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Using Purchase Restrictions to Cool Housing Markets : A Within-Market Analysis Somerville, Tsur; Wang, Long; Yang, Yang Sep 28, 2018

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Using Purchase Restrictions to Cool HousingMarkets: A Within-Market AnalysisTsur Somerville †Long Wang‡Yang Yang§This version: September 28, 2018†Sauder School of Business, UBC. 2053 Main Mall, Vancouver, BC, V6T 1Z2, Canada. (email:tsur.somerville@sauder.ubc.ca ).‡School of Entrepreneurship and Management, ShanghaiTech University, 393 Middle Huaxia Road,Pudong, Shanghai, China 201210 (email: wanglong@shanghaitech.edu.cn).§School of Hotel and Tourism Management, CUHK Business School, The Chinese University of HongKong, 12 Chak Cheung Street, Hong Kong SAR (email: zoeyang@cuhk.edu.hk).1Using Quantity Restrictions to Cool Housing Markets: A Within-Market AnalysisAbstractIn response to worsening housing affordability resulting from rapid housing priceappreciation, governments in some high housing price areas have introduced taxesor restrictions to reduce investment by non-residents in residential real estate. Westudy the effectiveness of these efforts using the restrictions imposed by local Chinesegovernments in November 2010 on apartment (condominium units) purchases. Ourcontribution comes from using data that exploits within city variation in restrictionimplementation to better control for unobserved city differences and the incorporationof land auction data to identify the supply effect of these policies. Our results suggestthat restrictions on non-owner-occupant purchases significantly reduce activity levelsby approximately 40% in the short run, compared to areas without restrictions. Theseeffects diminish with time. However, housing price changes are not different betweenrestricted and unrestricted areas. The results operate via end-user demand and notthrough the land market and the subsequent supply response by developers as neitherthe number of land auctions or prices paid for land have differential changes betweendistricts with and without purchase restrictions.Keywords: House prices, government restrictions, Chinese housing marketJEL Code: R21, R281 IntroductionSince the financial crisis, housing prices in a number of cities have experienced significantgrowth. In response to dramatically worsening housing affordability resulting from houseprice inflation, local residents have targeted their ire at residential real estate purchases bynon-residents, as they perceive external capital flows to residential real estate as a primarycause of the affordability challenges.1 Governments in Australia, Canada, Hong Kong, Israel,and Singapore have placed higher purchase taxes on non-resident buyers. The United King-dom and New York have changed the tax treatment afforded non-resident owners. Switzer-land has restricted the number of units available for investor purchase. The new governmentin New Zealand in the summer of 2018 introduced severe limits on foreign investment in res-idential real estate, similar to Australia’s restrictions that limit non-residents to purchasesin new developments only.2 While the calls for action have been strong, the evidence on theeffectiveness of these type of policies at addressing overheated markets is somewhat sparse.In this paper, we use within city variation in Chinese market tightening policies to evaluatethe success of these types of restrictions on investor demand in cooling housing markets andmoderating rapid house price appreciation.In late 2010 and early 2011 in the midst of a nationwide housing boom that grewfrom expansive policies following the world financial crisis, the Chinese government intro-duced measures to calm local housing markets. Beyond macro-prudential directives affectingmortgage interest rates, mortgage underwriting criteria, and access to mortgage credit, theChinese government also directed municipalities to limit the number of properties a house-hold could purchase. These restrictions targeted investment, preventing buyers, dependingon their residency status, from purchasing either a second or third property.3 Unlike themacro-prudential policies that were imposed on all significant cities and applied to all buy-ers, the purchase restrictions were enacted with variation: some cities did not introducerestrictions at all, while in others the implementation varied by location within the city. Weexploit the latter within city variation in these restrictions using development project leveldata to test the effects of the purchase restrictions on house prices and transaction volumes.In both western markets with rapid price appreciation that have worsened affordability1See Bryant, C. in Bloomberg Opinions, Aug 18, 1918 for a synopsis:https://www.bloomberg.com/view/articles/2018-08-20/can-t-afford-a-house-blame-the-apocalypse.2This is distinct from long standing restrictions in many areas of non-resident purchases of ”sensitive”oceanfront or agricultural land.3Much of this is not for rent. A Southwest University of Finance Study reported 20.9% of housing unitsunoccupied in 2011. As reported in Wall Street Journal, June 11, 2014, https://www.wsj.com/articles/more-than-1-in-5-homes-in-chinese-cities-are-empty-survey-says-1402484499.1for local residents and in Chinese cities the concern is that investors who purchase residentialreal estate for capital appreciation or as a store of wealth and not income flow are distortinghousing markets away from local incomes.4 Non-residents and capital inflow that supportthis type of purchase could cause local house prices to reflect larger asset markets ratherthan local labour markets.5 By limiting investor demand, the hope of governments thathave imposed purchase taxes or restrictions is that this will stop price appreciation and leadto corrections that bring markets back in line with local demand. The research questionthen becomes what is the effect of these policies on housing markets.The contributions of this paper to understanding the effects of government actionsto calm housing market stem from both a better matching of data to the identificationstrategy and supply side estimation using data from local government land auctions. Incomparison with other work, we are able to execute difference-in-differences (DiD) tests ata fairly granular level of geography, obtaining identification from the differences in changesbetween different districts within a city. This allows us to circumvent better the bias problemsfrom non-random treatment, because of the endogeneity of housing market conditions andpolicy actions, that occur with the cross country or inter-city analyses of housing marketinterventions in the extant literature. We argue that any unobserved patterns correlatedwith selection are likely to be more acute across cities than within cities because the lattershare the same housing and labour markets. Our approach remains subject to problemswith non-random treatment and inter-group differences because the allocation of district totreatment (restrictions) or non-treatment (no restrictions) is tied to the area’s distance fromthe city centre. We believe this to be a less acute violation of DiD assumptions. As well,our findings survive a variety of robustness and falsification tests that support the causalitywe cite.The second aspect that sets this work apart from others in the area is that we are ableto test for supply effects.6 The land supply data yields results on local government anddeveloper behaviour that serve to assess the price and volume effects in the apartment unitmarket. By using data on land auctions we test whether developers reduced their bids for4Mufson, S. ”In China, fear of a real estate bubble.” Washington Post, Jan. 11, 2010.http://www.washingtonpost.com/wp-dyn/content/article/2010/01/10/AR2010011002767.html. And morerecently Balding, C. ”Why China Can’t Fix Its Housing Bubble.” ]Bloomberg Opinions, June 24, 2018.https://www.bloomberg.com/view/articles/2018-06-24/why-china-can-t-fix-its-housing-bubble.5Favilukis and Van Nieuwerburgh (2017) model a city housing market with local residents and non-resident investors, demonstrating the effects on prices and welfare loss from capital inflows when investorsneither occupy nor rent out the apartments they acquire.6We use buildable area = maximum allowed floor area ratio x land area as our quantity measure ofthe supply from a given land auction rather than land area as it better reflects the potential amount ofapartments that could result from the auctioned land.2land, consistent with an expectation of long-term decline in demand, or local governmentsreduced the volume of land and potential buildable floor area they introduced into themarket, in which case local policy objectives would match the national priorities. Bothallow us to ascertain more clearly whether the apartment market outcomes reflect changesin demand or whether supply side effects are also present.We find that quantity restrictions have substantial immediate effects on transaction vol-ume but no effect on residential property prices. In the six months following the introductionof quantity restrictions, transaction volumes in the districts within a city with purchase re-strictions fall over 40% relative to volumes in unrestricted districts. Over time this differencedeclines in magnitude, to 30% for a twelve month window and 24% for a two year window.In contrast, the difference in the change in house prices pre-and post-policy between thesetwo areas are not statistically different from zero over any period in our data. The resultsare robust across tests comparing districts as a whole and if we use a border discontinuityapproach and limit the sample to developments within a 3 km band on either side of the bor-der between restricted and unrestricted districts. Falsification tests on using placebo datesand district boundaries for timing and location yield null results, supporting the argumentthat the quantity restrictions were responsible for the differences in transactions volumes.In comparison to our results, studies using cross-city panels, find higher volume effects andthat residential real estate prices in cities with restrictions fall by over 10% when comparedwith cites without such restrictions.The land supply tests on land auction prices and volume show no statistically differentfrom zero differential changes in the number of land auctions, buildable area “supplied”, andthe winning bids in these auctions between purchase restricted and unrestricted districtsbetween the pre- and post-restriction windows. However, in the case of the buildable areaallowed, the point estimates suggest a large decline, but the standard errors are also quitelarge. The point estimates for the number of auctions, though, are quite low in magnitude inaddition to being not statistically different from zero, so the buildable area coefficient maybe the result of a random composition effect. Overall, developers did not change their bidsfor land in restricted districts post-policy introduction when compared with unrestricteddistricts, nor did local governments show any relative difference in the the number of sitesbrought to auction. This is consistent with no supply response to the purchase restrictions.The remainder of the paper is structured as follows. In Section 2 we provide a briefsummary of Chinese housing policies with a focus on the mix of measures introduced by theChinese government in 2010 and 2011 with the objective of cooling down Chinese residentialreal estate markets. This is followed in Section 3 with a review of the literature on policies to3slow housing markets, covering both macro-prudential regulation and quantity restrictions,both in China and elsewhere. In Section 4, we describe the data used here as well as theidentification strategy to test for effects. Finally, in Section 5 we present the results for priceand volume effects at different levels of geography along with falsification and placebo testsfor robustness. Section 6 concludes.2 Chinese Housing Market InterventionsThe introduction of measures to cool the Chinese housing market in 2010 and early 2011followed a period of intense growth in the Chinese housing market. In the wake of the worldfinancial crisis, China pursued a program of stimulus led by an almost $US 600 billion invest-ment program announced in Nov 20087. Some pointed to this stimulus and the associatedincrease in liquidity as driving the real estate boom: Wu et al. (2014) estimate real landprices in key Chinese cities rose by a factor of five between 2004 and 2012. Media reportsdescribe high investment flows with investors owning apartments as pure stores of wealth:some estimated up to 30 percent of new apartments being purchased and left vacant8. Theconditions of rapid price appreciation, surging investment volume, and high rates of newconstruction following the post crisis stimulus eventually led the Chinese central governmentto introduce measures intended to rein in the housing market. The State Council issued twodirectives, the “Ten National Rules” (effective on April 17, 2010) and the “Eight NationalRules” (effective on January 26, 2011). These included changes to Housing Provident Fund(HPF) underwriting to raise the minimum LTV with the level determined by unit size andthe quantity of units owned.9 Minimum down payments on loans from commercial bankswere increased by 10 to 20 percentage points, with higher levels for second homes, and insome cases no financing for a third home. Interest rates were also raised, with a minimumallowed rate of 1.1 times the “benchmark rate.” Finally, there were steps taken to limit in-vestment in residential real estate directly by restricting the number of properties a personcould purchase. While these were directives from the centre, the implementation decision7Reported in the New York Times, Nov 9, 2008 “China Unveils Sweeping Plan for Economy”,http://www.nytimes.com/2008/11/10/world/asia/10china.html8“China’s Looming Real-Estate Bubble; A massive Keynesian spending program has misallocated capitaland set the stage for a crisis.” Wall Street Journal (on-line), Aug. 20, 2010.9The Housing Provident Fund (HPF) is a mandatory savings plan for government, state owned enterprise,and some private business employees. Individual contributions are matched by employers with withdrawalslimited to purchase owner-occupied real estate. This is a buyer’s lowest cost financing, but the amountsare limited and typically need to be supplemented with bank financing. Studies and summaries of the HPFinclude Tang and Coulson (2017), Xu (2017), Yang and Chen (2014), Yeung and Howes (2006). An exampleof the change is that for units greater in size than 90 m2, the minimum down payment required for HPFfunds rose from 20 to 30%, and the minimum LTV for a second unit purchased from 40 to 50%.4was left to lower levels of government, where provincial governments forward the messagesfrom the central government to the municipal and lower level governments. It was then upto a local government’s discretion to customize these policies and determine the timelinebased on local economic conditions.The implementation of these policies had considerable variation by jurisdiction. First,even the financing policies, which were imposed in all cities varied by implementation date:May 1, 2010 in Beijing to March 31, 2011 in Hefei10 In contrast to the changes to LTV rulesand interest rates, purchase restrictions, which limited purchases based on hukou, a person’sofficial city residency status, were not uniformly imposed. For instance, Guangzhou allowedthose with hukou to purchase an additional unit, but forbid any purchases by non-residents;Shanghai allowed both to purchase just one additional unit; and many other cities limitedresidents to two units and non-residents to one. In addition, not all cities imposed purchaserestrictions, and some of those that did so did not impose them uniformly throughout all thedistricts in the municipality or county. It is the latter group, cities that imposed restrictionson some districts but not on others, that we use for our analysis. We exploit the differencesbetween these groups before and after the imposition of restrictions in a standard difference-in-differences (DiD) identification strategy.For reasons described below in the data section we use data from four cities: Chengdu,Guangzhou, Hefei, and Qingdao. These cities provide us with variation by city type, date ofimplementation of purchase restrictions, and within city geography. Guangzhou is a Tier 1city, the others are Tier 2. The municipal governments introduced the policies at differenttimes between October 2010 and March 2011. In all four cities there are at least two districtswithout quantity restrictions on resident and non-resident buyers. The details, introductiontiming, and district allocation of the quantity restriction for each city are provided in TableA-1 in the Appendices.3 Literature ReviewThe root concern of this paper is the effect of “external” capital flows to real estate. Favilukiset al. (2013) reviewed the literature on country level capital flows and house prices and didnot find clear evidence of a relationship in the extant literature at that time. Studies usingcross-country panels of capital flows (as measured by the current account deficit) and houseprices have been somewhat mixed. Aizenman and Jinjarak (2009) and Sa et al. (2011) find a10Our larger sample of cities is limited to 126 of the largest or economically important Chinese cities.These include all major cities and provincial capitals.5positive correlation between the capital account and house price inflation, but Jinjarak andSheffrin (2011) do not. In contrast, theoretical models of foreign demand (Chao and Yu,2015; Tai et al., 2017) or non-residents more generally (Favilukis and Van Nieuwerburgh,2017) demonstrate how these inflows into local housing markets worsen affordability.11Greater success in demonstrating the relationship between capital inflows and houseprice inflation has come using city level and within city data. Cvijanovic and Spaenjers (2015)study non-resident demand in Paris and find capital inflows concentrate in the most desirableneighbourhoods and affect prices there in particular, but also more generally. Using a panel ofUK local authorities, Sa (2016) links the share of transactions that are registered to overseascorporations to local house price appreciation. Badarinza and Ramadorai (2018) show theeffect of country risk driven capital flight on house prices is greater in London neighbourhoodspopulated by residents of those countries. Using differences across immigrant groups by visaclass, Pavlov and Somerville (2017) find that unlike other work, when immigrants comewith high net worth, neighbourhood house prices increase faster than in areas with newimmigrants more generally.The most direct antecedent for this paper is the Hilber and Schoni (2016) study ofSwiss restrictions on second home purchases. They assess the effects of the January 2013Swiss “Second Home Initiative” (SHI) that banned the construction of new second homesin Swiss municipalities where these homes made up more than 20% of the housing stock,which effectively meant construction bans in areas with high resort tourism.12 They use adifference-in-differences (DiD) methodology, comparing areas where the ban binds comparedto those where it does not. They find that the ban resulted in increases in the price ofsecond homes (less future supply) but lowered the prices of primary homes in affected areasby 12% (negative economic impact). Our paper is somewhat different. First, our constraintsoccur in urbanized areas, not the tourist areas as in their paper. Second, we obtain ouridentification from differences within cities, which better controls for the non-randomness ofomitted variable problem in DiD estimation. Finally, we are able to study both prices andmarket activity, rather than just prices alone, and differentiate between demand and supplyresponses.Our paper builds more generally on the literature that studies the effectiveness of macro-11In Chao and Yu (2015) the welfare implications depend on how taxes on foreign buyers are used, whilein Favilukis and Van Nieuwerburgh (2017) the results are sensitive to non-resident versus local preferencesfor location.12As Hilber and Schoni note, the jurisdictions with more homeowners, more second homes, that are closerto a ski resort were most opposed to the initiative, which had greater support in urban areas with morerenters.6prudential policies in addressing overheating in housing markets.13 The analysis in this areahas tended to use cross country panels (examples include Cerutti et al. (2017) and Zhangand Zoli (2016)), but some work has looked at within country variation, principally Iganand Kang (2011) study of differences across Korea in the intensity of loan to value and debtto income constraints for mortgage lending. These papers find effects of these policies onhousing market activity, but less so on prices. The specific type of intervention we study,however, does not operate via the credit channel, but are explicit regulations on the quantityof units that can be purchased by an individual or household. In this we add to a muchmore limited literature that seeks to measure the effects of these actions. Beyond Hilber andSchoni (2016) this work primarily uses Chinese data because the aforementioned variationin policies and implementation across Chinese cities offers richer identification than cross-country panels or individual country time series analysis.While the purchase restrictions introduced in China occurred in tandem with nationaland local macro-prudential policies, as a non-financial system instrument they are more adirect restraint on demand. In form, they share more in common with policies in othercountries that have attempted to reduce non-resident demand through taxation. Thesepurchase restrictions have been the subject of a number of papers. They almost all tend touse a panel of cities and a DiD methodology, comparing cities with and without restrictions,before and after the introduction of the restrictions. The challenge for these papers, is thenon-randomness in the application of the treatment, the introduction of restrictions acrosscities. Those that did are overwhelming the bigger, more economically, faster growing citiesin China.Though not an official hierarchy, Chinese cities are typically broken down into three tofour tiers, where the designation reflects a mixture of their economic and political impor-tance.14 Using YiCai Global’s Rising Lab recent 2017 breakdown, which has six tiers, all ofthe four Tier 1 cities (Beijing, Guangzhou, Shanghai, Shenzhen) had purchase restrictions,as did 13 of 15 Tier 1A cities (and the two that did not are outliers in size, Chongqing, ora questionable inclusion, Donguan), 27 of 30 Tier 2 cities had purchase restrictions, and it13In contrast to the traditional “micro-prudential” policies, which target individual financial institutionsas they experience financial stress, macro-prudential policies combat general equilibrium problems of overallfinancial system health through policies that affect lending policies, irrespective of the health of individuallender. Hanson et al. (2011), Galati and Moessner (2013), Jorda` et al. (2016), and Kahou and Lehard (2017)provide an overview of macro-prudential polices, their effectiveness, and a discussion of the different elementsof macro-prudential regulatory tools.14For a discussion of Chinese city tiers see https://www.chinacheckup.com/blogs/articles/china-city-tiers.Rankings are not entirely consistent, for instance comparing YiCai Rising Lab and the South China MorningPost, but consistently the largest 4-5 economies are in Tier 1 and the next group of major economic centresand leading provincial capitals are in the next lower tier.7is only with Tier 3 cities that there are a large number of cities without restrictions (10 of70 Tier 3 cities had purchase restrictions). Therefore, comparing cities with restrictions tothose without mixes differences in political sensitivity, wealth, and economic growth.A number of the inter-city panels analyses of the restrictions have used different strate-gies to deal with this identification problem. Cao et al. (2015) apply a DiD methodologyto a panel of 70 cities for which they have the National Bureau of Statistics data, of which39 imposed restrictions. To address the problem of city differences they include pre-trendvariables and follow two stage approach of Donald and Lang (2007) to the DiD estimation.They find purchase restrictions associated with a 18% decline in prices and a 60% decline insales volume in the four quarters following the introduction of purchase restriction policies inrestricted versus unrestricted cities. Yan and Ouyang (2018) use propensity score matchingto define a more limited, but better matching of treatment and control groups to address theproblem of unobserved differences across cities. They end up with four cities with restric-tions that are matched to four control cities based on per capita GDP and population. Theirregressions have limited explanatory power. However, the difference in mean differences ap-pears to be a 20% relative decline in the prices in restricted cities. Similarly, Du and Zhang(2015) construct a replica of Beijing based on smaller lower status cities that did not adoptpurchase restrictions during the period May 2010 and Nov 2011. They compare Beijing priceappreciation with its replica and find that price appreciation in Beijing was 7.5 percentagepoints lower than predicted by the replica after the introduction of the restrictions.Unlike the inter-city analysis in other papers, Sun et al. (2017), estimate the effects ofpurchase restrictions in a single city, Beijing. Beijing has a large number of households in thehousing market that lack official residency status, so the strict restrictions on non-residents’purchases might be expected to have an acute effect. They use a regression discontinuitydesign to identify the existence of a structural break associated with the introduction ofpurchase restrictions on a variety of real estate market variables. They are not able toisolate the effect of purchase restrictions from other policies introduced at the same time,but they find a combined effect of a 23% decline in house prices post policy constraints.They too find larger effects on volume: a 51-77% reduction.Li et al. (2017) use a non-parametric approach that is data driven around the pattern ofmonthly growth rates in prices. They essentially test for the extent to which price movementsimmediately following the introduction of purchase restrictions deviates from the overallpattern of price movements. They break their analysis into groups by unit size. While theyfind some evidence that the restrictions slow housing price appreciation, it is less effectivefor larger units and for situations where rates of house price appreciation are particularly8high.15The papers cited above rely on a variety of specification techniques to overcome thechallenge of non-randomness in the application of restrictions. Methodologically, the con-tribution of this paper is that we use detailed data that provide housing market measuresat the project level. This allows us to take advantage of the differences in the imposition ofpurchase restrictions within cities. We argue that because the treatment and non-treatmentareas share the same general housing and labour markets and are the same local economy.We have treatment and control groups (different districts within a single city) that are muchmore similar in conditions than is the case in the existing research.The second part of our paper is an analysis of the effects of the restrictions on landsales by local governments to developers. This provides us with an indirect method to assessthe effects of the restrictions on the supply function. We know of no other analyses of thesetypes of restrictions on investor demand for residential real estate that address supply-sidefactors.4 Data and Identification4.1 DataThe data used in the analysis are from the Chinese Real Estate Index System (CREIS).CREIS records housing transaction data in China from information published by the central,provincial and local governments on a weekly or monthly basis. Transactions data arereported at the city, project, and deeds levels, where the first two are aggregate data and thelast are individual transactions. We use monthly project level aggregate data from CREIS.The data cover 49,525 projects in 126 cities from as early as 2005. However, we are interestedin the variation in purchase restrictions within a city by district limits, which limits us tonine of the cities in these data. And of these nine cities, we have sufficient pre-2011 data foronly four of them as prior to 2011 the CREIS data is very sparse, with no observations formost cities, especially for the deeds data. We are left with data of 2,014 projects in Chengdu,Guangzhou, Hefei, and Qingdao. Though we have fewer cities in the data, the key advantageof using within city variation is that it reduces the scope of the treatment from across very15There is also a literature in Chinese academic journals that studies the policies that we test. Liu (2013)and Wang and Huang (2014) establish different equilibrium models to gauge the effect of the purchaserestriction policy. Liu (2013) states that the direction of the housing price movement is unclear given thedifferent conditions. Wang and Huang (2014) suggest that the purchase quota policy may reduce housingprices, but at an insignificant magnitude.9different cities to within cities. Still, it does not fully solve the randomness problem as in thecities in our sample core urban districts have restrictions while more suburban ones do not.As we describe below we take steps to address these differences and validate our findings.The particular observations dates we use vary by city because the purchase restrictionswere introduced on different dates in the four cities. Guangzhou introduced policies onOctober 15, 2010; Qingdao on January 31, 2011; policies were implemented in Chengduon February 15, 2011; and on March 31, 2011 in Hefei. For project transaction volumes,we have observations from Oct 2009 on for all districts, but only from six months prior tothe restriction introduction for prices. We drop October 2010 for Guangzhou and February2010 for Chengdu from the data because the policies were implemented mid-month and weonly have monthly aggregations. In the basic set of regressions we will use a six monthpre-restriction window (before) and then either six or twelve month post-restriction window(after).Following the directives from the central government, these municipalities imposed re-strictions on the more central and core urban districts. Buyers of properties in more distantsuburban districts were not subject to the purchase restrictions. Figure 1 shows the distri-bution of projects across city districts for the four cities, differentiating between purchaserestricted and unrestricted districts. In contrast, the changes in housing finance rules, bothhigher interest rates, down payment requirements, and limits on HPF loans applied in allareas.[Figure 1 Inserted Here]In the data, each observation is a project’s summary statistics for a given month. Ofthese, we we use the average unit price (Chinese Yuan per square meter (m2)), total units soldin the project that month, and average unit size (m2)). We provide these summary statisticsfor the project aggregates in the four cities in Table 1 for the - 6 month / + 12 monthwindow. The data are broken down between purchase restricted and unrestricted districts,and for periods before and after the imposition of the restrictions. mean monthly salesvolumes per project are lower in the core-area restricted districts than in the unrestricteddistricts. Consistent with urban models, prices are higher and average unit sizes are lowerin more central restricted districts than in the unrestricted suburban districts both beforeand after the implementation of restrictions. Unit prices rise in both types of districtsafter the imposition of purchase restrictions, and sales volumes fall in both district types.The latter finding is consistent with the a decline in demand following the introduction oflending restrictions, higher interest rates, and higher down payment requirements that affect10all districts in these cities and were introduced at approximately the same time. However,the rise in prices over the period is not consistent with that explanation. We provide similardescriptive statistics by city in Appendix Table A-2. The patterns in each city are similarto those in the aggregate data shown in Table 1.[Table 1 Inserted Here]CREIS also complies land transaction information in China from information publishedby the central, provincial, and local governments on individual land auctions. The datasetincludes detailed land characteristics, such as transaction price, transaction date, listing date,reserve price of an auction, size and location of land parcel, maximum building area per unitof land or floor space ratio (FSR), land type (residential, commercial, industrial, mixed, andothers), transaction type (negotiation [xieyi ], English auction[paimai ], two-stage auction[guapai ], and sealed bid auction[zhaobiao]), and buyer name (both firm and individual). Welimit the data to residential land sales in the four cites used above. The summary statisticsfor Chengdu, Guangzhou, Hefei, and Qingdao for price and quantity measures are reportedin Table 2. As with unit sales, land prices are higher in the core restricted districts andprices rise in both regions over the period. Average land area and buildable area per landauction are lower in both regions post-restrictions. After is twelve months and before is sixmonths, so the number of auctions does decline in both areas. These are broken down bycity in Appendix Table A-3.[Table 2 Inserted Here]4.2 SpecificationIf the Chinese government interventions were successful, then we would expect to see botha decline in transaction volume as investors reduced purchases, and a decline in prices inresponse to the rightward shift in demand. We hope to exploit within market differences,where the restrictions in some areas result in a drop in demand in those areas, when comparedwith areas in the city that did not restrict demand. Between the pre- and post-restrictionperiods, the areas with restriction should have relative declines in both prices and volumes.The price effect, though depends, on the extent of downward price rigidity. In particular,if developers are not under pressure from lenders to liquidate unsold properties, and theybelieve that restrictions are temporary, it may be more profitable to not reduce prices andwait out the decline in demand.We use two different regression specifications for the DiD analysis. The first is the11standard treatment where we have a dummy variable Aftert that takes on the value of onein the months after the introduction of purchase restrictions. Projects in districts wherepurchase restrictions are or will be imposed have the value of one for the dummy variableTreati. The DiD effect is captured in the interaction of these two in Treati ∗ Aftert.Formally:yi,t = α + β1 ∗ Treati ∗ Aftert + β2 ∗ Aftert + β3 ∗Xi,t + µi + δt + i,t (1)where yi,t is one of the outcome variables (price or transactions) for project i in year-month t.Xi,t are other time and project specific control variables. µi refers to the project fixed effects,capturing the unobserved mean variations across projects. δt is the set of year-month fixedeffects. The estimated coefficient of interest for the DiD effect is β1. The dummy variableTreati does not enter on its own because it is subsumed in the project fixed effects µi. Policyimplementation dates vary, so Aftert is not perfectly co-linear with the year-month fixedeffects δt.We use two alternative specifications. Both address the effects the innate differencesbetween the treatment and non-treatment districts might have on the DiD coefficients ofinterest in ways not covered by Specification (1), which assumes no systematic time-varyingpre-treatment differences.The first allows for non-parallel trends in the data in the period prior to the treatment(introduction of restrictions). We do by allowing the the pre-treatment (months beforepurchase restrictions were applied) mean effect for the projects in districts where there willbe restrictions to vary from that of the non-treatment districts. Formally, we interact Treati(the treatment fixed effect) with Before′′t , which has the value of one for the second threemonths of the six month pre-restriction period and zero otherwise. Other elements are similarto specification (1):yi,t = α + β1 ∗ Treati ∗Before′′t + β2 ∗ Treati ∗ Aftert + β3 ∗ Aftert+β4 ∗Xi,t + µi + δt + i,t(2)Here β1 will show the sign and statistical significance of a pre-treatment trend difference forprojects in districts with purchase restrictions that would cause specification (1) to violatethe no parallel trends assumption. The estimated coefficient of interest for the DiD effect isβ2. The magnitude of the difference is the difference between β2 and β1.12The second alternative imposes more functional form for trend differences in the de-pendent variable before and after the introduction in restrictions across the two groups ofdistricts. Here we allow for different trends between the restricted and non-restricted areas,through Trend and Treat ∗ Trend, and then the difference in differences above and beyondthis through a third interaction Treat ∗ Trend ∗ After. The full specification is:yi,t = α + β1 ∗ Trend+ β2 ∗ Treati ∗ Trend+ β3 ∗ Treati ∗ Trend ∗ Aftert+β4 ∗ Aftert + β5 ∗Xi,t + µi + λmonth + i,t(3)The variables have the same meaning as noted above except that λmonth is a month fixedeffect for seasonality. The sign of the DiD effect is captured by β3 There is not a simpleparameter or combinations of parameters to identify the magnitude of the effects of therestrictions because they depends the values for Trend. We will estimate the changes foreach of the windows using the mid-trend value for each before and after window period. Aswith the two previous specifications stand alone values for Treat are subsumed in the projectfixed effects.5 Results5.1 Apartment SalesThese empirical estimates of the relative effect of purchase restrictions use monthly residentialdevelopment project level data for prices and sales volumes of apartment unit sales by month.In Table 3, we test the difference in individual development project mean log apartmentprices per m2 of floor area across districts before and after the introduction of purchaserestrictions. All else being equal, one would expect higher demand in unrestricted areas asinvestors shifted their purchases their from districts where they were constrained on howmany apartments they could buy. If the restrictions diverted demand from one region tothe other, then with any inelasticity in supply we would expect to see prices rise in theunrestricted areas relative to the districts with purchase restrictions.All regressions in Table 3 use a six-month pre-treatment window, which varies slightlyby city.16 The first three regressions use a six-month post-purchase restriction policy imple-16Purchase restriction introduction dates are: October 15, 2010 for Guangzhou, January 31, 2011 forQingdao, February 15, 2011 for Chengdu, and March 31, 2011 for Hefei. We drop the October 2010 observa-tion for Guangzhou and the February 2011 observation for Chengdu to keep clean pre- and post-restriction13mentation after window; the second three use a twelve-month post window. Within eachwindow length group, the regressions are ordered by specification. We follow this presen-tation structure in subsequent tables, though the post window lengths do vary for sometables.The DiD effect for specifications (1) and (2) is the coefficient on Treat ∗ After. Forspecification (3) it is the estimated coefficient on Treat ∗ Trend ∗After. The calculation ofthe magnitude of the effects varies by specification. For specification (1) it is the estimatedcoefficient on Treati ∗ Aftert; for specification (2) the difference between Treati ∗ Aftertand Treati ∗ Before′′t ; and for specification (3) specific trend start and end values appliedto the benchmark pre- and post-periods and then multiplied by Trendt, Treati ∗ Trend)t,and Treati ∗Trend)t∗Aftert.17. There is no statistically significant difference in the changein prices post-restriction implementation date between development projects in regions withpurchase restrictions and those without. The effects are also small in magnitude, rangingfrom 1.0 to 3.4% across specifications.[Table 3 Inserted Here]There remains the possibility that prices are just slow to adjust. In Table 4 we extendthe post-restriction introduction windows to eighteen and twenty four month post windows.Here too the effects are all statistically not different from zero, with standard errors largerthan the point estimates on the relevant variables. The estimates are also extremely smallin magnitude. In the absence of perfectly elastic supply, this suggests either no difference indemand, or strongly downward sticky prices in the restricted districts.[Table 4 Inserted Here]In contrast to the effect on prices, there are qualitatively large and statistically differentfrom zero effects of the purchase restrictions on differences in transaction volumes acrossthe two types of districts. Table 5 shows transaction volumes drop off much more after theintroduction of restrictions in projects in the districts with purchase restrictions than in thosewithout: falling by 42-51% in the six month window. As the analysis window lengthens, thesize of the effect declines, to a 30-36% decline for the twelve month window. These changesare statistically different from zero across all three specifications. Table 6 shows the resultsfor longer windows, where the effects are lower still. Though the price regressions did notsuggest a differential effect from the presence of restrictions, the effect is very strong andintroduction date sub-samples.17We use window mid-point trend values, where Trend=1 for Oct 2008. For + 6 month the values are 25and 31; for +/- 12 months they are 25 and 37. Strictly we calculate the trend effect pre and post for bothgroups and take the difference in the differences.14clear on the volume of property purchases. This suggests that the absence of a price effectis likely because of downward sticky prices or a significant inward shift in supply, given thestatistically significant and meaningful relative decline in transaction volume in the restricteddistricts.[Table 5 Inserted Here][Table 6 Inserted Here]To test for robustness beyond different specifications, we conduct border discontinuityregressions using the DiD methodology. Here we limit the sample to projects within 3kmof the border between districts where purchase restrictions are imposed and those wherethey are not. While the districts are different, this should reduce the variation in unob-served location characteristics between projects in the restricted vs. unrestricted districtsby excluding those that are particularly close (in the restricted districts) or far away (in theunrestricted districts) from the urban centre. The effect of limiting the analysis to projectson the border is that we should exclude the highest priced, most desirable, core urban areas,and least expensive, least desirable suburban districts, which we assume are most likely tobe fundamentally different, from the analysis. We show the included areas and projects oneither side of the border in Figure 3. Descriptive statistics mimicking those in Table 1 forprojects in the 3km band on either side of the border are shown in Appendix Table A-4,where we see a similar pattern to the district-wide statistics in Table 1.[Figure 3 Inserted Here]In Tables 7 and 8 we present the same regressions as those shown in Tables 3 and 5 butusing the more focused border discontinuity sample. The differences between the border andentire district samples vary slightly by specification, but the patterns and general magnitudesare consistent across both samples. The overall results for prices are again qualitativelysmall and not statistically different from zero. For decreases in transactions between therestriction and non-restriction districts we get large and statistically different from zerodeclines in relative transaction volume in the restricted zone. The six month window effectsare a bit larger than in the district analysis, with declines all approximately 48-51% acrossspecifications, falling to declines of 31-37% for the twelve month windows. Longer windowsyield consistent results with smaller aggregate declines in volume with window length, aswith the district regressions above.[Table 7 Inserted Here]15[Table 8 Inserted Here]In all these regressions using specification (2), for both prices and volumes, we regularlyreject a unique pre-trend for districts where subsequently the municipal government will im-pose purchase restrictions. The coefficient β4 on Treati ∗ Before′t identifies the percentagemean difference between prices or transaction volumes for projects in the districts that havepurchase restrictions imposed 3-6 months vs. 0-3 months prior to the restriction implemen-tation. This estimated coefficient is never statistically different from zero and is typicallysmall in magnitude. As a result, in subsequent apartment sales tables we will just presentspecification (1), for the land sales data we will re-test these three specifications.5.2 Falsification TestsTo test for possible spurious results in either geography or time, we conduct two falsificationtests. The first is a border discontinuity DiD placebo test where we create an artificialdistrict boundary within districts without purchase restrictions. This addresses whether thedifference we see in the DiD regressions above reflects purchase restrictions or just a moregeneral effect related to distance from the city centre, since the purchase restricted areasare closest to the urban core. For instance, the higher down payment requirements from themacro-prudential policies introduced during the same time period as the purchase restrictionscould depress demand more for higher priced properties, which are more likely to be locatedin purchase restriction, urban core areas. If price falls continuously with distance, then thiswould show up again in this placebo test. The second placebo test examines whether theDiD effects above just reflects more general time patterns, either as part of the real estatecycle or resulting from the broader macro-prudential restrictions on housing finance, thataffected districts deferentially. We proxy the introduction of the purchase restrictions asoccurring separately as prior and subsequent to when they actually occurred, and have bothpre- and post- periods lie entirely in the period either prior or post to the actual introductionof restrictions.The geographic tests create a placebo purchase restriction and 3km band in districtsthat do not actually have restrictions. One half of this band lies 0-3km from the border withthe actual purchase restriction districts but is entirely in non-restricted districts. This iscompared with the second half of the band that lies 3-6km from the border. The falsificationtest is that demand fell more for more expensive areas, as defined by proximity to, so weassign the placebo treatment effect to the 0-3 km band area, which is closer to the city centre.Table 9 show the results of this geographic falsification test for specification (1). There is16no statistically significant difference in the changes in prices or transaction volume betweenthe two areas pre-and post-restriction dates. As well, the point estimates are small. This isconsistent with the results we present above being because of the difference in restrictionsacross districts and not differences in proximity to the city centre.[Table 9 Inserted Here]The time falsification tests are presented in Table 10 again just using specification(1). Because of limited price data more than six months prior to the restriction impositiondates we are constrained to testing transaction volumes alone. However, we only obtainedstatistically different from zero results for volume. Regressions (1) and (2) have a placeborestriction assigned to a period prior to the actual restrictions: 0-6 months prior for regression(1) and 0-10 months for regression (2), where both pre-and post-restriction periods occurbefore the actual introduction of restriction. For regressions (3)-(5) both periods occurafter the actual introduction, so the placebo is assigning a no-treatment where one actuallyexisted. Within these groups, the regressions differ by window length. The results areconsistent: the estimated coefficient on the interaction Treati ∗ Aftert is consistently notstatistically different from zero. Hence, no differences in transaction volumes over the periodbetween the placebo and time period correct samples.[Table 10 Inserted Here]5.3 Land Supply - Government AuctionsThe analysis in the previous section evaluates the outcomes in the market for completedapartment (condominium) units. We cannot necessarily distinguish what part of the identi-fied changes comes from the effect on investor demand because of purchase restrictions, andwhat may come from a supply response. For instance, the observed drop in volume withouta decline in prices is consistent with a shift inwards in both demand and supply curves. Itis also consistent with a drop in demand but no drop in developer reservation price, becausethe profit maximizing strategy is to wait until the policies are reversed rather than sell at adiscount.To shed light on supply side effects, we perform the same DiD tests on the land supplymarket. In Chinese cities, local governments determine land supply through the auctionof lands they designate as available to developers, which is an important source of local17government revenue. With these auctions, the short-run quantity effects should reflect localgovernments’ decisions to bring land to the market, while price effects are determined bythe bids of developers, given the current and expected future supply of land and expectedconditions in the apartment market when they expect to sell units developed on the landup for auction. Thus, we interpret the quantity effects, number of land auctions and totalbuildable area, as reflecting government land supply, and the price effects developer demandgiven this supply.18 No decline in land supply, but a decline in prices suggests that there isan inward shift in developer supply. But if land auction bids do not decline, that is moreconsistent with the developers waiting out the policy without lower prices.Estimates of the differential effect of purchase restrictions on the price bid for land inrestricted and unrestricted districts rice effects in the land auctions are shown in Table 11.The dependent variable is the log of price paid for land per buildable m2, the land componentof potential buildable area. The coefficients on the DiD measures are not statistically differentfrom zero, rejecting the hypothesis that land auction prices changed deferentially in responseto the variation in purchase restriction on apartment buyers. The point estimates suggest amoderate decline of between 2 and 11%, but the standard errors are quite large to have anyconfidence in these magnitudes or price direction. The results imply that given the supplyof land for development, developers did not lower their bids more, or raise them less, in thedistricts with restrictions. This has two possible explanations, either the supply of auctionsdropped enough to keep prices stable or developers were confident that there would not bea major long term effect on profitability from the purchase restrictions, as land bids reflectsales of units at least two years further on in the development process.[Table 11 Inserted Here]To test for land supply effects by local governments we test two different measures ofquantity in land supply. The first is the number of land auctions that occurred, the secondis the total buildable area that could result from development on the auctioned land. Thenumber of auctions are aggregate counts per district-month, the totals in a district in agiven month, so our observation count is much lower than in the other analyses here. Forbuildable area per auction we use individual land auctions as the unit of observation andare assessing the variation over time and across districts in the amount of buildable areaoffered in any given land auction. Table 12 shows the relative change in the number ofland auctions between restricted and unrestricted districts over the period before and afterthe implementation of the purchase restrictions. There is no apparent change, the raw18Total potential supply of apartment space in the auctioned land is calculated as the total auction landarea times the maximum allowed floor space ratio (FSR), which is the built area to land area ratio used inland use regulations.18magnitudes of the point estimates are all below a 4% change and the standard errors arelarge relative to the point estimates. Table 13 presents the building area regressions. Heretoo, we cannot reject that buildable area per auction did not decline in restricted areas,compared with non-restricted areas, following the restrictions. However, the point estimatesof declines are large in magnitude, though offset by the very sizable standard errors. 19[Table 12 Inserted Here][Table 13 Inserted Here]The land supply regressions do not indicate a inward shift in supply in response tothe purchase restrictions. Land prices, the number of parcels auctioned, and the buildablepotential did not change in any differential way between districts with restrictions and thosewithout. This pattern is consistent with developers who see the government policies astemporary, to be reversed after some period. As a result, with no drop in the offered land inrestricted areas compared to unrestricted areas they did not have differential changes in bids.Such a response is also consistent with prices of their completed units remaining unchangedin the face of less buyer demand.6 ConclusionIn this paper, we look at the effects of restrictions on investor purchases of residential prop-erties on housing market outcomes. These restrictions were introduced in China, and else-where more typically as differential taxes, to try to calm overheated housing markets addressworsening affordability. Here we try to measure the effectiveness of the Chinese policies atachieving these objectives. While others have studied China’s restrictions policy, they haverelied on cross-city panels using a methodology that assumes policy treatment is random.Where we differ is that we exploit variation in the implementation of these policies withincities, which represents a step forward towards a cleaner test. While we do not fully es-cape the non-randomness problem, because restrictions are imposed in central districts andnot in suburban districts, our results are consistent with both robustness and falsificationtests. Additionally, we use data from government land auctions to compare outcome sin theend-user apartment market with conditions in the land input market. These comparisonsindicate that our observed results come from the shift in demand by apartment purchasersand not be changes in developer or government land seller actions.19Falsification tests like those applied to the project data and presented in Tables 9 and 10 do not yieldany statistically different from zero results.19Uniformly we find that districts within a city where there were restrictions on purchasesof apartments had significantly greater declines in transaction volume than did districtswithout these restrictions following their introduction. At the same time, there were nodifferential changes in transaction prices. The declines ere large, in excess of 40% in the firstsix months following the implementation of restrictions, but this declined to less than 30%after twelve months. The supply regressions also show no differential decline in land bidsand or in the number of land auctions over this period across the restricted and unrestricteddistricts of the four cities we study. Together this suggests that while buyers were affectedby the restrictions, developers did not drop prices and behaved in a manner consistent withan expectation that the restrictions were temporary and waiting to sell was more profitablethan dropping prices.Using our within-city sample we get different results than researchers who have studiedthese restrictions across cities. Our decline in volumes is at least 10 percentage points lower,and most striking, while they find price declines in cities with restrictions of up to 16%compared to those without, we find find no differential change in prices across districts.While the difference in differences methodology this is particularly not well suited to explainaggregate changes, this is especially true for this period in China when macro-prudentialpolicies that limited mortgage borrowing were also imposed across all principal cities.The stated objective of the restrictive policies was to tame high and accelerating houseprices and calm markets. We find little evidence on reversing housing price inflation, thoughmarket activity clearly declined. In this, the purchase restrictions are both consistent withthe contention that housing markets clear in both volume and prices, not just prices (Claytonet al., 2010; Stein, 1995), but importantly with the research on macro-prudential policiestghat finds that these too can have strong dampening effects on market activity but theirability to reverse problems of high house prices and address affordability are limited at best.20ReferencesAizenman, J. and Y. Jinjarak (2009). Current account patterns and national real estate markets. Journalof Urban Economics 66 (2), 1–13.Badarinza, C. and T. Ramadorai (2018). Home away from home? foreign demand and london house prices.Journal of Financial Economics On-line https://doi.org/10.1016/j.jfineco.2018.07.010.Cao, J., B. Huang, and R. N. Lai (2015). On the effectiveness of housing purchase restriction policy in china:a difference in difference approach. Working Paper .Cerutti, E., S. Claessens, and L. Laeven (2017). 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Mandatory savings, credit access and home ownership: The case of the housing providentfund. Urban Studies 54 (15), 3446–3463.Yan, Y. and H. Ouyang (2018). Effects of house-sale restrictions in china: a difference-in-difference approach.Applied Economics Letters 25 (15), 1051–1057.Yang, Z. and J. Chen (2014). Housing reform and the housing market in urban china. In Housing Affordabilityand Housing Policy in Urban China, pp. 15–43. Springer.Yeung, S. C. and R. Howes (2006). The role of the housing provident fund in financing affordable housingdevelopment in china. Habitat International 30 (2), 343–356.Zhang, L. and E. Zoli (2016). Leaning against the wind: Macroprudential policy in asia. Journal of AsianEconomics 42, 33–52.22Figure 1: Purchase Restriction by District and Geographic Distribution of Housing ProjectsNotes: This figure presents the the geographical distribution of housing projects across city districts for the four cities. The areas ofshaded regions correspond to the districts subject to the purchase restrictions. The dots in red represent the housing projects.23Figure 2: Purchase Restriction by District and Geographic Distribution of Transacted Land ParcelsNotes: This figure presents the the geographical distribution of transacted land parcels across city districts for the four cities. The areasof shaded regions correspond to the districts subject to the purchase restrictions. The dots in navy represent the housing projects.24Figure 3: 3 KM Border Analysis and Geographic Distribution of Housing ProjectsNotes: This figure shows the geographic distribution of housing projects within 3km of the border between districts with and withoutthe restrictions in each city. The dots in red denote housing projects located in the restricted districts and the triangles in blue representhousing projects located in the unrestricted districts.25Table 1: Summary Statistics - Housing Projects (-6/+12 months)Before Restriction After RestrictionMean S.D Mean S.DPanel A: All DistrictsAvg. Price/m2 8,200.41 5,219.12 9,356.20 6,478.49Total Transactions 40.26 63.34 25.98 46.81Avg. Unit Size(m2) 110.69 47.53 106.65 47.36Observations 3,303 7,465Panel B: Restricted DistrictsAvg. Price/m2 9,378.54 5,720.57 11,257.92 7,393.86Total Transactions 37.92 62.95 22.90 44.90Avg. Unit Size(m2) 106.99 45.85 103.37 45.35Observations 2,296 4,563Panel C: Unrestricted DistrictsAvg. Price/m2 5,514.23 2,088.27 6,366.01 2,717.28Total Transactions 45.59 63.95 30.81 49.28Avg. Unit Size(m2) 119.12 50.16 111.81 49.94Observations 1,007 2,902Notes: This table reports the project aggregates in four cities (Chengdu, Guangzhou, Hefei, andQingdao). The data are broken down between purchase restricted and unrestricted districts, andfor 6 months before and 12 months after the imposition of the restrictions.26Table 2: Summary Statistics: Land Auctions (-6/+12 months)Before Restriction After RestrictionMean S.D Mean S.DPanel A: All DistrictsAvg. Price/m2 of Buildable 1,636.91 1,964.69 1,654.94 4,042.24Land Area 46,481.29 46,070.92 39,918.21 40,160.87Buildable Area 110,199.19 137,017.04 98,243.17 121,477.48Distance to CBD 31.89 22.26 32.07 21.58Auction Type 0.51 0.50 0.49 0.50FSR 2.43 1.39 2.42 1.41Observations 413 537Panel B: Restricted DistrictsAvg. Price/m2 of Buildable 2,765.66 2,217.75 2,758.29 6,659.87Land Area 45,703.78 46,786.53 40,001.56 41,512.22Buildable Area 126,513.11 169,296.45 91,087.20 88,064.52Distance to CBD 22.22 12.31 26.49 15.84Auction Type 0.45 0.50 0.50 0.50FSR 2.93 1.53 2.63 1.42Observations 119 182Panel C: Unrestricted DistrictsAvg. Price/m2 of Buildable 1,180.04 1,649.26 1,089.28 1,056.17Land Area 46,796.00 45,854.86 39,875.47 39,509.68Buildable Area 103,595.93 121,259.45 101,911.86 135,419.57Distance to CBD 35.81 24.13 34.93 23.51Auction Type 0.53 0.50 0.49 0.50FSR 2.23 1.27 2.32 1.40Observations 294 355Notes: This table reports the district-month level summary statistics for land transactions indistricts with and without the purchase restrictions in four cities (Chengdu, Guangzhou, Hefei, andQingdao), 6 months before and 12 months after the implementation of the restrictions.27Table 3: District Level DiD - PricesDependent Variable ln(average transaction price)Time Window -6m to 6m -6m to 12mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before 0.009 0.016(0.016) (0.017)Treat*After 0.010 0.017 0.018 0.034(0.024) (0.026) (0.026) (0.029)Treat*Trend -0.002 0.003(0.004) (0.003)Treat*Trend*After 0.001 -0.000(0.001) (0.001)After 0.002 -0.002 0.011 0.047**(0.023) (0.019) (0.023) (0.020)Trend 0.015*** 0.007***(0.003) (0.002)ln(size) 0.039 0.039 0.039 0.081* 0.081* 0.083*(0.055) (0.055) (0.055) (0.045) (0.045) (0.045)Constant 8.653*** 8.654*** 8.363*** 8.461*** 8.465*** 8.263***(0.254) (0.254) (0.260) (0.206) (0.205) (0.221)Observations 6,779 6,779 6,779 10,768 10,768 10,768R-squared 0.883 0.883 0.883 0.849 0.849 0.848Year-Month FE Yes Yes No Yes Yes NoProject FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table shows the difference in individual development project mean log apartment prices per square meter across districts6 months before and 6-12 months after the introduction of purchase restrictions. Trend starts at 1 for Oct 2008. Standard errors areclustered at the district level and are shown in parentheses under the estimated coefficients. We use ***, **, and * to denote significanceat the 1%, 5%, and 10% level, respectively.28Table 4: District DiD with Longer Windows - PricesDependent Variable ln(average transaction price)Time Window -6m to 18m -6m to 24mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before 0.009 0.002(0.016) (0.017)Treat*After 0.009 0.020 0.013 0.003(0.027) (0.028) (0.030) (0.029)Treat*Trend 0.000 0.002(0.003) (0.002)Treat*Trend*After 0.000 -0.001(0.001) (0.001)After 0.011 0.126*** -0.032 0.152***(0.028) (0.022) (0.031) (0.022)Trend 0.000 -0.003**(0.002) (0.001)ln(size) 0.039 0.039 0.034 0.074* 0.074* 0.066(0.035) (0.035) (0.036) (0.042) (0.042) (0.043)Constant 8.639*** 8.640*** 8.741*** 8.442*** 8.446*** 8.622***(0.163) (0.162) (0.163) (0.197) (0.195) (0.186)Observations 14,805 14,805 14,805 20,388 20,388 20,388R-squared 0.837 0.837 0.835 0.833 0.833 0.830Year-Month FE Yes Yes No Yes Yes NoProject FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table shows the difference in individual development project mean log apartment prices per square meter across districts6 months before and 18-24 months after the introduction of purchase restrictions. Trend starts at 1 for Oct 2008. Standard errors areclustered at the district level and are shown in parentheses under the estimated coefficients. We use ***, **, and * to denote significanceat the 1%, 5%, and 10% level, respectively.29Table 5: District Level DiD - TransactionsDependent Variable ln(number of transactions)Time Window -6m to 6m -6m to 12mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before -0.108 -0.070(0.083) (0.087)Treat*After -0.423*** -0.618*** -0.299*** -0.431***(0.102) (0.090) (0.095) (0.093)Treat*Trend -0.005 0.049***(0.024) (0.017)Treat*Trend*After -0.012* -0.022***(0.007) (0.006)After -0.286* -0.534*** -0.217* -0.070(0.146) (0.168) (0.120) (0.143)Trend 0.016 -0.068***(0.017) (0.011)Constant 3.144*** 3.170*** 2.561*** 3.361*** 3.366*** 3.800***(0.139) (0.148) (0.373) (0.145) (0.154) (0.258)Observations 6,779 6,779 6,779 10,768 10,768 10,768R-squared 0.666 0.666 0.655 0.619 0.618 0.606Year-Month FE Yes Yes No Yes Yes NoProject FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table shows the difference in individual development project mean log transaction volume across districts 6 months beforeand 6-12 months after the introduction of purchase restrictions. Trend starts at 1 for Oct 2008. Standard errors are clustered at thedistrict level and are shown in parentheses under the estimated coefficients. We use ***, **, and * to denote significance at the 1%, 5%,and 10% level, respectively.30Table 6: District DiD with Longer Windows - TransactionsDependent Variable ln(number of transactions)Time Window -6m to 18m -6m to 24mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before -0.065 -0.079(0.090) (0.092)Treat*After -0.283*** -0.382*** -0.243** -0.385***(0.098) (0.102) (0.094) (0.108)Treat*Trend 0.025* 0.018*(0.015) (0.010)Treat*Trend*After -0.016*** -0.012**(0.006) (0.005)After -0.144 -0.300** -0.236* -0.688***(0.117) (0.144) (0.120) (0.108)Trend -0.023** -0.007(0.009) (0.006)Constant 3.409*** 3.401*** 3.280*** 3.372*** 3.359*** 2.951***(0.153) (0.161) (0.206) (0.160) (0.169) (0.127)Observations 14,805 14,805 14,805 20,388 20,388 20,388R-squared 0.588 0.588 0.568 0.551 0.550 0.535Year-Month FE Yes Yes No Yes Yes NoProject FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table shows the difference in individual development project mean log transaction volume across districts 6 months beforeand 18-24 months after the introduction of purchase restrictions. Trend starts at 1 for Oct 2008. Standard errors are clustered at thedistrict level and are shown in parentheses under the estimated coefficients. We use ***, **, and * to denote significance at the 1%, 5%,and 10% level, respectively.31Table 7: 3km Border Band DiD - PricesDependent Variable ln(average transaction price)Time Window -6m to 6m -6m to 12mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before -0.001 0.014(0.020) (0.023)Treat*After 0.003 0.012 0.017 0.035(0.022) (0.028) (0.023) (0.029)Treat*Trend -0.004 0.004(0.004) (0.004)Treat*Trend*After 0.001 -0.001(0.001) (0.001)After 0.036 0.020 0.040 0.077***(0.027) (0.030) (0.025) (0.028)Trend 0.013*** 0.005*(0.003) (0.003)ln(size) 0.017 0.016 0.018 0.067 0.066 0.067(0.063) (0.062) (0.063) (0.053) (0.053) (0.052)Constant 8.755*** 8.748*** 8.517*** 8.585*** 8.586*** 8.372***(0.292) (0.293) (0.290) (0.247) (0.248) (0.261)Observations 4,431 4,431 4,431 7,130 7,130 7,130R-squared 0.855 0.855 0.855 0.811 0.811 0.811Year-Month FE Yes Yes No Yes Yes NoProject FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table presents the same regression as those shown in Table 3, using a sample that contains projects within 3km of theborder between districts where purchase restrictions are imposed and those where they are not. The dependent variable is log averagetransaction price. Trend starts at 1 for Oct 2008. Standard errors are clustered at the district level and are shown in parentheses underthe estimated coefficients. We use ***, **, and * to denote significance at the 1%, 5%, and 10% level, respectively.32Table 8: 3km Border Band DID - TransactionsDependent Variable ln(number of transactions)Time Window -6m to 6m -6m to 12mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before -0.109 -0.054(0.094) (0.099)Treat*After -0.478*** -0.619*** -0.308** -0.422***(0.134) (0.133) (0.127) (0.136)Treat*Trend -0.012 0.077***(0.037) (0.022)Treat*Trend*After -0.012** -0.031***(0.005) (0.007)After -0.247 -0.382 -0.309* -0.149(0.160) (0.235) (0.165) (0.195)Trend 0.001 -0.064***(0.025) (0.017)Constant 3.219*** 3.265*** 3.322*** 3.383*** 3.428*** 3.284***(0.234) (0.256) (0.403) (0.257) (0.266) (0.361)Observations 4,431 4,431 4,431 7,130 7,130 7,130R-squared 0.668 0.668 0.666 0.618 0.617 0.608Year-Month FE Yes Yes No Yes Yes NoProject FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table presents the same regression as those shown in Table 5, using a sample that contains projects within 3km of theborder between districts where purchase restrictions are imposed and those where they are not. The dependent variable is log transactionvolume. Trend starts at 1 for Oct 2008. Standard errors are clustered at the district level and are shown in parentheses under theestimated coefficients. We use ***, **, and * to denote significance at the 1%, 5%, and 10% level, respectively.33Table 9: Falsification Tests: Placebo 3 km BorderDependent Variable ln(price) ln(volume)Time Window -6m to 6m -6m to 12m -6m to 6m -6m to 12mTreat*After -0.029 -0.028 0.058 -0.001(0.025) (0.032) (0.148) (0.150)After 0.057** 0.065** -0.683*** -0.658***(0.022) (0.024) (0.110) (0.141)ln(size) 0.004 0.027(0.075) (0.053)Constant 8.963*** 8.896*** 3.160*** 3.219***(0.345) (0.252) (0.197) (0.155)Observations 3,388 5,239 3,388 5,239R-squared 0.854 0.807 0.652 0.606Year-Month FE Yes Yes Yes YesProject FE Yes Yes Yes YesNotes: This table reports the results of geographic falsification test using specification (1). Thesample includes a 3km band in districts that do not have restrictions. The treatment group includeshousing projects lie 0-3km from the border in the non-restricted district. The control group containshousing projects lie 3-6km from the border in the non-restricted district. Standard errors areclustered at the district level and are shown in parentheses under the estimated coefficients. Weuse ***, **, and * to denote significance at the 1%, 5%, and 10% level, respectively.34Table 10: Falsification Tests: Placebo Restriction Date (Quantity Only)Model (1) (2) (3) (4) (5)Time Window(-12 to -6m) vs(-6 to 0m)(-20 to -10m) vs(-10 to 0m)(0 to 6m) vs(6 to 12m)(0 to 10m) vs(10 to 20m)(0 to 12m) vs(12 to 24m)Treat*After 0.084 -0.159 0.124 0.117 0.080(0.203) (0.280) (0.083) (0.076) (0.073)After 0.073 -0.048 -0.066 -0.208** -0.285***(0.186) (0.234) (0.094) (0.097) (0.098)Constant 3.604*** 2.307*** 2.957*** 3.027*** 2.987***(0.136) (0.240) (0.162) (0.164) (0.174)Observations 5,866 7,554 7,465 12,701 16,120R-squared 0.617 0.492 0.652 0.594 0.569Year-Month FE YES YES YES YES YESProject FE YES YES YES YES YESNotes: This table reports the results of time falsification test using specification (1). The dependent variable is log transaction volume.Model 1 to 5 have a placebo restriction assigned to a random month, and the regressions differ by window length. Standard errors areclustered at the district level and are shown in parentheses under the estimated coefficients. We use ***, **, and * to denote significanceat the 1%, 5%, and 10% level, respectively.35Table 11: Land Supply Analysis: Price (Transaction Level)Dependent Variable ln(transaction price/buildable land area)Time Window -6m to 6m -6m to 12mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before 0.032 -0.053(0.212) (0.206)Treat*After -0.051 -0.020 -0.067 -0.107(0.168) (0.244) (0.175) (0.221)Treat*Trend -0.074* -0.011(0.039) (0.021)Treat*Trend*After 0.009 -0.000(0.008) (0.007)After 0.059 -0.086 -0.034 0.049(0.202) (0.212) (0.176) (0.157)Trend 0.033 -0.003(0.035) (0.015)Auction Type -0.104 -0.103 -0.093 -0.149 -0.150 -0.126(0.172) (0.172) (0.168) (0.132) (0.132) (0.126)ln(size) -0.127*** -0.127*** -0.122*** -0.103*** -0.103*** -0.099***(0.044) (0.045) (0.045) (0.036) (0.036) (0.036)FSR -0.219*** -0.218*** -0.225*** -0.186*** -0.187*** -0.190***(0.040) (0.041) (0.038) (0.035) (0.035) (0.038)ln(distance to CBD) -0.212** -0.213** -0.204** -0.229** -0.228** -0.244**(0.100) (0.102) (0.097) (0.095) (0.096) (0.101)Constant 9.822*** 9.804*** 9.132*** 9.578*** 9.578*** 9.548***(0.615) (0.656) (0.884) (0.727) (0.731) (0.602)Observations 673 673 673 950 950 950R-squared 0.660 0.660 0.662 0.599 0.599 0.589Year-Month FE Yes Yes No Yes Yes NoLand Type FE Yes Yes Yes Yes Yes YesDistrict FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table presents the price effects in the land auctions in response to the purchase re-striction 6 months before and 6-12 months after the introduction of purchase restrictions. Thedependent variable is the log of price per buildable area. The Trend is a time trend variable equals1 for Oct 2008. Standard errors are clustered at the district level and are shown in parenthesesunder the estimated coefficients. We use ***, **, and * to denote significance at the 1%, 5%, and10% level, respectively.36Table 12: Land Supply Analysis: Quantity (District Month Level)Dependent Variable ln(number of transactions)Time Window -6m to 6m -6m to 12mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before -0.065 0.015(0.150) (0.143)Treat*After 0.038 -0.033 0.025 -0.002(0.201) (0.215) (0.163) (0.153)Treat*Trend -0.089 0.004(0.070) (0.034)Treat*Trend*After 0.019 0.000(0.017) (0.010)After -0.076 -0.346 -0.155 -0.063(0.286) (0.417) (0.248) (0.236)Trend 0.066 -0.006(0.059) (0.018)Constant 0.474** 0.483** 0.423 0.437*** 0.469*** 0.949*(0.212) (0.189) (1.060) (0.149) (0.147) (0.478)Observations 222 222 222 341 341 341R-squared 0.570 0.570 0.559 0.515 0.514 0.474Year-Month FE Yes Yes No Yes Yes NoDistrict FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table presents the price effects in the land auctions in response to the purchase re-striction 6 months before and 6-12 months after the introduction of purchase restrictions. Thedependent variable is the log transaction volume. The Trend is a time trend variable equals 1 forOct 2008. Standard errors are clustered at the district level and are shown in parentheses underthe estimated coefficients. We use ***, **, and * to denote significance at the 1%, 5%, and 10%level, respectively.37Table 13: Land Supply Analysis: Buildable Area (Transaction Level)Dependent Variable ln(buildable land area)Time Window -6m to 6m -6m to 12mModel Specification (1) (2) (3) (1) (2) (3)Treat*Before -0.101 -0.097(0.412) (0.363)Treat*After -0.409 -0.469 -0.352 -0.434(0.328) (0.467) (0.276) (0.366)Treat*Trend 0.087 -0.100*(0.094) (0.058)Treat*Trend*After -0.014 0.026(0.021) (0.019)After 0.044 0.086 -0.120 -0.383(0.382) (0.455) (0.305) (0.347)Trend -0.022 0.027(0.077) (0.034)Auction Type 0.189 0.187 0.158 0.168 0.167 0.197(0.188) (0.187) (0.195) (0.157) (0.155) (0.162)ln(distance to CBD) -0.066 -0.065 -0.071 -0.150 -0.149 -0.164(0.105) (0.103) (0.101) (0.100) (0.100) (0.105)Constant 11.764*** 11.723*** 11.395*** 11.906*** 11.922*** 11.918***(1.034) (1.022) (1.679) (0.665) (0.726) (0.589)Observations 673 673 673 950 950 950R-squared 0.534 0.534 0.527 0.457 0.457 0.443Year-Month FE Yes Yes No Yes Yes NoLand Type FE Yes Yes Yes Yes Yes YesDistrict FE Yes Yes Yes Yes Yes YesMonth FE No No Yes No No YesNotes: This table presents the price effects in the land auctions in response to the purchase re-striction 6 months before and 6-12 months after the introduction of purchase restrictions. Thedependent variable is the log buildable area. The Trend is a time trend variable equals 1 for Oct2008. Standard errors are clustered at the district level and are shown in parentheses under theestimated coefficients. We use ***, **, and * to denote significance at the 1%, 5%, and 10% level,respectively.38APPENDICESTable A-1: Policy Summary by CityCity Policy Date Treated Districts Control Districts Policy DetailsHefei Mar 31, 2011 Baohe District, Beicheng District, Residents are not allowed to purchase the 3rd home;Luyang District, Zhengwu District, Non-residents are not allowed to purchase the 2nd home;Yaohai District, Xinzhan District, Restrictions only apply to properties in selected districts.Shushan District Binhu New District,Jinkai District,Gaoxin DistrictGuangzhou Oct 15, 2010 Tianhe District, Conghua District, Residents are allowed to purchase an additional home;Fanyu District, Nansha District Non-residents are not allowed to purchase any homes;Baiyun District, Restrictions only apply to properties in the urban area,Haizhu District, suburban areas are not affected.Huadu District,Liwan District,Luogang District,Yuexiu District,Huangpu DistrictChengdu Feb 15, 2011 Chenghua District, Xindu District, Residents are not allowed to purchase the 3rd home;Wuhou District, Wenjiang District, Non-residents are not allowed to purchase the 2nd home;Jinniu District, Pi County, Restrictions only apply to properties in selected districts.Jinjiang District, Dujiangyan County,Qingyang District, Qingbaijiang District,Gaoxin District, Longquanyi DistrictQingdao Jan 31, 2011 Sifang District, Jimo, Residents are not allowed to purchase the 3rd home;Shinan District, Pingdu, Non-residents are not allowed to purchase the 2nd home;Chengyang District, Jiaonan, Purchase restriction only applies to the selected districts.Laoshan District, Jiaozhou,Shibei District, LaixiLicang District,Huangdao District39Table A-2: Descriptive Statistics of Housing Projects by City (-6/+12 months)Control TreatBefore After Before AfterMean S.D Mean S.D Mean S.D Mean S.DCity: HefeiAvg. Price/m2 5,237.92 1,393.55 6,651.88 3,345.39 5,792.35 1,515.73 7,628.54 4,547.24Total Transactions 23.32 28.55 13.39 24.03 25.42 48.90 15.25 25.90Avg. Unit Size(m2) 105.94 35.48 90.52 42.49 98.72 36.60 85.05 39.33Observations 232 375 369 591City: GuangzhouAvg. Price/m2 5,119.98 1,128.88 6,404.62 1,545.58 12,345.76 6,718.22 14,276.31 8,553.62Total Transactions 22.03 41.01 23.06 34.09 19.64 41.87 15.44 35.98Avg. Unit Size(m2) 105.83 32.66 117.22 42.46 115.73 48.85 121.34 49.81Observations 61 208 573 1,120City: ChengduAvg. Price/m2 5,615.66 2,166.52 6,211.72 2,341.34 9,046.84 3,914.80 10,935.34 6,208.18Total Transactions 57.23 72.56 36.07 54.24 51.70 66.99 29.96 53.03Avg. Unit Size(m2) 123.82 53.43 113.70 50.17 99.17 42.45 96.50 42.54Observations 671 2,105 1,032 2,131City: QingdaoAvg. Price/m2 5,981.58 4,004.82 7,345.29 4,805.90 9,271.10 8,415.40 10,497.57 8,708.98Total Transactions 17.72 23.63 17.14 28.65 40.67 81.57 19.91 40.02Avg. Unit Size(m2) 135.59 66.43 125.29 56.00 125.99 51.79 110.80 39.77Observations 43 214 322 721Notes: This table provides the summary statistics of Avg. Price/m2, total transactions, and average unit size of housing projects in eachcity before and after the implementation of the restrictions.40Table A-3: Descriptive Statistics of Land Transactions by City (-6/+12 months)Control TreatBefore After Before AfterMean S.D Mean S.D Mean S.D Mean S.DCity: HefeiAvg. Price/m2 1,763.56 1,670.68 1,268.25 1,019.64 2,321.28 1,358.47 1,628.39 1,804.10Land Area 58,154.86 61,546.08 43,354.24 50,712.46 35,401.18 41,462.18 28,042.84 27,395.71Buildable Area 158,250.31 187,696.54 140,487.78 178,318.25 113,542.01 115,375.04 82,192.26 80,330.10Observations 42 37 17 17City: GuangzhouAvg. Price/m2 1,152.06 711.74 1,085.44 838.11 3,941.47 3,176.56 2,494.62 1,730.89Land Area 23,134.31 19,325.09 49,315.82 49,367.04 41,123.22 58,960.65 38,604.60 39,558.73Buildable Area 58,089.60 40,365.40 99,507.76 101,780.44 92,602.22 121,864.97 84,165.25 83,887.93Observations 9 25 20 53City: ChengduAvg. Price/m2 1,680.77 2,323.90 1,246.09 847.35 2,690.56 1,940.28 2,563.05 1,549.70Land Area 53,869.54 46,649.04 51,627.28 44,017.80 54,132.58 51,604.08 35,408.57 27,810.83Buildable Area 135,817.18 123,877.76 172,713.54 177,069.20 217,051.03 255,899.65 128,855.63 96,308.38Observations 106 113 36 40City: QingdaoAvg. Price/m2 615.56 444.66 954.58 1,188.76 2,477.43 2,067.35 3,327.64 10,397.90Land Area 39,395.18 38,922.06 30,471.70 28,978.79 44,906.35 38,507.62 46,405.14 50,634.42Buildable Area 64,899.73 75,740.32 49,868.55 51,659.81 75,194.88 58,274.81 77,300.26 83,764.80Observations 137 180 46 72Notes: This table provides the summary statistics of Avg. Price/m2 (=Avg. Price/Buildable Area), land area, and buildable area of landparcels in each city before and after the implementation of the policy.41Table A-4: Descriptive Statistics of Housing Projects for Four Cities within 3km Border Bands (-6/+12 months)Control TreatBefore After Before AfterMean S.D Mean S.D Mean S.D Mean S.DAvg. Price/m2 5,565.70 1,879.14 6,316.05 2,485.12 8,834.60 5,252.85 11,096.26 7,287.25Total Transactions 50.35 68.13 33.03 49.35 44.62 70.16 24.64 47.09Avg. Unit Size(m2) 115.77 46.87 106.33 46.63 99.73 41.32 96.23 41.84Observations 639 1,900 1,499 3,092Notes: This table provides the summary statistics of Avg. Price/m2, total transactions, and average unit size of housing projects within3km border bands in each city before and after the implementation of the restrictions.42

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