essays on entrepreneurship and management by rafael perez ..., Exams of Entrepreneurship

Download essays on entrepreneurship and management by rafael perez ... and more Exams Entrepreneurship in PDF only on Docsity! ESSAYS ON ENTREPRENEURSHIP AND MANAGEMENT BY RAFAEL PEREZ RIBAS DISSERTATION Submitted in partial fulfillment of the requirements for the degree of Doctor of Philosophy in Economics in the Graduate College of the University of Illinois at Urbana-Champaign, 2014 Urbana, Illinois Doctoral Committee: Professor Darren Lubotsky, Chair Professor Roger Koenker Professor Murillo Campello Professor Ron A. Laschever Professor Richard Akresh ABSTRACT This dissertation consists of three essays on financial and institutional determinants of entrepreneurship and the importance of management style. Chapter 1: Direct and Indirect Effects of Cash Transfers on Entrepreneurship In this chapter, I exploit a liquidity shock from a large-scale welfare program in Brazil to investigate the importance of credit constraints and informal financial assistance in explaining entrepreneurship. Previous research focuses exclusively on how liquidity shocks change recipients’ behavior through direct effects on reducing financial constraints. However, the shock may also produce spillovers from recipients to others through private transfers and thereby indirectly affect decisions to be an entrepreneur. This essay presents a method for decomposing the liquidity shock into direct effects associated with relieving financial con- straints, and indirect effects associated with spillovers to other individuals. Results suggest that the program, which assists 20 percent of Brazilian households, has increased the number of small entrepreneurs by 10 percent. However, this increase is almost entirely driven by the indirect effect, which is related to an increase in private transfers among poor households. Thus the creation of small businesses seems to be more responsive to the opportunity cost of mutual assistance between households than to financial constraints. Chapter 2: Bankruptcy Law and the Creation of Small Business This essay investigates the relationship between bankruptcy law and the creation of small businesses by using the 2005 reform in the U.S. as a natural experiment. In theory, a pro-debtor law provides an insurance against business failure and thereby encourages en- trepreneurial investments. On the other hand, a pro-creditor law inhibits debtor’s abusive ii ACKNOWLEDGEMENTS I wish to express my deepest gratitude to my advisor Darren Lubotsky. He has generously dedicated his time and expertise to guide me through all the steps that takes to earn a Ph.D. His role was crucial to get me focused and set my short- and long-term goals. Without him I could not have completed this dissertation. I am also very grateful to my mentor, Murillo Campello. He has changed the course of my academic career, giving the most valuable professional advice that I have ever had. I have worked with him since an early stage of the graduate school and this relationship has taught me so many priceless lessons. The third role model to whom I would like to express my gratitude is Roger Koenker. His lessons inside and outside the classroom were just mind-blowing. Our meetings made my six years in Champaign-Urbana worthwhile. I am very thankful to him for teaching me and openly discussing a broad range of empirical methods in such a pleasant way. For their comments and professional advice, I am also grateful to the other members of my dissertation committee: Richard Akresh and Ron Laschever. Likewise, I should express my sincere appreciation to Dan Bernhardt, Heitor Almeida, and George Deltas for their support. For comments and suggestions that helped me to improve this dissertation, I am thankful to David Albouy, François Bourguignon, Habiba Djebbari, Francisco Ferreira, Giorgia Giovannetti, and Simon Bordenave. I would like to give very special thanks to Professor Werner Baer for his constant effort to support all Brazilian students at the University of Illinois, including myself. I am also grateful for the support given by Professors Anil Bera, Kristine Brown, Daniel McMillen, v Stephen Parente, Martin Perry, Walter Sosa, Joseph Petry, and Mary Arends. It is important to acknowledge the contribution given by friends and colleagues, who have provided fruitful discussions and helpful feedbacks: Rafael da Matta, who has helped me in every single step of this journey, from the Ph.D. application to the job placement, and Igor Cunha, who is the co-author of the third chapter of this dissertation; as well as Marco Rocha, Breno Sampaio, Gustavo Sampaio, Euler de Mello, Leonardo Lucchetti, Monse Bustelo, Sarah Miller, Andreas Hagemann, Fabricio D’Almeida, Leandro Rocco, Paulo Vaz, Diloa Athias, and Joao Bernardo Duarte. It was also an honor to share the same classroom with outstanding students such as Raul, Sergey, Angelo, Bruno, Josh, Seyed, Taka, Yashar, Young, Maria, Rafael Nivin, Eric, and Sascha. My friends and former colleagues, Fabio Veras Soares, Sergei Soares, Guilherme Hirata, and Elydia Silva, have also contributed to this achievement. So have my former advisors, Ana Flavia Machado and Lovois Miguel. Thank you all! Thanks to the friends that made my stay in Champaign-Urbana memorable: Felipe, Rafael Nogueira, Mauricio, Diego, Claudia, Mariangela, Cintia, Elisa, Ludmila, Renato, Anamaria, Virginia, Rayane, Vivi, Loló e Renata, Kiko e Thais, Pipoca e Aline, Luiz Fe- lipe, Andre e Rosa, Jimmie, Robert, Denis, Aisha, and all members of the Capoeira Club, Jonathan, Max, Shin, Stan, Sergei, Marcin, and all members of the Judo Club, and all Gentlemen, Hammeroids, and Barcelona players. Finally, nothing would be possible without the love and support of my parents, Clairton and Silvia Ribas, my brothers, Dado, Rena, and Rica, and my fiancée, Marjorie Souza. This dissertation is dedicated to my parents. vi Contents Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1 Chapter 1: Direct and Indirect Effects of Cash Transfers on Entrepreneurship 5 1.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 5 1.2 Theoretical Framework . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 1.3 Program and Data Description . . . . . . . . . . . . . . . . . . . . . . . . . 21 1.4 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33 1.5 Main Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 40 1.6 Potential Mechanisms . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 44 1.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 53 Chapter 2: Bankruptcy Law and the Creation of Small Business . . . . . . 65 2.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 65 2.2 The U.S. Personal Bankruptcy Law . . . . . . . . . . . . . . . . . . . . . . . 69 2.3 Data and Descriptive Statistics . . . . . . . . . . . . . . . . . . . . . . . . . 74 2.4 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 78 2.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 83 2.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87 Chapter 3: Contrasts in Styles and Managers’ Impact on Corporate Policy 88 3.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 88 3.2 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 95 3.3 What drives turnovers? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 99 3.4 Estimation Method and Inference . . . . . . . . . . . . . . . . . . . . . . . . 103 3.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 117 3.6 Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 127 Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 129 vii ploits a liquidity shock from a large-scale welfare program in Brazil to investigate the impor- tance of credit constraints and informal financial assistance in explaining entrepreneurship. Previous research focuses exclusively on how liquidity shocks change recipients’ behavior through direct effects on reducing financial constraints. However, the shock may also pro- duce spillovers from recipients to others through private transfers and thereby indirectly affect the decision to be an entrepreneur. Accordingly, I present a method for decomposing the liquidity shock into direct effects associated with relieving financial constraints, and indirect effects associated with spillovers to other individuals. Results suggest that the program, which assists 20 percent of Brazilian households, has increased the number of small entrepreneurs by 10 percent. However, this increase is almost entirely driven by the indirect effect, which is related to an increase in private transfers among poor households. Thus the creation of small businesses seems to be more responsive to the opportunity cost of mutual assistance between households than to financial constraints. The second essay, “Bankruptcy Law and the Creation of Small Business,” investigates the relationship between personal asset protection and the creation of small businesses by using the 2005 bankruptcy reform in the U.S. as a natural experiment. In theory, a pro-debtor law provides an insurance against business failure and thereby encourages entrepreneurial investments. On the other hand, a pro-creditor law inhibits debtor’s abusive behavior, improving the selection of projects. The reform was intended to reduce the number of abusive filings and can be viewed as 2 a shock that has affected each state in a different way. Although changes in state laws are often related to economic conditions, this reform was not triggered by any state in particular. The reform has actually lessened debtor’s asset protection yielded by state laws. Based on previous state exemption levels, I can identify households that were more and less affected by the reform. Results confirm the positive relationship between homestead exemptions and entrepreneurial activity, but this relationship is not necessarily causal. The reform, on the other hand, has only affected the creation of unincorporated businesses, whose all debt is legally considered their owners’ personal debt. The rate of incorporated businesses does not seem to be affected by changes in asset protection. The third essay of this dissertation, “Contrasts in Styles and Managers’ Impact on Cor- porate Policy,” approaches another dimension of economic productivity related to how large firms are managed: can differences across firms be explained by their managers’ skills? On one hand, some studies argue that managers do have different styles (e.g., Bertrand and Schoar, 2003). On the other hand, other studies show that their styles have no effect on corporate decisions and, as a result, on their performance (Fee, Hadlock, and Pierce, 2013). This debate is critical since CEO compensation increased 127 times faster than worker com- pensation in the last 30 years, with some results questioning if executives are worth the money. In collaboration with Igor Cunha, I propose a new approach to study how corporate policies are influenced by their top executives. First, we estimate a Bayesian random-effect model to estimate the contribution of executive-specific effects and firm-specific effects to the variance of corporate financial policy and performance. Then we employ empirical Bayes 3 simultaneous tests on the executive effects to verify heterogeneity in managers’ styles. Our results not only corroborate what is already found by Bertrand and Schoar (2003), showing that several executives carry their own style to their companies, but also show that their effect is almost negligible compared to firm- and industry-specific effects. 4 households are also affected by PROGRESA/Opportunidades in rural villages in Mexico. They suggest that these households increase food consumption by receiving private transfers from program participants and reducing their precautionary savings.4 In another study, Bandiera et al. (2009) assess the effect of asset transfers in Bangladesh. They show that this program has indirect effects on time allocation in risk-sharing networks and on durable consumption in family networks. In both studies, indirect effects are identified using non-participants, but their definition of direct effect is essentially the definition of ‘effect on the treated.’ As a matter of fact, “treated” households are also subject to spillovers. Even if all households are participating in the program, there may be externalities that either boost or attenuate the direct response to those transfers. This distinction is critical to understand targeted interventions, such as CCT and microfinance. On one hand, findings that are based on the comparison of treated and untreated villages tend to be interpreted as an exclusive consequence of participants’ responses. On the other hand, studies that compare individuals rather than villages might be biased by ignoring spillovers. According to Heckman, Lochner, and Taber (1998), the conventional treatment effect model is based on a partial equilibrium framework. If the intervention has general equilibrium consequences, then the net effect also depends on who else is treated and the interaction between the treated and the untreated. Other studies suggest that the liquidity shock promoted by cash transfers increases entrepreneurial activity at both the intensive margin, raising investments and profits (de Mel, 4Lehmann (2013) contests Angelucci and De Giorgi’s (2009) interpretation and suggests that the indirect effect on food consumption operates by raising non-food prices. 7 McKenzie, and Woodruff, 2008; Gertler, Martinez, and Rubio-Codina, 2012), and extensive margin, encouraging participants to start their own business (Bianchi and Bobba, 2013; Bandiera et al., 2013; Blattman, Fiala, and Martinez, 2013). In some of these studies, how- ever, the randomization of ‘treatment’ was made at the village-level, which implies that the effect should be viewed as the sum of individual and local responses (Hudgens and Halloran, 2008). Namely, what is often interpreted as an individual shock, which lessens financial constraints, could actually be a locally aggregate shock, which also affects other households in the same village. Another limitation in the current evidence is that most of randomized controlled trials (RCTs) are either restricted to rural areas, where job opportunities other than work in one’s own farm are scarce, or limited to small-scale pilots, which hold uncertainty about their maintenance. Therefore, little is known about the response of households to those programs once they reach urban centers as a permanent policy of social protection (Behrman et al., 2012). Moreover, the evidence on informal risk-sharing arrangements also comes mostly from rural villages (Fafchamps, 2011). Unlike those interventions, Bolsa Famı́lia is a widespread, large-scale program that has been introduced not only in rural and isolated areas, but also in large cities in Brazil. In 2006, about 20% of Brazilian households were already covered by the program and 70% of them were living in urban settlements. Accordingly, I exploit this intervention to inves- tigate small entrepreneurial activity and informal risk-sharing mechanisms in urban areas. As most of the literature, I define as entrepreneurs those who are either self-employed or small business owners (e.g., Blanchflower, 2000; Hurst and Lusardi, 2004). Furthermore, to 8 consider self-employment as an investment opportunity rather than a way to conceal earn- ings, I distinguish entrepreneurs from those who are self-employed in the informal sector. Informal self-employment is considered another type of occupation in which workers are not covered by social security and whose earnings cannot be verified by the government. While small entrepreneurs earn on average 45% more than formal employees per hour, the informal self-employed earn 30% less. Although the assignment of benefits in Bolsa Famı́lia is not random, I demonstrate that this is not a concern as long as the endogenous assignment of participants is not related to the overall amount of transfers received in the entire village. Namely, the fact that some poor households are more likely to participate in the program than others only affects the way the transfers are locally distributed. The total number of transfers per city or village is considered given because, from 2003 to 2007, the program was phased in based on a previ- ously drawn poverty map. As a result, each municipality should have a limited number of transfers to be offered. Then instead of comparing participants and non-participants in the same municipality, the overall effect is estimated simply by comparing municipalities using a difference-in-difference model. To relax the assumption of exogenous program size, this variable is also instrumented by the poverty map. Then a verifiable condition for the Instru- mental Variable (IV) approach is that the relationship between poverty and entrepreneurship does not change over time. Namely, there is no convergence in the entrepreneurship level across municipalities. Once the overall effect is consistently estimated, the direct and indirect effects are cal- culated by a two-step procedure. First, based on the previous assumptions, I estimate the 9 Section 1.6 presents tests for potential mechanisms, including confounding factors. Section 1.7 concludes the chapter. 1.2 Theoretical Framework To understand why cash transfers could have an indirect effect on entrepreneurship, I present a simple model in which being formally self-employed has a fixed cost. For equally poor in- dividuals, this fixed cost cannot be covered by formal credit due to their lack of collateral and high interest rates. The insufficient wealth can also make them unable to insure against business failure and then less willing to take risks (Bianchi and Bobba, 2013). These con- straints drive us to conclude that an individual liquidity shock should increase their chances of being self-employed. On the other hand, the formal market is not the only source of credit and insurance. Bilateral exchanges between neighbors, friends, and relatives might be a way in which small entrepreneurs cope with startup costs and business risks. Although empirical studies suggest that informal risk-sharing mechanisms do not fully compensate market failures (Townsend, 1994; Hayashi, Altonji, and Kotlikoff, 1996; Ravallion and Chaudhuri, 1997),7 efficiency is of- ten achieved within social networks (Fafchamps, 2000; Fafchamps and Lund, 2003; DeWeerdt and Dercon, 2006). According to Bloch, Genicot, and Ray (2008), social networks have the role of lessening information asymmetries and commitment constraints among their mem- bers. One may call this role social capital, which lowers the transaction costs of obtaining credit and insurance (Murgai et al., 2002; Fafchamps and Minten, 2002). 7See Ogaki and Zhang (2001) for an evidence favoring the full risk-sharing hypothesis at the village level. 12 With low transaction costs, low-skilled individuals do not necessarily spend all the cash transfer, but they may also lend to someone with better entrepreneurial skills to increase their income in the future. At the same time, small entrepreneurs need not count only on their endowments to start their venture. In this model, the fraction of eligible individuals participating in risk-sharing networks is the key to explain the size of direct effects, which lessens financial constraints, and the size of an indirect effect, which reduces the costs of informal credit and insurance. 1.2.1 Setup Consider a continuum of individuals who live for two periods and are heterogeneous in their entrepreneurial skills, q. All individuals maximize their expected utility, U , by choosing their consumption in period 1, c1, and consumption in period 2, c2: U = u (c1) + E [u (c2)] , where E [.] is the expectation operator and u (.) exhibits decreasing absolute risk aversion, so that u′′ < 0 and u′′′ ≥ 0.8 In period 1, these individuals are endowed with an initial wealth, a, and have to choose their future occupation, which can be either working in a low-skilled job (L) or working in their own business (M). Choosing the low-skilled job has no cost and pays w in period 2. To start their business, however, they must acquire capital in the first period, which costs k. This capital, along with the time allocated to self-employment in period 2, yields 8A time discount factor could be included, but it is not relevant for this problem. 13 either q with probability λ or δ otherwise. Namely, q represents the total revenue in case of business success, while δ is what they receive for reselling their capital (after depreciation) in case of failure. Another interpretation is that k represents the cost of formalization for the self-employed and δ is what they receive from social security (Straub, 2005). In summary, individual’s income before transfers and savings is: I1 ≡    a if L a− k if M and I2 ≡    w if L q w.p. λ if M δ w.p. 1− λ if M Depending on their entrepreneurial skills, q, self-employment (M) increases the expected payoff of some individuals.9 Nonetheless, I should also consider that it is riskier than a salaried job (L), so that δ < w and λ ∈ (0, 1). In addition to the initial endowment and earnings, poor individuals are entitled to cash transfers in period 1, d1, and in period 2, d2, with d1 = d2 = d. However, receiving d2 is conditional on eligible individuals staying poor based on an eligibility rule. With this rule, only those with verifiable earnings, I2, less than or equal to w remain eligible for the benefit. For those whose q > w, λ becomes not only the probability of business success, but also the probability of losing the transfer if self-employed. Let ζ indicate whether the eligibility rule is applied (ζ = 1) or not (ζ = 0). 9Other types of heterogeneity could be assumed, such as in wealth, risk aversion, and probability of success. However, with heterogeneous payoffs and risk-averse individuals, wealth heterogeneity becomes irrelevant. Heterogeneity in either risk aversion or probability of success would essentially yield the same results, but with a more complex insurance market. 14 If the eligibility rule is applied (ζ = 1), then an increase in future transfers, d2, will have an ambiguous effect. On one hand, it still provides insurance against business failure (IE). On the other hand, it increases the return of being wage employed, L, because choosing self-employment reduces the chances of receiving d2. This negative response is defined as the eligibility effect (EE): EE ≡ ∂y ∂d2 ∣∣∣∣ ζ=1 − ∂y ∂d2 ∣∣∣∣ ζ=0 ∝ −λu′ [q̂ + d2 + s∗M (q̂)] < 0 (1.3) Depending on how high is the probability of business success, λ, the eligibility effect can prevail over the insurance and credit effects — i.e., CE+ IE+EE < 0. Thus individuals at the margin of indifference might prefer keeping receiving a transfer than starting a business that does not pay much more. Proposition 1.1 (Effect of Cash Transfer with Credit and Insurance Constraints) Assume that individuals can neither borrow nor trade insurance. Under no eligibility rule, cash transfers have a positive net effect on the entrepreneurship rate. However, if future transfers are subject to an eligibility rule, then the net effect is ambiguous and decreasing in the probability of business success, λ. 1.2.2.2 Aggregate Liquidity Shock with Risk-Sharing Consider a risk-sharing network in which transaction costs are irrelevant, so that its members can efficiently trade bonds and insurance in the first period. The repayment of bonds is assumed to be contingent on business success in period 2.11 If the investment made by entrepreneurs is not successful, then they receive the insurance that they bought rather than 11Contingent bonds can also be interpreted as an insurance that entrepreneurs sell to non-entrepreneurs. Evidence of contingent loan repayment is presented by Udry (1994) and Fafchamps and Gubert (2007). 17 paying their loans. Another way of setting this model is assuming that credit and insurance are provided through gift exchanges without commitment (Kocherlakota, 1996; Foster and Rosenzweig, 2001). If the business is successful and the entrepreneur becomes richer, then a more valued gift is expected in return. Otherwise, non-entrepreneurs are expected to help entrepreneurs with their loss. The ratio between what is given in period 1 and what is received in period 2 defines the implicit prices of bonds and insurance. Given the equilibrium prices in this network, all individuals are now able to optimally transfer utility across periods and states — i.e., they are neither credit constrained nor insurance constrained. Therefore, the direct effect of cash transfers on the occupational choice depends only on the eligibility rule. If eligibility rule is not applied, the liquidity shock just changes the individual demand for credit and insurance, but it does not affect their occupational choice, CE = IE = 0. Otherwise, an increase in future transfers, d2, reduces the relative gain of being self-employed with respect to wage employment (EE). On the other hand, the cash transfered in both periods will also lower the cost of risk- sharing by changing the equilibrium prices of bonds and insurance. With more cash in hands, non-entrepreneurs will be more willing to share the risk with entrepreneurs, whereas entrepreneurs will reduce their need for inter-household transfers. As a result, the decreasing cost of risk-sharing gives the opportunity for slightly less-skilled individuals to invest in a more profitable occupation. Therefore, in an efficient risk-sharing arrangement, an aggregate liquidity shock will be used to cover the cost of capital, k, and the possible losses, w − δ, of a larger fraction of entrepreneurs. 18 Let y∗ be the Pareto efficient entrepreneurship rate among individuals in the same net- work. The general equilibrium effect (GE) of cash transfers is given by the overall effect on y∗ minus the direct response, which only comprises the eligibility effect, EE: GE ≡ dy∗ dd1 + dy∗ dd2 − EE > 0. (1.4) Proposition 1.2 (Effect of Cash Transfer in a Risk-Sharing Network) Assume that individuals belong to a risk-sharing network. The direct effect of cash transfers on the deci- sion of being an entrepreneur is negative due to the eligibility rule. However, the aggregate shock of cash transfers has also a positive indirect effect by lowering the cost of risk-sharing. 1.2.2.3 Direct and Indirect Effects and the Size of Risk-Sharing Networks Finally, consider a population in which some individuals participate in risk-sharing networks and others do not. In particular, let N be the number of risk-sharing networks in this population and αj be their size with j = 1, . . . , N . Note that ( 1− ∑N j=1 αj ) is the fraction of individuals who do not belong to a network, which are labeled as group 0. Also, for any j = 1, . . . , N , q̂j ≤ q̂0 — i.e., despite the network size, individuals connected to one has at least as much chance to be an entrepreneur as those who are not. The reason is they can always lean on their own savings if the price of insurance in their network is too high. If individuals are randomly distributed among these networks, then the relationship be- tween entrepreneurship rate and cash transfers is the following:12 ∆y ≈ (β1 + β2)∆d, (1.5) 12The assumption of exogenous networks is not necessary. Even if individuals are assorted based on q, for any j = 1, . . . , N , q̂j ≤ q̂0 still holds. 19 children up to 15 years old or pregnant women were eligible for the program. The monthly benefit was composed of two parts: a) US$38 for extremely poor families regardless of the number of children, and b) US$11 per children, up to three, for poor families. Thus an extremely poor family should receive a benefit between US$38 and US$72, whereas a moderately poor family should receive between US$11 and US$34.13 Like Bolsa Escola and Bolsa Alimentação, these benefit require a household commitment in terms of child education and health care. However, if the family is registered as extremely poor with no child, the US$38 transfered is actually considered unconditional. Families that receive the benefit can be dropped from the program not only in case of not complying with the conditionalities, but also when their per capita income becomes greater than the eligibility cut-off point. During the period covered by this study, whenever it was found that the household per capita income had been above the eligibility threshold, the family would be excluded from the payroll. Moreover, families are required to update their records in the single registry of social policies (Cadastro Único) at least once every two years. As for monitoring of the income information, the Federal Government regularly matches beneficiaries’ records with other governmental databases, such as the database on formal sector workers from the Ministry of Labor and Employment and the database of pensions and other social assistance programs. For instance, the government found that 622,476 participant households had earnings above the eligibility cutoff from October 2008 and February 2009. From this total, 451,021 13In 2004, the extreme poverty line for the program was US$33, the poverty line was US$66, and the value of the benefit per child was US$10. 22 households had their benefit canceled. From cross-checking its databases, the government had canceled the benefit of more than one million households from 2004 to 2008, which represents about 40% of the total number of withdraws. 1.3.2 Program’s Targeting In order to identify poor families around the country, local governments (municipalities) are free to decide about the priority areas and how the registering process takes place. However, they do receive some guidelines, under the form of quotas on the number of benefits. This cap of benefits is intended to prevent local governments from spending the federal transfers irresponsibly and using them for electoral purposes. As a result, each municipality has a maximum number of benefits that can be distributed, which is given by the estimated number of poor households. Although the program size cannot growth for electoral purposes, de Janvry, Finan, and Sadoulet (2012) show that its local performance has raised the chances of mayors being re- elected. Namely, politicians cannot take advantage by distributing more benefits, but they can be rewarded by the way the total number of benefits is distributed. The municipal quotas were initially defined by a poverty map, made by the National Statistics Office (Instituto Brasileiro de Geografia and Estat́ıstica, IBGE). This map was made using both the 2001 Household Survey and the 2000 Demographic Census and was used for the quotas until 2006, when it started being annually updated. In other words, given the target of 11 million families in the whole country, the 2001 poverty map guided how the program should have gradually grown across municipalities from 2003 to 2006. 23 Although the local government has the responsibility of registering poor families in the Single Registry (Cadastro Único), this registration does not mean automatic selection into the program. Registered families still have to prove they receive per capita income under the eligibility cut-off point and the total number of benefits cannot surpass the local quota. Under this cap, the order of eligible households is managed by the National Government and is based on per capita income and number of children. Figure 1.1 confirms that the number of benefits per municipality had strongly depended on the previous number of poor households, estimated using data from 2000 and 2001. In the top panel, we observe the relationship between the proportion of poor households (poverty headcount) in 2000, calculated using the Demographic Census, and the proportion of households covered by the program (program coverage) in 2004 and 2006, according to the official records. The initial poverty headcount explains 77% of municipal coverage in 2004, when the program was still expanding and had not reached the cap in most municipalities. In 2006, when the program reached its target, the relationship became even stronger and closer to the 45-degree line. 24 1.3.3 Data 1.3.3.1 Panel Sample and Variables All the data come from the National Household Survey (Pesquisa Nacional por Amostra de Domićılios, PNAD). This survey, which collects a broad set of information on demographic and socio-economic characteristics of households, included a special questionnaire on cash transfer programs in 2004 and 2006. This questionnaire asked whether any member of the household was beneficiary of each cash transfer program that was in place at the time of the survey. Henceforth, I consider as Bolsa Famı́lia all previous programs that had a similar goal and design (e.g., Bolsa Alimentação, Cartão Alimentação, Bolsa Escola, and PETI). In addition to these two survey years, I use the 2001 PNAD as a baseline. In 2001, the Bolsa Famı́lia program had not taken place yet and the other cash transfer programs did not have a significant size. However, I have to control for the small coverage of other programs that might contaminate the baseline outcomes. Accordingly, I identify those households receiving cash transfer from other social programs using the typical-value method developed by Foguel and Barros (2010). This method basically matches parts of household income, under the entry of ‘other incomes,’ with typical values transfered by each program. The PNAD is a cross-sectional survey, so it does not interview the same households every year. Thus I cannot construct a panel of households or even individuals. However, for each decade — i.e., the period between two Demographic Censuses —, the replacement of households on its sample occurs within the same census tracts.16 Namely, once a census 16A census tract is a neighborhood that has between 250 and 350 households in urban areas, 150 and 250 households in suburban areas, 51 and 350 households in informal settlement areas, 51 and 250 households in rural areas, and at least 20 households in indigenous areas (IBGE, 2003). 27 tract was selected for the sample in 2001, it kept being surveyed until 2009. Although they are not geo-referenced because the key variable is encrypted, we are able to identify the same census tracts and municipalities through the years. This sampling scheme permits the estimation of a fixed-effect model, described later in this chapter. Given the common characteristics of entrepreneurs, the sample is restricted to men who are between 25 and 45 years old and reside in urban areas. Indeed, empirical studies show that men are more likely than women to pursue entrepreneurial activity (Blanchflower, 2000; Karlan and Zinman, 2010). They also show that the probability of being an entrepreneur is increasing in age, but the probability of starting a new business is decreasing after 30 years old (Ardagna and Lusardi, 2010). Moreover, the desire for being self-employed is decreasing in age (Blanchflower, Oswald, and Stutzer, 2001). I also exclude public servants, people with higher education, and employers with more than five employees from the sample. Even though 6% of public servants were participating in the program in 2006, they are less likely to change occupation due to their job stability. The last two groups were excluded because only 1% of them were receiving the benefit in 2006, so they are not considered eligible for the transfer. In addition, business with more than five employees could already be well-established, so they are less sensitive at the extensive margin.17 Because of the exclusion of observation from the original sample, the survey weights are calibrated so that the three years have the same importance in the analysis. Table 1.2 presents the average number of observations per municipality in the final sample. About 130 households and 50 prime-age men are interviewed by municipality on average 17The exclusion of these employers reduces the sample by 1%, with no implication for the results. 28 every year. For some small municipalities, the number of observations may not be large enough to yield accurate estimates. However, the smaller the town, the more homogeneous is the population. Under such a circumstance, the program coverage at municipal level, which is the main intervention investigated in this paper, is given by the proportion of prime-age men living in a household that receives the conditional benefit. Table 1.2: Number of Observations per Municipality Std. Number of Mean Dev. Min. Max. municipalities 2001 Number of households 128.1 290.4 19 3,505 796 Number of sample-eligible men 52.4 128.1 5 1,571 796 2004 Number of households 136.8 305.1 23 3,575 796 Number of sample-eligible men 54.3 131.8 5 1,751 796 2006 Number of households 143.8 322.7 28 3,884 796 Number of sample-eligible men 56.4 136.1 5 1,753 796 ‘Sample-eligible men’ comprise men aged between 25 and 45 years old, with no college degree, and living in urban areas. This sample also excludes public servants and employers with more than five employees. According to Blanchflower (2000) and Blanchflower, Oswald, and Stutzer (2001), self- employment is the primary form of entrepreneurship. For this reason, I classify as en- trepreneurs those who either have this type of occupation or are small business owners. However, to distinguish entrepreneurial activity and informality, the definition also requires that they either perform a high-skilled job or contribute to social security. Namely, en- trepreneurs are subject to taxes and less vulnerable than informal workers in general. On the other hand, the government cannot track earnings of workers in the informal sector, whereas entrepreneurs have their earnings partially revealed on the government records. 29 Figure 1.2: Relationship between Entrepreneurship and Program Coverage 2001 2006 2006 − 01 difference 0 .01 .02 .03 ra te c ha ng e 0 .02 .04 .06 .08 en tr ep re ne ur sh ip r at e 0 .2 .4 .6 .8 2006 program coverage Entrepreneurship rate is measured by the proportion of small entrepreneurs per municipality. ‘2006 - 01 difference’ is the difference between entrepreneurship rates in 2006 and 2001 per municipality. Program coverage is measured by the proportion of individuals participating in the program in 2006. Municipalities where the program coverage was greater than 5 p.p. in 2001 are not included. Besides the increase of the formal sector and gradual expansion of Bolsa Famı́lia, other socio-economic improvements are observed in Table 1.3. As regards education, the proportion of adult men with a high school diploma increased 10 p.p. in five years. The same increase is seen in high school enrollment rate. In terms of health care, child mortality decreased from 12.7 deaths per 1,000 children up to 5 years old to 9.8 deaths. Finally, the proportion of houses linked to the sewer system increased 3 p.p. Given all the socio-economic improvements that happened in Brazil, it is critical to control for these variables to account for demographic changes and other social policies. 32 An important mechanism in which the program may affect entrepreneurship is through private transfers. This type of income is calculated as the sum of donations and other incomes, excluding retirement benefits, other pensions, rental earnings, and social benefits. The percentage of households receiving private transfers should increase along with liquidity in poor communities if they adopt informal risk-sharing strategies. In Table 1.3, we observe that this rate went from 4.3% in 2001 to 7.7% in 2006. 1.4 Empirical Strategy The empirical strategy consists of a difference-in-difference model estimated using a three- period dataset. As discussed above, the program coverage has been strongly driven by observables. According to Proposition 1.3, presented below, this condition is sufficient for the identification of the overall effect of the program using a model with municipality-level fixed effects. Furthermore, the identification assumption is weak enough to ignore the fact that some households are more likely to go after the benefit than others. The reason is that self-selection at the local level is not a concern when the comparison of treated and control observations occurs between municipalities, and not within municipalities. I call this assumption ‘Partial Aggregate Independence’ (PAI) because the aggregate growth of benefits is assumed to be exogenous even if the individual assignment is endogenous.18 In order to verify the reliability of the PAI assumption, I also present an Instrumental Variable (IV) strategy. The strategy uses the measure of local poverty in 2001, controlling for 18This assumption is the same adopted by Hsieh and Urquiola (2006) to identify the effect of choosing private schools over public schools on students’ achievement. 33 the current level of poverty and fixed effects, to predict variations in the program intervention. This instrument eliminates the part of variance in the program assignment that could be related to unobservable changes in the labor market. Moreover, the exclusion restriction is very likely to hold as long as the relationship between poverty and entrepreneurship does not change over time, which is a testable condition. This section also presents a definition for direct and indirect effects of cash transfer programs. The direct effect is understood as the individual response of households to the program benefit, while the indirect effect results from the interaction of individual responses. In contrast to Angelucci and De Giorgi’s (2009) definition, the indirect effect is seen not only as the impact that the program has on ineligible individuals, but also as the impact that it has on the whole community, including individuals receiving the benefit. Finally, I introduce a formal test to verify whether the indirect effect is different for indi- viduals who receive and do not receive the benefit (Proposition 1.4). Once the homogeneity in the indirect effect is confirmed, the estimated overall effect can be decomposed into the direct and indirect parts, adjusting for the self-selection bias. All proofs are provided in the appendix. 1.4.1 Fixed-Effect Model Let yivt be the decision of individual i living in municipality (city or village) v at time t of being an entrepreneur. Based on equation (1.5), this decision is determined by a linear structural model: yivt = β0 + β1divt + β2dvt + µv + µt + uivt, (1.6) 34 tor for β1 and β2 have the following asymptotic property: β̂1 p → β1 + E [uivtdivt] V ar (divt)− V ar ( dvt ) , β̂2 p → β2 − E [uivtdivt] V ar (divt)− V ar ( dvt ) . Note that the asymptotic biases cancel each other, so the estimator for τ = (β1 + β2) will be consistent if dvt is exogenous. Therefore, self-selection may be an issue if one compares individuals in the same city or village, but it is not if one compares cities and villages as a whole. Finally, the following proposition states the consistency of the identification strategy. Proposition 1.3 (Consistent Estimator for the Overall Effect) Consider the follow- ing equation: yivt = β0 + τdvt + µv + µt + uivt (1.7) If equation (1.6) is the true model, then the least squares (LS) estimator for τ in equation (1.7) is the sum of the LS estimators for β1 and β2 in equation (1.6): τ̂ = β̂1 + β̂2. Moreover, if the PAI Assumption holds, then the LS estimator for τ in equation (1.7) is consistent: τ̂ p → β1 + β2. Proposition 1.3 implies that the overall effect of the program, τ , can be consistently es- timated if we just omit divt in equation (1.6). Accordingly, I estimate equation (1.7) using a three-period data, with the standard errors clustered by municipality. For the sake of ro- bustness, I also include individual and local control variables in the main model and estimate another model with census-tract fixed effects. If the self-selection bias is proportional to the program size, dvt, violating the PAI assumption, then estimates conditional on census-tract 37 fixed effects should be different (less biased) than those conditional on municipality fixed effects. 1.4.2 Instrumental Variable Method One may argue that the PAI assumption is not reasonable because part of the variance of municipality coverage might be explained by unobservables related to the labor market. To consider only changes predicted by the measure of poverty in 2001, rather than changes caused by idiosyncratic behavior, I also estimate an Instrumental Variable (IV) model. In this model, the local coverage need not be strictly driven by observables, but it can be just partially affected by the program’s initial design. Assumption 1.2 (Instrumental Variable Assumption) Given the current poverty level, pvt, and unobserved fixed variables, the designed coverage is orthogonal to uivt. The designed coverage is captured by the interaction between the poverty headcount in 2001, pv0, and period dummies. Then the equation for the program coverage, dvt, is: dvt = γ0 + γ1 pv0 · I (t = 2004) + γ2 pv0 · I (t = 2006) + γ3 pvt + θv + θt + eivt. (1.8) The IV assumption implies that the residual relationship between occupational choices and the measure of poverty in 2001 does not change over time, unless by means of the own program coverage. Note that the constant relationship between occupational choices and the initial poverty headcount is controlled by the fixed effect, θv. Moreover, the current level of poverty, pvt, is also added as a control variable. Section 1.6.4 presents a test to verify whether that relationship changes over time. 38 Since the instrument is defined at the municipality level, the predicted change in the intervention also happens at the municipality level. Therefore, if the program coverage, dvt, is replaced by the individual treatment, divt, in equations (1.7) and (1.8), the estimated IV coefficient will be the same. See Proposition E.1 in the Appendix. This result reinforces the concept of overall effect defined above. Once the instrument is defined at the cluster level (e.g., randomization of treated villages), the comparison between treated and untreated individuals also happens in the cluster level — i.e., across villages rather than between individuals. On one hand, this IV approach avoids the problem of partial identification of the overall effect if using individual treatment. On the other hand, its interpretation cannot ignore the contribution of indirect effects for the estimated impact. 1.4.3 Separating Direct and Indirect Effects Unfortunately, estimating equation (1.7) does not reveal whether the effect of program size comes from either a direct effect on individuals receiving the transfer or an indirect effect that also affects individuals out of the program. Nonetheless, the PAI assumption is also sufficient for the indirect effect, β2, to be consistently estimated using only the sample of individuals out of the program (with divt = 0): yivt|(d=0) = β0,(d=0) + τ(d=0)dvt + µv,(d=0) + µt,(d=0) + uivt|(d=0) (1.9) Non-participants are subject to an overall effect, τ(d=0), that only comprises the indirect impact of the program. Therefore, the estimate of the indirect effect on this group can be 39 barely changes because the local-level instrument makes observations be compared between municipalities and not within municipalities. Namely, local coverage and individual benefit are interchangeable as a treatment variable, whose coefficients can both be interpreted as the overall effect of the program on participants. The estimated overall effect between 4-5 p.p. is found to be larger than PROGRESA’s in Mexico, estimated to be 0.9 p.p. by Bianchi and Bobba (2013). However, it is half as large as the Targeted Ultra-Poor program’s in Bangladesh (Bandiera et al., 2013) and the Youth Opportunities Program’s in Uganda (Blattman, Fiala, and Martinez, 2013). These two programs, nevertheless, are particularly intended to promote entrepreneurship, with the transfer being conditional on productive investments. 1.5.1.1 Type of Business Being Affected In order to analyze the nature of entrepreneurship being affected by the program, en- trepreneurs are classified by the type of business that they run. Namely, service, sales (wholesale and retail), and manufacturing. Table 1.5 shows the estimated coefficient of local coverage for these different types. Almost all the effect on entrepreneurship happens by increasing services, such as tailoring, shoe repair, automotive repair, and taxi driving. The remaining effect comes from sales business, while the effect on manufacturing is very close to zero. On one hand, the higher effect of services, followed by sales, is expected due to the lower cost of physical assets in this type of business. Some services do not even require a store and can be operated from home, while most sales and manufacturing business require 42 a larger initial investment in products and physical capital. On the other hand, services usually demand higher skills than sales. Unfortunately, no information on training programs is available, but we know that Bolsa Famı́lia does not have such a component. This result suggests that part of the transfers goes to the hands of already trained entrepreneurs, giving them the opportunity to formalize their activity. The creation of services, however, may not generate as many jobs as the creation of manufacturing businesses. The effect of Bolsa Famı́lia on job creation is discussed in Sections 1.6.2 and 1.6.3. 1.5.2 Direct and Indirect Effects In order to estimate the indirect effect of the program, I first have to verify whether it is homogeneous or not. According to Proposition 1.4, if the overall effect is linear, then the indirect effect of the program is homogeneous for the chosen sample. The first column of Table 1.6 indicates that the quadratic term for local coverage is very close to zero and not significant. Since the assumption of linear overall effect is not rejected, we can estimate the indirect effect of the program using only the sample of individuals who are not in the program. Columns (2) and (3) of Table 1.6 show this estimate. The indirect effect seems to be greater than the overall effect discussed above. That is, the direct effect should be negative. The last two columns show the estimates for the model including both levels of intervention — i.e., local and individual. These estimates are bias-adjusted using the previously estimated indirect effect. Nonetheless, the estimated selection bias is very close to zero.20 20The selection bias is measured with respect to entrepreneurship. Other intended outcomes, such as school enrollment and health care, may have different levels of bias. 43 The results indicate that, on one hand, cash transfers reduce the probability of partici- pants starting their own business in 3-4 p.p. On the other hand, the amount of cash trans- fered to poor towns seems to stimulate the creation of new businesses. A 10 p.p. increase in the program size seems to raise the entrepreneurship rate of poor individuals between 0.7 and 0.8 p.p. Because of this positive indirect effect, the net impact of cash transfers on entrepreneurship is also positive. This difference between direct and indirect responses is exactly the one predicted by Proposition 1.2. It indicates that small entrepreneurs are not as responsive to financial con- straints as to other general equilibrium mechanisms. However, there are several possible ex- planations for the negative direct effect and the positive indirect effect on entrepreneurship.21 In the next section, I show that the indirect response seems to be related to the promotion of informal financing mechanism among poor households. Furthermore, the hypothesis of increasing investment opportunity by shifting the aggregate demand is not supported by the following tests. 1.6 Potential Mechanisms 1.6.1 Transfers Between Households The first explanation for the positive indirect effect on entrepreneurship is the increasing number of households transferring money to each other. Like in Angelucci and De Giorgi’s (2009), the indirect effect of the cash transfer program might be driven by the existence of risk-sharing strategies within communities. If poor households follow these strategies, 21The negative direct effect does not seem to be driven by conditionalities on education because participants with no child also reduce entrepreneurial activity. See Appendix Table A.1. 44 that the higher the proportion of beneficiaries in the community, the higher the probability of being financially helped by another household. While individuals with better job opportunities may use these transfers as a safety net, individuals with less job opportunities may use them to start their own business. Since I do not know if current entrepreneurs had received other transfers before, I cannot conclude that these transfers are actually invested. The only conclusion that can be drawn is that the effect on receiving other transfers is the highest among those who most need them. Namely, the effect is significantly higher for the jobless, followed by informal workers. It is worth to clarify that I am not interested in the relationship between receiving other transfers and type of occupation, which cannot be identified as causal. The regressions presented in column (3) of Table 1.7 just intend to show the heterogeneity of the indirect effect by type of occupation. In order to verify whether the indirect effects on entrepreneurship and private transfers are related, I include the interaction between coverage and the predicted effect on private transfers in the regression (columns (4) and (5) of Table 1.7). This predicted effect is calculated by interacting coverage and several municipality characteristics in the estimation of private transfers. These “first-step” interactions already reveal, for instance, that the indirect effects of cash transfers on both private transfers and entrepreneurship are higher in lower density areas, with higher school enrollment rate and higher labor informality. Using the predicted effect on private transfers, I find that the larger this effect, the higher the indirect effect of Bolsa Famı́lia on entrepreneurship. Although this is just a back-of-the- envelope calculation, it indicates that entrepreneurial activity has increased through the promotion of informal risk-sharing mechanisms. 47 1.6.2 Aggregate Demand and Investment Opportunity If the indirect effect on entrepreneurship came from a shock in the aggregate demand, we should observe other changes in the labor market. For instance, increasing investment op- portunities should also affect the decision of high-educated men to become entrepreneurs. Moreover, with higher purchasing power, either more jobs should be created or higher salaries should be provided. Accordingly, I also estimate the indirect effect of cash transfers on these outcomes. The first two columns of Table 1.8 confirm that the program size has no significant effect on the probability of high-educated men becoming entrepreneurs. Thus we cannot say the program has encouraged the creation of local businesses in general. That is, the effect on entrepreneurship is concentrated among low-educated workers, who are probably connected to a network of eligible households. Furthermore, the estimates in columns (3) and (4) do not corroborate the hypothesis of job creation. Even though more low-educated men have taken the decision of being entrepreneurs, the program has had no effect on their overall employment rate. This result suggests that the program does not affect the demand side of the labor market. It may have just affected the occupational choice on the supply side. The direct and indirect effects of Bolsa Famı́lia on other occupational choices are discussed below. Although the employment rate has not been significantly affected by Bolsa Famı́lia, it is possible that the effect on the demand side has been just on wages. It is worth to notice that the estimated effect on wages can be misleading if the program has some influence on 48 local prices. Unfortunately, I do not have information on prices at the municipality level. However, I can use wages of low-educated public employees as a proxy for labor costs. Then the real effect on aggregate demand is assessed by the difference between private documented employees and public servants in terms of changes on wages. Indeed, the estimated coefficient for the interaction between program coverage and private employee, in the last two columns of Table 1.8, is very close to zero.23 1.6.3 Other Occupational Choices To understand where the responsive entrepreneurs comes from, I also investigate the effect of the program on other occupational choices. Besides entrepreneur, the alternatives are jobless, formal employee, informal employee, and informal self-employed. Table 1.9 presents the direct and indirect effects of the program on the probability of being in each one of these categories, vis-à-vis being in any other category. The estimated indirect coefficients indicate that the program has no significant effect on the proportion of jobless in intervened areas. The program does not have a significant indirect effect on the proportion of formal employees either. Once again, the hypothesis that the money injected in local economies shifts the demand for workers is not supported by these results. In other words, the increasing participation of documented employees in the Brazilian labor market in the 2000’s cannot be attributed as much to the Bolsa Famı́lia program as to other demographic and economic changes.24 23A regression of wages on program coverage, excluding public servants, would show that the effect is significantly positive. However, this effect is not only on private employees. The general effect on wages indicates that the impact does not come from the specific demand for labor, but from general labor costs. 24Articles in ‘The Economist’ magazine, published on Feb. 12 2009, and in ‘The New York Times’, published on July 31 2008, mentioned that Bolsa Famı́lia was an example of CCT program that has helped 49 Figure 1.4: Household Debt Outstanding and Interest Rate in Brazil Studied Period Interest Rate Debt 0 200 400 600 800 H ou se ho ld D eb t, B R L B ill io n 10 15 20 25 30 P rim e In te re st R at e, % p er y ea r Sep 2001 Sep 2004 Sep 2006 Sep 2010 Source: Central Bank of Brazil. Debt series is deflated by the National Consumer Price Index (INPC). Although the credit expansion started in the late 2000’s, other microcredit programs have been in place since the 1990’s. To test whether the results are driven by microcredit programs, I exclude from the sample the region where the largest and most significant program was introduced. The CrediAmigo program, created in 1997, is considered the largest microfinance program in the country, but it covers only municipalities in the Northeast region. Columns (4) and (5) of Table 1.10 show that the estimated effect on entrepreneurship slightly increases after omitting that region. Thus the results do not seem to be a consequence of the growth in microcredit either. Another form of convergence is through the migration of human capital. That is, social programs might have promoted the migration of potential entrepreneurs, as well as other 52 type of workers, to highly covered areas. As shown in Table 1.11, the program coverage has no significant effect on the probability of migrating from other municipality in the last four years. Therefore, the estimated effects are probably not due to changes in the composition of workers in the labor force, but due to changes in their decisions. 1.7 Conclusion This chapter investigated the causal relationship between conditional cash transfer (CCT) programs and the decision of being a small entrepreneur. Entrepreneurship is not usually an intended outcome of CCTs, since their goals are often strictly related to child development and income redistribution. However, investigating this outcome can tell us something about their broader impacts on economic development in the short run. Besides estimating the impact on an urban population, which is rarely seen in the literature about aid programs, the critical distinction of this analysis is the separation between direct and indirect effects. The identification of spillovers might reveal that the impact of those transfers goes well- beyond cash and conditionalities, uncovering the role of inter-household exchanges within the informal economy. Since the benefit is primarily assigned at the village level in most of the treated-control settings, evaluation designs usually allow only the identification of the overall effects of aid programs. In this study, the decomposition into direct and indirect effects is identified due to the variation in the size of the Bolsa Famı́lia program across municipalities in Brazil. Despite the issues with selection into the program, the overall effect is identified due to the exogeneity of the local coverage growth. Then the decomposition of this overall effect is 53 made by adjusting the coefficients for the estimated selection bias. Although this method is applied to observational data, it also introduces a new way of designing experiments, in which only the size (proportion of benefits) rather than the individual benefit is randomized at the cluster level.27 The results indicate that, on one hand, cash transfers have a negative direct effect on entrepreneurship, reducing the probability of beneficiaries to start their own business. This direct effect is associated with the negative impact that transfers have on the participation of workers in the formal sector. It suggests that the program encourage its beneficiaries to either reduce labor supply or move to the informal sector to not lose their cash benefit. This finding ratifies a major concern in welfare programs in general and reveals a caveat in terms of eligibility rules.28 On the other hand, the amount of cash transfered to poor villages seems to encourage the creation of new businesses, mostly in the service sector. There is no evidence, however, that this positive impact is driven by shocks in the aggregate demand. For instance, neither the proportion of high-educated entrepreneurs nor the number of formal jobs grew with the program. The lack of other impacts on the labor market indicates that Bolsa Famı́lia has indirectly changed the occupational choice of poor workers in the supply side, but not the demand for labor. This finding is not as exceptional as some CCT advocates claim, but it suggests that the program has been responsible for the formalization of low-skilled workers through self-employment. 27This new approach can be used to simplify the two-step randomization proposed by Duflo and Saez (2003) and Crepon et al. (2013). 28See Besley and Coate (1992), Kanbur, Keen, and Tuomala (1994), and Moffitt (2002). 54 Table 1.4: Overall Effect of Cash Transfers on Entrepreneurship Decision of being a small entrepreneur OLS FE IV (1) (2) (3) (4) (5) (6) program coverage, d -0.013* 0.042*** 0.040*** 0.058*** 0.056*** (0.008) (0.013) (0.013) (0.022) (0.021) individual benefit, d 0.057** (0.024) age (x10) 0.057*** 0.060*** 0.063*** 0.060*** 0.060*** 0.056*** (0.016) (0.016) (0.016) (0.016) (0.016) (0.017) squared age (x100) -0.002 -0.003 -0.004 -0.003 -0.003 -0.003 (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) white 0.039*** 0.032*** 0.025*** 0.032*** 0.032*** 0.026*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) black -0.011*** -0.014*** -0.013*** -0.014*** -0.014*** -0.014*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) married 0.024*** 0.025*** 0.030*** 0.025*** 0.025*** 0.027*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) elementary education 0.029*** 0.027*** 0.024*** 0.027*** 0.027*** 0.026*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) primary education 0.028*** 0.028*** 0.022*** 0.028*** 0.028*** 0.024*** (0.002) (0.003) (0.002) (0.003) (0.003) (0.003) high school 0.030*** 0.031*** 0.020*** 0.031*** 0.031*** 0.021*** (0.003) (0.002) (0.002) (0.002) (0.002) (0.002) log of population -0.004*** -0.023 -0.020 -0.025* -0.021 -0.016 (0.001) (0.015) (0.014) (0.015) (0.015) (0.014) year = 2001 0.000 0.006* 0.003 0.008* 0.008 0.005 (0.002) (0.004) (0.004) (0.005) (0.005) (0.005) year = 2004 -0.002 -0.001 -0.001 0.000 0.001 0.001 (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) poverty headcount -0.029* -0.029 (0.018) (0.018) elementary enrollment rate 0.01 0.011 (0.020) (0.021) primary enrollment rate -0.016 -0.016 (0.012) (0.013) high school enrollment rate -0.014 -0.014 (0.012) (0.011) child mortality (x1000) 0.019 0.022 (0.054) (0.055) coverage of sewer system -0.005 -0.007 (0.012) (0.013) prop. of house owners 0.029 0.028 (0.020) (0.020) Municipality Fixed-Effects No Yes No Yes Yes Yes Census Tract Fixed-Effects No No Yes No No No Number of observations 129,298 129,298 129,298 129,298 129,298 129,264 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Standard errors in parentheses are clustered by municipality. Sample includes only men with high school diploma or less. Column (1) presents the regression coefficients obtained by Ordinary Least Squares (OLS). Columns (2) and (3) present the fixed-effect regressions (FE) obtained using the within-group method. Columns (4), (5), and (6) present the fixed-effect, Instrumental-Variable regressions (IV) with ‘program coverage’ and ‘individual benefit’ instrumented by the interactions between poverty headcount in 2001 and year dummies. 57 Table 1.5: Overall Effect of Cash Transfers on Different Types of Business Decision of being a small entrepreneur in Services Sales Manufacturing FE IV FE IV FE IV (1) (2) (3) (4) (5) (6) program coverage, d 0.038*** 0.053*** 0.015** 0.019 -0.004 -0.004 (0.010) (0.017) (0.008) (0.013) (0.007) (0.011) age (x10) 0.031*** 0.031*** 0.023* 0.023* 0.001 0.001 (0.012) (0.012) (0.012) (0.012) (0.010) (0.010) squared age (x100) -0.002 -0.002 -0.001 -0.001 0.002 0.002 (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) white 0.016*** 0.016*** 0.015*** 0.015*** 0.006*** 0.006*** (0.002) (0.002) (0.001) (0.001) (0.001) (0.001) black -0.006*** -0.006*** -0.005*** -0.005*** -0.005*** -0.005*** (0.002) (0.002) (0.002) (0.002) (0.001) (0.001) married 0.000 0.000 0.012*** 0.012*** 0.006*** 0.006*** (0.001) (0.001) (0.001) (0.001) (0.001) (0.001) elementary education 0.011*** 0.011*** 0.011*** 0.011*** 0.008*** 0.008*** (0.001) (0.001) (0.001) (0.001) (0.001) (0.001) primary education 0.012*** 0.012*** 0.015*** 0.015*** 0.003** 0.003** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) high school 0.022*** 0.022*** 0.013*** 0.013*** -0.002 -0.002 (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) log of population -0.012 -0.014 -0.016* -0.017* 0.003 0.003 (0.011) (0.011) (0.009) (0.009) (0.008) (0.008) year = 2001 0.020*** 0.022*** -0.008*** -0.008*** -0.004** -0.004 (0.003) (0.004) (0.002) (0.003) (0.002) (0.002) year = 2004 0.001 0.001 0.001 0.001 -0.002 -0.002 (0.001) (0.001) (0.002) (0.002) (0.001) (0.001) Municipality Fixed-Effects Yes Yes Yes Yes Yes Yes Number of observations 112,321 112,321 112,321 112,321 112,321 112,321 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Standard errors in parentheses are clustered by municipality. Sample includes only men with high school diploma or less. FE columns present the fixed-effect regressions obtained using the within-group method. IV columns present the fixed-effect, Instrumental-Variable regressions with ‘program coverage’ instrumented by the interactions between poverty headcount in 2001 and year dummies. 58 Table 1.6: Nonlinear, Indirect, and Direct Effects of Cash Transfers on Entrepreneurship Decision of being a small entrepreneur All Non-participants All sample sample FE IV FE IV (1) (2) (3) (4) (5) program coverage, d 0.045 0.070*** 0.079*** 0.070*** 0.079*** (0.028) (0.015) (0.024) (0.015) (0.024) squared coverage, d 2 -0.006 (0.043) individual benefit, d -0.032*** -0.041*** (0.004) (0.006) age (x10) 0.060*** 0.063*** 0.063*** 0.064*** 0.064*** (0.016) (0.018) (0.018) (0.016) (0.016) squared age (x100) -0.003 -0.003 -0.003 -0.003 -0.003 (0.002) (0.003) (0.003) (0.002) (0.002) white 0.032*** 0.034*** 0.034*** 0.031*** 0.031*** (0.002) (0.002) (0.002) (0.002) (0.002) black -0.014*** -0.015*** -0.015*** -0.014*** -0.014*** (0.002) (0.003) (0.003) (0.002) (0.002) married 0.025*** 0.029*** 0.029*** 0.027*** 0.027*** (0.002) (0.002) (0.002) (0.002) (0.002) elementary education 0.027*** 0.028*** 0.028*** 0.025*** 0.025*** (0.002) (0.002) (0.002) (0.002) (0.002) primary education 0.028*** 0.028*** 0.028*** 0.027*** 0.027*** (0.003) (0.003) (0.003) (0.003) (0.003) high school 0.031*** 0.030*** 0.030*** 0.030*** 0.030*** (0.002) (0.003) (0.003) (0.002) (0.002) log of population -0.024 -0.031* -0.032* -0.024 -0.026* (0.015) (0.017) (0.017) (0.015) (0.015) year = 2001 0.006 0.004 0.005 0.005 0.008 (0.004) (0.004) (0.005) (0.003) (0.005) year = 2004 -0.001 -0.001 -0.001 -0.001 0.000 (0.002) (0.002) (0.002) (0.002) (0.002) Municipality Fixed-Effects Yes Yes Yes Yes Yes Number of observations 129,298 113,267 113,267 129,264 129,264 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Standard errors in parentheses are clustered by municipality. Sample includes only men with high school diploma or less. Column (1) presents the fixed-effect model with quadratic effect of program coverage. Columns (2) and (3) present the estimates of the indirect effect on individuals who do not participate in the program. Columns (4) and (5) present the estimates of the indirect effect (program coverage) and direct effect (individual benefit), with bias correction given by Lemma 1.1. Columns (2) and (4), as well as columns (3) and (5), are jointly estimated using Seemingly Unrelated Regressions (SUR). FE columns show fixed-effect regressions obtained using the within-group method. IV columns show fixed-effect, Instrumental-Variable regressions with ‘program coverage’ instrumented by the interactions between poverty headcount in 2001 and year dummies. 59 ESSAYS ON ENTREPRENEURSHIP AND MANAGEMENT BY RAFAEL PEREZ RIBAS DISSERTATION Submitted in partial fulfillment of the requirements for the degree of Doctor of Philosophy in Economics in the Graduate College of the University of Illinois at Urbana-Champaign, 2014 Urbana, Illinois Doctoral Committee: Professor Darren Lubotsky, Chair Professor Roger Koenker Professor Murillo Campello Professor Ron A. Laschever Professor Richard Akresh ABSTRACT This dissertation consists of three essays on financial and institutional determinants of entrepreneurship and the importance of management style. Chapter 1: Direct and Indirect Effects of Cash Transfers on Entrepreneurship In this chapter, I exploit a liquidity shock from a large-scale welfare program in Brazil to investigate the importance of credit constraints and informal financial assistance in explaining entrepreneurship. Previous research focuses exclusively on how liquidity shocks change recipients’ behavior through direct effects on reducing financial constraints. However, the shock may also produce spillovers from recipients to others through private transfers and thereby indirectly affect decisions to be an entrepreneur. This essay presents a method for decomposing the liquidity shock into direct effects associated with relieving financial con- straints, and indirect effects associated with spillovers to other individuals. Results suggest that the program, which assists 20 percent of Brazilian households, has increased the number of small entrepreneurs by 10 percent. However, this increase is almost entirely driven by the indirect effect, which is related to an increase in private transfers among poor households. Thus the creation of small businesses seems to be more responsive to the opportunity cost of mutual assistance between households than to financial constraints. Chapter 2: Bankruptcy Law and the Creation of Small Business This essay investigates the relationship between bankruptcy law and the creation of small businesses by using the 2005 reform in the U.S. as a natural experiment. In theory, a pro-debtor law provides an insurance against business failure and thereby encourages en- trepreneurial investments. On the other hand, a pro-creditor law inhibits debtor’s abusive ii ACKNOWLEDGEMENTS I wish to express my deepest gratitude to my advisor Darren Lubotsky. He has generously dedicated his time and expertise to guide me through all the steps that takes to earn a Ph.D. His role was crucial to get me focused and set my short- and long-term goals. Without him I could not have completed this dissertation. I am also very grateful to my mentor, Murillo Campello. He has changed the course of my academic career, giving the most valuable professional advice that I have ever had. I have worked with him since an early stage of the graduate school and this relationship has taught me so many priceless lessons. The third role model to whom I would like to express my gratitude is Roger Koenker. His lessons inside and outside the classroom were just mind-blowing. Our meetings made my six years in Champaign-Urbana worthwhile. I am very thankful to him for teaching me and openly discussing a broad range of empirical methods in such a pleasant way. For their comments and professional advice, I am also grateful to the other members of my dissertation committee: Richard Akresh and Ron Laschever. Likewise, I should express my sincere appreciation to Dan Bernhardt, Heitor Almeida, and George Deltas for their support. For comments and suggestions that helped me to improve this dissertation, I am thankful to David Albouy, François Bourguignon, Habiba Djebbari, Francisco Ferreira, Giorgia Giovannetti, and Simon Bordenave. I would like to give very special thanks to Professor Werner Baer for his constant effort to support all Brazilian students at the University of Illinois, including myself. I am also grateful for the support given by Professors Anil Bera, Kristine Brown, Daniel McMillen, v Stephen Parente, Martin Perry, Walter Sosa, Joseph Petry, and Mary Arends. It is important to acknowledge the contribution given by friends and colleagues, who have provided fruitful discussions and helpful feedbacks: Rafael da Matta, who has helped me in every single step of this journey, from the Ph.D. application to the job placement, and Igor Cunha, who is the co-author of the third chapter of this dissertation; as well as Marco Rocha, Breno Sampaio, Gustavo Sampaio, Euler de Mello, Leonardo Lucchetti, Monse Bustelo, Sarah Miller, Andreas Hagemann, Fabricio D’Almeida, Leandro Rocco, Paulo Vaz, Diloa Athias, and Joao Bernardo Duarte. It was also an honor to share the same classroom with outstanding students such as Raul, Sergey, Angelo, Bruno, Josh, Seyed, Taka, Yashar, Young, Maria, Rafael Nivin, Eric, and Sascha. My friends and former colleagues, Fabio Veras Soares, Sergei Soares, Guilherme Hirata, and Elydia Silva, have also contributed to this achievement. So have my former advisors, Ana Flavia Machado and Lovois Miguel. Thank you all! Thanks to the friends that made my stay in Champaign-Urbana memorable: Felipe, Rafael Nogueira, Mauricio, Diego, Claudia, Mariangela, Cintia, Elisa, Ludmila, Renato, Anamaria, Virginia, Rayane, Vivi, Loló e Renata, Kiko e Thais, Pipoca e Aline, Luiz Fe- lipe, Andre e Rosa, Jimmie, Robert, Denis, Aisha, and all members of the Capoeira Club, Jonathan, Max, Shin, Stan, Sergei, Marcin, and all members of the Judo Club, and all Gentlemen, Hammeroids, and Barcelona players. Finally, nothing would be possible without the love and support of my parents, Clairton and Silvia Ribas, my brothers, Dado, Rena, and Rica, and my fiancée, Marjorie Souza. This dissertation is dedicated to my parents. vi Contents Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1 Chapter 1: Direct and Indirect Effects of Cash Transfers on Entrepreneurship 5 1.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 5 1.2 Theoretical Framework . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 1.3 Program and Data Description . . . . . . . . . . . . . . . . . . . . . . . . . 21 1.4 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 33 1.5 Main Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 40 1.6 Potential Mechanisms . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 44 1.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 53 Chapter 2: Bankruptcy Law and the Creation of Small Business . . . . . . 65 2.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 65 2.2 The U.S. Personal Bankruptcy Law . . . . . . . . . . . . . . . . . . . . . . . 69 2.3 Data and Descriptive Statistics . . . . . . . . . . . . . . . . . . . . . . . . . 74 2.4 Empirical Strategy . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 78 2.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 83 2.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87 Chapter 3: Contrasts in Styles and Managers’ Impact on Corporate Policy 88 3.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 88 3.2 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 95 3.3 What drives turnovers? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 99 3.4 Estimation Method and Inference . . . . . . . . . . . . . . . . . . . . . . . . 103 3.5 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 117 3.6 Conclusions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 127 Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 129 vii ploits a liquidity shock from a large-scale welfare program in Brazil to investigate the impor- tance of credit constraints and informal financial assistance in explaining entrepreneurship. Previous research focuses exclusively on how liquidity shocks change recipients’ behavior through direct effects on reducing financial constraints. However, the shock may also pro- duce spillovers from recipients to others through private transfers and thereby indirectly affect the decision to be an entrepreneur. Accordingly, I present a method for decomposing the liquidity shock into direct effects associated with relieving financial constraints, and indirect effects associated with spillovers to other individuals. Results suggest that the program, which assists 20 percent of Brazilian households, has increased the number of small entrepreneurs by 10 percent. However, this increase is almost entirely driven by the indirect effect, which is related to an increase in private transfers among poor households. Thus the creation of small businesses seems to be more responsive to the opportunity cost of mutual assistance between households than to financial constraints. The second essay, “Bankruptcy Law and the Creation of Small Business,” investigates the relationship between personal asset protection and the creation of small businesses by using the 2005 bankruptcy reform in the U.S. as a natural experiment. In theory, a pro-debtor law provides an insurance against business failure and thereby encourages entrepreneurial investments. On the other hand, a pro-creditor law inhibits debtor’s abusive behavior, improving the selection of projects. The reform was intended to reduce the number of abusive filings and can be viewed as 2 a shock that has affected each state in a different way. Although changes in state laws are often related to economic conditions, this reform was not triggered by any state in particular. The reform has actually lessened debtor’s asset protection yielded by state laws. Based on previous state exemption levels, I can identify households that were more and less affected by the reform. Results confirm the positive relationship between homestead exemptions and entrepreneurial activity, but this relationship is not necessarily causal. The reform, on the other hand, has only affected the creation of unincorporated businesses, whose all debt is legally considered their owners’ personal debt. The rate of incorporated businesses does not seem to be affected by changes in asset protection. The third essay of this dissertation, “Contrasts in Styles and Managers’ Impact on Cor- porate Policy,” approaches another dimension of economic productivity related to how large firms are managed: can differences across firms be explained by their managers’ skills? On one hand, some studies argue that managers do have different styles (e.g., Bertrand and Schoar, 2003). On the other hand, other studies show that their styles have no effect on corporate decisions and, as a result, on their performance (Fee, Hadlock, and Pierce, 2013). This debate is critical since CEO compensation increased 127 times faster than worker com- pensation in the last 30 years, with some results questioning if executives are worth the money. In collaboration with Igor Cunha, I propose a new approach to study how corporate policies are influenced by their top executives. First, we estimate a Bayesian random-effect model to estimate the contribution of executive-specific effects and firm-specific effects to the variance of corporate financial policy and performance. Then we employ empirical Bayes 3 simultaneous tests on the executive effects to verify heterogeneity in managers’ styles. Our results not only corroborate what is already found by Bertrand and Schoar (2003), showing that several executives carry their own style to their companies, but also show that their effect is almost negligible compared to firm- and industry-specific effects. 4 households are also affected by PROGRESA/Opportunidades in rural villages in Mexico. They suggest that these households increase food consumption by receiving private transfers from program participants and reducing their precautionary savings.4 In another study, Bandiera et al. (2009) assess the effect of asset transfers in Bangladesh. They show that this program has indirect effects on time allocation in risk-sharing networks and on durable consumption in family networks. In both studies, indirect effects are identified using non-participants, but their definition of direct effect is essentially the definition of ‘effect on the treated.’ As a matter of fact, “treated” households are also subject to spillovers. Even if all households are participating in the program, there may be externalities that either boost or attenuate the direct response to those transfers. This distinction is critical to understand targeted interventions, such as CCT and microfinance. On one hand, findings that are based on the comparison of treated and untreated villages tend to be interpreted as an exclusive consequence of participants’ responses. On the other hand, studies that compare individuals rather than villages might be biased by ignoring spillovers. According to Heckman, Lochner, and Taber (1998), the conventional treatment effect model is based on a partial equilibrium framework. If the intervention has general equilibrium consequences, then the net effect also depends on who else is treated and the interaction between the treated and the untreated. Other studies suggest that the liquidity shock promoted by cash transfers increases entrepreneurial activity at both the intensive margin, raising investments and profits (de Mel, 4Lehmann (2013) contests Angelucci and De Giorgi’s (2009) interpretation and suggests that the indirect effect on food consumption operates by raising non-food prices. 7 McKenzie, and Woodruff, 2008; Gertler, Martinez, and Rubio-Codina, 2012), and extensive margin, encouraging participants to start their own business (Bianchi and Bobba, 2013; Bandiera et al., 2013; Blattman, Fiala, and Martinez, 2013). In some of these studies, how- ever, the randomization of ‘treatment’ was made at the village-level, which implies that the effect should be viewed as the sum of individual and local responses (Hudgens and Halloran, 2008). Namely, what is often interpreted as an individual shock, which lessens financial constraints, could actually be a locally aggregate shock, which also affects other households in the same village. Another limitation in the current evidence is that most of randomized controlled trials (RCTs) are either restricted to rural areas, where job opportunities other than work in one’s own farm are scarce, or limited to small-scale pilots, which hold uncertainty about their maintenance. Therefore, little is known about the response of households to those programs once they reach urban centers as a permanent policy of social protection (Behrman et al., 2012). Moreover, the evidence on informal risk-sharing arrangements also comes mostly from rural villages (Fafchamps, 2011). Unlike those interventions, Bolsa Famı́lia is a widespread, large-scale program that has been introduced not only in rural and isolated areas, but also in large cities in Brazil. In 2006, about 20% of Brazilian households were already covered by the program and 70% of them were living in urban settlements. Accordingly, I exploit this intervention to inves- tigate small entrepreneurial activity and informal risk-sharing mechanisms in urban areas. As most of the literature, I define as entrepreneurs those who are either self-employed or small business owners (e.g., Blanchflower, 2000; Hurst and Lusardi, 2004). Furthermore, to 8 consider self-employment as an investment opportunity rather than a way to conceal earn- ings, I distinguish entrepreneurs from those who are self-employed in the informal sector. Informal self-employment is considered another type of occupation in which workers are not covered by social security and whose earnings cannot be verified by the government. While small entrepreneurs earn on average 45% more than formal employees per hour, the informal self-employed earn 30% less. Although the assignment of benefits in Bolsa Famı́lia is not random, I demonstrate that this is not a concern as long as the endogenous assignment of participants is not related to the overall amount of transfers received in the entire village. Namely, the fact that some poor households are more likely to participate in the program than others only affects the way the transfers are locally distributed. The total number of transfers per city or village is considered given because, from 2003 to 2007, the program was phased in based on a previ- ously drawn poverty map. As a result, each municipality should have a limited number of transfers to be offered. Then instead of comparing participants and non-participants in the same municipality, the overall effect is estimated simply by comparing municipalities using a difference-in-difference model. To relax the assumption of exogenous program size, this variable is also instrumented by the poverty map. Then a verifiable condition for the Instru- mental Variable (IV) approach is that the relationship between poverty and entrepreneurship does not change over time. Namely, there is no convergence in the entrepreneurship level across municipalities. Once the overall effect is consistently estimated, the direct and indirect effects are cal- culated by a two-step procedure. First, based on the previous assumptions, I estimate the 9 Section 1.6 presents tests for potential mechanisms, including confounding factors. Section 1.7 concludes the chapter. 1.2 Theoretical Framework To understand why cash transfers could have an indirect effect on entrepreneurship, I present a simple model in which being formally self-employed has a fixed cost. For equally poor in- dividuals, this fixed cost cannot be covered by formal credit due to their lack of collateral and high interest rates. The insufficient wealth can also make them unable to insure against business failure and then less willing to take risks (Bianchi and Bobba, 2013). These con- straints drive us to conclude that an individual liquidity shock should increase their chances of being self-employed. On the other hand, the formal market is not the only source of credit and insurance. Bilateral exchanges between neighbors, friends, and relatives might be a way in which small entrepreneurs cope with startup costs and business risks. Although empirical studies suggest that informal risk-sharing mechanisms do not fully compensate market failures (Townsend, 1994; Hayashi, Altonji, and Kotlikoff, 1996; Ravallion and Chaudhuri, 1997),7 efficiency is of- ten achieved within social networks (Fafchamps, 2000; Fafchamps and Lund, 2003; DeWeerdt and Dercon, 2006). According to Bloch, Genicot, and Ray (2008), social networks have the role of lessening information asymmetries and commitment constraints among their mem- bers. One may call this role social capital, which lowers the transaction costs of obtaining credit and insurance (Murgai et al., 2002; Fafchamps and Minten, 2002). 7See Ogaki and Zhang (2001) for an evidence favoring the full risk-sharing hypothesis at the village level. 12 With low transaction costs, low-skilled individuals do not necessarily spend all the cash transfer, but they may also lend to someone with better entrepreneurial skills to increase their income in the future. At the same time, small entrepreneurs need not count only on their endowments to start their venture. In this model, the fraction of eligible individuals participating in risk-sharing networks is the key to explain the size of direct effects, which lessens financial constraints, and the size of an indirect effect, which reduces the costs of informal credit and insurance. 1.2.1 Setup Consider a continuum of individuals who live for two periods and are heterogeneous in their entrepreneurial skills, q. All individuals maximize their expected utility, U , by choosing their consumption in period 1, c1, and consumption in period 2, c2: U = u (c1) + E [u (c2)] , where E [.] is the expectation operator and u (.) exhibits decreasing absolute risk aversion, so that u′′ < 0 and u′′′ ≥ 0.8 In period 1, these individuals are endowed with an initial wealth, a, and have to choose their future occupation, which can be either working in a low-skilled job (L) or working in their own business (M). Choosing the low-skilled job has no cost and pays w in period 2. To start their business, however, they must acquire capital in the first period, which costs k. This capital, along with the time allocated to self-employment in period 2, yields 8A time discount factor could be included, but it is not relevant for this problem. 13 either q with probability λ or δ otherwise. Namely, q represents the total revenue in case of business success, while δ is what they receive for reselling their capital (after depreciation) in case of failure. Another interpretation is that k represents the cost of formalization for the self-employed and δ is what they receive from social security (Straub, 2005). In summary, individual’s income before transfers and savings is: I1 ≡    a if L a− k if M and I2 ≡    w if L q w.p. λ if M δ w.p. 1− λ if M Depending on their entrepreneurial skills, q, self-employment (M) increases the expected payoff of some individuals.9 Nonetheless, I should also consider that it is riskier than a salaried job (L), so that δ < w and λ ∈ (0, 1). In addition to the initial endowment and earnings, poor individuals are entitled to cash transfers in period 1, d1, and in period 2, d2, with d1 = d2 = d. However, receiving d2 is conditional on eligible individuals staying poor based on an eligibility rule. With this rule, only those with verifiable earnings, I2, less than or equal to w remain eligible for the benefit. For those whose q > w, λ becomes not only the probability of business success, but also the probability of losing the transfer if self-employed. Let ζ indicate whether the eligibility rule is applied (ζ = 1) or not (ζ = 0). 9Other types of heterogeneity could be assumed, such as in wealth, risk aversion, and probability of success. However, with heterogeneous payoffs and risk-averse individuals, wealth heterogeneity becomes irrelevant. Heterogeneity in either risk aversion or probability of success would essentially yield the same results, but with a more complex insurance market. 14 If the eligibility rule is applied (ζ = 1), then an increase in future transfers, d2, will have an ambiguous effect. On one hand, it still provides insurance against business failure (IE). On the other hand, it increases the return of being wage employed, L, because choosing self-employment reduces the chances of receiving d2. This negative response is defined as the eligibility effect (EE): EE ≡ ∂y ∂d2 ∣∣∣∣ ζ=1 − ∂y ∂d2 ∣∣∣∣ ζ=0 ∝ −λu′ [q̂ + d2 + s∗M (q̂)] < 0 (1.3) Depending on how high is the probability of business success, λ, the eligibility effect can prevail over the insurance and credit effects — i.e., CE+ IE+EE < 0. Thus individuals at the margin of indifference might prefer keeping receiving a transfer than starting a business that does not pay much more. Proposition 1.1 (Effect of Cash Transfer with Credit and Insurance Constraints) Assume that individuals can neither borrow nor trade insurance. Under no eligibility rule, cash transfers have a positive net effect on the entrepreneurship rate. However, if future transfers are subject to an eligibility rule, then the net effect is ambiguous and decreasing in the probability of business success, λ. 1.2.2.2 Aggregate Liquidity Shock with Risk-Sharing Consider a risk-sharing network in which transaction costs are irrelevant, so that its members can efficiently trade bonds and insurance in the first period. The repayment of bonds is assumed to be contingent on business success in period 2.11 If the investment made by entrepreneurs is not successful, then they receive the insurance that they bought rather than 11Contingent bonds can also be interpreted as an insurance that entrepreneurs sell to non-entrepreneurs. Evidence of contingent loan repayment is presented by Udry (1994) and Fafchamps and Gubert (2007). 17 paying their loans. Another way of setting this model is assuming that credit and insurance are provided through gift exchanges without commitment (Kocherlakota, 1996; Foster and Rosenzweig, 2001). If the business is successful and the entrepreneur becomes richer, then a more valued gift is expected in return. Otherwise, non-entrepreneurs are expected to help entrepreneurs with their loss. The ratio between what is given in period 1 and what is received in period 2 defines the implicit prices of bonds and insurance. Given the equilibrium prices in this network, all individuals are now able to optimally transfer utility across periods and states — i.e., they are neither credit constrained nor insurance constrained. Therefore, the direct effect of cash transfers on the occupational choice depends only on the eligibility rule. If eligibility rule is not applied, the liquidity shock just changes the individual demand for credit and insurance, but it does not affect their occupational choice, CE = IE = 0. Otherwise, an increase in future transfers, d2, reduces the relative gain of being self-employed with respect to wage employment (EE). On the other hand, the cash transfered in both periods will also lower the cost of risk- sharing by changing the equilibrium prices of bonds and insurance. With more cash in hands, non-entrepreneurs will be more willing to share the risk with entrepreneurs, whereas entrepreneurs will reduce their need for inter-household transfers. As a result, the decreasing cost of risk-sharing gives the opportunity for slightly less-skilled individuals to invest in a more profitable occupation. Therefore, in an efficient risk-sharing arrangement, an aggregate liquidity shock will be used to cover the cost of capital, k, and the possible losses, w − δ, of a larger fraction of entrepreneurs. 18 Let y∗ be the Pareto efficient entrepreneurship rate among individuals in the same net- work. The general equilibrium effect (GE) of cash transfers is given by the overall effect on y∗ minus the direct response, which only comprises the eligibility effect, EE: GE ≡ dy∗ dd1 + dy∗ dd2 − EE > 0. (1.4) Proposition 1.2 (Effect of Cash Transfer in a Risk-Sharing Network) Assume that individuals belong to a risk-sharing network. The direct effect of cash transfers on the deci- sion of being an entrepreneur is negative due to the eligibility rule. However, the aggregate shock of cash transfers has also a positive indirect effect by lowering the cost of risk-sharing. 1.2.2.3 Direct and Indirect Effects and the Size of Risk-Sharing Networks Finally, consider a population in which some individuals participate in risk-sharing networks and others do not. In particular, let N be the number of risk-sharing networks in this population and αj be their size with j = 1, . . . , N . Note that ( 1− ∑N j=1 αj ) is the fraction of individuals who do not belong to a network, which are labeled as group 0. Also, for any j = 1, . . . , N , q̂j ≤ q̂0 — i.e., despite the network size, individuals connected to one has at least as much chance to be an entrepreneur as those who are not. The reason is they can always lean on their own savings if the price of insurance in their network is too high. If individuals are randomly distributed among these networks, then the relationship be- tween entrepreneurship rate and cash transfers is the following:12 ∆y ≈ (β1 + β2)∆d, (1.5) 12The assumption of exogenous networks is not necessary. Even if individuals are assorted based on q, for any j = 1, . . . , N , q̂j ≤ q̂0 still holds. 19 children up to 15 years old or pregnant women were eligible for the program. The monthly benefit was composed of two parts: a) US$38 for extremely poor families regardless of the number of children, and b) US$11 per children, up to three, for poor families. Thus an extremely poor family should receive a benefit between US$38 and US$72, whereas a moderately poor family should receive between US$11 and US$34.13 Like Bolsa Escola and Bolsa Alimentação, these benefit require a household commitment in terms of child education and health care. However, if the family is registered as extremely poor with no child, the US$38 transfered is actually considered unconditional. Families that receive the benefit can be dropped from the program not only in case of not complying with the conditionalities, but also when their per capita income becomes greater than the eligibility cut-off point. During the period covered by this study, whenever it was found that the household per capita income had been above the eligibility threshold, the family would be excluded from the payroll. Moreover, families are required to update their records in the single registry of social policies (Cadastro Único) at least once every two years. As for monitoring of the income information, the Federal Government regularly matches beneficiaries’ records with other governmental databases, such as the database on formal sector workers from the Ministry of Labor and Employment and the database of pensions and other social assistance programs. For instance, the government found that 622,476 participant households had earnings above the eligibility cutoff from October 2008 and February 2009. From this total, 451,021 13In 2004, the extreme poverty line for the program was US$33, the poverty line was US$66, and the value of the benefit per child was US$10. 22 households had their benefit canceled. From cross-checking its databases, the government had canceled the benefit of more than one million households from 2004 to 2008, which represents about 40% of the total number of withdraws. 1.3.2 Program’s Targeting In order to identify poor families around the country, local governments (municipalities) are free to decide about the priority areas and how the registering process takes place. However, they do receive some guidelines, under the form of quotas on the number of benefits. This cap of benefits is intended to prevent local governments from spending the federal transfers irresponsibly and using them for electoral purposes. As a result, each municipality has a maximum number of benefits that can be distributed, which is given by the estimated number of poor households. Although the program size cannot growth for electoral purposes, de Janvry, Finan, and Sadoulet (2012) show that its local performance has raised the chances of mayors being re- elected. Namely, politicians cannot take advantage by distributing more benefits, but they can be rewarded by the way the total number of benefits is distributed. The municipal quotas were initially defined by a poverty map, made by the National Statistics Office (Instituto Brasileiro de Geografia and Estat́ıstica, IBGE). This map was made using both the 2001 Household Survey and the 2000 Demographic Census and was used for the quotas until 2006, when it started being annually updated. In other words, given the target of 11 million families in the whole country, the 2001 poverty map guided how the program should have gradually grown across municipalities from 2003 to 2006. 23 Although the local government has the responsibility of registering poor families in the Single Registry (Cadastro Único), this registration does not mean automatic selection into the program. Registered families still have to prove they receive per capita income under the eligibility cut-off point and the total number of benefits cannot surpass the local quota. Under this cap, the order of eligible households is managed by the National Government and is based on per capita income and number of children. Figure 1.1 confirms that the number of benefits per municipality had strongly depended on the previous number of poor households, estimated using data from 2000 and 2001. In the top panel, we observe the relationship between the proportion of poor households (poverty headcount) in 2000, calculated using the Demographic Census, and the proportion of households covered by the program (program coverage) in 2004 and 2006, according to the official records. The initial poverty headcount explains 77% of municipal coverage in 2004, when the program was still expanding and had not reached the cap in most municipalities. In 2006, when the program reached its target, the relationship became even stronger and closer to the 45-degree line. 24 1.3.3 Data 1.3.3.1 Panel Sample and Variables All the data come from the National Household Survey (Pesquisa Nacional por Amostra de Domićılios, PNAD). This survey, which collects a broad set of information on demographic and socio-economic characteristics of households, included a special questionnaire on cash transfer programs in 2004 and 2006. This questionnaire asked whether any member of the household was beneficiary of each cash transfer program that was in place at the time of the survey. Henceforth, I consider as Bolsa Famı́lia all previous programs that had a similar goal and design (e.g., Bolsa Alimentação, Cartão Alimentação, Bolsa Escola, and PETI). In addition to these two survey years, I use the 2001 PNAD as a baseline. In 2001, the Bolsa Famı́lia program had not taken place yet and the other cash transfer programs did not have a significant size. However, I have to control for the small coverage of other programs that might contaminate the baseline outcomes. Accordingly, I identify those households receiving cash transfer from other social programs using the typical-value method developed by Foguel and Barros (2010). This method basically matches parts of household income, under the entry of ‘other incomes,’ with typical values transfered by each program. The PNAD is a cross-sectional survey, so it does not interview the same households every year. Thus I cannot construct a panel of households or even individuals. However, for each decade — i.e., the period between two Demographic Censuses —, the replacement of households on its sample occurs within the same census tracts.16 Namely, once a census 16A census tract is a neighborhood that has between 250 and 350 households in urban areas, 150 and 250 households in suburban areas, 51 and 350 households in informal settlement areas, 51 and 250 households in rural areas, and at least 20 households in indigenous areas (IBGE, 2003). 27 tract was selected for the sample in 2001, it kept being surveyed until 2009. Although they are not geo-referenced because the key variable is encrypted, we are able to identify the same census tracts and municipalities through the years. This sampling scheme permits the estimation of a fixed-effect model, described later in this chapter. Given the common characteristics of entrepreneurs, the sample is restricted to men who are between 25 and 45 years old and reside in urban areas. Indeed, empirical studies show that men are more likely than women to pursue entrepreneurial activity (Blanchflower, 2000; Karlan and Zinman, 2010). They also show that the probability of being an entrepreneur is increasing in age, but the probability of starting a new business is decreasing after 30 years old (Ardagna and Lusardi, 2010). Moreover, the desire for being self-employed is decreasing in age (Blanchflower, Oswald, and Stutzer, 2001). I also exclude public servants, people with higher education, and employers with more than five employees from the sample. Even though 6% of public servants were participating in the program in 2006, they are less likely to change occupation due to their job stability. The last two groups were excluded because only 1% of them were receiving the benefit in 2006, so they are not considered eligible for the transfer. In addition, business with more than five employees could already be well-established, so they are less sensitive at the extensive margin.17 Because of the exclusion of observation from the original sample, the survey weights are calibrated so that the three years have the same importance in the analysis. Table 1.2 presents the average number of observations per municipality in the final sample. About 130 households and 50 prime-age men are interviewed by municipality on average 17The exclusion of these employers reduces the sample by 1%, with no implication for the results. 28 every year. For some small municipalities, the number of observations may not be large enough to yield accurate estimates. However, the smaller the town, the more homogeneous is the population. Under such a circumstance, the program coverage at municipal level, which is the main intervention investigated in this paper, is given by the proportion of prime-age men living in a household that receives the conditional benefit. Table 1.2: Number of Observations per Municipality Std. Number of Mean Dev. Min. Max. municipalities 2001 Number of households 128.1 290.4 19 3,505 796 Number of sample-eligible men 52.4 128.1 5 1,571 796 2004 Number of households 136.8 305.1 23 3,575 796 Number of sample-eligible men 54.3 131.8 5 1,751 796 2006 Number of households 143.8 322.7 28 3,884 796 Number of sample-eligible men 56.4 136.1 5 1,753 796 ‘Sample-eligible men’ comprise men aged between 25 and 45 years old, with no college degree, and living in urban areas. This sample also excludes public servants and employers with more than five employees. According to Blanchflower (2000) and Blanchflower, Oswald, and Stutzer (2001), self- employment is the primary form of entrepreneurship. For this reason, I classify as en- trepreneurs those who either have this type of occupation or are small business owners. However, to distinguish entrepreneurial activity and informality, the definition also requires that they either perform a high-skilled job or contribute to social security. Namely, en- trepreneurs are subject to taxes and less vulnerable than informal workers in general. On the other hand, the government cannot track earnings of workers in the informal sector, whereas entrepreneurs have their earnings partially revealed on the government records. 29 Figure 1.2: Relationship between Entrepreneurship and Program Coverage 2001 2006 2006 − 01 difference 0 .01 .02 .03 ra te c ha ng e 0 .02 .04 .06 .08 en tr ep re ne ur sh ip r at e 0 .2 .4 .6 .8 2006 program coverage Entrepreneurship rate is measured by the proportion of small entrepreneurs per municipality. ‘2006 - 01 difference’ is the difference between entrepreneurship rates in 2006 and 2001 per municipality. Program coverage is measured by the proportion of individuals participating in the program in 2006. Municipalities where the program coverage was greater than 5 p.p. in 2001 are not included. Besides the increase of the formal sector and gradual expansion of Bolsa Famı́lia, other socio-economic improvements are observed in Table 1.3. As regards education, the proportion of adult men with a high school diploma increased 10 p.p. in five years. The same increase is seen in high school enrollment rate. In terms of health care, child mortality decreased from 12.7 deaths per 1,000 children up to 5 years old to 9.8 deaths. Finally, the proportion of houses linked to the sewer system increased 3 p.p. Given all the socio-economic improvements that happened in Brazil, it is critical to control for these variables to account for demographic changes and other social policies. 32 An important mechanism in which the program may affect entrepreneurship is through private transfers. This type of income is calculated as the sum of donations and other incomes, excluding retirement benefits, other pensions, rental earnings, and social benefits. The percentage of households receiving private transfers should increase along with liquidity in poor communities if they adopt informal risk-sharing strategies. In Table 1.3, we observe that this rate went from 4.3% in 2001 to 7.7% in 2006. 1.4 Empirical Strategy The empirical strategy consists of a difference-in-difference model estimated using a three- period dataset. As discussed above, the program coverage has been strongly driven by observables. According to Proposition 1.3, presented below, this condition is sufficient for the identification of the overall effect of the program using a model with municipality-level fixed effects. Furthermore, the identification assumption is weak enough to ignore the fact that some households are more likely to go after the benefit than others. The reason is that self-selection at the local level is not a concern when the comparison of treated and control observations occurs between municipalities, and not within municipalities. I call this assumption ‘Partial Aggregate Independence’ (PAI) because the aggregate growth of benefits is assumed to be exogenous even if the individual assignment is endogenous.18 In order to verify the reliability of the PAI assumption, I also present an Instrumental Variable (IV) strategy. The strategy uses the measure of local poverty in 2001, controlling for 18This assumption is the same adopted by Hsieh and Urquiola (2006) to identify the effect of choosing private schools over public schools on students’ achievement. 33 the current level of poverty and fixed effects, to predict variations in the program intervention. This instrument eliminates the part of variance in the program assignment that could be related to unobservable changes in the labor market. Moreover, the exclusion restriction is very likely to hold as long as the relationship between poverty and entrepreneurship does not change over time, which is a testable condition. This section also presents a definition for direct and indirect effects of cash transfer programs. The direct effect is understood as the individual response of households to the program benefit, while the indirect effect results from the interaction of individual responses. In contrast to Angelucci and De Giorgi’s (2009) definition, the indirect effect is seen not only as the impact that the program has on ineligible individuals, but also as the impact that it has on the whole community, including individuals receiving the benefit. Finally, I introduce a formal test to verify whether the indirect effect is different for indi- viduals who receive and do not receive the benefit (Proposition 1.4). Once the homogeneity in the indirect effect is confirmed, the estimated overall effect can be decomposed into the direct and indirect parts, adjusting for the self-selection bias. All proofs are provided in the appendix. 1.4.1 Fixed-Effect Model Let yivt be the decision of individual i living in municipality (city or village) v at time t of being an entrepreneur. Based on equation (1.5), this decision is determined by a linear structural model: yivt = β0 + β1divt + β2dvt + µv + µt + uivt, (1.6) 34 tor for β1 and β2 have the following asymptotic property: β̂1 p → β1 + E [uivtdivt] V ar (divt)− V ar ( dvt ) , β̂2 p → β2 − E [uivtdivt] V ar (divt)− V ar ( dvt ) . Note that the asymptotic biases cancel each other, so the estimator for τ = (β1 + β2) will be consistent if dvt is exogenous. Therefore, self-selection may be an issue if one compares individuals in the same city or village, but it is not if one compares cities and villages as a whole. Finally, the following proposition states the consistency of the identification strategy. Proposition 1.3 (Consistent Estimator for the Overall Effect) Consider the follow- ing equation: yivt = β0 + τdvt + µv + µt + uivt (1.7) If equation (1.6) is the true model, then the least squares (LS) estimator for τ in equation (1.7) is the sum of the LS estimators for β1 and β2 in equation (1.6): τ̂ = β̂1 + β̂2. Moreover, if the PAI Assumption holds, then the LS estimator for τ in equation (1.7) is consistent: τ̂ p → β1 + β2. Proposition 1.3 implies that the overall effect of the program, τ , can be consistently es- timated if we just omit divt in equation (1.6). Accordingly, I estimate equation (1.7) using a three-period data, with the standard errors clustered by municipality. For the sake of ro- bustness, I also include individual and local control variables in the main model and estimate another model with census-tract fixed effects. If the self-selection bias is proportional to the program size, dvt, violating the PAI assumption, then estimates conditional on census-tract 37 fixed effects should be different (less biased) than those conditional on municipality fixed effects. 1.4.2 Instrumental Variable Method One may argue that the PAI assumption is not reasonable because part of the variance of municipality coverage might be explained by unobservables related to the labor market. To consider only changes predicted by the measure of poverty in 2001, rather than changes caused by idiosyncratic behavior, I also estimate an Instrumental Variable (IV) model. In this model, the local coverage need not be strictly driven by observables, but it can be just partially affected by the program’s initial design. Assumption 1.2 (Instrumental Variable Assumption) Given the current poverty level, pvt, and unobserved fixed variables, the designed coverage is orthogonal to uivt. The designed coverage is captured by the interaction between the poverty headcount in 2001, pv0, and period dummies. Then the equation for the program coverage, dvt, is: dvt = γ0 + γ1 pv0 · I (t = 2004) + γ2 pv0 · I (t = 2006) + γ3 pvt + θv + θt + eivt. (1.8) The IV assumption implies that the residual relationship between occupational choices and the measure of poverty in 2001 does not change over time, unless by means of the own program coverage. Note that the constant relationship between occupational choices and the initial poverty headcount is controlled by the fixed effect, θv. Moreover, the current level of poverty, pvt, is also added as a control variable. Section 1.6.4 presents a test to verify whether that relationship changes over time. 38 Since the instrument is defined at the municipality level, the predicted change in the intervention also happens at the municipality level. Therefore, if the program coverage, dvt, is replaced by the individual treatment, divt, in equations (1.7) and (1.8), the estimated IV coefficient will be the same. See Proposition E.1 in the Appendix. This result reinforces the concept of overall effect defined above. Once the instrument is defined at the cluster level (e.g., randomization of treated villages), the comparison between treated and untreated individuals also happens in the cluster level — i.e., across villages rather than between individuals. On one hand, this IV approach avoids the problem of partial identification of the overall effect if using individual treatment. On the other hand, its interpretation cannot ignore the contribution of indirect effects for the estimated impact. 1.4.3 Separating Direct and Indirect Effects Unfortunately, estimating equation (1.7) does not reveal whether the effect of program size comes from either a direct effect on individuals receiving the transfer or an indirect effect that also affects individuals out of the program. Nonetheless, the PAI assumption is also sufficient for the indirect effect, β2, to be consistently estimated using only the sample of individuals out of the program (with divt = 0): yivt|(d=0) = β0,(d=0) + τ(d=0)dvt + µv,(d=0) + µt,(d=0) + uivt|(d=0) (1.9) Non-participants are subject to an overall effect, τ(d=0), that only comprises the indirect impact of the program. Therefore, the estimate of the indirect effect on this group can be 39 barely changes because the local-level instrument makes observations be compared between municipalities and not within municipalities. Namely, local coverage and individual benefit are interchangeable as a treatment variable, whose coefficients can both be interpreted as the overall effect of the program on participants. The estimated overall effect between 4-5 p.p. is found to be larger than PROGRESA’s in Mexico, estimated to be 0.9 p.p. by Bianchi and Bobba (2013). However, it is half as large as the Targeted Ultra-Poor program’s in Bangladesh (Bandiera et al., 2013) and the Youth Opportunities Program’s in Uganda (Blattman, Fiala, and Martinez, 2013). These two programs, nevertheless, are particularly intended to promote entrepreneurship, with the transfer being conditional on productive investments. 1.5.1.1 Type of Business Being Affected In order to analyze the nature of entrepreneurship being affected by the program, en- trepreneurs are classified by the type of business that they run. Namely, service, sales (wholesale and retail), and manufacturing. Table 1.5 shows the estimated coefficient of local coverage for these different types. Almost all the effect on entrepreneurship happens by increasing services, such as tailoring, shoe repair, automotive repair, and taxi driving. The remaining effect comes from sales business, while the effect on manufacturing is very close to zero. On one hand, the higher effect of services, followed by sales, is expected due to the lower cost of physical assets in this type of business. Some services do not even require a store and can be operated from home, while most sales and manufacturing business require 42 a larger initial investment in products and physical capital. On the other hand, services usually demand higher skills than sales. Unfortunately, no information on training programs is available, but we know that Bolsa Famı́lia does not have such a component. This result suggests that part of the transfers goes to the hands of already trained entrepreneurs, giving them the opportunity to formalize their activity. The creation of services, however, may not generate as many jobs as the creation of manufacturing businesses. The effect of Bolsa Famı́lia on job creation is discussed in Sections 1.6.2 and 1.6.3. 1.5.2 Direct and Indirect Effects In order to estimate the indirect effect of the program, I first have to verify whether it is homogeneous or not. According to Proposition 1.4, if the overall effect is linear, then the indirect effect of the program is homogeneous for the chosen sample. The first column of Table 1.6 indicates that the quadratic term for local coverage is very close to zero and not significant. Since the assumption of linear overall effect is not rejected, we can estimate the indirect effect of the program using only the sample of individuals who are not in the program. Columns (2) and (3) of Table 1.6 show this estimate. The indirect effect seems to be greater than the overall effect discussed above. That is, the direct effect should be negative. The last two columns show the estimates for the model including both levels of intervention — i.e., local and individual. These estimates are bias-adjusted using the previously estimated indirect effect. Nonetheless, the estimated selection bias is very close to zero.20 20The selection bias is measured with respect to entrepreneurship. Other intended outcomes, such as school enrollment and health care, may have different levels of bias. 43 The results indicate that, on one hand, cash transfers reduce the probability of partici- pants starting their own business in 3-4 p.p. On the other hand, the amount of cash trans- fered to poor towns seems to stimulate the creation of new businesses. A 10 p.p. increase in the program size seems to raise the entrepreneurship rate of poor individuals between 0.7 and 0.8 p.p. Because of this positive indirect effect, the net impact of cash transfers on entrepreneurship is also positive. This difference between direct and indirect responses is exactly the one predicted by Proposition 1.2. It indicates that small entrepreneurs are not as responsive to financial con- straints as to other general equilibrium mechanisms. However, there are several possible ex- planations for the negative direct effect and the positive indirect effect on entrepreneurship.21 In the next section, I show that the indirect response seems to be related to the promotion of informal financing mechanism among poor households. Furthermore, the hypothesis of increasing investment opportunity by shifting the aggregate demand is not supported by the following tests. 1.6 Potential Mechanisms 1.6.1 Transfers Between Households The first explanation for the positive indirect effect on entrepreneurship is the increasing number of households transferring money to each other. Like in Angelucci and De Giorgi’s (2009), the indirect effect of the cash transfer program might be driven by the existence of risk-sharing strategies within communities. If poor households follow these strategies, 21The negative direct effect does not seem to be driven by conditionalities on education because participants with no child also reduce entrepreneurial activity. See Appendix Table A.1. 44 that the higher the proportion of beneficiaries in the community, the higher the probability of being financially helped by another household. While individuals with better job opportunities may use these transfers as a safety net, individuals with less job opportunities may use them to start their own business. Since I do not know if current entrepreneurs had received other transfers before, I cannot conclude that these transfers are actually invested. The only conclusion that can be drawn is that the effect on receiving other transfers is the highest among those who most need them. Namely, the effect is significantly higher for the jobless, followed by informal workers. It is worth to clarify that I am not interested in the relationship between receiving other transfers and type of occupation, which cannot be identified as causal. The regressions presented in column (3) of Table 1.7 just intend to show the heterogeneity of the indirect effect by type of occupation. In order to verify whether the indirect effects on entrepreneurship and private transfers are related, I include the interaction between coverage and the predicted effect on private transfers in the regression (columns (4) and (5) of Table 1.7). This predicted effect is calculated by interacting coverage and several municipality characteristics in the estimation of private transfers. These “first-step” interactions already reveal, for instance, that the indirect effects of cash transfers on both private transfers and entrepreneurship are higher in lower density areas, with higher school enrollment rate and higher labor informality. Using the predicted effect on private transfers, I find that the larger this effect, the higher the indirect effect of Bolsa Famı́lia on entrepreneurship. Although this is just a back-of-the- envelope calculation, it indicates that entrepreneurial activity has increased through the promotion of informal risk-sharing mechanisms. 47 1.6.2 Aggregate Demand and Investment Opportunity If the indirect effect on entrepreneurship came from a shock in the aggregate demand, we should observe other changes in the labor market. For instance, increasing investment op- portunities should also affect the decision of high-educated men to become entrepreneurs. Moreover, with higher purchasing power, either more jobs should be created or higher salaries should be provided. Accordingly, I also estimate the indirect effect of cash transfers on these outcomes. The first two columns of Table 1.8 confirm that the program size has no significant effect on the probability of high-educated men becoming entrepreneurs. Thus we cannot say the program has encouraged the creation of local businesses in general. That is, the effect on entrepreneurship is concentrated among low-educated workers, who are probably connected to a network of eligible households. Furthermore, the estimates in columns (3) and (4) do not corroborate the hypothesis of job creation. Even though more low-educated men have taken the decision of being entrepreneurs, the program has had no effect on their overall employment rate. This result suggests that the program does not affect the demand side of the labor market. It may have just affected the occupational choice on the supply side. The direct and indirect effects of Bolsa Famı́lia on other occupational choices are discussed below. Although the employment rate has not been significantly affected by Bolsa Famı́lia, it is possible that the effect on the demand side has been just on wages. It is worth to notice that the estimated effect on wages can be misleading if the program has some influence on 48 local prices. Unfortunately, I do not have information on prices at the municipality level. However, I can use wages of low-educated public employees as a proxy for labor costs. Then the real effect on aggregate demand is assessed by the difference between private documented employees and public servants in terms of changes on wages. Indeed, the estimated coefficient for the interaction between program coverage and private employee, in the last two columns of Table 1.8, is very close to zero.23 1.6.3 Other Occupational Choices To understand where the responsive entrepreneurs comes from, I also investigate the effect of the program on other occupational choices. Besides entrepreneur, the alternatives are jobless, formal employee, informal employee, and informal self-employed. Table 1.9 presents the direct and indirect effects of the program on the probability of being in each one of these categories, vis-à-vis being in any other category. The estimated indirect coefficients indicate that the program has no significant effect on the proportion of jobless in intervened areas. The program does not have a significant indirect effect on the proportion of formal employees either. Once again, the hypothesis that the money injected in local economies shifts the demand for workers is not supported by these results. In other words, the increasing participation of documented employees in the Brazilian labor market in the 2000’s cannot be attributed as much to the Bolsa Famı́lia program as to other demographic and economic changes.24 23A regression of wages on program coverage, excluding public servants, would show that the effect is significantly positive. However, this effect is not only on private employees. The general effect on wages indicates that the impact does not come from the specific demand for labor, but from general labor costs. 24Articles in ‘The Economist’ magazine, published on Feb. 12 2009, and in ‘The New York Times’, published on July 31 2008, mentioned that Bolsa Famı́lia was an example of CCT program that has helped 49 Figure 1.4: Household Debt Outstanding and Interest Rate in Brazil Studied Period Interest Rate Debt 0 200 400 600 800 H ou se ho ld D eb t, B R L B ill io n 10 15 20 25 30 P rim e In te re st R at e, % p er y ea r Sep 2001 Sep 2004 Sep 2006 Sep 2010 Source: Central Bank of Brazil. Debt series is deflated by the National Consumer Price Index (INPC). Although the credit expansion started in the late 2000’s, other microcredit programs have been in place since the 1990’s. To test whether the results are driven by microcredit programs, I exclude from the sample the region where the largest and most significant program was introduced. The CrediAmigo program, created in 1997, is considered the largest microfinance program in the country, but it covers only municipalities in the Northeast region. Columns (4) and (5) of Table 1.10 show that the estimated effect on entrepreneurship slightly increases after omitting that region. Thus the results do not seem to be a consequence of the growth in microcredit either. Another form of convergence is through the migration of human capital. That is, social programs might have promoted the migration of potential entrepreneurs, as well as other 52 type of workers, to highly covered areas. As shown in Table 1.11, the program coverage has no significant effect on the probability of migrating from other municipality in the last four years. Therefore, the estimated effects are probably not due to changes in the composition of workers in the labor force, but due to changes in their decisions. 1.7 Conclusion This chapter investigated the causal relationship between conditional cash transfer (CCT) programs and the decision of being a small entrepreneur. Entrepreneurship is not usually an intended outcome of CCTs, since their goals are often strictly related to child development and income redistribution. However, investigating this outcome can tell us something about their broader impacts on economic development in the short run. Besides estimating the impact on an urban population, which is rarely seen in the literature about aid programs, the critical distinction of this analysis is the separation between direct and indirect effects. The identification of spillovers might reveal that the impact of those transfers goes well- beyond cash and conditionalities, uncovering the role of inter-household exchanges within the informal economy. Since the benefit is primarily assigned at the village level in most of the treated-control settings, evaluation designs usually allow only the identification of the overall effects of aid programs. In this study, the decomposition into direct and indirect effects is identified due to the variation in the size of the Bolsa Famı́lia program across municipalities in Brazil. Despite the issues with selection into the program, the overall effect is identified due to the exogeneity of the local coverage growth. Then the decomposition of this overall effect is 53 made by adjusting the coefficients for the estimated selection bias. Although this method is applied to observational data, it also introduces a new way of designing experiments, in which only the size (proportion of benefits) rather than the individual benefit is randomized at the cluster level.27 The results indicate that, on one hand, cash transfers have a negative direct effect on entrepreneurship, reducing the probability of beneficiaries to start their own business. This direct effect is associated with the negative impact that transfers have on the participation of workers in the formal sector. It suggests that the program encourage its beneficiaries to either reduce labor supply or move to the informal sector to not lose their cash benefit. This finding ratifies a major concern in welfare programs in general and reveals a caveat in terms of eligibility rules.28 On the other hand, the amount of cash transfered to poor villages seems to encourage the creation of new businesses, mostly in the service sector. There is no evidence, however, that this positive impact is driven by shocks in the aggregate demand. For instance, neither the proportion of high-educated entrepreneurs nor the number of formal jobs grew with the program. The lack of other impacts on the labor market indicates that Bolsa Famı́lia has indirectly changed the occupational choice of poor workers in the supply side, but not the demand for labor. This finding is not as exceptional as some CCT advocates claim, but it suggests that the program has been responsible for the formalization of low-skilled workers through self-employment. 27This new approach can be used to simplify the two-step randomization proposed by Duflo and Saez (2003) and Crepon et al. (2013). 28See Besley and Coate (1992), Kanbur, Keen, and Tuomala (1994), and Moffitt (2002). 54 Table 1.4: Overall Effect of Cash Transfers on Entrepreneurship Decision of being a small entrepreneur OLS FE IV (1) (2) (3) (4) (5) (6) program coverage, d -0.013* 0.042*** 0.040*** 0.058*** 0.056*** (0.008) (0.013) (0.013) (0.022) (0.021) individual benefit, d 0.057** (0.024) age (x10) 0.057*** 0.060*** 0.063*** 0.060*** 0.060*** 0.056*** (0.016) (0.016) (0.016) (0.016) (0.016) (0.017) squared age (x100) -0.002 -0.003 -0.004 -0.003 -0.003 -0.003 (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) white 0.039*** 0.032*** 0.025*** 0.032*** 0.032*** 0.026*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) black -0.011*** -0.014*** -0.013*** -0.014*** -0.014*** -0.014*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) married 0.024*** 0.025*** 0.030*** 0.025*** 0.025*** 0.027*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) elementary education 0.029*** 0.027*** 0.024*** 0.027*** 0.027*** 0.026*** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) primary education 0.028*** 0.028*** 0.022*** 0.028*** 0.028*** 0.024*** (0.002) (0.003) (0.002) (0.003) (0.003) (0.003) high school 0.030*** 0.031*** 0.020*** 0.031*** 0.031*** 0.021*** (0.003) (0.002) (0.002) (0.002) (0.002) (0.002) log of population -0.004*** -0.023 -0.020 -0.025* -0.021 -0.016 (0.001) (0.015) (0.014) (0.015) (0.015) (0.014) year = 2001 0.000 0.006* 0.003 0.008* 0.008 0.005 (0.002) (0.004) (0.004) (0.005) (0.005) (0.005) year = 2004 -0.002 -0.001 -0.001 0.000 0.001 0.001 (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) poverty headcount -0.029* -0.029 (0.018) (0.018) elementary enrollment rate 0.01 0.011 (0.020) (0.021) primary enrollment rate -0.016 -0.016 (0.012) (0.013) high school enrollment rate -0.014 -0.014 (0.012) (0.011) child mortality (x1000) 0.019 0.022 (0.054) (0.055) coverage of sewer system -0.005 -0.007 (0.012) (0.013) prop. of house owners 0.029 0.028 (0.020) (0.020) Municipality Fixed-Effects No Yes No Yes Yes Yes Census Tract Fixed-Effects No No Yes No No No Number of observations 129,298 129,298 129,298 129,298 129,298 129,264 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Standard errors in parentheses are clustered by municipality. Sample includes only men with high school diploma or less. Column (1) presents the regression coefficients obtained by Ordinary Least Squares (OLS). Columns (2) and (3) present the fixed-effect regressions (FE) obtained using the within-group method. Columns (4), (5), and (6) present the fixed-effect, Instrumental-Variable regressions (IV) with ‘program coverage’ and ‘individual benefit’ instrumented by the interactions between poverty headcount in 2001 and year dummies. 57 Table 1.5: Overall Effect of Cash Transfers on Different Types of Business Decision of being a small entrepreneur in Services Sales Manufacturing FE IV FE IV FE IV (1) (2) (3) (4) (5) (6) program coverage, d 0.038*** 0.053*** 0.015** 0.019 -0.004 -0.004 (0.010) (0.017) (0.008) (0.013) (0.007) (0.011) age (x10) 0.031*** 0.031*** 0.023* 0.023* 0.001 0.001 (0.012) (0.012) (0.012) (0.012) (0.010) (0.010) squared age (x100) -0.002 -0.002 -0.001 -0.001 0.002 0.002 (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) white 0.016*** 0.016*** 0.015*** 0.015*** 0.006*** 0.006*** (0.002) (0.002) (0.001) (0.001) (0.001) (0.001) black -0.006*** -0.006*** -0.005*** -0.005*** -0.005*** -0.005*** (0.002) (0.002) (0.002) (0.002) (0.001) (0.001) married 0.000 0.000 0.012*** 0.012*** 0.006*** 0.006*** (0.001) (0.001) (0.001) (0.001) (0.001) (0.001) elementary education 0.011*** 0.011*** 0.011*** 0.011*** 0.008*** 0.008*** (0.001) (0.001) (0.001) (0.001) (0.001) (0.001) primary education 0.012*** 0.012*** 0.015*** 0.015*** 0.003** 0.003** (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) high school 0.022*** 0.022*** 0.013*** 0.013*** -0.002 -0.002 (0.002) (0.002) (0.002) (0.002) (0.002) (0.002) log of population -0.012 -0.014 -0.016* -0.017* 0.003 0.003 (0.011) (0.011) (0.009) (0.009) (0.008) (0.008) year = 2001 0.020*** 0.022*** -0.008*** -0.008*** -0.004** -0.004 (0.003) (0.004) (0.002) (0.003) (0.002) (0.002) year = 2004 0.001 0.001 0.001 0.001 -0.002 -0.002 (0.001) (0.001) (0.002) (0.002) (0.001) (0.001) Municipality Fixed-Effects Yes Yes Yes Yes Yes Yes Number of observations 112,321 112,321 112,321 112,321 112,321 112,321 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Standard errors in parentheses are clustered by municipality. Sample includes only men with high school diploma or less. FE columns present the fixed-effect regressions obtained using the within-group method. IV columns present the fixed-effect, Instrumental-Variable regressions with ‘program coverage’ instrumented by the interactions between poverty headcount in 2001 and year dummies. 58 Table 1.6: Nonlinear, Indirect, and Direct Effects of Cash Transfers on Entrepreneurship Decision of being a small entrepreneur All Non-participants All sample sample FE IV FE IV (1) (2) (3) (4) (5) program coverage, d 0.045 0.070*** 0.079*** 0.070*** 0.079*** (0.028) (0.015) (0.024) (0.015) (0.024) squared coverage, d 2 -0.006 (0.043) individual benefit, d -0.032*** -0.041*** (0.004) (0.006) age (x10) 0.060*** 0.063*** 0.063*** 0.064*** 0.064*** (0.016) (0.018) (0.018) (0.016) (0.016) squared age (x100) -0.003 -0.003 -0.003 -0.003 -0.003 (0.002) (0.003) (0.003) (0.002) (0.002) white 0.032*** 0.034*** 0.034*** 0.031*** 0.031*** (0.002) (0.002) (0.002) (0.002) (0.002) black -0.014*** -0.015*** -0.015*** -0.014*** -0.014*** (0.002) (0.003) (0.003) (0.002) (0.002) married 0.025*** 0.029*** 0.029*** 0.027*** 0.027*** (0.002) (0.002) (0.002) (0.002) (0.002) elementary education 0.027*** 0.028*** 0.028*** 0.025*** 0.025*** (0.002) (0.002) (0.002) (0.002) (0.002) primary education 0.028*** 0.028*** 0.028*** 0.027*** 0.027*** (0.003) (0.003) (0.003) (0.003) (0.003) high school 0.031*** 0.030*** 0.030*** 0.030*** 0.030*** (0.002) (0.003) (0.003) (0.002) (0.002) log of population -0.024 -0.031* -0.032* -0.024 -0.026* (0.015) (0.017) (0.017) (0.015) (0.015) year = 2001 0.006 0.004 0.005 0.005 0.008 (0.004) (0.004) (0.005) (0.003) (0.005) year = 2004 -0.001 -0.001 -0.001 -0.001 0.000 (0.002) (0.002) (0.002) (0.002) (0.002) Municipality Fixed-Effects Yes Yes Yes Yes Yes Number of observations 129,298 113,267 113,267 129,264 129,264 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Standard errors in parentheses are clustered by municipality. Sample includes only men with high school diploma or less. Column (1) presents the fixed-effect model with quadratic effect of program coverage. Columns (2) and (3) present the estimates of the indirect effect on individuals who do not participate in the program. Columns (4) and (5) present the estimates of the indirect effect (program coverage) and direct effect (individual benefit), with bias correction given by Lemma 1.1. Columns (2) and (4), as well as columns (3) and (5), are jointly estimated using Seemingly Unrelated Regressions (SUR). FE columns show fixed-effect regressions obtained using the within-group method. IV columns show fixed-effect, Instrumental-Variable regressions with ‘program coverage’ instrumented by the interactions between poverty headcount in 2001 and year dummies. 59 Table 1.9: Indirect and Direct Effects of Cash Transfers on Other Occupational Choices Fixed-Effect Model Formal Informal Informal Entrep. Jobless employee employee self-emp. program coverage, d 0.070*** -0.004 0.020 -0.066*** -0.020 (0.015) (0.021) (0.027) (0.023) (0.027) individual benefit, d -0.032*** 0.029*** -0.056*** 0.029*** 0.030*** (0.004) (0.009) (0.012) (0.010) (0.012) Municipality Fixed-Effects Yes Yes Yes Yes Yes Year dummies Yes Yes Yes Yes Yes Demographic Yes Yes Yes Yes Yes N. of obs. - all sample 129,264 129,264 129,264 129,264 129,264 N. of obs. - d = 0 113,267 113,267 113,267 113,267 113,267 Instrumental Variable Model Formal Informal Informal Entrep. Jobless employee employee self-emp. program coverage, d 0.079*** 0.002 -0.001 -0.092*** 0.011 (0.024) (0.034) (0.040) (0.034) (0.039) individual benefit, d -0.041*** 0.041*** -0.050*** 0.004*** 0.046 (0.006) (0.014) (0.016) (0.016) (0.017) Municipality Fixed-Effects Yes Yes Yes Yes Yes Year dummies Yes Yes Yes Yes Yes Demographic Yes Yes Yes Yes Yes N. of obs. - all sample 129,264 129,264 129,264 129,264 129,264 N. of obs. - d = 0 113,267 113,267 113,267 113,267 113,267 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Standard errors in parentheses are clustered by municipality. Sample includes only men with high school diploma or less. All coefficients are estimated using Seemingly Unrelated Regressions (SUR). The indirect effect (program coverage) is estimated using the sample of non-participants, whereas the direct effect (individual benefit) is estimated using all sample and bias corrected according to Lemma 1.1. Fixed-Effect models are estimated using the within-group method. In the Instrumental-Variable models, ‘program coverage’ is instrumented by the interactions between poverty headcount in 2001 and year dummies. 62 Table 1.10: Overall Effect of Cash Transfers on Entrepreneurship, Robustness Analyses Decision of being a small entrepreneur 2001-2004 excluding Northeast FE FE IV FE IV (1) (2) (3) (4) (5) program coverage, d 0.036** 0.040** 0.062* 0.055*** 0.083** (0.015) (0.018) (0.032) (0.019) (0.033) poverty -0.026 (0.022) poverty * year = 2001(a) -0.004 (0.015) poverty * year = 2004(b) 0.004 (0.011) age (x10) 0.060*** 0.052** 0.052** 0.071*** 0.071*** (0.016) (0.020) (0.020) (0.020) (0.020) squared age (x100) -0.003 -0.002 -0.002 -0.004 -0.004 (0.002) (0.003) (0.003) (0.003) (0.003) white 0.032*** 0.032*** 0.032*** 0.037*** 0.037*** (0.002) (0.002) (0.002) (0.002) (0.002) black -0.014*** -0.016*** -0.016*** -0.013*** -0.014*** (0.002) (0.003) (0.003) (0.003) (0.003) married 0.025*** 0.026*** 0.026*** 0.027*** 0.027*** (0.002) (0.002) (0.002) (0.002) (0.002) elementary education 0.027*** 0.026*** 0.026*** 0.030*** 0.030*** (0.002) (0.002) (0.002) (0.002) (0.002) primary education 0.028*** 0.028*** 0.028*** 0.030*** 0.030*** (0.003) (0.003) (0.003) (0.003) (0.003) high school 0.031*** 0.038*** 0.038*** 0.033*** 0.033*** (0.002) (0.003) (0.003) (0.003) (0.003) log of population -0.020 -0.007 -0.008 -0.040** -0.044** (0.015) (0.022) (0.022) (0.018) (0.019) year = 2001 0.008* 0.007* 0.010* 0.007 0.009* (0.005) (0.004) (0.005) (0.004) (0.006) year = 2004 0.000 -0.001 0.000 (0.003) (0.002) (0.002) test (a) = (b) = 0, p-value 0.820 Municipality Fixed-Effects Yes Yes Yes Yes Yes Number of observations 129,298 84,543 84,543 91,656 91,656 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Standard errors in parentheses are clustered by municipality. Sample includes only men with high school diploma or less. Column (1) presents the estimate of the overall effect on entrepreneurship controlling for a time-varying relationship with poverty. Columns (2) and (3) present the estimates of the overall effect in the 2001-2004 period (excluding 2006). Columns (4) and (5) present the estimates of the overall effect in regions other than the Northeast. FE columns show fixed-effect regressions obtained using the within-group method. IV columns show fixed-effect, Instrumental-Variable regressions with ‘program coverage’ instrumented by the interactions between poverty headcount in 2001 and year dummies. 63 Table 1.11: Overall Effect of Cash Transfers on Migration Migration FE IV (1) (2) program coverage, d 0.014 -0.030 (0.023) (0.043) age (x10) -0.067*** -0.067*** (0.023) (0.023) squared age (x100) 0.005 0.005 (0.003) (0.003) white 0.004* 0.004* (0.003) (0.003) black 0.003 0.003 (0.004) (0.004) married 0.021*** 0.021*** (0.003) (0.003) elementary education -0.004 -0.004 (0.004) (0.004) primary education 0.001 0.001 (0.002) (0.002) high school 0.006* 0.006* (0.003) (0.003) year = 2001 -0.057*** -0.063*** (0.006) (0.009) year = 2004 -0.002 -0.003 (0.003) (0.003) Municipality Fixed-Effects Yes Yes Number of observations 129,298 129,298 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Sample includes only men with high school diploma or less. Standard errors in parentheses are clustered by municipality. Columns (1) and (2) present the estimates of the overall effect on the probability of living in the same municipality for less than five years. FE column shows the fixed-effect regression obtained using the within-group method. IV column shows fixed-effect, Instrumental-Variable regression with ‘program coverage’ instrumented by the interactions between poverty headcount in 2001 and year dummies. 64 bankruptcy had become so common and why the 2005 reform was necessary to lessen the payoff of opportunist debtors. Even though the U.S. bankruptcy law has separate procedures for individuals and corpo- rations, personal bankruptcy system also applies to small firms. For unincorporated business, all debt is legally considered personal debt. Thus in the case of business failure, the owner can file for personal bankruptcy and have both business and personal debts discharged. Furthermore, creditors who lend to small incorporated firms often require that their own- ers personally guarantee the loan. This eliminates owner’s limited liability for firm’s debt and makes it an corporate/noncorporate hybrid. As a result, it is estimated that at least 20% of all personal bankruptcy filings contain some business debt (Sullivan, Warren, and Westbrook, 1989; Lawless and Warren, 2005). The empirical literature on the effect of bankruptcy law on entrepreneurship basically comprises two types of analysis: cross-country and cross-state in the U.S. Cross-country studies include the ones made by Acharya and Subramanian (2009), Armour and Cumming (2008), and Lee et al. (2011). Their findings suggest that pro-creditor laws are negatively correlated with the self-employment rate, creation of new businesses, and level of innovation. However, no law change is clearly identified as orthogonal to potential economic outcomes in these studies. It is hard to argue that reforms in the bankruptcy law have not been driven by shifts in the economic development of each country. The other set of studies, which includes Fan and White (2003), Berkowitz and White (2004), Garrett and Wall (2006), Georgellis and J.Wall (2006), Hasan and Wang (2008), 67 Mathur (2009), Cerqueiro and Penas (2011), and Primo and Scott (2011), investigates the effect of property exemptions in the U.S. states. Their findings suggest that higher property exemptions reduce access to credit, but this negative effect on business creation can be offset by increasing wealth insurance. Thus the net effect of property exemptions on the probability of owning a business seems to be non-monotonic. However, their findings also suggest that the net effect on innovative entrepreneurship is never positive. The identification strategy of these studies is criticized by Malani, Posner, and Hynes (2004), who claim that changes in state laws are not exogenous but instead driven by eco- nomic outcomes. Historical evidence suggests that state exemptions were used as a way to attract migrants, already in debt, to sparsely populated areas. The historical determinants of state exemptions seem also to explain their recent changes, which indicate a convergence between state laws. Moreover, they find that states that opt for low exemption levels ac- tually care about the increasing cost of existing and future bankruptcy petitions. If we consider that changes in bankruptcy laws follow to some extent the process of economic development, it is reasonable to predict that the correlation between debtor-friendly laws and entrepreneurship is positive between countries and negative within countries. Unlike changes in state laws, the Bankruptcy Reform of 2005 was not driven by the particular interests of any state. This act affected everybody in the U.S. regardless the location. On one hand, this type of reform can be considered orthogonal to changes in local economies, but it rarely allows the identification of counterfactual outcomes. On the other hand, limitations on the use of state homestead exemptions, along with the creation of a ’means test’ in the process of filing for bankruptcy under Chapter 7 — the one that 68 gives a fresh start — and higher costs of filing, makes some areas more affected by the new federal law than others. If we assume that the relationship between state laws and potential outcomes does not change over time under the absence of the reform — which is verified by the pre-reform trends —, a post-reform change in this relationship indicates a causal effect. This paper is not the first to exploit the 2005 reform to estimate the effect of bankruptcy law on entrepreneurship.2 However, it seems to be the first to perform a counterfactual analysis.3 2.2 The U.S. Personal Bankruptcy Law Before the 2005 reform, small entrepreneurs were allowed to choose between two personal bankruptcy procedures: Chapter 7 and Chapter 13. Under Chapter 7, also known as “liq- uidation,” debtors must give up all assets that exceed their state exemption level to the bankruptcy trustee, who uses these assets to repay creditors. Then all future earnings are completely exempt from repayment, allowing the debtor to have a “fresh start.” In prac- tice, most types of unsecured debt are discharged under Chapter 7, including credit card debt, installment loans, medical debt, unpaid rent, utility bills, tort judgments, and busi- ness debt if owning an unincorporated business. Other types of debt, such as secured loans, student loans, child support obligations, and debts incurred by fraud, cannot be discharged in Chapter 7. 2Paik (2013) estimates this effect by comparing entrepreneurship rates before and after 2005. However, he does not establish a control group, so many other economic changes might explain what happened between 2004 and 2006. 3Li, White, and Zhu (2011) use a similar identification strategy to estimate a reduced-form model of mortgage default rates. 69 effect after October 16, 2005. The general perception is that the reform is predominantly pro-creditor and restricts protections offered by the bankruptcy system (Paik, 2013). The provisions introduced by BAPCPA include a means test for debtors who want to file for bankruptcy under Chapter 7, limitations on the use of homestead exemptions, longer quar- antine between multiple filings, and increasing costs of filing. Prior to the 2005 reform, anyone could file for bankruptcy under Chapter 7 in spite of the income level. Under the new law, the eligibility of debtors to file under Chapter 7 is determined by their monthly family income averaged over six months. If debtors’ income is below the state median family income, then they are automatically eligible for Chapter 7. Otherwise, another test verifies whether the debtor has enough income left over after paying “allowed” monthly expenses. If the ’disposable income’ over a five year period exceeds either $10,000 or 25% of their unsecured debt, then the debtor cannot file for Chapter 7. If it is below these amounts, additional tests are applied. If the debtor is not eligible for Chapter 7 by failing the means test, as well as if the Court finds that the debtor is abusing the system, then either the case is dismissed or the debtor consents to a Chapter 13 repayment plan. With the new law, the repayment plan is applied for post-bankruptcy earnings in the next five years, rather than three to five years. Thus the value of I13 tends to higher. The remaining unsecured debts are not discharged until the repayment plan is completed. Since debtors can no longer automatically choose between Chapter 7 and Chapter 13, they may end up repaying more than what would be paid under Chapter 7. Namely, (U13 − I13) tends to be lower under the new law. 72 The new bankruptcy law puts restrictions also on the use of the homestead exemption. A debtor who has migrated state-to-state within two years must use exemptions from the state of origin. It prevents debtors from moving assets and residence to a state with more exemptions. In addition, the homestead exemption is limited to $125,000 unless debtors have owned their homes for at least 3.3 years at the time they file for bankruptcy. This makes it difficult or at least less beneficial to convert nonexempt assets (W ) into home equity (H). Accordingly, states with unlimited homestead exemptions, such as Texas, Kansas, and Iowa, as well as states with exemptions above $125,000, such as Minnesota and Nevada, tend to be more affected by the reform. Another reform provision increased the waiting period between two Chapter 7 cases from six to eight years and the period between two Chapter 13 cases from six month to two years. Also, the debtor cannot file for Chapter 13 for at least four years after a Chapter 7 case is discharged. Before the reform, debtors were allowed to file for Chapter 13 immediately following a Chapter 7 discharge in order to pay the remaining outstanding debts. This procedure, known as “Chapter 20,” used to increase debtors’ financial gain relative to filing under either procedure alone. Finally, debtors are now required to take a credit counseling course before they file for bankruptcy and a financial management course before their debts are discharged. They must also provide detailed financial information along with the past four years of tax returns to the bankruptcy court, being all filings subject to audit. Lawyers are required to conduct an investigation of their clients and can be held personally liable for inaccuracies. As a result, lawyers are also allowed to charge higher fees for this risk. Elias (2009) estimates that the 73 cost of filing has been raised from $800-$1,400 to $2,500-$3,500, not including courses and preparation of tax returns. 2.3 Data and Descriptive Statistics The main source of data used in this essay is the March Supplement of the Current Population Survey (CPS) from 2000 to 2008. This survey has the advantage of being a twice-observed annual panel and having an uninterrupted series. To match consecutive March CPS surveys, I adapt the algorithm proposed by Madrian and Lefgren (2000). For households that share the same identifier, I verify if at least one member has similar age and the same sex, race, and citizenship status in two different years. The attrition rate stays between 20-30%, which is close to that found by Drew, Flood, and Warren (2013) and Neumark and Kawaguchi (2004). I do not have to match all individuals over time because the unit of observation is the household. However, I consider that nonrelatives living together, such as roommates, foster children, and household guests, belong to a separate household. The measure of entrepreneurial activity is defined as the proportion of households with at least one member working full time as either self-employed or business owner, not in- cluding farming. Even though this measure is often used in the literature (e.g., Evans and Leighton, 1989; Fairlie, 1999; Quadrini, 1999; Blanchflower, 2000; Hurst and Lusardi, 2004), it is sometimes criticized for being too broad, since not every self-employed pursues a busi- ness opportunity (Parker, 2004; Ardagna and Lusardi, 2010) and not every entrepreneur is innovative (Baumol, Litan, and Schramm, 2007). To partially take these differences into account, I also distinguish household businesses between incorporated and unincorporated 74 It is worth to notice that the entrepreneurship rate was significantly higher in states with homestead exemptions greater than $125,000, including states with unlimited exemptions, before the bankruptcy reform. However, the average business earnings were lower in those states. These differences are consistent with the theory that the homestead exemptions work as an insurance for small businesses. Since the 2005 reform has reduced the role of high exemptions, entrepreneurship is expected to fall in those states. This prediction is confirmed in Figure 2.1, which also shows that high- and low-exemption states had followed similar trends until 2005. These parallel trends raise my confidence in using a difference-in- differences approach, as described in the next section. Figure 2.1: Proportion of Entrepreneurs per Homestead Exemption and Year .12 .14 .16 .18 P ro po rt io n of e nt re pr en eu rs 20 00 20 01 20 02 20 03 20 04 20 05 20 06 20 07 Year Homestead exemption > $125K Homestead exemption ≤ $125K 95% confidence interval 77 2.4 Empirical Strategy The empirical strategy consists of a difference-in-differences (DID) model that compares states with unlimited homestead exemptions (treatment 1), states with high, but limited exemptions (treatment 2), and states with low exemptions (control) over time. The DID parameters are estimated using nonlinear models — i.e., multinomial logit and bivariate probit. Both models are described below. 2.4.1 Multinomial Model of Entrepreneurial Choice Let yi,t be the entrepreneurial choice of household i at time t, which is equal to 0 if they do not have a business, equal to 1 if they have an unincorporated business, and equal to 2 if they have an incorporated business. This choice is determined by the following multinomial logit model: log Pr(yi,t+1=k) Pr(yi,t+1=0) = τk,1UE i + τk,2HE i + τk,3UE iRt + τk,4HE iRt + θk,t + β ′ kxi,t, for k = 1, 2, (2.1) where UE i identifies states with unlimited exemptions, HE i identifies states with limited exemptions above $125,000, Rt identifies the post-reform period (after 2005), θk,t represents year-specific effects, and xi,t is a vector of control variables. From equation (2.1), I can calculate the conditional probability of having an incorporated business: Pr (yt+1 = 2|xt,UE ,HE , t) = exp (τ2,1UE + τ2,2HE + τ2,3UE ·Rt + τ2,4HE ·Rt + θ2,t + β′ 2xt) 1 + ∑2 k=1 (τk,1UE + τk,2HE + τk,3UE · Rt + τk,4HE ·Rt + θk,t + β′ kxt) ; 78 and the conditional probability of having an unincorporated business: Pr (yt+1 = 1|xt,UE ,HE , t) = exp (τ1,1UE + τ1,2HE + τ1,3UE ·Rt + τ1,4HE ·Rt + θ1,t + β′ 1xt) 1 + ∑2 k=1 (τk,1UE + τk,2HE + τk,3UE · Rt + τk,4HE ·Rt + θk,t + β′ kxt) . For the average household, whose xi,t is equal to the mean vector x̄, the effect of the reform on the probability of having an incorporated business (k = 2) in unlimited-exemption states (UE = 1) is defined by the following DID parameter: DIDInc UE = Pr (y = 2|x̄,UE = 1,HE = 0, R = 1)− Pr (y = 2|x̄,UE = 0,HE = 0, R = 1) − [Pr (y = 2|x̄,UE = 1,HE = 0, R = 0)− Pr (y = 2|x̄,UE = 0,HE = 0, R = 0)] (2.2) The effect of the reform on the probability of having an unincorporated business (k = 1), DIDUninc UE , is similarly defined. Finally, the effect of the reform on the probability of having any type of business (k ∈ {1, 2}) in unlimited-exemption states (UE = 1) is: DIDAny UE = DIDInc UE + DIDUninc UE . (2.3) The effect of the reform in states with high, but limited exemptions (HE = 1), DIDAny HE , and its components, DIDInc HE and DIDUninc HE , are defined in the same way. The standard errors of the estimated effects are clustered by state and computed using the delta method, as suggested by Ai and Norton (2003).4 4See also Greene (2010). 79 Table 2.2: Wald Tests for Instrument Validity Householder Householder’s father Householder is a US citizen is native citizen with disability χ2 p-value χ2 p-value χ2 p-value initial condition, α = 0 3.13 0.077 63.51 0.000 101.9 0.000 starting a business, β0 = 0 5.46 0.020 7.39 0.007 0.01 0.907 keeping the business open, β1 = 0 0.76 0.383 38.33 0.000 0.83 0.362 either transition, β0 = β1 = 0 10.00 0.007 44.62 0.000 1.60 0.449 Tests are performed after estimating equations (2.4), (2.5), and (2.6). With the coefficients of equations (2.4), (2.5), and (2.6), I can calculate the conditional probability of starting a business: Pr (yt+1 = 1|yt = 0,UE ,HE , t, zt) = Φ2   τ0,1UE + τ0,2HE + τ0,3UERt + τ0,4HERt + θ0,t + β′ 0xt, − (γ1UE + γ2HE + γ3UERt + γ4HERt + ηt + α′zt) ,−ρ   1− Φ (γ1UE + γ2HE + γ3UERt + γ4HERt + ηt + α′zt) ; and the conditional probability of keeping a business open: Pr (yt+1 = 1|yt = 1,UE ,HE , t, zt) = Φ2   τ1,1UE + τ1,2HE + τ1,3UERt + τ1,4HERt + θ1,t + β′ 1xt, γ1UE + γ2HE + γ3UERt + γ4HERt + ηt + α′zt, ρ   Φ (γ1UE + γ2HE + γ3UERt + γ4HERt + ηt + α′zt) ; where Φ(.) is an univariate normal distribution and Φ2(.) is an bivariate normal distribution. For the average household, the effect of the reform on the probability of starting a business in unlimited-exemption states (UE = 1) is defined by the following DID parameter: DID Start UE = Pr (yt+1 = 1|yt = 0,UE = 1, R = 1, z̄)− Pr (yt+1 = 1|yt = 0,UE = HE = 0, R = 1, z̄) − [Pr (yt+1 = 1|yt = 0,UE = 1, R = 0, z̄)− Pr (yt+1 = 1|yt = 0,UE = HE = 0, R = 0, z̄)] ; (2.7) 82 and the effect on the probability of keeping a business open is defined by: DID Keep UE = Pr (yt+1 = 1|yt = 1,UE = 1, R = 1, z̄)− Pr (yt+1 = 1|yt = 1,UE = HE = 0, R = 1, z̄) − [Pr (yt+1 = 1|yt = 1,UE = 1, R = 0, z̄)− Pr (yt+1 = 1|yt = 1,UE = HE = 0, R = 0, z̄)] . (2.8) The parameters for states with high, but limited exemptions (HE = 1), DIDStart HE and DIDKeep HE , are similarly defined. Once again, the standard errors of the estimated effects are clustered by state and computed using the delta method. 2.5 Results 2.5.1 Testing Changes in Pre-Reform Trends Before I present the main results of this chapter, it is worth to discuss whether the difference- in-differences strategy is valid. In case the entrepreneurship rate in high-exemption states had followed its own trend until 2005, I cannot compare changes between high- and low- exemption states. Figure 2.1 already suggests that their trends look similar. To test trend differences, I run several logit regressions using only data between 2000- 2005, before the reform. In each regression, I include interactions between the treatment variables, UE and HE , and different time periods. The significance of these interactions raises a red flag regarding my identification strategy. Table 2.3 presents the test results. 83 Table 2.3: Testing Pre-Reform Differential Trends Type of business Unincorporated Incorporated coef. std. error coef. std. error unlimited exemption * (year > 2000) 0.129 0.095 -0.048 0.116 high exemption * (year > 2000) 0.103 0.110 -0.259 0.113** unlimited exemption * (year > 2001) 0.101 0.109 -0.011 0.101 high exemption * (year > 2001) -0.079 0.090 -0.141 0.148 unlimited exemption * (year > 2002) 0.074 0.060 0.123 0.133 high exemption * (year > 2002) -0.090 0.067 -0.167 0.094* unlimited exemption * (year > 2003) 0.042 0.066 -0.025 0.099 high exemption * (year > 2003) -0.056 0.094 -0.087 0.079 unlimited exemption * (year > 2004) 0.023 0.050 0.002 0.073 high exemption * (year > 2004) 0.133 0.150 -0.200 0.213 ***, **, * represent statistical significant at the 1%, 5%, and 10% levels, respectively. Each pair of rows comes from a different a multinomial logit regression. All regressions include control variables, as listed in Table 2.1. Standard errors are clustered by state. According to the test results, there is just a slight change in the trend in states with high, but limited exemption. This change should particularly affect the results for incorporated business, which must be carefully interpreted. 2.5.2 Effect of the Bankruptcy Reform on Entrepreneurial Choice The estimates, presented in Table 2.4, confirm that the decline in entrepreneurial activity has been higher in states with high and unlimited exemption levels after the bankruptcy reform in 2005. As a result, the proportion of households owning a business has become 2 p.p. lower in those states, which represents a 16% reduction from the baseline proportion. 84 excluded. In this case, the reform has reduced the permanence rate in 7 p.p. which represents 10% of the baseline rate. All regression coefficients appear in the appendix. 2.6 Conclusion In summary, the results of this chapter confirm that the bankruptcy laws that protect debtor’s assets encourages households’ entrepreneurial activity. In particular, homestead exemptions tend to work as an insurance for small businesses, making individuals more willing to start their own venture. This protection, however, affects only the creation of unincorporated firms, whose all debt is legally considered their owners’ personal debt. 87 Chapter 3 Contrasts in Styles and Managers’ Impact on Corporate Policy1 3.1 Introduction The growth in CEO compensation has been in the center of the corporate finance litera- ture.2 The financial crisis stimulated this discussion and brought it to the newspapers’ front page. After the financial crisis, CEO costs and benefits were extensively discussed, with no definitive answer. Important questions related to the relevance of CEOs remain unanswered: Are there significant differences between the ways CEOs run the firms? Do these differences provide a competitive edge for the firm? Would the firm’s corporate policies be significantly different if another, and perhaps less expensive, CEO was in office? A large body of literature suggest that CEOs’ characteristics (risk aversion, ability, over- confidence, etc.) should generate heterogeneity in the firm’s corporate policies.3 Empirically, 1In collaboration with Igor Cunha. 2See for example Bebchuk and Grinstein (2005), Custodio, Ferreira, and Matos (2013), Fernandes et al. (2013), Kaplan (2008) and Jensen, Murphy, and Wruck (2004). 3For instance, please see, Rotemberg and Saloner (1993, 1994, 2000), Aggarwal and Samwick (2003), Shleifer and Vishny (1989), Morck, Shleifer, and Vishny (1990), Malmendier and Tate (2005a,b, 2008), Goel and Thakor (2008), and Ben-David, Graham, and Harvey (2013). 88 the literature has tried to quantify the CEO style exploring CEO fixed effect. In their semi- nal paper, Bertrand and Schoar (2003) use an F-test on a set of CEO fixed effects calculated using executives observed in two different firms in order to measure the style. They found that the CEOs preferences (style), can explain the heterogeneity of the different firm’s cor- porate policies (investment, financial, and organizational). Other papers have found that CEO style affects the firm’s accounting (Bamber, Jiang, and Wang, 2010) and tax practices (Dyreng, Hanlon, and Maydew, 2010), CEO compensation (Graham, Li, and Qiu, 2012), leverage choice (Frank and Goyal, 2007), and performance volatility (Adams, Almeida, and Ferreira, 2005).4 In a recent paper, Fee, Hadlock, and Pierce (2013) challenge the previous results in the literature, criticizing the use of F-tests on three different grounds: (1) biases, (2) serial correlation and (3) Wooldridge (2010) warning about the validity of the F-test in panel data with an exploding N. In their paper, they explore the framework develop by Yonker (2011) and propose restricting the analysis to a sub-sample of turnovers considered exogenous to solve the bias problem and suggest a new test to overcome the F-test problems. They do not find evidence of CEO style affecting a firm’s corporate policy. Therefore, at this point there is no consensus on whether CEOs heterogeneous preferences could explain a firm’s corporate policy variation. In this chapter, we suggest an additional step to improve the inference on CEOs’ effects. Although Bertrand and Schoar (2003) results are subjected to criticism, the test suggested 4Earlier papers, instead of using fixed effects, directly observed the changes in policy around the turnover, see for example, Murphy and Zimmerman (1993), Denis and Denis (1995), and Weisbach (1995). 89