100262 AUTHOR ACCEPTED MANUSCRIPT FINAL PUBLICATION INFORMATION The Effect of a Land Titling Programme on Households’ Access to Credit The definitive version of the text was subsequently published in Journal of Development Effectiveness, (Forthcoming 2015), 2015-06 Published by Taylor and Francis and found at http://dx.doi.org/10.1080/19439342.2015.1057859 THE FINAL PUBLISHED VERSION OF THIS ARTICLE IS AVAILABLE ON THE PUBLISHER’S PLATFORM This Author Accepted Manuscript is copyrighted by the World Bank and published by Taylor and Francis. It is posted here by agreement between them. Changes resulting from the publishing process—such as editing, corrections, structural formatting, and other quality control mechanisms—may not be reflected in this version of the text. You may download, copy, and distribute this Author Accepted Manuscript for noncommercial purposes. 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(3) You must attribute this Author Accepted Manuscript in the following format: This is an Author Accepted Manuscript of an Article by Piza, Caio; Barros de Moura, Mauricio José Serpa The Effect of a Land Titling Programme on Households’ Access to Credit © World Bank, published in the Journal of Development Effectiveness(Forthcoming 2015) 2015-06 CC BY-NC-ND 3.0 IGO http://creativecommons.org/licenses/by- nc-nd/3.0/igo http://dx.doi.org/10.1080/19439342.2015.1057859 © 2015 The World Bank The Effect of a Land Titling Programme on Households’ Access to Credit Caio Piza (corresponding author) Economist on the Development Impact Evaluation Unit (DIME) in the Research Group at the World Bank 1818 H St. NW, Washington, DC 20433, USA Phone: +1 202 473 1744 Email: ctpiza@gmail.com Mauricio José Serpa Barros de Moura George Washington University, Washington, DC Graduate School of Political Management 5734 8th N. Street, Arlington, VA, 22205 Email: mjmoura@gwmail.gwu.edu mmoura@fas.harvard.edu 1 Acknowledgements: We would like to acknowledge the participants of the Mind the Gap Conference held in Cuernavaca, Mexico, the participants of the 26th Annual Congress of the European Economic Association held in Oslo, Stefan Dercon, Richard Dickens, Andy McKay, Inder Ruprah, and Tulio Cravo. All conclusions are exclusively ours. Abstract This paper assesses the effects of property titling on households’ access to and use of credit by focusing on household responses to an exogenous change in their formal ownership status. We isolate the credit effect on legal ownership by comparing households from communities in Osasco, Brazil. Our statistical estimates suggest that land-titling increases credit use, decreases reliance on credit borrowed from relatives, and increases credit borrowed from commercial banks. We also find that treated households increased their consumption of time- saving durable goods, which explains an observed reallocation of time among household members, with adults working more and children less. Keywords: Property Rights, Land Title, Access to Credit, Treatment Effects, Heterogeneous Effects. JEL: D23, O43, J22 2 I. Introduction A well-defined and properly enforced property rights system is critical to the functioning of markets (Coase, 1960). Considerable mutually beneficial transactions are impossible in the absence of well-defined property rights; such an absence could help to explain why countries have followed different development paths (North, 1990). Indeed, some societies and countries have found relatively affordable ways to secure property rights, such as those based on rooted norms and codes of conduct. Others struggled to find shortcuts to deal with such issues and had to rely on formal institutions (North, 1990 and Putnam, 1993). Monitoring costs and imperfect enforcement cast doubts on the capacity of formal institutions to secure property rights, particularly in places where state-wide institutions are almost absent (Olson, 1993). The lack of formal property rights, such as land titling, has immediate implications for households as well. This paper investigates the impact of a Brazilian land titling programme, Papel Passado, which targeted households living in local favelas – an environment constrained by the absence of the rule of law and heavily dependent on interpersonal relationships. Property titling is increasingly considered one of the most effective public policies to benefit poor populations and encourage economic growth around the world (Baharoglu, 2002; Binswanger et al., 1995). In Asia, for example, millions of land titles have been issued in Vietnam and Cambodia, while several governments are investing in social housing in Africa (Galiani & Schargrodsky, 2010). In Latin America, Peru offers the most famous example of a property-titling programme; in the 1990s, the government issued titles to 1.2 million urban households. In 2003, the Brazilian federal government announced a massive national plan to title 750,000 families. Since its launch, this programme, Papel Passado, has received US $15 million annually from the federal budget and has provided titles to over 85,000 families in 49 3 cities across 17 Brazilian states. The programme’s official goal is ‘to increase land titles in Brazil and to promote an increase in the quality of life for the Brazilian population,’ i and is intended to issue land titles to families living under illegal conditions (that is, residents squatting illegally in urban dwellings). Whether the land titling policy has resulted in either a de facto or de jure property right is an empirical question that this study investigates. The lack of formal property rights prevents households from using their land as collateral to access credit markets and invest in their properties (Besley, 1995). If such credit were available, households could invest in more productive projects, thereby increasing their labour productivity and income (Demsetz, 1967; de Soto, 2000; Banerjee and Duflo, 2007). In a recent study, Besley and Ghatak (2009, 2) called the de Soto effect ‘the idea that better access to collateral increases credit availability.’ In addition, the mere existence of a de facto property right could boost housing and property investment and – given that households would have a greater incentive to protect their asset value (Besley and Ghatak, 2009) – increase the households’ collateralisable wealth. Although one could expect some natural, almost deterministic, link between land titling and access to credit, the available evidence indicates that the relationship actually depends on the existence of land and credit markets (Deininger and Feder, 2009). For instance, Feder and Nishio (1999) demonstrate that well functioning financial markets are required for the existence of long-term credit contracts when land is used as collateral (most likely through institutional channels). If regulations restrict or disallow the enforcement of claims on collateral, or if the legal and enforcement administration for collateral contracts is too cumbersome to be effective, land registration systems will not provide the benefits that might otherwise be linked to the credit market, and vice versa. Along these lines, Riofrio (2001) has shown that Peruvian households with tenure security (but no land title) and those 4 with formally titled property have similar access to credit. On the other hand, Cockburn (1998) examines the Peruvian land titling programme and finds that property values alone do not guarantee a flow of private loans. In two recent studies, Field and Torero (2002) and Galiani and Shargrodsky (2010) look at the impact of land titling programmes in the peri- urban areas of Peru and Argentina and find that land titling had a very limited impact on credit demand. This paper aims to contribute to this debate by investigating the effect of a pilot version of the Brazilian land titling programme. We compare two similar neighbouring communities in the Brazilian city of Osasco. The town — with around 654,000 inhabitants and almost 6,000 families living informally on urban property — is located in the metropolitan area of São Paulo and is part of the Papel Passado programme map. In one of its communities, Jardim Canaã, all households received land titles in 2007. In another, Jardim DR, households were scheduled to receive land titles in 2012, making it a natural comparison group. Our analysis is based on a two stage survey focusing on the property rights issue that was conducted in Jardim Canaã and Jardim DR. The sample consists of 326 households distributed across both neighbourhoods (185 from Jardim Canaã and 141 from DR). The first stage of the survey was conducted in March 2007, before titles had been issued to Jardim Canaã, and the second stage in August 2008, almost 1.5 years after the titles had been received. The households in these two communities were located on municipal public land that they had illegally occupied. The main consequence of the land titling was that Brazilian law came to protect these new property owners. The government relinquished post rights over the land after the titling. Other land dispute cases in Brazil are much more complex if occupation occurs on private property, since this can open the door to endless legal battles. The majority of academic and policy attention on property rights has centred on rural households, presumably because of historic interest in agricultural investment and the related 5 politics of land reform (Feder and Deininger, 2009). Although the evidence for urban areas has grown, it seems to be concentrated in a few countries such as Peru (Field and Torero, 2002; Field, 2005; Field, 2007; Field and Torero, 2008), Argentina (Galiani and Shargrodsky, 2005, 2010), Brazil (Andrade, 2006; Moura et al., 2009, 2013, 2014), and Tanzania (Ayalew et al., 2011). We are unaware of many evaluations that look at the impact of land titling programmes in urban settings. Because of the design of the intervention, we are able to employ the difference-in- differences and ANCOVA estimators. We use the fixed and random effects models to check the robustness of our findings. We also match the samples at the baseline to deal with issues of attrition and unbalanced sampling at the household level. The results are very similar regardless of the model’s specifications and whether or not controls are added and samples are matched. We check the effect of the programme on different types of credit and find that most of the increase in credit use came from loans borrowed from commercial banks. The empirical exercise put forward in this study does face a few challenges, however. Given that the fieldwork only covers two clusters, we are unable to cluster standard errors at the community level. Since our standard errors might be underestimated, we use arbitrary inflation factors to check the robustness of our findings in the section that discusses potential caveats. Finally, we look for heterogeneous effects between formal and informal workers, since one may suspect that the upward trend in the credit supply that was observed in Brazil over the last decade was mostly concentrated on formal workers, and would therefore disproportionally benefit the households in the treated community given its larger share of formal workers compared to the control community. This would cast doubt on our identification strategy, as the common trend assumption would be unlikely to hold in this 6 case. The estimates do not reject the hypothesis of common effects for households whose head is a formal or an informal worker. Our findings suggest that land title programmes have a positive effect on the use of and access to credit. The average treatment effect on the treated points to an impact of 21 percentage points (about 48 per cent) on credit use and 31 percentage points (threefold increase) on access to credit, that is, credit borrowed from bank institutions. Additionally, even though the impact of land titling does not seem to differ by gender, it is definitely heterogeneous across different modalities of credit. One of our main findings shows that titled households stopped borrowing from relatives and shifted to formal institutions. Although we did not observe any impact on home investment, we did observe an increase in the consumption of durable goods, such as washing machines and stoves. The rest of the paper is divided as follows. Section II describes the theoretical framework, and section III presents the research methodology and data description. In section IV we discuss the empirical strategy, and section V presents the main results. Section VI sheds light on the mechanisms underlying the results, and in section VII we discuss potential caveats. The conclusion summarises the main results and outlines a few ideas for future work. II. Land Title and Credit: A Theoretical Background Several studies have documented the impact of land titling on an array of outcomes. A partial list includes Jimenez (1985), Alston et al. (1996), and Lanjouw and Levy (2002) on real estate values; Besley (1995), Jacoby et al. (2002), Brasselle et al. (2002), and Do and Iyer (2003) on agricultural investment; Place and Migot-Adholla (1998), Carter and Olinto (2003), and Field and Torero (2002) on credit access, labour supply, housing investment, and income; and Deininger and Ali (2008) and Goldstein and Udry (2008) on land title and productivity. In a recent literature review, Deininger and Feder (2009) show that the evidence of land titling 7 programmes is actually mixed and that context matters. However, Kerekes and Williamson (2010) claim that no general consensus on the effects of land titling has been reached in the available literature. In a study that we consider closest to ours, Field and Torero (2002) find that the Peruvian titling programme had positive effects, particularly on labour supply, credit access, and housing investments. They exploit timing variability in the regional implementation of the programme by using cross-sectional data on past and future title-holders midway through the project. Evidence of the impact of land titling programmes in Brazil remains limited. Andrade (2006) demonstrates the positive effect of land title on income using cross-sectional data from a sample of 200 families of the Comunidade do Caju, a poor, urban community in Rio de Janeiro. Moura et al. (2009) and Moura et al. (2014), using data from the same intervention covered in this study, found that land title reduced child labour by about eight hours per week, increased the labour force participation rate of household heads, and increased their hours worked at the lower tail end of the distribution of weekly hours worked. Additionally, Moura and De-Losso (2013) found a positive relationship between land title and households’ happiness levels. Although a causal link between property rights and access to credit has been theorised by many authors who have been inspired by Hernando de Soto’s books (1989 and 2000), such as Feder and Feeny (1991), Carter and Olinto (2003), Boucher et al. (2008), and Besley and Ghatak (2009), empirical evidence for such a relationship, particularly in urban areas, remains mixed. For example, Kerekes and Williamson (2010) investigate the impact of land title in rural Peru and do not find support for the argument that government land titling can be used as collateral to guarantee a loan. 8 De Soto (2000) evokes perhaps one of the most widespread arguments linking land title and access to credit. He argues that land titles open formal credit markets to the previously unbanked. Land titles serve as collateral and help to transform fixed assets into liquid assets. However, as argued by Dower and Potamites (2007), the collateral role of a formally titled property depends on the possibility of a legal transfer if the borrower defaults. The authors also emphasise that if this transferability is undermined by a weak legal infrastructure, political pressure, a thin land market, or simply the cost-benefit analysis of foreclosure given the size of the loans involved, then the collateral value of a title and its effectiveness in ensuring repayment are both questionable. Moreover, Kerekes and Williamson (2010) argue that a formal system of land titling does not necessarily lead to the benefits associated with secure property rights, such as increased access to credit and property enforcement. Dower and Potamites (2007) also show that titles play an important ex-ante role in providing information about the applicant to the potential lender. The basic concept is that the bank may prefer to lend to titled households, not only because the title mitigates the bank’s risk in the case of a default, but also because the title provides information about the likelihood of default or improves the borrower’s credit score ii. Commercial banks do not release the key variables that are used to compute clients’ credit scores. It is therefore difficult to address the specific role of land titles in assessing the general likelihood of default. Nonetheless, evidence suggests that titling improves Brazilian borrowers’ credit scores. Magalhães and Mario (2011) studied the application of a credit scoring system for a credit cooperative (credit union) in the State of Minas Gerais, Brazil iii. As one might expect, the authors find that land title is associated with a greater score for 9 homeowners compared to households that rent, and that official renters score higher than those who took up illegal residence in slums, particularly residents of slums. While this paper provides additional evidence in support of the argument that land titles increase access to credit, it neither investigates household credit behaviour (as in Field, 2007) nor specific credit contracts. As in Galiani and Schargrodsky (2005), this paper provides estimates for different types of credit to determine which source was most affected by the programme. The paper also sheds light on the link between land title and the consumption of durable goods. III. POTENTIAL MECHANISMS The available literature on the impact of land title has yet to precisely explain through which transmission channel land registration policy can affect credit availability. Therefore, without taking any firm position, we discuss two possible transmission channels through which land registration policy could affect credit availability. Besley et al. (2009 and 2010) argue that most accurately defined land rights affect the amount of collateral wealth that can be pledged as collateral in a credit contract. Under certain conditions, we can expect that a land title programme will have a positive effect on households’ access to credit through a higher share of collateral wealth. Credit could be used for durable goods acquisition (a proxy for investment), non-durable consumption, or house improvement. Unfortunately, the survey did not collect data on non-durable consumption. We found no impact on housing investment, but we did find that there was an increase in the price of houses and the acquisition of durable goods. The argument of Besley et al. (2009, 2010) gives us a roadmap of a causal chain that we will investigate. Along the lines they develop, tenure security could affect access to credit in two ways: (1) a de facto property right would 10 allow households to pledge their houses as collateral in informal credit contracts — that is, credit contracts with moneylenders; and (2) the intervention would increase tenure security, affecting house prices since they would be able to be negotiated in the formal housing market. The value of the houses and the wealth of households would increase, which would also increase the amount of credit available for borrowing from commercial banks. From our data, we are able to determine whether the price of titled properties increased with the programme. Such an increase would partially explain an increase in the demand for credit. We also need to determine what households did with the credit they borrowed. We look at the acquisition of durable goods and the labour supply of children and adults. With that in mind, we are able to shed light on the causal chain resulting from the intervention. Another plausible mechanism assumes that a land title programme is followed by a greater supply of public goods, such as security, electricity, garbage collection, and the provision of a sewage connection (for example, Hoy and Jimenez, 2006). Therefore, the supply of public goods would have positive externalities, such as increasing the housing value of a neighbourhood. With better defined property rights and an improved supply of public services, commercial banks could open branches in the newly secured area and other private sector investment could also take place. In this case, a land title programme would simultaneously affect both the demand for and the supply of credit, and we would be unable to disentangle the two. However, in the case of Osasco, the introduction of such public services was not immediately part of the land title programme. Only several months after the titling of households were public services — each under a different timetable and dynamic — supplied in the treated community. IV. Sample Selection, Data, and Descriptive Statistics A. Sample Selection 11 This section discusses the sample used to evaluate the titling programme and describes the dataset, presenting initial descriptive statistics. The Brazilian Federal Government chose Osasco as one of the cities to participate in the Papel Passado titling programme. Osasco has 30,000 people (about 6,000 families) living under informal conditions, which represents almost 4.5 per cent of its total population (ANOREG 2007). The programme timetable for Osasco established that all communities living in illegal conditions would be part of the Papel Passado in the 2007-2014 period. Yet, given that fiscal resources are limited, communities in Osasco did not all receive land titles at the same time. In 2007, Jardim Canaã, where 500 families live, was the first locality to receive land titles. The closest neighbourhood to Jardim Canaã is DR, home to 450 families. DR’s households joined the Papel Passado programme in 2012. Jardim Canaã and DR were built on municipal public land that was illegally settled (this particular land title programme only operates in illegally settled public areas). The main consequence of the programme is that the newly official property owners are now fully protected under Brazilian Law. The government does not have any post rights over the land/property after title is granted. Osasco’s City Hall has stated that there was no specific agenda behind the prioritisation of when localities received the titles, and that either community could have been the first recipient. If this claim is at least partially genuine, it minimises the issue of selection bias in this study’s non-experimental evaluations (Behrman and Todd 1999). In addition, 95 per cent of the first survey participants — both from Jardim Canaã and DR — did not expect to receive land titles. They were unaware of the Papel Passado programme, reducing a potential behavioural deviation from households included in the programme. iv 12 Note that the contamination bias v is also minimised, as the households of DR would benefit from the programme if someone in Jardim Canaã were willing to borrow on their behalf or if the programme displaced moneylenders from Cannã towards DR, inducing a supply shock in the informal credit supply. Due to their geographical proximity, Jardim Canaã and DR share similar economic and social characteristics. In fact, there is no visible physical border splitting these two neighbourhoods, making them essentially geographically united. The communities are located 2.5 miles from downtown Osasco and have precisely the same access to Osasco’s main economic centre and surrounding infrastructure. This ensures that the households from these two communities have access to the same markets and urban infrastructure. B. The Data The dataset originates from a two stage, door-to-door survey (answered by the family head) focusing on property rights. Minimising potential biases, the survey questionnaire and its interviewers did not provide the households with direct information on the objective of the research. Officially, for the people interviewed, the study was about general living conditions in Osasco. The questionnaire was administered to 326 randomly selected households and includes 39 questions. vi The methodology and format of the questions closely mirrors the national statistical survey (Pesquisa Nacional de Amostra de Domicílios, PNAD) from the Brazilian Statistical Bureau (Instituto Brasileiro de Geografia e Estatística, IBGE). It also requests information on household and individual characteristics including the social, personal, and economic benefits associated with property ownership. The study also tracked the households that moved away from both communities. In contrast to the 8 per cent of households that 13 moved away from Canaã, only 0.7 per cent of households (1 out of 141) moved away from DR during the same period. The researchers who conducted the door-to-door survey were not from Osasco. They first administered the questionnaires in March 2007, before titles had been issued to households of Jardim Canaã. The second stage was carried out with the same households in August 2008 (with 2% missing interviews) about 17 months later. The time gap between the stages was designed so that all households interviewed during the first stage would have possessed the land title for at least one year by the time of the second survey. vii Given the information in the surveys, a technique recommended by Bolfarine and Bussab (2005) was used to randomly select 326 sample households from the two localities: 185 from Jardim Canaã and 141 from DR. The approach consisted of choosing the first 150 households from Jardim Canaã and DR whose heads have the closest birth dates (day and month) to the three field researchers who conducted the survey interviews. Initially, each researcher received 50 names as their first base. After interviewing each household, researchers could then select the third and the fifth households on the right hand side of the first base. C. Descriptive Statistics Helms (2006) defines access to finance as the possibility that individuals or enterprises can access financial services, including credit, deposit, payment, insurance, and other risk management services. Thus, access to credit refers to household access to different sources of financing or credit. We follow this approach and borrow Galiani and Schargrodsky’s definition of the ‘use to credit’ variable (2005, 2010), which includes: (i) credit card and bank accounts; (ii) non-mortgage loans received; (iii) informal credit (from cooperatives and labour unions); (iv) department store credit (such as loyalty cards); and (v) mortgage loans received. 14 The survey questionnaire applied in this paper contains a set of questions that can be related either directly or indirectly to households’ access to and use of credit, and applies some of Galiani and Schargrodsky’s (2005, 2010) variables. Figure 1 illustrates credit availability for the treatment and comparison groups in the baseline, and reports the p-value for the difference in means. Fig. 1 – Credit Availability – Variables, Pre-Programme (2007) Mean Mean A=B: Comparison (A) Treated (B) p-value Department Store 0.35 0.36 0.9 Bank Personal Loan 0.08 0.09 0.78 Loan from Relatives 0.88 0.91 0.43 Credit Card 0.25 0.24 0.84 Credit Variable 0.36 0.36 0.92 Source: Research from the Osasco Land Title Survey. The T-test performed allowed for unequal standard deviations. Loyalty cards have several limitations as a channel to access credit. First, a loyalty card is not liquid, as it can be used only in the designated store. Second, it is closely attached to the consumption of either durables or non-durables that are available at the store that issued the card. As can be seen above, about 35 per cent of the households in both groups had loyalty cards. Personal loans is the main credit variable in this exercise for two reasons. First, it gives an idea of whether the intervention affected access to credit. Unfortunately, we do not really know if only 8 per cent of households had access to credit or if more households had access to credit but only 8 per cent actually borrowed from commercial banks. In this case, we cannot say whether access to credit was a binding constraint. Second, of all the categories listed in the table, personal loans is the one that probably gave households access to a larger 15 volume of credit to invest in the acquisition of more expensive durable goods. The low share of households using personal loans and the high percentage of households borrowing from relatives suggests that most of these households face some difficulty in accessing credit from formal bank institutions. Finally, one fourth of households said that they have credit cards. Credit cards are usually used for consumption, but credit constrained households may use them as working capital to invest in their houses or to acquire durable goods. viii Figure 2 reports the T-test for the difference in means for covariates in 2007, before the programme was put in place. The table presents characteristics of the dwellings and the households. The first three rows show that house prices and the proportion of households with a freezer were statistically equivalent. On the other hand, a larger percentage of households in the treated community had a washing machine. Since a washing machine is time saving, it is worth looking at the labour supply of household members. Although the average weekly hours worked by the household head is the same in both groups, the number of hours worked by children under the age of 16, the average monthly total household income per capita, and the informality rate are significantly lower in the treatment group, while the number of years of schooling that the household head has received is significantly higher. The lower intensity of child labour in the treated community could help explain the discrepancy in the monthly household income, but the means for the education level and the labour force status of the household head are a bit puzzling. 16 Fig. 2 – Test and Z-score for the difference of means for covariates in 2007 Mean Mean H0: A = B Comparison (A) Treatment (B) p-value Property characteristics House price 43,018.97 37,217.23 0.27 Washing machine 0.62 0.87 0.00*** Freezer 0.92 0.92 0.98 Characteristics of the household Gender of the head (female = 1) 0.31 0.34 0.48 Race of the head (non-white = 1) 0.69 0.64 0.43 Marital status of the head (married = 1) 0.61 0.65 0.52 Age of the head 42.60 39.40 0.06* Years of education of the head 5.00 9.00 0.00*** Labour force status of the head (informal = 1) 0.94 0.65 0.00*** Weekly hours of work of the head 10.10 10.40 0.81 Weekly hours of child labour (< 16 years old) 8.35 3.30 0.00*** Monthly household income per capitad 553.10 255.80 0.00*** Household size 3.96 3.84 0.53 # Number of Observations 137 168 Source: Research from the Osasco Land Title Survey and Central Bank of Brazil Notes: *, **, *** rejection of the null hypothesis of equal mean at 10, 5, and 1 per cent respectively. The T-test performed allowed for unequal standard deviations. a 0 = male, 1= female , b 1 = Afro-Brazilian, 0 = otherwise, c 1 = married, 0 = otherwise, d Currency exchange rate in 12/31/2008, 1 USD = 1.75 BRL (Brazilian Reais). The sample size for house prices is smaller (T = 104, C = 68) due to missing values. Even though this may appear to be counterintuitive at first glance, Zylberstajn and Balbinotto Neto (1999) argue that formal workers tend to receive additional benefits that are not reflected in the cash payroll, as is customary for formal employees in Brazil, and they also tend to have additional savings (length of service guarantee fund and public pension). ix Informal workers, on the other hand, do not have these benefits and rely instead on cash income to compensate for their lack of perks and savings. x Menezes et al. (2004) go further and conduct an empirical exercise to compare earnings in the formal and informal sectors in Brazil. They find that after controlling for education levels and self-selection into the formal sector, informal workers aged 24 to 54 have higher wages than their formal worker counterparts. xi Another potential confounder could stem from the deliberated expansion of credit lines to low-income households. Mendonça and Deos (2012), for instance, argue that Brazil’s 17 consumer credit expansion has been crucial to the growth of its private consumption sector over the last 10 years. They consider the evolution of the credit transactions/GDP ratio, which increased from 21.9 per cent in January to approximately 49 per cent in December 2011. Wheatley (2010) points out that the amount of credit in the economy jumped from 22 per cent of the gross domestic product in 2002 to approximately 47 per cent in 2010. He claims that this growth has come from C, D, and E classes (the middle to bottom of the economic pyramid). The expansion of credit card lending clearly translates this trend, with an increase from 28 million credit cards in 2000 to approximately 153 million in 2010, while credit card gross sales rose from BRL 46 billion to BRL 309 billion over the same period. Data from the Central of Bank of Brazil (2012) show a 4 basis point increase in the credit/GDP ratio during the period of our study (March 2007 to April 2008), from 32 per cent in 2007 to 36 per cent in 2008. However, the household debt service ratio was almost flat over the same period, as illustrated by Figure 3. Fig. 3: Brazilian household debt service ratio (measurement of debt against monthly gross income) 25% intervention 20% 15% 10% 5% 0% 2005 2006 2007 2008 2009 2010 2011 2012 Source: Central Bank of Brazil (2012). Although this credit expansion might be considered a shock in the supply side of credit market, due to a lack of information we are prevented from checking whether it was the same 18 for both the treated and comparison groups. Although the dummy year in the difference-in- differences regression captures any common shock over the period under study, one could argue that formal workers are less credit constrained than their informal counterparts, particularly regarding credit for mortgages. Even controlling for the labour force status of the household head in the regressions, as well as for individuals and communities fixed effects, it is likely that the statistics on household indebtedness over-represent the leverage behaviour of formal workers in particular. If so, the assumption of parallel trends, which is key in our identification strategy, would not hold, and the treatment effect would be biased upwards, because it would be picking the effect of the policy and credit supply shock simultaneously. We test for heterogeneous effects by interacting the treatment dummy with the labour force status (informality dummy) at the baseline. It is important to mention that a high percentage of indebted households observed in Brazil over this period borrowed mainly from credit card companies and loyalty cards. Access to these two modalities of credit is widespread in Brazil, including among informal workers. In fact, our data shows that the main sources of credit are loans from relatives, loyalty cards, and credit cards (see figure 1). IV. Empirical Strategy Our identification strategy depends on the assumption that in the absence of the intervention in Jardim Canãa, households from both neighbourhoods would experience the same variation in the use of and access to credit. However, the design of our fieldwork imposes many practical challenges. First, because we have only two clusters (communities), we are unable to distinguish between cluster effects and individual fixed effects. Second, the 19 number of clusters prevents us from taking intra-cluster correlation into account when estimating the standard errors. Third, we have data from only two points in time and are therefore unable to check whether outcomes of interest were following a similar path in both groups. We discuss below how we address each of these issues. We start the analysis using the difference-in-differences (DD) and ANCOVA methods to estimate the impact of the intervention (see McKenzie, 2012). The DD estimator compares the difference in the mean value of the outcomes between the treated and comparison groups at two points in time. The ANCOVA approach differs from the classical DD, as it controls for the baseline value of the outcome variable. Both approaches control for pre-treatment covariates to mitigate any bias related to unbalanced covariates. The average treatment effect on the treated (ATT) can be estimated through the following DD regression model: (1) where Yist is credit access by household head i in community s at time t ; is a dummy variable that is equal to 1 if the individual resides in the treated community ( s = 1 ) and is equal to 0 otherwise; Post t is a dummy variable that is 0 in 2007 (baseline period) and 1 in 2008; X ist is a vector of pre-determined observed characteristics of the household head i in community s in year t that includes dummies for gender, ethnicity, marital status, status in the labour market, years of schooling, and household size. Finally, u ist denotes the error term, which is assumed to be independent of X ist and Post t (see Meyer, 1995; Imbens and Wooldridge, 2008). Because all households in the treated community were treated, and we are comparing only two communities, we can omit the subscript s from the notation. 20 The parameter of interest is the coefficient α DD , which identifies the difference-in- differences estimator for the average treatment effect on the treated (ATT). As mentioned above, the interpretation of this parameter as the causal effect of land title on credit usage relies on the assumptions that (i) the selection for the treatment does not depend on unobserved individual and community characteristics that change over time; (ii) the access to and use of credit between the treated and comparison groups would evolve in parallel in the absence of the programme; and (iii) the intervention does not affect the availability of credit for households living in the comparison area; that is, no spillover effects are present. Assumption (i) is very likely to hold in the present context, since the treated and control communities were chosen arbitrarily and all households in the community assigned to the treatment were actually treated. In that sense, the intervention had no problem of take-up, and compliance was perfect in both groups. The second assumption is key in the DD framework. When a non-experimental dataset is used to assess the impact of the programme, the use of more than one period of pre-treatment data is usually recommended in order to check the plausibility of this assumption. If one observes the outcome variables following the same path before the intervention takes place, then the assumption becomes plausible and one is therefore more likely to believe that the DD framework is actually identifying the causal effect of the intervention. Unfortunately, we have just one period before the intervention was put forward and are therefore unable to check whether the outcome variables were following the same time trend in both the treatment and control groups. We also observe imbalances in some covariates at the household level. Such imbalances may suggest that the groups are actually different; consequently, the outcome variables would not differ only in level but in difference as well, thus invalidating our identification strategy. In such cases, it is strongly recommended that researchers use a matching technique to select a more homogeneous sample of households (Heckman et al., 1997; Abadie, 2005; Blundell and Dias, 2009). xii This 21 is the strategy that we pursue here. Our identification strategy relies on the assumption that the parallel trend holds in a matched sample. The identification of the ATT estimator follows a two step procedure. We first estimate a propensity score function, p(X), to find a more homogeneous sample of treated and control households, that is, households with similar probabilities of being treated given their observed characteristics. This is the so-called common support condition (Rosenbaum and Rubin, 1983). We then run the DD regression in the matched sample. These assumptions imply that, (2) and (3) In addition to the traditional pooled OLS estimator, which is used to estimate treatment effects with two period panel data, we run the fixed and random effects estimators to check the robustness of the results. Note that in the fixed effect model the coefficient for p(X) will not be identified, because it is fixed over time. Finally, we follow McKenzie (2012) and re-specify equation (1) to improve the efficiency of the estimates if the autocorrelation of the outcome variable is low (below 0.5). The ANCOVA specification takes the following format: (4) 22 In this case, the parameter of interest is δ . Since the intervention left no space for individuals to self-select into the programme, we expect both approaches to provide similar estimates. Because the regressions for the matched sample control for the estimated propensity score, standard errors are obtained with bootstrap with 1,000 repetitions (Davidson and MacKinnon, 2000). V. Empirical Results This section reports the unconditional DD estimate for the impact of land title on credit use. Figure 4 presents a descriptive analysis using an unmatched comparison group. Fig. 4 – Descriptive Effect of Land Title on Credit Use (2007, 2008) Comparison Treatment DD group (A) group (B) (percentage points) 2008 Frequency 42 68 2007 Frequency 36 36 Difference (1) – (2) 6 32 26 (%) 17 89 72 Number of Observations (households) 137 168 Source: Research from the Osasco Land Title Survey According to Table 3, the impact of land title on credit use was 26 percentage points (pp.) or 72 per cent. The table shows that credit availability increased by 6 pp. for the comparison group and by 32 pp. for the treated group. The increase observed among the comparison group suggests that even households without land titles were able to use more credit in 2008 than in 2007. This evidence illustrates the importance of controlling for a counterfactual distribution once the before-and-after analysis clearly overstates the impact of the programme. Moreover, it suggests that the credit expansion observed in Brazil in the last decade may have affected untitled households too; thus, the descriptive analysis suggests that 23 the increase in credit usage in the treatment group was not artificially caused by any displacement effect, that is, a reduction in credit availability to the control households xiii. These estimates are relatively similar to those of Dower and Potamites (2007) in their study in Indonesia. According to the authors, the average effect of land title on the probability of having had a formal bank loan was about 21 per cent, and the average impact on the amount of working capital approached 72 per cent. To verify whether the DD estimates are statistically significant and sensitive to the addition of covariates, we estimate eq. (1) with and without controls. The model pools the data for the two years and estimates the impact of the programme via OLS. Therefore, our estimates are based on a linear probability model. Despite the caveats underlying this approach — such as that (i) the predicted probability can be negative or more than a unit, and (ii) the assumption of linear relationship between the outcome variable and the covariates — this approach renders direct estimates of the impact of the programme xiv. The first column reports the naïve estimator, that is, the OLS without controls. This can be considered the benchmark estimate. The DD estimates are presented in columns two to four. The estimates are consistently the same, pointing to an effect of land titling on credit availability of 25 pp. The estimates are very precisely estimated in all cases. 24 Fig. 5 – Difference in Difference Estimates – Land Title Impact on Credit Availability (2007, 2008) Credit Credit Credit Credit In t=1 DD DD DD Title 0.26*** 0.0085 0.063 0.059 (4.78) (0.15) (0.99) (0.91) Title*Post 0.25*** 0.25*** 0.25*** (5.97) (5.87) (5.74) Post 0.066*** 0.067*** 0.067*** (3.09) (3.08) (2.85) Controls? No No Yes No Matched Sample? No No No Yes Observations 305 610 610 576 Adjusted R2 0.07 0.07 0.07 0.08 Note: Robust t statistics in parenthesis. For the matched sample the standard errors are bootstrapped with 1000 repetitions. ***, * Statistically significant at 1% and 10%, respectively. Due to imbalances in some covariates, the second column reports the DD estimate while controlling for a set of predetermined covariates such as the gender, age, and educational level of the household head, his/her marital status, and the household size. The third column reports the DD estimate for a matched sample. All estimates are identical to the benchmark, suggesting that the differences in observed characteristics are not really driving the results. The ANCOVA estimates are shown below. Fig. 6 – ANCOVA Estimates – Land Title Impact on Credit Availability (2007, 2008) Credit Credit Credit Credit In t=1 ANCOVA ANCOVA ANCOVA Title 0.26*** 0.25*** 0.30*** 0.29*** (4.78) (6.70) (6.48) (6.15) Autocorrelation Na 0.68*** 0.69*** 0.67*** Na (20.52) (20.9) (19.32) Controls? No No Yes No Matched Sample? No No No Yes Observations 305 305 288 288 Adjusted R2 0.07 0.50 0.50 0.57 Note: Robust t statistics in parenthesis. For the matched sample the standard errors are bootstrapped with 1000 repetitions. ***, * Statistically significant at 1% and 10%, respectively. 25 Figure 6 shows estimates that are slightly higher than the DD estimates, except in the model without any controls. The benchmark was replicated in this table to make comparisons easier. It is worth noting that the ANCOVA specification improves the goodness-of-fit and the precision of the estimates. This is, in fact, expected given that the baseline plays an important role in the empirical analysis as shown by the autocorrelation coefficient. xv The analysis below explores different types of credit that a household could use or access, such as those outlined in Figure 2. Different Types of Credit This sub-section turns to the impact of land title on the use of and access to different types of credit. This section provides DD and ANCOVA estimates for four sources of credit usage: loyalty cards, commercial banks, relatives, and credit cards. All estimates are provided for the matched sample. Figure 7 – DD Estimates – Land Title Impact on Use and Access to Credit, By Credit Category (2007, 2008) DD ANCOVA Loyalty Bank Loan from Credit Loyalty Bank Loan Credit Cards Loan Relatives Card Cards Loan Relatives Card Land title 0.18*** 0.31*** -0.077*** 0.0083 0.18*** 0.31*** -0.076*** 0.0062 (5.03) (7.86) (-3.74) (0.26) (5.22) (7.96) (-3.74) (0.19) Autocorrelation Na Na Na Na 0.78*** 0.76*** 0.96*** 0.89*** Na Na Na Na (25.0) (19.1) (72.8) (42.6) Constant 0.35*** 0.075*** 0.87*** 0.26*** 0.10*** 0.043*** 0.037*** 0.10*** (8.00) (3.11) (27.8) (6.44) (4.73) (2.80) (3.07) (3.69) Matched sample Yes Yes Yes Yes Yes Yes Yes Yes Observations 576 576 576 576 288 288 288 288 Adjusted R2 0.03 0.15 0.00 0.00 0.59 0.33 0.68 0.67 Note: T statistics in parenthesis with standard errors bootstrapped with 1000 repetitions. ***, * Statistically significant at 1% and 10%, respectively. 26 The most striking result in figure 7 is the magnitude of the effect of land titles on credit borrowed from commercial banks. Interestingly, the DD and ANCOVA are basically the same in all cases. The only difference lies in the estimate’s precision, but even in this regard they are very similar. This is an interesting result, given that it is line with de Soto’s prediction regarding the link between property rights and credit availabilityxvi. It seems that through this intervention, land title reduced the credit constraints of the treated households. The results suggest that after receiving land title, households became less likely to borrow from relatives. As FAO (2014a, 2014b) claim, property rights can substitute for social networks as a risk management strategy, leading to a lower need to house relatives. Of course, having property rights may allow households to invest in social capital and could, in theory, lead to expanded social capital. There is some evidence that cash transfer programmes allow households to integrate into social networks, since they are able to invest in those networks. By increasing the value of assets and linking households more strongly to a location, property rights could play a similar role in expanding social ties (FAO, 2014a, 2014b). This, once again, is consistent with the prior findings that the households we surveyed were likely facing obstacles to borrowing from commercial institutions. Finally, the increase in the use of loyalty cards is consistent with households’ choices to use this channel to acquire durable goods, such as laundry machines, colour televisions, and microwaves, as in many cases loyalty cards provide discounts for customers using such credit lines. DD and FE estimates for the consumption of durable goods are shown in Figure A.2 (annex). Fixed effects estimates suggest that titled households are more likely to have a washing machine and a stove, but are less likely to have a freezer, although the coefficient is not very precise. The coefficient for having a new television is positive but statistically insignificant. These results suggest that treated households may have used credit to newly purchase or renew the stock of durable goods. xvii 27 These results shed light on the sorts of credit that might be more sensitive to land title interventions. From our estimates, there seems to be a depressed demand for credit lines available from commercial banks. This is in line with the prior assumption that property rights can be used as collateral, as predicted by economic theory, but also that titled households would opt to use credit to invest in their properties. xviii Robustness Check In this section we report fixed effects (FE) and random effects (RE) estimates to check the robustness of our results. Under the assumption that unobserved characteristics are not driving the results, we should not reject the null of a Hausman test comparing the FE and RE coefficients. Columns two to four of figure 8 show the RE and FE estimates. Given that the RE and FE point estimates are identical, there is no need to perform a Hausman test in this case. The point estimates are very similar to the DD and ANCOVA estimates discussed above. These results provide extra support for these results and are identical to the simple comparison of means reported in the first column. Fig. 8 – Robustness Check – Fixed and Random Effects on Use and Access to Credit Credit Credit Credit Credit Credit In t=1 RE FE RE FE Title 0.26*** 0.047 Na 0.0048 Na (4.78) (0.74) Na (0.080) Na Title*Post 0.25*** 0.25*** 0.25*** 0.25*** (5.91) (4.18) (5.83) (4.12) Post 0.064*** 0.042 0.067*** 0.067** (2.97) (0.45) (2.91) (2.06) Controls? No Yes Yes No No Matched Sample? No No No Yes Yes Observations 305 610 610 576 576 R2/Within R2 0.07 0.28 0.28 0.28 0.28 Note: Robust t statistics in parenthesis. For the matched sample the standard errors are bootstrapped with 1000 repetitions. ***, * Statistically significant at 1% and 10%, respectively. 28 We also run FE and RE estimates for different modalities of credit, as shown in Figure 9. Fig. 9 Robustness Check – Fixed and Random Effects on Use and Access to Credit by Credit Category RE FE Loyalty Bank Loan from Credit Loyalty Bank Loan from Credit Cards Loan Relatives Card Cards Loan Relatives Card Land title 0.18*** 0.31*** -0.077*** 0.0083 0.18*** 0.31*** -0.077*** 0.0083 (5.03) (7.86) (-3.74) (0.26) (3.55) (5.56) (-2.64) (0.18) Constant 0.35*** 0.075*** 0.87*** 0.26*** 0.35*** 0.083*** 0.89*** 0.25*** (8.00) (3.11) (27.8) (6.44) (25.4) (5.33) (104.5) (21.7) Matched sample? Yes Yes Yes Yes Yes Yes Yes Yes Observations 576 576 576 576 576 576 576 576 R2/Within R2 0.17 0.32 0.08 0.08 0.18 0.32 0.07 0.08 Note: T statistics in parenthesis with standard errors bootstrapped with 1000 repetitions. ***, * Statistically significant at 1% and 10%, respectively. The RE and FE point estimates are identical to those reported in Figure 7. The results are very robust and strongly suggest that the programme under investigation made the households from Jardim Canaã more likely to use and access credit, particularly from commercial banks. Heterogeneous Effect This section discusses two potential sources of heterogeneity: the labour market status and the gender of the household head. We investigate the first potential source of heterogeneity, because the treatment group has a higher share of formal workers than the comparison group; this could confound the results in spite of the fact that the regressions control for the labour market status of the household head. If the expansion in credit observed 29 in Brazil during the last decade somehow had more benefits for formal workers than for informal workers, the estimates would be biased. To check for heterogeneity we run the following DD regression model xix: (5) where Z is a dummy that equals 1 if the head is an informal worker or female. Fig. 10 – DD Estimates – Testing for Heterogeneous Effects (2007, 2008) Z=Informal Z=Female Credit Credit Credit Credit Title*Post 0.27*** 0.26*** 0.20*** 0.21*** (3.76) (3.65) (3.87) (4.07) Title*Post*Z -0.033 -0.026 0.13 0.10 (-0.38) (-0.30) (1.58) (1.26) Controls? Yes No Yes No Matched Sample? No Yes No Yes Observations 610 576 610 576 Adjusted R2 0.07 0.08 0.08 0.07 Note: Robust t statistics in parenthesis. For the matched sample the standard errors are bootstrapped with 1000 repetitions. ***, **, * Significant at 1%, 5% and 10%, respectively. The results do not support any source of heterogeneity from the household head’s status in the labour market. The point estimate for the interaction term under investigation is statistically insignificant and insensitive to the common support condition. This result is somewhat surprising, as one could expect formal workers to use more credit, given that they tend to face fewer constraints than informal workers. A plausible explanation could be that formal workers tend to depend less on credit, as they have a much less volatile income stream. In this case, informal workers would use credit more intensively to smooth the effects of idiosyncratic income shocks. Unfortunately, we are unable to test any of these hypotheses. The Papel Passado programme only registered titles on behalf of women, independent of their role under the household arrangement. Furthermore, evidence suggests that women may be more credit constrained than men (Khandker, 1998; Aghion and Morduch, 2005; Mel 30 et al., 2009), and that women tend to oppose home sale more strongly than men (Datta, 2006). Given these findings, the impact of land title on credit availability is assumed to be greater for females. The descriptive statistics above suggest that women in the treated area are less credit constrained then the men, whereas we observe the opposite trend in the comparison area. The third and fourth columns of Figure 10 report the ATT for household heads who are women. As with informality, the coefficients are not statistically significant and suggest that the programme has a similar effect, regardless of the gender of the household head. VI. Shedding Light on the Causal Chain This section aims to shed light on the mechanism underlying the impact of the programme on use of credit — specifically, the increase in credit borrowed from commercial banks. We know from the discussion above that titled households borrowed less from relatives and more from commercial banks compared to untitled households. We interpret this result as an indication that untitled households are likely to be credit constrained. In this section, we look at the impact of the titling programme on the price of houses. Unfortunately, there are 127 cases with zero value for this variable. Given the relatively low sample size in our study, we concentrate on the size of the effect rather than its precision. We provide estimates including observations outside the common support. The results are presented in the table below. Though insignificant in statistical terms, the mean effect is positive and relatively large, suggesting that the policy may have affected housing prices positively. In relative terms, the mean effect corresponds to an increase of 28 per cent over the comparison houses at the baseline (see figure 2). Our data do not allow us to test any particular theory of change due to study design and sample size restrictions. Even so, it seems that the programme may have increased the value of the main households’ assets. According 31 to Besley and Ghatak (2009), the effect of land titling on housing prices would be the underlying mechanism triggering the increase in credit use and access. Fig. 11 – Difference-in-Differences Estimates: Causal Chain House price Washing machine Adult labour supply Child labour (1) (2) (3) (4) (5) (6) DD 12,174.33 0.058 0.12 15.8*** 10.5 -5.10*** -3.13* (1.51) (0.80) (0.52) (3.82) (0.40) (-2.60) (-1.76) Sigma 21.4*** 15.1*** (25.4) (6.50) Observations 364 492 118 528 36 528 36 Note: Robust t statistics in parenthesis. ***, **, * Significant at 1%, 5% and 10%, respectively. Estimates in columns (1) and (2) consider the subsample of households for which credit borrowed from commercial banks remained constant and increased in the endline respectively. Columns (3) and (5) consider the subsample for which washing machine acquisition increased in the endline, whereas columns (4) and (6) use the subsample of households for which this did not happen. We used tobit regresssions for the adult labour supply. Child labour tobit regresssions did not converge, and we therefore estimated OLS regressions. The table also shows interesting results that add to the findings discussed in Moura et al. (2009) and Moura et al. (2014) regarding the impact of this programme on time allocation of household members. Moura et al. (2009) find that the land titling programme reduced child labour by seven hours per week on average. Moura et al. (2014) looked at the labour supply of adults. They show that the programme increased the labour supply of adults by about 12 hours per week, particularly at the lower tail of the weekly hours worked distribution. A possible causal chain underlying the observed time reallocation of adults and children would have to do with sense of security resulting from the intervention; that is, adults of untitled dwellings would work at home to protect their housing and consequently send their children to work outside the home. With tenure security, adults and children would experience a time reallocation, with children staying at home and adults working outside the home. This is the 32 channel outlined by Field and Torero (2002) xx. This paper suggests an alternative channel that is closer to that suggested by Besley and Ghatak (2009). The table above suggests that the programme increased the price of houses, probably because the newly titled dwellings could be bought and sold in the formal housing market. This increase in house values probably helped households to access credit from formal banks, as the value of their collateralisable assets grew as a consequence of the policy. In columns one and two, we show the effect of land title on the consumption of washing machines for households for which credit use did not change (column one), and for households for which credit use increased (column two). Though not statistically significant, the point estimate in column two is twice as high the one shown in column one. These results suggest that households that used more credit were more likely to consume durables such as washing machines. Since washing machines are time-saving durable goods, their consumption might be one of the reasons for the observed reallocation of time of adults and children in titled households. The last four columns present a similar exercise for the labour supply of adults and children. The estimates indicate that the adult labour supply increased more among households that acquired washing machines (15 hours per week vs. 10 hours per week). Similarly, the last two columns show that child labour decreased more among households that bought washing machines. Putting all these results together, it seems that titled households benefited from higher house values by accessing credit in commercial banks and by consuming time-saving durable goods (such as washing machines), which apparently helped them to reallocate adults’ and children’s time. It is important to bear in mind that these estimates do not allow a causal interpretation due to the way that we split the data to perform the analysis. 33 VII. Potential Caveats So far, most of the estimates have been given a causal interpretation. Specifically, we have interpreted the estimates as ATT. If not fully persuaded by the identification strategy used in this paper, one might argue, for instance, that the treated and control communities, despite being next to each other, are actually different, given the different profile of the households living in them. We tried to deal with the differences in observed characteristics by matching households at the baseline to make the groups as comparable as possible. Even so, one could still argue that because we have only two points in time, one before and one after the intervention took place, we cannot check whether the matched sample was actually following the same time trend as before the intervention. Also, because the treated households have more educated heads working in the formal sector, our estimates would be biased if the credit offered by commercial banks targeted people with that profile. Although we have not found a statistically significant difference between formal and informal workers’ use of credit, one could argue that this is a consequence of lack of power. To be conservative, we suggest that the most sceptical readers interpret these estimates as an upper bound effect of the programme. It is worth noting that the magnitude of the point estimates would still remain high even if reduced by half – about a 12 pp. increase in credit use and a 16 pp. increase in credit borrowed from commercial banks. Keeping the precision the same, the point estimates would still be statistically significant at conventional levels. However, our standard errors have also been estimated conservatively, because we do not take into account intra-cluster correlation. Taking the estimates in tables 6 and 8 as the main results, one can see that even doubling (or in some cases tripling) the standard errors, the coefficients would remain statistically significant at conventional levels. Given the challenges associated with our dataset, we argue that the land titling programme assessed in this paper very likely increased credit use in the treated community by an economically relevant factor. 34 Conclusion Although existing studies (such as Field, 2007) indicate that land titling programmes seem to affect positively households’ access to credit, this particular study aims to fill an important gap in the literature on property rights and credit use and credit access. Since de Soto’s Mystery of Capital (2000) there has been increasing interest in determining the extent to which better defined property rights affect the economic lives of the poor. This paper has presented new evidence of the value of formal property rights in urban squatter communities in a developing country by studying the relationship between the exogenous acquisition of land titles and credit use. Understanding the multiple channels through which land titles influence economic outcomes is particularly valuable for the governments of all developing countries that are considering the implementation of titling programmes to address informal urban housing. We applied difference-in-differences estimates to measure the effect of land title on credit use and access. The ATT estimates point to an impact of 25 pp., approximately 70 per cent, in credit use. The results remain robust when different specifications and sample compositions (matched or unmatched) are applied. The main results also show that land title has heterogeneous impacts across credit modalities, with the largest relating to the credit borrowed from formal banks. We found that titled households stopped borrowing from relatives and borrowed more from commercial banks. The credit borrowed from commercial banks increased threefold (from 8 pp. to 39 pp.). Heterogeneous effects were also provided to investigate whether formal workers and male household heads are more likely to use or access credit than their counterparts — informal workers and female heads, respectively. 35 The analysis also sheds light on the mechanisms through which land titling affected credit use and why households demanded credit by looking at what happened to the price of houses, the consumption of durable goods, and the labour supply of adults and children. In fact, fixed effects estimates suggest that titled households became more likely to have a washing machine and stove, but less likely to have a freezer. This finding provides support for the prior assumption that land titles would incentivise households to invest more in their houses and in goods that are time consuming, such as washing machines. This analysis suggests various possibilities for further research; for example, the impact of land titling on other economic variables such as education and health outcomes of children could also be analysed, as could potential spillover effects on land markets in the control community. Research in these areas would improve the assessment of how such programmes affect the lives of the millions of households living in urban squatter communities in developing economies across the world. 36 ANNEX A Figure A.1 Propensity Score: Logit Estimates for the Selection of the Treatment Group (2007) Dummy = 1 if a household lives Dummy = 1 household lives in the in the treated area (Canaã) treated area (Canaã) Variables (Unmatched Sample) (Matched Sample) Gender (=1 if have) 0.32 0.11 (0.48) (0.51) Ethnicity (non-white) 0.04 0.02 (0.45) (0.45) Marital status (=1 if have) 0.58 0.35 (0.47) (0.49) Age -0.03* -0.01 (0.01) (0.01) Weekly hours of adult work 0.02 0.01 (0.01) (0.01) Weekly hours of child labour -0.03 -0.01 (0.02) (0.02) Years of education (head) 0.14*** 0.05 (0.05) (0.08) Monthly income per capita -0.01** -0.01 (0.00) (0.00) TV (=1 if have) -1.48** -0.68 (0.69) (0.85) DVD (=1 if have) -0.64 -0.29 (0.53) (0.58) Radio (=1 if have) -1.68*** -0.60 (0.50) (0.84) Car (=1 if have) -0.28 -0.09 (0.45) (0.48) Washing machine (=1 if have) 2.19*** 1.06 (0.65) (0.92) Refrigerator (=1 if have) -6.07*** -2.76 (1.07) (2.15) Informal worker -1.73*** -0.75 (0.62) (0.85) Credit -0.17 -0.03 (0.43) (0.45) Constant 8.18*** 1.87 (1.62) (4.09) Pseudo-R2 0.62 0.63 Prob>Chi2(16) – Joint Test 0.00 1.00 Observations 305 288 Note: ***, **,* Statistically significant at 1%, 5% and 10%, respectively. 37 Figure A.2 – Durable Goods – (2007) Mean Mean A=B: Comparison (A) Treated (B) p-value TV 1.22 1.21 0.92 Washing Machine 0.82 0.80 0.88 Freezer/Refrigerator 0.54 0.58 0.73 Microwave 0.25 0.26 0.84 Source: Research from the Osasco Land Title Survey Figure A.3 – DD and FE Estimates for Consumption of Durable Goods DD FE TV Freezer Stove Washing Machine TV Freezer Stove Washing Machine Title -0.39*** 0.003 -0.36 0.71*** Na Na Na Na (-2.95) (0.03) (0.039) (5.18) Na Na Na Na Title*post 0.011 -0.058 0.054 0.36* 0.011 -0.05* 0.054*** 0.36*** (0.06) (-0.37) (0.99) (1.90) (0.53) (-1.75) (3.07) (3.81) Year 0.025 0.058 0.00 0.33 0.025* 0.05* 0.00 0.33 (0.24) (0.48) (0.00) (0.27) (1.75) (1.75) (0.00) (1.42) Matched sample? Yes Yes Yes Yes Yes Yes Yes Yes Observations 576 576 576 576 576 576 576 576 Note: ***, **, * Statistically significant at 1%, 5% and 10%, respectively. i See Associação dos Notários e Registradores do Brasil – ANOREG, 2007. The quotation’s translation into English is ours. 38 ii A credit score is a numerical expression based on a statistical analysis of a person's credit files. It is used to represent the creditworthiness of that person. iii Credit unions are member-owned financial institutions. These institutions are created and operated by their members, and profits are shared amongst the owners. iv Randomisation bias occurs, for example, when the need to recruit a greater number of applicants induces programme administrators to change programme admissions standards. A similar problem happens if individuals are aware of the randomised evaluation and choose not to apply to the programme given the lower chance of receiving benefits. In both cases, results obtained from the evaluation may not be generalised to a context in which the programme is not being implemented as a randomised trial. v Contamination bias occurs when members of the control group seek and receive alternative forms of treatment. This is usually only a problem when there are close substitutes for the programme. vi The questionnaire is available upon request. vii The second Osasco Office of Registration (2.º Cartório de Osasco) provided us with the exact date that each household received its property title after being formally authorised to do so by Osasco's City Hall. viii Many stores in Brazil allow households to finance the acquisition of durables and non-durables goods using credit cards. In many cases, stores charge the same price if the good is bought at once or in installments. ix For example, a formal Brazilian employee usually receives a health care plan for the whole family, subsidised transportation, and meal plans. Furthermore, formal employees have FGTS—a compulsory savings account under Brazilian labour law. FGTS stands for the Fundo de Garantia por Tempo de Serviço (Length of Service Guarantee Fund). Under the FGTS, employers deposit 1/12 of the worker’s pay into a restricted bank account, the balance of which is released to the worker if/when he/she is fired without good cause. x In our data sample, 233 households include informal workers, representing 92 per cent of the workers of the comparison group and 64 per cent of the treated group (see Figure 2). xi This finding may go against what one might expect based on human capital theory, but it is consistent with what we observe in our dataset. xii According to Abadie (2005) and Blundell and Dias (2009), the assumption of parallel trends in the DD framework might be more difficult to defend when the sample of treatment and comparison groups is not balanced at the baseline. Abadie (2005), for instance, proposes a semi-parametric procedure to estimate the difference-in-differences matching estimator using weights computed based on the propensity score. We estimate the propensity score parametrically, using a logit regression, and run the difference-in-differences regression in the common support. To check balance, we use the pscore command in Stata. Balance is achieved with 7 strata and the results are available upon request. This estimator is known as the difference-in-differences matching estimator and was first suggested by Heckman et al. (1997) and used afterwards by, for instance, Smith and Todd (2005), Angelucci and Attanasio (2009), and Blundell et al. (2010). xiii The increase in credit use among the control households is observed for all types of credit that will be discussed below, except for credit borrowed from relatives. xiv The marginal effects obtained from logit regressions are almost identical to those obtained via linear probability model regressions. xv See McKenzie 2012 for a discussion of this point. xvi According to de Soto (2000), well-defined property rights, such as formally titled property, would enable poor entrepreneurs to access credit by using their property as collateral. 39 xvii This would very likely have implications for intra-household time allocation, as durable goods are expected to free up time for adults, particularly women, to work outside the home. xviii These results contradict Field’s findings (2004). 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