Draft midway through revision. Please do not circulate.
Housing Wealth and Retirement Timing
by
Martin Farnham*
Department of Economics
University of Victoria
Victoria, BC, V8W 2Y2
E-mail: mfarnham@uvic.ca
Purvi Sevak
Department of Economics
Hunter College
695 Park Avenue
New York, NY 10021
Email: psevak@hunter.cuny.edu
Abstract
Labor-supply effects of changes in house value are potentially important but under-studied.
Using the panel Health and Retirement Study merged to local house prices from the US Federal
Housing Finance Agency, we estimate the effect of house-price changes on actual and planned
retirement timing. We find no effect of house-price changes on the annual probability of retiring.
We also examine the effect of changes in house prices on the evolution of individuals’
expectations of retirement timing in a rational expectations framework. In this framework as
well, we find no evidence that house prices affect retirement timing. We find, as in previous
findings, that the evolution of retirement expectations is consistent with the rational expectations
hypothesis.
Keywords: retirement, wealth effect, housing, house prices
JEL codes: D12, E21, J26, R31
*
Corresponding author. We are grateful to the Michigan Retirement Research Center for helping to fund this
research. Martin Farnham gratefully acknowledges research funding from the Social Sciences and Humanities
Research Council. We would like to thank Jed DeVaro, Lucie Schmidt, Erik Hurst, Enrico Moretti, Herb Schuetze,
participants in the Michigan Retirement Research Center workshop, and members of the economics seminars at
University of Victoria and the CUNY Graduate Center for helpful comments. All errors are the authors’.
I. Introduction
According to the Case-Shiller House Price Index, house prices in the United States more
than doubled in real terms between 1997 and 2006.1 By the fourth quarter of 2010, the same
index had fallen more than 40% from its peak in real terms. Housing constitutes a large fraction
of the assets of the typical American family, and the effect of changes in housing wealth on
consumption of goods and services has received substantial consideration in the economics
literature. By contrast, relatively little attention has been paid to the effect of changes in housing
wealth on the consumption of leisure.
In this paper we use a quasi-experimental approach to measure the effect of housing
capital gains on labor supply. More specifically, we investigate whether changes in house prices
alter individual homeowners’ actual timing of retirement and their expected timing of retirement.
We identify the effect of capital gains on retirement transitions and expectations using variation
in house prices across metropolitan statistical areas (MSAs) and over time. We also use renters
as a quasi-control group. We match 16 years of panel data from the Health and Retirement Study
(HRS) to MSA-level data on local house price fluctuations from the US Federal Housing Finance
Agency2 (FHFA). We first estimate models of annual transitions into retirement and, consistent
with current findings in the literature (Coile and Levine, 2011) find no effect of housing capital
gains on the annual probability of retiring. Then, using time-varying data on individual
expectations of retirement timing which allows us to better control for unobserved individuallevel heterogeneity, we find that house-price increases have no statistically significant effect on
the evolution of retirement expectations.
1
2
Our calculations are based on the Case-Shiller Home Price Index deflated by CPI-U.
Formerly the Office of Federal Housing Enterprise Oversight.
1
A substantial number of papers attempt to estimate the marginal propensity to consume
goods and services out of changes in housing wealth (e.g. Bhatia, 1987; Engelhardt, 1996;
Skinner, 1996; Disney, et al., 2003; Belsky and Prakken, 2004; Lehnart, 2004; Case, et al., 2005;
Juster, et al., 2006; Morris, 2006; and Bostic, et al., 2009). Most of these papers find a marginal
propensity to consume out of housing wealth that is statistically significant and in the
neighborhood of 0.06, though findings vary.
A related literature finds that individuals adjust their retirement age in response to
changes in income or non-housing wealth. Such papers have identified wealth effects on
retirement timing using unexpected changes in Social Security benefits (e.g. Hurd and Boskin,
1984; Burtless, 1986; Krueger and Pishke, 1992), lottery winnings (Imbens, et al., 2001),
inheritances (Holtz-Eakin, et al., 1993; Goodstein, 2008), and unexpected stock market gains
(Coronado and Perozek, 2001; Hurd and Reti, 2001; Sevak, 2005). In most cases, these studies
find evidence of economically significant wealth effects on retirement timing.
Given 1) the magnitude of changes in house prices over recent years; 2) evidence of
housing wealth effects on consumption of goods and services; 3) evidence of non-housing wealth
effects on labor supply; and 4) the possibility that individuals respond differently to changes in
housing wealth than to changes in other forms of wealth (discussed further in Section II); the
question of whether housing capital gains affect labor supply is worth considering. Yet relatively
little empirical work has been done on this question. Coile and Levine (2009) consider the effect
of changes in local house prices using data from the March Current Population Survey (CPS)
over a 30-year period. They generally find no effect of house price increases on retirement
timing. Goodstein (2008) finds that a $20,000 increase in housing wealth lowers the labor force
participation rate of older men by about 1 percentage point, using data from the HRS.
2
Our analysis parallels this new literature in a number of ways. We roughly replicate Coile
and Levine (2009) using a different sample of older workers (HRS instead of CPS). Our
estimates confirm the Coile and Levine estimates that the annual probability of retirement is
statistically unaffected by housing capital gains at conventional significance levels. Our analysis
is closer to Goodstein in our use of MSA-level variation in the house price variable. But, similar
to Coile and Levine, we use renters as a quasi-control group.
However, we diverge significantly from the existing literature by extending our analysis
to exploit biennial data in the HRS on self-reported expected retirement age. This approach
complements—and in some cases provides advantages over—the existing literature in a number
of ways. First, retirement is measured with substantial error,3 and estimates with retirement as a
left-hand-side variable are likely to be of high variance as a result. Second, it is difficult to
identify, a priori, the relevant time frame in which actual retirements should respond to changes
in house prices. Coile and Levine give findings for specifications using one-year and five-year
changes in house prices. Goodstein uses 10-year changes. Since retirement may require
substantial planning, actual retirements may respond with long and variable lags to changes in
house prices. By contrast, expectations of retirement age can respond quickly to changes in
house prices. By focusing on the effect of house price changes on expectations we can forgo
having to choose between arbitrary judgments of appropriate lag structure and atheoretic
specification searches. Third, and most importantly, lagged expectations can serve as a sufficient
statistic for a wide range of individual-level characteristics unobservable to the econometrician.
As a result, our estimates of the effect of house prices on retirement timing are less likely to be
For example, individuals in the HRS frequently report being retired while working the same job they had in
the previous survey wave when they reported being not retired; many report being newly retired while
showing no decline in weekly hours worked from the previous survey, and many shift back and forth between
reporting being retired and not being retired.
3
3
subject to bias using this approach. Thus our use of expectations data allows us to shed new light
on the relationship between housing capital gains and retirement timing.
II. Theoretical Issues
Several studies noted above measure the effect of financial wealth windfalls on labor
supply. However it would be misguided to simply infer the effect of housing capital gains on
retirement expectations based on studies of financial wealth. One dollar of capital gain on
housing will likely have a different effect on consumer behavior than one dollar of capital gain
on most other assets for at least two reasons.
First, as housing prices rise, the user cost of housing faced by a household rises as well.
This means that future household liabilities rise at the same time that the value of the
household’s home rises. Dougherty and Van Order (1982) note that if individuals were infinitely
lived and planned to stay in their current home, housing capital gains would have no effect on
household wealth. This is because household assets and liabilities would rise by equal amounts
and hence cause no wealth effect on consumption. However, as others have noted (e.g. Skinner,
1989; Morris, 2006), finitely-lived households who experience housing capital gains experience
real wealth gains as a result. While that increase in household wealth is generally smaller than
the housing capital gain, due to the increased user cost of housing associated with higher house
values, Morris (2006) notes that the marginal propensity to consume out of housing capital gains
should increase in age and in the probability of a future move into less expensive housing (either
by trading down or by migrating to cheaper housing markets).4 5 This suggests that housing
In 1992, 26% of HRS respondents reported a 50% or higher chance that they would move in the next two
years. Among households who said there was some chance they would move, 28% thought they would move
to another state.
4
4
capital gains may matter to consumption (including consumption of leisure) of households
approaching retirement age.
Second, housing is a relatively illiquid asset. So while standard lifecycle consumption
theory predicts that permanent, unanticipated shocks to wealth should result in adjustment of
consumption of goods and services as well as leisure, there may be liquidity constraints limiting
adjustment when housing wealth increases. Venti and Wise (2004) note that elderly households
are slow to consume housing wealth. However, there are a number of ways in which households
may adjust their consumption without selling their home. Skinner (1996) notes that households
who save for precautionary reasons may view housing capital gains as helping them meet their
precautionary savings goal. Similarly, households that were targeting certain bequest levels may
be able to increase consumption if bequest targets are met sooner than expected due to housing
wealth gains. If this is the case, housing capital gains may allow people to increase consumption
with no need to sell their home or formally borrow against its equity.
Of course, individuals may access increased housing wealth through financial products
such as home equity loans and lines of credit, or reverse mortgages. They may also access this
wealth through informal borrowing markets. For instance, an elderly couple that intends to
bequeath their home to their children may receive financial assistance from their children in
exchange. The amount of this assistance may increase when the children observe that the home
to be bequeathed has increased in value.6 Of course, if these borrowing or precautionary saving
Empirical evidence on this claim is mixed. For instance, Skinner (1996) finds a greater propensity to
consume out of housing capital gains among younger households. Lehnert (2004) finds the marginal
propensity to consume out of housing gains to be non-monotonic in age but high among households
approaching retirement. Bostic, et al. (2009) and Morris (2006) find a greater marginal propensity to
consume out of housing gains among older households.
6 This is more likely to be true in instances where the children live in different real estate markets from their
parents.
5
5
mechanisms are absent, then changes in house value may have little to no impact on
consumption behavior, including consumption of leisure.7
Given the differences between housing capital gains and other financial windfalls that
households may experience, the presence and extent of housing wealth effects on retirement
timing remains an empirical question. While a number of studies have tested for the effect of
housing capital gains on the consumption of goods and services, little work has been done to
ascertain the effect of housing gains on the consumption of leisure.
III. Empirical Challenges, Responses, and Data
There are a number of challenges to measuring the effect of housing capital gains on
retirement timing, many of which relate to potential endogeneity of housing wealth. In this
section we describe these challenges and note methods we use to address them.
First, estimating causal effects of wealth changes is made difficult by the fact that some
variation in individual household wealth reflects individual heterogeneity in preferences that is
likely correlated with labor supply and saving decisions. In the context of retirement behavior,
high levels of individual housing wealth could cause early retirement, or plans to retire early
could cause high individual levels of wealth. All else equal, one individual who plans to retire
sooner than another individual will save more during her working years, because she will have
more years in retirement during which she must live off of her accumulated wealth.
Alternatively, wealthy individuals may have a strong taste for work and thus retire later.
Therefore, estimates of the effect of individual housing wealth on retirement timing could be
biased in either direction.
Thaler (1990) gives a third reason why households may respond differently to changes in different types of
wealth. He argues that households may view their wealth as existing in distinct “mental accounts” (for
instance housing wealth, stock holdings, and cash holdings). If households view these wealth types as nonfungible, identical windfall gains in different wealth types may generate different consumption responses.
7
6
Second, self-reported data on house values, while providing variation in wealth at the
individual level, are subject to classical measurement error. This will lead to attenuation of the
estimates of the effect of housing capital gains on retirement timing. Initial work with the HRS
data on self-reported house value suggests that substantial measurement error exists. And, as is
often the case with measurement error, it is particularly problematic when considering changes in
house value over time. An extensive discussion of mismeasurement in self-reported data on
house values can be found in Engelhardt (2003).
To address these first two issues, we use data on house values rather than data on home
equity, which is subject to active management by individuals. Furthermore, we use FHFA house
price indices (HPI) to proxy for changes in individual house values. In addition to lessening the
measurement error problem associated with self-reported house values, use of the MSA-level
data means that we do not need to account for additions or improvements that individuals have
made to their homes which would cause house prices to be endogenous.8 We further address the
issue of individual heterogeneity by using lagged retirement expectations in specifications that
model current retirement expectations.
Third, housing prices may be correlated with local labor market conditions. Local home
values may reflect current or future labor market opportunities, which may also be correlated
with retirement timing. If older individuals delay retirement in the face of high wages and if high
wages are positively capitalized into local house values, then failure to control for local labor
market conditions may lead to downward bias in estimates of the effect of housing capital gains
on retirement timing. As a result, in the specifications reported below we control for the worker’s
wage and for the local (county-level) unemployment rate in the current year. This further
8
Improvements may affect the HPI data, but the effect of improvements in the HPI is unlikely to be correlated with
unobservable individual characteristics of HRS respondents.
7
addresses concerns about the potential endogeneity of the housing wealth measure used in our
specifications.
Fourth, changes in housing prices may be correlated with changes over time in
unobserved local amenities that also affect an individual’s retirement timing decision. By
including renters—who should not respond to housing wealth effects—as a comparison group,
we will, under certain assumptions, be able to difference out the change in retirement timing that
is due to unobserved changes in local amenities capitalized into local housing values. Under
these assumptions, the difference between the responses of owners and renters to changes in
local housing prices can be interpreted as an effect of housing capital gains on retirement timing
that is purged of bias due to unobserved, time-varying heterogeneity in local amenities. This
method can also help to control for time-varying labor market conditions inadequately controlled
for in our specifications. The use of renters as a quasi-control group is yet another way that we
address concerns about the potential endogeneity of the housing wealth measure used in our
specifications. We discuss the merits of this difference-in-differences strategy further below.
In order to examine the effect of changes in house value on the retirement timing of older
individuals, we assemble a dataset based on observations on individual workers from the Health
and Retirement Study (HRS) for the years 1992 to 2008. The HRS is a nationally representative
panel of individuals near retirement age.9 The survey codes geographic identifiers in each wave
that allow matching to local-level data on house prices and local labor markets that we use in our
analysis.10
A baseline set of 7,650 randomly selected households with a member born between 1951
and 1961 was interviewed in 1992. Every two years, the HRS attempts to re-interview the
Detailed information on the HRS data is available at http://hrsonline.isr.umich.edu/data/index.html.
Geographic identifiers are available only through Institutional Review Board approved restricted access.
More information is available at http://hrsonline.isr.umich.edu/rda/
9
10
8
members of this household. If a subject refuses to conduct an interview or is unreachable in one
wave, the HRS continues to interview him in subsequent waves. 11 In each interview year,
respondents answer detailed questions about current and past labor supply, health, and other
topics. A designated “financial respondent” in each household provides detailed financial
information on the household. This includes values of various assets, including housing, real
estate, stocks, bonds, checking and savings accounts, individual retirement accounts (IRAs),
small businesses, and pensions. Since assets are reported at the household level and cannot be
attributed to one particular spouse, we measure wealth at the household level and assume that
households pool their resources.
We merge two sets of external data to the HRS panel. First, we use annual county-level
unemployment data from the Bureau of Labor Statistics (BLS) to control for local labor market
conditions, which may affect retirement timing and be correlated with local housing values.
Second, we merge data on local house prices from the Office of Federal Housing Enterprise
Oversight (FHFA). FHFA calculates quarterly house price indices (HPI) using data on repeat
sales of single-family homes. These data are provided to FHFA by Freddie Mac and Fannie Mae
and are based on sales of homes with standard mortgages. The HPI is a weighted average, across
actual houses, of changes in house prices. Because it relies on repeat sales, it is a “constant
quality” index. It avoids most problems of a changing quality of housing stock that occur when
one looks just at average sales prices of homes over time.12
We merge the FHFA HPI to HRS households based on the state and county the
household lives in at the time of the interview. The HPI is available at both the MSA level and
We linearly interpolate values when a respondent has missed an interview for one wave but has completed
interviews for the waves before and after it.
12 The FHFA methodology is a modified version of the weighted-repeat sales methodology originally
proposed by Case and Schiller (1989). A full technical description of the HPI is available at
http://www.FHFA.gov/Media/Archive/house/hpi_tech.pdf.
11
9
the state level, so for households that live in counties that are in MSAs, our measure of changes
in house values is quite local. For non-MSA dwellers, we must rely on state-level changes in
house value. Though we do not rely on self-reported data to calculate changes in house value, we
do use the household’s self-reported 1992 level of housing equity as a baseline wealth control in
some of the specifications discussed below. Since the HRS tracks moves by households, we are
able to assign to movers in our sample cumulative housing wealth gains across prior locations as
well as in the current location.
This time span of our analysis sample (1992-2008) encompasses a diverse array of real
estate market experiences across geography and over time. In Figures 2 and 3 we divide the 9 US
Census regions into West and East, respectively, and plot year-over-year growth in the FHFA
house price index for each census region. Growth rates vary dramatically over time and across
regions. At the MSA level, such variation is even greater.
IV. Two Empirical Models
Modeling the annual probability of retirement
The first specification we use in our analysis is a linear probability model of entry into
retirement, and it will serve to replicate the approach of Coile and Levine (2009). For this basic
specification, we use the following model of entry into retirement:
(1)
'
Ditretire  X it'   Wi,1992
  HPIi,t  uit
Dretire is a dummy variable equal to 1 if individual i retires at time t and equal to zero
 otherwise. X is a vector including control variables and a constant term. W is a vector of baseline
household wealth variables in real (year 2000) values. Measures of baseline household wealth
include home equity, business wealth, defined-contribution pension wealth, and other wealth in
1992. HPI, the variable of primary interest, denotes change in housing wealth. It is measured as
10
the one-year or five-year change in the FHFA house price index corresponding to the
individual’s MSA (or state if they live outside of an MSA). We denote changes in local house
values in percentage terms. 1314
Controls—contained in X—in our first specification include years of education, lagged
log wage,15 the county-level unemployment rate and dummy variables denoting age, race,
marital status, and an indicator of poor health. We control for whether the individual is covered
by a defined contribution or defined benefit pension plan and whether the individual has health
insurance that will cover them in retirement. Finally, we include year and state fixed effects. 16
Estimates of this model are obtained by OLS. Since the HRS is conducted every two
years but transitions can occur annually and data on house prices are annual, we annualize the
dataset for this analysis by linearly interpolating values of biennial covariates. We pool
observations from 1993 to 2004. This sample is comprised of male workers who are non-selfemployed, and who have not previously retired by time t-1. Thus, we only observe the first entry
into retirement in our sample. We define a worker as retired if he considers himself either
partially or fully retired. We refer to this sample as Sample A, and its construction is outlined in
the first panel of Table 1. Standard errors are clustered at the MSA level to account for the fact
that we have multiple observations on individuals using the same MSA-level measure of houseThe HPI is an index and so does not allow us to measure changes in house prices in dollar terms. To be
precise, a 5% change in housing wealth would be denoted as “5” in the data.
14 Coile and Levine (2009) also use a linear probability model and the percent change in the FHFA HPI.
15 We include log wage with a lag, because wage data are not collected in the survey wave when an individual
retires. Because we use lagged wage, our analysis may not completely control for wage at the time
expectations are formed. In other results, not shown here, we estimate the same model excluding
observations from the period of retirement. This allows us to use current log wage instead of lagged.
Quantitative results change very little.
16 Using the HRS permits us to use a somewhat richer set of controls than Coile and Levine (2009), who use
the CPS. We do not include a control for whether a child under age 18 is present in the home, as they do.
Otherwise, we use the same controls as they do plus controls for DC and DB pensions, whether the
individual’s employer offers health insurance to retirees, whether the individual is in poor health, the lagged
log wage of the individual, and various baseline wealth controls in 1992. In other specifications we include
changes in non-housing wealth and industry and occupation dummies. Results are not substantially affected.
13
11
price change. Results from this specification using the one- and five-year percent change in
house prices are given in Table 4. 17 Results are discussed in Section V.
As noted above, specifications that model the annual probability of retirement pose
certain challenges. Difficulty controlling for individual unobserved heterogeneity and right
censoring may all make it difficult to empirically discern an effect of housing capital gains on
retirement timing, if one is present. Furthermore, effects on actual retirement likely follow from
house-price changes with long and variable lags, which poses challenges for specification choice.
As a result, our remaining specifications exploit data on retirement expectations, which can
respond immediately to changes in house prices and which allow for better strategies to control
for unobserved heterogeneity.
Modeling expected age of retirement
Our second approach to measuring the effect of house price changes on retirement timing
focuses on expected retirement age and its response to changes in house value. Bernheim (1989),
Disney and Tanner (1999), Loughran, et al. (2001), and Haider and Stephens (2007) find
retirement expectations to be strong predictors of the actual transition into retirement. Testing for
the effect of house-price changes on retirement expectations provides some advantages over
testing for the effect of house-price changes on retirement realizations. Contrary to actual
retirements, which require time to plan, a worker’s expected retirement age can immediately
incorporate recent changes in house values. In addition, data on retirement expectations allow us
to observe responses to house-price changes before actual retirement occurs. This eliminates the
problem of right censoring that occurs with individuals in our sample whose future retirement
(beyond the sample frame) may, in fact, be affected by house-price changes, but whose
17
Results from alternative nonlinear specifications are quantitatively similar.
12
retirement we never observe. This right censoring could be expected to lead to downward bias in
estimates of the effect of housing capital gains on actual retirement transitions. Finally, in the
specification we use, lagged retirement expectations serve as a sufficient statistic for the levels of
a wide variety of covariates—both observable and unobservable—at the start of each period of
observation. Thus, we are more easily able to control for unobserved individual-level
heterogeneity than in our model of retirement realizations.
We follow the approach of Benítez-Silva and Dwyer (2005), who model current
retirement expectations as a function of lagged expectations and changes in health, demographic,
and economic variables since the last recorded retirement expectations.18 Their approach, in turn,
derives from Bernheim (1990) who studied expectations formation in a retirement context.
Benítez-Silva and Dwyer propose testing the rational expectations hypothesis by
estimating
(2)
Xt,ie    Xte1,i  t,i  t,i ,
where X t,ie denotes expected retirement age at time t of individual i; X te1,i denotes the lagged

expected retirement age;  is a vector denoting new information that arrives between t-1 and t;
 and  denotes an iid error term. Under the rational expectations
 hypothesis, the coefficient 
should equal zero and the coefficient  should equal 1. Under perfect foresight, values of  are
perfectly anticipated and thus already built into X te1,i . Therefore, under a strong, perfect foresight
version of rational expectations, all elements of  will equal zero. Without perfect foresight,
 as individuals revise expectations in response to the
elements of  will take on non-zero values
new information. Notice that while changes in key covariates between t-1 and t are included in
18
Benítez-Silva and Dwyer consider the effect of changes in net worth on retirement timing
(they find no effect), but do not separately consider the effect of changes in housing wealth.
13
equation (2), levels of key covariates are not included. This is because levels—at time t-1—of
determinants of one’s retirement age should be fully incorporated into the expected retirement
age at t-1. Benítez-Silva and Dwyer confirm this assumption empirically.
Measurement error complicates estimation of Equation 2.19 In the HRS, some
respondents report an expected year of retirement rather than an expected age. Because a
calendar year spans two different ages for any individual not born on January 1, expected
retirement age imputed from expected retirement year will tend to be measured with error. To
correct for measurement error, Benítez-Silva and Dwyer instrument for expected retirement age
using subjective survival probabilities to age 85 at time t-1 and an indicator for whether the
person is a smoker. We follow a similar approach. However, because the HRS stopped asking
respondents to report subjective survival probabilities to age 85 in the 2000 survey wave, and
because our data extend through 2008, we substitute subjective survival probabilities to age 75
into the instrument set. For a more detailed discussion of the empirical approach see BenítezSilva and Dwyer (2005).
Unlike Benítez-Silva and Dwyer, we are not interested in testing the rational expectations
hypothesis. However the empirical framework implied by that hypothesis provides a useful
setting in which to test whether individuals’ retirement expectations respond to news about
house-price changes. In particular we are interested in whether the estimate of the coefficient on
the percent change in the local FHFA House Price Index, hp, is negative. This would suggest
that increases in local house prices cause individuals to revise down their expected retirement.
As with our analysis of retirement realizations, we employ a specification that interacts a dummy
19
Sample selection could also complicate estimation, though we test for sample selection and do not find evidence
of it.
14
variable indicating homeownership with the percent change in HPI. This allows us to use renters
as a quasi-control group in the analysis.
In addition to the percent change in the individual’s local HPI, the vector  contains
variables that control for changes in other variables that may affect retirement timing. These
include changes in household income, financial wealth, business wealth, and health. Controls for
local labor market conditions, which one would expect to be correlated with local house prices,
include changes in the individual’s weekly wage and changes in the local unemployment rate.
To facilitate comparison with Benítez-Silva and Dwyer, we use similar criteria for
choosing our sample, though our sample spans a longer time period during which new, younger
cohorts were added to the overall HRS sample. We include both male and female respondents
who report working or searching for work and who report an expected retirement age.20 We
exclude respondents who fail to report retirement expectations for two survey waves in a row.
We also exclude respondents who report not having thought much about retirement. We assign
an expected retirement age of 77 (average longevity) to individuals who report planning never to
retire. Table 1 illustrates the sample selection for this analysis. Tables 6-7 gives estimates of
Equation 2 for different specifications and subsamples. We discuss these results in Section V.
V. Results
Table 4 gives estimates of equation (1), the linear probability model of annual retirement
transitions. A similar model is estimated by Coile and Levine (2009) and so our estimation of
equation (1) serves to replicate their approach using a richer dataset.21 A comparison of our
Table 4 with Coile and Levine’s Table 4 demonstrates that our findings for this specification are
20
21
We provide separate estimates for a sub-sample of male workers.
As noted above our specification contains a larger set of controls than that of Coile and Levine (2009).
15
broadly similar to theirs. We find no statistically significant effect of local house price change on
annual probability of retirement, even using renters as a control group.22
A glance at coefficient estimates on covariates in Table 4 suggests that having a defined
benefit pension, having retiree health benefits, being in poor health, and having a high level of
home equity in 1992 are all associated with higher probabilities of retirement. Being Hispanic,
being black, or being married are associated with lower probabilities of retirement, depending on
whether measures of 1-year or 5-year change in the local house price index are used as the key
independent variable.
Results for our second empirical specification, which models the effect of house-price
changes on expected retirement age, are given in Tables 5 and 6. Column 1 of Table 5 gives
estimates for a specification of Equation (2) estimated by OLS. The null hypothesis of rational
expectations is clearly rejected in this set of estimates. The coefficient estimate for the
constant—zero, under the null hypothesis—is statistically greater than zero at conventional
significance levels. The estimate of the coefficient on last-period expected retirement age—one,
under the null hypothesis—is statistically smaller than one at conventional significance levels.
The results suggest either that individuals’ expectations evolve in a decidedly non-rational way,
or that the model is misspecified. As noted above, measurement error is likely to be present in
the measures of expected retirement age. This warrants use of the instrumental variables
approach described above. Table 5, Column 2 gives estimates for an IV specification that
instruments for expected retirement age using individual’s subjective probability of living to age
75 and whether the individual is a smoker. Both of these instruments, at time t-1, should be
correlated with expected retirement age at time t-1 because they reflect the rate of time
We also find no effect of unexpected house-price changes. And specifications including changes in nonhousing wealth and industry and occupation dummies yield similar results. Results available upon request.
22
16
preference of the individual. But both instruments, assuming they are fully incorporated into
expected retirement age at time t-1, should have no independent effect on expected retirement
age at time t.
We perform IV estimation of equation 2 using GMM, which is robust to
heteroskedasticity of unknown form. IV estimates are given in Table 5, Column 2. Here,
coefficient estimates are consistent with rational expectations. The estimate of the constant term
is statistically indistinguishable from zero at conventional significance levels. The estimate of the
coefficient on lagged expected retirement age is statistically indistinguishable from one. The
Sargan statistic for testing the null hypothesis that overidentifying restrictions are valid is
statistically insignificant. The F-statistic for the 2 instruments in the first stage is 15.4, which is
greater than the threshold of 10 recommended by Bound, Jaeger, and Baker (1995).
The key estimate of interest for our purposes is the estimate of the coefficient on
Owner*%HPI. The estimate of -0.011, while of the anticipated sign, is small and statistically
insignificant. Consideration of the 95-percent confidence interval about this estimate reveals that
our estimates are not sufficiently precise to rule out the possibility of modest effects of house
prices on expected retirement age. However, overall our findings are consistent with the claim
that changes in house prices have no effect on retirement timing, as found in our analysis above
and the findings of Coile and Levine (2011).23
Recall that our sample includes both male and female individuals. If women of the HRS
generations view retirement differently than men, our results could be affected by their inclusion
in the sample. Thus, we re-estimate equation 2 using the instrumental variables approach on a
23
In another specification we estimate a Heckman-selection-corrected IV model to address potential sample
selection. We reject the null of sample selection and therefore do not provide those results here. The results for key
coefficient estimates are similar to those shown here and are available upon request.
17
male-only subsample. Results are given in Table 6, Column 3 are similar to those obtained using
the more inclusive sample.
There are three plausible explanations for finding that changes in house prices have no
effect on expected retirement age. First, and consistent with a strong form of rational
expectations, individuals may have perfectly forecast house-price changes in their area. Second,
individuals who experience housing gains may not be able to access that new housing wealth in
order to convert it into additional leisure. Third, individuals may view variation in house prices
as largely transitory.
While we cannot empirically rule out the possibility that individuals perfectly anticipated
the rise and fall of house prices over the last two decades, we find the first explanation
implausible. Bernheim (1989) and Benítez-Silva and Dwyer (2005) found that a significant
number of households commit forecasting errors in predicting their retirement age. These errors
must reflect imperfect anticipation of future determinants of retirement timing, and individuals
committing those errors must have updated their expected retirement age upon receiving the
news that led to their different-than-expected retirement age. If housing matters for retirement
realizations, we would expect to see it matter for retirement expectations.
The second explanation seems more plausible. After all, housing wealth is most available
to people who have access to credit and people who are mobile and have options to move to
areas with cheaper housing. While downsizing within a single real estate market can free up
some wealth for consumption of leisure, downsizing from an expensive housing market to a
cheap housing market is a more effective way to access housing gains and thus facilitate early
retirement. We might expect more highly educated households to have greater access to credit
and greater mobility. We might also expect people living in states on the East and West coasts
18
(which have mobile populations and high property values on average) to be better positioned to
liquidate housing wealth through moves to cheaper real estate markets.
We explore this possibility briefly by estimating equation 2 using the instrumental
variables approach for two subsamples that might be better positioned to access wealth in their
homes. One consists of individuals in the HRS with 16 or more years of education. The other
consists of individuals in the HRS who live in states on the East coast or West coast of the US.
Estimates obtained using these subsamples are given in Columns 1-2 of Table 6. In the case of
the highly educated subsample (Column 1), the coefficient estimate on Owner*%HPI is now
positive and still statistically indistinguishable from zero.24 In the case of the East-West coasts
subsample, the coefficient estimate is negative and still small and statistically insignificant. In
results not shown here, we perform IV estimation of equation 2 for a number of other
subsamples, including different sets of years, different sets of states, and individuals who
reported planning to move when they retired. None of these yield any substantial difference in
the coefficient estimate on Owner*%HPI. We also estimate a specification that allows
individuals to respond asymmetrically to gains and losses, and still find no effect of house prices
on expected retirement age. Results from all of these specifications are available upon request.
As a result of these additional findings we cannot conclude that the lack of an estimated effect of
house prices on retirement is due to borrowing or moving constraints.
The third explanation—that individuals view house-price changes as transitory—is given
credence by Lettau and Ludvigson (2004) and others (e.g. Fisher, Otto, and Voss, 2010) who
find that much of the change in house values over time is transitory, and—because households
Interestingly, the highly educated subsample has the “most rational” coefficient estimates for the constant and
coefficient on lagged expectations. However these are not statistically significantly different from those obtained
from the full sample.
24
19
realize this—has little effect on consumption. This is a plausible explanation for our findings, but
we leave further investigation to future research.
V. Conclusion
Estimating models of retirement realizations and retirement expectations using data from
the HRS and data from the Federal Housing Finance Agency on local house prices, we are
unable to find evidence that housing capital gains affecting retirement timing. Using a linear
probability model of annual transitions into retirement, we find no statistically significant
evidence of housing wealth effects on retirement timing—findings consistent with Coile and
Levine (2011). When we expand our analysis to use specifications that better allow us to control
for individual heterogeneity we still find no evidence of housing wealth effects on retirement
timing.
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23
Figure 1. Year over year change in FHFA National House Price Index
0.1
12 month change in HPI
0.05
0
-0.05
-0.1
24
Figure 2. Year over year change in FHFA House Price Index By Census Region (West)
Mountain
0.2
Pacific
0.15
West North
Central
0.1
West South
Central
-0.1
-0.15
-0.2
-0.25
25
Jan-09
Jan-08
Jan-07
Jan-06
Jan-05
Jan-04
Jan-03
Jan-02
Jan-01
Jan-00
Jan-99
Jan-98
Jan-97
Jan-96
Jan-95
Jan-94
-0.05
Jan-93
0
Jan-92
12 month change in HPI
0.05
Figure 3. Year over year change in FHFA House Price Index By Census Region (East)
0.15
0.05
-0.05
-0.1
-0.15
26
Jan-09
Jan-08
Jan-07
East North
Central
East South
Central
Middle
Atlantic
New
England
South
Atlantic
Jan-06
Jan-05
Jan-04
Jan-03
Jan-02
Jan-01
Jan-00
Jan-99
Jan-98
Jan-97
Jan-96
Jan-95
Jan-94
Jan-93
0
Jan-92
12 month change in HPI
0.1
Table 1: Sample Selection Among HRS Respondents
(NEEDS UPDATING)
A. Sample for One-Year Retirement Transitions, Table 4
Men ages 51-61 in 1992, for any interview 1992-2004
+ Working, not retired, and not self employed in previous year
+ Has no missing data
nobs
59,862
15,352
13,511
B. Sample For Model of Expected Retirement Age - Tables 5-6
Men ages 50 and older, for any interview 1992-2008
+ Working, or searching for work
+ Reported expected retirement age
+ Has thought about retirement
+ Has no missing data
27
9,849
Table 2: Summary Statistics for Analysis Sample
Mean
63.24
1.84
0.98
0.05
0.84
59.71
0.85
12.77
0.07
0.12
0.14
2.81
0.44
0.29
0.59
3.51
6.71
1.57
9.20
0.44
-0.34
3.38
Expected Retirement Age
Annual %DHPI
Unexpected Annual % DHPI
County Unemployment Rate
Own Home
Age
Married
Years of Education
Hispanic
Black
Poor Health
Log Wage
Has DB Pension
Has DC Pension
Has Retiree Health Benefits in 1992
DC Pension Balance in 1992 ($10,000s)
Home Equity in 1992 ($10,000s)
Business Equity in 1992 ($10,000s)
Other Wealth in 1992 ($10,000s)
2-Year D DC Pension Balance ($10,000s)
2-Year D Business Equity ($10,000s)
2-Year D Other Wealth ($10,000s)
Standard Deviation
3.53
4.18
3.35
0.03
0.37
3.46
0.36
3.14
0.25
0.32
0.35
0.61
0.50
0.45
0.49
10.54
7.71
16.87
25.64
17.46
20.98
73.38
Sample Size
3,938
Dollar measures are in year 2000 dollars. Percent changes in house prices are deflated by the
CPI (excluding housing).
Sample includes observations from 1992 to 2004 on men born between 1931 and 1941.
28
Table 3: Detailed Distribution of Selected Financial Variables
Mean
1.84
0.98
3.51
6.71
1.57
9.20
0.44
-0.34
3.38
Annual %DHPI
Unexpected Annual %DHPI
DC Pension Balance in 1992 ($10,000s)
Home Equity in 1992 ($10,000s)
Business Equity in 1992 ($10,000s)
Other Wealth in 1992 ($10,000s)
2-Year D DC Pension Balance ($10,000s)
2-Year D Business Equity ($10,000s)
2-Year D Other Wealth ($10,000s)
25th Percentile
-0.40
-0.59
0.00
1.80
0.00
1.10
-0.02
0.00
-1.36
Sample Size
3,938
Dollar measures are in year 2000 dollars. Percent changes in house prices are deflated by the CPI-X.
Sample includes observations from 1992 to 2004 on men born between 1931 and 1941.
29
Median
1.72
1.04
0.00
5.00
0.00
3.51
0.00
0.00
0.68
75th Percentile
3.51
2.89
2.24
8.90
0.00
9.10
0.73
0.00
4.83
Table 4: OLS Estimates of the Effect of Changes in House Price Index (HPI) on Retirement
Sample Contains Male Owners and Renters, not Retired at the Previous Wave
Years of Education
Hispanic
Black
Married
Has DB Pension
Has DC Pension
Has Retiree Health Benefits
Poor Health
Log wage (t-1)
DC Pension Bal. in 1992 ($10,000)
Home Equity in 1992 ($10,000s)
Business Equity in 1992 ($10,000s)
Other Wealth in 1992 ($10,000s)
Percent Change in HPI
Percent Change in HPI*Home Owner
Home Owner
County Unemployment Rate
One-Year Change in
HPI
-0.001
(0.001)
-0.006
(0.011)
-0.019
(0.008)
-0.018
(0.009)
0.032
(0.007)
-0.010
(0.007)
0.019
(0.005)
0.039
(0.01)
0.006
(0.005)
0.00038
(0.0004)
0.00093
(0.0004)
-0.00028
(0.0002)
0.00021
(0.0002)
-0.232
(0.147)
0.087
(0.18)
0.011
(0.007)
-0.003
(0.105)
R-squared
Sample Size
**
**
**
**
**
**
0.087
13,511
** Denotes statistical significance at the 5% level and * at the 10% level.
Robust standard errors are in parentheses.
Additional controls include industry, occupation, age, state, and year dummies.
30
Five-Year Change in
HPI
-0.003
(0.002)
-0.028
(0.014)
-0.019
(0.013)
-0.010
(0.013)
0.046
(0.01)
-0.002
(0.01)
0.024
(0.007)
0.034
(0.013)
0.007
(0.007)
0.00087
(0.0007)
0.00114
(0.0006)
-0.00037
(0.0003)
0.00002
(0.0002)
-0.035
(0.058)
0.013
(0.063)
0.010
(0.011)
-0.153
(0.186)
0.092
7,254
*
**
**
**
**
Table 5: The Effect of House-Price Changes on Expected Retirement Age
Renters vs. Owners (depvar=expected retirement age t)
(1)
OLS
0.483
(0.009)
Expected Retirement Aget-1
Constant
33.540
(0.677)
0.003
(0.012)
-0.814
(0.154)
-0.004
(0.012)
-0.004
(0.002)
0.009
(0.020)
0.0004
(0.0008)
0.0008
(0.0005)
%House Price Index (HPI)
Owner
Owner*(%HPI)
household income ($10,000s)
weekly wage ($1000s)
financial wealth ($10,000s)
business wealth ($10,000s)
local unemployment rate
-0.514
(4.860)
Health decline in last 2 years
-0.262
(0.132)
**
**
**
**
(2)
IV
0.907
(0.171)
**
6.186
(11.007)
0.007
(0.014)
-0.145
(0.319)
-0.011
(0.014)
-0.002
(0.002)
-0.002
(0.023)
-0.0001
(0.0010)
0.0005
(0.0006)
3.056
(5.606)
**
-0.235
(0.148)
p=.95
no
Overid. test (p-value for Sargan statistic)
Reject overid. restrictions?
Weak instruments test (F-stat)
Reject weak instruments?
F=15.39
yes
Reject rational expectations?
yes
no
R-squared
0.28
nobs
9,849
9,849
Because the HRS is a biennial survey, all changes are 2-year changes between survey waves.
Additional controls include state and year dummies.
**Denotes statistical significance at the 5% level and * at the 10% level.
31
Table 6. The Effect of House-Price Changes on Expected Retirement Age:
Renters vs. Owners (depvar=expected retirement age t)
(1)
IV
Highly
Educated
subsample
Expected Retirement Aget-1
Constant
%House Price Index (HPI)
Owner
Owner*(%HPI)
household income ($10,000s)
weekly wage ($1000s)
financial wealth ($10,000s)
business wealth ($10,000s)
local unemployment rate
Health decline in last 2 years
Overid. test (p-value for Sargan statistic)
Reject overid. restrictions?
1.008
(0.235)
-0.360
(15.249)
-0.024
(0.027)
0.041
(0.440)
0.013
(0.027)
-0.001
(0.003)
-0.006
(0.024)
-0.00004
(0.00104)
0.0004
(0.0006)
1.003
(10.003)
-0.247
(0.269)
(2)
IV
East-West
Coasts
subsample
**
0.828
(0.187)
10.963
(12.237)
0.013
(0.016)
-0.298
(0.381)
-0.015
(0.017)
-0.004
(0.003)
0.015
(0.033)
0.0004
(0.0023)
-0.0001
(0.0014)
6.900
(8.945)
-0.322
(0.208)
(3)
IV
Male
subsample
**
0.845
(0.182)
10.103
(11.714)
0.014
(0.019)
-0.163
(0.374)
-0.014
(0.021)
-0.002
(0.003)
0.017
(0.027)
0.0004
(0.0013)
0.0006
(0.0007)
-0.848
(7.583)
-0.540
(0.212)
0.62
no
0.30
no
0.97
no
Weak instruments test (F-stat)
Reject weak instruments?
F=7.68
no
F=11.76
yes
F=13.33
yes
Reject rational expectations?
no
no
no
nobs
3,621
4750
4819
Because the HRS is a biennial survey, all changes are 2-year changes between survey waves.
Additional controls include state and year dummies.
**Denotes statistical significance at the 5% level and * at the 10% level.
32
**