Dynamics of Wealth and Consumption:
New and Improved Measures for U.S. States
March 3, 2012
Xia Zhou1 |
Christopher D. Carroll2 |
_____________________________________________________________________________________
Abstract
Case, Quigley, and Shiller (2005) persuasively argue that the well-known
conceptual difficulties in measuring aggregate “wealth effects” might be lessened
by the use of state-level data. Unfortunately, the data required for a convincing
implementation of their idea have been either virtually nonexistent (for financial
wealth) or of questionable quality (for consumption). Our main contributions
are to provide the first directly observed panel data on financial wealth
at the state level, and to construct improved measures of state-level
spending growth. Using these data, we estimate rudimentary “wealth effects”
regressions that find a strong relationship between twice-lagged housing
wealth growth and current spending growth, but we find no relationship
between lagged financial wealth growth and current spending growth.
1Zhou: xia_zhou@fanniemae.com, Federal National Mortgage Association, 3900 Wisconsin Ave, Washington, DC 20016 2Carroll: ccarroll@jhu.edu, Department of Economics, 440 Mergenthaler Hall, Johns Hopkins University, Baltimore, MD 21218, http://www.econ2.jhu.edu/people/ccarroll, and National Bureau of Economic Research.
housing wealth effect, financial wealth effect
E2, G1
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Macroeconomic forecasting models often incorporate a “wealth effect” which asserts that movements in household net worth cause corresponding movements in aggregate consumption. U.S. data showing a striking negative relationship between the wealth-to-income ratio and the personal saving rate (see Figure 1) are often presented in support of this proposition, and statistical analysis finds a robust relationship between aggregate wealth movements and subsequent household spending growth.2
But a skeptic could find plenty of reasons to doubt that this correlation reflects
causation from wealth movements to consumption or saving outcomes. First, the
association could reflect simultaneity. For instance, any shock to consumers’
optimism or pessimism could have an impact on housing prices, stock prices, and
consumption growth in the same direction. Second, endogeneity could also reflect
reverse causality of consumption on wealth (for example, a consumption boom
might bid up stock prices as expected profits rise). Finally, simple kinds of
measurement error could lead to the observed association. For example, suppose
that income is measured with error. By construction, the personal saving
rate,
, will also be mismeasured in the same direction
as
. At the same time, the measured wealth-income ratio
will be biased in the opposite direction, generating a spurious negative
relationship.
In an effort to get around these problems, a substantial literature has turned to micro data. But household-level data suffer from serious measurement problems. There is a very limited choice of household-level data available for carrying out such studies in the U.S. For instance, the Panel Study on Income Dynamics (PSID) only measures food consumption, while the Consumer Expenditure Survey (CEX) has detailed but noisy data on household expenditures and poor financial information. The Survey of Consumer Finances (SCF) provides no measure of consumption at all.
An alternative approach, one that potentially avoids some of the problems related to both aggregate and household-level data, is to use regional data. First, if there is sufficient variation across regions, the endogeneity problem might be mitigated. For instance, consider a region-specific shock to consumers’ confidence, one that might also have a large impact on the consumption behavior of households in the region. However, if a well-integrated stock market exists, this region-specific shock might not have as great an impact on stock prices of persons who live in the region as a corresponding aggregate shock to confidence would have on aggregate stock prices. Therefore, the endogeneity problem between local wealth and local consumption is alleviated to some extent. Furthermore, it can be argued that regional data provides more comprehensive and better measures of the relevant variables than household-level data. Finally, regional data is more likely to cover a longer time period and therefore allow for richer dynamics.
Case, Quigley, and Shiller (2005) pioneered the estimation of wealth effects using regional data. We improve on their efforts in several ways. Most notably, after showing that CQS used a flawed method to construct state-level financial wealth, we construct a new panel dataset of financial wealth for U.S. states, using anonymous proprietary account-level records of geographic wealth holdings. We will argue that our new financial wealth dataset is much more accurate than existing alternative measures used previously in the literature. Another contribution of this paper is to construct a significantly improved state-level proxy for consumption data. Our two new datasets are then combined to provide new estimates of how household spending changes following movements in stock and housing wealth.
The rest of the paper is organized as follows: Section 2 reviews the related literature; Section 3 discusses the limitations of the currently available state-level consumption and stock wealth datasets; Section 4 describes the newly constructed data; and Section 5 presents the model specification and regression results, then uses those results to calculate the estimated contribution of disparate cross-state housing wealth movements to differences in the runup in consumption spending (prior to 2008) and the subsequent decline (after 2008). Some very rough calculations suggest that only a small portion of the post-2008 decline in spending can be attributed to the effects of housing price declines (though the estimated long lags in the housing wealth effect suggest that spending weakness may continue for some time). Section 6 concludes.
The existing literature on whether the marginal propensity to consume (MPC) differs out of different components of wealth is small. Davis and Palumbo (2001b) compared the stock market wealth effect with the non-stock-market wealth effect using U.S. aggregate data. The results, derived from a cointegration analysis, are, however, sensitive to model specification. The long-run effects of both types of wealth are estimated to be about the same (i.e., 0.06 for stocks and 0.08 for non-stocks) when the level of variables is used. Using logarithms, however, the results show an elasticity for non-stock wealth four times greater than that for stock wealth; this implies that the MPC out of non-stock wealth is at least twice as large as the MPC out of stock wealth. Additionally, using aggregate data (though applying a different method), Carroll, Otsuka, and Slacalek (2011) reported an immediate MPC out of housing wealth of about 1.5 cents and an immediate stock wealth MPC of 0.75 cents. This difference, however, is statistically insignificant.
Levin (1998) appears to be the first study in the U.S. to use household-level
data to estimate the differential effect of housing and stock wealth. Using the
Retirement History Survey, Levin found that housing wealth has essentially no
effect on consumption. Out of eight spending categories, only three reported a
statistically significant difference between the respective coefficients for
liquid and housing wealth. This finding contradicts the studies using
aggregate data summarized above. A possible reason could be the fact
that every interviewee in the survey is at least 65 years old. If elderly
people tend to view housing wealth more as consumption than as an
investment item, their housing wealth effect will be lower than would
otherwise be the case. Using the CEX and SCF, Bostic, Gabriel, and
Painter (2009) find that, while incorporating all households in their sample,
there is no evidence for an important housing wealth effect. Among home
owners, however, the housing wealth elasticity is found to be consistently
significant and larger than the stock wealth elasticity. Their paper also
suggests different consumption behaviors for credit-constrained versus non
credit-constrained samples. Using household-level data in the U.K., Campbell
and Cocco (2007) found the response of household consumption to housing
prices is rather large and significant. They also provide evidence for the
heterogeneity of this response. More specifically, the estimated housing
price elasticity is as large as for old home-owners but near zero
for young renters. Attanasio, Blow, Hamilton, and Leicester (2009),
however, found a larger relationship between consumption and house
prices for younger households. The authors then suggested that both
consumption and house prices are responding to some common factors.
Using a different British household-level dataset, Disney, Gathergood,
and Henley (2010) found a small housing wealth effect of
after
controlling for financial expectations, without which the estimated housing
wealth effect would be significantly biased up. If simultaneity of this kind
can be found even in micro data, where it should be harder to find, it
appears to justify the concern with simultaneity problems using aggregate
data.
The best known paper using geographical data is Case, Quigley, and
Shiller (2005). Using quarterly U.S. state-level data for 1982 through 1999,
the authors found a significant housing wealth elasticity of about
percent, but an economically negligible stock wealth elasticity under most
model specifications. When using a panel of annual data for 14 developed
countries, they found an even larger housing wealth elasticity, in the range of
percent. Nonetheless, under all cases, they found no evidence
for an important stock wealth effect. Case, Quigley, and Shiller (2011)
extended their state-level data up to 2009 and applied the same technique
to address the wealth effect question. Similar to their previous study,
the authors found significant and rather large housing wealth effect on
consumption and consistently found larger housing wealth effect than
stock wealth effect. However, after including data during
,
the recent housing market meltdown, the authors found that increases
and declines in the housing market have equally important effects on
consumer spending, which contradicts their previous findings. Bayoumi and
Edison (2003) used data for 16 industrial countries and found significant
wealth effects for most samples and periods. Their estimated housing
wealth effect was consistently larger than their estimated equity wealth
effect. Ludwig and Sløk (2002) found evidence contrary to the studies
cited above. Using annual data from 16 OECD countries, and taking
housing prices and stock market prices as proxies for their respective
wealth components, the authors reported an estimated stock wealth
elasticity twice the estimated housing wealth elasticity. Additionally, both
estimates were found to be positive and statistically significant. On the other
hand, Girouard and Blöndal (2001) also used OECD data, but were
unable to arrive at consistent results when comparing housing wealth
with financial wealth. Dvornak and Kohler (2003), using Australian
state-level data, found a larger stock wealth effect than housing wealth
effect.
Case, Quigley, and Shiller (2005) relate state-level quarterly spending growth to measures of quarterly state-level stock wealth and housing wealth for the U.S. for the period 1982 through 1999, and Case, Quigley, and Shiller (2011) extend that estimation to 2009. But serious problems afflict their measures of both financial wealth and consumption.
No direct measures of state-level financial wealth data exist, so CQS had to
construct their own estimates. The best data they were able to find was
occasional information about state-level holdings of mutual funds. In order to
produce a measure of state-level stock wealth, CQS assumed that the ratio of
mutual funds holdings to holdings of other financial assets was identical across
states (and equal to the aggregate value of that ratio), which implies that the
distribution of financial wealth across states can be constructed using
the pattern of mutual fund holdings (for years in which mutual fund
holdings are available). CQS obtained the mutual fund data for the years
1986, 1987, 1989, 1991, 1993, 2008, and 2009. In the absence of data
for other years, they assumed a constant distribution of mutual fund
holdings across states for the period and
.
During those years, then, movements in the stock wealth of each state
is assumed to mimic the movement of aggregate stock wealth. From
1999 to 2008, they assume that the ratio of mutual fund assets to total
assets increases linearly so that it matches the aggregate figure in 1999
and 2008. (2008-2009 is the only pair of adjacent years in which the
relevant data are available in both years to construct their measure without
interpolation).
One aspect of their methodology, at least, is subject to test: Their assumptions about the movements in the ratio of mutual fund holdings to total financial wealth. Figure 2 plots mutual fund holdings from FFA over the same period, and shows strong deviations from a linear increase in the ratio of mutual fund holdings to total financial assets at the aggregate level. Since aggregate data is the sum of state data, the CQS method must be producing mismeasurements of the state-level financial wealth data even if their assumption is correct that the ratio of mutual fund to total financial assets is identical across states. In principle, mismeasurement of a regressor tends to bias its coefficient toward zero; so an unfriendly interpretation of the CQS finding that the ‘financial wealth effect’ is small might be that this is because their measure of financial wealth changes is noisy.
To the best of our knowledge, there exist three distinct state-level sources of consumption data – those used by Asdrubali, Sorensen, and Yosha (1996); Case, Quigley, and Shiller (2005) and Case, Quigley, and Shiller (2011); and Garrett, Hernàndez-Murillo, and Owyang (2004). Of these, only CQS utilized the data to examine wealth effects. The consumption data used by Asdrubali, Sorensen, and Yosha (1996), and CQS used estimates of retail sales obtained from private sector sources. However, in both cases, the quality of these data derived from the private sources is questionable. First, the methodology used in the data construction is never explicitly revealed by either private source. Second, retail sales are presented for states that do not implement sales tax, which constitutes perhaps the single most important source for calculating state retail sales after the Census Bureau ceased reporting monthly retail sales by state, in 1997. Last but not least, both sources vaguely note that important state-level variables like wage and employment data are incorporated into the estimation of retail sales. As a result, use of these data is likely to generate unreliable estimations of the relationship between consumption and any variable that is correlated with wages or employment. (For example, a finding that ‘consumption growth is related to the predictable component of wage growth,’ a classic test of the permanent income hypothesis, would obviously be spurious if the measure of consumption was generated by imputation from wage growth data; the vague descriptions of the private firms’ data construction methods suggest that this is more than a hypothetical problem.)
Given these problems, we are skeptical of the empirical results of any study that uses data from these private sources. (For considerably more discussion of these sources and their doubtful properties, see Zhou (2010)).
More promising is the method of Garrett, Hernàndez-Murillo, and Owyang (2004), who computed quarterly retail sales by dividing sales tax revenue by the sales tax rate. In principle this could potentially yield a good measure of state retail sales, and this method therefore provides the basis of the measure of spending growth measure we use in this paper. One problem, however, is that the sales tax revenues are occasionally measured with serious errors; this results in observations with unreasonably large consumption variations and apparent outliers. We carefully examined these events and found that many of them could be explained, and many of those that could not be explained were nevertheless obviously errors. Thus, our dataset “cleans up” these outliers and thereby improves upon the data used in Garrett et. al. (2004).
This paper uses a panel dataset for U.S. states as well as Washington,
D.C., at a semiannual frequency for the period 2001 through 2005. The
newly constructed datasets are for stock wealth and consumption at the
state level. Other important variables include after-tax labor income
and housing wealth. All are expressed in real per capita terms. There is
evidence that the new data are more comprehensive and accurate than
other existing alternatives. Some important findings will be discussed
in the rest of this section. More detailed discussions can be found in
Zhou (2010).
We obtained anonymous account-level records on financial wealth holdings at the
ZIP+4 Code level from a private company. At the end of each semiannual cycle,
that company collects data from more than leading financial institutions in
its network. Reporting institutions include major banks, brokerage firms,
insurance companies and mutual fund dealers. Aggregate stock wealth growth
rates, as measured by both the Flow of Funds Accounts (FFA) and the new
dataset between 2000h1 and 2005h2, are presented in Figure 3. Despite using
completely different data sources, Figure 3 shows that the two series move
similarly to one another, suggesting that the new data is representative of the
nation as a whole.
Stock market wealth is defined as the sum of directly and indirectly held stocks and equity mutual funds (‘indirectly’ held assets are, e.g., IRA and Keogh accounts). Stock wealth growth is constructed using a consistent method for all 50 states plus the District of Columbia.3 The geographic distribution of stock wealth growth is plotted in Figure 4. We find similar patterns across states, something to be expected given the fact that the U.S. stock market is so well integrated. Since there exists no alternative state-level wealth data for comparisons, we use stylized facts about the U.S. to understand if the state heterogeneity manifested in the figure reflects reality.
Florida and Arizona are the two states that have the highest percentage of retired people. As reflected in Figure 4, their seasonal patterns also distinguish them from other states. In order to better illustrate the differences, Figure 5 compares the stock wealth growth of Florida and Arizona with the average stock wealth growth of the other states. It indicates that Florida and Arizona have a much higher stock wealth growth rate than the other states during the second half of each year, and a much lower stock wealth growth rate during the first half of each year. This phenomenon might seem strange at first glance, but is actually an outcome of the “snow-bird effect.” In the U.S., many retired people tend to move to Florida and Arizona during the winter and then move back to their permanent residences once the winter is over. If some such individuals update their physical mailing addresses with their financial institutions when they relocate, they effectively bring their assets along with them.4 Figures 5 therefore provide evidence that the data are indeed capable of capturing state-level variations that are both meaningful and independent of aggregate movements. (The patterns here also motivate our use of year-over-year growth averages in our empirical work, to avoid seasonal patterns of the kind identified here).
We exerted substantial effort to find any other measure of state-level financial resources with which the new data could be compared, without great success. The most plausible indicator is from Bloomberg, which reports local stock indices for 23 states; the literature on the “home bias” of investments would lead us to expect that the growth of this variable to be positively but not perfectly correlated with local stock wealth growth. Figure 6 presents the correlation between the local stock index and local stock wealth, broken down graphically. Out of the 23 calculated correlations, we find only 2 negative numbers. At the state-specific growth level, defined as state growth minus the U.S. national component, there are still 15 positive correlations. These facts further provide supporting evidence that the data is correlated with the true distribution of stock market wealth across states.
Since measures of personal consumption expenditure (PCE) at the state level are not available in the U.S., retail sales are used as a proxy for consumption. In the U.S., national retail sales account for roughly half of PCE, and The Retail Trade Survey is probably the single most important source for the national PCE estimation carried out by the Bureau of Economic Analysis (BEA). Actually, for nonbenchmark-year estimates for most categories of PCE, the retail sales series are used in the interpolation and extrapolation process, as well as the “control total” calculation for each retail control group.5 These considerations provide us with a rationale for using retail sales in place of consumption.
However, retail sales data are not directly available in the U.S. at the state level. Following Garrett, Hernàndez-Murillo, and Owyang (2004), quarterly state-level general sales tax revenues can be obtained from the Quarterly Summary of State and Local Government Tax Revenue, published by the U.S. Census Bureau. Together with general sales tax rates collected from various sources,6 state-level retail sales are computed by dividing the state general sales tax revenue by the general sales tax rate. One limitation of this method is that since 5 states do not have retail sales taxes, it can be applied only to 45 states and the District of Columbia. Nevada, however, is dropped in this study because of its discontinued data report and obvious poor data quality.
Strictly speaking, the computed retail sales are only one component of true
retail sales, as they exclude items that are either not subject to sales tax or are
part of special tax programs, i.e., liquor and cigarettes. Furthermore, there is
unquestionably serious measurement error in the computed retail sales from a
host of sources (including, for example, imperfect measurement of changes in
retail sales tax rates and the distribution of tax rates across categories of goods).
However, we discovered that 12 states actually directly report (taxable) retail
sales for the same period during which state-level stock wealth data is
available.7
These measures are more comprehensive than our computed measure of retail sales,
as they either include all consumption items (such as when government-reported
gross retail sales are used) or at least include those items that are part of special tax
programs.8
Furthermore, these government-reported measures should be
more accurate and reliable than the computed ones, since local
governments have access to more information regarding their own
sales tax system and tax collection practices than other people
do.9 10
Ideally, government-reported (taxable) retail sales should be used as a measure of consumption. However, since they are only available for a limited number of states, this paper compiles three sets of consumption data according to the quality of the retail sales data. The first one includes those 12 states that have government-reported retail sales or taxable retail sales; it is categorized as “Best Data.” The second set is called “Good Data,” which is the computed retail sales with outliers taken care of. The third set is called “Combined Data,” and is “Best Data” combined with “Good Data” whenever the former is not available. Table 1 presents the summary statistics of each set of consumption data. Please refer to the third chapter of Zhou (2010) for a more detailed discussion of the consumption data.
Other important variables used in this paper include quarterly after-tax labor income and housing wealth. After-tax labor income is calculated following Lettau and Ludvigson (2001). The formula used to construct state-level housing wealth is similar to the one adopted by CQS, and is given as follows:
One important data issue arises here. As mentioned above, all variables except the stock market wealth are available at quarterly frequencies. To make them analogous to the stock market wealth, this paper takes their means over the quarters for each half-year, thus converting them into semiannual frequencies.
The dataset, however, features evident and sizable seasonal patterns at the semiannual frequency, especially for the constructed consumption data. We made a considerable effort at removing these seasonal patterns in a consistent fashion, but were unable to do so at the semiannual frequency. This is largely because of the heterogeneity of seasonal patterns across states and the relatively short time horizon. (Many state governments recommend using longer time spans for more reliable trends.) It should be recognized that measures of taxable sales (or revenue) at higher frequencies could be unrepresentative for the purpose of comparison. This is because of timing errors over the year-long period. The above consideration persuaded us to use annual growth rates so as to eliminate seasonal effects, at the cost of fewer observations and thus a reduced regression power.
Additionally, to avoid a time aggregation problem, annual averages are not
used to calculate growth rates. Instead, is computed as the log difference
between consumption for the first half of year
and for year
. The first
half was chosen in consideration of the fact that the state fiscal year ends
on June 30th. It is arguable that data collected towards the end of a
fiscal year is more accurate than data collected at any other time of
year.
Since this paper relies heavily on the two newly constructed datasets, before examining wealth effects, we report a simple regression of the form
where
Many studies in the current literature, particularly those that focus on the immediate
response of consumption to wealth, adopt regressions similar to those used in
Equation 1.12
However, even if simultaneity problems did not exist, such regressions would not
yield straightforward measures of wealth effects, since they only report the
contemporaneous growth correlation between consumption and wealth.
Worse, in this specification it is not straightforward to test the interesting
hypothesis that stock and housing wealth effects are of equal size (which is
assumed whenever an overall “wealth effect” is estimated, but may not be
true).13
In order to solve this problem, this paper adopts an approach similar to that
employed by Carroll, Otsuka, and Slacalek (2011); those authors use
the ratio of the change in each variable relative to an initial level of
consumption spending. Here, we use average aggregate labor income between
and
as the denominator instead. Specifically, if we define
As with Equation 1, Equation 2 is subject to serious endogeneity problems, and thus must be considered as simply another description of the data. Table 4 indicates that under this model specification, income change is still the most correlated variable with respect to consumption.
In order to address the endogeneity and simultaneity problems that Equation 2 is subject to, we briefly revisit classic consumption theory. The relationship between consumption and wealth and income can be described by the Life-Cycle/Permanent Income Hypothesis. Specifically, a consumer wants to
The random walk proposition, therefore, can help us address the endogeneity and simultaneity problem, as it suggests that current consumption growth would not be correlated with any lagged wealth growth. Nevertheless, time aggregation and measurement error could cause current consumption changes to correlate with once lagged income and wealth changes, even if the PIH holds true. Aggregation also matters when the PIH holds in continuous time, and the measures of consumption are based on time averages. Under this situation, changes in time-averaged consumption will have nonzero first order serial correlations; this will lead to nonzero correlations between changes in consumption and once-lagged variables. It is also easy to prove that measurement errors in the consumption level could cause measured consumption changes that correlate with once-lagged explanatory variables.14 Given the above considerations, the following equation is employed to see if we can detect delayed effects of wealth changes:15
Equation 3 employs twice-lagged independent variables, and thus gives a rudimentary estimate of current MPCs out of changes in housing wealth and stock wealth that occurred two periods prior, which would be zero in the random walk model.
There are, however, two minor modifications that need to be made. First, what
captures here is not the real personal consumption for state
, but the
state’s taxable retail sales. Thus, using
, the estimation of Equation 3
actually yields the effect of changes in wealth on taxable retail sales. To gauge
the approximate change in real consumption, it is assumed that initial
state consumption can be determined by
, where
and
are aggregate personal consumption expenditure and after-tax
labor income, respectively. In addition, we assume that the ratio of retail
sales to real consumption holds constant over time, i.e.,
.
Therefore, changes in state consumption can be measured roughly by
Therefore, if we redefine
Table 5 summarizes the results of our estimations using Equation 3. It indicates that all three datasets report similar results, with the exception that none of the estimations from “Best Data” is statistically significant. Given the small sample size of the “Best Data” sample, this is perhaps not too surprising.
Table 5 shows that the coefficients of income changes are all positive and large. It therefore implies that income changes have a fairly big impact on consumption, despite the two-year lag. This, however, contradicts the random walk theory as predicted by the Permanent Income Hypothesis.
The wealth effect from lagged changes in financial wealth, on the other hand, is found to be both statistically insignificant and economically negligible. This finding is consistent with Dynan and Maki (2001), who found that the impact of stock wealth on consumption very quickly becomes apparent, and any lagged change in stock wealth beyond 9 months does not have any significant effect on consumption.
However, we observe highly significant and large coefficients for housing wealth
in two out of the three datasets. Additionally, all three datasets indicate an MPC
out of housing wealth changes that occurred two years prior around the
neighborhood of cents.
There are several reasons why the response to housing wealth shocks may be slower than the response to financial wealth shocks. Unlike stock prices that can be easily tracked daily online or in newspapers, house prices might be difficult to observe accurately or regularly. Homeowners might be less aware of short-run changes in house prices and it might take a homeowner a while to realize that his/her house price has changed. Additionally, the cost of realizing capital gains on housing wealth is lumpy. As a result, the response to housing wealth growth is not likely to be entirely contemporaneous.
What is more interesting is that the difference between the housing wealth effect and the stock wealth effect is found to be statistically significant for “Good Data,” and on the verge of being significant for “Combined Data.”
A method for formalizing the sluggishness of the response of consumption to changes in wealth was proposed by Carroll, Otsuka, and Slacalek (2011) (henceforth ‘COS’), who show how to derive “eventual” wealth effects implied by serial correlation in consumption growth. The basic idea is, if there is evidence of habit formation, consumption growth will be serially correlated. Thus, any impact that wealth changes have on consumption could be delivered through the serial correlation of consumption growth. The eventual wealth effect then can be derived by dividing the short run wealth effect by one minus the habit formation coefficient. We attempt to test this method of describing the consumption process using the equation derived by COS:
![]() | (6) |
where the coefficient is expected to indicate the strength of habit
formation.
Table 6 reports the estimations using Equation 6. Using currently available state-level instruments, the results provide no evidence of habit formation.16 This could be because of the short time horizon of the data, and the corresponding weakness of IV techniques like the one employed for this test.
The U.S. economy entered a serious downturn in 2007 and is currently going through a weak recovery. Therefore, it would be illuminating if we can conduct a wealth-effect analysis using state-level data post 2005. State-level financial wealth data, however, is currently only available through 2005. As a result, our analysis in this section is performed without financial wealth growth. This is arguably valid since financial wealth growth was found insignificant in previous sections.
Similar to Table 3 and 4, Table 7 and 8 describe the data between 2001 and 2009, and present the test of structural break after 2005. It shows that both income and housing wealth growth are positively and significantly correlated with concurrent consumption growth. The null hypothesis of equal correlation between consumption and income and/or housing wealth before and after 2005, however, is rejected under most scenarios. More interestingly, new data tends to present a higher correlation between consumption and income/housing wealth after 2005. Liquidity constraints might be a possible reason that income and wealth are more correlated with consumption during a recession.
Employing Equation 3, Table 9 repeats the wealth effect analysis without financial wealth growth. Neither income nor housing wealth effect is found to be significant. Furthermore, all three datasets show a negative coefficient for housing wealth growth, indicating that consumption will decline in reaction to increases in housing wealth two years ago. An obvious explanation is that the two-year lag is too long if there is a bubble that inflates and then bursts, and if there are immediate and once-lagged effects of housing wealth changes on consumption that are larger than the twice-lagged effects. Housing price bubbles and thus rapid increases in housing wealth occurred before the housing market breakdown is the exact reason why the economy took a sharp turn in 2007.
The rest of this section is inspired by the work of Mian and Sufi (2011), who study the patterns of household debt at the county level from 2002 to 2007, and investigate how they are correlated with the following economic recession and recovery. They find that not only did high household debt counties experience larger declines in prices during the recession, but they also recover more slowly after the recession. Employing their methodology, we take the 6 states that had the highest house price growth during 2001-2006, then show the subsequent behavior of house prices and consumption for 2007-2009. We do the same thing for the 6 states having the lowest housing wealth growth between 2001-2006.
Figure 9 compares consumption and housing wealth, both indexed to 2000h1,
for the top and bottom 6 states during 2001-2006. The figure reflects the
well-known fact that housing wealth growth was highly heterogeneous across
states. The top 6 states experienced a sharp increase in housing wealth up to
2006 and experienced an equally sharp decline in housing wealth starting 2007.
On the other hand, the bottom 6 states show a much smoother housing wealth
growth path through the whole period. Figure 9 further shows that consumption
of both high and low housing wealth growth states contracted in 2001-2003,
likely due to the recession that started in 2001. Nevertheless, consumption of the
top 6 states with high housing wealth growth was rapidly increasing
as the real estate bubble was forming. In contrast, consumption of the
bottom 6 states only grew slightly as the housing market was booming
nationwide. By the time when national housing price peaked, consumption
of the top 6 states has been about percent higher than its level
in 2000. But the bottom 6 states were still inching toward their 2000
level.
The observations above lead to an interesting question: Given what we knew from the 2001-2006 estimates, how well would we have been able to predict consumption declines after 2006 in the two groups of states had we known the housing wealth and income changes they would experience over 2007-2009? In other words, what fraction of the consumption declines after 2006 can be associated with the concurrent housing wealth and income changes? (We freely admit that this association cannot properly be interpreted as causal, for all the reasons articulated in the introduction).
To address this question, we start by regressing consumption growth, ,
on a time dummy, income growth, and housing wealth growth,
, using
data between 2001-2006. We then predict consumption growth for 2007-2009 by
setting the intercept term to be zero. Figure 10 compares the actual and
predicted consumption growth for the top and bottom 6 states. It shows that the
top 6 states experienced an immediate drop in consumption as soon as the
housing market turned south in 2007, and continued with a sharp decline in
2008 as the subprime crisis intensified. Table 10 further shows, however,
that of the cumulative decline in consumption from 2006 to 2009, only
about
percent can be ‘explained’ by the declines in income and
housing wealth. On the other hand, Figure 10 shows that states with the
bottom housing wealth growth hardly experienced any major consumption
contraction until 2009, when the subprime crisis had spread to non-subprime
areas and other industries. This nicely matches findings by Mian and
Sufi (2010) who find that spending on motor vehicles in non-housing-boom
states did not collapse until 2009, while motor vehicle purchases began
declining considerably earlier in the states that had a housing bubble then
bust. Together, these points suggest that, while problems in the housing
market may have been an important trigger for the 2008-2009 crisis, the
precipitous drop in consumption spending in that period went well beyond
what would have been expected just from the loss of housing wealth and
income.
This paper’s main contribution is to construct and describe two panel datasets:
One for financial wealth for U.S. states for 2000-2005, constructed from
anonymous proprietary account-level records of geographic wealth holdings, and
one for state-level consumption data, constructed using data on retail sales tax
revenues from the Census of State Governments (and, for some states, from
state-level estimates of retail sales); and to argue that these datasets are
substantially better than those that have been used by previous authors. We
then combine these datasets to provide new estimates of the relationship
between spending growth and current and lagged changes in stock wealth
and housing wealth. Consistent evidence is found for large but sluggish
housing wealth effects. Based on the results from our new approach,
two out of the three datasets indicate that the MPC out of a one dollar
change in two-year lagged housing wealth is about cents. In addition,
the twice-lagged income change is also found to be strongly related to
the current consumption change. Both findings lead to the rejection of
the random walk model of consumption. Furthermore, a statistically
insignificant and economically small stock wealth effect is found for almost all
specifications, although large standard errors mean that the differences of
the financial wealth effect from housing wealth effects are statistically
insignificant.
In addition, the paper finds evidence for a strong association between
consumption and housing wealth declines in the period after the real estate
bubble burst; the states with the biggest housing wealth decline experienced
substantially larger declines in consumption spending. Our results also lend
tentative further support to the proposition asserted in CQS, in Carroll, Otsuka,
and Slacalek (2011), and elsewhere that movements in housing wealth and
financial wealth have different effects, with housing wealth changes apparently
exerting a large influence on household spending even two years after the
impulse. In addition to their salience for explaining recent events, these results
might also help explain the strength of consumption following the bursting of the
stock market bubble at the end of the s: at the same time the
stock bubble was bursting, housing wealth had shown substantial gains,
and with a larger and more sluggish MPC might have been sufficient to
explain the strength of household spending in that era (in addition to its
weakness recently); see Figure 11 in the appendix for a breakdown of the
movements in wealth between financial and nonfinancial that supports this
story.
Note: The sharp seasonal fluctuations in wealth in Florida and Arizona likely reflect a “snow bird” effect, as wealthy retirees move in and out of these states on a seasonal basis.
![]() (a) State stock wealth growth versus local stock index growth |
![]() (b) Idiosyncratic state stock wealth growth versus idiosyncratic local stock index growth |
Variable | Obs | Mean | Std. Dev. | Min | Max |
![]() | 180 | 0.002 | 0.130 | -0.379 | 0.212 |
![]() | 180 | 0.055 | 0.050 | -0.027 | 0.227 |
Best ![]() | 48 | 0.010 | 0.040 | -0.067 | 0.119 |
Good ![]() | 180 | 0.003 | 0.042 | -0.095 | 0.099 |
Combined ![]() | 180 | 0.007 | 0.067 | -0.321 | 0.428 |
Avg ![]() | Avg ![]() | Std. Dev.
![]() | |
![]() | 0.001 | 0.015 | 0.027 |
![]() | 0.0007 | 0.045 | 0.069 |
![]() | 0.0007 | 0.040 | 0.062 |
Best Data
| |||||||
(1) | (2) | (3) | (4) | (5) | (6) | (7)
| |
![]() | 0.766![]() | 0.681![]() | 0.762![]() | 0.665![]() |
|||
(0.204) | (0.202) | (0.18) | (0.175) | ||||
![]() | 0.431![]() | 0.352![]() | 0.475![]() | 0.397![]() |
|||
(0.176) | (0.176) | (0.162) | (0.162) | ||||
![]() | 0.145![]() | 0.143![]() | 0.162![]() | 0.158![]() |
|||
(0.066) | (0.061) | (0.063) | (0.06) | ||||
Obs. | 48 | 48 | 48 | 48 | 48 | 48 | 48 |
![]() | 0.72 | 0.701 | 0.696 | 0.739 | 0.747 | 0.736 | 0.774 |
Partial ![]() | 0.154 | 0.095 | 0.079 | 0.212 | 0.236 | 0.202 | 0.318 |
Good Data
| |||||||
(1) | (2) | (3) | (4) | (5) | (6) | (7)
| |
![]() | 1.009![]() | 0.989![]() | 0.971![]() | 0.956![]() |
|||
(0.246) | (0.251) | (0.254) | (0.258) | ||||
![]() | 0.112 | 0.059 | 0.095 | 0.053 | |||
(0.086) | (0.085) | (0.086) | (0.085) | ||||
![]() | 0.093![]() | 0.039 | 0.086 | 0.036 | |||
(0.055) | (0.053) | (0.055) | (0.054) | ||||
Obs. | 180 | 180 | 180 | 180 | 180 | 180 | 180 |
![]() | 0.261 | 0.188 | 0.194 | 0.258 | 0.259 | 0.194 | 0.256 |
Partial ![]() | 0.091 | 0.002 | 0.009 | 0.088 | 0.088 | 0.009 | 0.085 |
Combined Data
| |||||||
(1) | (2) | (3) | (4) | (5) | (6) | (7)
| |
![]() | 1.054![]() | 1.028![]() | 0.983![]() | 0.964![]() |
|||
(0.21) | (0.21) | (0.216) | (0.217) | ||||
![]() | 0.131 | 0.076 | 0.107 | 0.065 | |||
(0.083) | (0.078) | (0.082) | (0.078) | ||||
![]() | 0.128![]() | 0.074 | 0.121![]() | 0.07 | |||
(0.05) | (0.049) | (0.05) | (0.049) | ||||
Obs. | 180 | 180 | 180 | 180 | 180 | 180 | 180 |
![]() | 0.368 | 0.287 | 0.301 | 0.368 | 0.372 | 0.303 | 0.371 |
Partial ![]() | 0.12 | 0.007 | 0.027 | 0.12 | 0.126 | 0.03 | 0.124 |
a. Partial refers to the proportion of variance explained by all variables other than the year dummies.
b. Standard errors in parenthesis. {*, **, ***} = significant at the {10%, 5%, 1%} level.
Best Data | Good Data | Combined Data | |
![]() | 0.844![]() | 1.305![]() | 1.368![]() |
(0.271) | (0.415) | (0.383) | |
![]() | 0.07![]() | 0.029 | 0.034![]() |
(0.021) | (0.021) | (0.02) | |
![]() | 0.017![]() | 0.007 | 0.004 |
(0.01) | (0.01) | (0.009) | |
![]() | 6.346 | 0.756 | 1.526 |
(Rejected) | (Accepted) | (Accepted) | |
Obs. | 48 | 180 | 180 |
![]() | 0.783 | 0.247 | 0.349 |
Partial ![]() | 0.357 | 0.119 | 0.157 |
Best Data | Good Data | Combined Data | |
![]() | 0.474 | 0.787![]() | 0.884![]() |
(0.503) | (0.38) | (0.332) | |
![]() | -.021 | -.004 | -.004 |
(0.033) | (0.026) | (0.025) | |
![]() | 0.046 | 0.058![]() | 0.047![]() |
(0.041) | (0.021) | (0.02) | |
![]() | 2.168 | 4.458 | 3.603 |
(Accepted) | (Rejected) | (Accepted) | |
Obs. | 24 | 90 | 90 |
![]() | 0.197 | 0.094 | 0.132 |
Partial ![]() | -.017 | 0.103 | 0.12 |
Best Data | Good Data | Combined Data | |
![]() | 0.422 | -.122 | -.014 |
(0.336) | (0.253) | (0.275) | |
obs | 24 | 90 | 90 |
![]() | 0.156 | -0.019 | 0.001 |
First Stage: | |||
Partial ![]() | 0.344 | 0.148 | 0.146 |
![]() | 0.092 | 0.009 | 0.01 |
Best Data
| |||
(1) | (2) | (3)
| |
![]() | 1.540![]() | 1.226![]() |
|
(0.351) | (0.3) | ||
![]() | 0.318![]() | 0.232![]() |
|
(0.07) | (0.06) | ||
obs. | 96 | 96 | 96 |
![]() | 0.657 | 0.635 | 0.704 |
Partial ![]() | 0.262 | 0.214 | 0.364 |
F-Test | 5.275 | 5.73 | 1.875 |
P-Val | 0.024 | 0.019 | 0.16 |
Good Data
| |||
(1) | (2) | (3)
| |
![]() | 1.588![]() | 1.533![]() |
|
(0.281) | (0.285) | ||
![]() | 0.181![]() | 0.047 | |
(0.063) | (0.059) | ||
obs. | 360 | 360 | 360 |
![]() | 0.349 | 0.263 | 0.349 |
Partial ![]() | 0.136 | 0.021 | 0.135 |
F-Test | 3.722 | 1.908 | 1.804 |
P-Val | 0.055 | 0.168 | 0.166 |
Combined Data
| |||
(1) | (2) | (3)
| |
![]() | 1.688![]() | 1.631![]() |
|
(0.256) | (0.262) | ||
![]() | 0.192![]() | 0.05 | |
(0.056) | (0.051) | ||
obs. | 360 | 360 | 360 |
![]() | 0.444 | 0.339 | 0.443 |
Partial ![]() | 0.183 | 0.029 | 0.183 |
F-Test | 5.574 | 1.263 | 2.839 |
P-Val | 0.019 | 0.262 | 0.06 |
a. Partial refers to the proportion of variance explained by all variables other than the year dummies.
b. Standard errors in parenthesis. {*, **, ***} = significant at the {10%, 5%, 1%} level.
c. F-Test and P-val is for the test of equal income and house wealth effect for the periods before and after 2005.
Best Data | Good Data | Combined Data | |
![]() | 1.554![]() | 2.088![]() | 2.230![]() |
(0.426) | (0.536) | (0.518) | |
![]() | 0.031![]() | 0.005 | 0.006 |
(0.009) | (0.01) | (0.008) | |
Obs. | 96 | 360 | 360 |
![]() | 0.674 | 0.3 | 0.382 |
Partial ![]() | 0.248 | 0.105 | 0.136 |
F-Test | 9.96 | 8.673 | 9.941 |
P-Val | 0.0001 | 0.0002 | 0.00006 |
Best Data | Good Data | Combined Data | |
![]() | -.709 | 0.792 | 0.647 |
(0.432) | (0.698) | (0.686) | |
![]() | -.026 | -.011 | -.006 |
(0.018) | (0.016) | (0.014) | |
Obs. | 72 | 270 | 270 |
![]() | 0.55 | 0.209 | 0.267 |
Partial ![]() | 0.047 | 0.007 | 0.003 |
F-Test | 3.187 | 4.619 | 3.731 |
P-Val | 0.048 | 0.011 | 0.025 |
a. Partial refers to the proportion of variance explained by all variables other than the year dummies.
b. Standard errors in parenthesis. {*, **, ***} = significant at the {10%, 5%, 1%} level.
c. F-Test and P-val is for the test of equal income and house wealth effect for the periods before and after 2005.
Year | Index of | Index of | actl. ![]() | pred. ![]() |
|
actl. ![]() | pred. ![]() | ||||
Top States | 2006 | 1.094 | 1.094 | ||
2007 | 1.091 | 1.093 | ![]() | ![]() |
|
2008 | 1.019 | 1.074 | ![]() | ![]() |
|
2009 | 0.920 | 1.062 | ![]() | ![]() |
|
Bot States | 2006 | 0.984 | 0.984 | ||
2007 | 0.986 | 0.982 | ![]() | ![]() |
|
2008 | 0.986 | 0.978 | ![]() | ![]() |
|
2009 | 0.937 | 0.976 | ![]() | ![]() |
|
APPENDIX
The data used in this paper were constructed during the author’s part-time
employment at a private company over two years. All financial data feeds are
provided as anonymous, ZIP Code data by product type. Absolutely no
non-public, personally identifiable information on U.S. households have been
used in this study.
Once the ZIP+4 Code level data is received by the private company, for ZIP+4
codes with fewer than households, the data are joined and averaged with
other ZIP+4 Codes to ensure a minimum household count of
per ZIP+4
code. The average value is then imputed identically back down to the
affected ZIP+4 Codes. The rules utilized to perform the joining and
averaging are complex and based on geographical proximity and other
factors.
The names of the financial institutions reporting to the private company are suppressed and cannot be revealed. However, it should be noted that the number of reporting institutions changes over time. Hence, the biggest concern with constructing the stock wealth data is the possibility that the variations in wealth are caused by reasons other than the wealth holding variations of the state residents. To minimize this problem, we expended a great deal of effort keeping track of all mergers and institutions’ membership in the network.
The formation of a consistent source of financial data over time was
performed at the state level. Thus, I could construct a common group of
reporting institutions for every TWO ADJACENT CYCLES. So the growth
rates could be calculated as the log difference of two adjacent values on
a rolling basis. Specifically speaking, for growth rate of stock wealth
for state at time
, we summed up the assets by those institutions
reporting at both
and
for state
, and then I took the log
difference.
Specifically, suppose is the total amount of stock wealth reported at time
for state
by institution
.
is the set of all institutions reporting at
time
for state
. So
is the set of all the institutions
reporting for state
at both time
and
. Therefore,
,
the growth rate of stock wealth of state
at time
is defined as:
After obtaining the correct growth rates, total stock market wealth for each state were imputed backward as
where and
.
Real stock wealth per capita is defined as
Many papers in the literature have estimated wealth effects by adopting the elasticity method. Consequently, we then investigate the respective housing wealth and stock wealth effects by estimating the following equation, as with most related studies:
Table 11 reports the regression results from Equation 13 for all three sets of consumption data. The findings are roughly consistent across the three datasets.The most outstanding and robust finding is the large coefficient for lagged housing wealth. The stock wealth effects reported in Table 11 are all statistically insignificant. Furthermore, in 2 of the 3 estimations, the size of the stock wealth effect is economically small. The hypotheses of equal housing wealth and stock wealth coefficients are, however, accepted in 2 out of 3 estimations.
Best Data | Good Data | Combined Data | |
![]() | 0.259 | 0.273 | 0.437![]() |
(0.326) | (0.288) | (0.307) | |
![]() | 0.267 | -.017 | -.020 |
(0.27) | (0.078) | (0.079) | |
![]() | 0.398![]() | 0.246![]() | 0.237![]() |
(0.201) | (0.099) | (0.083) | |
Test of ![]() ![]() | 0.136 | 3.609 | 4.068 |
(Accepted) | (Accepted) | (Rejected) | |
Obs. | 24 | 90 | 90 |
![]() | 0.335 | 0.043 | 0.118 |
Partial ![]() | 0.134 | 0.045 | 0.085 |
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