Home Equity and Labor Income: The Role of Constrained Mobility

Abstract

Using detailed data for U.S. homeowners, we document a negative, nonlinear relation between the loan-to-value ratio (LTV) of homeowners’ primary residence and their labor income. Consistent with high LTV individuals experiencing constrained mobility, we find stronger effects among subprime, liquidity- constrained individuals and those living in regions with limited alternative local employment opportunities and strict noncompete law enforcement. Though high LTV individuals are less likely to move across MSAs, they are more likely to change jobs without changing their residence. We find no effects among similar neighboring renters employed at the same firm and with a similar job tenure.

The Great Recession and the subsequent slow recovery in wages have heightened interest in understanding if and how mortgage debt and house price changes affect labor market outcomes. One potential channel that links the mortgage market to the labor market runs through labor mobility. If a homeowner’s equity is negative—if the mortgage debt outstanding is more than the value of the house—it can adversely affect labor mobility.¹ Reduced mobility can in turn lead to a higher likelihood of unemployment² or affect labor income for the employed individuals by reducing their bargaining power and the quality of match between an employee and an employer. In this paper, we use administrative wage data matched to the credit profiles of millions of homeowners in the United States to document the effect of home equity on labor income among employed individuals. Our data also allow us to examine the channels through which any such effects operate.

An underwater homeowner facing the prospect of moving to accept a better job opportunity can do one of three things. She can sell her house and compensate the lender for any possible shortfall between the sale price (net of transaction costs) and the mortgage outstanding. Her ability to do so will depend on her access to liquidity and the extent to which she is credit constrained. Alternatively, she can retain her house and possibly rent it. This will affect her ability to make a down payment on a new house. She may also perceive some costs originating either from rental market frictions or from her preference for homeownership. Finally, she has the option to walk away from her house and default on the mortgage. Each of these options has some cost associated with it and depending on the severity of credit constraints, a homeowner may be willing to give up some attractive (out-of-region) employment opportunities to remain in her current residence. This constrained mobility may in turn affect the homeowner’s incentives to search for opportunities in the first place and, consequently, her bargaining power with her employer, thereby adversely affecting her labor income.³

In addition to mobility, home equity may also affect labor income through a debt overhang channel. If a large fraction of a homeowner’s income goes toward servicing mortgage debt, then she may not have incentives to increase labor supply and seek better opportunities (e.g., Bernstein 2016; Donaldson, Piacentino, and Thakor 2019). Alternatively, low home equity may increase labor income if it provides additional incentives for the homeowner to reduce debt and avoid the possibility of a costly default (Lazear, Shaw, and Stanton 2016). We refer to this as the incentive channel. We evaluate the merits of these alternative channels that relate to home equity and labor income.

We use anonymized credit and employment data from Equifax Inc., one of the three major credit bureaus in the United States. The credit data include information on the credit histories of all individuals in the United States, including historical information on all their credit accounts, credit score, and ZIP codes of residence. The employment data cover over 30 million employees across the United States from over 5,000 firms and contain granular information, including information about employee wages, employee bonuses, employee commissions, employees’ job tenures, and firm-level details. This is one of the first papers to use such detailed credit and employment data about the U.S. population.

Using the intersection of the credit and employment data, we obtain a panel over the 72-month period between January 2010 and December 2015. We conduct our analysis on a random sample of 300,000 individuals from our data who have an active mortgage as of January 1, 2010. These mortgages were originated sometime before January 1, 2010. We observe the employer-reported incomes in the employment data. We measure home equity as the loan-to-value ratio (LTV) on the primary residence, where LTV is the ratio of total mortgage loan outstanding over the imputed market value of the house. Since we expect LTV to have a nonlinear effect on income, our main independent variables are a set of dummy variables that identify individuals with LTVs in different buckets. The construction and choice of these buckets are described in Section 2.

Both main sources of variation in LTV—changes in the amount of loan outstanding and changes in home values—are problematic for identifying our effects. Loan outstanding can change because of normal loan repayment—a function of loan maturity—and because of prepayments or delayed payments.⁴ All of these may be correlated with an individual’s income. To overcome this, we follow Bernstein (2016) and instrument LTV with a synthetic loan-to-value ratio (SLTV) that is constructed under the assumption of uniform maturity and interest rate for all borrowers and no prepayment or delayed payments.⁵ The exclusion restriction in our instrumental variables (IV) specification is that SLTV, which varies based on purchase cohort and house price changes since mortgage origination, affects labor income only through its effect on LTV. We discuss the validity of this assumption in section 2.

We proxy for changes in home values using ZIP-code-level house price indices. We control for local economic conditions (and hence the local labor market conditions) using ZIP-code-specific time fixed effects. We are able to do this because SLTV varies across individuals within a ZIP code based on when they bought their house (i.e., their purchase cohort). We also include within purchase cohort-time fixed effects to control for average nationwide cohort effects at a particular point in time. Finally, one could argue that local industry-specific shocks could differentially affect the labor market outcomes and house prices of individuals in a ZIP code belonging to different purchase cohorts. To evaluate this, we conduct a parallel placebo analysis using a sample of “renters” who reside in the same ZIP code as our homeowners, work for the same firm, are similar in age, and have similar levels of income, nonmortgage debt and job tenure. Our assumption is that the “renters” should be subject to similar labor market shocks as the homeowners.

We find a strong negative, nonlinear relation between LTV and income. Our IV estimates show that individuals with |$\it{LTV}\in{\rm[1,1.5)}$| earn

352.1 lower monthly income relative to those with |$\it{LTV}\in{\rm[0,0.3)}$|⁠, our base case. This effect is economically significant as it corresponds to 5.1|$\%$| of the sample mean. We also document slower income growth among individuals with high LTV values. Specifically, individuals with |$\it{LTV}\in{\rm[0,0.3)}$| experience 3.4 percentage points (pp) lower income growth (relative to the beginning of the sample) when compared to the base case. Thus, our results are consistent with both mobility and debt overhang channels and inconsistent with the incentive channel. We also find that individuals with |$\it{LTV}\in{\rm[0.8,1)}$| earn a lower income and experience slower income growth relative to individuals in the base case. This suggests that the negative effects of high |$\it{LTV}$| begin even at values below one. According to the mobility channel, this can happen if the transaction costs associated with selling a house reduce one’s ability to make a down payment for a new house (e.g., Stein 1995; Genesove, and Mayer 1997).

We find that LTV does not significantly affect the labor income and income growth for the individuals in our placebo sample. Thus, a renter who resides in the same ZIP code, works for the same firm, with similar age, levels of income, nonmortgage debt, and job tenure as a homeowner with |$\it{LTV}\geq1$| does not experience lower income and income growth as compared to a renter who is similar (on the above dimensions) to a homeowner with |$\it{LTV}\in{\rm[0,0.3)}$|⁠. The insignificant result suggests that unobserved local labor market shocks have a limited effect on our results.

To test the validity of the mobility channel, we examine the effect of LTV on labor mobility. We measure mobility as instances when the individual moves residence (with or without a change in employer) from one metropolitan statistical area (MSA) to another. We find that individuals with high LTV values are less likely to move. For instance, individuals with |$\it{LTV}\in{\rm[1,1.5)}$| are 0.1 pp less likely to move in a month relative to those in the base case. This effect is economically large when compared to the mean likelihood of moving of 0.13|$\%$| in a given month. Using credit scores and access to liquidity at the beginning of our sample as alternative measures of credit constraints, we find that the negative effect of LTV on labor mobility is stronger for borrowers with below median credit scores and for those with below-median undrawn credit limit relative to the mortgage outstanding. Similarly, the negative effect of high LTV on labor income is larger in absolute magnitude for borrowers with high levels of credit constraints.

Constraints on geographic mobility are likely to prove less detrimental to labor income if the local MSA provides alternative opportunities in the individual’s line of work.⁶ To test this conjecture, we differentiate between the MSAs in our sample based on the availability of jobs in an individual’s industry. The assumption is that it will be easier for an individual to shift to jobs within her industry than outside. Consistent with our conjecture, we find that the negative effect of high LTV on income is stronger for individuals living in MSAs that have a below-median level of industry-specific jobs, that is, a below-median level of the ratio of the number of the MSA’s residents employed in the specific industry identified using the three-digit NAICS code to the total number of employed residents in the MSA as of January 2010.

Next, we evaluate the importance of the debt overhang channel. An individual subject to debt overhang is likely to limit her labor supply and her efforts to improve her income until her debt load reduces by some amount. On the other hand, if an individual’s income is adversely affected by constrained geographic mobility, the individual may be more inclined to change jobs without changing residence in an effort to improve her income and compensate for the loss of out-of-region opportunities. Consistent with the mobility channel but inconsistent with the debt overhang channel, we find that individuals with high LTV values are more likely to change jobs without changing their residence. This effect is stronger among credit-constrained individuals whose inter-MSA mobility is relatively more constrained. We also find this effect to be stronger for individuals who reside in MSAs with greater industry-specific job opportunities. and those residing in states where noncompete laws are not strictly enforced. Employing the number of hours worked (for hourly wage employees) and the extent of variable pay (for salaried employees) as measures of labor supply, we also relate LTV to labor supply. Inconsistent with the debt overhang channel, we find no significant relationship between LTV and our measures of labor supply.

Constrained mobility due to high LTV can depress both income from the current job and the raise an employee receives when changing jobs. The former can happen if constrained mobility reduces an employee’s search efforts for alternative employment and, consequently, her bargaining power, whereas the latter can occur because of a constrained opportunity set.⁷ We find that both contribute to our baseline estimates. When we limit our sample to the time before an individual changes jobs for the first time and repeat our analysis, we find that individuals with |$\it{LTV}\in{\rm[1,1.5)}$| earn

351.6 lower monthly income relative to those with |$\it{LTV}\in{\rm[0,0.3)}$|⁠. We also find that high LTV individuals experience a 2-pp-lower wage increase when they change jobs.

A potential limitation of our analysis is that we do not observe the house price at mortgage origination and hence the amount of down payment at origination. This can potentially introduce noise in our estimates if the difference between the true LTV and our imputed LTV is correlated with income. A number of features of our analysis help overcome this problem. First, our use of multidimensional fixed effects helps control for a number of channels through which this potential measurement error could affect our estimates. For example, our within-cohort-time effects will control for any tendency of individuals within a purchase cohort to make a lower down payment—say, because of a credit boom—to buy their house. Second, the results of our placebo tests ensure that the measurement error has a limited effect on our estimates. If the measurement error were correlated with house prices and income trends for a specific set of individuals within the main sample, one would expect it to also affect the income trends of the corresponding renters. This is because both sets of individuals reside in the same ZIP code and are employed at the same firm and hence should be subject to similar economic conditions. Third, our use of nonparametric piecewise function instead of a linear function of LTV helps minimize the impact of noise on our estimates. For instance, if the true LTV is 1.26, while our imputed LTV is 1.15, this will not induce an error in our estimation because we will correctly assign the homeowner to the [1,1.5) bucket. This noise may, however, lead to misclassification errors if it pushes individuals into an incorrect LTV bucket (e.g., Schulhofer-Wohl (2012)).

We conduct a number of tests to further ensure that our inability to observe house prices at origination and the resultant misclassification error does not bias our conclusions. First, we compare our LTV measure to two different distributions in the Equifax Credit Risk Insight Servicing McDash (CRISM) data from Gerardi et al. (2018), who calculate LTV based on actual origination LTV values. We find our LTV distribution matches well with the data from CRISM. Second, we conduct a number of tests in which we repeat our baseline analysis using specifications where misclassification is likely to be smaller. Specifically, we reestimate our baseline test by dropping the observations that are close to the cutoffs for our bins, considering only one dummy variable as the independent variable that identifies observations with |$LTV>0.8$|⁠, and considering only one dummy variable while dropping observations on the neighborhood of the cutoff (i.e., those with |$LTV\in[0.7,0.9]$|⁠). Across all specifications, we find results similar to our baseline estimates. Third, potentially, actual down payments could be higher in ZIP codes where the homeowner expects house prices to increase. To the extent such expectations depend on time and geography, they should vary at the ZIP code purchase cohort level. To control for this, we repeat our estimates after including within ZIP code purchase cohort fixed effects and find our results to be unaffected. Fourth, we repeat our analysis for the subsample of ZIP codes that have more homogeneous house prices (i.e., those with low within ZIP code standard deviation in house prices). We expect the measurement error in LTV to be smaller in these ZIP codes and find similar estimates for this subsample. Fifth and finally, we repeat our analysis with alternative assumptions about the LTV at origination and obtain consistent results.

Our results provide strong support to the conjecture that steep declines in house prices in the presence of a large amount of mortgage debt is likely to worsen the match between employees and employers, and affect employee productivity. Given the decline in house prices during the great recession, our estimates imply that constrained mobility owing to high LTV values can explain up to a 2.3|$\%$| decline in wages. The negative spillovers that we document is of relevance to both policy makers and companies. Our results will help policy makers identify the geographies and the subpopulations that will be most constrained by low home equity. This can be used to design targeted policy interventions. Our results are also of relevance to firms interested in hiring and developing human talent as they show that credit constraints may affect an employee’s willingness to move for job opportunities. If firms can relax such constraints, that may enhance labor mobility and consequently productivity.

1. Related Literature

A growing literature examines the relation between home equity and labor market outcomes. The most researched outcome is labor mobility. Theory predicts that lower home equity should constrain labor mobility, say due to credit constraints (Stein 1995; Ortalo-Magne, and Rady 2006), nominal loss aversion (Genesove, and Mayer 2001; Engelhardt 2003; Annenberg 2011), or higher likelihood of defaults (Deng, Quigley, and Order 2000; Ghent, and Kudlyak 2011; Molloy, and Shan 2013). However, evidence on the topic is mixed. For instance, while Henley 1998; Chan 2001; Ferreira, Gyourko, and Tracy 2010; Ferreira, Gyourko, and Tracy 2012; Goetz 2013; Kothari, Saporta-Eksten, and Yu 2013; Modestino, and Dennett 2013, and Bernstein, and Struyven (2016) document a positive relation between home equity and labor mobility, others find weak, null, or opposite results (e.g., Aaronson, and Davis 2011; Molloy, Smith, and Wozniak 2011; Schmitt, and Warner 2011; Schulhofer-Wohl 2012; Farber 2012; Coulson, and Grieco 2013; Mumford, and Schultz 2013; Bricker, and Bucks 2016; Demyanyk et al. 2016).⁸ Yet others document the effect of housing lock on unemployment (Karahan, and Rhee 2013; Valletta 2013), macroeconomic fluctuations (Sterk 2015), and recovery from recession (Herkenhoff, and Ohanian 2011). Recent work by Brown, and Matsa (2017) shows that individuals seeking employment and residing in areas with greater house price declines are more likely to apply for jobs within the region of their residence. We contribute to this literature by using detailed credit and income data for a large sample of U.S. residents to document the consequences of housing lock on homeowners’ income. Precise employer-reported incomes allow us to document that employed, high LTV homeowners earn lower income. Importantly, the granularity of our data and the components of income that we observe (e.g., hourly workers, number of hours worked and variable pay) allow us to better evaluate and distinguish between the economic mechanisms, and identify the role of constrained mobility in reducing income for high LTV homeowners.

Closely related to our work, Cunningham, and Reed (2013) use survey data from the American Housing Survey (AHS) to document a negative relation between LTV and income, while Bernstein (2016) uses bank account data to infer income and document that negative home equity leads to reduced labor supply owing to debt overhang. In contrast, we use detailed employer reported data and do not find evidence of the debt overhang channel for the sample of employed individuals as we observe no change in labor supply for either hourly or salaried workers. Instead, our results suggest that individuals with negative home equity experience declines in income owing to constrained mobility likely because it reduces employee bargaining power or worsens the match between employees and employers, thus affecting employee productivity.

Our paper also relates to the broader literature that investigates the effect of leverage on different aspects of household decision making and the economy. For instance, prior studies have examined the effect of extreme leverage on entrepreneurial activity (Adelino, Schoar, and Severino 2015), employment opportunities (Mian, and Sufi 2014; Bos, Breza, and Liberman 2010), household consumption and investment decisions (Bhutta, Dokko, and Shan 2010; Foote, Gerardi, and Willen 2008; Fuster and Willen 2013; Guiso, Sapienza, and Zingales 2013; Mian, Rao, and Sufi 2013), and the real economy (Mian, and Sufi 2011; Mian, Sufi, and Trebbi 2015). Melzer (2015) finds that households with negative home equity reduce investments in their house, since they anticipate not to be residual claimants any more. Using administrative data from home affordable modification programs, Scharlemann, and Shore (2016) find that individuals with negative home equity are more likely to default on their mortgage. We contribute to this literature by highlighting a new dimension of the consequences of the spillover effects of home equity on the labor market.

2. Empirical Methodology

The main independent variables in our analysis are the indicator functions |$\left\{ 1_{\{l_{k}\leq\it{LTV}_{it-1}<h_{k}\}}\right\} $| which equal one when individual |$i$|’s loan-to-value ratio (⁠|$\it{LTV})$| at the end of year-month |$t-1$| is between |$l_{k}$| and |$h_{k}$| (i.e., |$\it{LTV}_{it-1}\in[l_{k},h_{k})$|⁠).⁹ Before we describe the construction of the indicator functions, we describe our calculation of LTV for which we use the imputation method described in Bernstein (2016). While we observe the exact loan amount outstanding at any point in time and changes in house prices at the ZIP code level, we do not observe individual home values at the time of initial purchase (or refinancing). Hence, we make some simplifying assumptions to calculate |$\it{LTV}$|⁠. Hereinafter, we refer to the month of mortgage origination or refinance as the month of origination.

The LTV we calculate at the time of origination depends on the number of mortgages an individual originates. If an individual originates a single mortgage in a month, we assume the LTV at origination to be 0.8. On the other hand, if the individual originates multiple mortgages in a month, we assume the origination LTV on the largest mortgage to be 0.8 and calculate the total LTV based on the total amount borrowed on all of the mortgages. This assumption is based on the common industry practice to cap the LTV on the primary mortgage at 0.8 in order to comply with GSE (Fannie Mae/Freddie Mac) guidelines. In cases where the borrower requires more than 80|$\%$| financing, the lender supplements the first mortgage with a second mortgage.

We divide the range of |$\it{LTV}$|s in our sample into six nonoverlapping buckets: |$[0,0.3)$|⁠, |$[0.3,0.4)$|⁠, |$[0.4,0.8)$|⁠, |$[0.8,1)$|⁠, |$[1,1.5)$|⁠, and |$(\geq1.5)$|⁠. We include indicator functions to represent these buckets excluding the |$[0.3,0.4)$| bucket, the base case. The coefficient |$\beta_{k}$| in Equation 1 is a measure of the difference in the average outcome variable for individuals with LTV between |$l_{k}$| and |$h_{k}$| as compared to the base case. We employ dummy variables instead of a linear term in |$\it{LTV}$| to identify any possible nonlinear effect of LTV on the outcome variables without imposing any functional form restriction, especially around |$LTV=1$|⁠. Our use of dummy variables will also greatly diminish any bias due to measurement error in LTV. To ensure that our results are not due to our choice of buckets, we repeat our baseline analysis with equal sized buckets with a spread of 0.1.

We include a robust set of controls in our specification. First, we include individual fixed effects (⁠|$\delta_{i}$|⁠) to control for individual-level, time-invariant characteristics. Second, we include ZIP-code-specific time effects (⁠|$\delta_{zt})$| to account for time-varying local economic conditions that could affect both |$\it{LTV}$| and labor income. For example, adverse local economic conditions may simultaneously decrease home values (thus increase |$\it{LTV}$|s) and labor income. Third, we include purchase cohort-specific time effects (⁠|$\delta_{ct})$| to control for time-varying life cycle and cohort effects. Together, |$\delta_{ct}$| and |$\delta_{zt}$| control for the average level of the outcome variable within a purchase cohort and a ZIP code at a particular point in time, respectively. Finally, we include a quadratic term in job tenure and age |$(X_{i,t-1})$| to account for time-varying individual-level factors that could affect their income.

Two main factors drive the variation in LTV|$_{it}$| in our sample: the outstanding loan amount and the change in ZIP-code-level house price index since mortgage origination. These factors have a multiplicative effect, which ensures that we have variation in |$\it{LTV}$| across individuals within the same ZIP code as well as variation in |$\it{LTV}$| across individuals within the same purchase cohort.

Outstanding loan amounts can change either from scheduled loan repayments over time—a function of loan maturity—or from partial prepayments or delayed payments. All of these choices could be related to an individual’s income. For example, an individual who experiences an increase in pay, may choose to use the windfall to partially prepay her mortgage. Similarly, individuals that experience a negative shock to their income may be late in their mortgage payments, which could affect the loan outstanding and consequently |$\it{LTV}$|⁠. To ensure such endogenous changes in loan amounts do not bias our conclusions, we isolate the variation in |$\it{LTV}$| due to changes in the regional house price index since mortgage origination.

Our exclusion restriction requires that after controlling for time- varying characteristics at the ZIP code level, time-varying cohort effects, individual-level, time-invariant characteristics, age and job tenure, SLTV affects labor income only through its effect on |$LTV$|⁠. As mentioned before, SLTV changes with house price since origination and time since origination. These generate variation at the ZIP code x cohort x time level. Our exclusion restriction could be violated by a local shock that both differentially affects the labor income of individuals belonging to different purchase cohorts as well as house prices. We conduct a placebo test using a population of renters to rule out such omitted variables. We discuss this further in Section 4.1.

3. Data

3.1 Sample construction

Our empirical analysis leverages anonymized data on individual credit profiles and employment information from Equifax Inc., one of the three major credit bureaus. The anonymized credit data contain information on the credit histories for all individuals (with a credit history) in the United States for the period 2010–2015. This includes anonymous information on historical credit scores along with disaggregated individual credit-account level information, such as account type (e.g., credit card, home loan), borrower location, account age, total borrowing, account balance, and any missed or late payments. The employment data covers millions of individuals from more than 5,000 employers in the United States and includes anonymous information on each employee’s wages, salary, bonus, average hours worked, and job tenure; firm-level details; and whether the employee remains employed at the firm at a given point in time. Kalda (2019) provides details on the representativeness of the employment data. This is one of the first papers to use such detailed credit and employment data on the U.S. population.

We merge the two data sets to obtain a panel with credit and employment information over the 72-month period between 2010 and 2015. We restrict the panel to homeowners with an active mortgage loan as of January 1, 2010. Note that these mortgages were originated sometime before January 1, 2010. While the earliest mortgage in our sample was originated in 1976, most of the mortgages were originated during the boom years of 2002–2006. To make the computations feasible, we draw a random sample of 300,000 individuals from this sample to conduct our analysis. We allow individuals to drop out of our sample if they are no longer employed with a firm included in our employment data.¹⁰

We retain individuals in our sample until the first time they move their residence. Thus, if an individual changes the ZIP code of her residence for the first time in January 2012, with or without the closure of the corresponding mortgage account, she is dropped from the sample starting January 2012. This is because once an individual changes residence, they internalize the cost of (high) |$\it{LTV}$| of their previous residence and are no longer affected by it. Also note that we include the first month’s income after the move in our sample to make sure the pay differential is captured by our estimates. Refinancing is reflected in our data by the closing of one account and the opening of a new account. In such instances, we retain the old account up until the month before its closure and then switch to the new account with a beginning |$\it{LTV}$| calculated using the procedure detailed in the previous section.¹¹

The ZIP-code-level house price data we use comes from Corelogic and covers the period 1976–2015. Specifically, we use Corelogic’s monthly house price indices (HPI) to impute changes in home values at the ZIP code level. These indices are calculated using a weighted repeat sales methodology and are normalized by setting the index value as of January 2010 to 100.

We note two issues with our sample that may potentially bias our estimates. First, our sample is confined to the individuals in the intersection of the credit and employment data. Thus, our sample may not be representative of the population of mortgage borrowers in the United States as the employment data are not comprehensive and consist of individuals employed at the 5,000 firms, from which Equifax obtains data. The firms in our sample are larger than the average firm in the United States with a median firm employing over 1,100 individuals. However, the income distribution is representative of the U.S. workforce. For instance, the median individual in the data is 41 years old with an annual salaried income of

41,015. This is comparable to the U.S. workforce where the median individual with full-time employment is 41.9 years of age, salaried, and earns an income of

$\$$

41,392. Second, our sample may be subject to a survivorship bias. Recall that we focus on individuals who are current on their mortgage as of January 2010. Depending on when they bought their house, these individuals may have gone through the crisis without defaulting on their mortgage even if their house was underwater. Thus, on average, the individuals in our sample may have a lower propensity to default on their mortgage.

3.2 Sample description and statistics

Figure IA1 compares the distribution of individuals in our sample across states in the United States to the same distribution of the entire population (as of 2010) based on the location of an individual’s residence. The numbers in the figure represent the percentage difference in this distribution, that is, [|$\frac{StatePopulation}{TotalPopulation}]_{Sample}-[\frac{StatePopulation}{TotalPopulation}]_{Census}$|⁠. The distribution of employees in our sample is comparable to the distribution of the U.S. population for most states. The residual differences arise from Nevada, Colorado, Nebraska, Missouri, and Minnesota being over-represented in our sample and Montana, Wyoming, Vermont, and West Virginia being under-represented.

Table 1 reports summary statistics for the key variables that we use in our analysis. We have a total of 14,031,645 individual-month observations. The top panel reports summary statistics for our outcome variables. The mean monthly income in our sample is

6,927 while the median is

$\$$

5,513. The mean increase in income is 10.1|$\%$| relative to January 2010. The mean probability that an individual moves MSAs in our sample is 0.13|$\%$| per month.

The bottom panel of Table 1 summarizes our independent variables. The mean (median) loan size in our sample is

192,400 (⁠

$\$$

112,100). Loan size is right skewed and has a maximum value of over

$\$$

695,000. We impute the purchase price based on our calculation of LTV at origination. The average loan balance in our sample is

$\$$

161,600, approximately 84|$\%$| of the original loan amount. The mean (median) |$LTV$| and |$S\it{LTV}$| in our sample are 0.7 (0.8) and 0.8 (0.8), respectively. The summary statistics for the indicator functions show that 89|$\%$| of the observations in our sample have |$\it{LTV}$| between zero and one. Of the individuals with |$\it{LTV}$| between zero and one, 4|$\%$| have |$\it{LTV}$| less than 0.3, 11|$\%$| have |$\it{LTV}$| between 0.3 and 0.4, 54|$\%$| have |$\it{LTV}$| between 0.4 and 0.8, whereas 20|$\%$| have |$\it{LTV}$| between 0.8 and 1. About 11|$\%$| of our observations have |$\it{LTV}$| greater than 1. Overall, about 5|$\%$| of our sample observations switch bins during our sample period.

Figure 1 displays the density plot for the number of loan originations across time. Consistent with the spike in mortgage originations in the early 2000s, most individuals in our sample originate loans between 2002 and 2006. Hence, the individuals in our sample are likely to have experienced a decline in house prices during the Great Recession.¹²

4. Empirical Results

4.1 Home equity and labor income

We begin our empirical analysis by estimating Equation 1 and present the results in Table 2. The dependent variable in column 1 is the level of income measured in dollars (Income (⁠

⁠)). The positive and significant coefficient on |$1_{\{0\leq\it{LTV}<0.3\}}$| in column 1 indicates that individuals with |$\it{LTV}\in{\rm[0,0.3)}$| earn

$\$$

66.5 higher monthly income as compared to individuals with |$\it{LTV}\in{\rm[0.3,0.4)}$|⁠, our base case. Individuals with |$\it{LTV}\in{\rm[0.4,0.8)}$| earn similar income, whereas those with |$\it{LTV}\geq0.8$| earn lower income than our base case. For instance, those with |$\it{LTV}\in{\rm[0.8,1)}$| earn

$\$$

83.2 less. The magnitude of this effect increases with |$\it{LTV}$| values as individuals with |$\it{LTV}\in{\rm[1,1.5)}$| earn

$\$$

129.3 less than the base case. This effect is also economically significant as it corresponds to 1.8|$\%$| of the mean income in the sample. Interestingly, we do not find any statistical difference in income for individuals with |$\it{LTV}\geq1.5$|⁠.

In column 2, we repeat our analysis with logarithm of income as the dependent variable where we find that monthly income of individuals with |$\it{LTV}<0.8$| is not statistically different from those with |$\it{LTV}\in{\rm[0.3,0.4)}$|⁠. However, individuals with |$\it{LTV}\geq0.8$| earn lower income as compared to the base case. In contrast to column (1), individuals with |$\it{LTV}\geq1.5$| earn 0.3-pp-lower income than the base case.

In columns 3 and 4, we repeat our tests with income growth as the outcome variable. Specifically, we model the percentage change in income relative to January 2010 in column 3 and 12-month log change in income in column 4. Across both measures, we find that individuals with |$\it{LTV}\geq0.8$| experience lower income growth. For instance, from column 3, individuals with |$\it{LTV}\in{\rm[0.8,1)}$| experience 0.2-pp-lower income growth, whereas those with |$\it{LTV}\in{\rm[1,1.5)}$| experience 1-pp-lower income growth relative to the base case. These magnitudes are economically significant as they correspond to 2|$\%$| and 10|$\%$|⁠, respectively, of the mean income growth in the sample. Estimates in column 4 paint a similar picture.

In columns 5–8, we repeat our analysis for the placebo sample that we construct as follows. For every homeowner in the main sample, we identify an individual who as of January 2010, resides in the same ZIP code, works for the same firm, is similar in age, and has similar levels of income, nonmortgage debt, and tenure at the firm, but does not have an open mortgage account. We refer to these individuals as renters. We then attribute the homeowner’s |$\it{LTV}$| to the renter. Since the renters live in the same area and work for the same firm with similar tenure as the homeowner, their labor income should be subject to similar economic shocks. If our prior results are due to unobserved economic conditions affecting both house prices and labor income, or are driven by correlations between measurement error and income trends, then that should play out in the renter sample as well. We find no significant relationship between |$\it{LTV}$| and labor income in the placebo renter sample. This assures us that correlated unobserved economic conditions or measurement error may have a limited effect on our results.¹³

Table 3 presents the results of the IV regression described in Equation 5. We have six first-stage regressions, one for each |$\it{LTV}$| bucket indicator. In panel A of Table 3, we provide the coefficients along with F-statistic for each of the first-stage regressions. We find that all the instruments are strong with the F-statistics being significantly greater than the threshold of 10 (Bound, Jaeger, and Baker 1995; Staiger, and Stock 1997).

Panel B reports the coefficients for the second stage. The results in column 1 show that consistent with our ordinary least squares (OLS) results, labor income decreases with home |$\it{LTV}$|⁠. Comparing the magnitude of our coefficient estimates between the OLS and IV specifications, we find that our IV estimates are much larger than our OLS estimates. For example our IV estimates indicate that individuals with |$\it{LTV}\in{\rm[0.8,1)}$| earn

263.7 less income and those with |$\it{LTV}\in{\rm[1,1.5)}$| earn

$\$$

352.1 less income as compared to individuals with |$\it{LTV}\in{\rm[0.3,0.4)}$|⁠. Both magnitudes are economically significant as they correspond to 3.8|$\%$| and 5.1|$\%$| of the sample mean, respectively. Individuals with |$\it{LTV}\geq1.5$| earn

$\$$

178.6 less than individuals in the omitted category.

In column 2, we focus on logarithm of income and find IV estimates larger than the corresponding OLS estimates. Finally, in columns 3 and 4, we focus on income growth and find that individuals with high |$\it{LTV}$| experience slower income growth as compared to the base case. For example, from column 3 we find that individuals with |$\it{LTV}\in{\rm[0.8,1)}$| experience 2.4pp-lower income growth, whereas those with |$\it{LTV}\in{\rm[1,1.5)}$| experience 3.4-pp-lower income growth as compared to our base case.

Possible downward bias in our OLS estimates could explain the differences between our IV and OLS estimates. At least five factors may potentially drive a wedge between LTV and SLTV: partial prepayment of the mortgage, having a mortgage tenure less than 30 years (say, 15 years), late payments, mortgage modifications following defaults and a mortgage interest rate different from that assumed in our SLTV calculation (e.g., adjustable-rate mortgages). While partial prepayment, shorter tenure and modifications (hereinafter we refer to these combined as prepayment) are likely to depress LTV relative to SLTV, late payments is likely to increase LTV relative to SLTV. The effect of difference in interest rates can be ambiguous. Our summary statistics (see Table 1) indicate that LTV is on average lower than SLTV, a finding that indicates that prepayments dominate late payments in our sample. Data limitations keep us from evaluating the role of specific factors that may drive the differences between our IV and OLS estimates. For instance, we do not have information on the floating versus fixed rate mortgages in our sample.

In columns 5–8, we repeat our IV analysis within the placebo sample of renters and find no significant relationship between |$\it{LTV}$| and income (income growth). This provides strong evidence that unobserved labor market shocks and measurement error may have a limited effect on our results.¹⁴

To ensure that our results are not sensitive to the specific |$\it{LTV}$| buckets we pick, we repeat our tests with dummies to indicate 16 different |$\it{LTV}$| buckets instead of the six we have in the tables. We construct these buckets as follows. We divide the |$\it{LTV}$| values in our sample into 16 different buckets of which 15 buckets are of 0.1 width each. Since the number of observations with |$\it{LTV}$| greater than 1.5 are small, we combine all these observations into one bucket: |$\it{LTV}\in[>=1.5)$|⁠. As before, the omitted category is the bucket with |$\it{LTV}\in(0.3,0.4]$|⁠. Figure 2 plots the results with these 16 |$\it{LTV}$| bucket indicators.

In panel A of Figure 2, we model Income (⁠

and plot the coefficient estimates along with confidence intervals (CI) at the 95|$\%$| level. The estimates suggest that income for individuals with |$\it{LTV}$| less than 0.3, and |$\it{LTV}$| between 0.4 and 0.8, is not statistically different from income for individuals with |$\it{LTV}\in(0.3,0.4]$|⁠. However, individuals with |$\it{LTV}\geq0.8$| earn lower income relative to those in base case. In panel B, we model Income (⁠

$\$$

⁠) for the placebo sample and find no significant relationship between income and |$\it{LTV}$|⁠.

Our exclusion restriction may be violated by shocks that affect both house prices and the income of individuals that belong to different cohorts and reside in different regions in a differential manner. For example, regional (industry) booms that induce (migration and) home purchases in specific areas during specific time periods and differentially affect future income of new migrants and incumbents many years later may bias our estimates. A number of factors relating to our analysis help assuage this concern. First, if our results are driven by individuals moving to a particular ZIP code in response to a regional boom, then it should also affect the individuals in our placebo sample. This is because the individuals in our placebo sample are at a similar stage in terms of life cycle (age) and career trajectory (tenure) as our main sample. However, we find an insignificant relationship between LTV and income in our placebo sample. Second, we reestimate our baseline tests by including MSA x cohort x time fixed effects along with ZIP code x time fixed effects. The former likely controls for MSA level time-varying economic shocks. Table IA3 reports these results, which are similar to our baseline estimates. Finally, we also estimate our test by including ZIP code x industry x time fixed effects along with cohort x time fixed effects. We define industry at the three-digit NAICS code level. These additional fixed effects should control for local industry shocks. We again find our results to be robust to this specification. The results of these tests are discussed in detail in Section 5.4. Overall, these results lend support to our exclusion restriction and suggest that specific regional shocks are unlikely to drive our estimates.

4.2 Home equity and labor mobility

In this section, we examine the effect of |$\it{LTV}$| on labor mobility and how this effect interacts with an individual’s credit constraints. The results are reported in Table 4, where the dependent variable |$Mobility$| is a dummy variable that equals one in year-month |$t$| if the MSA associated with individual |$i$|’s primary residence in month |$t$| is different from their MSA in month |$t-1$|⁠. Although we include the full set of |$\it{LTV}$| indicator variables, we only report the coefficients on |$1_{\{0.8\leq\it{LTV}_{it-1}<1\}}$| and |$1_{\{1\leq\it{LTV}_{it-1}<1.5\}}$| for brevity. In column 1, we find that individuals with |$\it{LTV}\in{\rm[0.8,1.5)}$| are less likely to move than those with |$\it{LTV}\in{\rm[0.3,0.4)}$|⁠. Specifically, individuals with both |$\it{LTV}\in{\rm[0.8,1)}$| and |$\it{LTV}\in{\rm[1,1.5)}$| are 0.1 pp less likely to move in a month. These effects are economically large when compared to the mean likelihood of moving in a month of 0.13|$\%$| in our sample.

In columns 2 and 3, we examine the role of credit constraints on the effect of |$\it{LTV}$| on mobility. We use two measures of credit constraints: aggregate amount of undrawn credit limits on card accounts (column 2) and credit scores (column 3), both of which are measured as of January 2010. We classify borrowers with low (high) levels of credit constraints based on having Above- (Below-)median access to undrawn credit or credit score, and perform our cross-sectional tests by including interaction terms between the indicator variables that identify |$\it{LTV}$| buckets and Above and Below dummy variables. We find that higher |$\it{LTV}$| lowers mobility, especially for borrowers with Below-median access to liquidity and credit scores. In columns 4–6, we examine the effect of |$\it{LTV}$| on mobility for the placebo renters sample and find no significant relationship between |$\it{LTV}$| and mobility in the sample of renters.¹⁵

As before, to alleviate the concern that our results may be sensitive to the specific |$\it{LTV}$| buckets we use, we implement a specification wherein we include dummies to indicate 16 |$\it{LTV}$| buckets. In panel A of Figure 3, we model Mobility for our main sample and present the coefficient estimates along with the 95|$\%$| confidence intervals (CI). The estimates suggest that mobility of individuals with |$\it{LTV}<0.8$| is not statistically different from those with |$\it{LTV}\in(0.3,0.4]$|⁠. However, individuals with |$\it{LTV}\geq0.8$| are less likely to move than individuals in the base case. In panel B, we plot the estimates for the placebo sample and find no significant relationship between |$\it{LTV}$| and mobility.

4.3 Home equity and labor income: The mobility channel

In this section, we evaluate the merits of the “mobility” channel by testing for possible heterogeneity in the relation between |$\it{LTV}$| and labor income.

4.3.1 Heterogeneity by credit constraints

In the previous section, we find that high |$\it{LTV}$| is associated with a decline in mobility and this effect is stronger among credit constrained individuals. If this stifled mobility drives the negative relation between high |$\it{LTV}$| and income, we expect to see a larger decline in income for credit-constrained individuals with high |$\it{LTV}$|⁠. We evaluate this in Table 5.

As before, panel A classifies homeowners based on undrawn limits as a proportion of mortgage outstanding as of January 2010, and panel B differentiates between borrowers based on their credit scores as of January 2010. We find that the negative effect of |$\it{LTV}$| on labor income and income growth is stronger for individuals with below-median access to liquidity and a below-median credit score.¹⁶ In columns 4–6 of both panels, we examine the heterogeneity in the relation between |$\it{LTV}$| and income for the placebo sample and find no significant effect of |$\it{LTV}$| on income for individuals with different levels of credit constraints.

4.3.2 Heterogeneity by market conditions and noncompete laws

If the negative association between |$\it{LTV}$| and labor income that we uncover is due to constrained mobility, then it should be especially stronger for individuals who reside in areas with fewer alternative job opportunities. Individuals who reside in areas with more job opportunities are more likely to be able to change jobs without changing residence. For such individuals, the negative association should be muted. We evaluate this hypothesis by examining the heterogeneity in the relation between |$\it{LTV}$| and income based on the industry-specific opportunities available in the MSA of the individual’s residence. The intuition behind using industry-specific opportunities is that individuals may find it easier to transition to new jobs within the same industry as they can more easily leverage their skills in such jobs. For instance, an IT professional looking for growth opportunities is more likely to search for opportunities within her sector. Such a professional residing in the San Francisco Bay Area may find it easier to change jobs without changing residence than if she were living in St. Louis.

We measure the industry-specific opportunities available in a region as the ratio of the number of residents of a MSA employed in the specific industry based on three-digit NAICS code to the total number of employed residents in the same MSA as of January 2010. Thus, a higher number indicates that a larger fraction of jobs in that region are from the industry of an individual’s employment. This is likely to indicate the industry specialization of the local area. We differentiate between individuals residing (and working) in MSAs with Above- and Below-median levels of industry-specific jobs and repeat our tests in Table 6. We find that the effect of |$\it{LTV}$| on labor income and income growth is greater for individuals who reside in MSAs with fewer industry-specific jobs.

In a similar vein, if the negative association between |$\it{LTV}$| and labor income is driven by the mobility channel, high |$\it{LTV}$| values should have a stronger effect for individuals who are restricted from accepting other job opportunities in the same or related industry within the region of their residence. We evaluate the merits of this prediction by exploiting the differences in noncompete laws at the state level. Among other things, noncompete laws prohibit employees from working for a competitor within a reasonable geographic area for a set period of time after their employment. Hence, individuals residing in states where noncompete laws are strictly enforced may not be able to take up other nearby job opportunities in the same or related industry as their current job even if such opportunities exist. Consistent with this argument, we find that the effect of |$\it{LTV}$| on labor income is greater for individuals who reside in states with strict noncompete laws as reported in Table IA5.¹⁷

4.4 Home equity and labor income: Wage gains during job change

If high LTV imposes costs when an individual moves residence, then she is likely to move only if she receives an attractive job opportunity that more than compensates for the additional imposed costs. Thus, when we focus on inter-MSA job changes, we expect high LTV individuals to experience a larger wage gain as compared to low LTV individuals. Table 7 presents the results of this test.

For this analysis, we include one observation per inter-MSA job change and exclude individual and within cohort-time effects because there is not enough variation within the same individual or cohort-time. The outcome variable in column 1 is the log change in income at the new job relative to the old job. We find that individuals with LTV between 1 and 1.5 experience 0.9-pp-higher wage growth when they change jobs across MSAs as compared to individuals with LTV between 0.3 and 0.4. We repeat our tests in column 2 with the percentage change in income that accompanies a job change as an outcome variable and find similar results.¹⁸ These results are consistent with individuals with high LTV perceiving a cost to moving across MSAs.

4.5 Home equity and labor income: The debt overhang channel

The debt overhang channel may also contribute to our results. This channel argues that indebted individuals are reluctant to bear the costs of working because they must use their wages to make debt repayments. Hence, these individuals are likely to reduce labor supply and job search efforts (both within and outside their “commuting zone”), which may explain a decline in income for high LTV individuals (e.g., Donaldson, Piacentino, and Thakor 2019). On the other hand, if our results are driven by constrained geographic mobility, high LTV individuals may show greater inclination to search for jobs within their area of residence in order to partially offset the loss of out-of-region opportunities (e.g., Brown, and Matsa 2017).

To distinguish between the two channels, we focus on job changes within the area of individuals’ residences, that is, job changes not involving residential mobility. Specifically, we construct an indicator variable, Job change, that captures job changes in the absence of geographic mobility. This variable is equal to one in month |$t$| if an individual changes employers during that month while continuing to reside in the same address until month |$t$|+6.¹⁹ The change in employer includes both changes to another employer in our sample and to employers not in our sample. In the latter case, the individual would drop out of our sample in month |$t+1$|⁠.²⁰

In Table 8, we evaluate the effect of LTV on Job change for our main sample. In column 1, we find that individuals with |$LTV\in[1,1.5)$| are 0.2 pp more likely to change jobs without moving residence than individuals with |$LTV\in[0.3,0.4)$|⁠. This result is economically significant when compared to the sample mean of Job change of 1.7|$\%$|⁠. Previous results have shown that high LTV especially constrains the mobility of individuals with low access to credit and low levels of liquidity. Therefore, if LTV affects Job change through the mobility channel, then these same individuals should be more affected. We find results consistent with this argument in columns 2 and 3.

High LTV individuals residing in MSAs with greater availability of industry-specific jobs within their industry of employment may find it easier to change jobs within their area of residence. We examine this plausibility in column 4, where we find more pronounced effects of LTV on Job change for those who reside in MSAs with above-median levels of industry-specific jobs. Finally, in column 5, we examine heterogeneity in the relation between LTV and Job change based on enforceability of noncompete laws across states, but we do not find any significant differences.²¹

Our data further allow us to directly test for the debt overhang channel by evaluating changes in labor supply on the intensive margin. Our sample includes both hourly wage workers and salaried workers. We conduct separate tests for these employees to evaluate changes in labor supply. First, for hourly workers, we relate the hours worked with home LTV using our baseline specification. Panel A of Table 9 presents these results where we do not find any significant relation. Second, for salaried workers, we relate the fraction of variable pay to LTV. Under the assumption that labor supply adjustments are more likely to affect variable pay, the debt-overhang hypothesis would predict a decrease in the fraction of variable pay for individuals with high LTV. Here again, we find an insigificant relation between the fraction of variable pay and LTV as reported in panel B of Table 9. If anything, the fraction of variable pay may be larger for very highly leveraged individuals, though the economic magnitudes are small. These tests do not offer support for individuals adjusting their labor supply on the intensive margin in response to high home LTV.²²

4.6 Home equity and labor income: Current job versus job change

Constrained mobility due to high LTV can depress both income from an employee’s current job and the wage gain an employee experiences when changing jobs. The former can happen if constrained mobility reduces employee search effort for alternative employment and, consequently, her bargaining power. The latter can happen due to the constrained opportunity set the employee faces when she searches for a job. For instance, high LTV individuals who are not willing to move will likely look for opportunities within the region of their residence. Given the way we construct our sample, both will contribute to our baseline estimates. In Tables IA11 and IA12, we evaluate the importance of each in turn.

In Table IA11, we evaluate the baseline effect by limiting the sample up until the first month an individual changes jobs. Thus, we do not include any observations from the new job. Within this constrained sample, we repeat our baseline tests and results similar to our baseline estimates. For instance, in column 1, we find that individuals with |$\it{LTV}\in{\rm[1,1.5)}$| earn

351.6 less than the base case (similar to the baseline estimate of

$\$$

352.1). Thus, individuals with high LTV endure a wage discount in their job, which significantly contributes to our baseline estimates.

In Table IA12, we evaluate the extent to which the wage change that accompanies a job change is related to home LTV. For this analysis, we include one observation per job change, and exclude individual and within cohort-time effects because there is not enough variation within the same individual or cohort-time. We find that individuals with high LTV experience lower wage increase when they change jobs relative to the base case. For instance, from column 1, individuals with LTV between 1 and 1.5 experience a 2-pp-lower wage increase when they change jobs as compared to the base case. Thus, constrained mobility adversely affects the wage change the individual experiences when she changes jobs.

Note that the average change in income accompanying a job change is a function of the fraction of job changes with and without a change in residence and the income changes that accompany these. Our results indicate that individuals with high LTV experience fewer inter-MSA job changes (those that are accompanied by a change in residence), experience a higher income gain when they do experience an inter-MSA job change, and experience a lower income gain on average with a job change. These combined indicate that these individuals should experience a smaller income gain with an intra-MSA job change.

5. Robustness

5.1 Sample selection

A potential concern with our analysis is that individuals may drop out of our sample if they stop being employed within the firms covered in the Equifax data. This sample selection may potentially bias our estimates, especially if the probability of attrition from the sample correlates with LTV. We conduct a number of tests to evaluate this potential bias. We begin with Panel A of Figure IA3 that plots the attrition rate in our sample through time. It shows that on average we lose about less than 1|$\%$| of our sample every month, an attrition rate that seems to be relatively constant during our sample period. To evaluate the extent to which our estimates may be driven by this selection, we reestimate our baseline results on a subsample that only includes individuals who we are able to observe throughout our sample period. Table IA13 reports the results for this subsample and we find them to be very similar to our baseline estimates.

The next set of tests examines different characteristics of individuals who drop out of our sample and potential factors that may drive the attrition rate. First, in panels B through D of Figure IA3, we compare the evolution of credit profile of individuals who drop out of our sample at some point (the attrition sample) to that of individuals who remain in our sample (the remain sample). Specifically, we plot average values of credit scores, mortgage debt balances, and nonmortgage debt balances through our sample period for both samples. We find that while credit scores and mortgage balances across the two samples are different during the first half of the sample period, the differences are eliminated during the latter period. Second, we evaluate whether the attrition rate relates to different individual characteristics. Figure 4 reports these results wherein we plot the average probability of attrition in a given month across different levels of age, credit score, total debt, mortgage debt, LTV, and SLTV. We find no systematic patterns between attrition rate and these characteristics, though there seems to be some differences across individuals with different SLTV buckets.

Finally and most crucially, we test to determine whether the probability of attrition is related to LTV using our baseline specification. Table 10 reports these results where we find no significant relation between our LTV buckets and the probability of attrition. Further, the last panel of Figure 4 shows a similar nonsignificant relation between LTV buckets and attrition rate with more granular LTV buckets. Overall, these results indicate that sample selection is unlikely to significantly bias our results.

5.2 Measurement and misclassification error problem

Since we do not observe the house price at the time of mortgage origination, our origination LTV could be different from the actual LTV at origination. Hence, the difference between actual and assumed down payments (⁠|$\%$|⁠) will drive a wedge between the LTV we calculate and the actual LTV. In addition, individual house prices can change at a faster or slower rate than the ZIP-code-level house prices. The measurement error induced by these factors may potentially bias our estimates, but a number of factors help assuage these concerns. First, our use of multidimensional fixed effects will help control for some sources of this measurement error. For example, the cohort- specific time effects we include will control for the tendency of individuals within specific purchase cohorts to put down more or less down payment. Second, the insignificant estimates from our placebo analysis suggests that the measurement error is unlikely to affect our estimates. If the measurement error was correlated with income trends for individuals within the main sample, one would also expect it to be correlated with income trends for renters. This is because both groups of individuals are subject to similar economic conditions since they are of the same age, reside in the same ZIP code, and are employed at the same firm with similar tenure. Third, our use of nonparametric piecewise function instead of a linear function of LTV helps minimize the effect of noise in our LTV. For instance, if the true LTV is 1.26, while our imputed LTV is 1.15, this will not induce an error in our estimation because we will correctly assign the homeowner to the [1,1.5) bucket. This noise may, however, lead to misclassification errors if we assign individuals to incorrect LTV buckets (e.g., Schulhofer-Wohl 2012).

Notwithstanding these arguments, we perform a number of tests to ensure that this measurement problem and the resultant misclassification do not drive our results. We begin by evaluating how our LTV measure compares to two different LTV distributions reported in Gerardi et al. (2018), which are based on actual origination LTV values. The first LTV distribution is constructed using a sample of active, owner-occupied, first-lien mortgages that are not in foreclosure.²³ We call this distribution CRISM 1. The second LTV distribution is constructed using a more restricted sample of single-family, prime-age (homeowner ages 24 to 65) mortgages with LTV ratios below 2.5 and positive mortgage balances.²⁴ We call this distribution CRISM 2. The sample requirements used in our paper are more similar to those used to construct CRISM 2 than CRISM 1. Table IA14 compares the percentage of our sample that belongs to different LTV buckets to the percentage of CRISM samples belonging to the same buckets for the years 2011 and 2013.²⁵ Overall, our sample LTV distribution matches the CRISM 2 distribution well. Although our LTV distribution contains a slightly greater (lower) proportion of mortgages in the “low” (“high”) LTV group during both years, the magnitude of these differences is economically small. For example, in 2013, 65.4|$\%$| (7.3|$\%$|⁠) of our sample belongs to the “low” (“high”) LTV group, while 62.2|$\%$| (7.5|$\%$|⁠) of the CRISM 2 sample belongs to the “low” (“high”) LTV group. The time trends in our LTV distribution also match the time trends in the CRISM 2 distribution well. For example, the proportion of mortgages in our sample that belongs to the “low” (“high”) LTV group increases (decreases) from 47.5|$\%$| to 65.4|$\%$| (18.3|$\%$| to 7.3|$\%$|⁠) between 2011 and 2013. For the CRISM 2 sample, this proportion increases (decreases) from 45.1|$\%$| to 62.2|$\%$| (21.7|$\%$| to 7.5|$\%$|⁠) over the same period.

We also conduct a number of tests where we repeat our baseline analysis using specifications where misclassification is likely to play a smaller role. First, we reestimate our baseline test by dropping the observations that are close to the cutoffs for our bins. Specifically, for all cutoff points, we drop observations with |$LTV\in[c-0.02,c+0.02]$|⁠, where |$c$| is the cutoff value. For example, for the bin that identifies observations with |$LTV\in[0.8,1)$|⁠, we drop observations with |$LTV\in[0.78,0.82]$| and |$LTV\in[0.98,1.02]$|⁠. To the extent misclassification is more likely to occur around the cutoffs, dropping observations near the cutoff will reduce the error. Table 11 reports results for these tests where we find similar results to our baseline. Second, we reestimate our analysis by including only one dummy variable as the independent variable. This dummy identifies observations with |$LTV>0.8$| (i.e., we split the sample into only two bins). This will reduce the misclassification as it is likely to occur around only one cutoff point of 0.8. Finally, we reestimate our analysis using a combination of the above two tests, meaning we employ one dummy variable that identifies observations with |$LTV>0.8$| and drop observations on the neighborhood of the cutoff (i.e., those with |$LTV\in[0.7,0.9]$|⁠). Table IA15 reports results for these tests with only one dummy as the independent variable. Panel A estimates our results for the entire sample, and panel B drops observations with |$LTV\in[0.7,0.9]$|⁠. Across both samples, we find estimates consistent with our baseline.

Finally, we conduct additional robustness tests to ensure that our results are not unduly influenced by the assumptions we make about the origination LTV. In panel A of Table IA16, we repeat our estimates by assuming that the origination LTV is alternatively 0.75 and 0.85 for individuals who originate one mortgage during a month. In the case of multiple mortgage originations, we continue to assume that the LTV of the larger mortgage is 0.8. We find our results to be unaffected.

In panel B of Table IA16, we recalculate LTV at origination using ZIP-code-level median house price. We obtain information on ZIP-code-level median house price from the Corelogic data set, which tracks the transactions that occur at a given ZIP code in a month and reports the median sales price. To minimize the error in this calculation, we restrict the sample to the most homogeneous ZIP codes, that is, those where the standard deviation in transaction prices is in the bottom decile. Since an overwhelming majority of the mortgages in our sample were originated during the 2001 through 2006 period, we evaluate historical price deviations at the ZIP code level using data from the period between 1990 and 2000. We find our results to be unaffected by this change.²⁶

Overall, these results suggest that the measurement error, if any, and the resultant potential misclassification are unlikely to have a significant effect on our estimates.

5.3 Instrument construction and alternative instrument

To ensure that our results are not sensitive to our choice of interest rate and loan maturity that we employ to construct our instrument, we repeat our estimation with alternative assumptions. First, we use a time-varying interest rate based on the national average interest rate on all mortgages issued during the month of origination instead of a constant interest rate for all mortgages in our sample. Second, we use interest rates and loan maturities that vary by region and time; that is, we use state-level averages for these variables for the month of mortgage origination.²⁷ Panels A and B of Table IA19 report the results that we find are similar to our baseline estimates.

In addition, we also use an alternative instrument from Bernstein, and Struyven (2016) and follow their specification to verify our results. This instrument constructs synthetic LTV (i.e., SLTV) that is only a function of house price change since origination and keeps the loan outstanding constant during the sample period. Specifically, the only difference between our instrument and their instrument is that they assume no amortization on the loans. Table IA20 reports results for this specification, where panel A reports the first stage, and panel B reports the IV estimates. As before, we find results consistent with our baseline estimates.

5.4 Unobserved economic conditions

The biggest threats to our identification are potential unobserved local economic shocks that are correlated with both ZIP-code-level house price changes and the purchase cohort. For example, industry-level shocks that differentially affect older and newer cohorts residing within the same ZIP code may bias our estimate. While our parallel analysis with the subsample of renters is designed to overcome this concern,²⁸ we additionally repeat our estimates after including within-ZIP-code industry-time effects. This further helps rule out localized industry-specific shocks. Table IA21 reports the results of this analysis that we find are similar to our baseline estimates. In addition, as mentioned before, Table IA3 reports additional results of tests that control for regional shocks. Overall, these results lend support to our exclusion restriction and suggest that specific regional shocks are unlikely to drive our estimates.

6. Economic Implication

In this section, we quantify the economic implication of our estimates. To do this, we use our estimates from Table 3 and the distribution of LTVs in our sample. Our estimates imply that a 1|$\%$| fall in nationwide average house price will result in a 0.1|$\%$| decline in monthly wages. This happens because of an increase in the proportion of individuals with high LTVs. This effect is significant, especially given that annual house prices fall by more than 13|$\%$| in over 5|$\%$| of the ZIP-code-years in our sample (see Figure IA2). This implies that house price changes can lead to a 1.3|$\%$| decline in monthly wages in over 5|$\%$| of our sample ZIP-code-years. Another way to contextualize these estimates is to consider that from January 2007 to December 2010, average U.S. house prices declined by 23.03|$\%$|⁠.²⁹ Our estimates imply that such a decline could result in a 2.3|$\%$| decline in wages due to constrained mobility.

We can also quantify our estimates in terms of the aggregate loss in total wages due to constrained mobility. Assuming that the distribution of LTV among all individuals with an open mortgage in the credit data is the same as the distribution of LTV in our sample, our estimates imply an aggregate loss of

452.27 billion in wages over our 6-year sample period due to high LTV constraining mobility.³⁰

7. Conclusion

This paper uses detailed credit and employment data for millions of individuals in the United States to estimate the effect of home equity on labor income and explore the mechanisms through which this effect operates. We document a strong negative relation between LTV of an individual’s primary residence and income for a sample of employed individuals. As compared to individuals with LTV between 0.3 and 0.4, individuals with LTV between 1 and 1.5 earn

352.1 (5.1|$\%$|⁠) less per month and experience slower income growth. We also document a negative relation between LTV and labor mobility, especially among liquidity- and credit-constrained individuals.

Consistent with constrained mobility affecting labor income, we find that high LTV individuals who are liquidity- and credit-constrained experience greater declines in income. However, high LTV individuals residing in MSAs with greater employment opportunities and in regions with lax noncompete law enforcement experience relatively smaller income declines. This is because they are able to move jobs without changing their residence to partially offset the loss of out-of-region opportunities.

Given the house price declines during the Great Recession, our estimates imply a 2.3|$\%$| decline in monthly wages due to constrained mobility. Our results will help policy makers identify the geographies and the subpopulations that will be most constrained by low home equity. This can be used to design targeted policy interventions. Our results are also of relevance to firms interested in hiring and developing human talent as they show that credit constraints may affect an employee’s willingness to move to take advantage of job opportunities. If firms can relax such constraints, doing so could enhance labor mobility and, consequently, productivity.

Authors have furnished an Internet Appendix, which is available on the Oxford University Press Web site next to the link to the final published paper online

Acknowledgement

For helpful comments, we thank Sumit Agarwal, Stephanie Cummings, Andreas Fuster, Naser Hamdi, Matt Notowidigdo, Nagpurnanand R. Prabhala, Felipe Severino, and Toni Whited and conference and seminar participants at the SFS Calvacade 2017, AFA Philadelphia 2018, Emory University, Georgia State University, Purdue University, University of Michigan, University of Texas-Dallas, and Washington University. We thank the Wells Fargo Center for Finance and Accounting Research, the Center for Research in Economics and Strategy, and the Olin Business School for financial support. This paper represents the views of the authors only and not of Equifax Inc. We are deeply grateful to Equifax Inc. for supporting the research and allowing us access to their data. Supplementary data can be found on The Review of Financial Studies web site.

Footnotes

References