N22 | Macro Paper Warehouse

Does Deposit Insurance Promote Deposit Stability? Evidence from the Postal Savings System during the 1920s

Mon, 01 Jan 0001 00:00:00 +0000

Overview

Research question. Does deposit insurance promote financial depth by arresting the outflow of deposits from the banking system during periods of bank distress? The paper tests and quantifies the deposit-stabilizing effect of state-level deposit insurance schemes operating in the United States during the 1920s.

Setting and identification. Between 1908 and 1929, eight primarily Midwestern states adopted some form of deposit insurance. The paper exploits the discontinuity in deposit insurance coverage at state borders to identify the causal effect of insurance on depositor behavior. The identification strategy compares outcomes in contiguous city pairs straddling deposit-insurance (DI) and non-deposit-insurance (NDI) state borders — a quasi-experimental design that controls for observed and unobserved confounders by using narrow geographic areas where the only relevant policy difference is the presence or absence of deposit insurance.

Proxy for “mattress money.” The paper uses postal savings deposits as a proxy for money withdrawn from the banking system. The U.S. Postal Savings System (established 1911) was backed by the full faith and credit of the federal government, with a maximum individual account limit of $2,500, and was widely viewed as a far safer alternative to commercial bank deposits. The authors validate this proxy by demonstrating, via Johansen cointegration tests, that the nationwide ratio of postal savings balances to total bank deposits is cointegrated (rank 1) with the currency-deposit ratio — a well-established indicator of banking distress.

Data. The empirical analysis covers 1921–1929. The main postal savings dataset is drawn from Annual Reports of the Postmaster General. Bank suspension data are drawn from FDIC manuscript lists compiled in the 1930s by FDIC economist Clark Warburton, providing location, charter type, and suspension/reopening dates. The sample includes 74 city pairs across 14 states (7 DI: North Dakota, South Dakota, Nebraska, Kansas, Oklahoma, Texas, Mississippi; 7 NDI: Minnesota, Iowa, Missouri, Arkansas, Louisiana, Tennessee, Alabama), with an average distance between paired cities of approximately 18 miles.

Main findings — postal savings regressions (Table 4). Using OLS with city-pair and year fixed effects and standard errors clustered at the NDI city level, the paper finds that following a bank suspension within a 10-mile radius, postal savings deposits in NDI cities grew 16 percent more than deposits in the corresponding DI city. The effect is positive and statistically significant at the 20-mile radius but smaller — approximately 9 percent — and is statistically indistinguishable from zero at the 30-mile radius. The localized decay with distance is consistent with a geographically contained flight-to-safety response. Critically, when the same specification is estimated for periods after deposit insurance was discontinued, the effect at all radii is statistically nil, providing a falsification test ruling out omitted unobserved factors as the driver.

Persistence of effects (Table 5). Arellano-Bond GMM dynamic panel regressions confirm that the disintermediation effects are persistent. The lagged dependent variable enters with a negative and statistically significant coefficient (approximately −0.20 for the 10-mile regression), indicating mean reversion, but the bank suspension coefficients remain robust. Implied long-run effects for the 10-mile and 20-mile equations are approximately 0.151 and 0.100, respectively, suggesting sustained rather than transitory deposit diversion away from the banking system in the absence of deposit insurance.

Banking capacity (Table 6). Because the postal savings deposit limit constrained the intake of funds — particularly severely during distress episodes, as documented through narrative evidence from the 1915 Congressional Record — the postal savings regressions underestimate the true effect of deposit insurance. The paper therefore estimates an alternative specification at the county level, comparing deposits at state-chartered banks in paired DI and NDI border counties. The results indicate that deposit insurance is associated with approximately a 56 percent increase in county-level deposits at state-chartered banks (coefficient 0.574, significant at 5 percent, robust to inclusion or exclusion of year fixed effects). By contrast, the analogous coefficient for national banks — which were prohibited by the OCC from participating in state deposit insurance schemes — is positive but statistically insignificant, providing a placebo test consistent with the interpretation that deposit insurance, not unobserved county characteristics, drove the banking capacity difference.

Scope conditions. All effects are estimated for state-chartered bank deposits in predominantly agricultural, Midwestern border counties during 1921–1929, a period characterized by an average annual bank suspension rate of 2.22 percent (versus 0.3 percent during 1911–1920). The paper acknowledges that state deposit insurance schemes of this era generated moral hazard (as established by prior literature), and frames the contribution as quantifying the stability-enhancing component rather than the net welfare effect.

Policy implication. The 56 percent banking capacity differential implies that deposit runoffs in the absence of insurance are substantially higher than the 3–10 percent runoff rates assumed in the Basel III Liquidity Coverage Ratio (LCR) framework, and more consistent with the 25–50 percent runoffs observed in non-systemic institutions in Denmark following an exogenous reduction in deposit insurance limits (Iyer et al., 2016).

In depth

Q1. Why is the Postal Savings System a valid proxy for “mattress money,” and what evidence supports this?

The postal savings system was backed by the full faith and credit of the United States, making it categorically safer than commercial bank deposits, and was explicitly designed to attract savings hidden in mattresses. The authors validate the proxy empirically by showing that the nationwide ratio of postal savings balances to total bank deposits is cointegrated (Johansen test, rank 1) with the currency-deposit ratio — a series that rises during banking distress as depositors convert bank funds to currency. Contemporary narrative accounts from the 1915 Congressional Record further confirm that postal savings offices experienced sharp deposit inflows during local banking distress, with deposit intake frequently constrained by the $2,500 individual account cap.

Q2. What is the identification strategy, and why does it address endogeneity concerns?

The strategy exploits the discontinuity in deposit insurance at state borders by comparing relative postal savings deposit growth in contiguous city pairs — one city in a DI state, one in an adjacent NDI state — conditioning on bank suspensions within 10, 20, or 30 miles. The authors argue that deposit insurance legislation was a statewide political decision driven largely by partisan composition (Democrats favored it, Republicans opposed it), making it implausible that interests concentrated at border cities systematically determined which states adopted it. Six of the seven NDI control states introduced deposit insurance legislation but failed to pass it, underscoring that the policy variation was not determined by border-specific characteristics. A falsification test using the same city pairs after deposit insurance was discontinued shows zero effects, ruling out time-invariant unobserved heterogeneity as the driver.

Q3. What are the main quantitative results from the city-pair postal savings regressions?

Following a bank suspension within 10 miles, postal savings deposits in NDI cities grew 16 percent more than in DI cities (coefficient 0.162, significant at 5 percent). At the 20-mile radius the differential is approximately 9 percent (coefficient 0.0933, significant at 5 percent). At the 30-mile radius the coefficient is 0.0997 and statistically indistinguishable from zero. These results are estimated with OLS using city-pair and year fixed effects and standard errors clustered at the NDI city level, based on 524 observations for the 10- and 20-mile specifications and 66 observations for the post-discontinuation falsification regressions.

Q4. How does the paper establish that distance matters for the flight-to-safety effect?

The monotonic decline in the estimated coefficient from 0.162 (10 miles) to 0.093 (20 miles) to a statistically insignificant 0.100 (30 miles) indicates that the diversion of deposits into postal savings was geographically localized. This pattern is consistent with depositors responding primarily to nearby bank failures rather than to distant ones, and it supports the interpretation that the effect is driven by local banking distress rather than by state-level or regional macroeconomic shocks that would affect all pairs symmetrically.

Q5. Are the disintermediation effects of bank suspensions temporary or persistent?

The Arellano-Bond GMM dynamic panel regressions (Table 5) show that the effects are persistent. The lagged dependent variable coefficient is approximately −0.205 (10-mile) and −0.188 to −0.201 (20-mile), indicating partial mean reversion but not full reversal. Year-1, Year-2, and implied long-run dynamic effects are all statistically significant and of similar magnitude (approximately 0.145–0.152 for the 10-mile equation and 0.096–0.100 for the 20-mile equation), indicating that once depositors shift funds to postal savings in response to bank suspensions, a substantial portion of the effect persists in subsequent years. This is consistent with prior literature showing that deposits leave the banking system quickly but return slowly.

Q6. Why are the postal savings coefficient estimates considered a lower bound on the true effect of deposit insurance?

Two institutional features constrained the postal savings system from fully capturing flight-to-safety deposits. First, individual accounts were capped at $2,500, and narrative evidence shows that this limit was severely binding during distress — depositors attempted to place far more than the ceiling allowed. Second, the re-depositing rate of postal savings funds back into local banks was not 100 percent: during 1921–1923 only 32–47 percent of postal savings deposits were re-deposited in banks, compared to 72–82 percent in calmer years. Because the postal savings system could not absorb unlimited deposits and did not fully recycle absorbed funds into local banking, its level understates the true flight of deposits from the banking system in NDI states.

Q7. How does the county-level banking capacity test address the censoring problem?

The paper estimates log-ratio regressions comparing county-level deposits at state-chartered banks in DI versus NDI border counties, using a “DI Active” indicator that switches on when deposit insurance is in effect in a given state-year and switches off when schemes are discontinued. Because different states discontinued their insurance at different times, there is sufficient within-county variation to identify the DI coefficient even with year fixed effects. The estimated coefficient of 0.574 (without year FE) and 0.557 (with year FE) translates to approximately a 56 percent higher deposit level in state-chartered bank counties with deposit insurance, with virtually identical estimates across specifications.

Q8. What is the placebo test for national banks, and what does it show?

National banks were prohibited by the Office of the Comptroller of the Currency from participating in state deposit insurance schemes. If deposit insurance — rather than unobserved county characteristics — is responsible for the 56 percent banking capacity premium, then county deposits at national banks in DI states should show no corresponding premium. The Table 6 results confirm this: the DI Active coefficient for national bank deposits is positive (0.165 to 0.267) but statistically insignificant, providing a falsification result consistent with the causal interpretation for state-chartered banks.

Q9. How does the paper situate deposit insurance’s stabilizing benefits relative to its moral hazard costs?

The paper explicitly frames its contribution as quantifying the stability-enhancing component of deposit insurance separately from the moral hazard component. It cites extensive prior literature (Calomiris 1992, 1993; Wheelock 1992, 1993; Wheelock and Wilson 1994) establishing that the 1910s–1920s state schemes generated moral hazard: insured banks reduced capital-to-asset ratios, relaxed lending standards, and increased risk exposure. The paper does not contest those findings but argues that the two effects are analytically separable and that the stabilization benefit had significant quantitative magnitude — a benefit that should be accounted for when assessing the net welfare effects of deposit insurance design.

Q10. What are the implications for the Basel III Liquidity Coverage Ratio framework?

The Basel III LCR formula assumes that during distress 3 percent of “stable deposits” and 10 percent of “less stable deposits” run off. The paper’s finding that deposit insurance is associated with a 56 percent increase in banking capacity implies that in the absence of insurance, deposit runoffs are far higher than these Basel assumptions — substantially larger than 10 percent and more consistent with the 25–50 percent runoffs observed for non-systemic banks in Denmark following an insurance limit reduction (Iyer et al. 2016). The authors argue their results suggest that empirical grounding for the LCR runoff assumptions remains insufficient, consistent with critiques by Allen (2014) and Diamond and Kashyap (2016).

Key Concepts

Postal Savings System (as “mattress money” proxy). The U.S. Postal Savings System (1911–) accepted deposits up to $2,500 per individual, backed by the full faith and credit of the United States. In this paper, postal savings deposits are used as a quantitative proxy for money withdrawn from the banking system during distress — “money under the mattress” — validated by cointegration with the currency-deposit ratio.

Policy discontinuity / border-pair design. The identification strategy exploits the fact that deposit insurance was adopted at the state level, creating a sharp policy discontinuity at state borders. Contiguous city pairs straddling DI and NDI state borders are treated as quasi-experimental units, with the within-pair difference in postal savings deposit growth serving as the outcome, controlling for time-invariant city-level heterogeneity and common time effects.

Relative Postal Savings Deposit Growth (RPS). The dependent variable defined as the log-ratio of postal savings deposits in the NDI city to postal savings deposits in the DI city within a pair, and then first-differenced over time. This construction controls for city-pair-level time-invariant characteristics and isolates the differential response to bank suspensions.

Bank suspension. In this paper’s context, a bank suspension is any closure of a bank (state-chartered or national) at a specific geographic location, as recorded in FDIC manuscript lists compiled by Clark Warburton during the 1930s. The variable used in regressions is the change in the number of suspensions within R miles (R = 10, 20, 30) of the paired postal savings offices.

Financial depth / local banking capacity. The paper uses county-level deposits at state-chartered banks as a measure of local banking market size. Deposit insurance is hypothesized to increase financial depth by preventing the diversion of funds out of the banking system during distress, and the 56 percent estimated premium is the paper’s primary measure of the insurance’s capacity-enhancing effect.

DI Active indicator. A time-varying binary variable equal to 1 when deposit insurance was legally in effect in a given state at a given time, and 0 otherwise (including after repeal). Because different states repealed their schemes at different times (Oklahoma 1923, Texas 1927, South Dakota 1927, North Dakota 1929, Kansas 1929, Nebraska 1930, Mississippi 1930), this variable provides within-county variation that identifies the banking capacity coefficient after controlling for county and year fixed effects.

Moral hazard vs. stability-enhancing components. The paper distinguishes analytically between the moral hazard effect of deposit insurance (insured banks undertake riskier projects, reduce capital buffers, relax lending standards) and the stability-enhancing effect (depositors retain funds in the banking system, preventing runs). The paper’s contribution is to quantify the latter component in isolation, using a setting where the two effects can be separated by focusing on depositor — rather than banker — behavior.

Failing Banks

Mon, 01 Jan 0001 00:00:00 +0000

Correia, Luck, and Verner ask a foundational question in banking: why do banks fail? Specifically, they seek to adjudicate between two theoretical views — the solvency view (failures caused by deteriorating asset quality and insolvency) and the bank runs view (failures caused by depositor coordination failure that can bring down otherwise solvent banks) — using the longest micro-level panel of U.S. commercial bank balance sheets assembled to date.

The authors construct a panel covering approximately 37,000 distinct banks across two samples: a historical sample of all national banks from 1863 to 1941 (sourced from OCC Annual Reports, digitized via OCR) and a modern sample of all commercial banks from 1959 to 2024 (from FFIEC Call Reports merged with the FDIC failure list). More than 5,000 banks fail across the full sample, with 2,887 failures before 1935 and 2,233 after 1959. The sample spans institutional regimes before and after the Federal Reserve (founded 1913) and the FDIC (founded 1933/1934).

Three sets of findings emerge. First, failing banks are characterized by deteriorating fundamentals well before failure: rising non-performing loans and declining solvency (equity-to-assets falls by 8 percentage points in the five years before failure in the modern sample), increasing reliance on expensive noncore funding (rising by 18% of assets in the decade before modern-era failures), and a boom-bust pattern in real assets (expanding by 34% from ten years to three years before failure before contracting). These patterns are consistent across the pre-FDIC and modern eras.

Second, bank failures are highly predictable from publicly available accounting data. Using simple regression models with insolvency risk, noncore funding reliance, and asset growth as predictors, the area under the ROC curve (AUC) for predicting failure within one year reaches 86% in the historical sample and 90–95% in the modern sample. Pseudo-out-of-sample performance is nearly as strong as in-sample performance. A bank in the top 5th percentile of both insolvency risk and noncore funding vulnerability faces a three-year failure probability of 27% in both the historical and modern samples, compared to unconditional rates of 2.5% (historical) and 1% (modern) — a 10- to 25-fold increase.

Third, while large deposit outflows consistent with bank runs were common in pre-FDIC failures — deposits declined on average by 14% immediately before failure in 1880–1934, and by 21% in the period before the banking holiday — failures with runs are as predictable as failures without runs, and they occur in banks with similarly weak fundamentals. Recovery rates on failed banks’ assets averaged only 52% of book value in pre-FDIC failures. Using a framework comparing recovery rates to leverage, the majority of pre-FDIC failed banks appear to have been fundamentally insolvent. Even under the extreme assumption of zero value destruction from failure, runs on banks that were not fundamentally insolvent account for fewer than 8% of pre-FDIC failures; under an assumption of 20% value destruction from failure, this share rises to 22%.

OCC bank examiners classified fewer than 2% of pre-FDIC failures as caused by runs or liquidity issues; most were attributed to losses, fraud, or external shocks. The aggregate failure rate is also largely predictable: regressing the actual bank failure rate on predicted aggregate failure risk yields an R-squared of 40%.

Scope conditions: the historical sample covers only national banks (market share ranging from ~80% in the 1870s to ~45% in the 1930s); the modern sample excludes de novo banks (younger than three years); deposit outflow data for the historical period begin in 1880; and FDIC failure transaction data for the modern period begin in 1993.

Q: What are the two main theoretical views the paper evaluates, and how does the paper distinguish between them? A: The solvency view holds that bank failures are caused by deteriorating asset quality and insolvency, with the runnable nature of liabilities playing no essential causal role. The bank runs view holds that the runnable nature of demandable deposits is central, with depositor coordination failure capable of bringing down otherwise solvent banks (Diamond and Dybvig, 1983) or weak-but-solvent banks (Goldstein and Pauzner, 2005). The paper distinguishes between them using three empirical tests: predictability of failures from fundamentals, deposit outflows before failure, and asset recovery rates in failure.

Q: How predictable are bank failures, and what does predictability imply for the bank runs view? A: In the historical pre-FDIC sample (1863–1934), the in-sample AUC for predicting failure within one year is 86%; in the modern sample (1959–2024) it is 90–95%. Pseudo-out-of-sample AUC is nearly as strong as in-sample AUC. High predictability is consistent with the solvency view and fundamental-based panic run models, but is inconsistent with non-fundamental self-fulfilling runs (Diamond and Dybvig, 1983), which should strike randomly. Predictability also cuts against the assumption of rational, forward-looking depositors in fundamental-run models, since attentive depositors would act on observable signals and accelerate failure, reducing predictability.

Q: What is the boom-bust pattern in failing banks’ assets? A: In the decade before failure, failing banks’ real total assets expand by 34% from ten years to three years before failure, then contract over the final two years. The boom-and-bust pattern is present in both the historical and modern samples but is more pronounced in the modern period. The boom is driven primarily by loan growth (particularly real estate lending and C&I lending in the modern sample) rather than by growth in liquid assets, consistent with the view that rapid credit expansion produces future credit losses.

Q: How does noncore funding behave in failing banks, and why does it matter? A: In failing banks in the modern sample, noncore funding (time deposits plus wholesale funding) rises by 18% of assets over the decade before failure, while demand deposits decline as a share of assets. In the historical sample, noncore (wholesale) funding also rises gradually. Noncore funding is a signal of failure for multiple reasons: it is more expensive than core deposits, eroding profitability; it can finance risky asset growth; it reflects realized losses being funded at the margin; and it increases funding fragility, making banks more vulnerable to shocks.

Q: How strong is the joint signal from insolvency and noncore funding? A: A bank in the top 5th percentile of both insolvency risk and noncore funding vulnerability faces a three-year failure probability of 27% in the historical sample and 27% in the modern sample. The unconditional three-year failure probability is 2.5% in the historical sample and 1% in the modern sample. This amounts to a 10- to 20-fold increase in failure probability, illustrating that the combination of solvency and funding weakness is a powerful joint predictor.

Q: Were deposit outflows common before the FDIC, and did they decline after its introduction? A: In the 1880–1934 historical sample, deposits in failing banks declined on average by 14% between the last call report and failure, with 25% of pre-FDIC failures preceded by outflows exceeding 20%; during the period before the banking holiday the average deposit decline was 21%. In contrast, in the modern sample (1993–2024), average pre-failure deposit outflows were only 2.5%, and outflows exceeding 20% occurred in only 3% of failures, consistent with deposit insurance insulating most depositors.

Q: Are failures with large deposit outflows (runs) less connected to weak fundamentals than other failures? A: No. The paper finds that failures with large deposit outflows are as predictable as failures without large deposit outflows. The relationship between insolvency risk or noncore funding and three-year failure probability is similar for failures with and without large deposit outflows. This implies that runs did not disproportionately strike banks with otherwise strong fundamentals.

Q: What do asset recovery rates reveal about the insolvency status of pre-FDIC failed banks? A: Recovery rates on pre-FDIC failed banks averaged 52% of book value of assets. Under the extreme assumption that receivership destroys zero bank value, runs on non-fundamentally-insolvent (weak but solvent) banks account for fewer than 8% of pre-FDIC failures. Under the equally extreme assumption that failure destroys 20% of bank value, this share rises to 22%. The majority of pre-FDIC failed banks therefore appear to have been fundamentally insolvent.

Q: What did contemporary OCC bank examiners attribute as the causes of bank failures? A: OCC bank examiners classified most pre-FDIC failures as caused by losses, fraud, or external economic shocks. Runs and liquidity issues together account for fewer than 2% of OCC-classified failures, notwithstanding the common occurrence of large deposit outflows before many of these failures. This examiner evidence supports the solvency view.

Q: Can bank-level fundamentals predict systemic banking crises and aggregate failure waves? A: Yes. The authors aggregate out-of-sample predicted failure probabilities to construct a predicted aggregate bank failure rate. The R-squared from regressing the actual aggregate bank failure rate on this predicted rate is 40%, indicating that spikes in bank failures during systemic crises are substantially accounted for by the prior deterioration of bank-level fundamentals.

Q: Why is predictability higher in the modern sample than in the historical sample? A: The authors identify several reasons. Accounting data quality is higher in the modern sample. Historical national banks operated as unit branches with less geographic diversification, making idiosyncratic shocks more important and harder to predict. Modern-era failures are preceded by larger lending booms that produce more predictable downstream losses. Additionally, in the modern context bank failures are largely supervisory decisions, and frictions in the supervisory process may delay closure and thereby increase predictability.

Q: What role do the authors assign to depositor inattention? A: The high predictability of failures combined with the finding that many failing banks had high predicted failure probabilities before actually failing suggests that depositors were often slow to react to observable signals of bank weakness. The authors note this points to behavioral frictions such as neglect of downside risk (Gennaioli et al., 2012) and sleepy or inattentive depositors (Hanson et al., 2015; Jiang et al., 2023), rather than the rational, forward-looking depositor assumption embedded in standard bank run models.

Q: What is the paper’s overall interpretive conclusion about the relative importance of solvency versus runs? A: The primary cause of bank failures is almost always and everywhere a deterioration of bank solvency. Runs were more common in the historical pre-FDIC data as a mechanism triggering failure, but they typically closed banks that were already fundamentally insolvent. Non-fundamental, self-fulfilling runs on otherwise healthy banks appear to be an uncommon cause of bank failures. Under the solvency view, even when runs occur, they are the trigger and final mechanism rather than the root cause.

Insolvency risk: A bank’s proximity to default, proxied in the historical sample by surplus profits relative to equity (capturing profitability and capitalization) and in the modern sample by net income to assets. High insolvency risk reflects declining profitability and eroding capital buffers.

Noncore funding: Expensive, risk-sensitive funding sources outside core demand deposits, including time deposits, wholesale funding (bills payable, rediscounts), and non-deposit wholesale borrowings. Banks relying heavily on noncore funding face higher funding costs, reduced profitability, and greater fragility to funding shocks.

Fundamental run: A run triggered when bank fundamentals are so weak (theta at or below the lower threshold in the Goldstein-Pauzner framework) that all depositors have an incentive to withdraw regardless of others’ actions — the bank is effectively insolvent and failure is inevitable.

Panic-based run: A run triggered when bank fundamentals are moderately weak (below the threshold equilibrium in Goldstein-Pauzner) but the bank would have been able to pay all creditors absent the run; the run itself destroys value and causes failure.

Non-fundamental (self-fulfilling) run: A run on an otherwise solvent bank driven purely by depositor coordination failure, as in Diamond and Dybvig (1983); failure arises from one of two equilibria and is not predicted by fundamentals.

Recovery rate: Funds ultimately collected by the receiver throughout receivership proceedings divided by the book value of assets at suspension; used as a proxy for the degree of fundamental insolvency at failure. Pre-FDIC recovery rates averaged 52% of book value.

Area Under the ROC Curve (AUC): A measure of binary classification performance used to quantify the predictability of bank failures; an uninformative predictor has AUC of 0.5, while AUC of 1.0 indicates perfect classification. In this paper, AUC ranges from 86% (historical, one-year horizon) to 95% (modern).

Boom-bust pattern: The systematic tendency of failing banks to experience rapid loan-driven asset growth in the years preceding failure followed by asset contraction in the final two years before failure — present in both the historical and modern samples, more pronounced in the latter, with real assets expanding by 34% from ten to three years before failure.

The Price of Housing in the United States, 1890–2006

Mon, 01 Jan 0001 00:00:00 +0000

Lyons, Shertzer, Gray, and Agorastos construct the first consistent, annual, quality-adjusted market rent and home sales price series for American cities spanning 1890–2006. The paper addresses a fundamental data gap: no annual city-level series existed for market rents at any point in the 20th century, and no annual city-level sales price series existed prior to 1975. Existing national series—the BLS Rent of Primary Residence (RoPR) for rents and the Shiller index for sales—carry well-documented methodological limitations that the authors argue have produced materially misleading stylized facts about long-run U.S. housing markets.

The Historical Housing Prices (HHP) dataset draws on just under 2.7 million newspaper real estate listings from 30 U.S. cities across 1890–2006. Listings must contain a price, a size measure (rooms or bedrooms), property type (house or apartment), and a location indicator. The authors construct hedonic price indices using a rolling-windows methodology—baseline three-year rolling windows with annual step size—that controls for size, type, and standardized within-city location, allowing coefficients to vary over time rather than imposing a fixed vector across the full century. City-level indices are aggregated to national indices using population weights from census data interpolated between census years. Listed prices serve as proxies for transaction prices; the authors validate these against census distributions and against post-1975 FHFA and Case-Shiller series.

The paper’s findings revise several established stylized facts. First, real market rents did not fall over the 20th century as implied by the RoPR series. Instead, real rental price levels were approximately 20% higher in 2006 than in 1890, fluctuating within a relatively narrow band. The RoPR series, by contrast, implies a near-halving of real rents between 1914 and 2006. Second, the paper documents a substantial interwar housing boom-bust absent from the Shiller index: real sales prices rose approximately 47% between 1920 and 1928, then fell 27% by 1935, with the 1928 peak not recovered in real terms until 1968. Third, contrary to the Shiller index’s depiction of minimal housing price growth from 1950 to 1995, the HHP series shows real sales prices rising 21% between 1953 and 1974—a period for which Shiller relies on a truncated sample of government-backed mortgages that excluded higher-valued homes.

On the return to homeownership, the paper finds average nominal housing returns across 1890–2006 of approximately 11% per year, composed of 3.8% capital gain and 7.2% rental return. Gross market rental yields exceeded 8% annually for much of 1900–1945, fell to 7% by 1960, and to 3% by 2006. Capital gains were largely unimportant before the 1940s and became the dominant return component only from 1970 onward; the post-1980 period with sustained capital gains is characterized as historically anomalous. Returns varied substantially across cities, with some cities outperforming the S&P 500 in the prewar era while most underperformed equities from 1981–2006.

The paper also examines implications for the CPI. The HHP series implies nominal rents grew at approximately 3.5% per year from 1914 to 2006, versus 2.6% per year for the RoPR component. A back-of-the-envelope alternative CPI using HHP rental data yields overall price growth of 3.3% per year rather than the official 3.1%, suggesting the measured increase in U.S. living standards since World War I may be modestly overstated. Finally, cross-city analysis shows that land constraints and, increasingly, regulatory constraints explain divergence in price growth across cities, with the role of zoning becoming more pronounced after 1980.

Q: What is the core data source and how are the indices constructed? A: The HHP dataset comprises just under 2.7 million newspaper real estate listings from 30 U.S. cities, 1890–2006, sampled from real estate sections (typically the last Sunday of each month). Valid listings require price, size, property type, and within-city location. Hedonic indices are estimated using rolling three-year windows with annual steps, controlling for size, type, and standardized location, allowing hedonic coefficients to evolve over time rather than imposing a fixed vector. City indices are aggregated to national indices using population-weighted census data interpolated between census years.

Q: Why are the HHP series based on listing prices rather than transaction prices, and how is this limitation addressed? A: Transaction-price records require local archival effort infeasible across 30 cities over 116 years, and rental transaction data are essentially unavailable historically. The authors argue that hedonic mix-adjustment makes listed prices strong predictors of selling prices during normal market conditions, and that a substantial share of houses transact at their exact listing price. Validation against census distributions and against post-1975 FHFA and Case-Shiller series supports the approach; the authors acknowledge listing prices may diverge from transaction prices at cyclical peaks and troughs.

Q: What does the paper find about the long-run trajectory of real market rents, and how does this revise existing understanding? A: The HHP series shows real rental price levels in 2006 were approximately 20% higher than in 1890 or 1914, fluctuating within a relatively narrow band over the century. The BLS RoPR series implies real rents fell by nearly half between 1914 and 2006. The HHP findings align with the most influential proposed corrections to the RoPR by Gordon & van Goethem (2007) for 1915–1939 and broadly with Crone et al. (2010) in terms of overall growth levels for 1940–1995, though the HHP series shows a sharper rental spike after World War II rent controls were lifted that the BLS methodology captures only with deliberate lag.

Q: What does the paper find about the interwar housing cycle, and why does the Shiller index miss it? A: The HHP series documents that real sales prices rose approximately 47% between 1920 and 1928, then fell 27% by 1935, with the 1928 nominal peak not regained until 1946 and the real peak not until 1968. The Shiller index for 1890–1934 is based on a 1934 survey of owner recollections of past transaction prices and assessed values, which the authors argue reflects homeowners’ lack of awareness of the changing value of their homes over prior decades. The HHP finding is consistent with census data, Nicholas & Scherbina’s study of New York City, and Fishback & Kollmann’s analysis of New Deal reports.

Q: What does the paper find about the 1953–1974 period, and what explains the divergence from the Shiller index? A: The HHP series shows housing sales prices increased 21% in real terms between 1953 and 1974, while the Shiller index (based on the Home Purchase Component of the CPI) implies a moderate decline of around 10%. The Shiller index for this period uses a truncated sample of government-backed mortgages subject to FHA loan limits; when the authors truncate their own data using the same statutory FHA limits ($30,000 in 1973, $45,000 in 1974, $60,000 in 1977), approximately 50% of their 1971–1979 listings are excluded and their truncated series matches the Shiller index more closely. This supports the Greenlees (1982) critique of downward bias in the Home Purchase CPI component.

Q: What are the long-run return components to homeownership at the national level? A: Average nominal housing returns across 1890–2006 were approximately 11% per year: 3.8% capital gain and 7.2% rental return. Before World War II (1890–1945), average nominal rental returns ranged from 7.9% to 8.3% per sub-period while capital gains averaged near zero or negative in real terms. Only in 1981–2006 did capital gains (averaging 5.8%) exceed the rental return (averaging 5.3%). The return to housing has thus been dominated by rental income over the long run, with the post-1980 era of sustained capital gains constituting a historical anomaly.

Q: How do rental yields evolve over the sample period? A: Gross market rental yields exceeded 8% annually for much of 1900–1945, with spikes after both World Wars and a dramatic fall from nearly 11% to below 7% during the early 1920s boom, consistent with a bubble dynamic before the Great Depression. Yields fell to approximately 7% by 1960 and to 3% by 2006. City-level heterogeneity was substantial: rental returns exceeded 15% in some cities in the two decades before the Great Depression, and most cities saw returns above 10% nominally during 1930–1945, while even by 1981–2006 cities like Phoenix and St. Louis averaged above 12%.

Q: What does the paper find about housing and the business cycle? A: Real growth rates in GDP and housing prices moved in the same direction in 72 of 116 years for sales prices and 65 of 116 years for rental prices. The paper identifies three major downturns where falling rents led falling prices which led falling GDP: the Great Depression (rents fell from 1924, prices from 1929, GDP from 1930), the early 1990s recession (rents from 1988, prices from 1990, GDP from 1991), and the end-of-sample period (rents from 2002). Only after World War I (1920–21) and World War II (1945–46) did clear economic contractions occur without equivalent housing price downturns.

Q: What does the paper find about cross-city variation in housing returns, and what does this imply for the volatility puzzle? A: Capital gains and rental returns vary substantially across cities and time periods; some cities saw returns exceeding the S&P 500 before World War II (including New York and Chicago), while most underperformed equities from 1981–2006. The authors argue that the apparently low volatility of housing returns at the national level documented by Jordà et al. (2019) is partly an aggregation artifact: local housing markets with very different trajectories are combined into a national index, dampening measured variance. The mild positive correlation between city-level capital gains and rental returns has an R² of 0.24.

Q: What are the implications for CPI measurement? A: The HHP series implies nominal rents grew at approximately 3.5% per year from 1914 to 2006, compared with 2.6% per year for the BLS RoPR component, with higher growth concentrated in the years after both World Wars and in the 1965–1985 period. A back-of-the-envelope alternative CPI substituting HHP rental data yields overall price growth of 3.3% per year rather than the official 3.1%. If rental price growth before 1985 is understated in the BLS data, then there has been less improvement in the U.S. standard of living since World War I than was previously understood.

Q: What does the paper find about the role of supply constraints in explaining cross-city price divergence? A: Natural land constraints are positively linked to price growth throughout the 20th century, with the relationship sharpest during 1930–1945 (before the postwar suburban expansion) and again after 1980. Regulatory constraints—measured at the turn of the millennium—have become an increasingly important driver of cross-city price differences, consistent with zoning functioning as a tax (Gyourko & Krimmel 2021). The paper also finds evidence suggesting land-use regulations are partly driven by expectations of future price growth, consistent with the homeowner-voter hypothesis (Fischel 2015; Trounstine 2018).

Q: How does the paper validate its series against existing sources? A: The HHP rental series aligns closely with the Rees and Jacobs (1961) series for 1890–1914. For sales, the HHP series matches the Case-Shiller-Weiss and FHFA repeat-sales indices at both national and city level after 1990 despite methodological differences. The paper finds approximately 25% more price growth than the CSW series over 1975–2006 (117% versus 90% in the 30 HHP cities), attributing some of the divergence to OFHEO appraisal-based valuations before 1992 and the HHP coverage of the broader owned housing market beyond single-family homes.

Historical Housing Prices (HHP) Project: A dataset of just under 2.7 million newspaper real estate listings from 30 U.S. cities, 1890–2006, used to construct annual, quality-adjusted hedonic price indices for both rented and owned housing segments at the city and national level.
Rolling-windows hedonic methodology: An index construction approach that runs sequential hedonic regressions over two-, three-, or five-year overlapping windows with annual step size, allowing the coefficients on size, type, and location to evolve over time rather than imposing a fixed vector across the full sample period, reducing bias from unobserved quality changes.
Market rent vs. contract rent: Market rent (the listing price for a rental unit actively advertised) is conceptually distinct from contract rent (the rent paid by tenants currently in situ), which is what the BLS RoPR series measures. Market rents adjust to vacancy and lease resets faster than contract rents, producing substantially more short-run volatility and a materially different long-run trend.
Gross rental yield (rent-to-price ratio): Annual rental income from a property divided by its market sales price, computed as RI_{c,t} / HPI_{c,t}. Gross yields exceeded 8% annually for much of 1900–1945 and fell to 3% by 2006 nationally, making rental income the dominant component of total housing returns for most of the century.
Total return to housing: The sum of the capital gain (percentage change in sales price) and the rental return (rental income divided by sales price), computed at annual, city, and national frequency for 1890–2006. The average nominal total return was approximately 11% per year, with 3.8% from capital gains and 7.2% from rental income.
Rent of Primary Residence (RoPR): The BLS survey-based series measuring changes in contract rents for a rotating panel of rental units, used as the shelter component of the CPI. The HHP series implies this series understates rental price growth by approximately 0.9 percentage points per year (3.5% vs. 2.6% nominal growth), concentrated in post-World War periods and 1965–1985, due to tenant non-response bias and delayed incorporation of new construction.
Supply constraints and cross-city divergence: Natural land constraints (geographic barriers to development) and regulatory constraints (zoning and land-use regulation) that limit housing supply, both positively associated with price growth, with regulatory constraints becoming increasingly important after 1980 and consistent with the hypothesis that land-use regulations are partly driven by homeowner expectations of future price appreciation.