R31 | Macro Paper Warehouse

Do Credit Conditions Move House Prices?

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

Overview

Research Question. To what extent did an expansion and contraction of credit drive the 2000s housing boom and bust? The existing literature offers sharply divergent answers — ranging from credit explaining virtually none of the boom (Kaplan, Mitman, and Violante 2020) to credit explaining the majority of it (Favilukis, Ludvigson, and Van Nieuwerburgh 2017, who find credit alone explains 60% of the rise in price-to-rent ratios). Greenwald and Guren argue that the source of these divergent findings is a single structural assumption: the degree to which credit-insensitive agents (landlords and unconstrained savers) can absorb credit-driven demand for housing, which in turn depends on the degree of segmentation between the owner-occupied and rental housing markets.

Key Mechanism. The paper organizes the literature around a “tenure supply” curve, defined in price-rent ratio versus homeownership rate space. A perfectly inelastic (vertical) supply curve — corresponding to perfect segmentation, in which housing cannot move between the owner-occupied and rental sectors — implies that credit expansion bids up house prices with no change in the homeownership rate. A perfectly elastic (horizontal) supply curve — corresponding to a frictionless rental market with deep-pocketed landlords who price at the present value of rents — implies that credit expansion raises the homeownership rate but not the price-rent ratio, because landlord reservation prices are unaffected by credit. Intermediate degrees of segmentation produce intermediate outcomes: credit raises both the price-rent ratio and the homeownership rate, with the relative magnitudes determined by the slope of the tenure supply curve.

Empirical Strategy. To measure where reality falls on this spectrum, the authors estimate the relative elasticity of the price-rent ratio to an identified credit supply shock, compared to the elasticity of the homeownership rate to the same shock. This ratio is a sufficient statistic for the slope of the tenure supply curve. They use three distinct identification strategies from prior literature — (1) Loutskina and Strahan (2015), instrumenting for local credit supply using differential city-level exposure to changes in the conforming loan limit (CLL); (2) Di Maggio and Kermani (2017), exploiting the 2004 OCC preemption of state anti-predatory-lending laws for national banks; and (3) Mian and Sufi (2019), using differential city-level exposure to the 2003 private label securitization (PLS) expansion through bank funding composition. Regressions are estimated on annual CBSA-level panels using local projection IV (LP-IV) or event-study reduced-form methods. Key data include the CoreLogic repeat-sales house price index, the CBRE Torto-Wheaton same-store rent index (a repeat-rent index for multi-unit apartment buildings, constructed from newly-leased units), and Census Housing Vacancy Survey homeownership rates.

Main Empirical Findings. All three instruments consistently find that credit supply shocks generate a significant increase in house prices and the price-rent ratio but a much smaller, rarely statistically significant, effect on the homeownership rate. Under the LS LP-IV, the price-rent ratio peaks at an increase of 0.471, while the homeownership rate response reaches only 0.037 at the 2-year horizon and peaks at 0.101 after 5 years. The ratio of price-rent to homeownership responses ranges from 3 to infinity across the three instruments and horizons. These estimates imply a substantial degree of segmentation — the no-segmentation model falls far outside the 95% confidence intervals at all horizons.

Structural Model and Calibration. The authors construct a general equilibrium model featuring a representative borrower, landlord, and saver, with long-term fixed-rate mortgages subject to loan-to-value (LTV) and payment-to-income (PTI) limits following Greenwald (2018). The key modeling innovation is within-type heterogeneity in the benefit of owning versus renting, captured by logistic distributions for both borrowers and landlords. The dispersion parameter of the landlord distribution (σω,L) governs the slope of the tenure supply curve and is calibrated to minimize weighted distance to the LS empirical impulse responses. The resulting benchmark calibration yields σω,L = 2.877, with the benchmark model’s price-rent-to-homeownership ratio between 6.98 and 9.31 depending on the horizon — consistent with the empirical estimates.

Quantitative Results on the 2000s Boom. The paper then uses the calibrated model to simulate a credit standard relaxation (LTV limits relaxed from 85% to 99%, PTI limits from 36% to 65%) from 1998 Q1 through 2007 Q1, with a reversion at the start of the bust. This credit relaxation alone explains 34% of the peak rise in price-rent ratios observed in the boom, with a lower bound of 26% accounting for parameter uncertainty. In contrast, the no-segmentation model explains -1%, while the full segmentation model explains 38%. Adding a 2 percentage point permanent decline in mortgage spreads alongside the credit standard relaxation allows the benchmark model to explain 72% of the observed rise in price-rent ratios and 80% of the rise in loan-to-income ratios, compared to only 4% in the no-segmentation model. In a “full boom” scenario where additional demand and supply shocks are added to match the entire boom in price-rent ratios and homeownership, removing the credit relaxation reduces the rise in price-rent ratios by 55% in the benchmark economy — larger than the 34% explained in isolation due to nonlinear interactions — compared to only 5% in the no-segmentation economy.

Scope Conditions and Extensions. These results apply to the benchmark calibration in which landlords do not use credit and saver housing demand is fixed. When landlords are allowed to use credit (LTV limit of 65% relaxed to 85% during the boom), the role of credit is strengthened: the recalibrated model explains 80% of the rise in price-rent ratios from combined credit and rate changes, suggesting the benchmark is a lower bound. When savers are allowed to frictionlessly trade housing with borrowers, credit explains 54% of the rise in price-rent ratios even after recalibration — a roughly 25% reduction relative to the benchmark 72%, representing what the authors characterize as an extreme lower bound given that saver housing markets are in practice substantially segmented due to indivisibility, quality, and location differences.

Policy Implications. The findings imply that macroprudential policies tightening LTV and PTI ratios can be effective at restraining house price growth, but only in the presence of the significant rental market segmentation found in the benchmark economy. In the no-segmentation economy, removing the credit relaxation from the full boom reduces price-rent ratio growth by only 5%.

In depth

Q1. What is the core theoretical insight that reconciles the divergent findings in the prior literature on credit and house prices?

The key difference is the degree to which credit-insensitive agents — specifically landlords and unconstrained savers — can absorb credit-driven demand for housing. Models with perfectly segmented rental markets (no rental sector or fixed homeownership rate) feature borrowers competing only with each other for a fixed stock, so credit expansion bids up prices. Models with frictionless rental markets feature deep-pocketed landlords who supply housing at a price equal to the present value of rents, which is unaffected by credit; credit expansion then raises the homeownership rate rather than prices. Intermediate degrees of frictions produce intermediate outcomes. This mechanism had not been recognized as the source of the literature’s divergence before this paper.

Q2. What is the “tenure supply curve” and why is its slope the key empirical object?

The tenure supply curve describes the menu of price-rent ratios at which landlords are willing to supply varying amounts of owner-occupied housing (given total housing stock), traced out in price-rent ratio versus homeownership rate space. Its slope determines how the equilibrium responds to a credit-induced demand shift: a steep (inelastic) supply curve translates credit expansion primarily into price-rent ratio increases; a flat (elastic) supply curve translates it primarily into homeownership rate increases. Identifying this slope empirically is therefore sufficient to discipline any macro-housing model’s predictions about the role of credit in price dynamics, for arbitrary underlying shocks.

Q3. How do the authors identify the slope of the tenure supply curve empirically?

They estimate the slope as the ratio of the causal elasticity of the price-rent ratio to that of the homeownership rate, with respect to an identified credit supply shock. Three instruments are used: (1) the Loutskina-Strahan shift-share instrument based on differential exposure to changes in the conforming loan limit, estimated by LP-IV on an unbalanced panel of 62 CBSAs from 1992 to 2016; (2) the Di Maggio-Kermani event study based on the 2004 OCC preemption of state anti-predatory-lending laws, covering 262 CBSAs for house prices and 82 CBSAs for homeownership from 2001 to 2010; and (3) the Mian-Sufi event study based on differential exposure to the 2003 PLS expansion via non-core deposit share, covering 245 CBSAs using ACS and FHFA data. In practice, they estimate the inverse slope (ratio of homeownership to price-rent response) because the first stage is far stronger using price-rent ratios as the endogenous variable.

Q4. What are the empirical results on the relative price-rent and homeownership responses?

Across all three instruments, credit supply shocks significantly raise the price-rent ratio but have a much smaller, rarely statistically significant effect on the homeownership rate. Under the LS LP-IV, the price-rent ratio peaks at 0.471 after 2 years, while the homeownership rate reaches only 0.037 at 2 years and peaks at 0.101 at 5 years. The naive point-estimate ratios range from 2.93 to 12.83 at horizons 2 through 5, with the 4-year estimate negative (implying an infinite slope). The directly estimated inverse slope coefficients are small (0.05 to 0.24) and never statistically different from zero. The DK instrument yields slopes of 6.72 in 2005, 3.67 in 2006, and 3.40 in 2007. The MS instrument yields a slope of approximately 4.49 in both 2006 and 2007. The lower bound of the 95% confidence intervals corresponds to slopes of at least 1.8 to 8.4.

Q5. What is the key modeling contribution on the structural side?

The key innovation is the introduction of within-type heterogeneity in ownership preferences for both borrowers and landlords, modeled as logistic distributions. This heterogeneity allows the model to generate a fractional and time-varying homeownership rate — a feature absent from most prior macro-housing models — and maps directly into the slopes of the demand and tenure supply curves. The dispersion in landlord ownership costs (σω,L) governs the supply curve slope and is calibrated to match the empirical impulse responses. Without this heterogeneity, the model would produce corner solutions with all housing owned by one type.

Q6. How is the landlord dispersion parameter σω,L calibrated, and what is the estimated value?

The calibration minimizes a weighted sum of squared deviations between model and data impulse responses for the price-rent ratio and homeownership rate, using the LS LP-IV estimates. Deviations are weighted by the inverse of empirical standard errors. Because model impulse responses jump on impact while empirical responses are hump-shaped (due to search frictions), the calibration uses only horizons 2 through 5 years. The minimum-distance estimate yields σω,L = 2.877, alongside a mortgage spread shock persistence of 0.965 and a shock size of -0.041 (corresponding to an annualized CLL subsidy of approximately 17 basis points, within the 10-24bp range found in prior literature). The benchmark model’s implied price-rent-to-homeownership response ratio ranges from 6.98 to 9.31, consistent with the empirical estimates.

Q7. What lower bound does the paper derive for σω,L, and how does the no-segmentation model compare?

A credible set for σω,L is derived by targeting the upper and lower bounds of the 95% confidence interval for the estimated inverse slope. The lower bound for σω,L (targeting the top of the confidence interval) is 0.810; the lower bound targets the bottom of the confidence interval but is best matched by the full segmentation case (σω,L → ∞). The no-segmentation economy (σω,L = 0) produces inverse ratios between 4 and 32 times the empirical upper bound, placing it far outside the credible set.

Q8. What is the model’s quantitative finding on the role of credit standard relaxation in isolation?

A credit standard relaxation (LTV from 85% to 99%, PTI from 36% to 65%) implemented from 1998 Q1 to 2007 Q1 and then reverted explains 34% of the peak rise in price-rent ratios in the benchmark model, with a lower bound of 26% conditional on parameter uncertainty. In the full segmentation model, the same relaxation explains 38%, while in the no-segmentation model it explains -1%. Credit standard relaxation also explains 51% of the rise in loan-to-income ratios in the benchmark, compared to 31% in the no-segmentation model.

Q9. What does adding a decline in mortgage rates contribute?

Adding a permanent 2 percentage point decline in mortgage spreads alongside the credit standard relaxation increases the benchmark model’s explained share of the price-rent ratio boom from 34% to 72%, and the loan-to-income ratio share from 51% to 80%. The no-segmentation model explains only 4% of the price-rent ratio boom and 38% of the loan-to-income ratio boom under the same combined experiment.

Q10. How does the “full boom” counterfactual estimate the marginal contribution of credit?

The full boom experiment adds exogenous demand shocks (shifts to µω,B) and supply shocks (shifts to µω,L) on top of the credit relaxation and rate decline, calibrated to exactly reproduce the observed peak increase in both the price-rent ratio and the homeownership rate during the boom. Removing the credit relaxation from this full boom scenario reduces the rise in price-rent ratios by 55% and the rise in loan-to-income ratios by 74% in the benchmark economy. This exceeds the 34% figure from the credit-alone experiment due to strong nonlinear interactions: without the credit relaxation, binding PTI limits constrain households’ ability to finance properties even when ownership preferences rise, dampening both price and credit growth. In the no-segmentation economy, removing the credit relaxation reduces price-rent ratio growth by only 5%.

Q11. What are the implications of allowing landlords to use credit?

When landlords face an LTV limit of 65% relaxed to 85% during the boom, the credit expansion also shifts the tenure supply curve upward (as in Panel (d) of the supply-demand framework), leading to a larger price-rent ratio response and a smaller homeownership rate response than in the baseline. Without recalibration, this model explains 81% of the price-rent ratio rise. After recalibration of σω,L (which is required because landlord credit changes the mapping from empirical moments to structural parameters), the model explains 80% of the price-rent ratio rise. This implies the benchmark results are a lower bound on the role of credit in driving house prices.

Q12. What are the implications of allowing savers to frictionlessly trade housing with borrowers?

When savers are allowed to frictionlessly adjust their housing demand (purchasing housing from or selling to borrowers as credit conditions change), the price-rent ratio response is dampened because savers absorb excess borrower demand. After recalibrating σω,L, the combined credit-and-rate experiment explains 54% of the price-rent ratio boom — roughly 25% less than the benchmark 72%. The authors regard this as an extreme lower bound because in practice saver and borrower housing markets are substantially segmented due to indivisibility, location, and quality differences.

Q13. What are the implications for macroprudential policy?

Macroprudential policies that tighten LTV and PTI limits are effective at slowing house price growth in the benchmark economy, where rental market frictions are substantial. In the full boom counterfactual, tightening credit standards reduces the rise in price-rent ratios by 55%. However, in the no-segmentation economy, the same tightening reduces price-rent ratio growth by only 5%, because landlords readily absorb credit-driven demand and pin prices to the present value of rents. The effectiveness of macroprudential policies is therefore deeply dependent on the degree of rental market segmentation.

Q14. Why do the authors prefer the CBRE Torto-Wheaton rent index over typical rent measures?

The TW index uses a repeat-rent methodology on newly-leased multi-unit apartments, which better captures current market conditions than median rent measures, which are biased by composition changes and are sticky due to long-term lease contracts. Since the price-rent ratio is meant to capture the rent a unit could command if leased instead of sold, newly-leased apartment rents are more appropriate for constructing this ratio. The TW index is available for 53 CBSAs from 1989 and 62 CBSAs from 1994.

Q15. Why do the authors estimate the inverse slope rather than the slope directly?

The first stage for the homeownership rate response is very weak — the estimated coefficients are small and imprecise, so using the homeownership rate as an endogenous variable would suffer severe weak instrument problems. Instead, the authors use the price-rent ratio as the endogenous variable (with a much stronger first stage) and the homeownership rate as the outcome, obtaining the inverse slope (homeownership response per unit price-rent ratio response). The upper bounds of the 95% confidence intervals for the inverse slope range from 0.12 to 0.56 across horizons, corresponding to lower bounds on the slope of 1.8 to 8.4.

Key Concepts

Tenure Supply Curve. The menu of price-rent ratios at which landlords are willing to supply varying quantities of owner-occupied housing (i.e., sell rental units to potential homeowners) at a given total housing stock. Defined in price-rent ratio versus homeownership rate space. Distinct from the absolute supply of housing via the construction sector; shifts in the construction margin affect absolute quantities and prices but not necessarily the price-rent ratio or the ownership share. The slope of this curve — not the level — is the central empirical and structural object of the paper.

Market Segmentation (in the paper’s sense). The degree to which credit-insensitive agents (landlords, unconstrained savers) cannot absorb credit-driven demand from constrained borrowers. Perfect segmentation means owner-occupied and rental housing are entirely non-fungible, so all credit-driven demand falls on a fixed supply of owned units. Zero segmentation means landlords (or savers) can frictionlessly convert between owned and rented housing at a price tied to present discounted rents. In this paper, segmentation is measured continuously by the slope of the tenure supply curve.

Sufficient Statistic (for segmentation). The ratio of the causal elasticity of the price-rent ratio to the causal elasticity of the homeownership rate, both with respect to the same identified credit supply shock. This ratio identifies the slope of the tenure supply curve and is sufficient to calibrate a structural model to recover the role of credit in driving house prices for arbitrary combinations of shocks, even when those shocks differ from the identifying variation.

Ownership Benefit Heterogeneity. An additional idiosyncratic utility flow (positive or negative) that borrowers or landlords receive from owning versus renting a given unit, modeled as a logistic distribution. This within-type heterogeneity generates a fractional and time-varying homeownership rate in the model and maps directly into the slope of the demand and tenure supply curves. The dispersion parameter σω,L for landlords governs the slope of the tenure supply curve; higher dispersion implies a steeper (more segmented) supply curve and larger price-rent ratio responses to credit shocks.

Marginal Collateral Value (CB,t). The shadow value to borrowers of the additional credit that can be collateralized by an additional dollar of housing value, equal to µB,t × FLTV × θLTV in the model. A relaxation of credit standards (raising θLTV or θPTI) or a decline in credit costs raises CB,t, increasing borrower reservation prices and shifting the housing demand curve outward. This is the channel through which credit conditions enter house price dynamics.

Local Projection IV (LP-IV). A generalization of Jordà (2005) local projections to instrumental variables settings, as in Ramey (2016) and Ramey and Zubairy (2018), extended to a panel context with CBSA and time fixed effects. Used to estimate impulse responses of price-rent ratios, house prices, and homeownership rates to credit supply shocks at horizons 0 through 5 years, instrumenting for endogenous credit growth using the conforming loan limit shift-share instrument.

Conforming Loan Limit (CLL) Instrument. A shift-share instrument for local credit supply constructed by interacting the share of mortgage originations in the prior year falling within 5% of the current year’s CLL with the percentage change in the national CLL. Cities where a larger fraction of loans cluster near the CLL threshold experience a larger credit supply shock when the CLL increases, because more loans shift from unsubsidized to GSE-subsidized rates. The instrument is constructed using the change in the national CLL only to avoid endogeneity from high-cost area adjustments.

Homeownership, Polarization, and Inequality

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

This paper asks why job polarization and income inequality are higher in large U.S. cities, and proposes a novel housing-market mechanism that operates independently of — but interacts with — the skill-biased technical change (SBTC) explanations dominant in the existing literature.

The core argument is that large cities have experienced faster growth in house prices relative to both wages (price-wage ratio) and rents (price-rent ratio) since 1980. This excess price growth has priced middle-income households out of homeownership in expensive cities. Because low-income households cannot afford to own anywhere and high-income households can afford to own everywhere, it is specifically middle-income (middle-skilled) households whose location choice becomes entangled with their tenure choice. These households increasingly sort toward smaller, more affordable cities where they can purchase a home. This selective out-migration hollows out the middle of the income distribution in large cities, producing greater employment polarization and income inequality there.

Empirically, the paper uses Census and ACS data from 1980 to 2019 covering 465 commuting zones (CZs). Polarization is measured following Autor and Dorn (2013) by assigning 3-digit occupations to income percentiles fixed at 1980 levels; inequality is measured by the Gini coefficient and variance of log annual wages. Housing costs are captured by hedonic price and rent indices and three derived ratios. OLS and IV results (instrumented using the interaction of land unavailability and long-run changes in real interest rates) show that doubling of prices is associated with a 1 percentage point decline in the middle-skilled employment share; doubling of the price-rent ratio is associated with an 11.3 percentage point decline; doubling of the price-wage ratio with a 5.3 percentage point decline. Inequality follows the same pattern: doubling prices raises 100x the variance of log wages by 2.3 points; doubling the price-rent ratio raises it by 11.7 points; doubling the price-wage ratio by 7.7 points.

The migration mechanism is documented using 2001–2019 CPS ASEC data, which — uniquely among available sources — reports reasons for moving. A doubling of the price index, price-wage ratio, or price-rent ratio in the origin state relative to the destination raises the probability that a middle-income (2nd–4th quintile) household moves for housing-related reasons by approximately 5–10 percentage points in absolute terms, implying a 50–80% relative increase compared with low- or high-income households making a housing-related move.

The theoretical framework extends the standard spatial equilibrium (Rosen-Roback) model with two additions: skill heterogeneity and housing tenure choice. Households face a minimum house size constraint and a payment-to-income (PTI) constraint (calibrated at lambda = 0.308). These constraints create distinct skill thresholds for homeownership that vary by city; the interaction between location and tenure choices applies only to middle-skilled households who can afford ownership in cheap but not expensive cities.

In the quantitative model, calibrated separately for 1980 and 2019 with two locations (top 30 CZs vs. the rest), counterfactual experiments show that holding price-wage ratios at their 1980 levels reduces the excess polarization gap between large and small CZs by 93% and the excess inequality gap by 40%. Holding price-rent ratios constant reduces the polarization gap by 96% and the inequality gap by 27%. By contrast, shutting down SBTC entirely reduces the polarization gap by only 54% and the inequality gap by 73%. These results establish that while SBTC is an important driver, its effect on polarization and inequality is substantially amplified by faster house price growth in large cities; without the housing affordability channel, the effect of SBTC on disproportionate polarization would be 63–81% smaller and on the inequality gap 18–36% smaller.

Q: What is the paper’s central research question? A: The paper asks why job polarization and income inequality are systematically higher in large U.S. cities than in small ones. Prior literature attributed this to skill-biased technical change, external labor demand shocks, or IT-driven displacement of routine jobs; this paper proposes a complementary, housing-market-based explanation that does not rely on features of the production technology.

Q: What is the core mechanism linking house prices to polarization? A: When price-wage and price-rent ratios are higher in large cities, middle-income households face binding minimum-size and payment-to-income constraints that prevent them from owning a home there but not in cheaper cities. Because homeownership carries financial advantages, these households sort toward smaller, more affordable cities. Low-income households cannot afford ownership anywhere and high-income households can afford it anywhere, so only the middle group’s location choice is distorted by tenure considerations. This selective out-migration hollows out the middle of the income distribution in expensive large cities.

Q: What empirical patterns in CZ-level data motivate the paper? A: Doubling CZ size is associated with a 1.9 percentage point greater fall in the middle-skilled employment share and a 2.7 point higher growth in 100x the variance of log wages from 1980 to 2019. Larger CZs also experienced 3.4% higher price growth, 3.1% higher price-wage ratio growth, and a 10% greater increase in price-rent ratios. These associations persist after controlling for initial CZ size and other characteristics.

Q: What do the OLS and IV results show about house prices and polarization? A: A doubling of house prices is associated with a 1 percentage point decline in the middle-skilled share; a doubling of the price-rent ratio with an 11.3 percentage point decline; and a doubling of the price-wage ratio with a 5.3 percentage point decline. IV results using the interaction of land unavailability and the change in real interest rates as an instrument confirm the negative relationship remains statistically significant, suggesting a causal interpretation is plausible.

Q: What do the OLS and IV results show about house prices and income inequality? A: A doubling of prices is associated with a 2.3 point increase in 100x the variance of log wages; a doubling of the price-rent ratio with an 11.7 point increase; and a doubling of the price-wage ratio with a 7.7 point increase. IV results suggest a causal relationship between price growth and income inequality at the CZ level.

Q: What evidence does the paper provide for the migration mechanism? A: Using 2001–2019 CPS ASEC data (which reports stated reasons for moving, unlike the ACS), the paper estimates logit regressions of interstate migration for housing-related reasons. A doubling of the price index in the origin state relative to the destination raises the probability of a housing-related move for middle-income (2nd–4th quintile) households by 5–6 percentage points; a doubling of the price-wage ratio raises it by 6–7 percentage points; and a doubling of the price-rent ratio raises it by 7–10 percentage points. These effects imply a 50–80% relative increase in housing-related migration probability for the middle quintiles compared with the bottom or top quintile. Housing-related movers constitute over 12% of all interstate migrants in the sample.

Q: What is the key finding about homeownership rates? A: There is no statistically significant relationship between the change in homeownership rates and the growth in prices, price-rent, or price-wage ratios from 1980 to 2019. This is consistent with the model’s mechanism, in which middle-income households who cannot afford ownership in large cities move away rather than simply switching to renting there — so aggregate local ownership rates need not fall.

Q: How does the theoretical model generate the polarization result? A: The model extends the Rosen-Roback spatial equilibrium framework with skill heterogeneity and housing tenure choice. Two skill thresholds — one for minimum-size-constrained ownership and one for unconstrained ownership — interact with the price-wage and price-rent ratios of each city. Proposition 1 proves that a city with higher price-wage and price-rent ratios will have a lower middle-skilled share, because middle-skilled workers (those who can afford to own in cheap but not expensive cities) are drawn to cheaper locations. Proposition 2 shows that in a world with only renters or only owners, skill shares would be identical across cities regardless of price differences — the polarization result requires heterogeneity in tenure choice.

Q: What does the no-SBTC counterfactual show? A: Holding the parameters governing local returns to skills at their 1980 levels (shutting down skill-biased technical change) reduces the difference in the decline in the middle-skilled share between large and small CZs by 54% and the gap in the increase in the variance of log wages by 73%. This is broadly consistent with prior literature attributing the bulk of disproportionate polarization and inequality in big cities to SBTC.

Q: What do the constant price-ratio counterfactuals show? A: When price-wage ratios are held at 1980 levels (but SBTC is allowed to operate), the excess polarization gap between large and small CZs falls by 93% and the excess inequality gap by 40%. When price-rent ratios are held at 1980 levels, the polarization gap falls by 96% and the inequality gap by 27%. When both are held constant simultaneously, the polarization gap falls by 89% and the inequality gap by 27%. These results show that the effect of SBTC on polarization would be 63–81% smaller in the absence of the housing affordability amplification channel.

Q: Who are the largest losers from rising price-wage ratios in large cities? A: The counterfactual welfare analysis identifies middle-skilled workers with skill levels between approximately 0.29 and 0.80 as the primary losers. In the counterfactual with fixed price-wage ratios, workers with skills from 0.29 to 0.57 who previously could not afford ownership in large cities are now able to own there, and those with skills from 0.57 to 0.80 spend a smaller share of income on housing. This group either lost homeownership opportunities or was induced to move to less productive CZs by the actual price growth that occurred.

Q: How is the quantitative model calibrated and structured? A: The model is calibrated separately for 1980 and 2019 as two stationary spatial equilibria. It features two locations (the top 30 CZs, which account for 49.3% of employment, and the remaining CZs). Key parameters include a Frechet elasticity of 6.1, an agglomeration externality of 0.04, a PTI constraint of 0.308, and an annual discount factor of 0.96. Land shares differ between large and small CZs (0.3965 vs. 0.2239). The model finds that the price-rent ratio was relatively stable in large cities but fell in small ones, while the price-wage ratio increased much more in large CZs — both indicators point to purchasing a home becoming relatively more expensive in large CZs.

Q: What are the paper’s policy implications? A: Zoning reforms and other policies that increase housing supply in large, unaffordable cities could produce a more efficient spatial allocation of labor, greater aggregate productivity, and more economically diverse — less polarized and less unequal — cities, while also reducing the wealth gap between owners and renters. Policies that promote homeownership by reducing the cost of owning without raising housing supply may reduce local polarization and inequality but could lower aggregate output and do not necessarily increase homeownership rates.

Q: How does this paper relate to existing explanations for city-level polarization? A: The paper’s housing-market mechanism is explicitly complementary to SBTC-based explanations (Baum-Snow, Freedman, and Pavan, 2018; Cerina et al., 2023), external demand shock explanations (Davis, Mengus, and Michalski, 2020), and IT-displacement explanations (Eeckhout, Hedtrich, and Pinheiro, 2024). The paper’s key added contribution is that even if SBTC were the primary driver of disproportionate polarization, its measured effect would be substantially smaller in the absence of faster house price growth in large cities — the housing market amplifies rather than replaces the technology channel.

Job polarization (city-level): The hollowing out of middle-income employment shares in a commuting zone, measured as the change in the share of workers in occupations assigned to the 21st–80th income percentile (using the 1980 occupation-to-percentile mapping fixed over time). In this paper, polarization is greater in cities where price-wage and price-rent ratios grew faster, attributed to selective out-migration of middle-skilled households.

Price-wage ratio: The ratio of hedonic house prices to median annual wages in a commuting zone, constructed from Census and ACS data. A higher price-wage ratio tightens the payment-to-income constraint on potential homebuyers and is the primary driver of the skill threshold for homeownership in the model.

Price-rent ratio: The ratio of hedonic house prices to rents in a commuting zone. In the model, a higher price-rent ratio reduces the financial advantage of owning over renting, raising the skill threshold at which ownership becomes optimal. The paper treats price-rent and price-wage ratios as distinct channels that both independently amplify polarization.

Housing tenure choice: The household decision to own or rent, modeled as a discrete choice made at the start of life that interacts with location choice. Ownership requires satisfying both a minimum house size constraint and a payment-to-income (PTI) constraint (lambda = 0.308). The interaction between tenure and location choices is the paper’s key model innovation; it exists only for middle-skilled workers whose income is sufficient for ownership in cheap but not expensive cities.

Skill threshold for homeownership (s*_i): The minimum skill level at which a worker in city i chooses to own rather than rent, defined by Lemma 2. This threshold is decreasing in local labor productivity and increasing in price-wage and price-rent ratios. Workers with skill below s*_i in all cities always rent; those with skill above s*_i in all cities always own; those in between face city-dependent tenure choice that distorts their location decision.

Skill-biased technical change (SBTC): In the paper’s quantitative model, SBTC is represented by faster growth in the skill dispersion parameter (alpha_it) in large CZs, reflecting differential productivity growth concentrated at the top of the skill distribution. The paper finds SBTC accounts for 54% of the polarization gap and 73% of the inequality gap in its counterfactual, but argues its effect is amplified 4–5x by the housing affordability channel.

Payment-to-income (PTI) constraint: The constraint that a homebuyer cannot spend more than a fraction lambda (calibrated at 0.308) of annual labor earnings on the annual housing payment (user cost times price times quantity). This constraint, together with the minimum house size, determines the income threshold for ownership and makes location and tenure choices interdependent for middle-skilled workers.

Riding the Housing Wave: Home Equity Withdrawal and Consumer Debt Composition

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

Layer 1 — Overview

Research Question

This paper investigates how rising house prices affect the composition of household debt portfolios in Sweden during 2010–2014. Specifically, the authors ask whether homeowners who experience housing wealth gains use home equity withdrawals to substitute relatively expensive unsecured consumer (non-mortgage) debt with cheaper collateralized mortgage debt — a form of debt re-optimization — and what individual and policy factors drive this behavior.

Data and Methodology

The study uses a monthly individual-level panel dataset sourced from Upplysningscentralen (UC), the Swedish credit bureau, covering approximately 4.8 million individuals (62 percent of the Swedish adult population) from July 2010 to July 2014. The UC data captures approximately 80 percent of total household credit volume and 97 percent of household mortgage loans. Parish-level house price indices come from Valueguard, and municipality-level education data come from Statistics Sweden. The empirical analysis draws on a random sample of approximately 150,000 individuals, of whom 81,667 (81 percent) are classified as homeowners — defined as individuals holding a mortgage throughout the entire sample period.

The primary identification strategy uses renters as a control group for homeowners in a difference-in-differences (DiD) framework, exploiting the variation in local (parish-level) house price growth. Because Sweden’s rental market is heavily regulated and uses a queuing allocation system, the rent-versus-own decision is largely exogenous to individual wealth, making renters a credible counterfactual for homeowners. The authors also use two instrumental variables to address endogeneity of house price growth: (1) historical house price volatility at the municipal level from 1981–2005 (the “Palmer instrument”), and (2) a “building-friendly” instrument measured as the share of municipal planning appeals overruled by county authorities, derived from Sweden’s 2013 National Board of Housing survey. A difference-in-difference-in-differences (DDD) approach is employed to examine the role of DTI constraints and financial literacy. Home equity withdrawals are identified as increases in outstanding mortgage balances of at least SEK 20,000, after excluding cases where the equity was used to purchase a new property.

Main Findings

Total debt and mortgage growth: A one percentage point increase in local house prices is associated with an increase of SEK 959.1 in total household debt for homeowners relative to renters, driven primarily by mortgage growth. This effect is robust to instrumental variable estimation.
Debt re-optimization — unsecured loans: Conditional on withdrawing home equity in month t, homeowners reduce their outstanding unsecured consumer loan balances by 53.5 percent in the following month (t+1). This is large relative to the U.S. benchmark of 16.7 percent reported in Bhutta and Keys (2016). The average reduction in unsecured loan balances across all equity withdrawers is SEK 9,624 per withdrawal event, while credit card debt declines by only SEK 73.3 — an economically negligible amount. For equity withdrawers who had pre-existing unsecured loan balances and actively repaid them, outstanding unsecured loans fell by SEK 55,040 — nearly six times the full-sample average. For this subsample, 17.7 percent of the total withdrawn home equity was applied to unsecured loan repayment (versus 2.98 percent for the full sample of equity withdrawers).
Credit card debt: The effect of equity withdrawal on credit card balances is not statistically significant. This reflects the institutional feature that credit cards in Sweden are used primarily as payment instruments within a 30–45 day interest-free grace period, not as a credit facility. Swedish credit card outstanding balances average only 16 percent of a debtor’s monthly disposable income, compared to 201 percent in the U.S.
Heterogeneity by homeowner type: The debt re-optimization finding is specific to equity withdrawers. House traders increase non-mortgage debt alongside mortgage debt. Amortizers show neither effect at meaningful scale. The substitution between unsecured loans and mortgage debt is not observed for non-withdrawing homeowners.
DTI and financial literacy: The debt re-optimization effect is strongest for borrowers with above-median DTI ratios residing in municipalities with above-median education levels (used as a proxy for financial literacy). Borrowers in this high-DTI, high-literacy group paid down approximately SEK 10,000 more in unsecured loans after a home equity withdrawal than high-DTI borrowers in low-literacy areas. A larger fraction of their withdrawn equity was also directed toward unsecured loan repayment.
Macroprudential policy: The introduction of an 85 percent LTV cap in October 2010 is associated with an increase in non-mortgage debt, particularly unsecured consumer loans, by both existing equity withdrawers and new mortgage borrowers. For new mortgagors entering after the LTV cap, the ratio of unsecured loans to mortgage debt increased by 1.68 percentage points, consistent with borrowers using unsecured loans to fund the required 15 percent downpayment. The debt re-optimization behavior itself (i.e., paying back unsecured loans with withdrawn equity) was found to persist both before and after the LTV cap introduction, with no statistically significant difference between regimes.
Interest rates: Both the probability and the size of home equity withdrawal are negatively correlated with the mortgage rate and positively correlated with the spread between the unsecured loan rate and the mortgage rate. During the sample period, mortgage rates averaged between 2.5 and 3 percent, while unsecured loan rates were on average two to three times higher.

Scope Conditions

The results are specific to Sweden during a housing boom period (2010–2014), under interest-only floating-rate mortgages with full recourse, and in the context of a tightly regulated rental market that makes the renter vs. owner distinction largely exogenous. The re-optimizing behavior requires actively rising house prices to generate the equity needed for withdrawal; the authors note this strategy is fragile if house prices were to decline. Swedish households increased their total debt levels even while re-optimizing its composition, raising financial stability concerns.

In depth

Q1. What exactly is “home equity withdrawal” in the Swedish institutional context, and how does it differ from the U.S.?

A: In Sweden, home equity withdrawal occurs exclusively by increasing the existing outstanding mortgage balance against an updated home valuation; there are no HELOCs, home equity loans, or cash-out refinancing products as in the U.S. Households must pass a credit check and comply with the 85 percent LTV limit (post-October 2010). Some banks require a minimum withdrawal of SEK 100,000. Fixed transaction costs include a bank administration fee (around SEK 700 for apartment owners) and a fixed fee to the building association (around SEK 750), making the process cheap but not costless.

Q2. How do the authors identify home equity withdrawal events in the data?

A: An equity withdrawal event for individual i in month t is defined as a positive change in outstanding mortgage balance greater than SEK 20,000 (approximately the average monthly disposable income), conditional on no simultaneous change in residential address, property type, or acquisition of a second property. This threshold is applied to avoid measurement error from minor rounding or bank adjustments. After applying all exclusion criteria, the authors identify 46,499 equity withdrawal events over the sample period.

Q3. What is the identification strategy for isolating the causal effect of house prices on debt portfolios?

A: The primary identification uses renters as a control group in a DiD framework. Because Sweden’s heavily regulated rental market (with queuing systems and rents far below market rates) makes the rent-vs-own decision largely exogenous to individual wealth, renters experience the same local economic conditions as homeowners but cannot access the equity-based financing channel. The key identifying assumption is that unobserved local economic shocks — which may jointly drive house prices and credit demand — affect renters and homeowners similarly. Two IVs are used as robustness checks: historical municipal house price volatility (1981–2005) and a “building-friendly” regulation index.

Q4. What is the first-stage strength of the Palmer instrumental variable?

A: The estimated coefficient on the historical house price volatility instrument in the first-stage IV regression is 0.00022 and is statistically significant at the 1 percent level. The first-stage F-statistic is 38.41, which exceeds conventional weak-instrument thresholds, confirming that historical volatility is a strong predictor of current house price growth across municipalities.

Q5. Why is credit card debt not reduced by equity withdrawals in Sweden, even though it carries higher interest rates than unsecured loans?

A: Credit cards in Sweden function predominantly as payment instruments within a 30–45 day interest-free grace period rather than as actual credit facilities. Average outstanding credit card balances amount to only 16 percent of debtors’ monthly disposable income (versus 201 percent in the U.S. during the same period), and balances are typically repaid in full at month-end. Because cardholders are not accruing significant interest on their balances, there is no financial incentive to extinguish credit card debt using withdrawn home equity.

Q6. How is the 2.98 percent figure for equity used in debt repayment to be interpreted?

A: Across all home equity withdrawers (including those who have no pre-existing unsecured loans), the average share of the total amount withdrawn that is applied to unsecured loan repayment in the following month is 2.98 percent. This low average reflects that the majority of homeowners do not hold outstanding unsecured consumer loans and therefore have no debt to repay. When the sample is restricted to equity withdrawers who both held outstanding unsecured loans before the withdrawal and actively repaid some portion in the following month, the repayment share rises to 17.7 percent of the withdrawn amount.

Q7. What is the DDD specification used to identify the roles of DTI and financial literacy, and what do the triple interaction terms reveal?

A: The DDD specification interacts the equity withdrawal indicator with a high-DTI dummy (above-median DTI at the individual level in the current month) and a high-financial-literacy dummy (municipality’s share of post-secondary educated residents above the national median in that year). The triple interaction term (EquityWithdrawal × HighDTI × HighLit) is negatively significant at approximately −SEK 9,913 to −9,966 (in thousands, i.e., around −SEK 10,000) in the unsecured loan repayment regression. This implies that, conditional on withdrawing equity, borrowers with both high DTI and high financial literacy municipality background reduced their unsecured loans by roughly SEK 10,000 more than high-DTI borrowers in low-literacy areas.

Q8. How does the introduction of the 85 percent LTV cap in October 2010 affect non-mortgage debt?

A: Comparing a three-month window before and after October 2010, the authors find that: (a) before the LTV cap, changes in household debt did not respond significantly to house price growth for any debt type; (b) after the LTV cap, all debt types — including unsecured consumer loans — increased significantly in areas with higher cumulative house price growth. The interaction term between house price growth and the post-LTV dummy is positively significant for non-mortgage debt, driven by unsecured loans. For new mortgage borrowers, the ratio of unsecured loans to mortgage debt increased by 1.68 percentage points after the LTV cap, consistent with constrained borrowers using blanco (unsecured) loans to fund the mandatory 15 percent downpayment.

Q9. Does the LTV cap affect the debt re-optimization behavior (i.e., the use of withdrawn equity to repay unsecured loans)?

A: The authors find that equity withdrawers reduce unsecured loans both before and after the LTV cap introduction. The interaction terms between the LTV dummy and equity withdrawal indicators (both dummy and size) are not statistically significant, indicating that the debt re-optimization behavior per se — the channel of using withdrawn equity to pay down non-mortgage debt — was not materially altered by the macroprudential tightening. The authors caution that the very short pre-cap period (only three months of data from July to September 2010) limits statistical power for this comparison.

Q10. What is the role of interest rate spreads in driving equity withdrawal decisions?

A: Both the probability of withdrawing equity and the size of the withdrawal are negatively correlated with the prevailing mortgage rate and positively correlated with the spread between the unsecured loan rate and the mortgage rate. This implies that equity withdrawal is more common and larger in magnitude when mortgages are cheaper or when the relative cost premium on unsecured lending is higher — consistent with the debt re-optimization motive. Results for the interest rate analysis are reported in Appendix B.2.

Q11. How do the results differ across homeowner subgroups (equity withdrawers, house traders, amortizers)?

A: Among equity withdrawers: mortgage increases and unsecured loan decreases are both statistically significant (debt re-optimization). Among house traders: mortgage increases significantly and non-mortgage debt also increases (no substitution — they borrow across all categories to finance property purchases). Among amortizers: changes in both mortgage and non-mortgage debt are smaller in magnitude and primarily reflect active principal repayment rather than refinancing activity. The substitution between unsecured and mortgage debt is thus exclusive to equity withdrawers.

Q12. What is the overall change in Swedish house prices and aggregate debt during the sample period?

A: The house price index rose by 20 percent between July 2010 and July 2014, with particularly strong appreciation after January 2012 following a mild dip in the second half of 2011. Over the same period, aggregate mortgage balances of homeowners increased by 16 percent. Aggregate non-mortgage debt also increased, though from a much smaller base. In the cross-sectional regression, a one percentage point increase in house prices is associated with an SEK 926.7 increase in total individual debt (4 percent of average house value of SEK 21,500 per percentage point).

Q13. What are the robustness checks and do they alter the conclusions?

A: The following robustness checks are reported: (1) redefining equity withdrawers as those who withdrew exactly once (Tables A4–A6); (2) restricting equity withdrawers to those withdrawing SEK 20,000–100,000 to exclude potential house traders; (3) using alternative house price growth windows of 12, 24, and 48 months (Tables A7–A9); (4) using the “building-friendly” regulation IV (Tables A2–A3); (5) supplementary time-series panel regressions (Appendix B.1). All robustness checks yield qualitatively consistent results, with the substitution from unsecured loans to mortgages preserved across specifications.

Q14. What are the financial stability implications the authors identify?

A: Despite the debt re-optimization behavior, total indebtedness among Swedish equity withdrawers does not decline — they increase their mortgage balances more than they reduce unsecured loans. Swedish average household DTI is approximately double that of the U.S. (OECD, 2022). The authors note that if house prices were to fall, homeowners relying on equity withdrawal for debt restructuring would lose access to this financing channel and face the full cost of high-interest unsecured debt. Additionally, the circumvention of the LTV cap through unsecured loan substitution raises financial stability concerns because it concentrates households in more expensive, unprotected debt.

Key Concepts

Home Equity Withdrawal (Sweden-specific): The act of increasing an existing outstanding mortgage balance against a revalued home, which is the only channel for equity extraction in Sweden. Unlike the U.S., there are no HELOCs, home equity loans, or cash-out refinancing products. Subject to the 85 percent LTV cap introduced in October 2010 and a minimum threshold (SEK 100,000 at some banks).

Debt Re-optimization: The behavior by which homeowners substitute relatively expensive unsecured consumer debt with cheaper collateralized mortgage debt during a housing boom, using the proceeds of home equity withdrawal to repay unsecured loans. In the paper’s usage, this implies a deliberate, financially sophisticated portfolio adjustment — not merely passive debt accumulation.

Blanco Loans (Unsecured Consumer Loans): Unsecured personal loans in Sweden (referred to as “blanco” loans in Swedish). These carry interest rates historically two to three times higher than mortgage rates. In the Swedish context, they are used both as consumer finance and — especially after the 85 percent LTV cap — as a source of downpayment funds. They are the primary non-mortgage debt instrument that equity withdrawers pay down.

Loan-to-Value (LTV) Cap: The macroprudential regulation introduced by the Swedish Financial Supervisory Authority in October 2010, limiting mortgage debt (including home equity withdrawals) to 85 percent of the property’s market value. This applied both to new mortgage originations and to existing mortgagors increasing their mortgage balance. In the paper, this is treated as an exogenous policy event against which behavioral responses are measured.

Financial Literacy Proxy (Municipal Education Level): Because individual-level financial literacy data are unavailable, the paper uses the share of a municipality’s residents with post-secondary education in a given year as a municipality-level proxy for financial literacy. Municipalities above the national median in this share are classified as high-literacy areas. The classification can change year to year.

Debt-to-Income (DTI) Ratio: The ratio of an individual’s total outstanding debt to annual disposable income, used in the paper as a measure of financial constraint. A borrower is classified as “high DTI” if their DTI exceeds the cross-sectional median for all borrowers in that month. High-DTI borrowers in the paper’s sample tend to be younger, have larger mortgages, and have more unsecured loan balances.

Interest-Only Floating-Rate Mortgage: The predominant Swedish mortgage structure during the sample period. Most mortgages are effectively three-month floating-rate contracts with no amortization requirement (until June 2016), making Swedish borrowers more sensitive to short-term interest rate movements than borrowers in fixed-rate amortizing mortgage systems. This institutional feature means that increases in home equity during the sample period derived almost entirely from house price appreciation rather than principal repayment.

Slum Upgrading and Long-Run Urban Development: Evidence from Indonesia

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

This paper estimates the long-term causal effects of the Kampung Improvement Program (KIP), one of the world’s largest slum upgrading programs, on urban development in Jakarta, Indonesia. KIP ran from 1969 to 1984 across three staggered waves (Pelita I-III), covered 110 square kilometers (25% of Jakarta’s area), and served approximately 5 million residents at a total cost of roughly $500 million (2015 USD). The program provided basic physical upgrades — paved roads and footpaths, sanitation and drainage, and community buildings such as schools and health clinics — along with a verbal non-eviction guarantee for 15 years. Residents were not relocated.

The central research question is whether preserving slums through upgrading entails long-run dynamic inefficiency: as Jakarta formalizes, do KIP areas lag behind non-KIP areas in ways that generate opportunity costs from land misallocation?

The authors assemble high-resolution data on KIP policy boundaries, current assessed land values (nearly 20,000 sub-blocks), building heights from a novel photographic survey of 19,518 pixels stratified across Jakarta, and multiple novel measures of informality — a rank-based photographic index (0 to 4), an attributes-based index across fifteen binary characteristics, and administrative data on unregistered land-parcel titles. They also use digitized historical maps from 1937 and 1959 to identify pre-KIP kampung boundaries.

Two empirical strategies address program selection bias (KIP planners prioritized the worst-condition kampungs first). The first restricts the sample to historical kampungs that existed before KIP and includes locality fixed effects, comparing treated kampungs against nearby untreated ones within the same neighborhood. The second is a boundary discontinuity design (BDD) comparing observations within 200 meters of KIP boundaries. Both strategies include eighteen predetermined controls for historical landmarks, infrastructure, and topography including flood proneness.

Average effects (robust across both strategies): KIP areas today have land values approximately 14-17 log points (roughly 15%) lower than observably equivalent non-KIP areas, and are about 8-12 percentage points less likely to contain buildings taller than three floors — half the control-group mean of 0.24. KIP areas are more informal across all three informality metrics: the rank-based index is higher by 0.29 standard deviations, the attributes-based index by 0.05 SD units, and the share of unregistered parcels is 3 percentage points higher. Building heights corroborate the land-value finding: imputing the hedonic value of missing tall buildings in KIP accounts for approximately 90% of the aggregate land-value impact ($2.2 billion of $2.4 billion).

Heterogeneity by real estate potential is a central finding. The authors construct a predicted land index for 2,058 hamlets in Jakarta using non-KIP land values. In the lowest quintile (Q5), KIP areas show a positive and statistically significant effect of +10 log points on land values, consistent with direct capitalization of the upgrades. This effect reverses in higher-potential areas: the estimate reaches -28 log points in Q2 and -30 log points in Q1, as non-KIP neighborhoods formalize while KIP areas lag.

Surplus calculations integrating land values, building heights, horizontal built-up coverage (35% for KIP vs. 18% for non-KIP), and demand and supply elasticities reveal that 90% of total surplus losses are concentrated in the top two quintiles (Q1 and Q2), which comprise 47% of KIP’s coverage area. In Q1, KIP surplus is lower by $2,369 per square meter; in Q2, the gap is $1,044 per square meter. In the bottom two quintiles, KIP delivers greater surplus (up to +$347 per square meter in Q5), covering an estimated 3 million residents across 57 square kilometers.

Mechanisms consistent with delayed formalization include significantly higher population density in KIP areas (+33 log points, or 39%) and greater land fragmentation (+9 parcels per pixel relative to a non-KIP mean of 19), both of which raise relocation and land assembly costs. The original KIP investments show no differential effect by type or intensity after four decades, consistent with their 15-year projected useful life. Endogenous sorting is ruled out as a confounder: if anything, educational attainment is slightly higher in KIP areas.

Q: What is the Kampung Improvement Program (KIP) and what did it provide? A: KIP was a slum upgrading program implemented in Jakarta, Indonesia from 1969 to 1984 across three five-year plan waves (Pelita I, II, III). It covered 110 square kilometers and 5 million residents at a total cost of approximately $500 million (2015 USD). The program provided three categories of basic physical improvements — vehicular and pedestrian road access, sanitation and drainage infrastructure, and community buildings (schools, health clinics) — along with a verbal non-eviction guarantee for 15 years. Crucially, upgrades were designed to be basic, with a planned useful life of only 15 years, to avoid attracting higher-income groups.

Q: What is the core research question and theoretical concern motivating the paper? A: The paper asks whether slum upgrading programs, while immediately beneficial to residents, entail dynamic inefficiency by delaying formalization as cities develop. The concern is that preserving slums through upgrades and non-eviction guarantees can create opportunity costs from land misallocation when surrounding areas formalize and redevelop into higher-value formal structures. This is framed as a trade-off between the direct welfare benefits of upgrading (affordable in-situ housing for millions) and the long-run costs to urban land productivity.

Q: How does the paper address the selection bias problem — KIP targeted the worst-condition kampungs first? A: Two complementary strategies are used. First, the historical kampung specification restricts the sample to areas that were kampungs before KIP (from 1937 and 1959 maps) and includes locality fixed effects, so treated and control units are compared within the same neighborhood and share the same real estate market by assumption. Second, a boundary discontinuity design (BDD) compares observations within 200 meters of KIP boundaries with boundary fixed effects and quadratic distance controls. A falsification test using sequential KIP waves confirms the approach: the raw data shows a monotonic pattern (Wave I worst: -0.40 log points, Wave II: -0.29, Wave III: -0.17) consistent with selection bias, but this pattern disappears in the historical kampung specification (Wave I: -0.13, Wave II: -0.11, Wave III: -0.14), supporting the identification assumption.

Q: What are the average effects of KIP on land values and building heights? A: In the historical kampung specification, KIP areas have land values 14 log points (approximately 15%) lower than non-KIP historical kampungs within the same locality. The BDD estimate is similar at -17 log points. For building heights, KIP areas are 12 percentage points less likely to contain a building taller than three floors in the historical kampung sample (8 percentage points in the BDD), relative to a non-KIP control mean of 0.24 — meaning KIP areas are roughly half as likely to have tall buildings. The average effect on floors is -1.6 floors, relative to a control mean of 5 floors.

Q: How do the authors validate that land value estimates are not distorted by measurement error in informal areas? A: The authors impute the hedonic value of missing tall buildings in KIP using a hedonic regression estimated solely on non-KIP historical kampungs. KIP areas have 145 fewer buildings with more than ten floors; combined with a 57% price premium for tall buildings (relative to a base price of 13.4 million Rupiahs per square meter), the implied land value loss from missing buildings above ten floors is approximately $1.3 billion, and from buildings between four and ten floors is $0.9 billion, for a total imputed effect of $2.2 billion. This accounts for approximately 90% of the aggregate land value impact from the historical kampung specification ($2.4 billion), assuaging concerns that lower measured land values in KIP reflect data quality differences rather than true price gaps.

Q: How does the KIP effect vary across the distribution of real estate potential? A: The authors construct a predicted land index for 2,058 Jakarta hamlets by regressing non-KIP log land values on hamlet fixed effects, then rank hamlets into quintiles. In Q5 (lowest predicted land values, least likely to formalize), KIP areas show a statistically significant positive effect of +10 log points on land values, consistent with direct capitalization of the upgrades. Moving to higher-potential areas, the effect attenuates and reverses: it is -28 log points in Q2 and -30 log points in Q1, where non-KIP areas have formalized. This cross-sectional pattern traces out the dynamic inefficiency predicted by theory.

Q: What informality measures does the paper construct and what do they show? A: The paper constructs three complementary informality metrics. First, a rank-based photographic index (0 = very formal, 4 = very informal) coded by two trained Jakarta-based research assistants from approximately 28,000 hand-coded photographs, with inter-rater correlation of 0.78. Second, an attributes-based index averaging fifteen binary characteristics across vehicular access, neighborhood appearance, and structural permanence, standardized to a z-score. Third, the area share of unregistered land parcels from the Indonesian National Land Agency’s 2020 digital land maps. KIP areas score higher on all three: the rank-based index is higher by 0.29 SD units, the attributes-based index by 0.05 SD units, and the unregistered parcel share is higher by 3 percentage points.

Q: What mechanisms explain why KIP areas remain informal and have lower land values? A: The paper identifies three mutually reinforcing mechanisms. First, KIP areas have significantly higher population density (+33 log points or 39% in the historical kampung sample, equivalent to 51 more people per pixel), which raises relocation costs. Second, KIP areas have greater land fragmentation, with 9 more parcels per pixel relative to a non-KIP mean of 19, exacerbating holdout problems during land assembly; a back-of-the-envelope calculation attributes a 9% land value effect (60% of the total 15% effect) to this channel. Third, the verbal non-eviction guarantees and improved conditions likely strengthened residents’ tenure perceptions and encouraged them to stay, leading to sub-division of parcels over time. The original KIP investments show no differential effect by type after four decades, consistent with their designed 15-year useful life, and KIP areas have similar access to public amenities today.

Q: How does the paper calculate surplus and what are the results? A: The surplus framework compares KIP (informal, tends to stay informal) against non-KIP counterfactuals (more likely formal) on three dimensions: non-KIP areas have (i) higher land values, (ii) taller structures, but (iii) lower horizontal built-up coverage than slums (18% vs. 35% for KIP). Consumer surplus uses a linear demand approximation with elasticity of 0.2 for non-KIP and 0.16 for KIP (backed out from differences in housing budget shares). Producer surplus integrates a Cobb-Douglas supply curve with elasticities of 1.4 (formal) and 1.3 (informal). In Q1, KIP property value is $1,873 per square meter vs. $3,098 for non-KIP, a difference of $1,225 in value terms and $2,369 in surplus terms. The surplus gap falls to $1,044 in Q2, and halves again in Q3, becoming positive (+$347 per square meter) in Q5. Ninety percent of total surplus losses are concentrated in Q1 and Q2, which cover 47% of KIP’s area.

Q: What do the case studies of kampung clearances illustrate? A: Three Jakarta kampungs cleared in 2015-2016 are examined. Kampung Bukit Duri (Q5, lowest real estate potential) shows a surplus difference of +$572 per square meter in favor of KIP — meaning clearance there is socially inefficient. Kali Pessangrahan (Q3) shows a surplus difference of -$307. Kalijodo (Q2) shows -$910 per square meter, suggesting sizable societal gains from formalization. However, even in Kalijodo, residents were relocated 24 km away to Marunda (a Q5 area), where consumer surplus is only 46% of Kalijodo’s — illustrating that societal gains from formalization do not automatically translate into Pareto improvements for evicted residents.

Q: What robustness checks address alternative explanations? A: The paper runs several tests. A placebo BDD using 45 non-KIP historical kampung boundaries finds no significant discontinuity, ruling out the hypothesis that slums generically have persistently lower land values. Bandwidth robustness shows consistent BDD estimates from 150 to 500 meters. Tests for spatial spillovers find no spatial decay pattern in land values near KIP boundaries, consistent with the prevalence of gated communities in formal Jakarta minimizing neighborhood contamination. Endogenous sorting is examined using 2010 Census data on 10 million individuals: educational attainment is slightly higher in KIP, and in-migration is slightly lower (1-2 percentage points below mean) with migrants having slightly more years of schooling — both inconsistent with an explanation based on low-skill sorting into KIP. Direct congestion effects from population density are also ruled out by estimating spatial decay around 45 dense non-KIP informal hamlets, finding no decay large enough to explain the land-value effects.

Q: What are the policy implications for slum upgrading in other developing countries? A: The paper’s framework suggests that slum upgrading’s cost-benefit balance depends critically on where the upgraded area sits in the real estate potential distribution. In low-potential areas (bottom quintiles of the land index), upgrading delivers net surplus even decades later and implicitly provides affordable housing at scale to millions of residents. In high-potential areas (top quintiles), the opportunity costs from delayed formalization can be large — up to $2,369 per square meter in surplus terms — and the paper suggests that stronger land market institutions to share surplus with informal residents could partially mitigate these costs. The paper also notes that formalization involves complex institutional and political challenges: relocating millions of kampung residents is logistically difficult, compensation is frequently inadequate or absent, and land assembly faces severe holdout problems.

Dynamic inefficiency in cities: The phenomenon, in the context of this paper, whereby preserving informal slum settlements through upgrading delays their formalization, generating opportunity costs from land misallocation as surrounding formal areas develop. Distinguished from static inefficiency: KIP may raise resident welfare while simultaneously reducing aggregate land productivity.

Slum upgrading: A policy providing basic public goods improvements (roads, sanitation, community buildings) and tenure security (typically verbal non-eviction guarantees) to existing slum residents in situ, without relocating them. Contrasted with formalization (redevelopment) and sites-and-services programs.

Boundary discontinuity design (BDD): The paper’s second identification strategy, comparing outcomes for observations within 200 meters on either side of KIP program boundaries, with boundary fixed effects and quadratic distance controls, under the assumption that absent KIP, unobserved real estate potential varies smoothly at program boundaries.

Predicted land index: A hamlet-level index constructed by regressing non-KIP log land values on hamlet fixed effects across 2,058 Jakarta hamlets, used to proxy real estate market potential and rank neighborhoods into quintiles from highest (Q1) to lowest (Q5) development stage.

Informal surplus: The surplus generated within the informal housing sector, including built-up volume from high horizontal coverage (35% for KIP kampungs) and low-cost informal structures, which is destroyed upon formalization and must be weighed against the gains from taller, higher-value formal developments.

Land fragmentation: The number of distinct land parcels per unit area (pixel), measured from Jakarta’s 2011 cadastral maps. Higher fragmentation exacerbates holdout problems in land assembly, raising the cost of redevelopment and contributing to delayed formalization.

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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.

To Own or to Rent? The Effects of Transaction Taxes on Housing Markets

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

Layer 1 — Summary

Using sales and leasing transaction records for the Greater Toronto Area (2006–2018), this paper finds three novel effects of a higher property transaction tax: higher buy-to-rent transactions alongside lower buy-to-own transactions despite both being taxed, a lower sales-to-leases ratio, and a lower price-to-rent ratio. The empirical identification exploits the City of Toronto’s introduction of a city-level Land Transfer Tax (LTT) in February 2008 — covering only the city and not surrounding GTA municipalities — comparing outcomes on opposite sides of the city border before and after the tax change. A 1.3 percentage-point higher effective LTT rate causes buy-to-rent purchases to rise by 9.3% while owner-occupier purchases fall by 9.6%; the leases-to-sales ratio rises by 26% and the price-to-rent ratio falls by 3.8%. To explain these facts, the paper develops a search model featuring household tenure choice (own vs. rent) subject to heterogeneous credit costs, endogenous homeowner moving decisions, and free entry of buy-to-rent investors; the key mechanism is that the LTT reduces homeowners’ mobility — because owner-occupiers expect to transact multiple times over their lifetimes and thus bear the tax repeatedly — discouraging entry into ownership and raising demand for rentals, which in turn attracts investor entry even though investors too pay the tax, since investors need not re-transact whenever a tenant vacates. The implied deadweight loss is large at 111% of tax revenue, with more than half of this due to distorting decisions to own or rent; taking the rental market into account accounts for losses equal to 73% of tax revenue, which is two-thirds of the total loss.

In depth

Q1. Q: What are the three novel empirical facts documented in this paper?

A: Using MLS data on both sales and leases in the Greater Toronto Area, the paper documents: (1) a 1.3 pp higher effective LTT rate causes buy-to-rent (BTR) investor purchases to increase by 9.3%, in stark contrast to a 9.6% fall in owner-occupier (buy-to-own) purchases — a divergence that is counterintuitive because both types of buyer are subject to the same tax; (2) the ratio of leases to sales rises by 26%, indicating that rental-market activity increases relative to ownership-market activity; and (3) the price-to-rent ratio falls by 3.8%, meaning house prices decline relative to rents.

Q2. Q: What is the empirical identification strategy and why is it credible?

A: The paper uses a geographic regression discontinuity approach comparing communities on opposite sides of the Toronto city border, where the new city-level LTT applies on one side but not the other, in a difference-in-differences framework spanning January 2006–January 2008 (pre-policy) and February 2008–February 2012 (post-policy). The sample is restricted to properties within 3 or 5 km of the boundary. The paper verifies that property characteristics do not differ significantly across the border and that cross-border differences do not change after the LTT, supporting the parallel-trends assumption. The effective LTT rate increase is measured at 1.3 percentage points (assuming 40% first-time buyers, who receive a partial exemption). Buy-to-rent transactions are identified in the MLS data by matching properties that appear in both the sales and leases datasets within an 18-month window following sale.

Q3. Q: What is the intuition for why the LTT raises buy-to-rent investment even though it taxes investors?

A: The mechanism hinges on the asymmetry in expected future transaction costs between owner-occupiers and investors. Owner-occupiers face idiosyncratic match-quality shocks — they periodically want to move to a different property as their circumstances or preferences change — so choosing homeownership means expecting to pay the LTT on each future move. This makes homeownership less attractive relative to renting, reducing household entry into the ownership market and increasing demand for rental properties. Investors (landlords), by contrast, do not need to re-transact in the ownership market simply because a tenant moves out; they retain the property and find a new tenant. Investors therefore face a lower expected frequency of LTT payments per year of property holding than owner-occupiers. As a result, the LTT’s negative effect on investor returns is smaller in magnitude than the increase in rental demand it generates. In equilibrium, the price-to-rent ratio falls by enough to attract more BTR investors in spite of the direct cost the tax imposes on them, and investor purchases rise.

Q4. Q: How does the LTT affect homeowner mobility (the “lock-in” effect) and what are its welfare implications within the ownership market?

A: The LTT makes existing homeowners more tolerant of poor match quality with their current property, since the cost of moving — paying the tax again — has risen. Moving rates therefore decline as households remain in properties for longer on average. To mitigate future tax costs, buyers also become more selective (“picky”) when initially matching with a property, requiring higher match quality before purchasing. This reduces the frequency of moves but increases the cost and duration of search for new buyers. The welfare consequences within the ownership market are: (a) misallocation of properties among owner-occupiers as average match quality falls because households move less often to renew it; partially offset by (b) higher initial match quality for newly matched buyers, but at the cost of longer search. The LTT-induced distortions within the ownership market account for a loss equal to 38% of tax revenue.

Q5. Q: What are the model’s quantitative predictions for the four-year post-reform period, and how do they compare to the empirical estimates?

A: The model is calibrated to the City of Toronto for 2006–8 (homeownership rate ~54%) and simulated for a 1.3 pp LTT increase, with the mobility hazard rate used as the internal calibration target. For the four-year period following the tax change, the model predicts: owner-occupier transactions fall by 14%; buy-to-rent transactions rise by 35%; the leases-to-sales ratio rises by 15%; the price-to-rent ratio falls by 1.6%; and the homeownership rate falls by 0.23 percentage points. These figures are broadly consistent in magnitude with the estimated LTT effects on the variables not directly targeted in calibration (i.e., the transaction-volume and price-to-rent results from the empirical estimation).

Q6. Q: What are the long-run (steady-state) effects and why do they differ from the four-year effects?

A: Tenure-choice variables are very slow to adjust because annual flows are small relative to housing stocks. In the new steady state, the homeownership rate falls by 2.4 percentage points and the leases-to-sales ratio rises by 23% — both substantially larger than the four-year effects. By contrast, four-year effects on owner-occupier transactions and the price-to-rent ratio are already close to their new steady states. Buy-to-rent transactions overshoot their steady-state level (the four-year rise of 35% compares to a steady-state rise of 5.1%) because of a one-off surge in investor entry as the rental market absorbs the transition; once the stock of rental properties has adjusted, the flow of new buy-to-rent purchases settles lower.

Q7. Q: How are the welfare (deadweight) losses decomposed across distortion channels?

A: The new LTT generates a total welfare loss equivalent to 111% of the extra revenue it raises. The decomposition is: distortions to flows between the rental and ownership markets (i.e., the tenure-choice margin) account for a loss equal to 60% of extra revenue; distortions within the rental market account for 13% of tax revenue; distortions within the ownership market (lock-in and match-quality misallocation) account for 38% of tax revenue. The presence of the rental market in the analysis — encompassing both the across-market and within-rental-market channels — accounts for a loss equivalent to 73% of tax revenue, which is two-thirds of the total loss. The paper characterises this as “large.”

Q8. Q: What is the across-market misallocation mechanism behind the 60% welfare loss from tenure distortions?

A: Because owner-occupiers expect to transact more frequently than buy-to-rent investors, the same ad valorem tax falls more heavily on owner-occupiers. In equilibrium, the cost of credit paid by the marginal home-buyer must fall — that is, fewer creditworthy households enter ownership. This displaces some creditworthy households into the rental market, creating a misallocation: properties are allocated away from owner-occupiers (who value them as a place of residence and benefit from match quality) toward rentals intermediated through investors. The welfare loss arises because credit-worthy households who would prefer to own are now renters, and the resource costs of intermediating through investors are incurred unnecessarily.

Q9. Q: What policy experiment does the paper consider beyond the baseline LTT analysis?

A: The paper studies an alternative tax structure that imposes a higher LTT rate on buy-to-rent investors relative to owner-occupiers, calibrated to nullify the implicit tax advantage investors enjoy under a uniform rate. By raising barriers to investor entry, this differential tax reduces the across-market welfare losses from lower homeownership. However, the paper notes an important caveat: pushing the investor tax rate ever higher to boost homeownership would ultimately produce large welfare costs in the opposite direction, as households who cannot qualify for mortgage credit (uncreditworthy households) would be displaced into the ownership market by a shortage of rental properties. Investors play a socially valuable role in providing housing access to households who cannot or choose not to bear the costs of credit.

Q10. Q: What data source is used and why is it unusually well-suited to this analysis?

A: The paper uses Multiple Listing Service (MLS) records from the Toronto Regional Real Estate Board covering the Greater Toronto Area, 2006–2018. The dataset is distinctive in including both sales transactions and lease transactions, allowing the paper to match the two and construct the novel buy-to-rent identifier. MLS data cover approximately 78% of detached-house transactions in the Toronto Land Registry for 2006–2012, and the rental listings capture over 90% of properties listed on alternative platforms. This combination of sales and lease records is what makes it possible to document the three novel empirical facts and to study both the ownership and rental markets jointly.

Key Concepts

Buy-to-rent (BTR) transaction: In this paper’s definition, a sale in the ownership market where the buyer subsequently lists the same property on the rental market within 18 months. BTR buyers are investors/landlords who supply rental housing by purchasing from the ownership market. Distinct from buy-to-own (owner-occupier purchases) and buy-to-sell (flipping) transactions. Identified in the MLS data by matching address and transaction dates across the sales and leases databases.

Buy-to-own (BTO) transaction: A sale in the ownership market where the buyer occupies the property as a homeowner — the residual category after removing BTR and buy-to-sell transactions from total sales. In the City of Toronto, the fraction of all transactions classified as BTO declined from 89% to 84% between 2006 and 2017.

Effective LTT rate: The mean land transfer tax paid as a percentage of the sales price, combining provincial- and city-level taxes, averaged over detached-house transactions in the City of Toronto and adjusted for first-time buyer exemptions. The introduction of the city-level LTT in February 2008 raised the effective LTT rate by 1.3 percentage points (assuming 40% first-time buyers).

Match quality: In the paper’s search model, the idiosyncratic value a particular household places on a particular property, which evolves stochastically over time. When match quality deteriorates sufficiently, a homeowner wishes to move to a better-matched property. Match quality is the source of the “lock-in” effect: higher transaction taxes raise the threshold quality decline a household is willing to tolerate before moving, reducing mobility. Because investors are not tied to a specific property in the same way (a tenant moving out does not require the investor to transact), this mechanism falls more heavily on owner-occupiers than on BTR investors.

Lock-in effect: The reduction in homeowner mobility caused by a higher transaction tax. Homeowners become more tolerant of deteriorating match quality (stay longer in poorly matched properties) and more selective when initially purchasing (require higher match quality to justify the transaction cost). The paper treats this as operating on the intensive margin of homeownership decisions, contrasted with the extensive margin (the own-vs.-rent choice).

Credit cost / credit friction: Heterogeneous household-level costs of accessing mortgage finance or credit. In the model, a household must pay a credit cost to enter the ownership market. Households with lower credit costs are more likely to choose homeownership; a higher transaction tax effectively raises the total cost of ownership (since it must be paid on each future move), shifting the margin at which the credit cost equals the net benefit of owning, thereby reducing the equilibrium homeownership rate.

Leases-to-sales ratio: The ratio of new lease transactions to sales transactions in the housing market, used as a measure of the relative activity of the rental and ownership markets. A higher ratio indicates more households are being accommodated in the rental market relative to the ownership market. The LTT raises this ratio by 26% in the empirical estimation and 15% in the four-year model simulation, with a steady-state increase of 23%.

Price-to-rent ratio: The ratio of house prices to rents, used as a summary statistic for the relative cost of owning versus renting. In the paper’s model, a fall in the price-to-rent ratio is the price signal that attracts additional buy-to-rent investor entry: as tenure-choice distortions shift more households toward renting, rents rise relative to prices, improving the return to BTR investment until the rental market clears. The LTT lowers the price-to-rent ratio by 3.8% empirically and 1.6% in the four-year model simulation.

Deadweight loss as a fraction of tax revenue: The welfare cost of the LTT measured in units of tax revenue raised, allowing comparison across tax instruments. The paper finds a deadweight loss of 111% of tax revenue for the Toronto LTT. Prior literature, which focused only on the intensive margin (mobility distortions within the ownership market), missed the across-market and within-rental-market channels that together account for 73 percentage points of this total.

Summary based on published open-access version. AI-assisted, human review pending.