlated with supply
elasticity, so estimates of the effects of housing prices that using elasticity as an instrument
change when controlling for housing demand due to industr composition. I estimate a dura-
bles consumption-house price elasticity of 0.08 from 2000-2006, 40% smaller than previous
estimates. Post-2006, the estimated elasticity is 0.31 and housing prices rather than local
conditions explain consumption changes.
2.1 Introduction
The close relationship between housing prices, business cycles, and consumption is extremely
well documented (Mian and Sufi, 2014a; Mian et al., 2013; Leamer, 2007; Guren et al., 2017).
This correlation was particularly salient during the Great Recession, which followed a crash
in the housing market. The size of the housing boom and bust preceding the Great Recession
varied across the United States and cities with the most volatile housing prices had the most
volatile consumption as well. Several papers have used cross-sectional variation in house
price changes to quantify and explain the effect of housing prices on consumption and other
99
regional variables. While it is tempting to interpret the observed correlation between housing
prices and consumption as causal, the factors driving the regional differences in the size of
the boom and bust may also have had a direct effect on consumption, motivating the use of
instrumental variables strategies that exploit plausibly exogenous variation in the size of the
boom and bust (Mian and Sufi, 2014a; Mian et al., 2013). This paper reevaluates the reasons
for heterogeneity in housing prices from 2001-2011. The regional variation in the housing
boom can be attributed to both housing supply differences and to differences in demand
which arise from differential growth in local industries. This differential growth affected
both local housing demand (which affected house prices) and household consumption.
The most widely-used empirical model of the housing market attributes regional diffe-
rences in the size of the housing boom and bust primarily to differences in the elasticity of
housing supply across regions. While elasticity alone partially explains the regional varia-
tion in housing price growth from 2001-2006, this model also gives rise to empirical puzzles.
Regions with a less elastic housing supply did see greater price appreciation, but they also
had more new construction, even though most housing market models predict that higher
prices are due to less new construction. Moreover, housing supply elasticity explains only a
small fraction of the variation in price appreciation in general and under-predicts the size of
the price boom in the Southwest (Nathanson and Zwick, 2012). This paper shows that part
of the reason for these puzzles is that demand shocks due to local industry exposure had
important effects on housing price growth.
The United States experienced steady GDP growth in the early 2000s, but there was
substantial variation in this growth across industries. Therefore, differential composition
of industries translated into variation in income growth. Areas that were more exposed to
declining industries, particularly manufacturing, experienced a much smaller housing boom
and bust. Interacting exposure to growing industries with the measure of housing price
elasticity developed by Saiz (2010), I show that housing prices rose most in areas where both
local employment was in growing industries and housing was inelastically supplied. As a
simple proxy for exposure to slower-growing industries, I consider the fraction of employment
in manufacturing in 1998. Using manufacturing employment share as a proxy for regional
housing demand yields estimates which are consistent with a simple theoretical framework.
100
Furthermore, industry exposure is highly correlated with housing supply elasticity, im-
plying that estimates which do not control for heterogeneous demand they may suffer from
omitted variables bias. Accounting for local industry exposure partially resolves the hou-
sing market puzzles. Areas with larger housing demand shocks had more construction from
2001-2011 and, when controlling for these shocks, housing supply elasticity no longer has
a statistically significant negative effect on new construction. Moreover, the addition of
industry controls reduces the unexplained "excess" price growth in Southwestern cities by
0.09 log points - from 0.26 to 0.17 - from 2001-2006 in preferred specifications (although it
does little to explain the relatively larger bust in these areas). Including industry exposure
also improves the R2 of regression specifications used to explain prices appreciation from
2001-2006.
A flourishing body of empirical literature uses variation in housing prices over this period
to study how housing prices affect household consumption (Mian et al., 2013; Dynan, 2012;
Kaplan et al., 2016). Because regional demand shocks played an important role in the size
of the housing boom and bust, I show that much of the correlation between housing prices
and consumption from 2001-2006 was due to the effects of income growth on both housing
demand and consumption rather than the direct effect of housing prices on consumption.
I estimate the effect of housing prices on consumption by instrumenting for housing
prices using housing supply elasticity, the method pioneered by Mian and Sufi (2011). I
augment this instrument by controlling for local industry composition. Accounting for local
industry exposure, I find that the estimated effect of housing prices on both durables and
non-durables consumption expenditures from 2001-2006 is reduced by about 65% compared
to models which do not include these variables. In several specifications I cannot statistically
reject that the consumption-house price elasticity is zero after adding industry controls. This
is because regions with an elastic housing supply also had more manufacturing, which both
led to relatively lower prices and relatively lower demand for consumption. Estimates that
do not control for manufacturing exposure may conflate these two effects.
On the other hand, the estimated consumption-housing price elasticity for the 2006-2011
period is large and statistically distinguishable from zero, even after accounting for industry
exposure. The addition of industry controls either has no effect on or increases the estimated
101
consumption-house price elasticity. The reason for the difference between 2001-2006 and
2006-2011 estimates is that the sign of the omitted variable bias is positive from 2001-2006
but negative from 2006-2011. The direct effect of manufacturing exposure on consumption
was negative from 2006-2011, as it was from 2001-2006. At the same time, the effect of
elasticity on housing prices was positive because more elastic areas had smaller housing
busts. Since manufacturing-heavy regions also had an elastic housing supply, these two
effects partially cancel each other out in estimates which do not account for the correlation
between housing supply elasticity and manufacturing. Putting together my results from
both time periods, I show that the effect of housing prices on consumption was small from
2001-2006 but large from 2006-2011 and that this difference is statistically significant.
A different consumption elasticity with respect to positive and negative house price shocks
is consistent with several existing theories. In the model proposed by Berger et al. (2015),
housing booms change the composition of home-owners by increasing the number of liquidity-
constrained individuals who own homes. Because the typical homeowner is more liquidity
constrained when housing prices start to fall than when they start to rise, falling prices
cause greater changes to consumption than rising prices do. A second possible reason is
that cashflow shocks, rather than changes to the value of home equity, are important for
household default and consumption. The effect of cashflow shocks on consumption may have
been greatest in areas with falling housing prices because homeowners' monthly mortgage
payments were highest in these areas, as these were the areas with the largest housing booms.
2.2 Data
The bulk of the estimates are based on panels of state- and city-level statistics described in
this section. Using this panel, I calculate five-year differences of many of the main variables
that comprise the years 2001-2006 (what I call the housing boom) and 2006-2011 (the bust);
results are similar using different years to denote the boom and bust. My main units of
analysis are states and U.S. CBSA / Metropolitan Divisions based on 2013 definitions.
Data on housing prices is from the Federal Housing Finance Administration (FHFA).
The main results of this paper are very similar using county-level housing price measures
102
from Zillow. Both are aggregated to the CBSA / Metropolitan Division level.
Several empirical results investigate the effects of local shocks on housing demand. As a
source of plausibly exogenous variation in local demand, I use two measures of local exposure
to industries which expanded or contracted during the relevant time periods. The first is a
measure of regions' ex ante exposure to industries with large ex post growth. Measures of
this sort are commonly known as "Bartik shocks" (from Bartik, 1991) and are widely used
in the empirical study of regional macro-economics. To create this measure, I predict income
growth for city i by interacting i's exposure to each industry j with industry j's national
payroll growth:
Bartiki = Exposurei, x Growth
This measure is constructed using 2-digit NAICS industries. I fix the year of exposure
to 1998 - prior to the start of the housing boom - and use growth over 1998-2006 to create
the measure.
A second source of regional demand variation comes from exposure to the manufacturing
sector. Manufacturing was the largest employer in 1998 (among 2-digit NAICS industries)
and underwent a dramatic decline over the time that coincided with the housing boom. Much
of the variation in the Bartik measure is due to variation in exposure to manufacturing.
Moreover, the relationship between manufacturing exposure and housing prices is also of
interest on its own. Regional labor force exposure data is provided by County Business
Patterns (CBP). I use 1998 as a base year for regional industry exposures. Using 2001 as a
base year yields very similar results. I focus on measuring labor force exposure at the 2-digit
NAICS level to ensure that measurements are uniform even as NAICS definitions changed
for more detailed categories.
Exposure to trade shocks provide an alternative source of exogenous demand. Using a
measure from Acemoglu et al. (2014), I find similar but noisier results.
To quantify regional elasticity of housing supply, I use the measure created by Saiz
(2010). This measure was downloaded from Albert Saiz's web site. Saiz (2010) provides
several version of the elasticity measure, including measures of legal barriers to construction,
103
land unavailability, and population size, as well as a composite index that combines all three.
Following the existing literature on consumption, I study both the overall elasticity measure
and the land unavailability measure, which I convert to 1-unavailability so that a greater
value for either measure corresponds to a more elastic area. Because the unavailable land
measure is less likely to be time-variant than the composite elasticity measure, previous
research has preferred this as an instrument for housing prices during the boom and bust,
as its time invariance may make it less affected by the factors that directly affected housing
prices. Therefore, most of the findings in this paper will use the land unavailability measure
as well.1
County-level housing unit counts are taken from Intercensal Estimates. Housing con-
struction is measured as the log change in total number of housing units, according to
intercensal estimates from the U.S. Census Bureau. Calculating new construction as the
number of permitted units (using HUD data) divided by existing units yields similar results.
Cities with a decline in units of above 0.05 log points are not included.
As additional control variables, I measure regional demographic features using largely
data collected from the 2000 Decennial Census. These demographic controls are per capita
income, the fraction of households with a mortgage, median age, and the fraction of houses
that are owner-occupied. I also measure the fraction of mortgages that were denied in each
region in 1996, which Mian and Sufi (2009) argue is a measure of latent mortgage demand.
Results are similar when using a variety of other control variables taken from the housing
literature, such as those used in Albouy (2015).
Aggregate consumption data is from BEA regional accounts, which includes household
consumption divided into several categories. I subtract housing and furniture from the overall
measure and durables measure in order to study only non-housing consumption. Because
regional accounts PCE data is only available at the state level, and not at the CBSA level,
estimates using this data have states as their unit of analysis rather than CBSAs.
Few sources of CBSA-level consumption data have a long history available. In order to
proxy for consumption at the CBSA level for the 2001-2006 period, I use retail employment
'Furthermore, Section 2.4 will present evidence that the composite elasticity measure is correlated with
unmeasured demand to a greater degree than the unavailable land measure, thus validating this approach.
104
measured in County Business Patterns, which Mian and Sufi (2014b) show is closely linked
to consumption. Guren et al. (2017) argue that this is a good consumption proxy. For 2006-
2011, I aggregate household-level data from Nielsen Homescan non-durables expenditure that
is collected as part of a nationally representative survey of retail consumption expenditures.
Table 2.1 shows summary statistics of the main variables.
2.3 Theoretrical Framework and Motivating Evidence
The size of the housing boom varied greatly by city. Figure 2-1 shows the path of housing
prices in the 20 largest U.S. cities beginning in 2000. Cities in the American Southwest and
on the coasts, such as Boston, Las Vegas, San Francisco and New York, experienced the
largest booms. But many cities - those at the bottom of the graph - barely had housing
booms at all. These are mostly Midwestern and Southern cities. The line at the very
bottom of the graph represents Dallas, which had the smallest housing boom among major
U.S. cities.
In this section, I describe the benchmark framework that explains variation in housing
prices accommodating both heterogeneous demand shocks and heterogeneous housing sup-
ply elasticities. I derive predictions of this model and relate these predictions to previous
research on the housing market from 2001-2011. I then discuss how these predictions relate
to estimates of the house-price consumption elasticity.
I begin with a model of the housing market similar to models in Saiz (2010), Glaeser et
al. (2008) and Davidoff (2013). Suppose that housing is supplied in a spot market. Cities
vary in their elasticity of housing supply .2 The quantity of new housing supplied in city
i is qi. This is increasing in housing price shocks pi, which are mediated by housing supply
2I abstract from housing demand elasticity which in reality may also vary by city. Harmon (1988)
reviews research on demand elasticity and estimates a long-run average demand elasticity of approximately
1, justifying this assumption in my model. In my empirical estimates, I show my results are robust to the
inclusion of control variables associated with demand elasticity.
105
elasticity. Supply and demand are:
A log(q') = /j Alog(pi). (2.1)
A log(q') = -A log(pi) + A log(yi). (2.2)
This yields
A log q A log(yi) (2.3)
#3 + I
1
A log pi = A log(yi) (2.4)
# + 1
A large body of recent literature implicitly adopts the assumption that the housing boom
was caused by a national housing demand shock that was either uniform or independent
of the supply elasticity. Under this assumption, it is possible to to study the effect of
housing prices on various outcomes using the Saiz (2010) supply elasticity as an instrument
for housing prices. Combining this assumption with Equations 2.4 and 2.3 yields several
empirical predictions, some of which have been tested by the existing literature.
The first prediction is that more elastic regions should have smaller price increases. Pre-
vious papers, such as Glaeser et al. (2008), have found that this prediction does hold em-
pirically. I confirm their findings in Table 2.2, which estimates an empirical analogue to
Equation 4 under the assumption that demand shocks are independent of housing supply
elasticity:
A log pi = Elasticityi + c, (2.5)
Using both measures of housing supply elasticity, I find that inelastic cities had larger booms
and larger busts, and these relationships are statistically significant at the 1% level. However,
the small R2 of these specifications indicates that much of the variation in housing prices
remains unexplained.
The second prediction is that elastic regions should have greater quantity growth than
inelastic regions, at least from 2001-2006.' Davidoff (2014) and Davidoff (2013) show that
3 Glaeser et al. (2008) show that when prices are following a housing bubble, the theoretical association
between prices and elasticity is of ambiguous sign.
106
this does not hold over periods lasting several decades. I show this for the 2001-2006 period
in Table 2.3, which again estimates Equation 2.5, but with quantities (number of housing
units) as the dependent variable rather than prices. The overall rate of permitting in the
more-inelastic and more-elastic half of the country is graphed in Figure 2-4. It is negative
using both measures from 2001-2006, statistically significantly so for the overall elasticity
measure. Given the large and positive price effects of housing supply using both measures,
this is hard to make sense of these results in the uniform shock framework. Instead, it implies
that city-level housing supply elasticities are likely correlated with local demand shocks. If
areas with an inelastic housing supply had large demand shocks, then they would have had
larger price increases but not necessarily smaller construction booms.
The estimated association between composite elasticity and new units, shown in Column
2, is large enough to reject zero effect at the 1% level, whereas the association between
available land and new units is negative but not so large as to reject zero effect even at the
10% level. This provides some support for the view that the available land measure is less
endogenous than the composite elasticity measure in the sense that it is less correlated with
unobserved demand shocks, making it more appropriate to use as an instrument for housing
prices. By contrast, neither elasticity measure has an association with new construction that
is statistically distinguishable from zero from 2006-2011.
Another possible concern with the assumption of independent demand shocks is that it
gives rise to incorrect predictions about housing prices in specific regions of the United States.
The housing boom was especially large in cities located in the Southwestern U.S. despite the
fact that these cities had a high housing supply elasticity. Table 2.4 estimates Equation 2.5
adding an indicator for cities in Nevada, Arizona and New Mexico. In these cities, housing
prices rose 0.26 log points more than what one would expect from their elasticity alone
during the boom and fell by 0.34 log points more than one would expect during the bust.
These inconsistencies with the "uniform shock" model provide a motivation for incorpo-
rating city-specific demand shocks. From Equations 2.3 and 2.4, one can make three key
predictions about housing demand shocks. First, anything that raises city payrolls can raise
demand for housing in that city, and therefore lead to more construction and higher prices.
Second, these effects are mediated by housing supply elasticity: The effect on prices should
107
be greater in cities with an inelastic housing supply and the effect on quantities should be
greater in cities with an elastic housing supply. Third, to explain why construction is un-
conditionally negatively correlated with housing supply elasticity, demand shocks should be
greater in inelastic areas.
Local demand shocks also matter for estimates of the consumption-house price elasticity.
If demand shocks are correlated with housing supply elasticity elasticity, then the latter may
not be a valid instrument for housing prices, as Davidoff (2014) and Davidoff (2013) argue.
The reason is that local economic conditions which affect housing demand may also directly
affect the outcome variables in question. For example, if local income shocks are correlated
with the housing price elasticity, then the negative correlation between consumption growth
and house price growth may be due to income shocks rather than housing prices per se.
Adding demand shocks as control variables may therefore provide new insight into the reasons
for the correlation between housing prices and consumption.
The next section will show that exposure to growing industries, and specifically to the
manufacturing sector, satisfies the predictions for local demand shocks and resolves the
puzzles with the housing market model. It also changes the coefficient estimates for the
housing-price consumption elasticity.
2.4 Empirical Results
The empirical results are divided into three parts. The first part presents estimates of the
effects of industry exposure on housing prices. Compared to models built on the assump-
tion of independent or uniform demand shocks, a model which explicitly accounts for local
demand explains more of the variation in housing prices from 2001-2006. Second, I revisit
the puzzles discussed in the previous section. Accounting for local housing demand shocks
and their correlation with housing supply elasticity partially solves the puzzles. In the third
section, I provide new estimates of the elasticity of consumption with respect to housing
prices. I do this first by using the Saiz elasticity as an instrument for housing prices and
controlling for local demand shocks.
108
2.4.1 Housing Prices
The 2001-2006 housing boom was larger in cities with positive predicted demand shocks -
areas with large and positive Bartik shocks or less manufacturing exposure. Moreover, the
effect of demand on prices was greatest in cities where the housing supply was inelastic, which
allows for a rejection of the null hypothesis that housing supply elasticity alone explains why
some areas had larger housing booms and busts than others. Regional demand shocks and
their interaction with supply elasticity have greater explanatory power. This is consistent
with the theoretical predictions developed in Section 2.4. Furthermore, estimates of the effect
of supply elasticity on housing prices and other outcomes that do not control for demand
associated with industry exposure suffer from an omitted variables bias. This is because
supply elasticity is highly correlated with industry exposure, and industry exposure affects
housing prices directly through its effects on housing demand.
Visual evidence for the association between available land and manufacturing exposure
is shown in Figure 2-2. Table 2.6 formally confirms the strength of this relationship using
several supply elasticity measures and industry exposure, including the manufacturing ex-
posure measure, the Bartik shock, and import competition as measured by Acemoglu et al.
(2014). These estimates consistently show that areas with more available land - those that
are easier to build in - had great ex ante exposure to the manufacturing sector than areas
that are harder to build in. Furthermore, Table 2.14 shows that an association between hou-
sing supply elasticity and manufacturing exposure even holds within-states across-CBSAs,
pointing to a strong fundamental (as opposed to merely regional) link between land avai-
lability and industry location. A natural explanation for this link is that factories require
space, and therefore areas with lots of unavailable land have more of them.
Table 2.12 shows estimates of the effect of industry exposure on local payrolls. Their
strong correlation with regional payrolls bolsters the argument that they are an omitted
variable that directly affects housing demand, as payrolls are the mediating variable that
affects housing prices in the framework introduced in the previous section. This association is
not surprising; as discussed by Autor et al. (2013) (and many other papers), greater exposure
to the manufacturing sector is associated with negative labor market outcomes in the early
109
2000s. Columns 1 and 3 show this for the boom and bust period respectively. Columns 2
and 4 quantify the effect of the Bartik shock on regional payrolls. As expected, the signs are
positive and statistically significant for the Bartik shock. Furthermore, because the same
industries continued to grow from 2001-2006 as from 2006-2011, the sign of both shocks
during both the boom and the bust.
Visual evidence in 2-3 shows a strong negative relationship between house price growth
and ex ante manufacturing share. CBSAs with more manufacturing workers had lower house
price growth. The evidence in the figure suggests a somewhat nonlinear effect, whereby ma-
nufacturing concentration is less informative for areas with the greatest house price growth.
Table 2.13 in the Appendix uses the change in exposure to Chinese imports as a regional
demand shock, a measure created in Acemoglu et al. (2014). Although the estimates in this
table are noisier than those using industry shares, the signs and directions are consistent
with demand shocks.
A prediction of the empirical framework is that the interaction between housing elasticity
(or available land) and demand shocks should matter for housing prices. Tables 2.5 and 2.7
show regression estimates from specifications of the following form:
AY = a + 1Elasticityj + 2Exposurej + 3Elasticityj x Exposurej + E (2.6)
where Exposures is either the Bartik shock or manufacturing exposure, Y is either prices or
quantities, and the time period is either 2001-2006 or 2006-2011, respectively the boom and
bust.
Figure 2-3 shows the strong negative relationship between housing prices and manufactu-
ring share at the CBSA level. Cities with more manufacturing experienced relatively smaller
housing booms than cities with more manufacturing. The relationship also appears to be so-
mewhat nonlinear, with there being little effect on housing prices for cities with a sufficiently
low fraction of the workforce in manufacturing.
Columns 1 and 2 of Table 2.5 show how the interaction between demand shocks and
elasticity affected housing prices from 2001-2006. In line with theoretical predictions, regions
with more exposure to growing industries - meaning either a higher Bartik shock or a lower
110
manufacturing share - had the greatest growth in housing prices. However, in areas with
more available land, the effect of growing industries on prices was dampened.4
The signs of the main effects are flipped in Columns 3 and 4 compared to Columns 1
and 2, meaning that areas with greater exposure to industries that grew from 2001-2006 had
housing prices that fell in relative terms, rather than rose.
The model in Section 2.4 does not explain why positive income shocks from 2001-2006
should be associated with falling housing prices from 2006-2011. This result is at odds
with a model in which housing demand comes only from local income shocks. Rather, it is
consistent with the mean reversion that is a general feature of housing markets which predates
the most recent boom-bust cycle. Glaeser and Gyourko (2006) explain mean reversion in the
housing market with a model of slow-moving construction combined with mean-reverting
fundamental shocks. Other authors, such as Shiller (2015), instead argue that this pattern
is essentially behavioral, reflecting extrapolation by investors.
2.4.2 Housing Market Puzzles
I now show how accounting for housing demand shocks affects the empirical puzzles discussed
in Section 2.3. Both the housing supply puzzle and the Southwest Cities puzzle are reduced,
but not eliminated, after incorporating industry shares as demand shocks. This means that
while industry exposure is likely an important and typically unmeasured factor affecting
housing demand, it may not be the only one.
The first puzzle is that areas with an inelastic housing supply had more new construction
from 2001-2011 than areas with an elastic housing supply. Table 2.7 jointly considers the
effect of elasticity and industry exposure on construction. The main finding is that larger
demand shocks led to more construction, particularly so from 2001-2006, the time period
that is puzzling from the perspective of elasticity alone. Furthermore, theory predicts that
the interaction between elasticity and demand shocks should be positive, i.e., in areas with
a more elastic housing supply, positive shocks increase housing quantities by more than in
areas with a negative housing supply. Estimates on the interaction terms in Table 2.7 show
a negative affect, however, albiet one that is never precisely estimated enough to reject a
4A similar result holds when using the composite supply elasticity measure rather than unavailable land.
111
zero (or even positive interaction) at conventional levels of statistical significance. This is
either because the data is simply noisy, or because there are other omitted variables which
continue to affect housing demand even as they are correlated with supply elasticity. The
disappearance of the large and highly significant negative effect shown in Table 2.3 is therefore
only a partial resolution of this puzzle.
Table 2.8 shows that the "excessive" growth in Southwestern cities is partly explained
by demand shock associated with the manufacturing sector. Controlling for demand shocks,
the estimated coefficient on the Southwest cities indicator falls to about 0.19 log points from
2001-2006 and to 0.33 log points from 2006-2011 (significant at 1%), shown in Columns 1
and 2. Additional demographic controls (Columns 3-4 reduce the estimated effect further),
and controls for industry shares chosen using a doubly-robust post-LASSO procedure yields
smaller results still.5 Nonetheless, the estimated coefficient on the Southwest dummy are
still highly statistically significant, indicating that this puzzle is also only partially solved.
This section has explored the relationship between industry exposure, housing supply
elasticity and housing prices. I have shown that the incorporation of manufacturing exposure
as a demand shock partially resolves both puzzles.
2.4.3 Consumption-House Price Elasticity Estimates
The dramatic rise and fall in housing prices from 2001-2011 has been identified as a key reason
for the equally dramatic rise and fall in household consumption. Theoretical research in this
area has relied on the robust and large relationship between housing prices and consumption
documented by recent empirical work for both periods of rising and falling prices.6 However,
5To do this, first the independent variable (prices) and the treatment variable (the Southwest) indicator
are independently LASSO-regressed on the possible controls, which include all two-digit NAICS industry
shares and the demographic controls. The LASSO implementation used here is the lassoregress stata package
by Wilbur Townsend, which uses cross-validation to select parameters. The final OLS regression then controls
for the union of the control variables selected in both LASSO procedures. The algorithm is described in
further detail in Chernozhukov et al. (2015).
6 What follows is an abbreviated list of the empirical papers in this area which are most closely related
to mine: Mian et al. (2013) show that regions of the U.S. where household debt/income ratios increased the
most between 2002 and 2006 had the greatest declines in housing consumption between 2006 and 2009; this
holds even when housing supply elasticity as an instrument for debt/income ratios. Mian and Sufi (2014a)
use a similar technique to study household borrowing and spending from 2002 to 2006. Kaplan et al. (2016)
replicate the findings of Mian et al. (2013) using store-level scanner data. Dynan (2012) uses household-level
data from the Panel Study of Income Dynamics to show that consumption fell most among highly-leveraged
112
the estimated consumption-house price elasticity changes when I control for local industry
exposure.
Table 2.9 shows estimates of following OLS equation:
ALog(C.) = #3ALog(P) + 6i
where i indexes MSAs and time-differences are taken over 2001-2006 and 2006-2011. I follow
Campbell and Cocco (2007) and Attanasio et al. (2002) in estimating the consumption
response to housing prices, rather than housing wealth which Mian et al. (2013) and Kaplan
et al. (2016) use. 7
The estimates show a positive correlation between housing prices and the several cate-
gories of consumption during both 2001-2006 and 2006-2011. This table uses a state-level
measure of aggregate consumption from PCE regional accounts as well as CBSA-level esti-
mates that use retail employment as a proxy for consumption, following Guren et al. (2017),
as well as non-durables consumption from Nielsen Homescan data for the years 2006-2011
only.
A larger set of estimates from NIPA state-level regional accounts data is shown in Ta-
bles 2.9 of the Appendix, for the years 2001-2006. Consistent with theoretical predictions,
durables consumption has a greater elasticity than non-durables. 8 The association between
housing prices and food and beverages consumption is similar to overall nondurables con-
sumption.9
The OLS elasticity estimates are comparable to those found in Kaplan et al., 2016.
households between 2007 and 2009 even when controlling for overall changes in household wealth. Closely
related to these papers is the finding of Mian and Sufi (2014b) that falling housing prices affected local
regional employment in the non-tradables sector, which is closely associated with local consumption. This
list neglects both relevant empirical research from before the Great Recession and studies which estimate
the effects of housing prices on outcomes other than household consumption.
7Berger et al. (2015) convert the housing net worth elasticity estimated by Mian et al. (2013) to a house
price elasticity by multiplying it by the mean ration of housing wealth to total wealth, 0.25-0.33. Reversing
this calculation would convert the house price elasticities estimated here to housing net worth elasticities.
8I subtract PCE housing consumption from PCE durables consumption to measure non-housing durables.
9 Changes in consumption expenditures are likely driven by both increased real consumption and higher
prices. Stroebel and Vavra (2014) and Kaplan et al. (2016) show rising goods prices are associated with rising
housing costs and that approximately 20% of the increased expenditure is due to rising prices. Unfortunately,
no regional PCE deflators exist at the state level for the time periods under consideration here, so I do not
separately calculate the effects on real consumption and its price.
113
Table 4 in Kaplan et al., 2016 shows an estimated elasticity of consumption with respect ot
housing prices of 0.12-0.18 over the 2006-2009 period, i.e. the bust; for 2006-2011, I estimate
elasticities of 0.12 (for CBSA retail employment, which proxies for consumption), 0.16 (for
NIPA goods less housing) and 0.19 (in Nielsen data). All of the coefficient estimates are all
statistically significant at the 1% level.
Next, I follow Mian and Sufi (2011), Mian et al. (2013) and others in instrumenting
for housing prices using the Saiz (2010) land availability measure. As the previous section
showed, a higher housing price elasticity was associated with a smaller boom and bust. This
IV procedure is a first pass towards purging local demand shocks from estimates of the
consumption-house price elasticity. Controlling for industry mix or manufacturing exposure
as well alleviates many of the concerns with demand shocks that are correlated with the
housing supply elasticity, as shown in the previous section. The specification therefore
includes controls for these variables: The second state is
AConsumption = /1 1AHousingPrices + 2DemandShock (2.7)
and the first stage is
AHousingPrices=  /1SaizElasticity + f 2DemandShock (2.8)
Results from specifications without any controls are shown in Table 2.10. Specificati-
ons using additional measures of consumption are in Tables 2.15 (for 2001-2006) and 2.16
(for 2006-2011). Consistent with previous papers, I consistently find an effect between 0.1
and 0.25, with the larger estimates for durables and smaller estimates for non-durables.
State-level estimates are more noisily measured but otherwise consistent with CBSA-level
estimates.
Comparing the OLS to the 2SLS estimates, it is clear that the instrumented estimates are
in many cases larger than the OLS estimates. This is true as well in, for example, Kaplan et
al. (2016) and Mian et al. (2013). The reason this is surprising is that the likely direction of
bias in the OLS estimates is upwards: Any unmeasured income or wealth shock would raise
demand for both non-housing consumption and for housing, inducing a spurious positive
114
correlation between housing prices and other kinds of consumption. Therefore, one would
expect that a valid instrumental variables strategy should reduce the estimated association
between housing prices and consumption.
This fact, combined with the positive observed elasticity between elasticity and industry-
exposure, motivate the addition of industry measures as control variables. Simply adding
the Bartik shock as a control variable, in Table 2.11, reduces the estimated effect of housing
prices on retail employment from 0.14 to 0.05 from 2001-2006. State-level measures of goods
spending fall from 0.125 to 0.11. Using manufacturing share as a control, and using LASSO
to choose industry shares as controls, yields similar results (shown in Tables 2.17 and 2.18).
The effects are reversed during the bust period. Because greater industry growth is
associated with greater declines in housing prices during the bust period, the sign of the
omitted variables bias is reversed. Adding the Bartik shock as a control variable actually
increases coefficient estimates from 2006-2011; the estimated effect on retail spending rises
from 0.14 to 0.20 during this time period, and the state-level measure of goods is hardly
affected.
Combining the results from both time periods, I can reject that the elasticity of retail
employment with respect to housing prices is the same from 2001-2006 and 2006-2011. This
asymmetry is not apparent without controls, because the direction of bias varies between
time periods.
The findings in this section have two main implications for empirical research on the
effects of housing prices on consumption and other economic outcomes. The first implication
is that there are good reasons to believe that regiona# demand shocks are correlated with
the elasticity of housing supply. Therefore, the empirical research should either control for
relevant demand shocks - such as ex ante industry shares - or use methodologies that do
not rely on regional variation alone. In this case, controlling for industry shocks decreased
the estimated effect of housing prices on consumption from 2001-2006 but decreased it from
2006-2011. For other variables, the sign and magnitude of the bias may be different.
The second implication is that variation in exposure to underlying demand shocks may
be important for understanding heterogeneous outcomes during the boom and bust periods.
This is especially salient when studying the interaction of housing prices and individual
115
characteristics, such as home-ownership or wealth. If variation in these other characteristics
is correlated with variation in exposure to demand shocks, then it may be the demand shocks
rather than housing prices that explain economic behavior. For example, if manufacturing
workers are poorer or more likely to be renters than non-manufacturing workers, then the
effects of manufacturing decline may look like differential exposure to the housing boom.
2.5 Conclusion
This paper has examined the effects of housing demand shocks on housing prices and con-
sumption during the boom and bust. My findings indicate that demand shocks due to
industry exposure explain much of the correlation between housing prices, income and con-
sumption from the years 2001-2011.
From 2001-2006, regions with employment in high-growth industries had greater housing
demand. Housing prices rose by more in these regions, and most of all in regions where the
housing supply was inelastic. Controlling for local demand shocks partially solves puzzles
that arose under previous work which did not control for housing demand shocks. In par-
ticular, an inelastic housing supply is associated with greater construction over this time
because inelastic housing supply is associated with positive job growth. Controlling for de-
mand shocks also increases the explained fraction of housing price variance and reduces the
"excess" housing price growth that occurred in the American Southwest. Finally, controlling
for demand shocks reduces the estimated elasticity of durable and non-durable consumption
with respect to housing prices by a out 65%.
From 2006-2011, exposure to high-growth industries was associated with rising payrolls
and rents but falling housing prices. This is consistent with mean reversion following the
2001-2006 boom rather than direct changes in housing demand. Controlling for demand
shocks does not decrease the estimated elasticity of consumption with respect to housing
prices.
116
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118
Table 2.1: Summary Statistics
CBSA State
2001-2006 2006-2011 2001-2006 2006-2011
Mean St. Dev Mean St. Dev Mean St. Dev Mean St. Dev
Bartik Shock 1.07 0.03 1.07 0.03 1.07 0.02 1.07 0.02
Manuf. Share 0.16 0.08 0.16 0.08 0.15 0.06 0.15 0.06
Elasticity 2.55 1.44 2.55 1.44 2.24 1.03 2.24 1.03
House Price 0.32 0.2 -0.17 0.23 0.37 0.19 -0.23 0.21
Payrolls 0.19 0.1 0.06 0.08 0.21 0.07 0.09 0.07
Permits 0.08 0.05 0.03 0.02 0.07 0.04 0.03 0.01
Retail Emp. 0.06 0.09 -0.07 0.07 0.06 0.06 -0.07 0.04
1-Unavail Land 0.74 0.21 0.74 0.21 0.76 0.15 0.76 0.15
Durables 2947 372 2844 421
Goods 10124 890 11055 1060
Log(Durables) 0.15 0.07 -0.04 0.08
Log(Goods) 0.21 0.05 0.09 0.05
Log(Total C) 0.24 0.03 0.11 0.04
Total C 24897 3343 27787 3932
Count 265 265 51 51
Table 2.2: House Prices and Elasticity
(1) (2) (3) (4)
CBSA Price CBSA Price State Price State Price
2001-2006 2006-2011 2001-2006 2006-2011
Avail. Land -0.523*** 0.467*** -0.535*** 0.560*
(0.0492) (0.0613) (0.151) (0.218)
Constant 0.704*** -0.513*** 0.770*** -0.656***
(0.0403) (0.0498) (0.116) (0.174)
R2 0.293 0.182 0.207 0.166
N 265 265 48 48
Sources: Saiz (2010), FHFA.
Retail measures retail employment; Goods measure goods consumption.
* p < 0.05, ** p < 0.01, *** p < 0.001
119
Table 2.3: Supply Elasticity and Housing Units
(1) (2) (3) (4)
Units Units Units Units
2001-2006 2001-2006 2006-2011 2006-2011
Avail. Land -0.0186 -0.00609
(0.0164) (0.0116)
Elasticity -0.00704*** -0.00250
(0.00195) (0.00133)
Constant 0.0949*** 0.0990*** 0.0424*** 0.0442***
(0.0133) (0.00660) (0.00933) (0.00411)
R2 0.00561 0.0384 0.00176 0.0138
N 263 263 265 265
Sources: Saiz (2010), HUD.
Units measured as log change in housing units.
* p < 0.05, ** p < 0.01, *** p < 0.001
Table 2.4: Supply Elasticity and Prices in Southwest States
(1) (2) (3) (4)
Prices Prices Prices Prices
2001-2006 2006-2011 2001-2006 2006-2011
Elasticity -0.0675*** -0.0528*** 0.0712*** 0.0664***
(0.0117) (0.0109) (0.0117) (0.0114)
Southwest 0.213*** 0. 140** -0.294*** -0.275**
(0.0444) (0.0502) (0.0855) (0.0863)
Bartik Shock 2.048*** -0.572
(0.303) (0.393)
Constant 0.481*** -1.825*** -0.339*** 0.307
(0.0327) (0.340) (0.0341) (0.439)
R2  0.271 0.362 0.258 0.261
N 265 264 265 264
Sources: ,
Southwest indicator equals 1 for Nevada, New Mexico and Arizona.
* p < 0.05, ** p < 0.01, *** p < 0.001
120
Table 2.5: Housing Prices, Demand Shocks, and Elasticity
(1) (2) (3) (4)
House Prices House Prices House Prices House Prices
2001-2006 2001-2006 2006-2011 2006-2011
Avail. Land 3.564* -8.640***
(1.466) (2.027)
Bartik Shock 4.760*** 4.425*** -7.032*** -3.657***
(1.033) (0.546) (1.471) (0.760)
Avail. Land x Bartik Shock -3.548** 8.079***
(1.313) (1.816)
Elasticity 0.886*** -1.107***
(0.191) (0.231)
Elasticity x Bartik Shock -0.853*** 1.067***
(0.176) (0.214)
Constant -4.694*** -4.448*** 7.412*** 3.709***
(1.158) (0.603) (1.645) (0.835)
R2   0.396 0.397 0.239 0.279
N 264 264 264 264
Sources: Saiz (2010), CBP, HUD.
* p < 0.05, ** p < 0.01, *** p < 0.001
Table 2.6: Housing Elasticity and Industry Exposure
(1) (2) (3) (4) (5) (6)
Avail. Land Avail. Land Avail. Land Elasticity Elasticity Elasticity
Manuf. 0.639*** 5.212***
(0.150) (1.214)
Bartik Shock -2.002*** -13.34***
(0.363) (2.889)
Import Exp. 0.0131* 0.0539
(0.00664) (0.0469)
Constant 0.639*** 2.961*** 0.715*** 1.705*** 17.33*** 2.438***
(0.0310) (0.399) (0.0210) (0.199) (3.221) (0.143)
R2  0.0562 0.0979 0.0110 0.0792 0.0919 0.00394
N 264 264 264 264 264 264
Sources: Saiz (2010), CBP.
* p < 0.05, ** p < 0.01, *** p < 0.001
121
Table 2.7: Housing Units and Elasticity, Controlling for Industry Bartik
(1) (2) (3) (4)
Units Units Units Units
2001-2006 2001-2006 2006-2011 2006-2011
Avail. Land 1.082 0.0737
(0.569) (0.377)
Bartik Shock 1.304** 0.542* 0.399 0.225
(0.442) (0.223) (0.284) (0.126)
Avail. Land x Bartik Shock -0.958 -0.0560
(0.510) (0.341)
Elasticity 0.00751 -0.0453
(0.0618) (0.0353)
Elasticity x Bartik Shock -0.0101 0.0410
(0.0566) (0.0325)
Constant -1.381** -0.510* -0.413 -0.211
(0.494) (0.247) (0.314) (0.138)
R2  0.139 0.134 0.132 0.132
N 262 262 264 264
Sources: Saiz (2010), CBP, HUD.
* p < 0.05, ** p < 0.01, *** p < 0.001
Table 2.8: Prices in Southwest States and Elasticity, Controlling for Industry Shares
(1) (2) (3) (4) (5) (6)
Prices Prices Prices Prices Prices Prices
01-06 06-11 01-06 06-11 01-06 06-11
Southwest 0.188*** -0.327*** 0.166** -0.293*** 0.113* -0.215*
(0.0496) (0.0895) (0.0592) (0.0793) (0.0503) (0.0886)
Avail. Land -0.448*** 0.467*** -0.386*** 0.400*** -0.238*** 0.215***
(0.0508) (0.0636) (0.0520) (0.0626) (0.0473) (0.0594)
Controls Ind Ind Ind, Demo Ind, Demo LASSO LASSO
R2 0.421 0.264 0.521 0.398 0.619 0.572
N 264 264 264 264 264 258
Sources: Saiz (2010), FHFA, CBP, US Census Bureau.
Industry controls are Bartik shock and manufacturing share; Demographic controls from 200 Census.
LASSO-chosen controls are chosen using double-robust LASSO from industry controls and shares of 2-digit
NAICS industries using doubly-robust procedure as described in the text. Southwest indicator equals 1 for
Nevada, New Mexico and Arizona.
* p < 0.05, ** p < 0.01, *** p < 0.001
122
Table 2.9: House Prices and Consumption: OLS
(1) (2) (3) (4) (5)
CBSA CBSA CBSA State State
Retail Retail Nielsen Goods Goods
01-06 06-11 06-11 01-06 06-11
House Prices 0.245*** 0.115*** 0.193*** 0.113*** 0.160***
(0.0211) (0.0170) (0.0476) (0.0221) (0.0285)
Constant -0.0204* -0.0520*** 0.116*** -0.0420*** 0.124***
(0.00822) (0.00476) (0.0166) (0.00634) (0.00933)
0.326 0.165 0.0414 0.411 0.453
N 264 265 265 51 51
Sources: NIPA regional accounts, FHFA, CBP.
Retail measures retail employment; Goods measure goods consumption excluding housing.
* p < 0.05, ** p < 0.01, *** p < 0.001
Table 2.10: House Prices and Consumption: Typical 2SLS
(1) (2) (3) (4) (5)
CBSA CBSA CBSA State State
Retail Retail Nielsen Goods Goods
01-06 06-11 06-11 01-06 06-11
House Prices 0.141** 0.137*** 0.299 0.125 0.182**
(0.0433) (0.0406) (0.153) (0.0812) (0.0707)
Constant 0.0122 -0.0484*** 0.134*** 0.168*** 0.129***
(0.0140) (0.00800) (0.0289) (0.0307) (0.0175)
R2 0.267 0.159 0.0287 0.204 0.444
N 264 265 265 48 48
Sources: NIPA regional accounts, Saiz (2010), FHFA, CBP.
Goods consumption categories from NIPA exclude housing.
* p < 0.05, ** p < 0.01, *** p < 0.001
123
Table 2.11: Consumption and Elasticity, Controlling for Industry Bartik
(1) (2) (3) (4) (5)
CBSA CBSA CBSA State State
Retail Retail Nielsen Goods Goods
01-06 06-11 06-11 01-06 06-11
House Prices 0.0453 0.197*** 0.291 0.108 0.179**
(0.0573) (0.0473) (0.177) (0.0783) (0.0693)
Bartik Shock 1.009*** 0.481*** -0.0882 314.2*** -71.39
(0.226) (0.144) (0.554) (66.20) (59.37)
Constant -1.075*** -0.571*** 0.230 0.0457 0.157***
(0.238) (0.155) (0.602) (0.0269) (0.0359)
R2 0.253 0.150 0.0299 0.424 0.457
N 264 264 264 48 48
Sources: NIPA regional accounts, Saiz (2010), FHFA, CBP, CBP.
Retail measures retail employment and Goods measure total goods
from NIPA excluding housing.
* p < 0.05, ** p < 0.01, *** p < 0.001
124
2.6 Figures
UO -
04
a
C 0
a.
0-
2000 2002 2004 2006 2008 2010 2012
Year
Figure 2-1: Housing Prices in 20 Largest CBSAs
125
LO
0
CD
0 0
N -
.0o -
0 5 10 15
Saiz (2010) Elasticity
Figure 2-2: Elasticity vs Manufacturing Share
0
U -
00
0)0
C0 0
0 0. 
C ~q* 0 .0
*0*
HwF arg0 00 ~I0 0 0 20 0 of
0 2 .46 .0 .08  
Hous Prc Grth 201-0
0 0 %
0 .2 4.6.8
House Price Growth, 2001-2006
Figure 2-3: 2001-2006 House Price Growth and 1998 Manufacturing Employment Share
126
aC-2
:t-! 7
2C100 2dO5 2d10 2d15
Year
Inelastic Cities - Elastic Cities
Figure 2-4: Total Permitting Post-2000, in Above- and Below-Median Elasticity Half of
Country
127
2.7 Appendix Tables
Table 2.12: Payroll Growth and Industry Shares
(1) (2) (3) (4)
Payrolls Payrolls Payrolls Payrolls
2001-2006 2006-2011 2001-2006 2006-2011
Manuf. -0.637*** -0.238**
(0.101) (0.0867)
Bartik Shock 1.476*** 0.444
(0.249) (0.226)
Constant 0.297*** -1.441*** 0.100*** -0.431
(0.0171) (0.276) (0.0151) (0.250)
R 0.226 0.215 0.0471 0.0290
N 264 264 264 264
Sources: Saiz (2010), FHFA, County Business Patterns.
* p < 0.05, ** p < 0.01, *** p < 0.001
128
Table 2.13: Housing Prices, Import Exposure, and Elasticity
(1) (2) (3) (4)
House Prices House Prices House Prices House Prices
2001-2006 2001-2006 2006-2011 2006-2011
Avail. Land -0.531*** 0.509***
(0.0935) (0.129)
Import Exp. -0.0401 -0.0533** 0.0519 0.0589**
(0.0356) (0.0201) (0.0480) (0.0226)
Avail. Land x Import Exp. 0.0202 -0.0375
(0.0429) (0.0580)
Elasticity -0.0848*** 0.0954***
(0.0201) (0.0220)
Elasticity x Import Exp. 0.00972 -0.0127
(0.00626) (0.00687)
Constant 0.761*** 0.590*** -0.594*** -0.464***
(0.0750) (0.0553) (0.103) (0.0642)
R2 0.324 0.296 0.205 0.253
N 264 264 264 264
Sources: Saiz (2010), CBP, HUD, Acemoglu et al (2016).
Import exposure measures change in exposure to Chinese imports from 1991-2011.
* p < 0.05, ** p < 0.01, *** p < 0.001
Table 2.14: Housing Elasticity and Industry Shares, with State FEs
(1) (2) (3) (4)
Avail. Land Avail. Land Elasticity Elasticity
Manuf. 0.348* 4.289***
(0.148) (1.117)
Bartik Shock -1.390*** -10.42***
(0.402) (2.791)
Constant 0.686*** 2.282*** 1.855*** 14.10***
(0.0279) (0.443) (0.188) (3.097)
State FE Yes Yes Yes Yes
R2 0.511 0.527 0.549 0.548
N 264 264 264 264
Sources: Saiz (2010) FHFA, CBP.
* p < 0.05, ** p < 0.01, *** P < 0.001
129
Table 2.15: House Prices and Consumption: Other Goods, 2001-2006
(1) (2) (3) (4) (5) (6)
Total Goods Durables Nondurables Vehicles Food and Bev
House Prices 0.104* 0.125 0.241* 0.0749 0.397** 0.0920
(0.0505) (0.0812) (0.117) (0.0713) (0.144) (0.0670)
Constant 0.197*** 0.168*** 0.0608 0.213*** -0.156** 0.141***
(0.0192) (0.0307) (0.0417) (0.0280) (0.0507) (0.0252)
R2 0.340 0.204 0.369 0.0968 0.377 0.205
N 48 48 48 48 48 48
Sources: NIPA regional accounts, Saiz (2010), FHFA.
Goods consumption categories from NIPA exclude housing.
* p < 0.05, ** p < 0.01, *** p < 0.001
Table 2.16: House Prices and Consumption: Other Goods, 2006-2011
(1) (2) (3) (4) (5) (6)
Total Goods Durables Nondurables Vehicles Food and Bev
House Prices 0.163** 0.182** 0.298** 0.130* 0.553*** 0.137
(0.0606) (0.0707) (0.102) (0.0644) (0.135) (0.0710)
Constant 0.146*** 0.129*** 0.0315 0.163*** 0.0322 0.162***
(0.0145) (0.0175) (0.0254) (0.0163) (0.0353) (0.0161)
R2 0.537 0.444 0.448 0.329 0.463 0.316
N 48 48 48 48 48 48
Sources: NIPA regional accounts, Saiz (2010), FHFA.
Goods consumption categories from NIPA exclude housing.
* p < 0.05, ** p < 0.01, *** p < 0.001
130
Table 2.17: Consumption and Elasticity, Controlling for Manufacturing Share
(1) (2) (3) (4) (5)
CBSA CBSA CBSA State State
Retail Retail Nielsen Goods Goods
01-06 06-11 06-11 01-06 06-11
House Prices 0.0736 0.183*** 0.305 0.113 0.172*
(0.0527) (0.0452) (0.174) (0.0948) (0.0776)
Manuf -0.394*** -0.196*** -0.0235 -0.140 0.137
(0.0782) (0.0534) (0.241) (0.238) (0.160)
Constant 0.0975*** -0.00917 0.138* 0.193** 0.105**
(0.0272) (0.0148) (0.0593) (0.0700) (0.0389)
R2 0.291 0.171 0.0265 0.231 0.473
N 264 264 264 48 48
Sources: NIPA regional accounts, Saiz (2010), FHFA, CBP, CBP, US Census Bureau.
Retail measures retail employment and Goods measure total goods form NIPA excluding housing.
* p < 0.05, ** p < 0.01, *** p < 0.001
Table 2.18: Consumption and Elasticity, Controlling for Post-LASSO Industry Shares
(1) (2) (3) (4) (5)
CBSA CBSA CBSA State State
Retail Retail Nielsen Goods Goods
01-06 06-11 06-11 01-06 06-11
House Prices 0.0526 0.291* 0.542 0.0790 0.152
(0.107) (0.144) (0.511) (0.0734) (0.101)
LASSO Ctrl Yes Yes Yes Yes Yes
R2 0.429 0.161 0.0744 0.766 0.678
N 261 261 261 48 48
Sources: NIPA regional accounts, Saiz (2010), FHFA, CBP, CBP, US Census Bureau.
LASSO-Chosen controls are chosen from industry shares and demographics using doubly-robust
post-LASSO as described in the text.
* p < 0.05, ** p < 0.01, *** p < 0.001
131
132
Chapter 3
The Geography Channel of House
Price Appreciation
With Gregory Howard
This chapter, written with Gregory Howard, develops a theory whereby increased demand
for living in housing-supply-inelastic regions raises aggregate house prices. We show that
this channel contributed significantly to the U.S. house price boom from 2000 to 2006. As an
example of our framework, we show that a decline in manufacturing, an industry concentrated
in elastic areas, raises national house prices. Our framework also predicts that changes in the
price-rent ratio, from interest rates or other changes in the mortgage market, increase relative
locational demand for high-rent areas, which are typically inelastic. Changes in locational
demand therefore fill in a missing link between changes in aggregate credit conditions and
aggregate house prices. We show evidence of this in the data.
3.1 Introduction
House prices rose significantly in the early 2000s. The boom was spatially heterogeneous,
with some areas seeing house prices more than double, and some areas seeing almost no
increase. This paper provides a new, fundamentals-based explanation for the housing boom:
inelastic-housing-supply regions became relatively more attractive places to live. We show
theoretically how changes in relative regional demand cause changes in the aggregate price,
and estimate that this force explains 30 percent of the increase in aggregate house prices
133
from 2000 to 2006.
We focus on two specific reasons that locations with inelastic housing supply became
relatively desirable places to live. One such force is the decline in manufacturing, an industry
concentrated in elastic areas (Liebersohn, 2017). Another is the increase in the price-rent
ratio,1 through interest rates or other changes in credit markets. This causes ex ante more
expensive areas, which are also inelastic, to become attractive relative to cheaper areas, a
prediction we find support for in the data. As demand increased for inelastic areas, house
prices rose nationally in equilibrium.
The reason this change increases aggregate house prices is simple: if someone moves from
a high-elasticity place to a low-elasticity place, the effect on house prices is large and positive
in the low-elasticity place, but small and negative in the high-elasticity place. So on average,
house prices go up.2 We generalize this intuition, and give a relationship between the cross-
sectional and the national house price changes based on the covariance of local house price
changes with the local housing supply elasticity.
Figure 3-5 illustrates the cross-sectional forces we highlight in this paper. Around 2000,
there was a marked decline in manufacturing (Charles, Hurst and Notowidigdo, 2016; Autor,
Dorn and Hanson, 2013). As would be expected in most urban models, 3 this created a large
gap in house prices between high-manufacturing areas, such as the Midwest, and the rest of
the country. Because the Midwest has a relatively elastic housing supply, higher population
growth on the coasts compared to the Midwest led to a higher aggregate equilibrium price
level.
'In our paper, the relevant ratio is between construction cost and user cost of housing, but whether the
house is owned or rented is not essential to our framework.
2 In fact, populations increased almost everywhere during the time period we study, so the mechanism
occurs through changes in the relative growth rates of different regions. Interestingly, before the housing
boom, net migration was strongly toward elastic areas of the country, but populations were closer to constant
because more births and fewer deaths occur in inelastic areas. It was a sharp drop in net migration towards
elastic areas that led inelastic areas to gain relatively in population. We break down the components of
population change in more detail in Appendix 3.11.
3Models in the tradition of Rosen (1979) and Roback (1982) imply that differences in house prices reflect
differences in wages across regions, and manufacturing decline is widely thought to be one of the main drivers
of differential wage changes during the time period we study.
134
While the example of manufacturing explains the forces of the geography channel well, it
plays a smaller quantitative role than a national change in the price-rent ratio. As interest
rates fall, or any other national shock that changes the ratio of the user-cost of housing to the
construction cost of housing, expensive places to build housing will become relatively more
affordable. Hence, there is an increase in relative demand for initially high-rent/high-price
areas.4 If, ex ante, rents and elasticity are negatively correlated, this will lead to an increase
in aggregate prices through the geography channel.
This paper makes several contributions. First, we formalize a theory of why a shift in
demand from high-elasticity to low-elasticity areas would increase national house prices. We
show that a negative covariance between housing supply elasticity and the change in local
house prices leads to aggregate house price increases. Using formulas we derive from this
model, we show how to quantify the geography channel of house price appreciation for the
decline in manufacturing or an increase in the price-rent ratio.
Our second contribution is to establish several empirical facts which support the key
ingredients of our model. We argue that changing demand for living in different regions
explains many of the cross-sectional patterns of housing. Supporting this, Figure 3-6 shows
the relationship between population growth and housing unit growth from 2000 to 2006. The
two variables are almost perfectly correlated: Population changes nearly one-for-one with
housing units. Moreover, the R2 is this relationship is 0.91-after accounting for population
growth, very little of housing unit growth remains unexplained.
Further support comes from the fact that that places with lower initial manufacturing
shares and higher initial costs of living experienced larger increases in housing quantities
and prices. In contrast, there was no relationship between these variables and the amount
of housing per capita, implying that population changes were the main force for cross-
sectional housing demand. To provide further evidence that the cross-sectional differences
4 In our model, agents do not consume a larger quantity of housing, shutting down a channel which other
papers have highlighted. The only choice agents have in the housing market is their choice of location. We
provide empirical evidence to support this assumption.
135
are primarily due to changes in locational preferences, we show in a new dataset that the
cross-sectional changes in rents look quite similar.
Third, we quantify the importance of the geography channel for national house prices
using new sources of data combined with simple formulas derived from theory. We con-
struct a new housing supply elasticity measure for commuting zones (CZs) and show this is
strongly negatively correlated to house price increases. Using the formula from the theory
we developed, we estimate the geography channel increased house prices by 0.089 log-points,
almost 30 percent of the total boom in real terms. Other measures of elasticity do not have
the national coverage that this measure provides, which is essential to consider the aggregate
effect that comes through changing relative demand across all regions (and in the model,
this requires applying a national market clearing condition). We show that the correlation
with manufacturing shares from 2000 can explain about a sixth of the geography channel,
but that the price-rent ratio change explains significantly more.
Finally, we show that our theory predicts a housing boom during the time when the
boom actually occurred.
Economists have largely focused on two theories to explain the housing boom: an incre-
ase in credit supply 5 or a shift in expectations of future house prices.' Compared to this
literature, we develop a theory of housing supply that we can use to understand the cross-
sectional and aggregate implications of these theories. Because the enormous increase in
prices did not lead to a huge increase in the quantity of houses, research has focused on the
changing qualities of housing. For example, Kaplan et al. (2017) and Garriga and Hedlund
(2017) both present quantitative models of the boom that allow people to choose between
renting and owning. We focus on people's choice of the location, which we find to be a key
5 For example, several papers have argued that the increase in subprime mortgages was a key cause of
the boom, e.g. Mian and Sufi (2009). Other papers have argued that falling interest rates are particularly
important such as Mayer and Sinai (2009), while others have emphasized changes to borrowing constraints,
such as Greenwald (2016).
6 For example, Glaeser and Nathanson (2017), DeFusco, Nathanson and Zwick (2017), and Foote, Gerardi
and Willen (2012). Kaplan, Mitman and Violante (2017) also suggest changing expectations play a large
role in the boom-bust cycle of house prices in a quantitative model. They also suggest a large role for credit
supply in explaining other phenomenon during the time period.
136
aspect to understanding the boom.7 This is consistent with our evidence that rents and
prices looked relatively similar in the cross-section. 8
There exists a literature predicated on the idea that certain regions of the country are
more sensitive to national or regional house price movements (e.g. Mian and Sufi, 2009;
Stroebel and Vavra, 2014; Palmer, 2015; Aladangady, 2017; Guren, McKay, Nakamura and
Steinsson, 2018). This paper provides a natural explanation for why that is the case, and why
inelastic regions appear to be more "sensitive." But it also highlights a potential concern:
the rise in national house prices may be caused by cross-sectional changes that are correlated
to "sensitivity." This could be a concern for the exclusion restriction when using a sensitivity
measure as an instrument.9
Also closely related is Charles et al. (2016), which establishes the parallel timing of
the manufacturing decline and the housing boom, showing they had offsetting employment
effects. To our knowledge, ours is the first paper to suggest this timing may not have been
a coincidence, but that the manufacturing decline had an effect on the housing boom. 10
Finally, there is a large overlap with papers that investigate the interaction between
migration and housing. Most similarly, Garriga, Hedlund, Tang and Wang (2017) argues
that rural-to-urban migration and land use restrictions led to a housing boom in China.
7Many other qualities of housing are inherently tied to its location. For example, houses in rural areas
typically have more acreage. And houses in the south are more likely to have a swimming pool. To map this
into our framework, we think of this as part of the amenity value of the location. In the short-run, qualities
such as the square footage or the acreage of a house are difficult to change.
8 We consider a change in the price-rent ratio as a shock in our model. But a model that takes housing
supply seriously has to answer the question of to what extent that changes house prices, and to what extent
it changes rents. For example, if the elasticity of every city in our model was the same, then such a shock
would not move house prices at all. Instead, rents would fall one-for-one with the increase in the ratio.
9 For example, suppose regions received random productivity shocks that increased the desirability to live
in that region. When, by luck, those productivity shocks are correlated to the housing supply elasticity,
national house prices will change, as summarized by Lemma 1. Therefore, those areas' house prices will,
on average, be increasing more when national house prices are increasing, appearing as if they were more
sensitive. But in this setup, the interaction of national house prices and local housing supply elasticity (or
sensitivity) will be correlated to the productivity shocks, and so would not make a good instrument for
the effect of house prices on consumption. This would be consistent with Davidoff (2016), which is titled
"Supply Constraints Are Not Valid Instrumental Variables for Home Prices Because They Are Correlated
With Many Demand Factors."
10Autor, Dorn and Hanson (2017) discuss the fact that the manufacturing decline in general, and the
China shock in particular, may have affected the cross section of house prices.
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In the U.S., Van Nieuwerburgh and Weill (2010) suggests that changing wages can explain
a significant share of house price dispersion from 1975-2005. Glaeser and Gyourko (2005)
suggests housing markets may explain sluggish population responses. Davis, Fisher and
Veracierto (2014) investigate this hypothesis and argue other migration frictions are more
important. These models have their bases in Rosen (1979) and Roback (1982), as does ours.
By closing the model, we add an aggregate market-clearing condition on housing from which
we can analyze the effects of relative location demand on aggregate house prices.
3.2 Theory: The Geography Channel
In this section, we lay out a model of the U.S. economy disaggregated to the commuting
zone level. The goal of this model is to illustrate why changes in locational preferences would
aggregate to a change in national house prices, and to provide sufficient statistics to estimate
how large such effects might be.
Denote a commuting zone by n E {1,... , N}. Time is discrete and denoted by t. For
notational convenience, the t is dropped for equations that hold within a single period.
There is a fixed total population, L, but it can move between locations. The population in
each location is denoted Ln. There are three sectors of production in each CZ: tradables,
non-tradables, and housing. The productivity of producing tradable goods in each region is
denoted by An.
3.2.1 Consumers
Consumers are identical, myopic, and able to move between locations. Conditional on a
location, each consumer provides labor inelastically and consumes tradables, non-tradables,
and housing. The key assumption in our model is that each consumer consumes a fixed
amount of housing, which we normalize to 1. Section 3.1 defends this assumption, arguing
that much of the cross-sectional variation in housing demand is indeed due to the number of
138
people, not housing per capita. Agents associate each CZ with an amenity value, a,. and
receive utility
U(V(c T, c'), a,,)
subject to
pP~NT  cCN~T  ++C Tc i w.-r h=w -r
where rh  is the rental price of housing, and we normalize the price of tradable goods to 1.
Because consumers are mobile, U is equalized across space.
Their indirect utility from consumption can be represented as
V=v n -rhP(pNIT)
where P is the price index for u.
Land-owners
There are local immobile landowners that own all the land in the city. In each period, they
sell the land to the housing investors; work; and consume tradables, non-tradables, and
housing. Denote their variables the same way as the consumers, but with a superscript Z.
Investors
Investors consume tradables, are risk-neutral and have discount rate .. They can build
housing anywhere in the country, and then rent out that housing. Denote their consumption
as ci.
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3.2.2 Technology
There are three types of production. Non-tradables are produced linearly with the same
productivity across space, which we normalize to 1.
YN T L N~T
Tradables are produced linearly with productivity An.
y = A LT
Housing is a durable good that depreciates at rate 6. It is produced locally with land, labor,
tradable goods.
= (1 - 6)H,,t_ 1 + H(Zn, A Li', XT t)
where H is constant returns to scale. Importantly, we assume that the productivity term
augments labor in the housing market as well. Because of this assumption, there are no
Balassa-Samuelson effects on the price of housinig. Alternatively, we could have assumed
that the construction labor market was segmented from the rest of the labor market, or that
construction labor is more mobile across commuting zones than other labor.11
3.2.3 Market Clearing
Each period, the non-tradable, housing, and labor markets must clear in each CZ.
Lnc NT + LcNT,Z _ NT
L + LZ = Hn
Lc + L = L pT + L n+ L 
"Garin (2017) presents some evidence of construction workers commuting across commuting zones.
140
The tradable market and the number of people clear nationally:
=c ZLnc + LZc TZ +
n n
SLn +L= L
n
3.2.4 Prices
We normalized the price of tradables to 1. Hence, the wage is An and the price of non-
tradables is also An.
The price of housing can be represented
P, = ph(Hn't - (1 - 6)H.,_1 , ZH)
So in steady-state, p = ph(6H, Zn). Define the short-run elasticity of housing supply CT- to
be
1 h
0n (Op"h(H, Zn)) pn
OHn Hn
Note this means that the long-run housing supply elasticity is y which is bigger and pro-
portional to c-n.
The relationship between house prices and rents is given by the investor's indifference
condition:
p1 =2  +E [p ]n 1 +r n
Define R = 1 r . In steady-state, rh = Rph, so R is the price-rent ratio. Note that this
assumption implies that house prices and rents will comove cross-sectionally, a fact we do-
cument in the Section 3.2. We abstract away from local differences in the price-to-rent
ratio.
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3.2.5 Aggregate house prices
In this section, we want to consider the effects of a small shock to A, or R. Throughout
this section, we will consider comparative statics, i.e. a change in steady-states. But given
the structure of the model, these comparative statics also encompass the dynamics in house
prices.1 2 We then theoretically investigate the way manufacturing decline and interest rate
changes affect aggregate house prices as an example of the geography channel's mechanism.
Lemma 1. The change in the initial-population-weighteda ggregate house price index is given
by
d log p h =- Cov(d log p , uM)
where the covariance is initial-population-weighted.
This equation illustrates that if prices in inelastic places rise compared to prices in elastic
places, prices must rise on average. The equation is simply a rearrangement of the housing
market-clearing condition and the definition of elasticity. The only assumptions it uses are
that each agent consumes one unit of housing, and that housing markets clear.
To set intuition, imagine a shift in population from a high-elasticity place to a low-
elasticity place. In the high-elasticity place, there are fewer housing units needed, so prices
go down, but not by much. In the low-elasticity place, there are more units needed, and
prices rise by a lot. Prices rise by more in the low-elasticity area because it is relatively
inelastic, and so, on average, they rise overall.
In later sections, we estimate this covariance and suggest that it is indicative of the
magnitude of the geography channel. To the extent that differences in house prices reflect
different locational preferences, this will be valid. However, to estimate the contributions of
specific locational shocks, we need to exploit more of the structure of the model.
Specifically, consider local house prices changes in equilibrium. We can implicitly diffe-
12 In Section 3.3 we show that the cross-sectional variation in house prices with respect to manufacturing
or rents has been persistent over time, suggesting this approach might not be too unrealistic.
142
rentiate the indirect utility function to see how utility and productivity affect house prices.
d log r = dU + ) d log w,
n rh dV rh rh P(Wn)
While this looks messy, it reduces nicely in special cases. If all goods are tradable, so P 1,
and if U = V + ce, then
h_ 1 Wf
dlog r = dU + -d logwn
n rn
which is the familiar equation from a typical Rosen-Roback model.
The role of manufacturing
Given Lemma 1, the natural thing to do when calculating the role of manufacturing might
be to regress the change in log house prices on manufacturing, and correlate the elasticities
with the projected values. Under certain assumptions in our model, that would be correct.
If we assume U = - log(1 - V) + a and that all consumption is of non-tradable goods, then
we get that d log rh = dU + d log wn. Hence the proportional change in house prices is driven
by the proportional change in wages, or in this simple model, productivity.
Proposition 1. Under the above assumptions, the change in national house prices when A
changes is given by
dlogph Cov(d log An, 0-,)
This result comes because dU is the same in all places. While these assumptions are
important for the algebraic simplicity of this result, other assumptions on the utility function
will give similar intuition: that relative wage decreases in elastic areas will raise average house
prices.
This result means that if areas that are comparatively elastic experience declines in
productivity, national house prices will rise as a result. In particular, we know from previous
work that elasticity and manufacturing share are positively correlated. During the 2000s,
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the manufacturing industry declined (Charles et al., 2016; Autor et al., 2013), so this will
cause an increase in the average national house price.
If we assume that d log A, = #manufacturing share, + E, where E, is i.i.d., then
gh Cov(manufacturing share,, o-)d log p,= -#
In practice, because they are the same in the model, we will regress cross-sectional house
prices on manufacturing share, and use that / to estimate manufacturing's contribution to
the housing boom.
Of course, the assumption on the utility function to get this exact result is unusual.
However, even under more general assumptions, we expect changes in cross-sectional pro-
ductivity to have an effect on cross-sectional house prices. Because of Lemma 1, this will
change aggregate house prices. Quantitatively, manufacturing will play a smaller role than
the price-rent ratio, so we would rather maintain our assumption to make clear the intuition
of our model rather than worry about the precise estimate.
The geography of the price-rent ratio
Because house prices are equal to the cost of production, and the quantity of housing demand
is inelastic, it is not clear that this model would predict an increase in house prices if R
decreased. But in fact, the geography channel provides a mechanism whereby this does
occur.
To see this, consider the case in which consumption is tradable and utility is additive.
Assume A is constant, so
1
dlogp h = -dlog R + dlogr h = -dlog R + 1 dV
rn
Cov(- ,u-)
Lemma 1 implies that d log ph = - dV whereas, by taking the average, we see
d log ph = -d log R + E [-L] dv. The theorem below is an algebraic manipulation of these
144
two equations.
Proposition 2. In the setup with tradable goods and additive utility, the response of aggregate
house prices to a change in the national price-rent ratio is given by:
COV(rh, n)dlo
dlogph = - d log R
This theorem has an additional ingredient besides Lemma 1. Here, the price-to-rent ratio
has an effect on the location choices of consumers. This is a natural consequence of a model
with unit housing demand because a percentage change in rents will matter more in areas
where rents were initially high. In more expensive areas, the same percentage change leads
to a greater dollar change in the user cost of housing, which is what agents care about.
In addition, we present evidence in the next section that both population and house prices
reacted in the ways you might expect from this model.
So a change in the house price-rent ratio can have aggregate consequences in this model
because the utility of consumers changes. The effect of this utility change on different cities
will be based on ex ante rents. If those rents are correlated with elasticity, aggregate house
prices will change. Specifically, if rents are higher in inelastic areas, as is the case in the
data, then a decrease in the interest rate will raise national average house prices.
3.3 The Cross-Section of Local Housing Demand
This section presents evidence of a key component of our model: that cross-sectional changes
in housing demand explain a substantial part of the cross-sectional changes in house prices
from 2000-2006. Our first piece of evidence is that the initial size of the manufacturing
sector and the initial rent level of a commuting zone explain population and house price
changes. Second, Section 3.3.2 presents evidence that areas with rising house prices also
had rising rents. This finding provides further evidence that cross-sectional house price
145
changes reflected changes in relative locational demand; the patterns we document are not
an anomalous feature of the home-ownership market, but exist in the rental market as well.
To show this, we create a new index of multifamily operating incomes using data from
Commercial Mortgage-Backed Security (CMBS) records which we argue is closely linked
to rents. Section 3.3.3 presents evidence that the shifts in housing demand we highlight
continued to affect relative house prices even after the end of the housing bust, indicating
that these changes are not due to a transient factor linked exclusively to the boom-and-bust
period.
3.3.1 Population Growth and House Prices
This subsection presents evidence supporting a key assumption of the model - that cross-
sectional variation in house prices was caused by demand to live in particular areas. Figure
3-6 showed that there was a nearly one-for-one relationship between housing units and popu-
lation growth, indicating a close relationship between population movement and changes to
the housing markets. To provide further evidence, we also show that and low-manufacturing
areas and high-initial-rent areas had the greatest population and price increases. Throug-
hout this section, we will treat the initial manufacturing share and rent level as exogenous,
but in Appendix 3.10, we address the question of causality.
First, we provide evidence that exposure to the manufacturing sector affected populati-
ons and prices in the way one would expect from a regional demand shock. The relationship
between manufacturing and population is shown in left half of Figure 3-1. From 2000-2006
there was an overall net migration from areas with high to areas with low manufacturing.
On average, a 10 percent higher fraction of the population employed in manufacturing cor-
responded to lower population growth of 0.007 log-points. A similar pattern holds for price
changes, shown in the right half of Figure 3-1. Low-manufacturing areas had greater price
increases as well.
Changing labor demand may cause population changes for a variety of reasons, including
146
changes to domestic migration, international migration, birth, and death. Appendix 3.11
decomposes population changes and shows that domestic migration is by far the largest
driver of the features we see in the data.
Similarly, we see data consistent with an increase in demand for places with higher initial
rents, as our model predicts. Data for rents comes from the 2000 ACS, and we use the
median rent by commuting zone.1 3 As can be seen in Figure 3-2, places with higher initial
rents experienced larger increases in population and larger increases in house prices.
Along these two dimensions (manufacturing and initial rents), the increase in cross-
sectional housing demand is driven by population changes, not changes in per capita housing.
This can be seen in Figure 3-3. The y-axis scales on these graphs were adjusted to be
comparable to the graphs that showed the change in population. There is no statistically or
economically significant relationship between the increase in housing per capita and either the
manufacturing share or the median rent. This null result is important because it emphasizes
that population changes are a major driver of housing demand during this time period. It
consistent with our assumption of unit housing demand regardless of location. 14
3.3.2 Rents and Prices
Because regional demand for housing is the model's key mechanism, the cross-sectional
predictions for house prices hold for rental prices as well. Here we present new evidence that
rents and house prices co-moved cross-sectionally. If cross-sectional patterns of house prices
in the early 2000s were explained exclusively by anomalous features of the housing market
1 3The public ACS data classifies geographies at the PUMA level, which we convert to commuting zones
using the Missouri Census Data Center MABLE/Geocorr web application. This could lead to some mis-
measurement, but we expect that to be small, as housing costs are typically thought to be fairly smooth
geographically.
"Along these lines, we have also investigated whether housing demand changes would have been caused
by differential changes in the size of housing. Using data from the Census of Construction, we see no cross-
sectional relationship between house price increases and the change in average square footage or lot size.
Unfortunately, for these measures, our geographic scope is more limited, and we can only do the analysis at
the Census Division level (n = 9). This result is consistent with the finding by Albouy and Zabek (2016):
most of the increase in housing values is due to changes in land values, not to major changes in the dispersion
of the size or amenities of houses.
147
during this time (such as geographically concentrated increases in sub-prime lending), then
one would not expect to find such a strong comovement of rents and prices.
To study the relationship between rents and house prices, we construct a new regional
index of multifamily net operating incomes using data from Commercial Mortgage Backed
Securities. Net operating income is very closely related to property rents, as it measures the
difference between effective rental income and operating expenses from the perspective of
landlords. We believe that our index has several advantages over other widely-used measures,
such as the rent index provided by the BLS. Other series that have been used as proxies for
rents, such as fair market rents, attempt to measure something different.
The source of our data is records of commercial mortgage-backed securities (CMBS)
collected and provided by the firm Trepp. These data are used to price and track CMBS
and have near-universal coverage of the CMBS market. Although CMBS have existed since
the mid 1980s, they represented an insubstantial portion of the commercial mortgage market
until the late 1990s. Black, Krainer and Nichols (2017) show that, as of 2017, 20 and 25
percent of all commercial mortgages are securitized, with a larger portion among Class A
in the largest urban property markets. This may make the sample less representative of the
entire rental market but may make it better for measuring the fundamental value of living in
a city. Distortions in the rental market, such as rent control and insurance motives between
renters and landlords, may mean that rents are not reflective of the fundamental value. A
sample that skews towards more recently-built and high-occupancy buildings may be less
subject to such biases.
The data sample is constructed as follows. We include only multifamily properties with
mortgages originated in 1999 or later. We drop mortgages that are for more than one
property or which appear as part of more than one security. For each property, we calculate
average values of property's net operating income and occupancy rate by year. Operating
incomes are deflated by the urban CPI. Property location information and construction year
come from origination information. We calculate the property age from its construction year.
148
Summary statistics are shown in Table 3.1.
There are three main advantages to using CMBS data as compared to BLS rents data.
First, because it comes from an administrative data source, the CMBS data does not suffer
from biases associated with the surveying process, as Crone, Nakamura and Voith (2010)
document for the CPI rents series. Second, the CMBS data have broader geographic coverage
than the BLS provides. Third, we believe net operating income of newer buildings is more
likely to reflect the desirability of living in a specific location.
To create the index, we estimate annual changes in property-level net operating incomes
using the following specification:
log(Incomeit) = #3 + -yi + 6 log(Occupancyit) + cit
where the year fixed-effects 3t constitute the index and -yi is a property-level fixed effect.
This "repeat incomes" index is akin to a repeat-sales house price index. We estimate this
specification separately for each CZ. Our choice of how to include occupancy does not matter
much, omitting it (6 = 0) or calculating the index for income per occupant (6 = 1) does not
change the results.1 5
As the NOI estimates control for both property and year fixed effects, it is not possible
to control for property quality which changes as buildings age. Gordon and Van Goethem
(2004) study the effects of changing quality in the BLS rents series and estimate a substantial
downward bias as compared to a hedonic index. Therefore the within-property estimates we
develop are suited only for understanding cross-sectional differences in NOI growth rather
than changes in average NOI growth over this time.1 6
"Likewise, the index does not change significantly when weighting by the inverse time between observa-
tions or when using FGLS to estimate optimal weights as a linear or quadratic function of time between
observations. This is likely because the vast majority of properties provide new data every year, so weighting
schemes are not as important as they are for repeat-sales indices.
1 6 The average estimated NOI growth from 2000-2005 is only 2 percent in the repeat incomes index, but
this estimate is downward-biased because building quality declines as buildings age. As long as one focuses
on cross-sectional differences in log NOI, this bias is not important under the assumption that property
depreciation, and hence bias, is the same across regions. (This is also a well-known issue for housing price
indexes.) In a simple hedonic model, we estimate a substantial increase in national NOI over the period
149
Figure 3-4 shows the relationship between price growth and net operating income growth
from 2000-2006 using the repeat income index. The slope of the fit line is large and positive,
supporting the claim that positive fundamental shocks affected both prices and rents in the
same cities. The fact that the slope is less than one may reflect that house prices in some
markets "overshot," a common narrative in the boom and bust period, or that rents are
fairly sticky year-to-year. Looking at a longer time period from 2000 to 2015, the change in
rents or house prices gives the same coefficient when regressed on housing supply elasticity.
The relationship between rents and house prices demonstrates that CZs with rising prices
really did become more desirable to live in. This finding is important for distinguishing our
model from models instead emphasizing changes to the possibility or desirability of home-
ownership that vary by region. If housing price changes were driven solely by people choosing
to own rather than rent, we would not expect such a relationship.
3.3.3 The Persistence of Shifts in Demand
As a final piece of evidence that cross-sectional house price changes reflect differential de-
mands for location, we show that the relationship between house prices and manufacturing
has lasted for many years after the crisis. This is expected: neither the decline in manufac-
turing nor interest rates have rebounded significantly, although credit conditions did move
around a fair amount.
In Figure 3-7, we show the event study of manufacturing and rent's effect on house
price changes since 2000. Specifically, we estimate the following regression, weighted by
population:
log(p'.1) - log(Pn,2000 ) = /tmn,2000 + '7t + En,t
we study, with the largest NOI increase 1999-2003 when prices increased by 0.11 log-points in total. In the
hedonic model, the vector of controls includes dummy variables for property age, the log(occupancy), and
log(property square feet). To ensure that the estimates are not biased towards the cities where securitization
is most popular, we weight the estimates by the inverse number of CMBS observations available, keeping
only those cities and years where data from at least 30 properties are available. The estimates do not change
significantly when interacting these control variables or using higher-order terms.
150
where ph is the house price index and m is the manufacturing share of region n. The left
side of the figure plots the #t's. Similarly, the right-side of the figure shows the results for a
similar regression, replacing manufacturing share with median rent. Within each figure, we
also show the same regressions using our measure of NOI.
The main takeaway is that the change in house prices with respect to these two vari-
ables, especially manufacturing, has persisted over a long time. In fact, the relationship
between manufacturing and the house price change from 2000-2015 is about as strong as
the relationship between manufacturing and the house price change from 2000-2006. For
manufacturing this strong relationship never really went away, suggesting that this reflected
a change in the desirability to live in those areas, not some factor specific to the housing
boom itself. For initial rents, the relationship did become indistinguishable from zero over
the years 2000-2011, but the effect has rebounded since then. Importantly, the effect on
NOI is comparable to the effect on house prices. Our argument that low-manufacturing and
initially expensive regions became attractive places to live is reflected in both house prices
and rents.17
3.4 The Magnitude of the Geography Channel
In this section, we put numbers on the expressions derived from our model, arguing that the
geography channel is large. First, we create a measure of elasticity that covers the entire
country. We then use that measure of elasticity to compute the values of those expressions.
1 7The change in house prices is larger than the change in rents from 2000 to 2006. This could be for several
reasons: one possibility is that rents are sticky, and would move more but for pricing frictions. Another
is that expectations of future rents did not match the realization of those rents. In fact, the migration of
people towards low-manufacturing and high-rent areas was strong during the boom, and slowed down or
reversed in the bust. Figures showing this can be seen in Appendix 3.11. This is entirely consistent with
"speculators" that moved in response to the initial shock. Lemma 1 is consistent with this possibility, and
our model would not require much of a tweak to incorporate such forces as well.
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3.4.1 Constructing a measure of elasticity
In order to estimate the covariance between an economic shock affecting wages and the
elasticity of housing supply, we must first have an estimate of housing supply elasticity.
Existing measures of this elasticity are inadequate for our needs because they do not provide
comprehensive coverage of the entire United States, mostly focusing exclusively on MSAs
(e.g. Saiz, 2010). This is especially crucial because while the Saiz measures cover much of the
population, it systematically undercovers areas that are high in manufacturing concentration.
In this section, we construct a measure for commuting zones, providing full coverage for the
United States.
We construct elasticities similar to the methodology of Saiz (2010) by directly estimating
the effect of a change in housing units on house prices, projecting this relationship onto
three measures associated with land availability: land use regulations, population density,
and coastal areas.
Specifically, we estimate the following model for the years 1980-2000, using decadal data
on housing units from the Census and house prices from the Federal Housing Finance Agency.
A log Ph= e=o+31WRLURIi+02WRLURI missing +#3 log pop density +8 4 coastali A log Hi,t + o't + ci,t (3.1)
where WRLURI is the Wharton Residential Land Use Regulatory Index, pop density is
the population of a CZ divided by- the total square miles in it, and coastal is a dummy
variable for having a county defined as coastal by the National Oceanic and Atmospheric
Administration.18 We use an exponential function to guarantee our elasticities are positive.
The year fixed effect is meant to capture national changes in the cost of construction and
inflation.
In our baseline specification, we estimate the model using GMM, imposing that each of
18The WRLURI is calculated for places. We took a population-weighted average for all places within a
CZ. For CZs in which WRLURI is not available, we coded it as zero, and coded "WRLURI missing" as 1, so
that these (primarily rural) areas would still have an elasticity calculated. To classify coastal CZs, we used
NOAA's definition of coastal counties. Any CZ that contained a coastal county was coded as coastal.
152
the four variables in the exponential, A log Hi,,, and year dummies are orthogonal to the
error term. The results are show in Column (3) of Table 3.2. If some areas of the country
had more extensions to their houses installed, this would violate this assumption because
that would be an omitted variable that drove up house prices and drove down housing units,
as more people could live in each house. Another example that would violate this assumption
is Hurricane Katrina, which destroyed a lot of the housing stock and directly affected the
desirability of living in New Orleans. However, we think that these examples are rare, and
do not introduce much bias in our regression, so we adopt this as our baseline.
Nonetheless, because of these concerns, we run two robustness checks, swapping out the
moment condition that E[A log Hj,tcj,t] = 0 for instruments. In column (1), we use a shift-
share instrument, similar to Bartik (1991), based on two-digit SIC codes. In column (2), we
simply use differences in log population. The second column should ease concerns such as
changing housing types, and the first column covers a broader range of endogeneity concerns,
such as events like Hurricane Katrina. In addition, we also estimate the model using non-
linear least squares, a method which amounts to placing different weights on variables in our
moment conditions (column 4).
The estimated coefficients are intuitive, as seen in column 3. Areas with more land
regulation, higher population density, and coastal areas have house prices that move more
when population changes. The negative point-estimate of 32 also makes sense: it implies
areas with no measured land-use regulatory index are similar to those with an index of about
-0.99, which is the 10th percentile of the WRLURI distribution.
The results are quite similar using non-linear least squares or using population growth
for the moment condition. For the estimation using the Bartik instruments, however, the
results are much larger and noisier. Nonetheless they maintain the same signs for each of
the coefficients. Interestingly, the model using Bartik instruments converges to where areas
with no measure of WRLURI are perfectly elastic.1 9 This is not unreasonable given that
19 0r are e433 5 times more elastic, anyway. This is the result of numerical approximation in the Stata gmm
algorithm. Imposing a coefficient of -oo and re-running the regression gave the same estimates for the other
153
these are almost entirely rural commuting zones.
To transform our estimates into elasticities, we construct each CZ's elasticity using the
following formula and our preferred estimates from column (3):
o-i = exp(-#o - # 1WRLURIJ - 2WRLURI missingi - #3 log pop densityi - #4coastalj)
The average elasticity we estimate is 2.93, in line with previous estimates. A map of the
elasticities we estimate are presented on the left of Figure 3-8.
Our measure is highly correlated with the estimates in Saiz (2010), at least for the
geographic areas that he covers. On the right in Figure 3-8, we present the comparison of
estimated elasticities, for the areas of the country on which they overlap. Each dot represents
a set of counties in the infimum of the MSA and CZ partitions, the largest partition that
refines both. The population-weighted correlation between the two measures is 0.62.
3.4.2 The Geography Channel
We wish to see how much the geography channel contributed to the increase in house prices
between 2000 and 2006. During this time period, real house prices increased 0.32 log-points. 20
Now that we have estimated elasticities for each CZ in the country, we can plug these values
into the previous formulas.
We use county-level house price data from the FHFA. In order to construct an index for
each CZ, we take the population-weighted average increase by county. If a county does not
have house price data, we do not include it in our averages. We look at total log-change
between 2000 and 2006. In total, we have house price indices for 648 CZs, covering 99.8
percent of the total population. 21
The geography channel of house price appreciation, as calculated using Lemma 1, is
coefficients.
20We took the national FHFA data, and deflated by the CPI.
21 In comparison, MSAs cover about 80 percent of the population.
154
Cov(rd& og ) which explains an aggregate increase of 0.089 log-points, about 28 percent of
the total increase in house prices. The interpretation of this number is that if there were
local changes that caused the house price dispersion we saw in the data, then we would
expect national house prices to rise about 9 percent in our model.
To check the robustness of our results, we also use the Saiz (2010) elasticities instead of
the ones created in Section 3.4.1. For this to be correct, the assumption would have to be
that no one was able to move in or out of the MSAs covered by this measure. Nonetheless,
because this measure of elasticity existed and was popular before our paper, it serves as
a reasonable check that these results are not due to the choices we made in constructing
our measure. The Saiz elasticities suggest an increase of 0.072 log-points, in line with our
number. Intuitively, it makes sense that our number is slightly larger because using Saiz's
elasticities fails to capture any movement from non-metropolitan areas into MSAs.
The Role of Manufacturing
The decline of manufacturing played a large role in explaining this variation in house prices.
Regressing the change in house prices on the manufacturing share gives an estimate of -
1.29, with a confidence interval of [-1.45, -1.10].22 A one standard-deviation increase in
manufacturing share, about 12.3 percentage points, lowered local house prices by 0.158 log-
points.
The relationship between manufacturing and elasticity is shown in Figure 3-9. As can be
seen, there is a strong relationship between the two. The covariance of manufacturing and
elasticity divided by the average elasticity is 0.011, which means that manufacturing alone
increased the national house price index by .014 log-points. This is about 16 percent of the
total geography channel contribution.
To put this number in context, it might be helpful to consider a naive back-of-the-
22The regression is population-weighted and uses robust standard errors. Manufacturing is from County
Business Patterns and is measured as of 1990; using 2000 manufacturing yields estimates that are slightly
larger in magnitude. Using QCEW data to measure manufacturing yields estimates that are smaller.
155
envelope calculation based on the same regression of house price changes on manufacturing
share." To calculate the national effect, such a methodology might multiply the local effect
by the national manufacturing share, leading a naive reader to think that manufacturing
actually lowered national house prices by 0.26 log-points. In contrast, our simple model,
which takes into account general equilibrium, gives a very different answer and requires only
one additional statistic.
The Geography of Increasing Price-Rent Ratios
As outlined in the theory, changes in the price-rent ratio can have effects on patterns of
mobility and aggregate house prices, even when agents have unit housing demand. In this
section, we quantify how large these effects are on the aggregate. First, we need an estimate
of the increase in price-rent ratios. As a proxy, we use the decline in 30-year mortgage rates
from Freddie Mac, which declined about 0.32 log-points over this time period. Hence, we
will do some calculations for an increase in the price-rent ratio of 0.32 log-points.24
The relationship between inverse rents and elasticity is shown in Figure 3-10. Not surpri-
singly, rents are higher in inelastic areas. The term multiplying the change in the price-rent
ratio evaluates to -0.13, meaning that a decline in interest rates will cause an increase in
house prices as higher-priced areas become more affordable. Using our preferred measure of
R, the total effect on national house prices from Proposition 2 is .038 log-points. This is
more than 40 percent of the total geography channel.
This number may be an underestimate of the contribution of the geography of price-rent
ratios. Our model also makes a prediction on the cross-sectional house price changes that
should occur in response to an interest rate change. 2  But the cross-sectional house price
changes are actually much larger, implying we might understate the magnitude in. This
23We should make it very clear that we do not endorse this methodology, and are simply including this
exercise as a warning to not use it.
24This is a smaller increase in price-to-rent ratios than one might get from other data sources. For example,
Greenwald (2016) tries to match data that shows an increase of about 60 percent.
25Namely, a regression of the change in house prices on initial rents should have a coefficient of
156
could be for a variety of reasons. One possibility is that 0.32 log points underestimates the
total increase in the price-rent ratio.2" Second, if the gains to living in a location accrue
primarily in the future, as in Bilal and Rossi-Hansberg (2018), then lower interest rates may
encourage people to "invest" in certain locations more.2 7 Third, it could also be that the
migration itself improves the labor markets or the amenities in the receiving city (Diamond,
2016; Gyourko, Mayer and Sinai, 2013; Howard, 2017).
A reduced form way to consider the cross-sectional regression would be an exercise similar
to estimating the effect of the manufacturing decline. We regress house price changes on
initial rents, and then use Lemma 1 to calculate a contribution. In this formulation, initial
rents are responsible for house prices rising 0.093 log-points, roughly the same size as the
entire geography channel. Based on this calculation, we would argue that the change in price-
to-rent ratio can explain roughly 30 percent of the total house price appreciation during this
time.
Declining Cities and External Validity
It has been hypothesized and shown in the data (Glaeser and Gyourko, 2005; Notowidigdo,
2011) that cities with declining populations have lower housing-supply elasticities. 28 The
time period of interest to us is a time where almost no CZs experienced a decline in housing
units (see Figure 3-6). In fact, by 2000 population, only 1.4 percent of the country lived in
a commuting zone with fewer housing units in it in 2006 than in 2000. This means that the
relative population flows that we document empirically cause changes in relative population
growth rates but not net declines in population. More than a third of those people lived in
26 For example, the availability of credit was changing at that time, which many papers, several of which
we mentioned in the introduction, have shown.
2 7For example, living in a certain city may increase human capital, raising future wages.
281In our own data, we have also included a term in our elasticity estimation for a dummy of having
declining housing units. The coefficient on that is 3.46 (with standard error 0.71), suggesting hugely more
inelastic housing supply in declining cities, a factor of 30. Effectively, areas with housing unit declines are
completely inelastic. Other coefficients did not change significantly. We strongly prefer the linear piece-
wise estimation that we are doing rather than a continuous specification as Notowidigdo (2011), because we
believe the economics more strongly justify concavity around 0, but we do not believe that extrapolating
that concavity to large house price changes is appropriate.
157
New Orleans, where the decline in housing .units was caused by Hurricane Katrina. Hence,
we do not expect this force to have much relevance in this time period.
However, it could easily matter in other time periods, where there is not population
growth or increases in national housing per capita. So it makes sense to consider what
would happen with the geography channel at other times. Here, the first-order variation in
elasticity is over whether a city is shrinking or not, swamping any effects of whether people
prefer to live in coastal areas, highly land-use-regulated areas, or population dense areas.
Proposition 3 (Declining Cities). If any city declining in housing becomes completely ine-
lastic and aggregate housing is not increasing, then any change in the relative desirability of
cities leads to a negative aggregate change in house prices.
Increases in population, fluctuations in houses per capita, and housing depreciation all
make this situation less likely. Nonetheless, this result provides a stark example of how the
geography channel can lead to house price declines instead of increases, even if the relative
desirability of coastal, highly-regulated, urban areas is increasing. The key difference between
our results and this proposition is that aggregate housing was increasing significantly during
this period, such that almost no cities were declining in their housing stock.
3.5 The Timing of the Housing Boom
Our theory makes predictions on the timing of the housing boom. Aggregate house prices
should increase most when the cross-sectional covariance between local house price changes
and elasticity is most negative. In this section, we show that this covariance was highly
correlated to the movements of national prices.
The point is illustrated in Figure 3-11. In this figure, we regress changes since 2000 of
various local variables on housing supply elasticity. Hence, the point of the orange line in the
year 2010 represents the population-weighted regression coefficient of the the change in log
house prices from 2000 to 2010 on housing supply elasticity. This regression is significantly
158
negative from 2000-2006, then becomes less negative during the bust, and is increasing again
during recent years.
Also pictured on the left side of Figure 3-11 are the cross-sectional relationships of rents
and population with elasticity. Interestingly, the movement of people seems to lead changes
in house prices. The biggest population shift toward inelastic areas occurs between the years
1996 and 2003. This may represent some sluggishness in house price changes. 29 We include
the rents data to show that it exhibits similar timing patterns, although unfortunately, our
data extends only back to 2000. The rents data also indicate an increasing desirability to
live in inelastic areas, though rents do appear to be more slow-moving.
These patterns are consistent with the timing that we saw for initial rent levels and
manufacturing, in Figure 3-7.
3.6 Conclusion
Much of the literature on the housing boom has focused on why the demand for the quantity
of housing or home-ownership increased, but little has focused on the relationship between
housing demand and the location of that housing. This paper demonstrates that considering
this geography can explain a significant fraction of the overall boom. Using intuitive statistics
derived from a formal model of regional housing demand, we show that the geography channel
can explain 30 percent of the aggregate increase in house prices from 2000-2006.
The result questions the appropriateness of testing theories using the cross-section of
housing without explicitly considering the role of mobility. In particular, housing demand
is regionally heterogeneous in the face of national shocks and regions are linked through
mobility. For these reasons, local housing markets cannot be viewed in isolation.
Our results have abstracted from several important facts, including the dynamics of the
boom. However, we believe that our findings are highly compatible with dynamic models
29 Interestingly, and in support of our theory, there was a similar movement of people towards inelastic
areas before the 1980 housing boom.
159
which show how changes to house prices may be magnified for institutional or behavioral
reasons. Our results on rents and house prices could be useful in calibrating a model of
expectations that could help explain the overshooting and subsequent housing bust.
160
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163
3.7 Figures
(0 90 0 0 Cl
.. 00
0 C
N N 0 Cl
.C
0 * 0
0
0
0C 0 0 0
0 0 at
0 
0)
0 . -0 0
0
-J
0
0 .1 .2 .3 .4 .5 . .2 r1 .3 .4 .5
Manufacturing Share, 2000 Manufacturing Share, 2000
Figure 3-1: Housing Demand and Manufacturing Share
164
0 0
0
b
CD 0 Q4 CD0
N N 0n 0
0 0 C- *
Cl
0) 0
0)
a a;0 I
0
a OC 0)0
0 0.
00
0) N0
-j
10 0
0
N
200 400 600 800 1doo 200 400 600 800 1000
Median Rent, 2000 Median Rent, 2000
Figure 3-2: Housing Demand and 2000 Rents
CD
CD 0
0
N
0
0
0
0)
C
M CV)a1
C -fiPe
C.) O 5Dc
D0~
10 0)
0) 0
Tj dtll
0
0
0)
0
-j
0 .1 .2 .3 .4 .5 200 400 660 86o 100
Manufacturing Share, 2000 Median Rent, 2000
Figure 3-3: Houses per capita and manufacturing, rents
165
Log house price growth vs log apt. income, 2000-2006
Slope=0.95 (0.18)
U,
0)
0 0
0)
0)
J0-
-.5 C .5
Change in Log Multifamily CRE NOI
Figure 3-4: Multifamily NOI and House Price Growth
FHFA House Price Index
Purchase-Only House Price Indices, 1990-2017
0
C.,.
LI)
E
0
X C)
C)
~~- I
1990m1 1995m1 2000m1 2005m1 2010m1 2015m1
Year
East North Central Census Division All-US
U.S. Federal Housing Finance Agency, retrieved from FRED, Federal Reserve Bank of St. Louis.
Figure 3-5: House Prices in the Midwest and the Rest of the U.S.
166
Log housing unit growth vs population growth, 2000-2006
Slope=0.97 (0.02)
a
0
C
CD
0
0)
0V--
C4 -
CI
-.2 6 .2 .4
Log population change
Figure 3-6: Population Growth and Housing Units
Manufacturing Share, 1990 Inverse Rents, 2000
5-
-------
C
C &C~I -
C.)
8~
1995 (5'2000 2005 2010 2015 1995 200 2005 2010 2015
--- House Prices -+-- Rents
--- House Prices -+- Rents
Figure 3-7: The Persistence of House Prices
167
0 -
o
0
o* .00.
0 .
o0~)80
0 6
M 6.07 - 50.48 0 5 10 15
l3.49- 6.07 Saiz (2010) Elasticity
0.57 - 1.77
N 0.68- 0.97 Estimated elasticity --- 45 degree line
.05 - .6
Figure 3-8: Map of Estimated Elasticities (bin cutoffs at the population-weighted 10th, 25th,
50th, 75th, and 90th percentiles) and Comparison of estimated elasticities with Saiz (2010)
0
08% 0 8 0 0
.0 (O 0*  00 0 ( 
0 00 *0 ~ 0 0 0 0
00 Q a 0 0 0 0000.. 0 0
p.o00  Boo 0f 0 8 0
o~ 0 9o a~ A 0 ( 6000 0 
CO- 430 080 (9 0000 0 c c o%0( CoO0 0 0.
0 
96 000 V0 OO p 0 1)
00 ~ o 0 ao Q 0 0
go 0 0 0
0~ ~ 0o?~
cm-  
C1-
6 .2 .4 .6
Manufacturing Share, 1990
0 elasticity - Fitted Values
Graph trimmed at 98th percentile of elasticity
Figure 3-9: Estimated Elasticity and Manufacturing Share by CZ
168
0~ 0 0 0r
0 00 89 "o "I
to 0 
0 
008 06 'go oo0 00d 8 o
0 . '0 0 000 08
.001 .0015 .002 .0025 .003 .0U35
Inverse Rent
o elasticity - Fitted Values
Graph trimmed at 98th percentile of elasticity
Figure 3-10: Inverse Rent versus Elasticity
Elasticity
C~J
-0
0
0
AV-J
0
0
C J
0
1995 2000 2005 2010 2015
- Population (left axis) -- +-- House Prices (right axis)
-- Rents (right axis)
Figure 3-11: Regression coefficients of house price, rent, and population growth since 2000
on elasticity
169
3.8 Tables
Table 3.1: Summary Statistics of CMBS Property Data
Standard 1 0 th goth
Mean Deviation Percentile Median Percentile
Net Operating Income ($1000s) 725.8 1,246 85.75 406.9 1,659
Occupancy (Percent) 94.59 66.45 87.58 95.21 100
Loan-to-Value (Percent) 69.29 20.99 46.67 72.70 79.80
Appraised Value ($1000s) 10,590 23,323 1,035 5,000 24,300
Units 155.0 230.9 20 108 320
Building Age (years) 36.91 25.97 11 32 76
170
Table 3.2: Estimates to construct elasticity
(1) (2) (3) (4)
GMM, Bartik GMM, Pop Growth GMM, Housing Growth NLLS
-9.385 -2.234** -3.409** -3.597***
(17.89) (0.817) (1.131) (0.946)
#1, WRLURI 0.979 0.198 0.362+ 0.253
(1.314) (0.150) (0.188) (0.189)
/32, WRLURI missing -4355.1 -0.199 -0.358 -0.0579
(.) (0.413) (0.762) (0.555)
,33, Log Pop Density 1.012 0.296* 0.446* 0.469**
(0.956) (0.149) (0.206) (0.161)
/4, Coastal 2.632 0.357+ 0.522+ 0.426+
(11.45) (0.199) (0.291) (0.229)
N 918 922 922 922
Standard errors in parentheses
+ p < 0.10, * p < 0.05, ** p < 0.01, *** p < .001
171
3.9 Proofs
3.9.1 Proof of Lemma 1
Agents demand one unit of housing, implies that the total amount of housing is fixed by the
population. Therefore,
Nid log H =0
By the definition of housing supply elasticity, d log Hi = o-id log pi, so
Nio-id logph = 0
The result is an algebraic rearrangement, solving for E> d log pZ. I
3.9.2 Proof of Proposition 1
Since dU is the same across space, Cov(dlogp, ) = Cov(d log An, o-) The rest is an
application of Lemma 1. ED
3.9.3 Proof of Proposition 2
Using the two equations above it in the text,
dlogph - -dlogR+E [,] d log ph - Cov( , -s)J
Simplifying, and using the fact that E[I] = E[c-n]E[L] + Cov(Un-, 1) gives the desired
reslt hh
result. F-I
172
3.9.4 Proof of Proposition 3
Suppose house prices anywhere increased. Then housing supply in that area increases, and
housing supply somewhere else must decrease, by the assumption on the aggregate. But
housing supply cannot decrease anywhere because it is completely inelastic in declining
areas. Therefore, house prices cannot increase anywhere. If there is a change in the relative
desirability, and house prices cannot increase in the relatively more desirable location, they
must fall in the relatively less desirable location. Therefore, on average, house prices fall. D
3.10 Causality
In this section, we argue that the cross-sectional correlations that we observe in the data are
causal.
Manufacturing. In the main body of the paper, we show that areas with a higher
manufacturing share had smaller increases in house prices and population. We believe this
link is causal: higher manufacturing led to worse employment outcomes during this time
period, leading people to move away. This belief is reflected in columns (1) and (3) of Table
3.3, where we use the manufacturing share as an instrument for log employment change, and
show that it led to higher house prices and population.
To confirm this causal interpretation, we show that the effects of the China Shock, de-
veloped by Autor et al. (2013), have similar effects and magnitudes. The China shock is a
constructed instrument that measures the import competition that certain commuting zones
faced from Chinese manufacturing. They argue that trade with China was one of the major
factors leading to the decline in manufacturing. See their paper for an argument as to why
their shock is orthogonal to other factors affecting local employment. Given that, their shock
should also be orthogonal to other causes of population and house price changes. The results
from using the China shock as an instrument are of similar magnitudes to simply using the
manufacturing share. This suggest that jobs lost from manufacturing did cause changes in
173
population and house prices that are of the magnitude we estimate in the main body of the
paper.
Table 3.3: Log Change, 2000-2006
(1) (2) (3) (4)
House Price House Price Population Population
Log Employment Change 3.016*** 1.858* 0.414*** 0.374***
(0.665) (0.825) (0.105) (0.0999)
Instrument Manuf Share China Shock Manuf Share China Shock
First-stage F 23.60 21.83 23.38 21.66
Observations 648 641 706 691
Standard errors in parentheses
* p < 0.05, ** p < 0.01, *** p < 0.001
Initial Rents. Another claim that we make in the main body of the paper is that as
credit conditions changed, areas with higher initial rents had larger increases in house prices.
In Table 3.4, columns (1) and (3) are the regression coefficients from figures we show in the
main body. However, it may be that inverse rents and house prices are correlated for more
mechanical reasons than the story we present. For example, if rents started to change before
the year 2000 and changes in rents are persistent, then that persistence could be causing a
bias in the regression. Or rents might rise because of anticipated future house price increases,
resulting in a bias from reverse causality.
To address this concern, we instrument inverse rents with a measure of natural amenities
from the U.S. Department of Agriculture. This measure is based on winter temperatures,
winter sun, summer temperature, summer humidity, topographic variation, and water area.
The scale was actually developed in 1999, so is very unlikely to be influenced by cross-
sectional patterns that occurred after that. Interestingly enough, as seen in columns (2) and
(4), the effects are even larger when instrumenting with amenities, suggesting that there was
indeed a strong force towards moving to high-rent areas.
As shown in the paper, initial rents and elasticity are quite correlated. And there are
various theories for why low elasticity areas are more "sensitive" to national house price
swings than high elasticity areas. Population movements towards inelastic areas is the key
174
Table 3.4: Log Change, 2000-2006
(1) (2) (3) (4)
House Prices House Prices Population Population
Inverse Rent -402.7*** -1074.0*** -34.95** -117.2*
(57.31) (184.4) (12.71) (49.05)
Instrument - Amenity - Amenity
First-stage F 48.62 48.73
Observations 648 641 708 691
Standard errors in parentheses
* p < 0.05, ** p < 0.01, *** p < 0.001
argument in favor of our theory, but we can also run a horse race between inverse rents and
elasticity to see which explains house price movements better. In columns (1)-(3) of Table
3.5, we show that, indeed, inverse rents and elasticity both are predictive of house price
changes from 2000 to 2006. But when both are included in the regression, only inverse rents
are still predictive. Elasticity has almost no predictive power conditional on inverse rents.
Using the Saiz (2010) elasticities, both inverse rent and elasticity are predictive. The
reader might be concerned that this could be simply because our measure of elasticities
is noisy. But we think the different results are actually instructive. There are two major
differences between our regressions, both of which help us to understand why elasticity is
insignificant in column (3). The first difference is that the Saiz elasticities are only in MSAs,
so house price changes outside of cities are not included in those regressions. But, in fact,
there was significant house price appreciation in many such places, many of which are quite
elastic, and some of which also have high initial rents. The second difference is that our
measure of elasticity is quite different for Las Vegas than Saiz. Our estimated elasticity is
approximately 9, while his is approximately 1.4. In fact, the fact that we estimate Vegas to
have a high housing supply elasticity makes it an outlier in our regression, and helps drive
the horse race. Because prices went up significantly in Las Vegas, it helps inverse rents win
the horse race against elasticity.
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Table 3.5: Log House Price Change, 2000-2006
(1) (2) (3) (4) (5) (6)
Inverse Rent -402.7*** -402.1*** -468.9*** -233.1**
(57.31) (56.58) (70.94) (81.25)
Elasticity -0.0345*** 0.000248 -0.142*** -0.106***
(0.00834) (0.00482) (0.0203) (0.0253)
Elasticities Saiz Saiz Saiz
Observations 648 647 647 269 269 269
Standard errors in parentheses
* p < 0.05, ** p < 0.01, *** P < 0.001
3.11 Components of Population Change
Our theory critically depends on taking the total stock of people as exogenous. This as-
sumption would be violated if the key components of regional population change were due
to anything except domestic migration. If international migration, death, or birth were dri-
ving these changes, we would be worried that population was not due to a trade-off of where
to live, but that the outside option was living outside of the United States, or something
else entirely.
Therefore, in this appendix, we show that domestic migration is the key driver of po-
pulation changes along the key dimensions we emphasize, and that domestic migration and
new housing units are highly correlated.
The first thing to establish this is to break down the population line from the left side
of Figure 3-11. In that figure, we show that population increased in relatively inelastic
areas during the years we emphasize. We break down these population changes using the
postcensal Census estimates, which use various data sources to estimate each of the compo-
nents. Because of this methodology, the components may not add up to the total change in
population in years that the Census is taken, 2000 and 2010.
We show this decomposition in Figure 3-12. The change in relative population is due
almost entirely to domestic migration. Over our whole sample, more people are born and
176
MC aU-)
=~ CD
00
()
LO
1994 2d00 2d06 2012
- Log Population Change -e- Domestic Migration
' Births minus deaths - International Migration
Figure 3-12: The components of yearly population change, regressed on local housing supply
elasticity
fewer people die in inelastic areas, and there is more international migration to those areas.30
But in the early part of our sample, domestic net migration was towards elastic areas,
canceling these other forces out. But during the period right before the boom, net migration
towards elastic areas fell significantly, meaning that population in inelastic areas expanded
relatively. We view this as consistent with a change in the relative demand to live in inelastic
areas.
Similar to this exercise, we can show that the population changes in response to ma-
nufacturing and initial rents are also due to domestic migration. We show this in Figure
3-13. In the years near the turn of the millennium, domestic migration decreased toward
manufacturing areas, and increased towards high rent areas. As before, the relative amount
of births, deaths, and international migration are not changing that much. Not surprisingly,
given that the decline in manufacturing predates our sample period, there is significant net
population decline throughout this period, but it is particularly pronounced in the time
right before the housing boom. The opposite is true for high rent areas. While the relative
population change is never negative, it is effectively zero before 1996, when there is a six
year period where population increases dramatically.
3 0 We only show births net of death, but both are flat and contribute to relative population increases in
inelastic areas.
177
0,
M.
MC
a-
1994 2000 2006 2d12 1994 2000 2006 2012
Log Population Change -+- Domestic Migration Log Population Change -+- Domestic Migration
Births minus deaths International Migration a Births minus deaths International Migration
Figure 3-13: The components of yearly population change, regressed on manufacturing share
(left) and rent (right)
0
Ci
0
C)P
.3 -.2 -.1 0 .1 .2
Net Inmigration (Fraction of Population)
Figure 3-14: The change in log house units versus domestic net inmigration as a fraction of
population
The second thing we show is that domestic net migration is a major driver of local housing
quantities. To do this, we plot the change in the log housing units versus the total domestic
net inmigration as a fraction of initial population for the years 2000-2006, similar to our
Figure 3-6, but focusing only on the change in population due to domestic migration. The
overall picture, shown in Figure 3-14 looks quite similar. The coefficient is slightly smaller,
0.84, and the r2 falls as well, to 0.7. Nonetheless, the point remains: the main determinant
of housing units is the number of people moving into that commuting zone.
178