RDP 2016-04: Housing Prices, Mortgage Interest Rates and the Rising Share of Capital Income in the United States Appendix C: Banking Deregulation and Housing Capital Income

In this appendix, I look for more direct evidence that the deregulation of the US banking sector contributed to the rise in housing capital income by boosting the supply of mortgage credit and, in turn, the demand for owner-occupied housing. Before doing so, it is helpful to briefly outline the institutional background to US banking deregulation.

The US banking sector has undergone significant reform in recent decades (Kroszner and Strahan 1999; Sherman 2009). During the last quarter of the twentieth century, federal and state authorities removed geographic restrictions on: 1) intrastate bank branching (i.e. establishing branches within a state); 2) interstate banking (i.e. establishing subsidiary banks across states); and 3) interstate branching (i.e. establishing branches across states) (Jiang, Levine and Lin 2014).

This culminated in the passage of the Riegle-Neal Interstate Banking and Branching Efficiency Act in 1994. After this time, both national and state-chartered banks were allowed to operate and open branches across state borders without formal authorisation from the state authorities. However, states retained the right to impose restrictions on the extent of geographic expansion. For instance, states were allowed to place limits on the size of banks or forbid ‘de novo branching’ (i.e. the establishment of new branches).

Rice and Strahan (2010) construct an index to capture the differences in restrictions on interstate branching across states and over time. The regulation index runs from 1994 to 2005 and takes values between 0 and 4. The value of the index depends on the number of different branching restrictions in place at a point in time (up to a maximum of four restrictions). For my purposes I ignore the number of restrictions and simply construct a ‘deregulation index’ that takes the value of 1 if at least one restriction has been removed and is 0 otherwise. In effect, I assume that every state is fully restricted in 1994 (i.e. the index equals 0) and is fully unrestricted as soon as at least one restriction is removed (i.e. the index equals 1).[17] As will be discussed, I do this to aid the interpretation of the results in a difference-in-difference modelling framework. My key results are not affected by ignoring the additional information contained in the number of state-level restrictions. I also extend the series beyond 2005 by keeping the value of the index for each state constant at its 2005 level.

To identify the effect of financial liberalisation on housing capital income I exploit variation over states and time in exogenous restrictions on interstate bank branching. My identification strategy is based on an experimental research design that has been used extensively in the banking and housing economics literature (e.g. Jayaratne and Strahan 1996; Black and Strahan 2002; Kerr and Nanda 2009; Rice and Strahan 2010; Michalski and Ors 2012; Krishnamurthy 2013; Berger et al 2015). My strategy most closely follows the method outlined in Favara and Imbs (2015). Consider the following panel regression:

where the dependent variable is the relative price of owner-occupied housing for metropolitan statistical area m in state s in year t. The explanatory variables include a dummy variable (INELASTIC) for whether the metro area is above its state median in terms of being inelastic in housing supply. This is interacted with a dummy variable for whether the state has deregulated or not in a particular year (DEREG). The deregulation index equals 1 as soon as the state deregulates (and stays equal to 1 thereafter). Note that the (in)elasticity index varies by metro area while the deregulation index varies across states and over time.

Note also that I focus on relative prices in the regression because the preceding analysis suggested that the long-run rise in the share of housing capital is due to relative prices. Furthermore, the data on housing capital income at the MSA level is of relatively poor quality.[18]

The staggered pace of reform across states provides important variation in the timing (and size) of the credit supply shock. But it also raises the question of what caused this variation. It could be argued that the removal of restrictions on interstate branching was endogenous to local housing market conditions (i.e. E(DEREGst * εmst)≠0). For example, state policymakers may have been more open to entry by out-of-state banks if conditions in their housing market were particularly weak. Any subsequent increase in housing demand (and relative prices) may just reflect a return to more normal conditions, rather than the adoption of the law. However, Kroszner and Strahan (1999) provide evidence that the bank branching restrictions were correlated with the lobbying power of small banks, and not with contemporaneous economic conditions. (States were less likely to deregulate when the small banks held significant market share as they were less inclined than large banks to expand across state borders.)

Regardless, I circumvent this problem by exploiting variation in housing supply elasticity within a state at a given point in time. More specifically, I include linear state-specific time trends (λst) in the regression model. These trends absorb any linear changes in relative housing prices across states and, more importantly, may also capture latent factors that influenced state policymakers to remove the branching restrictions at a particular point in time. The assumption underlying this strategy is that the decision to change state laws may be associated with average conditions in the state but is unlikely to be correlated with conditions between metro areas within a state.

The timing of deregulation may also be correlated with the supply elasticity of the local housing market. For example, expansion-minded large banks may have been more inclined to push for deregulation in areas that are particularly constrained by supply in order to capture the rents associated with any increase in housing demand. But this would just imply a negative correlation between the level of the deregulation index and the elasticity of housing supply and should not bias the coefficient estimates. Moreover, I find that the main results hold even after excluding the largest capital cities, such as Chicago, Los Angeles and New York, where this problem is likely to be most acute.

There may also be serial correlation in the relative price of housing and in the deregulation indicator (which is essentially a state-specific time series of zeroes and ones). To deal with this serial correlation and estimate conservative standard errors, I follow the recommendation of Bertrand, Duflo and Mullainathan (2004) and collapse the model to two periods – ‘before’ and ‘after’ deregulation. I do this by taking the unweighted average of each variable in the pre- and post-deregulation periods. I then take the difference between these two periods to arrive at the final specification to be estimated:[19]

where I have removed the time subscript to highlight the fact that it is a cross-sectional regression with one observation per metro area in the sample. This is essentially a difference-in-differences model. The causal effect of credit supply on the relative price of housing is identified by the difference in relative housing price growth between inelastic metro areas (the treatment group) and elastic metro areas (the control group) within the same state following the removal of the branching restrictions (the treatment).

A positive coefficient on the inelasticity indicator (β) indicates that the relative price of housing rose by more in the inelastic metro areas than in the elastic metro areas of the same state following deregulation. This would be consistent with the hypothesis that the credit supply shock had a relatively large impact on real housing prices in metro areas with more restricted housing supply.

There are a few differences between my identification strategy and that followed by Favara and Imbs (2015). First, I allow for state-specific time trends in the specification and hence exploit variation between metro areas within the same state at a given point in time. They instead exploit variation between a treated group of banks and a placebo sample of non-bank mortgage lenders that were not affected by the change in bank branching laws. Second, I focus on the determinants of growth in relative housing prices rather than housing price growth per se. I therefore allow for the possibility that a rise in housing prices might reflect a more general increase in prices in the local area. It is important to control for non-housing prices as housing and non-housing prices tend to positively co-move across cities (Albouy et al 2014); cities where housing is expensive are cities where non-housing services (e.g. restaurant meals, haircuts, dry cleaning) are also expensive. Third, to control for serial correlation, I collapse the data to two periods while they estimate models with lagged dependent variables on the full sample of annual observations.

To test the causal effect of financial deregulation on the relative price of housing I first look for graphical evidence that the common (or parallel) trends assumption is satisfied (Angrist and Pischke 2009). The trends in the relative price of housing for the inelastic and elastic metro areas are plotted in Figure C1. The series are both indexed to 100 in the year in which deregulation occurred. The graphical evidence is consistent with the hypothesis that housing prices increased (relative to non-housing prices) at the time of deregulation and that this effect was much stronger in the metro areas in which housing is inelastically supplied.

Figure C1: Relative Price of Housing
Year of deregulation = 100
Figure C1: Relative Price of Housing

Sources: Author's calculations; Carrillo et al (2014); Federal Housing Finance Agency

Next I turn to the statistical evidence. The results of estimating Equation (C1) are shown in Table C1. I show estimates with and without state fixed effects and with and without controls.

The basic OLS estimates (column 1) point to an average treatment effect (ATE) of around 4 per cent. In other words, the relative price of housing increased by 4 per cent in the inelastic metro areas relative to the elastic metro areas, on average, after deregulation. The inclusion of control variables (column 2) – namely, population growth and real personal (per capita) income growth – reduces the economic significance of the estimated ATE but it remains statistically significant at the 1 per cent level. As might be expected, (per capita) personal income growth is positively correlated with a higher relative price of housing. Population growth appears to have an insignificant effect, at least in the fixed effects specifications.

The preferred within-state estimates indicate that the relative price of housing rises by 2.7 per cent, on average, in the inelastic metro areas relative to the elastic metro areas following deregulation (column 3). Similar results obtain if I replace the dummy for inelastic metro areas with a continuous variable for the extent of elasticity. In a sense, this variable measures the ‘intensity of treatment’ – the more elastic is the housing stock the less effect the credit supply shock should have on relative housing prices. And I find that in metro areas in which the supply of housing is particularly inelastic, the effect of deregulation on housing prices is stronger (column 4).

Table C1: The Effect of Deregulation on Relative Housing Prices
  OLS   Fixed effects
(1) (2) (3) (4)
Inelastic supply dummy 0.040***
Inelastic supply indicator         0.010*
Population growth   0.177***
Real personal income growth   0.383***
Constant 0.126***
State fixed effects No No   Yes Yes
R2 0.046 0.174   0.707 0.698
Observations 276 276   276 276

Notes: Standard errors are clustered by state; ***, **, and * denote significance at the 1, 5 and 10 per cent level, respectively; t statistics in parentheses

In terms of economic significance, if the elasticity index were increased from the 25th percentile to the 75th percentile, the relative price of housing would rise by 1.7 percentage points less in response to the credit supply shock than otherwise. In a rough sense, this would be equivalent to converting the amount of developable land from an ‘inelastic’ city like Denver, Colorado to a more elastic city like Kansas City, Missouri.

Overall, the results are consistent with the hypothesis that the removal of interstate bank branching constraints had a relatively large effect on prices in the metro areas in which the supply of housing is inelastic. This is expected if supply constraints matter, namely that better access to credit will feed through to house prices more in regions where the supply of houses cannot adjust as easily.[20]


Prior to 1994, eight states permitted some limited interstate branching (i.e., Alaska, Massachusetts, New York, Oregon, Rhode Island, Nevada, North Carolina and Utah). But the option to branch out of state lines was never exercised, except in a few cases. [17]

More specifically, there is information available on gross value added for the real estate sector by metro area but there are problems with BEA's methodology and its ability to measure GDP at the MSA level. GDP data is collected at the state level, not the metro level. The BEA allocates a state's GDP to metro areas using state-level GDP by industry and county-level earnings by industry. The state's GDP within each industry is allocated to counties based on county earnings data for each industry. The earnings of workers employed in the housing industry are likely to be a very imperfect proxy for the income earned by landlords and home owners. Moreover, the MSA-level data are only available since 2001, while most of the run-up in the share of housing income occurred prior to this period. [18]

The construction of the dummy variable for the deregulation (treatment) period allows me to interpret the estimated coefficients ‘more cleanly’ as average treatment effects. Alternatively, I could leave the regulation index in its original form, with values ranging from 0 to 4, and this would mean that the regulation index would still appear in the regression specification in first differences. This would implicitly place greater weight on states that retained multiple restrictions. For example, a state that retained two restrictions on bank branching would effectively experience a demand shock that was twice as large as that of a state that retained just one restriction. [19]

In unreported results, I find that the estimated treatment effect is not affected by excluding certain large states (e.g. California and New York). The results are also not affected if I include a wider range of control variables, such as the stock of housing, housing vacancy rates and demographics (e.g. population size, the age structure of the population). These results are available upon request. [20]