[Skip to main content](/content/review/b3e64110-83ee-4fd7-87d8-65a6fe06010b/source/4f962575d3f54a01b8d4f54dcd6f36f0#main-content/index.html) Effects of Rent Control on Housing Dynamics (public) Research reportView only Loading... AlertsChat September 12, 2025 # What are the effects of rent control policies on housing market dynamics and tenant stability? ## Rent control policies yield mixed results, decreasing rents in controlled units by 4-47% and extending tenant stays by up to six years, while simultaneously reducing housing supply and increasing eviction filings, with effects varying by policy design and local market conditions. # Abstract Rent control policies yield mixed effects on housing market dynamics and tenant stability. In regulated markets, studies report rent declines ranging from 4% to 47% in controlled units while some analyses note rent increases in uncontrolled or post‐decontrol sectors. In one San Francisco study, rents rose concurrently with a 15% reduction in housing supply and a 20% drop in tenant mobility. Other research documents tenants staying an extra six years under tighter regulation, although reports of 83–127% higher eviction filings suggest displacement risks in certain settings. Separate analyses show shifts in market composition. For example, one study cited annual rent subsidies of about US$2440 (roughly 27% of income), and another observed reduced racial disparities accompanied by increased minority presence. These findings, based on quasi‐experimental and econometric approaches across diverse jurisdictions, indicate that the impacts of rent control vary with policy design and local market conditions. Methods We analyzed 40 sources from an initial pool of 989, using 8 screening criteria. Each paper was reviewed for 5 key aspects that mattered most to the research question. More on methods Papers identified with Elicit search n = 989 Papers screened using: Intervention Type, Outcome Measures, Study Design, Geographic Context, Public/Social Housing Focus, Housing Voucher/Assistance Focus, Empirical Data, Comparison Groups n = 989 Papers screened out n = 949 Papers included for extraction n = 40 Press enter or space to select a node.You can then use the arrow keys to move the node around. Press delete to remove it and escape to cancel. Press enter or space to select an edge. You can then press delete to remove it or escape to cancel. ## Paper search Using your research question “What are the effects of rent control policies on housing market dynamics and tenant stability?”, we [searched](https://support.elicit.com/en/articles/553025) across over 126 million academic papers from the [Semantic Scholar](https://www.semanticscholar.org/) corpus. We retrieved the 989 papers most relevant to the query. ## Screening We screened in sources based on their abstracts that met these criteria: - **Intervention Type**: Does this study examine rent control, rent stabilization, or rent regulation policies? - **Outcome Measures**: Does this study measure at least one of the following: housing market outcomes (rental supply, housing prices, construction rates, property maintenance, market competition) OR tenant stability outcomes (residential mobility, displacement rates, tenure length, eviction rates, housing security)? - **Study Design**: Is this study one of the following: randomized controlled trial, quasi-experimental design, natural experiment, longitudinal study, cross-sectional study with comparison groups, systematic review, or meta-analysis? - **Geographic Context**: Was this study conducted in urban or metropolitan areas with rental housing markets? - **Public/Social Housing Focus**: Is this study NOT focused solely on public housing or social housing programs without rent control components? - **Housing Voucher/Assistance Focus**: Is this study NOT examining only housing voucher or rental assistance programs without rent regulation? - **Empirical Data**: Is this study NOT purely theoretical or modeling without empirical data? - **Comparison Groups**: Is this study NOT a case study or descriptive study without comparison groups or control conditions? We considered all screening questions together and made a holistic judgement about whether to screen in each paper. ## Data extraction We asked a large language model to extract each data column below from each paper. We gave the model the extraction instructions shown below for each column. - **Study Design Type**: Identify the primary research design used in the study. Look in the methods section for explicit description of the study design. Possible design types include: - Difference-in-differences - Quasi-experimental - Empirical analysis - Econometric study - Cross-sectional analysis If multiple design elements are used (e.g., difference-in-differences with discontinuity design), list all relevant approaches. Be precise about the specific methodological approach. If the design type is not clearly stated, review the analytical methods and statistical techniques used to infer the most appropriate design classification. - **Geographic Setting and Context**: Extract the specific geographic location(s) where the study was conducted. Include: - Country - City/metropolitan area - Specific neighborhoods or regions (if applicable) If multiple geographic areas are studied, list all of them. Note any specific contextual details about the housing market that are relevant to understanding the rent control policy (e.g., housing density, urban vs. suburban, economic conditions). If geographic context is not explicitly stated, check methods, data sources, and results sections for implicit geographic information. - **Rent Control Policy Details**: Extract comprehensive details about the rent control policy: - Year of policy implementation - Specific type of rent control (first-generation, second-generation, etc.) - Key policy mechanisms (e.g., price caps, exemptions) - Scope of application (which housing units are covered) Look in introduction, methods, and policy description sections. If multiple policy aspects are discussed, provide a comprehensive summary. If policy details are complex, create a bulleted list to capture nuanced information. Note any explicit exceptions or special conditions in the policy. - **Policy Impact Outcomes**: Identify and extract the specific outcomes measured related to rent control policy: - Rental prices (regulated and unregulated sectors) - Housing supply - Land values - Maintenance investments - Tenant stability - Demolition rates - Housing market dynamics Extract quantitative values where available. If multiple outcomes are measured, list all with their specific measurements and statistical significance. Prioritize outcomes directly addressing rental prices, housing supply, and market dynamics. Look in results and discussion sections for comprehensive outcome reporting. - **Key Quantitative Findings**: Extract the primary quantitative results, focusing on: - Magnitude of effects - Statistical significance - Confidence intervals or standard errors (if provided) - Directional impact of rent control policy Prioritize results that directly answer the research question about housing market dynamics and tenant stability. If multiple statistical models or analyses are presented, extract results from the primary or most comprehensive analysis. Include specific numeric values and percentage changes where available. Ensure extracted findings are directly quoted or paraphrased from the results section, maintaining the original statistical context. # Results ## Characteristics of Included Studies Study Study Location/Period Rent Control Policy Type Primary Outcomes Measured Methodology Full text retrieved Diamond et al., 2019a San Francisco, USA; 1994 onward Not explicitly labeled; limits rent increases, multi-family 2-4 units built 1900-1990 Rental prices, housing supply, tenant stability, maintenance Quasi-experimental Yes Jofre-Monseny et al., 2023 Catalonia, Spain; 2020 Not specified; price caps, high coverage Rental prices, housing supply Difference-in-differences, event-study, quasi-experimental No Munch & Svarer, “Rent Control and Tenancy Duration” Denmark Not specified in abstract Tenancy duration, mobility Econometric study No Mense et al., 2017 Germany; 2015 Second-generation; exception for new units Rental prices, land values, supply, maintenance Difference-in-differences with discontinuity, quasi-experimental No Breidenbach et al., 2021 Germany; 2015 Not specified in abstract Rental prices, quality Quasi-experimental (triple difference event study) No Mense et al., 2019 Germany; 2015 Second-generation; rent ceiling, multiple exceptions Rental prices, supply, land values, maintenance, mobility Quasi-experimental (difference-in-differences with discontinuity) Yes Gyourko & Linneman, 1989 New York City, USA; 1943 onward First-generation; rents frozen, later exemptions Rental prices, supply, tenant stability, maintenance Econometric, cross-sectional Yes Autor et al., 2012 Cambridge, MA, USA; 1970-1995 First-generation; strict caps, no vacancy decontrol Rental prices, supply, land values, maintenance, turnover Quasi-experimental, difference-in-differences, econometric Yes Early & Phelps, 1999 USA; 1984-1996 Not specified; new construction exempt Rental prices (uncontrolled sector), supply Econometric study No Fallis & Smith, 1985 Toronto, Canada Not specified; exemptions Rental prices (controlled/uncontrolled) Econometric, cross-sectional No toof Pageof View 30 more rows Across 40 studies of rent control policies, the following patterns were observed: Primary Outcomes Measured: - Rental prices:Measured in 25 studies. - Housing supply (including new construction and conversions):Measured in 20 studies. - Tenant stability (including tenure duration, mobility, turnover, and displacement):Measured in 16 studies. - Maintenance, quality, investment, or renovations:Measured in 9 studies. - Evictions or eviction filings:Measured in 3 studies. - Land values, property values, or wealth transfer:Measured in 5 studies. - Vacancy rates:Measured in 2 studies. - Market dynamics (including spillovers, misallocation, search/matching costs, and disequilibrium):Measured in 6 studies. - Rent burden, rent discounts, or rent subsidy:Measured in 4 studies. - Community composition or segregation:Measured in 2 studies. - Owner/tenant knowledge, queue time, and income distribution:Each measured in 1 study. - Other outcomes (such as distribution, race, tenant welfare, and consumption):Found in 5 studies. Rent Control Policy Type: - First-generation rent control:Studied in 7 studies. - Second-generation rent control:Studied in 10 studies. - Third-generation rent control:Studied in 1 study. - Rent stabilization:Explicitly labeled in 3 studies. - No clear specification of policy type:21 studies. - User value system (other):1 study. Methodology: - Quasi-experimental methods (including difference-in-differences, event study, regression discontinuity, interrupted time series, and triple difference):Used in 24 studies. - Econometric methods (including cross-sectional and empirical econometric analysis):Used in 21 studies. - Empirical analysis (not otherwise specified):Used in 11 studies. We did not find mention of some outcomes or policy types for several studies, either due to lack of reporting or lack of access to the full text. * * * ## Effects ### Effects on Housing Market Dynamics Study Outcome Measure Effect Direction Effect Size Statistical Significance Diamond et al., 2019a Market rents, supply Increase in rents, decrease in supply 15% supply reduction, 20% decrease in mobility No mention found Jofre-Monseny et al., 2023 Average rents Decrease in rents 4–6% reduction No mention found Munch & Svarer Tenancy duration Increase in duration +6 years (most vs. least regulated) No mention found Mense et al., 2017 Rents (regulated/unregulated), land values Increase in unregulated, decrease in regulated, increase in land values No mention found No mention found Breidenbach et al., 2021 Rental prices Decrease in rents (short-term) Up to 5% (all), 9% (some types) Significant, effect vanishes after 1 year Mense et al., 2019 Regulated/free-market rents Decrease in regulated, increase in free-market No mention found No mention found Gyourko & Linneman, 1989 Rent subsidy Increase in subsidy $2440/year (27.2% income) 95% confidence interval: $2367–$2511 Autor et al., 2012 Rents, property values Increase in rents post-decontrol 40% (controlled), 13% (never-controlled) No mention found Early & Phelps, 1999 Uncontrolled rents Increase in rents Positive, significant Yes Fallis & Smith, 1985 Rent difference Attributable to controls ~50% of difference No mention found toof Pageof View 30 more rows Across 40 studies, the following patterns were observed in effect direction and statistical significance: - Decrease in rents:Reported in 11 studies. - Increase in rents:Reported in 10 studies. Some studies reported both increases and decreases, depending on market segment (for example, regulated versus unregulated units). - Decrease in supply or construction:Found in 4 studies. - Increase in supply or construction:Found in 3 studies. - Increase in tenant stability or tenure:Found in 2 studies. - Decrease in tenant stability or tenure:Found in 1 study. - Increase in evictions or displacement:Found in 3 studies. - Decrease in evictions or displacement:Found in 1 study. - Increase in property or land values:Found in 1 study. - Decrease in property or land values:Found in 1 study. - Increase in vacancy:Found in 2 studies. We did not find studies reporting a decrease in vacancy. - Increase in rent burden, savings, discounts, or subsidy:Found in 5 studies. - Mixed, minimal, or no effect:Reported in 5 studies. - Other outcomes (queue times, demographic changes, misallocation costs):Reported in 2–3 studies. Statistical significance: - Explicit statements of statistical significance:Found in 9 studies, based on available full texts or abstracts. - Explicit statements of non-significance:Found in 2 studies. - No mention of statistical significance:In the available full texts or abstracts for the remaining 29 studies. The most common outcome measures were rents or rental prices, supply or construction, tenant stability, tenure or mobility, evictions or displacement, property or land values, and rent burden, savings, or subsidy. We did not find mention of outcome measure information in the available full texts or abstracts for some studies, and some studies reported multiple outcomes. * * * ### Effects on Tenant Stability and Demographics ### Tenant Composition and Income Distribution Study Outcome Measure Effect Direction Effect Size Statistical Significance Gyourko & Linneman, 1989 Rent subsidy, tenure Increase in subsidy, increase in tenure $2440/year, significant tenure increase 95% confidence interval: $2367–$2511 Donner & Kopsch, 2023 Subsidy, queue, income Increase in subsidy for high-income, increase in queue 21 vs. 10 years (high vs. low subsidy) No mention found Chen et al., 2023 Rent discount, race Decrease in racial disparity, increase in discount $410/month, $4–5.4B/year No mention found Sims, 2011 Minority/poor presence Increase in minority, decrease in poor No mention found Robust Zapatka & Galvao, 2022 Rent burden, composition Decrease in burden, increase in Hispanic/foreign-born No mention found No mention found Ahern & Giacoletti, 2022 Wealth transfer Regressive 2–8% by income Significant toof Pageof Across these 6 studies: - Outcome measures: - Rent subsidy or discount: 2 studies. - Regressive or high-income benefit effects: 2 studies. - Minority or racial/ethnic composition or disparity: 2 studies. - Rent burden: 1 study. - Wealth transfer: 1 study. - Some studies covered multiple topics. - Effect direction: - Regressive effects or greater benefits for high-income groups: 2 studies. - Positive effect of subsidy on tenure: 1 study. - Reduced racial disparity: 1 study. - Increased minority presence and decreased poor presence: 1 study. - Reduced rent burden with increased Hispanic/foreign-born presence: 1 study. - Statistical significance: - Statistical significance or robustness was reported in 3 studies, based on available full texts or abstracts. - We did not find mention of statistical significance in the available full texts or abstracts for the other 3 studies. * * * ### Residential Mobility and Tenure Duration Study Outcome Measure Effect Direction Effect Size Statistical Significance Diamond et al., 2019a Mobility Decrease in mobility 20% reduction No mention found Munch & Svarer Tenancy duration Increase in duration +6 years No mention found Mense et al., 2019 Mobility Decrease (high-income), increase (low-income, short distance) No mention found No mention found Karpestam, 2022 Mobility Decrease (older units), increase (newer units) 5.7% decrease with 10% increase in income No mention found Nagy, 1997 Tenure duration Increase in duration (stabilized) No mention found No mention found Chapple et al., 2022 Outmigration Decrease (low socioeconomic status, stabilization), increase (market-rate) 1–2% increase in outmigration No mention found toof Pageof Across these 6 studies: - Outcome measures: - Mobility: 3 studies. - Tenancy or tenure duration: 2 studies. - Outmigration: 1 study. - Effect direction: - Decrease only (in mobility): 1 study. - Increase only (in tenancy/tenure duration): 2 studies. - Mixed effects, with both increases and decreases depending on subgroup or context (for example, by income, unit age, or stabilization status): 3 studies. - Effect sizes: - 20% reduction in mobility: 1 study. - 5.7% reduction in mobility with a 10% increase in income: 1 study. - Increase of 6 years in tenancy duration: 1 study. - 1–2% increase in outmigration: 1 study. - Statistical significance: - We did not find mention of statistical significance in the available full texts or abstracts for any of the 6 studies. * * * ### Neighborhood Segregation and Community Composition Study Outcome Measure Effect Direction Effect Size Statistical Significance Sims, 2011 Segregation Increase in segregation No mention found Robust Chapple et al., 2022 Exclusionary impact Increase in exclusion No mention found No mention found Chen et al., 2023 Racial disparities Decrease in disparities No mention found No mention found toof Pageof Across these three studies: - Outcome measures: - Segregation: 1 study. - Exclusionary impact: 1 study. - Racial disparities: 1 study. - Effect direction: - Increase in the measured outcome (segregation or exclusion): 2 studies. - Decrease in disparities: 1 study. - Statistical significance: - Statistical significance was described as “robust” in 1 study. - We did not find mention of statistical significance in the available full texts or abstracts for the other 2 studies. ## References [Jordi Jofre-Monseny, Rodrigo Martínez-Mazza, M. 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Back ## Rational Eviction: How Landlords Use Evictions in Response to Rent Control Eilidh Geddes, Nicole Holz Social Science Research Network· 2025· 3 citations SourceDOI Plain textPDFFigures Searching for PDF Unable to find PDF from source Back Study Design Type Difference-in-differences Geographic Setting and Context \- Country: United States \- City/metropolitan area: San Francisco \- Specific neighborhoods or regions: Not specified, but ZIP code-level data is used \- Contextual details: Urban area with high housing costs and density Rent Control Policy Details \- Year of policy implementation: 1994 \- Specific type of rent control: Involves rent increases capped at 60% of the regional CPI \- Key policy mechanisms: Price caps (60% of the regional CPI), exemptions for small owner-occupied buildings before 1994, vacancy decontrol, just cause regulations for evictions \- Scope of application: Buildings with fewer than 5 units that were owner-occupied and built before 1980 Policy Impact Outcomes \- Tenant stability: 83% increase in eviction notices, 125% increase in wrongful eviction claims \- Housing market dynamics: Effects concentrated in low-income areas, higher in years when rent control provisions are more binding \- Rental prices: Weak evidence of small declines in rents in heavily exposed ZIP codes Key Quantitative Findings \- For every 1,000 newly rent controlled units, there were 12.05 additional eviction notices and 4.6 wrongful eviction claims. \- 83% increase in eviction notices and 125% increase in wrongful eviction claims in areas with average exposure to rent control. \- Annual effect: 20.07 additional eviction notices per 1,000 treated units. \- Effects are statistically significant and persistent. \- Policy change led to 847 additional evictions, which is 59% of the total increase from 1994 to 2000. Rent control policies seek to ensure affordable and stable housing for current tenants; however, they also increase the incentive for landlords to evict tenants since rents re-set when tenants leave. We exploit variation across zip codes in policy exposure to the 1994 rent control referendum in San Francisco to study the effects of rent control on eviction behavior. We find that for every 1,000 newly rent controlled units in a zip code, there were 12.05 additional eviction notices filed in that zip code and an additional 4.6 wrongful eviction claims. These effects were concentrated in low income zip codes. Applied and Frank Limbrock for help with data applications. David Dranove for helpful paper and title suggestions. All errors are our own. Any opinions expressed paper 1Introduction As housing prices rise, more cities and states are turning to rent control policies with the goal of ensuring long-term affordable housing. 1 In a typical rent control policy in the United States, leases must be renewed at statutorily limited rent increases. Rent control policies reduce the returns from operating in the rental market, creating well-studied incentives to leave it. To moderate these incentives, many rent control policies include "vacancy decontrol" provisions, which allow landlords to reset rents to market rates when tenants move. These policies limit the reductions in returns to operating in the rental market but create incentives to induce tenant turnover, either through tenants moving or evictions. The more often tenants move, the more often a landlord can raise rents to market rates. In this paper, we examine whether a large-scale rent control expansion in San Francisco led to more eviction notices or increased complaints about wrongful evictions. We document a large increase in eviction notices and complaints, concentrated in buildings directly affected by the policy. We then use a differences-in-differences research design that exploits ZIP codelevel variation created by the passage of a 1994 ballot referendum that led to the removal of a rent control exemption for small buildings built before 1980. We find substantial increases in both the number of eviction notices and wrongful eviction claims filed with the San Francisco Rent Board in areas more affected by the policy change. We begin by documenting a sharp increase in eviction notices reported to the Rent Board overall starting in 1995, when rent control was expanded. Under San Francisco's Rent Ordinance, unless the tenant is in breach of the lease in some way, legal evictions require the landlord or a member of their immediate family to occupy the unit after the tenant leaves, remove all rental units from the rental market under the Ellis Act, 2 or demolish the rental unit. The rise in eviction notices is concentrated in the types of evictions that are most related to rent control-based incentives: owner move-in evictions and Ellis Act evictions. These evictions remove units from the rental stock, at least in the short term. Owner movein evictions preserve the opportunity for the landlord to return to the rental market. We do not observe large increases in evictions that landlords cannot directly control, such as evictions for non-payment. We also observe a sharp increase in claims of wrongful eviction. Wrongful evictions include a misrepresentation of the owner's plans to the tenant to convince them to leave 1 Oregon adopted a state-wide rent control policy in 2019. Saint Paul, Minnesota adopted rent control policies in 2021. New York state expanded rent stabilization policies to more municipalities in 2019. 2 CA Govt Code § 7060 (2022) earlier, incorrect notice being given around an eviction, or a self-help eviction in which the landlord either removes the tenant directly or interferes with the habitability of the unit. While there are many ways for a landlord to legally evict, these generally do not allow the landlord to receive the immediate benefit of resetting the rent to the market rate. For example, with an Ellis Act eviction, the owner must remove all units from the rental market. In contrast, wrongful evictions may produce this benefit for the landlord. Our ZIP code-level differences-in-differences analysis compares ZIP codes with more and fewer units that become newly eligible for rent control based on their age and size. We find an 83% increase in eviction notices filed with the Rent Board and a 125% increase in the number of wrongful eviction claims for ZIP codes with the average level of new exposure to rent control. These estimates are robust to a variety of alternative specification choices, including those that leverage sub-ZIP code variation for a subset of our outcome variables where more granular data are available. The increase in evictions occurs gradually over the five years following the policy change, likely due to market rents increasing over time. Our largest effects occur in years in which rent control would be particularly binding, as measured by a large gap between the rise in average rent prices and the allowed rental price increase under rent control. These effects are large and economically significant. We find an annual effect of an increase of 20.07 eviction notices per 1,000 treated units in a zip code. Over the six years in our post period (1995-2000), this translates roughly into 12% of newly rent controlled units receiving an eviction notice. If even a small fraction of these eviction notices result in tenants moving, these eviction proceedings represent a substantial limitation on the rent control policy's ability to ensure that tenants can stay in their existing housing situation, even if the policy on net resulted in a decrease in mobility (Diamond et al. (2019)). One important facet of the policy context is that eviction notices and wrongful eviction claims are collected only for rent controlled units. Therefore, some increase in evictions post-expansion would be expected if landlords of newly rent controlled units behave the same as the landlords of previously rent controlled units, who own larger buildings that were rent controlled many years before. We show that evictions increase above and beyond the expected mechanical increase that would arise from more units being subject to eviction reporting requirements (that which would be expected if the behavior of small-building landlords exactly replicates the behavior of previously controlled landlords), suggesting either that the policy expansion created excess short-run evictions or that small-building "momand-pop" landlords optimize differently in the face of rent control than the landlords of larger buildings do. To help distinguish between these two possible explanations, we compare buildings with 3-4 units that are newly rent controlled to buildings with 5-6 units3 that were previously rent controlled; we observe more evictions at buildings with 3-4 units, which is consistent with our results being driven by reoptimization behavior by landlords in the period immediately following the implementation of rent control. We additionally document heterogeneity with respect to median income in a given ZIP code, where our estimated effects for low-income ZIP codes are at least 60% higher than our estimated effects for high-income ZIP codes. This heterogeneity is important in the setting of rent control in which the goal of the policy is to prevent lower-income tenants from being displaced from their homes when rents rise. We do not find similar heterogeneity by rent prices or changes in rent prices suggesting this discrepancy is not being primarily driven by rent-based incentives for landlords. Understanding the distributional consequences is important for policy makers in situations in which concerns about gentrification may be a major driver of the adoption of rent control policies. Our paper contributes to the literature on rent control (Autor et al., 2014; Early, 2000; Glaeser and Luttmer, 2003; Olsen, 1972; Sims, 2007) by documenting the behavior of landlords who stay in the market, by showing that this response leads to formal complaints filed by tenants, and by highlighting the dynamics of this behavior over time. Much of the literature looking at supply-side responses focuses on how supply to the rental market is affected. The most closely related paper, Diamond et al. (2019), uses the same institutional setting and similar research design and finds that landlords reduced the rental supply by 15% by selling to owner-occupants and redeveloping buildings, while rent control limited renter mobility by 20%. Whereas Diamond et al. (2019) focuses on how landlords respond to rent control by exiting the market, our paper shows how landlords adjust their behavior while staying in the rental market, or at the very least, preserving the option to easily re-enter. These additional evictions can limit the positive anti-displacement effects of rent control. We make several further contributions. Basu and Emerson (2000)'s model shows how rent control policies such as San Francisco's create an inherent adverse selection problem in which landlords do not know how long a given tenant intends to stay in a unit. Morestationary tenants are less profitable because landlords cannot reset the rent until the tenant leaves. Our finding of an increase in evictions in response to the policy change suggests that landlords newly subject to rent control may be particularly prone to use eviction proceedings to get a new draw from the pool of tenants. Additionally, we show how the use of vacancy decontrol as a tool in the rental market coincides with periods in which rent control is particularly binding. Whereas one may expect evictions to spike immediately after the policy was passed (through landlords converting to condos or otherwise exiting the market), our results show that evictions do not increase until landlords have a financial reason to attempt to re-let, when market rents across San Francisco exceed the allowed increase in rental prices. Finally, our work shows heterogeneity across landlords in the propensity to use these tools; the rise in eviction notices we find exceeds the increase had pre-policy landlord behavior continued. Our results highlight that landlords are able to use the evictions process to circumvent rent control policies and that the use of these evictions proceedings spikes in periods of rapid rent increases. Other work in this area focuses on the effects of price changes on eviction behavior. Asquith (2019a) and Asquith (2019b) examine how landlords in San Francisco respond to price increases under rent control using bus lines as an instrument for prices. These papers find evidence of an increase in owner move-in evictions, consistent with our findings, but no evidence of increases in Ellis Act evictions. Additionally, there were increases in condo conversions. Pennington (2021) finds that evictions in rent controlled units fall after rents decrease due to an increase in housing supply. Our contributions are complementary to these findings: we document the effects of an expansion of rent control, which may affect the market differently than price changes, specifically study "wrongful" eviction claims, and highlight that different types of landlords may behave differently. In particular, small landlords may have a greater ability to leverage owner move-in evictions. The rest of this paper is organized as follows. Section 2 discusses the institutional details of rent control in San Francisco. Section 3 describes the theoretical context. Section 4 describes the data, and Section 5 describes our empirical design. Section 6 describes our results: we find an increase in wrongful eviction claims and eviction notices following the removal of a rent control exemption. Finally, Section 7 concludes. 2Background In this section, we describe the details of rent control in San Francisco and the policy variation that we study in this paper. In 1979, San Francisco passed its Rent Ordinance (Diamond et al., 2019). Buildings built and occupied before 1979 above a certain size had rent increases capped at 60% of the regional CPI (Asquith, 2019b).4 Under this legislation, rents would likely fall below market-rate rents over time. Under the Rent Ordinance, small (less than 5 units) owner-occupied buildings were exempted from rent control. This exemption was lifted by the passage of a ballot referendum in 1994,5 which expanded the number of units subject to rent control within San Francisco by about 68% for the average ZIP code. As of 2015, roughly 60% of San Francisco's rental stock was rent controlled (40% of the overall housing stock), largely because a sizable amount of the rental stock was built before 1979 (San Francisco Planning Department 2018). San Francisco's rent control policy features "vacancy decontrol," which allows landlords to reset the rent to market rate when a tenant leaves the unit (Asquith, 2019a). 6 These regulations also include "just cause" regulations, in which landlords must have grounds for a lease termination or eviction.7 Landlords can only evict tenants for one of 16 specific legal reasons, and they must have an "honest intent, without ulterior motive." Landlords can then raise rents to market rate only in a limited number of situations. Specifically, they can raise the rent when a tenant leaves the apartment. Therefore, landlords might be incentivized to offer a cash buyout to existing tenants to induce them to move. Landlords can also perform an owner-move in eviction. Such an eviction could entail the landlord or an immediate family member moving into a unit; it could also entail selling some fraction of the building to a third-party, who could then owner-occupy one unit. 8 On the one hand, this is less financially beneficial, since although they can raise the rent after a true owner move-in eviction, they would raise the rent on themselves or an immediate family member. If they re-let the unit before three years has passed, the rent control regulations prohibit them from raising the rent above what the prior tenant would have paid. 9 On the other hand, it is easy for landlords to evade these laws. The Rent Board only audits 10% of units each year, and if a unit's rent is found to be higher than what is allowed based on owner tenancy and rent control laws, the landlord will be assessed a fee of up to $1,000 per month when excess rent was charged. 10 This means that in expectation, the punishment for evading the owner-move-in evictions laws is quite low. Many landlords may find the idea of claiming an immediate family member will move in, forcing the current tenant to leave, and then re-letting to a new tenant at market price attractive, even though it is technically illegal. There are additional potential benefits associated with leasing to a new tenant: if the previous tenant was likely to reside in the unit for many years, it may be financially advantageous to find a new tenant. Owner move-in evictions thus preserve some option value; the owner can choose when to return to the rental market or keep the unit owner-occupied. One potential way that landlords can respond to the expansion of rent control is by removing their units from the rental market by converting to condos. Condo conversion was further incentivized by the passage of the Costa-Hawkins Rental Housing Act in 1995. This Act banned cities from applying rent control to single family homes or condominiums. To combat condo conversions, San Francisco has a number of provisions that aim to limit the ability of landlords to convert to condos. In 1993, the city established a 200-unit limit on condo conversion for 6 or fewer unit buildings for four years. In December 1994, the city established lottery pools: the eligibility requirements for these pools effectively blocked landlords of newly rent controlled buildings from participating in the lottery for two years. This creates an upper bound on the number of evictions that can be attributed to the condo conversion lottery. Starting in 1997, applicants could convert to condos if they had 2-6 units, 1 or more units were continuously occupied by one of the owners for three continuous years, and they won the lottery with a cap of 200 units per year. In 2001, the city established a lottery bypass for buildings with 2 units where, conditional on satisfying ownership requirements, an unlimited number of owners could convert to condos. For additional details on this lottery (and the history of rent control in San Francisco), see Asquith and Reed (2021) and Asquith (2020). Figure 1 shows the total number of eviction notices per year in San Francisco split 9 https://sfrb.org/topic-no-204-evictions-based-owner-or-relative-move 10 A punishment of up to six months of imprisonment in the county jail is also possible for landlords who violate rent control laws. Notes: This figure shows the number of eviction notices filed with the San Francisco Rent Board by type over time. Owner move-in and Ellis Act evictions can be initiated by the landlord without some violation of the lease contract by the tenant. Non-payment, breach, and nuisance evictions all require some kind of action by the tenant. It is not possible to further break down evictions classified as "Other." Data Source: San Francisco Rent Board Evictions Notices (San Francisco Rent Board, 2021) by type. Prior to the policy change, all eviction types trended comparably. After the policy change, nuisance and non-pay evictions have stayed constant,11 while there have been increases in owner move-in, breach, and "other" evictions. The evictions that have risen are "no-fault" evictions, which landlords directly control, and which we would expect to rise most in response to a rent control policy. However, these eviction types are also subject to many regulations, and it is possible that many of these eviction notices were wrongfully handled by landlords. Wrongfully handled "no-fault" evictions are one reason why a tenant might file a wrongful eviction claim with the Rent Board. Other reasons could include being forced out because of repair issues or because of landlord harassment. One of the first steps in fighting a wrongful eviction is filing a claim with the San Francisco Rent Board, which handles reports of evictions that violate Rent Ordinances. If a landlord is found to have wrongfully evicted a tenant in violation of the Rent Ordinances, they face financial penalties. In general, the eviction process begins when a landlord serves an eviction notice to their tenant. The landlord has ten days to file the eviction notice with the Rent Board, but for no-fault evictions, more notice is required. For example, Ellis Act evictions require the eviction notice to be filed with the Rent Board 120 days before the withdrawal date. If the tenant does not move out before the withdrawal date, then the landlord can file and serve an "Unlawful Detainer Summons and Complaint" to the tenant in order to remove them from the unit; the tenant has five days to respond in court. The court will set a trial date and if the landlord wins, a sheriff will carry out the eviction. A wrongful eviction claim can be made at any time during the eviction process,12 though many grounds for wrongful eviction inherently require a notice to be served first. 13 There is no financial cost to filing a wrongful eviction claim; however, the tenant must be aware of the option to do so and pay the hassle cost of filing. Once a wrongful eviction claim is filed, the Rent Board determines whether there is evidence of an unlawful eviction. If so, there will be an investigatory hearing before an Administrative Law Judge, who prepares a report for the Rent Board of Commissioners. The Rent Board of Commissioners will then determine whether to take further action (including making a referral to the District Attorney for criminal prosecution).14 Wrongful eviction claims may vary with tenant incentives. The longer a tenant stays in a rent controlled unit, the lower their relative rent, and the higher the benefit to filing a wrongful eviction claim if they are evicted. 3Theoretical Context In this section, we introduce the choices that landlords must make and discuss how rent control with vacancy decontrol changes the incentives that landlords face. Rent control not only shifts the returns to remaining in the rental market but also changes the value of a new tenant, both through a new opportunity to select a tenant and to set rent. These changes in relative values will affect both the decision to stay in the rental market and landlords' attempt to turn over tenants. We model landlords as making rational decisions at the end of the lease period for each tenant. We first lay out how landlords will behave before rent control with unrestricted rent setting ability and no guaranteed renewals. Landlords first decide whether to stay in the rental market. They remain in the rental market if the expected value of discounted future profits from the rental market exceeds the value of the property; otherwise, they will sell the unit and exit the rental market. Once they decide to stay in the rental market, they decide whether to offer a lease renewal to their existing tenant. They offer a new rental price, taking into account the probability that their tenant accepts and given the value of that tenancy to the landlord. There is some cost of turning over the unit to a new tenant. Because tenants vary in quality (how well they take care of the unit and their propensity to pay rent on time), there is some uncertainty about the quality of a new tenant. The value of an existing tenant is already known. Under this system, long-staying tenants have a higher value to the landlord because they minimize uncertainty and turnover costs. If the landlord decides not to renew the lease, they receive a new set of applications from the tenant pool at the new rental price they post. They pick a new tenant from the set of applications to maximize the expected value of the tenant. After rent control, the choice set of the landlord changes. Again, they must decide whether or not to stay in the rental market. The landlord's options to leave the rental market are limited by regulations. 15 If they stay in the rental market, they face three options. The first option is to continue renting the unit to the existing tenant. If they chose that option, the rent is limited by the rent control regulation. Therefore, continuing to rent to the existing tenant has become a weakly worse option than it was without rent control, depending on whether market rents have risen above the rent increase allowed under the rent stabilization policy. The second option is to legally remove the tenant. This option would involve renting to family members (owner move-in evictions), selling a portion of the building (to enable another owner to live in the building),16 or paying the tenant to leave voluntarily. After a certain time period (for an owner move-in eviction), the owner may then re-rent the unit. Under rent control, the incentives for the landlord may change both rental prices and the tenants that they select. Nagy (1997) suggests the prices charged upon re-letting may be even higher than those charged in the uncontrolled sector. Basu and Emerson (2000) show that the value of tenants to landlords decreases with the duration that the tenant stays in the unit, allowing additional future resets of the rental price to occur. Landlords will elect this option if the benefits of the new lease (higher rent, better tenant selection given rent control regime) exceed the costs of the legal eviction (paperwork costs, costs of foregone rent for having a family member or additional owner occupy the unit for a period of time). The third option is to illegally remove the tenant. If unchallenged, this option potentially brings the benefits of higher rent and better tenant selection immediately. However, there are considerable risks and costs involved in a wrongful eviction. The Rent Board audits 10% of units each year to ensure landlords are charging the correct rent. If, for example, a landlord evicted a tenant due to their immediate family member moving in, but then the family member did not move in and the unit was instead leased at a price higher than that which the previous tenant paid, the landlord can be fined up to $1,000 per month of overcharged rent and can be sentenced to up to six months in the county jail. Tenants also have the ability to file wrongful eviction claims. Fighting these claims imposes some cost initially on the landlord with additional penalties if landlords are found to have violated rent control policies. Several factors may shift the decision making of the landlords. First, note that tenant selection incentives will be strongest when tenants were selected when there was no rent control. Without rent control, landlords are incentivized to screen tenants for longevity. They always have the option of non-renewal or large rent increases, so tenants that minimize turnover costs are preferable.17 However, this tenant is far from optimal under rent control; landlords would prefer to maximize turnover as long as increases in market rent year over year are sufficient to cover turnover costs.18 Landlords who selected tenants when there was no rent control may be stuck with low-turnover tenants who they would prefer to replace with newly screened tenants. These incentives may mean that there is a transition period for landlords whose properties are newly rent controlled; they may behave differently from landlords whose properties were previously rent controlled in the short run. However, in the long run, earlier re-optimizations may result in similar behavior to landlords whose properties were already subject to rent control. This suggests that there may be additional displacement effects in the short run that policy makers may wish to consider if the goal of the policy is to keep existing residents in their homes (as opposed to minimizing displacement of the first set of tenants who lease after a new rent control policy is put in effect). Second, landlords' propensity to engage in wrongful eviction behavior will vary depending on the likelihood of being challenged by a tenant or being caught engaging in wrongful behavior. A landlord is less likely to wrongfully evict a tenant who the landlord anticipates will fight the eviction or has the means to win a larger settlement in the ensuing legal fight. Tenants with lower incomes or who live in neighborhoods with lower median incomes may be even more likely to face a wrongful eviction because their landlords may believe that lower income is correlated with a lower likelihood of hiring legal counsel and effectively navigating the legal system. Finally, the distortionary effects of rent control on the behavior of landlords depends on the degree to which rent control is binding and expectations of landlords about future rent increases. In the extreme, suppose that rent control limits are such that there is no reasonable expectation of rent limitations (for instance, the maximum landlords are able to increase rent is 1,000% year over year). In such a world, we would expect no change in landlord behavior as a result of the policy. In contrast, if market rents are rapidly growing relative to the allowed rent increase, we would expect to see large changes in landlord behavior to induce turnover. This heterogeneity leads us to make several testable predictions that we explore in the data. First, we predict an increase in eviction proceedings that exceeds that of previously rent controlled landlords in the short term. Second, this increase should be concentrated in time periods where market rents exceed the allowable rent increases. Third, we should see larger increases in wrongful eviction claims in neighborhoods where landlords are less likely to expect a successful challenge to an eviction. 4Data In this section, we describe the data we use to measure the expansion of San Francisco's rent control policy at the ZIP code level and the response to this policy by landlords in terms of eviction notices and wrongful eviction claims filed by tenants. 4.1Measuring Rent Control To understand the level of rent control treatment in each ZIP code, we use data on each unit's location, the number of units in the building, and the year the building was built for all residential units in the San Francisco Assessor's Secure Housing Roll from 1999. Since the rent control policy only affected small buildings with fewer than 5 units that were owneroccupied and built before 1980, we categorize buildings as newly rent controlled if they have less than 5 units and were built in 1979 or earlier. The policy only affected owner-occupied units, so we further restrict our definition to buildings with at least 2 units. 19 We describe the construction of this ZIP code level measure in Appendix Section A. We do not have an exact owner-occupancy measure in 1994 when the policy was passed. Figure 2 provides a map of our measure by ZIP code. Notes: This map depicts exposure at the ZIP code level for the San Francisco policy change. Exposure is measured as the number of units in a ZIP code in buildings with 2-4 units that were built prior to 1979. Data sources: 1999 San Francisco Assessor's Secure Housing Roll and authors' calculations Some buildings may be counted as treated when they were actually rent controlled both before and after the policy change because they were not owner-occupied. This miscategorization may attenuate our results.20 In subsection A.2 of the data appendix, we discuss an alternative measure of exposure that attempts to adjust for this owner-occupancy element, defining the alternative treatment measure as the number of buildings with between 2 and 4 units, which were built before 1980, and which were owner occupied in 1999. Our results are robust to using this different measure. We construct further measures of treatment that address the discrepancies that may result from our treatment data coming several years after the implementation of the policy. First, we use other publicly available data sets on building demolitions and parcel splits to directly correct this measure. However, because there are discrepancies between these data sets and the assessor data we primarily use (likely due to the hand-filled nature of the assessor data and updating lags across paper records), we additionally construct "worst-case" scenario treatment measures that assume that: 1) all new single family homes built between 1995 and 1999 replaced a duplex (to account for demolitions), 2) that all condos built before 1980 were converted in the post period, 3) all condo modifications were condo conversions that replaced rent controlled units, and 4) all new condos replaced rent controlled units (to account for condo conversions). Finally, we construct a measure that assumes all new construction in the post period replaced rent controlled units. These measures are highly correlated because there were relatively few changes to the housing stock in San Francisco in the 1990s. 4.2Measuring Evictions We measure the response of landlords to the rent control expansion using the ZIP code-level number of eviction notices and wrongful eviction claims. Both measures originate with the San Francisco Rent Board. 21 We do not observe eventual outcomes; eviction notices may not result in an eviction and wrongful eviction claims may not result in landlords being found in violation of regulations. Our eviction notices data have address information for our entire sample period and the reason for the eviction beginning in 1997. 22 During our sample period, these data are missing ZIP codes of many units and the reason for eviction for many units prior to 1997; we discuss these limitations and our attempts to rectify the missing information in Appendix subsection A.3. Since data on wrongful eviction claims exists at the ZIP code level, we aggregate most analyses to the ZIP code level. 23 Both wrongful eviction claims and eviction notices can only be submitted by individuals who already live in or are landlords of rental units subjected to rent control. When rent control expands, even if the total number of evictions stays constant, the number of wrongful evictions claims could increase solely due to more tenants living in rent controlled apartments 21 One limitation of these data is that only certain types of evictions are required to be reported to the Rent Board; other types of evictions may be optionally reported. (https://www.sf.gov/information/generaleviction-notice-requirements) 22 We thank Brian Asquith for generously sharing the address-level data on evictions post-1997. City-wide data on justifications for eviction notices are also available and are used in Figure 1 . 23 This limitation precludes breaking out wrongful eviction claims per type or conducting any wrongful eviction claims analysis at the sub-ZIP code level. 2) and (3) report averages for ZIP codes with below and above the median level of treatment, measured by the number of newly rent controlled units. The difference between the ZIP codes with higher exposure to the policy change and lower exposure to the policy change is reported in column (4). Stars represent p-values of a t-test comparing the difference in column (4) to zero. Number treated refers to the number of units in buildings with 2-4 units built before 1980. This number is an overestimate of the actual number of treated units as not all of these units were in buildings that were owner-occupied prior to 1994. Data Sources: 1999 San Francisco Assessor's Secure Housing Roll (Office of the Assessor-Recorder, 1999), San Francisco Rent Board Evictions Notices and Wrongful Evictions Claims (Board, 2005; U.S. Census Bureau and Social Explorer, 2022) and therefore being allowed to submit a wrongful eviction claim to the Rent Board. We discuss the implications of this and rule out that this mechanical effect drives results in Section 5. Table 1 displays summary statistics for our analysis dataset. Panel A reports characteristics at the ZIP code level from the 1990 census. We report these statistics for ZIP codes overall, for ZIP codes below the median level of exposure (the "low treatment" group), and for ZIP codes above the median level of exposure (the "high treatment" group). We also report the difference for each characteristic between the control and treatment groups and test whether this difference is statistically significant. We find no differences between our less treated and more treated ZIP codes. In Appendix Table C2 , we include these variables continuously in a regression framework and find no statistically significant relationship between any of these characteristics and the number of treated units. Panel B examines housing characteristics. We see that there are differences across our highly treated and less treated ZIP codes in both pre-and post-period housing characteristics. Our highly treated ZIP codes both have more newly rent controlled units and more units that were previously rent controlled. There are also differences in levels of the number of eviction notices and wrongful eviction claims before the policy. 4.3Patterns In this section, we explore patterns in the data related to our three primary hypotheses. Recall we would expect to see increases in evictions at newly rent controlled buildings where landlords have not previously been able to set rent or pick tenants optimally given rent control regulations. These increases should be larger in periods when there is market pressure to do so in the form of rapidly rising rents. Finally, we should expect more eviction activity in neighborhoods where landlords are less likely to anticipate challenges from tenants. We start by plotting the number of evictions at different building types over time in Figure 3 , subfigure (a). We classify buildings as being previously rent controlled (5 or more units, built before 1980), newly rent controlled (2-4 units, built before 1980), single family buildings (1 unit, not condo classified), and condominiums (1 unit, classified as condos). Before the policy change, all building types trend similarly in terms of eviction notices. After the policy change, there is a sharp increase in evictions at buildings directly affected by the policy change: newly rent controlled buildings. Then, in subfigures (b), (c), and (d), we show the average number of eviction notices, wrongful evictions claims, and owner move-in eviction notices by ZIP code for ZIP codes in Notes: Subfigure (a) plots total evictions in San Francisco by different classifications of buildings. Newly rent controlled buildings are buildings with 2-4 units built before 1980. Previously rent controlled buildings are buildings with 5+ units built before 1980. Condos are buildings listed as condos built before 1980. Subfigures (b) and (c) show the average number of eviction notices and the average number of wrongful eviction reports made to the San Francisco Rent Board, respectively, by year for three treatment tercile groups. Subfigure (d) splits owner move-in eviction notices by treatment terciles for ZIP codes. These data are not available with any reliability at the ZIP code level before 1994. Low treatment ZIP codes are those in the lowest tercile of units newly exposed to rent control after the policy change. Middle treatment ZIP codes are those in the middle tercile. High treatment ZIP codes are those in the highest tercile. Our treatment is measured by the number of units that are newly rent controlled; they are in buildings that were built before 1980 and have 2-4 units. The timing of the policy change is marked by a vertical line. Data Sources: 1999 San Francisco Assessor's Secure Housing Roll (Office of the Assessor-Recorder, 1999), San Francisco Rent Board Evictions Notices and Wrongful Evictions Claims (San Francisco Rent Board, 2021) the lowest, middle, and highest tercile of the number of units newly treated by rent control as determined by the age and unit size of the building. Before the referendum's passage in 1994, all three terciles had roughly constant average reports of eviction notices and wrongful eviction claims. Starting in 1996, we see sharp increases in the number of wrongful eviction claims made in ZIP codes with medium or high levels of units newly exposed to rent control policies. However, in ZIP codes where relatively few units are newly exposed to rent control, we see that wrongful eviction claims remain roughly constant. Because reliable ZIP code-level data on eviction notice types is not available before 1994, we plot owner move-in evictions by treatment terciles starting in 1994 when the data became available. Owner move-in evictions are within control of the landlord, whereas other eviction types either require the landlord to convert to a condo or sell the unit, or require the tenant to have been at fault for the eviction. Thus, we would expect the increase in evictions to be concentrated in owner move-in evictions. From this, we see that the increase in owner move-in evictions in Panel A is driven largely by ZIP codes in the highest treatment tercile. If landlords follow the law, there are only limited reasons why they would want to perform owner-move-in evictions; however, since penalties are low in expectation (only 10% of units are audited annually), landlords may find the risk of illegally re-letting after an owner movein eviction worth taking. Next, we explore whether evictions increase more in times where market rents exceed the rate of increase allowed. Figure 4 displays the allowed rent increase relative to the percent change in the rent CPI along with the number of evictions in different treatment ZIP codes over time. In the ten years between 1995 and 2005, the percent change in rent CPI was far higher than the approximately 2% increases that landlords were allowed, leading to a large incentive to evict and reset rents to the higher market rates. During this same timeframe, evictions were highest, especially for the ZIP codes in the highest tercile of treatment. Subfigure (b) displays this pattern, plotting eviction notices by treatment tercile over the longer time horizon. Finally, we explore whether differences in ZIP code median income are correlated with evictions. We break ZIP codes into six groups, based on treatment tercile and whether the ZIP code has above or below median income. Figure 5 displays both eviction notices (subfigure (a)) and wrongful eviction claims (subfigure (b)) for these groups. The solid lines display the effects for each treatment tercile for low-income ZIP codes, whereas the dashed lines display effects for high-income ZIP codes. There are higher levels of eviction notices and wrongful eviction claims in low-income ZIP codes than in high-income ZIP codes, suggesting Notes: Subfigure (a) shows allowed rent increases and the San Francisco rent price index, both in percent changes year over year. The allowable increase is set to be 60% of the percent increase in the consumer price index in San Francisco, calculated annually for the one-year period ending each October 31. Subfigure (b) shows the average number of evictions by treatment tercile from 1990 until 2010. Data Sources: Rent Arbitration Board (Rent Arbitration, 2022), U.S. Bureau of Labor Statistics, 1999 San Francisco Assessor's Secure Housing Roll (Office of the Assessor-Recorder, 1999), San Francisco Rent Board Evictions Notices and Wrongful Evictions Claims (Board, 2005) that low-income ZIP codes experienced the brunt of the increase in evictions after the rent control policy was expanded. Appendix Figure B5 , subfigure (b) shows wrongful evictions per eviction notice by treatment tercile and income; there does not appear to be a larger or smaller increase in the proportion of notices also being submitted as wrongful eviction claims in low-versus high-income ZIP codes. Together, the patterns in this section show that evictions increased most in the most heavily treated areas, that evictions increased more during times when the incentive to evict was higher due to higher market rents, and that these increases were more dramatic in lower-income areas. 5Empirical Design Thus far, we have presented descriptive evidence documenting a rise in evictions following the passage of the 1994 referendum that lifted the exemption for small owner-occupied buildings. This rise in evictions was concentrated largely in buildings that would have been newly exposed to rent control, in ZIP codes with a high concentration of newly rent controlled buildings, and in eviction types that are in the direct control of landlords, as opposed to those that would require some fault of the tenant. This evidence is consistent with the citywide increase in evictions being driven by the policy change. To further support this hypothesis, we now present a differences-in-differences design that allows us to more rigorously test whether ZIP codes with different levels of exposure to the policy were trending similarly prior to the passage of the policy. We can also quantify the size of the effects over time and test whether the effects were different in ZIP codes with different characteristics. 5.1ZIP Code-Level Analysis To explore whether ZIP codes with more newly rent controlled units experienced more eviction notices and wrongful eviction claims, we use a continuous treatment differences-indifferences design. This design exploits variation across ZIP codes in the number of units who become exposed to rent control policies after the passage of the voter referendum in late 1994. We use this variation as our primary specification because we can then analyze both eviction notices and wrongful eviction claims as wrongful eviction claims are available only at the ZIP code level. Below, we discuss further analysis that we do at the sub-ZIP code level using eviction notices. We estimate the following linear regression model: where α i are ZIP code-level fixed effects;24 τ t are year fixed effects; Post t is an indicator for whether the year is 1995 or after; and Number Treated i is the number of newly treated units at the ZIP code level, calculated as discussed in Section 4. The two outcomes we study are the number of eviction claims at the ZIP code level and the number of wrongful eviction claims at the ZIP code level. 25 estimate this model both in levels (as written in Equation 1), but also as fractions of the total number of units in ZIP codes to account for the fact that denser ZIP codes may have more treated units because they have more units overall. The parameter we aim to identify is the average causal response (ACR), which indicates the additional increase in evictions due to an additional treated unit (Angrist and Imbens, 1995). To identify the ACR, we must make three assumptions: the Stable Unit Treatment Value Assumption (SUTVA), parallel trends, and the homogeneity of the treatment effect across differently treated groups (Callaway et al., 2021). SUTVA requires that there are no spillovers between our treatment groups. This assumption could be violated in our setting if there are either anticipatory effects or spillovers across different ZIP codes. We find no evidence of anticipatory effects in our raw data plots in Figure 3 . Additionally, given that the ballot referendum passed by a small margin, it is unlikely that tenants or landlords would have known whether the referendum would pass ahead of time (Harrison, 1994). A bigger concern is spillovers across units. To interpret our results as causal effects, we must assume tenants in units in less treated areas are not increasingly (or decreasingly) evicted due to price equilibrium effects caused by the policy change. This is more likely to be true in areas that were previously heavily rent controlled because the high stock of rent controlled units would lead to stronger equilibrium effects. The fact that we find that the post-1994 increase in evictions was largely concentrated in units that we would predict were directly affected by the policy bolsters this assumption. While we cannot measure overall rent effects due to lack of available data on rents at the ZIP code level in the 1990s, we can control for the number of previously treated units. We also can sign the size of the bias under the assumption that removing more units from market rents would create upward pricing pressure on market rents. This pricing pressure would create incentives for landlords in all rent controlled units to evict tenants, so if neighborhoods that are less treated by the policy still experience an increase in evictions due to the policy, our estimated effects will be a lower bound. We also make a parallel trends assumption that requires that neighborhoods would have experienced similar trends in eviction levels had they been assigned a different number of treated units. Our raw data plots support this assumption. To further address concerns that ZIP codes with higher levels of treatment may have trended differently from those with lower levels of treatment, we estimate several alternative specifications. First, we include treatment tercile-specific linear time trends. If it was the case that ZIP codes with more housing units (and thus more treated units) were trending differently in the 1990s, this specification should allow us to capture these different trends. Second, we include the interaction between the number of previously treated units and the post period. This both allows us to capture spillovers and to account for differences in the housing stock across more and less treated ZIP codes. Finally, we estimate regressions at the census-tract and building type-ZIP level (described in greater detail in Section 5.2) that allow us to include ZIP-year fixed effects to account for the fact that ZIP codes with more treated units may have trending different in the absence of the policy. Finally, we must assume the homogeneity of treatment effects across differently treated groups. Regardless of the number of rent controlled units in ZIP codes, the treatment effect of adding an additional rent controlled unit must be the same. This assumption would be violated if ZIP codes (or the individuals who live there) could select into different levels of treatment, since the covariates of individuals in neighborhoods who selected into different levels of treatment may affect their potential treatment effect. If this was the case, we would expect to see differences in characteristics potentially related to effect sizes based on the number of treated units. We find no evidence of differences in characteristics across groups in Panel A of Table 1 , although we note that we are not powered to detect small differences. In Appendix Table C2 , we examine these relationships in a linear regression framework and find no evidence of demographic characteristics predicting treatment. 5.1.1Dynamics To explore the dynamics of the effects over time, we break down the pre and post periods into individual years in an event study specification. We interact each year with the number treated units in a given ZIP code. There is a single treatment time in our setting, so event time and calendar time are equivalent. Our event study specification is: (2) We normalize to 1994, the year that the policy passed. 5.1.2Heterogeneity by Median Income We explore heterogeneity by median income in the 1990 census. We group ZIP codes into whether their median income in the 1990 census is above or below the median across ZIP codes. We estimate the following specification: where Low Income i is an indicator for whether a ZIP code's median income was below the median for San Francisco in the 1990 census, and γ t are year low income fixed effects. 5.2Sub-ZIP Code Level Analyses We supplement our main analysis with analysis that uses the individual-level evictions data we have available. We merge address-level eviction notices data with data from the Assessor's office. 26 We then can identify the size of the building at which the eviction occurred. We construct a ZIP code-level measure of the number of evictions at buildings with 2-4 units to estimate the direct effect of the policy. Recall that our main specification may pick up both evictions at newly rent controlled buildings as well as evictions at previously rent controlled buildings. We additionally use these address-level data to identify the number of evictions that occur at the census tract level as well as the number of newly treated units at the census tract level. These data allow us to estimate two additional specifications that include ZIP code by year fixed effects. First, we leverage information on the classification of the building to isolate the effects on newly treated buildings as follows: where Evictions ijt measures the number of eviction notices in ZIP code i for building type j in year t, α j are building type fixed effects, α it are ZIP code by year fixed effects, and Post t × Number Treated i × I(Newly Treated j ) captures the intensity of treatment at the ZIP code level for only the newly affected buildings (this term is zero for all other building types). We classify buildings as newly rent controlled (2-4 unit buildings built before 1980), previously rent controlled (5+ unit buildings built before 1980), condo buildings built before 1980, and single family homes. Second, we estimate regressions at the census tract level as follows: where Evictions cit measures the number of eviction notices in census tract c in ZIP code i in year t, α c are census tract fixed effects, α it are ZIP code by year fixed effects, and Post t × Number Treated c is the interaction of being in the post period with the number of treated buildings in the census tract. 6.1Effect of Rent Control on Eviction Notices We begin by examining the effects of rent control on eviction notices in Table 2 . Column (1) reports our estimate of Equation 1 that leverages variation at the ZIP code level. For every additional 1,000 newly rent controlled apartments, there are 20.07 additional eviction notices filed in that ZIP code. Since there were about 1,688 newly rent controlled units in each ZIP code on average, this effect constitutes an 83% increase over the pre-treatment average level of evictions for the averagely treated ZIP code. Alternatively, we can estimate this proportionally. Column (2) presents results from a specification in which our treatment variable is instead the fraction of total units in a ZIP code who are newly rent controlled, and our outcome variable is the fraction of units in a ZIP code that experience an eviction. Our results from this specification are qualitatively similar to those in our primary specification. Column (3) uses an alternative outcome measure: how many evictions we see at 2-4 unit buildings built before 1980. This specification allows us to examine whether our effects are primarily driven by newly rent controlled buildings. We find that there are 16.88 eviction notices filed at newly rent controlled buildings for every 1,000 newly rent controlled buildings, suggesting that our effects are primarily driven by these newly rent controlled buildings. We build on this analysis in Column (4), where we include as additional control groups other building types and includes ZIP code-year fixed effects. Including these other buildings as control groups allows us to account for ZIP code specific trends in the housing market. Our estimated effect is robust to the inclusion of these fixed effects. In Appendix Table C6 , we further examine the effects on other building types; consistent with this, we find evidence of small spillover effects, but that the effects are concentrated in the newly rent controlled buildings. Finally, in Column (5), we estimate a specification similar to our main specification but instead at the Census tract level. This specification allows for the inclusion of ZIP codeyear fixed effects, again accounting for ZIP code specific trends in the housing market. 27 Our coefficient estimate is very similar to that in the main specification. In Appendix Table C4 , we show robustness to a variety of alternative specification choices. First, we use a binary measure of treatment, which discretizes exposure, to address concerns that rent control exposure should not enter the specification linearly. We compare neighborhoods with above-median numbers of newly rent controlled units to those with below-median exposure. We find large effects comparable to our main specifications. Second, we use an alternative measure of the number of newly rent controlled units to address concerns that we have mismeasured treatment by not accounting for the fact that buildings needed to be owner-occupied to be eligible for the exemption to rent control prior to 1994. In Appendix A, we detail the steps we take to account for this regulatory feature. We find that use of this alternative measure of policy exposure does not substantively change our results; while our estimates change in size, this change is proportional to the change in our treatment variable. Third, we include treatment tercile-specific linear time trends that allow for ZIP codes in different categories to be on different housing market trends through our sample period. Finally, we control for the effect of previously rent controlled units by including the interaction term between the number of previously rent controlled units and the post period. Our results are robust to the inclusion of these additional controls. We further investigate whether our effects can be attributed to the mechanical increase in the number of units whose evictions would be reported to the Rent Board beyond comparing our effect sizes to the effect that would be expected if newly rent controlled units experienced evictions at the same rate as previously rent controlled units. Only units covered by the Rent Ordinance will generate either eviction notices or wrongful eviction claims in our data. Nonrent controlled units may still receive eviction notices for non-payment of rent, but these are not required to be reported to the Rent Board. Additionally, these units are not covered by "just cause" provisions, and so tenancies can be ended without eviction proceedings at all. Because only those in rent controlled units were eligible to submit eviction notices and wrongful eviction claims to the Rent Board, we worry that the effect of rent control on evictions is not due to a behavioral change, but instead mechanical. Suppose 1% of tenants are evicted regardless of rent control status. If an additional 100 buildings are subjected to rent control, then an increase of one eviction would be expected, mechanically. To explore whether the effects we find are mechanical or due to behavioral change, we examine the proportion of rent controlled tenants that face eviction notices before and after the policy change. If the rate of eviction stays constant over time, then the effects are purely due to changes in data reporting, whereas if the rate increases at the time of the policy change, then effects are likely due to behavioral changes by landlords. To evaluate whether our effects are driven by the change in reporting, we compare the average number of eviction notices and wrongful eviction claims to the number of units covered by the Rent Ordinance before and after the expansion of rent control. In 1994, there were 930 eviction notices recorded with the Rent Board across San Francisco and 122,052 total rent controlled units. This represents a 0.7% eviction rate for rent controlled units. By 1998, there were 2,867 evictions with 164,264 rent controlled units, a 1.7% eviction rate, more than doubling the eviction rate in 1994. We cluster standard errors at the ZIP code level, which is our level of treatment variation. Since there are only 25 ZIP codes, we report p-values from a wild cluster bootstrap, which more accurately estimates clustered standard errors when the number of clusters is small (Cameron, Colin A. et al., 2008; Canay et al., 2021). p-values for each relevant regression estimate are calculated using the routine provided by Roodman et al. (2019). 6.2Mechanisms We now turn to a discussion of possible mechanisms. Recall we made three predictions about how the expansion of rent control would affect evictions: eviction notices would rise, they would rise more in periods of rapid rent increases, and they would rise more in ZIP codes where residents are less likely to fight the eviction. We have thus far documented a rise in evictions. We now investigate whether this was accompanied by a rise in wrongful eviction claims, whether our effects are more concentrated in low income ZIP codes, and the time dynamics of our effects. Wrongful Eviction Claims and Heterogeneous Effects By Rent and Income One prediction of our theoretical model is that landlords should engage more in eviction behavior (particularly the wrongful kind) in situations where they expect the costs of doing so to be lower. These costs may be lower for tenants with fewer resources to fight eviction proceedings. One potential proxy for these resources is ZIP code income levels. In Table 3 , we test whether we find effects of expanded rent control on on wrongful eviction claims and we test whether there are different effects, both on wrongful eviction claims and eviction notices, in high and low income ZIP codes. Columns ( 1) and (3) report our estimates of Equation 1 for eviction notices and wrongful eviction claims, respectively. Note that Column (1) is identical to our main specification in Table 2 . For every additional 1,000 newly rent controlled apartments, there are 20.07 additional eviction notices filed in that ZIP code and an additional 7.632 wrongful eviction claims. Since there were about 1,688 newly rent controlled units in each ZIP code on average, these effects constitute an 83% and 125% increase over the pre-treatment average level of evictions for the averagely treated ZIP code. In Appendix Table C5 , we report additional estimates of the effects on wrongful eviction claims from alternative specifications; our results are robust to a variety of additional controls and specification choices. Columns ( 2) and (4) of Table 3 report the results of Equation 3, evaluating whether low-income ZIP codes are more likely to experience higher evictions. We find that lowincome ZIP codes are significantly more affected by the increases in rent control, both in terms of eviction notices and wrongful eviction claims. In our preferred specification, lowincome neighborhoods experience nine more eviction notices per 1,000 treated units than high income ZIP codes. This represents effect sizes that are 63% larger in low-income ZIP codes. Similarly, we find evidence of larger effect sizes for wrongful eviction claims for lowincome ZIP codes relative to high-income ZIP codes; our estimated effects are 160% larger in low-income ZIP codes. One may worry that rent prices and incomes are correlated, and that the large increases in evictions are not due to lower incomes of residents in those ZIP codes but are because rents in lower-income areas start off low and have more room to increase, leading to larger incentives to evict in those areas. In Appendix Figure B8 , we show the relationship between 1990 and 2000 rent and income across ZIP codes in San Francisco. Although income and rent are correlated (especially in 1990), we do not find significantly different effects of rent control on evictions in low-versus high-rent areas as we do when splitting by income (see Appendix Figure B7 ). This suggests that the heterogeneity by income is not explained by differences in rents. Unfortunately, limited data are available on other characteristics of tenants or landlords in these lower income ZIP codes, so we cannot rule out that lower income ZIP codes are different in other ways. For instance, it may be the case that tenants in lower income ZIP codes are particularly likely to stay in their rental units for a long time, increasing the burden of rent control policies for landlords. However, we view these results as suggestive that low income tenants may be particular vulnerable to landlords using eviction proceedings in response to new rent control policies. Dynamics Figure 6 reports our event study coefficient estimates of Equation 2. While there is very little difference between the high-and low-exposure ZIP codes before the policy changed, supporting the parallel trends assumption, after the policy changed, we see that both eviction notices and wrongful eviction claims rise only in ZIP codes with higher levels of exposure. The effect increases over time, consistent with the increasing incentives to evict. We report our differences-in-differences estimates in the dashed line. We additionally report what the mechanical increases in eviction behavior resulting from the increase in the number of units covered by the Rent Board would be, assuming that behavior remained constant from the pre-period. This is the increase in eviction notice reporting that would be expected if newly rent controlled landlords behaved similarly to previously rent controlled landlords. We show that our estimated effects for eviction notices greatly exceed the mechanical effect of the policy, consistent with changing eviction behavior in the post period. Our average estimate of the effect on wrongful eviction claims is not statistically different than the mechanical increase; however, the effect for individual years is statistically significantly higher than the predicted mechanical effect. This suggests that either the type of "mom-and-pop" smaller-scale landlords behave differently than larger-scale landlords in the face of a rent control policy, or that the short-term effects of a rent control policy led to larger increases in evictions than the equilibrium/long-term effect. In Appendix Figure B4 , we show a time series of the number of eviction notices and wrongful eviction claims, which demonstrates a large jump up in the ratio of evictions to rent controlled units following the policy change. This figure suggests that just after rent control expanded, landlords adjust by evicting tenants, many times wrongfully. The gradual increase after the policy change makes sense; as time passes from the policy change, the difference between market rent, which can freely increase, and controlled rents, which can increase by at most about 2% each year, increases. With it increases the incentive to evict a tenant in order to reset the rent to market rate or convert the building to condos. Indeed, Diamond et al. (2019) find an 8 percentage point increase in condo conversions following this same rent control expansion. between year dummies and the number of treated units in a ZIP code. We normalize 1994 to be zero. Error bars shown are for the 95% confidence interval. The differences-in-differences estimate for the interaction of the post-period with the number of treated units is shown as a gray dashed line with the 95% confidence interval shown as a shaded region on the graph. Standard errors are clustered at the ZIP code level. Effects are scaled to be the effect per 1,000 treated units. The average number of treated units in a ZIP code is 1,688. The dark purple circles show what the mechanical effect of the policy change would have been if eviction behavior post policy was consistent with eviction behavior pre policy. Subfigures (c) and (d) show our event study coefficient estimates on the interaction between year dummies and the number of treated units in a ZIP code (light purple) and this added to the interaction of these estimates with the triple interaction with low income (dark purple). Data Sources: 1999 San Francisco Assessor's Secure Housing Roll (Office of the Assessor-Recorder, 1999), San Francisco Rent Board Evictions Notices and Wrongful Evictions Claims (San Francisco Rent Board, 2021) We focus primarily on the short-run effects, as the parallel trends assumptions for our identification strategy become harder to justify in the longer run. However, in Figure 7 , we present suggestive evidence on the longer-term effects on eviction notices and compare these effects to the difference between aggregate rent prices and statutorily allowed rent increases. The effects converge to the expected mechanical increase of 57% by the early 2000s and are higher in periods where rent prices are rising faster than the statutorily allowed rent increases. In particular, we see large effects in the run-up to the dot com bubble, where there is considerable growth in housing prices. 6.3Potential Equilibrium Effects Evaluating the direct effects of the policy on rent is difficult as rent data at the ZIP codelevel from the 1990s are difficult to find. In Appendix Figure B6 , we look at the effects of the policy on rent using ZIP code-level rents from the 1980, 1990, and 2000 census and find weak evidence that rents in ZIP codes that were heavily exposed to this rent control expansion experienced small declines relative to other ZIP codes, possibly due to the direct effects of the policy change. In Appendix A.4, we further explore how the policy may have affected both units directly affected by the policy and those indirectly affected by the policy by leveraging address-level data, which allows us to estimate the effects separately for buildings likely to have been directly affected (those newly rent controlled) and those affected only indirectly (those that were rent controlled before the policy change). In Appendix Table C6 , we estimate the effect of the policy separately for eviction notices at buildings with different classifications. In Panel A, we find a statistically significant effect of the policy only for evictions at buildings that were likely newly rent controlled. We also look at the effects of the number of previously rent controlled units to explore the spillover effects of the policy. In Panel B, we find effects of the number of previously rent controlled units are largest for evictions at previously rent controlled buildings. In Panel C, we include both the number of newly treated units and previously rent controlled units and find that the effects of newly rent controlled units are concentrated on newly rent controlled buildings, where there are possible spillovers to previously rent controlled buildings. 6.4Discussion Several behavioral changes could drive our results: landlords could increase lawful evictions, landlords could increase wrongful evictions, and tenants could change how they challenge evictions. To see our results, landlord behavior must be changing given that we see large increases in eviction notices. These eviction notices are particularly concentrated in owner Notes: Subfigure (a) shows allowed rent increases and San Francisco rent price index, both in percent changes year over year. The allowable increase is set to be 60% of the percent increase in the consumer price index in San Francisco, calculated annually for the one-year period ending each October 31. Subfigure (b) shows our event study coefficient estimates on the interaction between year dummies and the number of treated units in a ZIP code over the longer time horizon from 1990 until 2010. We normalize 1994 to be zero. Error bars shown are for the 95% confidence interval. The differences-in-differences estimate for the interaction of the post period with the number of treated units is shown as a gray dashed line with the 95% confidence interval shown as a shaded region on the graph. Standard errors are clustered at the ZIP code level. Effects are scaled to be the effect per 1,000 treated units. The average number of treated units in a ZIP code is 1,688. Data Sources: Rent Arbitration Board (Rent Arbitration, 2022), U.S. Bureau of Labor Statistics, 1999 San Francisco Assessor's Secure Housing Roll (Office of the Assessor-Recorder, 1999), San Francisco Rent Board Evictions Notices and Wrongful Evictions Claims (Board, 2005) move-in evictions, as shown in Figure B9 , which are in the direct control of the landlord and less likely to be influenced by tenant behavior. 28 is change in evictions could be driven either by an increase in wrongful or legal evictions. We do not find evidence of large changes in the proportion of wrongful eviction claims per eviction notice at the ZIP code level related to the number of newly rent controlled units. However, there is an overall increase in the ratio of wrongful eviction claims per eviction notice: there were 0.25 claims per notice pre policy and 0.34 claims per notice post policy. Newly rent controlled tenants may behave differently in response to an eviction notice than previously rent controlled tenants. This change could go in either direction: If the policy change coincided with greater awareness of tenant rights, there could be an increase in the number of wrongful eviction claims for rent controlled tenants. However, newly rent controlled tenants may either have less incentive to file a claim (their rent is not as far removed from market rent as that of a long-term rent controlled tenant) or may be less aware of the regulations around just cause evictions, making them less likely to file a wrongful eviction claim. Landlords of newly rent controlled buildings may also behave differently than landlords whose buildings were previously rent controlled landlords. We find large increases in the number of eviction notices filed relative to the number of rent controlled units (see Appendix Figure B4 ). This may be because of the "mom-and-pop" nature of the newly controlled landlords, but it also could be because of the sudden change of incentives that newly controlled landlords face. Recall that all newly controlled landlords decided to operate in the rental market at a time when they could charge market rates, select tenants, and set rent prices with the understanding they could increase rents. To provide some evidence on the relative importance of these two mechanisms, we plot a comparison between buildings with 2 units, buildings with 3-4 units, and buildings with 5-6 units in Figure 8 . It is likely that owners of buildings with 3-4 units would be similar to owners of buildings with 5-6 units in the absence of differential rent control legislation. We show that buildings with 5-6 units do not follow the same dynamics in the late 1990s, suggesting that the adjustment to rent control plays at least some role in driving our results. When landlords are newly subjected to rent control regulations, they may respond by 28 Lack of data availability on eviction types at a more granular level than city wide prior to 1997 limits us from running our analysis on particular types of evictions at the ZIP code or building level. In Appendix Figure B9 , we plot the types of eviction notices for units in newly treated buildings and in previously treated buildings from 1997 to 2000. either leaving the rental market altogether or by adjusting their behavior while remaining in the rental market. Owner move-in evictions provide one tool that could help landlords achieve either goal. In particular, owner move-in evictions, if executed properly, temporarily remove a unit from the rent controlled market. After the required occupancy period, landlords then have the ability to return to the rent controlled market, set rents, and select tenants in an optimal way given the regulations. They also can chose to continue to have that unit owner-occupied. 29 This option value of owner move-in evictions may make this an attractive option for landlords. To assess whether our results are fully driven by landlords using owner-move in evictions to fully exit the rental market30 as an alternative to condo conversions, demolitions, or rehabilitations, we leverage our building-level evictions data. We measure what percent of evictions in 1995 were followed by another eviction at the same address between 1998-2000. We find that 9.9% of addresses that had an eviction in 1995 also had another eviction between 1998 and 2000, suggesting that while some of our evictions likely represent a true exit from the rental market, others reflect a change in behavior for landlords who stay in the rental market (or at least wish to retain the option to). Year Newly Rent Controlled: 3-4 Unit Buildings Newly Rent Controlled: 2 Units Previously Rent Controlled: 5-6 Units Notes: The figure plots total eviction notices for buildings with 2 units, 3-4 units, and 5-6 units. Data Sources: San Francisco Rent Board Eviction Notices; 1999 San Francisco Assessor's Secure Housing Roll 7Conclusion San Francisco's expansion of rent control in 1994 led to a dramatic increase in rent control. Landlords of newly rent controlled units faced new incentives to turn over the units in order to raise the rents to market levels. One mechanism through which they could do this was eviction, either lawful or unlawful. We study the effects of the policy change on both eviction notices and wrongful eviction claims and find substantial increases in both in ZIP codes that were heavily affected by the policy change. San Francisco's rent control policy change led to an increase of roughly 20 eviction notices and seven wrongful eviction claims per 1,000 units treated with rent control. Since San Francisco has roughly 1,688 treated units per ZIP code and 25 ZIP codes, we estimate that the rent control policy led to 847 more eviction notices and 322 more wrongful eviction claims than would have happened otherwise. This effect translate into an 83% increase over pre-period eviction notices. The magnitude of this effect is thus comparable to the effect of a large demand shock: Asquith (2019b) finds a roughly 100% increase following price increases resulting from new tech company shuttle service transit stops in a later time period in San Francisco. Additionally, this effect is 2-3 times the estimated effect of a large supply shock in the same setting: Pennington (2021) finds a roughly 30% decline in owner move-in evictions in response to new housing construction. These effects are fairly persistent; it takes about seven years for our effect sizes to fall to the levels that would be predicted by the increase in rent controlled units that are subject to reporting requirements to the San Francisco Rent Board. These dynamics suggest that policy makers should expect that the initial few years after the adoption or expansion of rent control policies will result in changes in the market that will adjust to a new equilibrium in the long run. They highlight that while rent control policies may limit displacement in aggregate, there still may be tenants who are displaced as landlords respond to the policy. Given that not all informal evictions will result in wrongful eviction claims, our effects may be lower bounds on the number of tenants who experience some attempt by their landlord to displace them, either through legal or illegal channels. We further document two sources of heterogeneity in our effect sizes. First, we find that our effects are concentrated in low-income areas. These areas are not necessarily those that saw the largest increases in aggregate rents during the 1990s, suggesting that landlords may be more willing to engage in eviction activity in places where there are fewer resources to fight that behavior. Second, we find that while there is not geographic variation by rent prices, our effects are higher in years when we would expect that the rent control provisions are more binding. We are cautious about interpreting our results too broadly, as the policy change we study only affects a particular kind of rental unit: small buildings that are owner occupied. "Mom-and-pop" landlords may be more willing to get out of the rental business altogether in response to changes in rent control regulation. Alternatively, they may be positioned to take advantage of owner move-in evictions in a way larger landlords are not. Additionally, small landlords may be more likely to skirt the legal restrictions, either because they are not aware of the correct legal proceedings or because they are more willing to take legal risk than a large-scale landlords. Even so, our estimates imply that San Francisco's rent control expansion is responsible for a large portion of the increase in evictions in the 1990s. The 847 additional evictions comprise 59% of the increase in evictions overall in San Francisco from 1994 to 2000. A Data Appendix A.1 Assessor Data Cleaning Details In our analysis, we use data from the San Francisco Assessor's Secure Housing Roll from 1999. 31 The apartment address data from the Assessor's office does not include unit ZIP codes, so we merge the assessor data to the San Francisco's Addresses with Units-Enterprise Addressing System dataset (SFA). The SFA includes complete addresses with ZIP codes, using the parcel number or unit address. While we can match most units with this procedure, some are either missing from the SFA data or do not have unit address information in the assessor data. For these, we either use the Google Map's API to determine ZIP code based on SITUS or use the San Francisco Planning tool to determine the unit's address based on its parcel number. There are two primary challenges in our use of this data. First, because the assessor dataset is derived from hand-filled forms, there are missing fields for a small number of observations. We address this by imputing information on the missing fields. If any building is listed as having zero units (0.9% of buildings are listed with zero units), we replace the number of units using the median number of units based on that building's class code. This means that, since multi-family residences with class codes of "Flats and Duplexes" have a median of two units, any multi-family residences with that class code will be reassigned to have two units if it has zero units listed in the dataset. Next, for any building that is missing information on the year built (0.6% of buildings are missing the year built), we assume that it was built before 1980 since the median year built of all buildings in San Francisco is 1925. We additionally explore using future years of assessor data to fill in this missing information as the data will be updated with future transactions; this procedure results in finding information for 0.4% of observations with missing unit information (or where the value for units is 0) using data from 2000 and another 9% of remaining missing observations using 2001 data for units. For year built, using data from 2000 provides information on 16% of missing or nonsensical values, and data from 2001 provides information on 28% of the remaining missing or nonsensical values. However, given our default imputation methods, this results in updates to relatively few buildings and changes the treatment status of even fewer buildings. The second challenge is that we are unable to observe what the housing stock looked like in 1994, at the time of the policy change. In response to the expansion of rent control, landlords may have demolished newly rent controlled buildings or converted to condos. In the extreme, we can bound how much this changes our results by assuming all newly built buildings replaced rent controlled buildings or that all condos were converted in the window between 1994 and 1999. We additionally attempt to correct for these changes by relying on other datasets from San Francisco. In particular, we measure how many buildings were demolished between 1995 and 1998 and track how many parcels were split to measure new condos. We do so in the following way. First, we identify new parcels added between 1994 and 1999. We identify condos as multiple parcels located at the same geographic location with residential zoning. We keep all parcels where there is more than one and less than five parcels at the same location. We then merge these parcels to the assessor data and keep all buildings built before 1980. This procedure results in 869 units, roughly in line with the 200 units per year allowed to convert to condos. We update our ZIP code measure of treatment to add these units back to our number of newly treated units. 32 en, we adjust for the number of buildings that were demolished. We find 62 buildings that would have been newly rent controlled were demolished in between 1994 and 1999. We further update our ZIP code measure of treatment. All resulting measures of treatment are highly correlated. Table C3 reports the correlations between various treatment measures as well as the average number of treated units at the ZIP code level across each adjustment. In this table, we additionally report "worstcase" scenarios that assume that all condos were converted, that new construction replaced rent controlled units, or that building modifications replaced rent controlled units. These measures will be upper bounds on the number of truly rent controlled units in 1994. It is unsurprising that our measures are highly correlated. Condo conversions were highly limited in the 1990s; only 200 units per year could be converted to condos. Additionally, there was a freeze on converting newly rent controlled units for the first couple of years after the expansion of rent control at the end of 1994. We default to using the measure constructed using only the 1999 assessor data due to inconsistencies across publicly available datasets; however, our results are robust to using the alternative measures of treatment we have discussed. In Appendix Table C1 , we compare the number of rental units in our dataset from 1999 to those in the 2000 census to ensure we have correctly categorized and in some cases, imputed, the building size correctly. The differences between measures from our dataset and the census are quite small and could be due to measurement error in either the census or the assessor data (recall that the assessor data relies on hand-filled forms that were later digitized). In Appendix Table C2 , we report results of a regression of various ZIP code characteristics on the number of treated units in our sample to show that the number of treated units in each neighborhood was not confounded with neighborhood characteristics. We find no significant differences in any observable characteristics of neighborhoods. While this is not necessary to interpret our differences-in-differences results as causal effects, it helps establish credibility for the required (and untestable) identification assumptions: that neighborhoods with different levels of treatment would have trended similarly if the policy had not passed, and that treatment effects are homogeneous across neighborhoods with different levels of treatment intensity. A.2 Alternative Treatment Measure Although we do not know whether owners occupied their units in 1994 when the policy changed, we can approximate this using a 1999 measure of owner occupancy. To create this, we determine whether the owner's mailing address listed in the Assessor's dataset matches the physical address of the unit. We use this measure of owner occupancy to create an alternative measure of exposure, defined as the number of units in a ZIP code that had between 2 and 4 units, were built before 1980, and were owner-occupied in 1999 (the earliest year of Assessor data available). This alternative measure of exposure to the rent control policy is displayed in Appendix Figure B1 . While some areas become more or less exposed based on this alternative measure, the distribution of exposure to rent control looks largely similar to that in Appendix Figure 2 . In Appendix Figure B1 we display a map of San Francisco, where ZIP codes with higher numbers of treated buildings are shown in darker blue. This figure uses the treatment definition that includes 1999 owner occupancy. In comparing to our preferred measure of treatment, which does not account for owner occupancy, it is clear that the two definitions of treatment affect the same neighborhoods to roughly the same extent. Finally, in Appendix Figure B2 , we show the event study results of running our main event study regression using the measure of treatment that includes a 1999 measure of owner occupancy. The pattern of results is the same as those in Figure 6 , which does not use any measure of owner occupancy to measure treatment status. While the magnitudes of effects are much larger, since the average number of owner-occupied treated units is lower than the measure that does not take owner-occupancy into account, the proportional effects are similar to those in our main specification. A.3 Validating and Cleaning Eviction Notice Data To measure evictions, we use data from the San Francisco Rent Board, which publishes two measures. First, the Rent Board publishes counts of eviction notices from 1990 and onward for San Francisco as a whole. These counts include eviction notices that were verified by the Rent Board. This dataset is not available at the individual rental unit level before 1997 due to missing fields in the pre-1997 data. However, the total number of annual evictions is published each year starting in 1990. The Rent Board also publishes a dataset at the ZIP code-year level of wrongful eviction claims from 1990 and onward. This dataset includes all allegations of wrongful evictions made by tenants, regardless of whether their eviction was legal or not, and regardless of whether the eviction went through. We have individual-level data directly from the Rent Board before 1997 and from Brian Asquith from 1997 onwawrd. The Rent Board has provided us with their pre-1997 individuallevel eviction notices data with the caveat that the data have missing fields and have not been audited or checked. First, we check that the pre-1997 data are not missing observations. To do this, we compare the annual number of evictions in the pre-1997 + post-1997 dataset to the published annual number of evictions, finding that the numbers match between the pre-1997 data and the published statistics. If substantial numbers of observations were missing in the data, we would expect to see fewer evictions in the pre-1997 data. We show this comparison in Appendix Figure B3 . Since we do not see this, we proceed assuming all evictions are accounted for in the data. Next, we evaluate missing fields in the pre-1997 dataset. We find that 32% of fields are missing ZIP codes, and 30% of fields are missing the reason for the eviction. Only 0.06% of fields are missing an address. For those observations that are missing ZIP codes, we use Google Maps Places API, searching for the unit's address and filling in the ZIP code that Google Maps associates with the address. We find ZIP codes for all but 124 of the 2,649 rows with missing ZIP codes, so that overall we have ZIP codes for 98% of the data. To ensure the Google Maps API accurately assigns ZIP codes, we compare Google Maps ZIP codes to the ZIP codes included in the data. We find that 88% of ZIP codes are correctly identified by the Google Maps API. We proceed by using the ZIP code given by the eviction notices data unless it is missing, in which case we use the ZIP code given by the Google Maps API, acknowledging the existence of some measurement error in the ZIP code variable. Since there is no way to fill in a missing cause of eviction, we proceed with the understanding that eviction cause data may be unreliable. A.4 Address-Level Data In this section, we discuss how we link address-level eviction notice data from the San Francisco Rent Board. We observe 7,921 eviction notices from 1990-1996 and 11,805 eviction notices from 1997-2000. We merge these addresses to address-level data from the Assessor to obtain information on the treatment status of each unit. We are able to successfully match 81% of evictions before 1997 to addresses in the Assessor data. We are able to successfully match 85% of evictions after 1997 to addresses in the Assessor data. We think it is likely that the remaining unmatched represent minor data errors in the eviction notice data. 33 e then classify evictions as occurring at buildings that were newly treated or previously treated. Newly treated units are units in buildings with 2-4 units built prior to 1980. Previously treated units are in buildings with more than 4 units built prior to 1980. As discussed in Section 4, our measures of treatment are imperfect because we do not observe owner occupancy at the time of the policy change. Many small buildings may have been subject to rent control even before the policy change because they were not owner-occupied. These two categories account for 75% of the evictions we see. We group the remaining units into two further categories. The first is condos built before 1980 where their status as a condo may have changed. We group all remaining units into the final category. The vast majority of these units are single-family dwellings. Table C6 uses a regression framework to explore where our effects are concentrated. Rather than calculating the total number of eviction notices for each ZIP code, we instead construct the number of eviction notices for buildings in different categories. Panel A looks at our main treatment effects. We find large effects on the number of eviction notices for possibly newly rent controlled buildings, but no effects on evictions at other buildings. We further explore whether there are potential spillovers to other buildings by including as an alternate treatment measure the number of previously rent controlled buildings (in Panel B) and by including both measures jointly (in Panel C). Unsurprisingly, in Panel B, we see increases in evictions at previously rent controlled buildings in ZIP codes with many previously rent controlled units. Notes: This figure shows the robustness of event study coefficient estimates to an alternative measure of treatment in which we attempt to condition treatment on the building being owner-occupied. We show our estimated coefficients on the interaction between year dummies and the number of treated units in a ZIP code. We normalize 1994 to be zero. Error bars shown are for the 95% confidence interval. The differencesin-differences estimate for the interaction of the post period with the number of treated units is shown as a gray dashed line with the 95% confidence interval shown as a shaded region on the graph. Standard errors are clustered at the ZIP code level. Subfigure (a) reports effects on eviction notices, while subfigure (b) reports effects on wrongful eviction claims. Effects are scaled to be the effect per 1,000 treated units. The average number of treated units in a ZIP code is 1,688. Data Sources: 1999 San Francisco Assessor's Secure Housing Roll and San Francisco Rent Board Eviction Notices and Wrongful Eviction Claims Notes: This figure shows our event study coefficient estimates on the interaction between year dummies and the number of treated units in a ZIP code on self-reported rents from the 1980, 1990, and 2000 decennial census. We normalize 1990 to be zero. Error bars shown are for the 95% confidence interval. Effects are scaled to be the effect per 1,000 treated units. The average number of treated units in a ZIP code is 1,688. Data Sources: 1999 San Francisco Assessor's Secure Housing Roll and 1980-2000 U.S. Census Notes: This figure shows our event study coefficient estimates on the interaction between year dummies and the number of treated units in a ZIP code (light purple) and this added to the interaction of these estimates with the triple interaction with low income (dark purple). We normalize 1994 to be zero. Error bars shown are for the 95% confidence interval. Standard errors are clustered at the ZIP code level. Effects are scaled to be the effect per 1,000 treated units. The average number of treated units in a ZIP code is 1,688 Notes: This table shows estimates from differences-in-differences regressions on eviction notices. Column 1 shows the results from our preferred specification, a differences-in-differences regression using the number of treated units at the ZIP code level as a continuous treatment measure. B Appendix Figures Column 2 adds heterogeneity by median income. Columns 3 and 4 replace the treatment measure with the number of units eligible for the rent control policy that were also owner occupied in 1999. Columns 5 and 6 replace the treatment variable with an indicator for the number of treated units in the ZIP code exceeding the median number of treated units across ZIP codes. Data Sources: 1990 U.S. Census, 1999 San Francisco Assessor's Secure Housing Roll, San Francisco Rent Board Eviction Notices. Notes: This table shows estimates from differences-in-differences regressions on eviction notices for different types of buildings for 1990-1996. Panel A includes as the treatment variable the number of newly rent controlled units in a ZIP code. Panel B includes as the treatment variable the number of previously rent controlled units in a ZIP code. Panel C includes separately both the number of newly and previously treated rent controlled units in a ZIP code. The outcome variable in column 1 is the number of eviction notices at buildings that are possibly newly rent controlled (built before 1980 with 2-4 units) in a ZIP code. The outcome variable in column 2 is the number of eviction notices at buildings that were previously rent controlled (built before 1980 with more than 5 units). The outcome variable in column 3 is the number of eviction notices at buildings built before 1980 with 1 unit in the parcel that are condominiums. The outcome variable in column 4 is the number of eviction notices at all other buildings (largely single family homes). Data Sources: 1999 San Francisco Assessor's Secure Housing Roll, San Francisco Rent Board Eviction Notices. annex Notes: This figure shows the number of eviction notices by reason for previously rent controlled units and newly rent controlled units from 1997 to 2000. Recall that reliable data on eviction reasons is not available at the unit level prior to 1997. For eviction notices that list multiple reasons for the eviction, we take the first reason listed. Data Source: San Francisco Rent Board Eviction Notices The demolition permit measure adds in all units that were demolished between 1995 and 1999. The parcel split measure adds in all units from new parcels between 1995 and 1999 with 2-4 units. It assumes all new parcels replaced newly rent control units. The next five measures assume various changes from the Assessor data all affected newly rent controlled units. We assume all single family homes replaced rent controlled duplexes, that all new builds replaced rent controlled duplexes, that all condos were converted from rent controlled units in the post period, that all condo modifications represent condo conversions from rent controlled units, and that all newly built condos replaced rent controlled units. C Appendix Tables The final measure we include in this table is our measure that captures owner occupancy. Notes: This table shows estimates from differences-in-differences regressions on wrongful eviction claims. Column (1) shows the results from our preferred specification-a differences-in-differences regression using the number of treated units at the ZIP code level as a continuous treatment measure. Column (2) adds heterogeneity by median income. Columns (3) and ( 4) replace the treatment measure with the number of units eligible for the rent control policy that were also owner-occupied in 1999. Columns ( 5) and ( 6) replace the treatment variable with an indicator for the number of treated units in the ZIP code exceeding the median number of treated units across ZIP codes. Data Sources: 1990 U.S. Census, 1999 San Francisco Assessor's Secure Housing Roll, San Francisco Rent Board Wrongful Eviction Claims Funding We thank Frank Limbrock for help with data applications.We thank David Dranove both for helpful paper and title suggestions.Brad Curtis provided excellent research assistance.All errors are our own.Financial support for this research came from the National Science Foundation Graduate Research Fellowship under Grant NSF DGE-1842165. Loading PDF... StripeM-Inner Paper sources Abstract screening pilot Abstract screening results Extraction pilot Extraction results Research report * * * Modify setup