Short-Term Rentals and the Housing Market: Quasi-Experimental Evidence from Airbnb in Los Angeles

Online short-term rental (STR) platforms such as \textit{Airbnb} have grown spectacularly. We study the effects of STR-platforms on the housing market using a quasi-experimental research design. 18 out of 88 cities in Los Angeles County have severely restricted short-term rentals by adopting Home Sharing Ordinances. We apply a panel regression-discontinuity design around the cities' borders. Ordinances reduced listings by 50% and housing prices by 2%. Additional difference-in-differences estimates show that ordinances reduced rents also by 2%. These estimates imply large effects of Airbnb on property values in areas attractive to tourists (e.g. an increase of 15% within 5km of Hollywood's Walk of Fame).


Introduction
Short-term housing rentals (STRs) have become very important due to the rise of online STRplatforms which provide opportunities for households to informally offer accommodation to visitors. The largest online platform is Airbnb. The surge in popularity of STR-platforms has led to substantial opposition because of a decrease in housing affordability (Samaan 2015, Sheppard & Udell 2016, unfair competition, and illegal hotelization (CBRE 2017). Negative externalities (e.g. noise, reduction in perceived safety) due to the presence of tourists in residential buildings are also frequently mentioned (see e.g. Lieber 2015, Williams 2016, Filippas & Horton 2018.
Local governments around the globe have responded quite differently towards regulating STRs.
Most cities have not significantly regulated these platforms, but a limited number of cities have recently put severe restrictions in place. Berlin, for instance, requires STR-hosts to occupy the property for at least 50% of the time (O'Sullivan 2016). San Francisco imposes a 14% hotel tax (i.e. a Transient Occupancy Tax ) and a cap of maximum 90 rental days per year (Fishman 2015). Amsterdam even imposes a maximum cap of 30 rental days per year as of 2019.
In this paper we aim to measure the impact of Airbnb on housing markets and the related effects of policies that restrict the market for STRs. There are arguably three main mechanisms of how short-term renting impacts property markets (see Turner et al. 2014): 1. Efficient use effect. Short-term rentals generate income from idle space, increasing the value due to additional income opportunities. Moreover, residential properties can now be used by their most profitable use (i.e. by short-term renters). This should be an efficiency gain that spurs an increase in housing demand, which increases house prices (see e.g. Turner et al. 2014).
2. Rental housing supply effect. Short-term rentals may in turn lead to a reallocation of existing housing stock away from the long-term rental market towards privately owned housing, which increases rents (see e.g. Quigley et al. 2005).
3. Externality effect. Short-term rentals may create negative nuisance externalities, lowering nearby property values. If neighbors fear turnover or unfamiliar people in their neighborhood, this may reduce demand for housing (see e.g. Filippas & Horton 2018).
To identify the effects of Airbnb on the housing market, we exploit exogenous variation provided by the implementation of so-called Home-Sharing Ordinances (HSOs) in Los Angeles County.
18 out of 88 cities implement regulations that essentially ban informal vacation rentals; hosts renting out entire properties are now subject to the same formal regulations as regular hotels and bed and breakfasts. Short-term home sharing is not always prohibited, albeit restricted in those cities.
There are several reasons why we focus on Los Angeles County. First, it is an area that is attractive to tourists and has thousands of listings on Airbnb. It is in the global top 10 of cities in terms of Airbnb listings and is the second most popular Airbnb city in the U.S. after New York. Second, there is substantial spatio-temporal variation in the implementation of HSOs within this county. For example, HSOs have been implemented in cities that receive many tourists (e.g. Santa Monica), as well as in cities that are more at the edge of the Los Angeles Conurbation (e.g. Pasadena). We think this might add to external validity of the results shown in the paper. Third, by focusing on 18 cities, rather than on the introduction of an HSO in one single city, we substantially reduce the likelihood that our results are contaminated by an unobserved event (e.g., a change in a city-specific policy) that occurs around the same time as the introduction of the HSO. Fourth, in Los Angeles County, in contrast to for example New York, renters are (usually) not allowed to list a property on Airbnb (Lipton 2014). 1 This facilitates the interpretation of the distributional consequences of our results: renters generally lose from Airbnb-induced higher rents (and hardly benefit from the opportunity of subletting to short-term renters).
The variation in restrictions between cities enables us to use a spatial regression discontinuity design (RDD), which we combine with a difference-in-differences (DiD) set-up: we essentially focus on changes in the number of Airbnb listings, as well as in house prices, close to the borders of cities that have implemented HSOs. More specifically, we use micro-data on Airbnb listings and house prices between 2014 and 2018. Our main results are then based on observations within approximately 2 km of borders of HSO areas. We distinguish between effects on different types of listings (home sharing, entire properties) as well as on the prices in different areas (e.g., with high and low tourist demand).
By applying the Panel RDD we identify the first effect -the efficient use effect -which is arguably the key mechanism to explain the effects on house prices. Conditional on local area fixed effects, properties close to the border of an area where an HSO is implemented are otherwise identical, except that in one area short-term renting is restricted. Theory then indicates that there is a discrete decrease in house prices at HSO borders, because houses within a treated area offer less value to homeowners.
One potential issue with the Panel RDD approach is that by comparing house prices (as well as listings) in two neighboring cities -one which implemented an HSO and the other which did not implement any HSO -substitutability between houses on the two sides of the city border may inflate the effect of the HSO implementation. We provide a range of statistical tests which all show that this 'manipulation' is completely absent. 2 The economic intuition for the absence of manipulation is that tourist demand tends not to be very local (e.g., tourists are indifferent between locations which are a couple of minutes drive from each other), so tourist accommodations compete with each other over longer distances. Hence, given an elastic demand function for tourist accommodation, there is no incentive to move listings just across the border. 3 Short-term rental platforms also reduce housing supply available for local (long-term) rental markets, which increases rents (Hilber & Vermeulen 2016) -the rental housing supply effect.
When the expected economic returns on rental and privately owned properties are the same, then the housing supply effect estimated in the rental market should be the same as the efficient use effect (estimated using house prices). 4 We cannot measure the rental housing supply effect by applying a Panel RDD for rents, because properties that are next to each other, but on 2 The use of a Panel RDD, which relies on observations close to cities' borders, has an important advantage to a standard DiD, as it does not require the parallel trend assumption to hold, but requires that changes in variables correlated to the treatment are continuous at the border. We provide evidence that the latter holds. One cannot test whether the assumption of a parallel trend holds, but it is possible to test whether there are parallel pre-trends. We show in Figure 7 in Section 6.2 that the pre-trends are parallel, so one may interpret our results also from a DID perspective.
3 In line with this line of reasoning, we will show that Airbnb accommodation prices are not affected by HSOs. The latter suggests that the market for short-term rentals is highly competitive and that tourist demand for local accommodation is highly elastic. Consistent with that, we find suggestive evidence that the number of formally registered traveler accommodations increase due to HSOs. We show that there is no discrete change in the population density or housing units at the border 4 However, note that the effects of short-term rentals on house prices may be different from those on rents in the short run, because house prices may include anticipation effects towards future changes in policies. However, we do not find evidence for this. different sides of the HSO border experience identical changes in housing supply and offer the same value to renters (see Glaeser & Ward 2009). This implies that there should be no discrete jump at HSO borders for rents. 5 To capture the rental housing supply effect we employ an alternative strategy: we use ancillary data on aggregate rents for zip codes and a DiD estimation strategy, while we focus on properties further away from the HSO borders. The DiD approach relies on more restrictive identifying assumptions than the Panel RDD approach. We assess the validity of the DiD approach in this context is by applying the same approach to house prices, finding very similar effects.
We also test for the third effect -the externality effect -by investigating the price change of properties outside HSOs but close to areas where HSOs have been implemented. Many papers find that housing market spillovers are very local (see e.g. Linden & Rockoff 2008, Autor et al. 2014, Fisher et al. 2015, Pope & Pope 2015, Ahlfeldt & Holman 2018, Diamond & McQuade 2019, Koster & Van Ommeren 2019. We therefore also test for differences between effects of Airbnb of prices of condominiums and single-family homes. One expects that local externalities are particularly important for condominiums, so if the effect of Airbnb on condominium prices would be lower this means that an external effect could be present. We do not find evidence that the externality effect is important for LA County.
We have two main results. Our first result is that HSOs are very effective in reducing Airbnb listings. The ordinances strongly reduced the number of Airbnb listings of entire properties and home sharing by about 50% in the long run. We further show that home sharing listings have not been reduced when home sharing is still allowed, which is the case in 4 out of the 18 cities with HSOs. Our second result is that the HSO reduced house prices by about 2% on average. This effect is robust to a wide range of placebo-tests and specification choices.
To explore the price effect further, we estimate a 'structural equation', i.e. we capture the effect of demand for short-term rentals on housing prices using an IV approach. We measure short-term rental demand using the Airbnb listings rate -the share of HSO properties to the number of housing units. Using HSOs as supply-shifting instruments for the listings rate around the 5 A Panel RDD analysis of rents confirms the absence of a discontinuity in rents. Another consequence is that at the HSO side of the border, the economic return of a rental property is less than of a privately owned property used for short-term renting. This makes it plausible that the share of rental housing drops at the HSO side of the border. Our observation period is too short and the quality of housing tenure data unfortunately not good enough to quantify such a change.
border, we show that short-term rental demand for accommodation increases prices of residential properties -a standard deviation increase in the Airbnb listings rate increases prices by 5.5%.
Using the DiD estimation strategy, we further show that rents decrease by about the same amount as house prices, likely because of the reduced supply of rental housing. 6 Furthermore, we demonstrate that there are no effects on rents around the HSO border, confirming that rental properties close to HSO borders are close substitutes for renters.
We then show that Airbnb imply modest property value increases for LA County as a whole: the total average property value increase due to Airbnb since 2008 is 3.6%. However, this masks the fact that a large part of LA County is not very urbanized and does not attract tourists. By contrast, the effects of Airbnb on the housing market can be large in central urban areas -within 2.5km of Hollywood's Walk of Frame, property values have increased by almost 15% due to Airbnb. Within 2.5km of beaches, prices have increased by 5.8%. The decision to implement an HSO is a political one, with a clear group of winners and losers, and strong distributional effects: owners lose from HSO-induced house price reductions, whereas (long-term) renters benefit from lower rents.
Related literature. In recent years, the sharing economy has received increasing attention.
Economists have examined home sharing from various angles such as racial discrimination in the online marketplace (Edelman et al. 2017, Kakar et al. 2016, negative externalities of tourism (Van der Borg et al. 2017, Gutiérrez et al. 2017) and its effects on the hotel industry (Zervas et al. 2017). We are not the first empirical study on the effect of short-term rentals on the housing market, but current studies, although suggestive, do to the best of our knowledge not surmount the various endogeneity issues. Sheppard & Udell (2016) conclude that housing values increased by about 31% due to Airbnb. Horn & Merante (2017) show that a high Airbnb density increases asking rents by 1.3-3.1%. Barron et al. (2018) show that Airbnb increases house prices and rents in U.S. cities. Garcia-López et al. (2018) also report a positive effect on rents in Barcelona. A 6 Our finding that the effect on rents and prices are very comparable differs from the prediction of a theoretical model by Barron et al. (2018), which predicts that the effect on prices exceeded those on rents, because homeowners have an additional option in the short-rental market. This result is unlikely to hold in our context, because cities without HSOs may introduce measures to reduce short-term letting in the future. However, there may be a range of other reasons why this prediction does not hold, including sorting of heterogeneous agents due to spatial variation in the HSO, heterogeneous housing, differences in capitalization between rental and owned markets (Grainger 2012). few reports -which essentially rely on correlations -have studied the impact of Airbnb as well. 7 These studies have in common that they do not examine the effect of short-term rental policies and do not convincingly address the endogeneity issue that neighborhoods tend to become more attractive to residents and tourists at the same time. 8 Our study is the first one that addresses this issue by exploiting quasi-experimental variation provided by changes in regulation to estimate the effect of Airbnb on the housing market. Furthermore, and this is even more important, we are the only study which studies the effect of regulation of Airbnb itself, which is of key policy interest.
Our paper also relates to a literature studying the effects of tourism and amenities on housing markets. Carlino & Saiz (2008), for example, show that the number of tourists visiting a city is a good predictor of the growth of U.S. metropolitan areas in the 1990s. Ahlfeldt et al. (2017) and Gaigné et al. (2018) Koster & Rouwendal 2017). In these studies, it is impossible to disentangle the effects of tourism and amenities. An exception is a recent paper by Faber & Gaubert (2019), which shows that tourism generates substantial local and national economic gains driven by spillovers on manufacturing and national integration respectively. Our paper therefore contributes to this literature by using a quasi-experimental research set-up, enabling us to isolate the effects of tourism demand, proxied by Airbnb listings.
Conceptually, our paper is close to a literature measuring the effect of land use regulation and zoning, as the HSO can be seen as an example of a zoning regulation. Most studies in this field show that housing supply constraints are associated with increasing housing costs, a strong 7 New York Communities for Change looked at correlations between Airbnb and neighborhood mean rent increases (NYCC 2015). Samaan (2015) looks at the rental market in Los Angeles and reports a 4 percentage points faster growth of rents in popular Airbnb neighborhoods. Lee (2016) argues that Airbnb reduces the affordable housing supply in Los Angeles, because landlords remove units from the housing market by listing on Airbnb. Wachsmuth & Weisler (2017) argue that Airbnb has introduced new revenue flows to the housing market which are systematic but geographically uneven.
8 Probably Barron et al. (2018) comes the closest to causal inference by using a difference-in-differences strategy and using an instrument based on both the popularity of Airbnb and how touristy an area is. We do not think the instrument solves the endogeneity issues. High-amenity areas, in particular US inner cities, have both attracted tourists and residents in recent decades (see Couture & Handbury 2019).This has led to price appreciation and growth in listings, which is not due to Airbnb. Reassuringly, our estimates are of a similar order of magnitude as Barron et al. (2018), despite the differences in the identification strategy and the focus of Barron et al. (2018) on many cities in the US. reduction in new construction, and rapid house price growth (Glaeser et al. 2005, Green et al. 2005, Ihlanfeldt 2007, Hilber & Vermeulen 2016. However, they do not identify the underlying mechanisms that lead to price increases. Glaeser & Ward (2009) find that local constraints do not increase the price between localities, because areas that are geographically close are reasonably close substitutes. Using a spatial regression discontinuity design, Koster et al. (2012), Turner et al. (2014) and Severen & Plantinga (2018) also study the local effects of regulation and find that the effects of regulation for homeowners may be up to 10% of the housing value.
One major difference with these studies (with the exception of Severen & Plantinga 2018) is that our research design does not rely on cross-sectional variation in land use regulation, but rather identifies the effect based on changes in regulation over time.
Finally, our paper is related to a large literature on housing regulation, including rent-controlled or public housing (Olsen & Barton 1983, Fallis & Smith 1984, Moon & Stotsky 1993, Glaeser & Luttmer 2003, Anderson & Svensson 2014, Autor et al. 2014, and affordable housing (Quigley & Raphael 2004, Diamond & McQuade 2019, Koster & Van Ommeren 2019. In this literature, it is common to study a policy where a fixed share of houses is regulated in order to help poor households. Regulation creates then an efficiency effect as well as a housing supply effect.
Studies typically focus either on the efficiency effect (see Glaeser & Luttmer 2003, Anderson & Svensson 2014 or the housing supply effect (see Fallis & Smith 1984). In contrast to the existing literature, we study a regulation type which induces efficiency and housing supply effects for the full housing market, rather than a sub-segment of the market. Hence, the aggregate welfare and distributional effects are expected to be more pronounced. Recent studies also explicitly take into account spillovers of providing subsidized housing and find that these spillovers are very local (Autor et al. 2014, Diamond & McQuade 2019, Koster & Van Ommeren 2019. This paper proceeds as follows. In Section 2 we discuss the research context. Section 3 introduces the data and provides descriptives. In Section 4 we elaborate on the identification strategy, followed by graphical evidence in Section 5. We report and discuss the main results in Section 6, which is followed by back-of-the-envelope welfare calculations and distributional implications of HSOs and Airbnb in Section 7.2. Section 8 concludes.

Airbnb in Los Angeles County
In 2007, Brian Chesky and Joe Gebbia came up with the idea of putting an air mattress in their living room and turning it into a bed and breakfast, marketed through an online platform (Lagorio-Chafkin 2010). The website -later called Airbnb and officially launched in 2008 -is a platform that connects hosts that own accommodation (rooms, apartments, houses) with guests seeking temporal accommodation. Prospective hosts list their spare rooms or entire apartments for a self-established price and offer the lodging to potential guests. 9 Airbnb charges a fee to both the host and guest.
Airbnb has grown rapidly since its launch in Los Angeles County (as in other major cities across the globe), with now more than 40 thousand listings, about 2.5% of all residential housing. 60% of those listings are entire properties (Inside Airbnb 2017). 10 Figure 1 clearly shows that Airbnb listings are heavily concentrated in popular areas like Venice, Santa Monica, Hollywood and Downtown LA. Nevertheless, we also record many listings in areas that are further away from the center (e.g. Pasadena, Hermosa Beach).
Many cities around the world have imposed some form of regulation, e.g. by requiring hosts to register their STR activities with the local authorities. However, an increasing number of cities also explicitly restrict short-term housing rentals, which are defined as lettings of up to 30 consecutive days. Cities that impose so-called Home Sharing Ordinances (HSOs) typically distinguish between two types of informal STRs: 'home sharing', whereby at least one of primary residents lives on-site throughout the visitor's stay, and 'vacation rentals', which are for exclusive use of the visitor.
In Figure 1 we show the names of 18 cities that have imposed HSOs during our study period 2014-2018. The other 60 cities -including the largest one, the City of Los Angeles -did not impose regulations in this period. 11 These 18 cities, which contain close to 5 percent of the 9 With more than 4 million listings -more properties than the top 3 hotel brands, Marriott, Hilton, and IHG, combined (Airbnb 2017) -Airbnb emerged as one of the main figureheads of the sharing economy, in which technology companies disrupt well-established business models by facilitating direct, peer-to-peer exchanges of goods and services (Lee 2016).
10 According to Airbnb, it generated $1.1 billion in economic activity in the City of Los Angeles. Its typical host earned $7, 200 per year from hosting and it helped 13% of its hosts to save their home from foreclosure and another 10% from losing their home to eviction (Airbnb 2016, Inside Airbnb 2017. 11 In 45 cities, short-term renting is technically illegal, because it is not mentioned in the residential housing  Our empirical approach relies on the fundamental assumption that around the implementation of the HSOs other policies did not change in the 18 cities compared to their immediate surroundings. We are not aware of such policy changes (but have actively searched for this). We also offer statistical support for this assumption. In Section 6.5 we perform a range of placebo tests using information on price changes around the borders of other sets of cities and using the same borders but in other time periods. All these tests indicate that there are no changes in listings and prices at the placebo borders investigated. This makes it implausible that other policies (or e.g. differences in school quality) changed exactly around this period. 13

Data
We employ Airbnb listings data obtained from web scrapes for 15 different months from the websites www.insideairbnb.com between October 2014 and September 2018 for Los Angeles County. We double check these data with data on listings from www.tomslee.net. 14 LA County is the most populous county in the United States (more than 10 million inhabitants as of 2018).
We know the location (up to 200m) and whether a property is listed in one of the 15 months of observation. 15 For the analysis where we analyze the effects of HSOs on listings, we construct a panel dataset of all accommodations that have been listed between 2014 and 2018. We create a variable that equals one when the accommodation is actually listed in a certain month.
We also use micro-data on housing transactions, obtained from the Los Angeles County Assessor's Office. The data provides information on sales prices and a range of property characteristics (e.g., condominium, single-family home, construction year) for all transacted residential properties.
We focus on transactions from January 2014 until early 2018, as these match closely to the period our Airbnb data refers to. Ancillary data on properties' locations, exact building locations and neighborhood characteristics is obtained from the Los Angeles County's GIS Data Portal.
We disregard extreme outlier observations and transactions with missing information on either prices or property size or type (condominium or single-family home), as well as transactions referring to multiple parcels or units. 16 For the analysis of the effect of Airbnb demand on house prices, there are two technical issues when matching listings data to house prices. First, the data on listings is based on 15 snapshots during our study period. Second, we do not have information on listings from January to 14 Airbnb is not the only STR-platform available to prospective hosts. This is unlikely problematic, because hosts who consider to use other platforms are likely also to use Airbnb, which is the dominant platform, as the cost of advertising on Airbnb is negligible. According to www.beyondpricing.com, HomeAway -Airbnb's most important competitor -had 3,578 listings in Los Angeles in 2016, while Airbnb had 8,367 listings (which is less than observed in our data). Data on individual HomeAway listings is not available to us. Later on, we will instrument the observed listings rate by the HSO (which affected all listings) to address any measurement error. Only if due to the HSO, demand from one platform shifted to another, which seems unlikely, some of our results would be affected.
15 Through Inside Airbnb, we also have information for a subset of listings on the number of reviews, which we will show for descriptive purposes.
16 More specifically, we remove transactions referring to properties cheaper than $50000 or more expensive than $5 million. We also omit transactions with a m 2 price that is below $200 or above $20000. We further disregard repeat sales with yearly price differences larger than 50%. Additionally, we exclude properties smaller than 50m 2 or larger than 1000m 2 and parcels smaller than 50m 2 or larger than 10ha.
October 2014. We deal with both issues by constructing an imputed measure which imputes the listing probability based on the nearest two dates for which we have information. 17 We also use an alternative approximated measure, available for the whole period for which we observe house prices, following Zervas et al. (2017) and Barron et al. (2018). This alternative measure is derived from information on listings on the date of their first review (if this information is missing, the date at which the host became active on Airbnb) and last review, while assuming that the property is continuously listed between these two reviews. To capture Airbnb demand, we use the Airbnb listings rate -defined by the number of listings divided by the number of housing units -within 200m of each property. 18 The results using this measure are essentially the same. As an alternative to the listings rate, we have also used the density of listings (within 200m) to calculate Airbnb demand, which provides largely similar results.
We further gather monthly data on listed median rents and house prices at the zip code level from Zillow, which is a large real estate database company. 19 Zillow has micro-data on over 110 million homes across the United States, not just those homes currently for sale but also for rent.
For each zip code in each month, Zillow posts the median listed rent and median listed sales price. For LA County, we have information on 114 (out of 311) zip codes.
In the econometric analysis, we will also distinguish between geographical areas within the County of Los Angeles. An area is defined by us as a City or a neighborhood within the City of Los Angeles (which is by far the largest city) or a so-called 'unincorporated' area. In total, we have 252 areas. Table 1 reports the main descriptive statistics for the Airbnb listings. We observe that, on average, rental prices per night in areas where HSOs are implemented are somewhat higher than in other areas. Hence, the HSOs are predominantly implemented in areas where there is more 17 For example, when we observe that a property is listed in March, but not in May, the imputed listing probability is 0.5 in April 2015. Before October 2014 we use data on listings from October 2014.

Descriptives
18 Information on the location of housing units is obtained from the American Community Survey, which provides information at the census block group (of, on average, 540 housing units). We draw circles around each property and calculate the area-weighted number of housing units within 200m. To avoid outliers for a low number of housing units, we replace the lowest 2.5% of the number of housing units by the value of the 2.5 th percentile. In Appendix A.4.7 we show that our results are rather insensitive to outliers. 19 The most detailed data publicly available is at the so-called Zillow -neighborhood. Because these data are only available for a few neighborhoods in LA County, we use the more aggregated zip code level. demand for tourist accommodation. In other observable characteristics, such as accommodation size, number of reviews and the share of entire properties, listings in HSO areas seem to be similar to listings in other areas. The most notable difference is that the distance to the beach is lower in areas where HSOs are implemented, as several beach towns, such as Santa Monica, Manhattan Beach and Redondo Beach, have implemented HSOs. We note that the condominium share of Airbnb listings is about 0.5, which exceeds the condominium share of housing transactions (see Table 2). Hence, the forbidding of  the number of listings was almost 4 times higher than in October 2014. However, the growth in listings has been much lower in areas where HSOs were implemented during our study period.
The trend in listings particularly diverges in 2017 once more cities implemented HSOs.

Figure 2 -Airbnb in LA County
We report descriptive statistics for the housing transactions data in Table 2. The house price and the price per m 2 are substantially higher in HSO areas, respectively 52% and 68%. The listings rate is about 0.7% in HSO areas and 0.5% outside HSO areas. The spatial (see Figure 1) and temporal (see Figure 2) variation in the listings rate is large: for the majority of houses (65%), there are no listings within 200m.
Properties in HSO areas are about 10% larger, but at the same time the share of condominiums is about twice as high in these areas. This may reflect that HSOs tend to be implemented in upscale areas where prices are higher and which are inhabited by rich households that have high demands for space. These figures emphasize the need to focus on observations that are close to HSO borders in order to have a comparable control group. As one may expect, HSO areas tend to be more touristy: the distance to the beach is on average about half in these areas, whereas the density of tourist pictures is about twice as high, compared to non-HSO areas.
Finally, we turn to the data on rents and house prices from Zillow for zip code areas. We report descriptives in Table 3. The average rent per m 2 is about $26 in both areas. Although rents are very similar for both areas, we find a 17% lower average house price per m 2 outside HSO areas.
The listings rate is lower in HSO areas (0.8%), then outside these areas (1.4%). Also at the zip code level, there is substantial variation in the listings rate. The zip code area with the highest rate, 14.3%, is located in Venice (City of LA), followed by a zip code in Hollywood (City of LA) with 8.9%.
A priori, it is difficult to judge the quality of the information offered by Zillow. Quite reassuringly, the correlation between median house prices in Zillow and median house prices using the Assessor Office's data (which we use for micro analyses) is high (ρ = 0.941). However, when we demean prices by zip code and month fixed effects, the correlation is only moderate (ρ = 0.322). This suggests that results might be dataset specific. However, we will show that our results are not driven by the choice of the dataset.

Econometric framework
The main econometric issue when aiming to estimate a causal effect of Airbnb on the housing market is that Airbnb listings are not randomly allocated across space but are concentrated in neighborhoods that are attractive to both residents and visitors with a demand for short-term letting. One way to address this issue is to compare adjacent cities that differ in regulation of Airbnb and then use a Spatial RDD around the cities' borders. This ignores however that cities differ in other ways than in their regulation of Airbnb. We address the latter by exploiting variation over time in the HSO around the borders of HSO areas. The HSOs induced exogenous changes in the propensity to list a property on Airbnb, which may have resulted in changes in house prices. Consequently, as we will use panel data (for listings as well as house prices), we will employ a Spatial Panel Regression-Discontinuity Design. In this design, we will assume that cross-border spillovers are absent (i.e. we assume that the Stable Unit Treatment Value Assumption (SUTVA) holds), for which we give ample evidence (using graphical as well as econometric evidence). We will also estimate difference-in-differences models (for rents, but also for prices), which do not rely on this assumption.

HSOs and Airbnb listings
The first step is to estimate the effect of the HSO on a property's probability of being listed on Airbnb. We distinguish between the probability of being listed as an entire home and the probability of being listed as home sharing. We will estimate linear probability models, where we estimate the effects of the HSO on both probabilities separately. 20 We use a Spatial RDD, where the running variable is the distance to the nearest border of an area where an HSO is implemented or will be implemented in the future. The effect of the HSO is captured by a discrete jump in the probability of being listed after its introduction. Let ikt be a dummy variable indicating whether a property i near a border of an HSO area k is listed in month t and h ikt be a dummy indicating whether the HSO has been implemented. The variable d ik denotes the distance to the border, where d ik > 0.
One may argue that differences in unobservables of properties between HSO areas and neighboring areas may be correlated to the implementation of an HSO. For example, differences in attractiveness of certain locations that are discrete at, or even further away from, the border (e.g., school quality) may be present, which are correlated to h ikt and influence ikt at the same time. We therefore include property fixed effects λ i , which control for difficult-to-observe but time-invariant differences between locations, and µ kt , which capture HSO-border area by months fixed effects. More specifically, µ kt are dummy variables that are equal to one on both sides of the shared border between two adjacent cities (or a neighborhood in the City of LA) in a specific month (hence, we include a fixed effect for each month/web scrape in each HSO-border area). This implies: where α is the parameter of interest and ψ 1 , ψ 2 , ψ 3 , ψ 4 , λ i and µ kt are other parameters to be estimated. In this specification, ψ 1 and ψ 3 capture the possibility that distance trends in listings may be different on both sides of the border before and after the treatment. ψ 2 and ψ 4 aim to capture differences in those trends over time by including a linear interaction with time. Note that because we include property fixed effects, λ i , we effectively only use data on properties that have been listed at least once. It also implies that h ikt d ik and (1 − h ikt )d ik are perfectly collinear with λ i , which we address by imposing that ψ 3 = ψ 4 = 0. Hence, in essence, we have a regression-discontinuity design, which aims to identify a discontinuity in changes over time in 20 Our motivation not to estimate multinomial discrete choice models, but to estimate separate models is that in our data properties never switch between being listed as an entire home to home sharing. This also implies that the HSO did not induce hosts of entire properties to shift to home sharing. Results are very similar when we estimate Logit models, or Conditional Logit Models of location choice using Poisson regressions.
listings at the border, where we allow for different time differences in distance trends at both sides of the border.
In this setup, we only include observations that are within a small distance b of a border of an HSO. We use a uniform kernel function with a bandwidth b, and do not include higher-order polynomials of the border trends (see Imbens & Lemieux 2008). This approach is supported by Gelman & Imbens (2019) who show that such an approach is preferred over specifications including high-order polynomials of the running variable.
In RDDs, estimated parameters are often sensitive to the choice of the bandwidth b. We therefore show results for different bandwidths. Our preferred specification is based on an approach proposed by Imbens & Kalyanaraman (2012) to determine the optimal bandwidth, b * , which is calculated conditional on control variables (property fixed effects and HSO-area×month fixed effects). We discuss the procedure to determine b * in more detail in Appendix A.2. In our context, the optimal bandwidth is about 1.8 km, so quite small. Importantly, we show that our results are rather insensitive to the choice of bandwidth, also when choosing much smaller bandwidths. 21

Reduced-form effects
We employ a similar approach to measure the effect of the HSO on house prices. The main difference is that we include census block fixed effects rather than property fixed effects, as we have fewer repeated observations. Let p ijt be the house price of property i in census block j near a border of an HSO area k in month t with time-invariant housing characteristics x ijk . We estimate: where β is the parameter of interest. Similar as above, ω 1 , ω 2 , ω 3 and ω 4 capture parameters related to the spatial trends before and after the treatment (first difference) and over time (second difference). 22 η j and θ kt refer to census block and HSO border×month fixed effects respectively.
This equation implies that we compare price changes along the borders of HSO areas to see if prices have changed in the treated areas due to the HSO. Again, we will show results given different bandwidths, but our preferred specification is based on the optimal bandwidth.
The above approach ignores that there may be variation over time in the effect of HSOs. This is important, as anticipation effects of new laws may underestimate the effects of HSOs.
Furthermore, we wish to take into account that house prices usually adjust gradually over time (implying that long-term effects may be stronger). 23 In the empirical analysis we estimate specifications where we allow the HSO-effect to be time-specific, so we are also able to test for anticipation and adjustment effects of HSOs.

Effects of the listings rate on house prices
The results from equation (2) are informative on the average treatment effect of the HSO on house prices, where the average applies to estimates along the borders of HSO areas. However, it is plausible that the effect strongly varies over space depending on local tourist demand for accommodation. The latter strongly covaries with the demand for Airbnb, captured by the listings rate a ijkt , potentially reducing the external validity of the estimated average treatment effect. In particular, one expects that areas that are popular with tourists are more strongly affected than areas that are not.
We will therefore also estimate a 'structural equation' where we estimate the effect of the listings rate in the direct vicinity, a ijkt , on prices using an IV approach. 24 Because a ijkt is endogenous (as listings are imputed and so are measured with error, and residents and visitors have preferences for similar locations), we use arguably-exogenous variation in the listings rate caused by HSOs.
The second stage is then given by: 22 ω3 and ω4 are now identified because we include census block, rather than property, fixed effects. 23 Moreover, we will see that the HSO-induced reduction in listings is limited within the first year after the introduction, making it more plausible that the price reaction will be slower. 24 We refer to section 3.1 for how we constructed the listings rate variable.
whereâ ijkt is obtained from: where the ∼ refer to first-stage coefficients andδ is the effect of the HSOs on the listings rate.
We expectδ to be negative.

HSOs, Airbnb and rents
Short-term rentals may lead to a reallocation of existing housing stock away from the long-term rental market towards privately housing used for short-term renting, reducing the supply of available rental stock for locals, which should increase rents.
In contrast to house prices, given the assumption of a spatial equilibrium, long-term rents should not be different at HSO borders given two assumptions: (i) rental properties at different sides but very close to these borders are close substitutes and offer the same value to renters; and (ii) renters are not allowed to list their property on Airbnb.
We will test the first assumption by estimating regressions where we only include properties close to HSO borders (i.e. 1km), which should lead to a statistically insignificant rent effect.
The second assumption is also likely to hold, as in Los Angeles almost all rental leases include a provision explicitly forbidding to sublet the property (Lipton 2014).
Given that theory does not suggest a discontinuity in rents at the border and that we have information on rents at the zip code level (which would make the use of a discontinuity design in any case less convincing), we pursue a standard difference-in-differences approach where we regress rents, r jt , on h jt , where j refers to zip codes areas. We then have: where φ is the parameter of interest, η j are zip code fixed effects and θ t are month fixed effects.
This is a standard difference-in-differences specification, with the notion that we have multiple treatments at different times in our study period. 25 In line with the previous set-up we will also estimate a 'structural equation' by regressing rents on the listings rate, using an IV approach.
The key assumption underlying a DiD strategy is that there is a common trend between the treatment and control group. This assumption cannot be tested, but, as is standard, we examine this concern by undertaking an event study in the empirical analysis and show that there is no statistically significant effect before the HSO was implemented, which suggests (but does not prove) that the common trend assumption holds. Importantly, this strategy is less convincing than the Panel RDD, which does not require such assumption, but we have an alternative way to test it. We will demonstrate that when applying a DiD strategy to house prices, then the house price effects are comparable to the ones obtained using the more credible Panel RDD approach. The latter makes it plausible that the rent results are reliable.

Treatment effects
Before we turn to the regressions results, we illustrate our research design graphically. In Figure   3, we first focus on the impact of the HSO on Airbnb listings. We include property and border segment×month fixed effects, and include a 4 th -order polynomial of distance to the border outside HSO areas and a 2 nd -order polynomial of distance to the border multiplied by the treatment inside treated areas (as we have fewer data points that are closer to the border inside HSO areas). 26 The inclusion of property and border segment×month fixed effects implies that we identify the effects over time. In Figure 3a, we plot the conditional probability of listing on Airbnb. We observe a sizable drop in type of listings in areas where HSOs have been implemented.
The difference is about 8 percentage points. 27 Given a listing probability of about 0.30 (for residences that have been listed at least once), this implies a reduction in listings of 27%. Hence, in line with anecdotal evidence, this suggests that the HSO was very effective in reducing STRs. Notes: Spatial differences in variables are conditional on property and border segment×month fixed effects. Hence, we identify the effects over time. Negative distances indicate areas outside HSO areas and areas inside HSO areas but before treatment. The dots are conditional averages at every 500m interval. The dotted lines denote 95% confidence intervals based on standard errors clustered at the census block level. We include a 4 rd -order polynomial in untreated areas and a 2 nd -order polynomial in treated areas. Figure 3a is also important, as it provides evidence of the complete absence of cross-border crossings of listings due to the HSO. We do not find any evidence that a drop in listings at the HSO side of the border accompanied with an increase in listings just at the other side (if anything, the figure implies the opposite). We come back to this issue in section 6.1.
Let us now investigate whether there are differences in changes of characteristics of houses listed on Airbnb between treated areas and areas in the close vicinity. Figure 3b shows that there is essentially no difference in how Airbnb prices per night and availability changed over time between HSO areas and neighboring areas. Hence, it is not the case that properties just outside HSO areas become more expensive. The latter suggests that the demand for Airbnb listings is locally elastic and the market is extremely competitive, which is consonant with the absence of cross-border listing effects). Some HSOs still allow for home sharing. In Figure 3c we investigate if there is an decrease in the share of listings entire homes relative to home sharing. We do not find a statistically significant jump in the change in the share of entire homes at the border.

Figure 4 -House prices: variation near the HSO borders
Notes: Price differences are conditional on census block and border segment×month fixed effects. Hence, we identify the effects over time. Negative distances indicate areas outside HSO areas and areas inside HSO areas but before treatment. The dots are conditional averages at every 500m interval. The dotted lines denote 95% confidence intervals based on standard errors clustered at the census block level. We include a 4 rd -order polynomial of price differences in untreated areas and a 2 nd -order polynomial in treated areas.
In Figure 3d we show that the type of accommodations on offer does not seem to change due to HSOs, as the change in accommodation size is not statistically significantly different at the border.
We repeat the exercise, but now focus on house prices. The results are reported in Figure 4.
Prices decrease by about 4% at the HSO border. It appears that this effect is highly statistically significant. In Appendix A.3, we further investigate whether discontinuities in changes in housing characteristics exist at the border. We do not find evidence for this. One may be concerned that this result is mainly explained by the very local decrease in house prices within 500m of the border. In the next section we show that, once we include more detailed census block or property fixed effects, the estimated effect becomes more precise and is very robust to bandwidth choice.
Again we do not find any evidence of cross-border effects, as house prices close to but just outside HSO areas are not higher.

Sorting and public goods
In spatial RDDs one should be concerned about sorting. It might be that a discontinuity in prices due to implementation is partly caused by a change in the demographic composition of the neighborhood (see Bayer et al. 2007, for cross-sectional evidence on school districts). Using Census Block Group level data from the American Community Survey (ACS) 2014-2016, Figure   5 shows that all household characteristics are continuous at the border. Importantly, changes in population density and the share of owner-occupied housing is the same on both sides of the border (Figure 5a). The latter is noticeable as one might expect to see a relative increase in home-ownership (as to be able to rent out to tourists) in the areas where Airbnb is still allowed if rents do not change. The reason may be that in the short run it may be hard to evict long-term renters. Hence, HSOs did not seem to have led to a fundamental change in housing tenure. We also do not detect changes in the household composition, measured by income, share of blacks, single households or median age. Nevertheless, in sensitivity analyses (see Appendix A.4.7) we will control for changes in the housing stock and demographic characteristics and show that this does not affect the results.
One could also be concerned that a discontinuity in prices arises because of a differential provision of public goods. While temporal changes in the quality of public goods are usually not abrupt, large cross-sectional differences in public good quality may provoke sorting. An important public good is school quality (see Black 1999, Bayer et al. 2007. 28 Using 2017 test score data of students between the 3 rd and 11 th grade on English and Mathematics from the California Assessment of Student Performance and Progress (CAASPP), we checked for possible discontinuities in changes of student performance around the HSO borders. Figures 5g and 5h show that no such discontinuity exists, indicating that the HSO is unlikely to be correlated to school quality. 29 In a non-spatial RDD, it is common to investigate whether the density of the running variable is continuous at the threshold, because a discontinuity reveals that some individuals manipulate their position around the threshold. In spatial RDDs -using data on the housing stock in we do not find meaningful differences in changes in densities across borders before HSOs were 28 We also checked for other spatial differences in e.g. property taxes, but we did not find any meaningful difference.
29 Note that not all school districts are pertaining to one city. For example, the City of Carson is served by the Los Angeles and Compton school districts. West-Hollywood is also part of the LA school district. Notes: Spatial differences in variables are conditional on census block group and border segment×month fixed effects. Hence, we identify the effects over time. Negative distances indicate areas outside HSO areas and areas inside HSO areas but before treatment. The dots are conditional averages at every 500m interval. The dotted lines denote 95% confidence intervals based on standard errors clustered at the census block group level. We include 3 rd -order polynomials in untreated areas and a linear function in treated areas. implemented.

HSOs and Airbnb listings
In Table 4 we report the baseline results of the impact of HSOs on Airbnb listings. In Panel A, we focus on listings of entire homes or apartments. In column (1)  In column (2) (3) we therefore multiply the optimal bandwidth by 2 and in column (4) divide it by 2. This produces similar results, with a point estimate of 7.0. One may still be concerned that the bandwidth is on the high side. We therefore divide the optimal bandwidth by 5 in column (5), so that we include only observations within 334m of the borders. We find a slightly lower, albeit somewhat less imprecise, effect of 4.8 percentage points. Reducing the distance even further is not informative, as the location of listings is known up to a 200m radius. 30 The finding that the effect is similar for very small bandwidths is particularly important as this implies that listings do not move just across the border of an HSO area (consistent with graphical evidence in 5.1), which would imply that we 30 When we apply the 'non-parametric' approach, implying that ψ1 = ψ2 = ψ3 = ψ4 = 0, on observations within 334m of the borders, we find a 7.1 percentage point effect, precisely estimated with a standard error of only 1.4.  (7). Standard errors are clustered at the census block level and in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10.
would overestimate the effects of HSOs. 31 In column (6) of Panel A we make a distinction between different types of HSOs. Recall that four cities that have implemented HSOs still allow for home sharing. As we focus here on listings of entire homes, one expects that the different types of HSOs have similar effects. We therefore include an interaction of the HSO with a dummy indicating whether home sharing is allowed.
In line with expectations, we do not find that the effect on listings of entire properties -which 31 In theory, it is possible that HSOs induce higher listings rates just outside the HSO border. Clearly, this is not what we see in the data and is in line that Airbnb prices for tourist accommodation are continuous across HSO borders. See also the placebo-check in Section 6.5 where we shift the border 1km outwards and find no effects on listings. are always restricted -is different between the two types of HSOs.
Up to now, we have ignored measurement error in the running variables, i.e. the distances to the border, which may be important as Airbnb reports the location of listings up to a distance of 200m. Measurement error usually induces bias in the estimates, potentially even more so within a regression discontinuity framework (Davezies & Le Barbanchon 2017). Arguably, the bias in our HSO estimates will be small, because the extent of the measurement error is small. For example, given the plausible assumption that measurement error is uniformly distributed between 200m, the measurement error variance appears only to be 5-10% of the distance variances (on both sides of the border), indicating that the attenuation bias in the effect of the running variables should be an order of magnitude smaller than the estimated effect size of the running variables. As this argument may not be entirely convincing, we have examined the importance of measurement error by estimating models excluding the distance to the border variables. We find then almost the same HSO effects, indicating that measurement error in the running variable is unlikely to have any effect on our estimates.
The imprecise reporting of the location by Airbnb may also affect our estimates by creating mis-classification error in the treatment variable if Airbnb misreports the city of each listing, which should lead to underestimates. To examine this, we have estimated models where we exclude observations within 200m of the border. See the last column of Table 4. We indeed find a slightly stronger effect in column (7). 32 In Panel B of Table 4 we analyze the effects of HSOs on listings of home sharing. We repeat the same set of specifications as in Panel A. The effect is about 50% smaller than for entire homes/apartments. More specifically, the coefficient in column (1) implies that the probability to list a room has decreased by 3 percentage points. This effect is somewhat stronger (−4.4 percentage points) once we include border segment×month fixed effects. Given an average probability to be listed of 0.28, this implies a decrease of 16%. The finding that the percent effect on home sharing is smaller makes sense as some cities do not completely forbid home sharing (e.g. Santa Monica). If we include border segment×month fixed effects (column (2)) or change the bandwidth (columns (3) to (5)), this leaves the results essentially unaffected. 33 In column (6) we again include an interaction of the HSO with a dummy indicating whether home sharing is allowed. As one expects, we do not find that home sharing listings have been reduced in areas where home sharing is still allowed, whereas home sharing listings have been substantially reduced in areas where short-term renting is completely banned, with a percentage point reduction that is about the same as for entire homes/apartments. We think this provides strong evidence that the changes in the listing probabilities are related to the implementation of HSOs. Column (7) highlights that measurement error is not really an issue, as exclusion of listings within 200m of a border leads to almost the same estimate as the baseline estimate.
In Figure 6 we show an event study on how the effect of the HSO on Airbnb listings varies over time by re-estimating our preferred specification shown in column (2) of Table 4, while interacting the effect of the HSO with time dummies. Before and at the moment of implementation there is no effect. Hence, there do not seem to be pre-trends in listings related to HSOs. However, after a year, we find a (marginally) statistically significant reduction in listings of entire properties of about 6.5 percentage points. After 2.5 years, the effect has increased to 15 percentage points for entire homes, which implies a reduction in listings of almost 50%. Therefore, in the long-run the HSO had a very strong effect on listings of entire properties. A similar pattern emerges for home sharing, where we find that the long-run decrease in listings is 13 percentage points (or 47%).
Why does the effect become stronger over time? One explanation is that, in the beginning, households/investors did not yet know whether and to what extent the ordinance would be enforced. After a while, it became clear that it was being enforced, implying potentially hefty fines.
In Appendix A.4.1 we investigate the effects of the HSOs on the listing probability as well as prices for each city separately. We show that the coefficients are generally negative, or when positive, statistically insignificant. However, standard errors are often somewhat large, so we cannot make precise statements for individual cities.
We also investigate the effects of the HSO on Airbnb rental prices of properties in Appendix A.4.2. We do not expect that at the border rental prices do change, because tourists are unlikely 33 When we exclude the spatio-temporal trend variables as in (5)  to differentiate between accommodation in a treated area and neighboring areas. We indeed find that rental prices of Airbnb properties are not significantly different at the border. However, one may expect differences further away from the border if tourists have a strong preference of (not) staying in a certain area. We therefore also estimate DiD models where we exclude properties close to HSO borders (<1km). Still, we do not find any effect of HSOs on Airbnb rental prices. These results are in line with the belief that the market for short-term rentals is highly competitive: restrictions on short-term rental supply by HSOs (as well as additional Transient Occupancy taxes) do not impact the spatial equilibrium of rental Airbnb prices.
We also investigate the effects of HSOs on the number of formally registered traveler accommodations in Appendix A.4.3, using data from the County Business Patterns. Because we have data on only a few years and the data is only available at the zipcode level, the results are imprecise. However, the point estimates seem to point towards a sizable 5% increase in the number of formal traveler accommodations after implementation of an HSO. Hence, we interpret this as suggestive evidence that HSOs have led to an increase in formal accommodation.

HSOs and house prices
We have seen that the HSO strongly reduces the probability of using a property for short-term renting. We expect that this will have a negative effect on house prices. In Table 5 we report the results. Notes: Standard errors are clustered at the census block level and in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10.
We start with a Panel RDD, including census block and HSO area×month fixed effects, as outlined above. The results in column (1)  In column (2) we add border segment×month fixed effects leading to essentially the same result.
The results do not materially change when we choose other bandwidths in columns (3) and (4).
However, it becomes too imprecise to be statistically significant at conventional levels in column (4). We even further reduce the bandwidth to only 362m in column (5). Now, the point estimate is very close to the baseline estimate in column (2), albeit imprecise. Clearly, columns (4)  Nevertheless, we find that in 6 cities the effect is negative (and for two cities, the effect is highly statistically significant). For most of the cities, these effects are not statistically different (at the 5% level) from the baseline estimate, which suggests that the variation in estimates between cities might be entirely due to random variation and not due to more fundamental factors (e.g., the extent the HSO is enforced).
A well-known issue with exploiting changes in house prices over time is that one has to take anticipation effects into account. Anticipation effects may have been important as discussions on the HSO predate implementation. On the other hand, it might have taken some time before observations in column (5), we find again a similar effect of −2.2%, which is statistically significant at the 5 percent level, despite the strong reductions in the number of observations. 36 Professional investors' daily revenue from renting out short-term is about twice the daily revenue from renting out long-term. Given that the renting costs (excluding the capital costs of acquiring the property) are about 20% of the revenue (we use information here from agencies that manage short-term renting for households), then the willingness to pay by professional investors exceeds those of the current marginal house owners by about 60%. the HSO capitalized into house prices. We have tested this, with results shown in Figure 7. We find that before implementation of the HSO there is no statistically significant price decrease, hence there is no anticipation effect. At the moment of implementation we find that prices are about 2% lower. The price effect is stable over time. The absence of anticipation effects also imply that there is no evidence for pre-trends, which would potentially invalidate our research design. We test more extensively for pre-trends in Appendix A.4.4.

Negative external effects related to tourism
In Table 6, we investigate to what extent negative external effects related to tourism play a role. This is important, because the estimates discussed above are the net effects of 2 opposing mechanisms. One mechanism is that the HSO reduces demand for housing, which decreases house prices, whereas the other mechanism is that it reduces negative tourist externalities, which increases house prices. Alternatively, because we find that the net effect of the HSO is negative, the estimates may be interpreted as underestimates of the efficient use effect, where the size of the underestimate depends on the size of the externality effect. To investigate the importance of the externality effect, we consider two approaches. The first approach is based on the idea that if an HSO reduces negative effects of tourism locally (e.g., up to 500m of a property which is not allowed to use short-term letting), then this has two consequences: (i) a HSO reduces tourism externalities for properties just outside treated areas; (ii) the reduction in negative externalities due to the HSO is less for properties just inside HSO borders compared to properties that are fully surrounded by treated locations. Consequently, when the externality effect is substantial, the price effect may be different close to HSO borders.
To investigate this, we calculate the share of land within a 500m ring of a treated area. Hence, for houses further away than 500m from the border, the share is either zero (when located outside a HSO area or inside an HSO area but before treatment) or one (when located in a treated area), whereas for houses within 500m, the share is between zero and one. If there are substantial negative external effects of Airbnb, conditional on the treatment dummy, one expects to see price increases when the share of land in HSOs is higher (see for a similar approach in the context of measuring the external effects of land use regulation, Turner et al. 2014). As the added measure is quite collinear with the HSO measure, we do not find statistically significant effects for the HSO and share of HSO land within 500m. However, the point estimates have the expected signs: the treatment effect is now −2.4%, so slightly more negative, in line with the idea that we now only capture the effect on demand, while the effect of the share of land in treated areas is positive, 0.9%, in the direction suggested by theory. In addition, to examine whether the effect is more local (because the externalities may not spread out over 500m), we have as an alternative included the share of land in treated areas within 100m in column (2).
This blows up standard errors even more because of severe collinearity, so not much can be learned from the latter exercise. 37 It is imaginable that the externality effect of Airbnb is even more local, such that it only shows up within buildings. To investigate this, in column (3)  All in all, we do not find strong evidence for the presence of a local external effect, implying that the estimated effect of the HSO only reflects an efficient use effect.

Airbnb listings and house prices
One could argue that the average treatment effect estimated around the border of HSO areas does not say much about the effect of Airbnb on house prices, because neighborhoods with a higher tourist accommodation demand are more strongly affected by the ordinances (as a relative decline in the listings probability implies a stronger absolute decrease in the listings rate in areas with a higher initial listings rate). We therefore estimate a 'structural equation' wherein we estimate the direct impact of the listings rate on house prices using an IV approach. To deal with endogeneity issues -omitted variable bias and potentially measurement error in the listings rate -we employ an instrumental variable approach using the HSOs in the different cities. Table 7 reports the regression results for the two-stage Panel RDD. 38 We observe in Table   7 that the instrument is strong in all specifications as the first-stage F -statistic is above the rule-of-thumb value of 10 in all specifications. In column (1), Panel A, we find that a 1 percentage point increase in the Airbnb listings rate increases property prices by 5.2%. In column (2) we include border segment×month fixed effects.
The effect reduces to 3%. A standard deviation increase in the listings rate is associated with a 1.845 × 0.0226 = 5.5% increase in prices, so the effect of Airbnb is substantial. The elasticity of prices with respect to the average listings rate in the sample is 0.0300/0.585 = 0.0513. When we only focus on areas where an HSO is implemented this elasticity is very similar and equal to 0.0402. 39 Changing the bandwidth substantially does not change the results much, although the coefficient becomes imprecise for small bandwidths. 40 In columns (5) and (6) of Table 7 we make sure that the choice to determine the listings rate within 200m is not affecting our results. When we use the listings rate within 100m, the coefficient is 0.0251, which is very similar to the baseline estimate. Moreover, when using the 38 Table 7 also report the bandwidths. We obtain the bandwidth from the first stage: a regression of the listings rate on the HSO dummy.
39 These estimates are of a similar order of magnitude as Barron et al. (2018), who use a completely different identification strategy. 40 We also considered to further reduce the bandwidth, as in the previous tables. However, because of a weak first stage, the results are uninformative and imprecise and available upon request. Given that both reduced-form effects of HSOs on listings and prices are statistically significant for small bandwidths, we do not consider this a major issue. Notes: We exclude transactions occurring within half a year after implementation of the HSO. We instrument the listings rate a dummy indicating whether an HSO has been implemented. Robust standard errors are clustered at the census block level and in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10.
listings rate within 500m the coefficient is slightly higher than the baseline estimate. Hence, our results are rather insensitive to the area choice.
Because we have to impute listings data for the months where we do not have Airbnb data, one may criticize the listings rate variable. To show robustness, we first use only the months for which we have actual Airbnb data. In column (7) we show that this leads to a very imprecise estimate and a rather weak first stage. In any case, note that the point estimate is higher than the baseline estimate.
To investigate further whether our proxy for Airbnb listings matter, we use a different proxy for Airbnb intensity, by approximating listings using the first and last review and assuming that the property is continuously listed in between, following Zervas et al. (2017) and Barron et al. (2018). The mean approximated listings rate is 0.54, which is very comparable to the mean imputed listings (0.59). The cross-sectional correlation between the imputed and approximated measures is quite high (ρ = 0.812). However, more relevant, as we exploit variation over time in this measure, is that the correlation over time between these two measures is much lower (ρ = 0.416). In column (8) we show that we also find a positive and marginally significant effect of this alternative measure. If anything, the impact is somewhat stronger, albeit not statistically significantly different from the baseline estimate.

Placebo checks and sensitivity
It is important to show the robustness of our results. In this subsection we will show some 'placebo'-estimates and summarize the most important robustness checks.
In Table 8  One obvious candidate for a placebo is to shift the borders of HSO areas 1km outwards to make sure that we do not capture some spatial trend that is correlated to the treatment variables. It seems that this is not an issue, as the effects of the placebo-HSOs on listings and house prices are statistically indistinguishable from zero. In the second placebo test, we investigate the issue that in some cities Airbnb is officially not allowed because the zoning code does not allow for short-term renting, but as discussed in Section 2, these zoning codes are not enforced. We treat those cities (listed in Appendix A.1) as if an HSO would have been implemented. To determine the timing of the placebo HSOs for each of those cities, we take the timing of the nearest city that has implemented an HSO. The results in column (2) confirm that those cities do not see a decrease in listings or house prices.
As a third placebo check, we treat each neighborhood in the City of Los Angeles with a placebo HSO. This is relevant as the City of LA had plans to restrict Airbnb. At the time of writing Airbnb is still allowed, but hosts may only operate one short-term rental at a time and will only be able to rent out their properties for 120 days a year. Again, to determine the timing, for each neighborhood in LA we take the nearest city that has implemented an HSO. Column (3) in Table 8 shows that there is no effect of this placebo HSO on listings or prices.
Column (4) continues by checking whether 'unincorporated' areas, which have identical regulation with respect to public goods and STRs, have seen changes in listings and prices. To determine the timing of the placebo HSOs we again use the date of implementation of the nearest HSO area. The coefficients clearly indicate that there is no effect of the placebo HSO. We find a slight positive effect in on prices, but we think this is merely a Type II error, given the absence of an effect on listings.
In the final placebo checks we investigate whether we can detect any effect on housing prices using data from exactly 5 and 10 years earlier (from 2009 until 2013 and from 2004 until 2008) and assume that the HSO would have been implemented exactly 5 or 10 years earlier. Because Airbnb data is not available from before 2014, we cannot estimate this placebo test for listings. For house prices, we again find that estimates are economically small and statistically indistinguishable from zero. This is important, because this suggests that there are not statistically significant pre-trends in prices that may explain the price effect we find in our analysis.
Therefore, the placebo-estimates reported in Table 8 confirm that the finding of a reduction in listings and house prices due to implementation of the HSO is not a statistical artifact and unlikely the result of a differential provision in the change of public goods or other regulation.

HSOs, listings and rents
So far, we focused on the effects of HSOs and Airbnb listings on house prices. One may wonder whether the results also hold if we extend the analysis to rents. We reiterate here that differences in rents should capture the housing supply effect -short-term rentals may lead to a reallocation of existing housing stock away from the long-term rental market towards privately owned housing.
Because renters should be indifferent to properties that are close to HSO borders, we cannot use a Panel RDD to identify the housing supply effect. We therefore use a more standard difference-in-differences strategy and include observations further away from the border. Table 9 reports the results. In Panel A we test for the effect of HSOs on rents, while in Panel B we test for the direct effect of listings, while instrumenting the listing rate with the dummy indicating whether an HSO has been implemented in the area.
In column (1), Panel A, we show that due to HSOs, rents have decreased by 2.3%. Column (2) shows that the effect is similar when we exclude properties that are further away than 25km from any HSO area, which ensures that we exclude the low-density outskirts of LA County where rent trends may be very different. In column (3), we also drop observations close to (1km) but outside HSO areas. The results indicate an effect that is only slightly stronger (2.2%).
This estimate is very close to the preferred estimate for prices, reported in column (2), Table 5.
Column (4) explicitly tests whether rents are continuous at the borders of HSO (within 2km of both sides). We indeed find no statistically significant difference between HSO areas and areas outside HSOs. Moreover, the point estimate is very close to zero. This is evidence for the idea that properties that are close to the HSO border are (likely) close substitutes. In column (5), Panel A, we control for second-order polynomial distance to the CBD×year and distance to the beach×year trends, leading to slightly lower effects. Finally, we only keep observations in column (6) that are inside HSO areas and further away than 2.5km from any HSO border. We find that house prices then decrease by 2% when an HSO is implemented.
We also test whether pre-trends and/or anticipation effects are an issue. Figure 8 replicates the Notes: In all specifications we include observations inside HSO areas. In Panel B we instrument the listings rate with a dummy indicating whether an HSO has been implemented. Standard errors are clustered at the zipcode level and in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10.
specification with distance to CBD and beach trends, zipcode and month fixed effects. This specification only includes zipcodes that are further than 1 and less than 25km from a (future) treated area. We find no effect before implementation: the effect is small and statistically insignificant. After half a year, the effect of HSOs becomes statistically significant at the 5% level. The long-run effect after 2 years is about 5%, albeit somewhat imprecise.
In Panel B, Table 9, we use the listings rate. We instrument for the listings rate with the HSO dummy. The results show that the instruments are sufficiently strong and in Appendix A.4.8 we show that the HSO dummy also has the expected sign and is statistically significant and negative in all case. In column (1) we find that when the listings rate increases by 1 percentage point (0.69 standard deviations), rents increase by 4.9%. The effect is slightly lower when we only include observations within 25km of an HSO border (column (2)). This effect is comparable to the results we found in Table 7. The effect becomes higher when we exclude zipcodes outside HSO areas that are within 1km of an HSO border (column (3)). In line with previous results, we do not find any effect of the listings rate when focusing on zipcodes close to HSO borders (column (4)). If we control for distance to CBD×year and distance to the beach×year trends, the effects are comparable. The estimates in column (5) and (6) are a bit higher than the effects on prices, but note that they are not statistically significantly different from the baseline estimate for prices.
In Appendix A.4.8 we make sure that the results also hold for median list prices: we show that the house price effects using the DiD estimation strategy deliver similar results as the ones reported in Tables 5 and 7. This suggests that the DiD strategy is a plausible alternative estimation strategy. Moreover, these ancillary regression highlight that the average treatment effect identified through a Panel RDD is about equal to the average treatment effect identified through a DiD strategy.
7 The overall price and welfare effects of Airbnb and HSO

The overall price effects of Airbnb and HSO
We continue to calculate the overall effects of Airbnb and HSO on the housing market. In Table   10 we investigate the total effects of Airbnb and HSOs on average property prices for LA County as a whole and for specific areas, based on our estimates combined with descriptive information on house prices and number of listings in these areas. To be more precise, we evaluate the total effect of Airbnb using the listings rate in these areas as of September 2018. We then consider two counterfactual scenarios; one where no HSOs would have been implemented and another where HSOs would apply to all cities in LA County. As the rent effect is very similar to the effects on prices (for which we provided evidence in Section 6.6), we just report price effects here, and use a discount rate of 3.3% (obtained from Koster & Pinchbeck 2018).
In all scenarios, we assume that the effect of Airbnb listings is linear. 42 This assumption is likely innocuous when we focus on the price effects for LA County as a whole, and likely reasonable when we focus on areas with listings rates not too far from the average listing rate (equal to 1.21%), but for areas with very high listings rates (such as Venice), the predicted price effects should be interpreted with caution.
Our estimates imply that the gains of Airbnb for LA County as a whole are quite modest (3.6%).
This result makes sense, because many areas in LA counties have a low listings rate. However, there are also areas with higher listings rates. It is for example interesting to focus on areas within 5km of Hollywood's Walk of Fame, a major tourist hotspot, where the listings rate is more than four times the County's average. When we focus on these areas, the house price effect due to Airbnb is estimated to be 14.7%, which we consider to be substantial. When we limit ourselves to areas within 2.5km of the Walk of Fame, we find even a more pronounced effect effect of 20%. One may wonder whether these effects are realistic and how they compare with nominal changes in prices during this period. It appears that nominal house prices within 5km of Hollywood have increased by more than 40% in the last 10 years, so it seems that our estimated effects are not unrealistically high, and explain about 1/3 of the nominal price increase.
We also consider the effects in beach towns. Within 2.5km of the beach, the price increase due to Airbnb is estimated to be equal to 4.8%. If we concentrate on specific cities and neighborhoods, the price effects of Airbnb vary substantially. In one of the most popular LA neighborhoods -Venice -the total price increase is more than 30%. On the other hand, in Pasadena (which is about 15km from Downtown LA), the effects of Airbnb are modest.
Let us consider the two counterfactual scenarios. First, we consider that all HSOs are abandoned. Within 2.5km of a beach, this implies that the listings rate and house prices increase respectively by about 5% and 0.3%. For Santa Monica, which is well known for its strict HSO, the listings rate would increase by 60% and the house price by almost 2.5%, which is substantial. For locations near Hollywood, abandoning HSOs does not imply large changes in property values, because hardly any areas within close distance of Hollywood are targeted by HSOs.
By contrast, if all cities would implement HSOs this can have large effects in areas attractive to tourists. For example, in Venice the listings rate would drop by 30% and house price by 11.6%.
Hence, HSOs are likely to have large effects in areas attractive to tourists.
Our results also imply that in neighborhoods attractive to tourists, the distributional consequences of Airbnb are grave: in popular areas, incumbent homeowners have benefited more than $3-15 thousand per year due to Airbnb, whereas renters likely lost a similar amount, as renters are not allowed to list their property on Airbnb, while paying higher rents at the same time.
As a consequence, there are clear distributional implications of HSOs. Homeowners will lose from the HSO, as the demand for housing will decrease. This effect is due to a less efficient use of housing (because properties are not available for their most profitable use). However, (long-term) renters are likely to gain because more houses become available for rent so rents decrease. This offers a plausible explanation as to why cities around the world that have heavily restricted STRs typically have a high share of renters. 43

Welfare implications: back-of-the-envelope calculations
We showed that the HSO leads to lower house prices and rents. This effect is due to a less efficient use of housing and a reduction in supply of rental housing respectively. To get an idea of the order of magnitude of the quantitative welfare effect, we will now derive the welfare effects of the HSO based on back-of-the-envelope calculations. 43 We have analyzed the conditional relationship between the share of renters and the probability to implement an HSO using data for 88 incorporated cities and two unincorporated places in the Los Angeles area. Slightly surprisingly, for these data, there is no correlation between the share of renters and the introduction of the HSO, but as shown in Appendix A.5, when we condition on income per capita (and, less importantly, a range of demographic indicators), then there appears to be a strong effect of the share renters on the probability to implement an HSO: the results suggest that there is proportional relationship between these two variables. We perceive this result as suggestive only, as we do not have exogenous variation in the share of renters. We also gathered some data for 29 other U.S. cities. We find again suggestive evidence that a majority of renters is associated with more stringent Airbnb regulations using a sample of 29 major U.S. cities. We use the maximum number of days per year allowed for short-term renting as an (inverse) measure of stringency. The maximum allowed number of rental days is 45 for cities with a majority of renters, while it is 246 for all other cities (the correlation between maximum allowed number of rental days and the share of renters is −0.25).
We make several restrictive assumptions. We assume that welfare effects are fully captured by changes in house prices and rents in competitive markets, where homeowners own the land, in line with a large urban economics literature (see e.g. Brueckner 1990). Furthermore, we assume that (i) Owners and renters have a discount rate of 3.3% and (ii) the same marginal utility of income. Given that owners tend to be richer than renters, this assumption tends to overestimate the losses related to the introduction of the HSO. However, given that we focus on rather expensive housing (and therefore relatively rich renters), this assumption seems defensible.
(iii) Welfare effects of tax avoidance are assumed to be absent. 44 (iv) The demand functions for housing are linear and the total housing stock is given. 45 (v) We focus on the comparison between observations that are either in or far from the HSO border (which implies that we avoid the complication that rental properties close to the border are not affected by the HSO, see Section 6.6). (vi) Home-ownership and renting are perfect substitutes. (vii) We consider the case where outside investors buy properties to list on Airbnb and assume that the investors' WTP slightly exceeds the highest WTP of incumbent households. 46 In Figure 9 we show the demand effects of the HSO. We have drawn housing supply H * and the equilibrium quantity of STR listings. In the initial situation, in the absence of regulation, the equilibrium quantity of STRs is given by H STR and the units used for residential housing is H * − H STR . In Figure 9, the HSO implies that H STR = 0, which means a reduction in the total surplus equal to A-B-E-F. Per property, the reduction in surplus is E-F. Table 5 indicates a 1.8% decrease in property values due to HSOs.

Our preferred estimate in
We calculate then the welfare effect using the average house price in HSO cities and obtain an annual welfare loss of HSOs of about $1250 per property. Given the substantial benefits of Airbnb, this seems a reasonable number. The intuition for such a substantial loss is that the 44 This assumption is not restrictive regarding avoidance of transient occupancy tax, because this tax is collected by Airbnb. The assumption is more restrictive though regarding income tax, but then only for moderate suppliers (as there is an annual tax-free allowance of $7, 500 for home sharing letting, whereas annual earnings of more than $20, 000 are automatically reported to the US income revenue service). Consequently, our decreases in welfare because of efficiency losses are likely overestimates, but this does not have any consequence for the distributional implications. 45 This assumption is not essential, as non-linear demand functions implied by our log-linear hedonic price functions, provide almost identical welfare results.
46 Note that when the investors' WTP does not exceed the highest WTP of incumbent households, then our welfare estimates are overestimates. We believe, however, that the assumption is defensible. Note further that because the proportion of STRs is small compared to the other houses, about 2.5% in our data, the slope of the investors' demand function is essentially irrelevant. investors' WTP (which reflects the WTP of Airbnb users) is likely much higher than the WTP of the marginal incumbent household that is being priced out of the market. Given that tax evasion is assumed away, and that we assumed that the marginal utility of income is the same for renters and owners, we believe that the annual welfare loss of HSOs of about $1250 per property suggested by our back-on-the-envelope should probably be interpreted as the maximum welfare loss.

Conclusions
We have seen a spectacular growth of online short-term housing rental platforms in recent years.
However, it is yet unknown how these platforms affect the housing market.
We exploit quasi-experimental variation in Airbnb listings to test the impact of short-term rentals on house prices and rents. We focus on Los Angeles County, where 18 cities have implemented Home Sharing Ordinances that restrict short-term rentals between 2014 and 2018.
Using microdata for house prices, and listings, we apply a Spatial Panel Regression-Discontinuity Design around the borders of those areas and exploit the differences in timing of the HSOs.
Home Sharing Ordinances reduce Airbnb listings by about 50%, and reduce house prices by 2% on average, which captures the fact that houses cannot be used for their most profitable use anymore. Using aggregate data and a difference-in-differences estimation strategy we find essentially the same effects for rents. Forbidding short-term rentals may lead to a reallocation of away from privately owned housing towards the long-term rental market -a rental housing supply effect.
On average, the total effect of Airbnb on property values in LA County is modest (3.6%). This makes sense because in large parts of this county, Airbnb is not so popular. However, in areas attractive to tourists, where the Airbnb listings rates are quite high, the effects of Airbnb are substantial. Within 5km of Hollywood's Walk of Fame, for example, the increase in property values is almost 15%. In Venice Beach, which is a popular tourist destination, Airbnb may have increased property values by more than 30%.
Our estimates imply that Airbnb regulation has stark distributional implications, because it induces losses for homeowners that are very substantial in areas that are popular for tourists.
The opposite holds for households who typically rent and who can only gain from regulation as it increases rental housing supply and therefore reduces rents.
Ignoring the distributional consequences, our results suggest that Airbnb regulation has a negative effect on overall welfare, given the important proviso that tax avoidance by suppliers of Airbnb listings is limited. Rather than regulating short-term rental platforms quantitatively, it seems feasible to address current tax avoidance more directly. Tax avoidance of the transient occupancy tax (as well as a tourist tax, if present) can be minimised, by letting Airbnb collect revenue. For example, in LA County, but also in other cities in California, including San Francisco, Airbnb collects the (ad-valorem) transient occupancy tax for the city (without revealing information about Airbnb hosts). Tax avoidance of income tax can be addressed, by using the same tax rate for all hosts, while letting Airbnb collect the revenue.

A.1 Data appendix
Below, in Table A1, we report the results of our data gathering endeavors. Ready-to-use data on Home Sharing Ordinances is not available, so we have browsed the Internet and phoned local officials to know whether the city has implemented an HSO some time during our study period.
For each city we report whether is has implemented an HSO, whether home sharing is permitted, whether a STR needs to register at the municipality and whether officially STRs are not allowed according the residential zoning code. Furthermore, we list the sources from which we get the information.

A.2 Bandwidth selection
We use the approach proposed by Imbens & Kalyanaraman (2012), who show that the optimal bandwidth can be estimated as: where the constant C K = 3.4375 and N is the number of observations.σ 2 − andσ 2 + are the conditional variances of respectively ikt or log p ijt given d i = c on both sides of the threshold Because we exploit variation in prices and the HSO over time to determine the bandwidths, we first demean the variables by month and property or census block fixed effects. In many specifications we add additional covariates (e.g. housing characteristics). We then determine the conditional variance of the dependent variable given all covariates and fixed effects at the Usually, adding covariates does not affect the optimal bandwidth much (Imbens & Kalyanaraman 2012). Indeed, adding a wide array of controls barely influences the optimal bandwidth in our specifications.  0  0  0  0  phone interview  Alhambra  0  0  0  0  phone interview  Arcadia  2017  7  1  1  1  0  phone    Negative distances indicate areas outside HSO areas and areas inside HSO areas. The dots are conditional averages at every 500m interval. The dotted lines denote 95% confidence intervals based on standard errors clustered at the census block level. We include a 4 rd -order polynomial in untreated areas and a 2 nd -order polynomial in treated areas.
densities of key variables after the HSO has been implemented.

A.3.1 Cross-sectional differences in listings
In Figure A1 we illustrate cross-sectional differences in listings before and after the HSOs were implemented. In Figure A1a, we compare the probability of being listed before a HSO was implemented on both sides of the border. It is clear that there was essentially no difference between HSO areas and surrounding areas. However, after the HSO was implemented, the probability of being listed is approximately 4 percentage points lower (see Figure A1b).

A.3.2 Discontinuities in housing characteristics
An important assumption in the Panel Regression Discontinuity Design is that changes in covariates, except for the treatment variable, are continuous at the border. We therefore investigate in Figure A2 whether changes in housing characteristics over time do not show discontinuities. Figure A2a highlights that the change in the share of condominiums is not statistically significantly different at the border of HSO areas. Figure A2b further shows that there is small discrete jump in the change in construction year at the border, but this jump is only statistically significant at the 10% level. This would imply that after an HSO has been implemented, slightly newer properties are traded in HSO areas. To control for this effect we include construction decade dummies in the regressions.
For property size we also find a small jump, but the difference is again only marginally statistically Notes: Spatial differences in variables are conditional on census block and border segment×month fixed effects. Hence, we identify the effects over time. Negative distances indicate areas outside HSO areas and areas inside HSO areas but before treatment. The dots are conditional averages at every 500m interval. The dotted lines denote 95% confidence intervals based on standard errors clustered at the census block level. We include a 4 rd -order polynomial in untreated areas and a 2 nd -order polynomial in treated areas.
significant. To the extent the price effect partly captures changes in the houses on offer in HSO areas, we control for the property size in the house price regressions. Finally, we do not find a statistically significantly different jump in the number of bedrooms ( Figure A2d).

A.3.3 Conditional McCrary tests
A test for discontinuities in densities of the running variable before the introduction of the HSO might be informative, as a discontinuity might be indicative of unobserved housing or household traits (e.g. different types of households sorting themselves into treated areas) that are potentially correlated with the treatment. However, this test should take into account the geography of the area and borders of the areas, as discontinuities in listings or housing transactions may also indicate that some areas border mountainous areas, parks or the sea.
We therefore estimate a two-step density test in the spirit of McCrary (2008). In the first step second step we estimate this distribution for listings and for housing transactions respectively.
Our test is then the difference in the estimated densities between the second and first step.
Hence, a negative (or positive) density differential would indicate that there are fewer (or more) listings/transactions than expected given the spatial distribution of buildings.
The results are reported in Figure A3. Figure A3a tests for the continuity of the density differential of listings before an HSO was implemented. We find that there is no difference in the density for listings at the HSO border. We repeat the same exercise, but now for housing transactions in Figure A3b. This test indicates a discontinuity due to a higher density of housing transactions just across the border in HSO areas. Note however that the discontinuity is economically very small, so we do not consider this as a problem.
We repeat this exercise by estimating the adapted McCrary's density test after an HSO was implemented, but given the spatial distribution of buildings in 2014. In Figure A4a we show that Airbnb listings are now discontinuous after the HSO. The density is much lower in treated areas, which is in line with the finding that listings have been reduced due to the implementation of HSOs. For house prices ( Figure A4b) we find essentially the same difference in density of transactions as in A3b, which we think is reassuring: the HSO did not lead to a different market turnover on both sides of the HSO borders.

A.4 Other regression results and robustness
In this part of the Appendix we will subject our results to a wide range of robustness checks and report some additional results. We subject our results to a wide array of additional robustness checks in Appendix A.4.7. In Appendix A.4.8 we check for sensitivity of the results using the Zillow data, so the results using a DiD estimation strategy.

A.4.1 City-specific effects
Here we analyze city-specific effects. We re-estimate the preferred specification where we include border segment×month fixed effects. Given that the number of observations for many cities is limited, one expects that only for a handful cities the coefficient is statistically significant. On the other hand, if there is a substantial number of coefficients with the wrong sign, and these coefficients are statistically significant, then our identification strategy would be less convincing.
We report the results in Table A2.
In columns (1) and (2) we report the results for respectively listings of entire properties and home

A8
sharing. We exclude observations in and near cities that have implemented HSOs before the first observation in the data and cities for which we have fewer than 1000 listings over the whole sample period. Column (1) shows that the point estimates related to HSOs are almost always negative and in three cases highly statistically significant. Column (2) also shows that most coefficients are statistically significant and negative and comparable to the results in column (1).

A.4.2 HSOs and Airbnb short-term rental prices
Did HSOs have an impact on short-term rental prices of Airbnb properties? We explore this in Table A3. These are hedonic price analyses using observations of properties that are listed (in our dataset). We emphasize that spatial equilibrium theory indicates that at the border short-term rental prices would not change, because tourists are unlikely to differentiate between accommodation in HSO areas and immediately adjacent areas and are therefore unlikely to be willing to pay higher prices in areas that have implemented HSOs.
In column (1) we estimate the Panel RDD and do not find a statistically significant effect of an HSO on Airbnb rental prices. This also holds if we include border segment×month fixed effects in column (2) and change the optimal bandwidth in columns (3), (4) and (5). In column (6) we include property fixed effects. In all cases the effect of an HSO on prices is economically negligible and statistically insignificant, confirming spatial equilibrium theory.
We extend these results by using the same difference-in-differences approach as in Section 6.6.
In Table A4 we report the results. In column (1) we include all observations in LA County.
The effect of HSOs is small and statistically insignificant. This also holds if we only include observations within 25km of any HSO border. In column (3), we exclude observations that are close (<1km) within a border. Column (4) further controls for distance to CBD and distance to the beach trends. The final column we exclude observations within 5km of an HSO border. All  results are economically small and far from being statistically significant.
All in all, we do not find any evidence that Airbnb rental prices are affected by HSOs, which is Notes: In all specifications we include observations inside HSO areas. Standard errors are clustered at the zipcode level and in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10.
in keeping with the notion that the market for Airbnb properties is competitive and tourists demand for local accommodation is elastic.

A.4.3 HSOs and formal accommodation
We investigate here how the formal hotel industry benefited from the implementation of HSOs.
Again, at the border, we expect few effects. However, when comparing HSO areas with areas further away from the border, we might expect to see an increase in the number of officially registered traveler accommodations, which we investigate here (we do not have information on hotel rates).
We obtain yearly data from the County Business Patterns at the zipcode level and keep NAICSsector 72111, which are traveler accommodations, including hotels, casino hotels and other traveler accommodations. Because the latest County Business Pattern data is from 2016, we also include 2012 and 2013, so that we have data for 5 years. We take the same approach as in Section 6.6, where we use a DiD design.  accommodations have increased due to the HSO.

A.4.4 Anticipation effects and pre-trends
Here we investigate pre-trends of house prices further. Note that the Panel RDD would imply that price trends in HSO areas and neighboring areas are the same. However, if anticipation effects are important, because HSOs are announced or anticipated, prices may already adjust before the actual treatment. We did not find evidence for this in Figure 7 in Section 6.2, but we investigate this further in Figure A5 by allowing for price changes 3 years before treatment.
We do not find evidence for pre-trends. That is, before the treatment year there is no statistically significantly lower price in treated areas. One may be concerned that this is an issue of precision, as the point estimate is still negative and around 2% the year before treatment. We emphasize that this may be due to announcement of HSOs before actual implementation. For example, in We test for longer pre-trends (respectively 5 and 10 years before the treatment) in Section 6.5 by taking samples of house prices preceding the current sample. By running placebo regressions Notes: We estimate standard errors corrected for cross-sectional dependence using a Bartlett kernel and given the indicated spatial cut-offs. *** p < 0.01, ** p < 0.05, * p < 0.10.
we show that there is no evidence that prices where already decreasing in areas where HSOs are to be implemented.

A.4.5 Spatial HAC standard errors
Spatial data is usually not interdependent. More specifically, unobserved characteristics of a property (e.g. crime, maintenance quality) are likely correlated over space and time. Although these variables are unlikely to be correlated with the HSO and therefore do not affect the consistency of the estimated coefficients, spatial dependence may imply that the estimated standard errors are biased.
In this paper we cluster at the census block level to partly address this issue (see Moulton 1990), but clustering implies strong parametric assumptions as to how observations relate to other observations. We aim to allow for more general forms of dependence. We therefore use Conley's (1999) procedure to allow for spatial dependence. We use a linear Bartlett kernel to determine kernel weights, indicating how one observation relates to the other. We use an initial spatial window, denoted by sw, equal to the bandwidth used in the RDD.
In column (1) of Table A6 we report the baseline specification with standard errors clustered at the census block level. If we then allow for cross-sectional dependence within 1.86km in column (2), we find very similar, and even slightly smaller, standard errors. In the following specifications we increase the spatial window to up to 10 times the optimal bandwidth (almost 20km) in column (5). If anything, the standard errors become slightly smaller, but are very comparable to the results clustered at the census block level. Hence, we conclude that spatial dependence is not an issue of major concern.
A.4.6 Airbnb listings and house prices: first-stage results In this part of the Appendix we consider the first-stage results. The second-stage results are reported in Table 7. The dependent variable is the Airbnb listings rate within 200m of the property in Table A7.
In column (1), Table 7, the coefficients imply that the HSO has reduced listings on average by about 0.4 percentage points, which is 67% of the mean listings rate. However, there is substantial heterogeneity, as expected. The effect of HSOs on the listings rate tend to become somewhat stronger once we include HSO border segment×month fixed effects. Columns (3) and (4) in Table 7 show similar effects once we respectively increase or decrease the bandwidth. Columns (5) and (6) show that the first-stage coefficient becomes somewhat stronger if we calculate the listings rate within 100m, while it is somewhat lower if we take the listings rate within 500m.
Column (7) only consider the months for which we have listings data. This leads to a very similar first stage. Also if we consider an alternative approximated measure for listings, the first stage is very similar.

A.4.7 Additional sensitivity analyses
Here, we subject our results to an additional range of robustness checks. We report the reduced-form results for prices in Table A8.
The first column improves on identification by including property fixed effects rather than census block fixed effects. Because we look at a relatively short time period, this greatly reduces the number of degrees of freedom because most properties are sold only once between 2014 and 2018.
Still, we find a negative and statistically significant effect of HSOs that is even somewhat higher: an HSO seems to be associated with a price decrease of 4.9%. 47 However, using a Hausman T -test, it appears that this coefficient is not statistically significantly higher than the baseline estimate where we include census block fixed effects.
In this paper we use a Panel RDD to identify the house price effects based on an optimal 47 Note that using property fixed effects implies that identification mainly occurs based on transactions sold both in 2014 and 2018, because properties are usually not transacted in subsequent years. This implies that we identify here a long-run effect of HSOs.
HSO implemented -0.3919*** -0.5882*** -0.5229*** -0.4875*** -0.7245*** -0.4519*** -0.5577*** -0.4148*** (0  Notes: The listings rate is instrumented witha dummy variable indicating whether an HSO has been implemented. Robust standard errors are clustered at the census block level and in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10. uncorrelated to geographical features of a location, which may impact price trends (e.g. through the propensity to build on the land). Because the average length of a straight border segment is just below 50m, we cannot include border segment×month fixed effects, as this will lead to a too low number of degrees of freedom. We do not find that the price effects of the HSO are very different. The estimate is similar, but imprecisely estimated because of the high number of fixed effects.
We repeat a similar set of specifications when estimating the 'structural equation' as to evaluate the impact of Airbnb listings on house prices. In all specifications we instrument the listings rate with the HSO dummy. The results are reported in Table A9.
Column (1) uses property fixed effects. The estimated effect is similar, but very imprecise.
In column (2) we find a considerable stronger effect of the listing rate when we include trends instead of selection a particular bandwidth: a 1 percentage point increase in the listings rate is associated with a price increase of 8.7%, which seems to be unrealistically strong. This suggests that using a local linear approach is preferred over including all observations (see Gelman & Imbens 2019). When we control flexibly for differential price trends between more and less touristy areas in column (3), the coefficient of listings rate is somewhat higher than in the preferred specification. The same holds in column (4) when we control for changes in Notes: In all specifications we include observations inside HSO areas. Standard errors are clustered at the zipcode level and in parentheses. *** p < 0.01, ** p < 0.05, * p < 0.10.
neighborhood characteristics, and column (5) where we use straight border-segment×year fixed effects.
Column (6) we make sure that the results where we test the impact of the listings rate on prices are not driven by a few, potentially unrealistic, outliers. Indeed, when we exclude observations with a rate above 15%, the results are, if anything, stronger.
A.4.8 Sensitivity analyses for difference-in-differences estimation strategy In this Appendix section we check for sensitivity of the results using the Zillow data, so the results using a DiD estimation strategy. We first report first-stage regression results in Table A10, corresponding to the second-stage results reported in Panel B of Table 9. It can easily be seen that HSOs reduce the listings rate by about 0.45-0.55 percentage points, which is comparable in magnitude as reported in Table A7.
In Table A11 we repeat the DiD analysis, but now we take the median list price in the Zillow data as dependent variable. We find negative effects of the HSO in all specifications, with magnitudes that are very comparable as previously reported. Note that if we only include observations within 1km in column (4) we find a strong negative impact of HSOs, although the coefficient is somewhat imprecise. This is in contrast to the absence of any effect of HSOs on rents within 1km, and in line with the idea that long-term rents will not be discontinuous at the HSO border, while prices are. The reason is that two rental properties will be close substitutes and people are unlikely to be willing to pay more for a property that is just inside an HSO area.  do not care so much about the potential revenues from Airbnb, while poorer households could use the money. This is confirmed in column (3) where we further include a set of other demographic controls. There seems to be a proportional increase of the share of renters with respect to the probability to receive an HSO. In column (4) where we control for house type, the coefficient becomes even somewhat stronger. Although we refrain from giving a causal interpretation to these regressions, we think the correlations are in line with the idea that renters have more incentives to vote for the implementation of an HSO.