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Three essays in the economics of education : evidence from Canadian policies Duhaime-Ross, Alix 2015

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Three Essays in the Economics ofEducation: Evidence from CanadianPoliciesbyAlix Duhaime-RossB.A.&Sc.(Hons), McGill University, 2007M.A., Concordia University, 2010A THESIS SUBMITTED IN PARTIAL FULFILLMENT OFTHE REQUIREMENTS FOR THE DEGREE OFDOCTOR OF PHILOSOPHYinThe Faculty of Graduate and Postdoctoral Studies(Economics)THE UNIVERSITY OF BRITISH COLUMBIA(Vancouver)July 2015c© Alix Duhaime-Ross 2015AbstractThis dissertation evaluates the effects of various public policies related to education in Canada.Chapter 2 analyses the long-term effects of mandating immigrant children to attend school inthe language of the majority. Using the 1977 introduction of Bill 101 in Quebec, a law thatcompelled children, with some exceptions, to attend school in French, I identify the impacts ofstudying in French on first- and second-generation immigrant children in Quebec. I find strongevidence that the law led to a significant increase in immigrants’ propensity to use French athome and at work, in their probability of being employed or in school, being part of the labourforce, and choosing to live outside of the Montreal metropolitan area. Chapter 3 tests the em-pirical predictions of three theoretical saving frameworks in the context of saving for a child’spost-secondary education: the life-cycle saving model, the fixed-goal saving model, and the pro-crastination saving model. Using regression discontinuity and panel data regression techniques,I evaluate the effects of three Canadian education saving incentive programs on parents’ savingbehaviour in Registered Education Savings Plans (RESPs). The results indicate that the ac-tions of parents are generally consistent with the procrastination saving model. I estimate thathigher matching rates on contributions and lump-sum subsidies increased RESP contributionsand savings among lower-income families who applied for the programs. Furthermore, grantsconditional on opening an account generally caused all parents to start saving earlier for theirchild. Chapter 4 evaluates the impacts of education savings in incentivised education savingsaccounts on children’s overall education savings and their academic performance. To identifythese effects, I employ an instrumental variable approach that relies on the structure of Cana-dian saving incentives offered to parents for contributions to RESPs. I find no effect of the savingincentives on parents’ overall decision to save for their child’s post-secondary education. Amongparents who do save, I estimate a small but significant crowding-out effect of RESP savings oneducation savings in other types of saving vehicles. Finally, I find no evidence of a causal impactof savings in RESPs on children’s performance in school.iiPrefaceThis dissertation is original, unpublished, independent work by the author, Alix Duhaime-Ross.Chapter 3 has been approved by the UBC Human Ethics Research Board under the name“Parents’ Savings for Their Child’s Post-Secondary Education: Which Incentives Work andWhy?” and project number H14-02265. The views expressed in chapter 3 are those of theauthor, and do not necessarily reflect the views of Employment and Social Development Canadaor of the federal government.iiiTable of ContentsAbstract . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiPreface . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . iiiTable of Contents . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . ivList of Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viList of Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . viiiAcknowledgements . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xDedication . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . xii1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 12 Does Schooling in the Majority Language Matter? Evidence from Quebec’sBill 101 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32.2 Institutional Background . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 82.3 Empirical Approach . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 122.4 Empirical Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 202.5 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 412.6 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 432.7 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 483 Parents’ Savings for their Child’s Post-Secondary Education: Which Incen-tives Work and Why? . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 643.1 Context and Motivation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 643.2 Institutional Background: Education Saving Incentive Programs in Canada . . . 663.3 Theoretical Saving Models and Predictions . . . . . . . . . . . . . . . . . . . . . 703.4 Data . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 753.5 Empirical Strategy and Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . 773.6 Discussion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 873.7 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 903.8 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 923.9 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 99ivTable of Contents4 The Effects of Incentivised Education Savings Accounts on Children’s Educa-tion Savings and Academic Performance . . . . . . . . . . . . . . . . . . . . . . 1074.1 Introduction . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1074.2 Contribution and Related Literature . . . . . . . . . . . . . . . . . . . . . . . . . 1104.3 Institutional Background: Education Saving Incentive Programs in Canada . . . 1144.4 Empirical Approach . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1174.5 Empirical Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1264.6 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1354.7 Figures . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1364.8 Tables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1405 Conclusion . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 150Bibliography . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 152Appendices . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 167A Charter of the French Language . . . . . . . . . . . . . . . . . . . . . . . . . . . 167B Additional Tables and Figures for Chapter 2 . . . . . . . . . . . . . . . . . . . 168C Additional Tables and Figures for Chapter 3 . . . . . . . . . . . . . . . . . . . 179D Additional Tables and Figures for Chapter 4 . . . . . . . . . . . . . . . . . . . 182vList of Tables2.1 Description of the Three Main Samples of Analysis . . . . . . . . . . . . . . . . . 482.2 Rules of Applicability of Bill 101 . . . . . . . . . . . . . . . . . . . . . . . . . . . 482.3 Descriptive Statistics (Sample 1) . . . . . . . . . . . . . . . . . . . . . . . . . . . 492.4 Effects on Language Use at Home and at Work . . . . . . . . . . . . . . . . . . . 502.5 Effects on Post-Secondary Education Attainment . . . . . . . . . . . . . . . . . . 512.6 Effects on Labour Market Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . 522.7 Effects on Income . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 532.8 Effects on the Probability of Living in Montreal . . . . . . . . . . . . . . . . . . . 542.9 Effects on Labour Market Outcomes by Residential Location . . . . . . . . . . . 552.10 Robustness and Placebo Tests (Sample 1) . . . . . . . . . . . . . . . . . . . . . . 562.11 Pooled 2006 and 2011 Results . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 582.12 Estimates of the Average Treatment Effects on the Treated . . . . . . . . . . . . 602.13 Effects on the Probability of Living Outside of Quebec in 1981 . . . . . . . . . . 612.14 Bounded Main Estimates (Sample 1) . . . . . . . . . . . . . . . . . . . . . . . . . 633.1 Value of the Canada Education Savings Grant (CESG) . . . . . . . . . . . . . . . 993.2 Recent Performance of the Canada Education Savings Program (CESP) . . . . . 993.3 Model Predictions for Each Saving Incentive Program . . . . . . . . . . . . . . . 1003.4 Saving Outcome Measures over Time . . . . . . . . . . . . . . . . . . . . . . . . . 1013.5 Saving Outcome Measures by Year of Birth of the RESP Beneficiary . . . . . . . 1023.6 Effects of the ACES Initial Grant on Parents’ Saving Behaviour . . . . . . . . . . 1033.7 Effects of the ACES Initial Grant on RESP Take Up . . . . . . . . . . . . . . . . 1043.8 Effects of the CLB on Parents’ Saving Behaviour . . . . . . . . . . . . . . . . . . 1043.9 Effects of the A-CESG on Parents’ Saving Behaviour . . . . . . . . . . . . . . . . 1053.10 Summary of the Empirical Results Obtained . . . . . . . . . . . . . . . . . . . . . 1064.1 Demographic Characteristics of Children in the Sample by Cross-Section . . . . . 1404.2 Statistics on Saving Amounts for Children in the Sample (1999-2012) . . . . . . . 1414.3 Effect of the CESG on a Child’s Probability of Having Education Savings . . . . 1424.4 Effect of the CESG on a Child’s Probability of Having Education Savings byIncome Groups . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1434.5 Effect of the CESG on a Child’s Probability of Having RESP Savings . . . . . . . 1444.6 Effect of the CESG on a Child’s Amount of RESP Savings (First Stage Results) . 145viList of Tables4.7 Effect of RESP Savings on a Child’s Probability of Having Other Education Savings1464.8 Effect of RESP Savings on a Child’s Amount of Other Education Savings . . . . 1474.9 Effect of RESP Savings on a Child’s Amount of Overall Education Savings . . . . 1484.10 Effect of RESP Savings on Academic Performance . . . . . . . . . . . . . . . . . 149B.1 Definitions of the Language Variables Used in the Analysis . . . . . . . . . . . . 170B.2 Effects on the Probability of Living in Quebec’s Provincial Capital . . . . . . . . 171B.3 Effects of Bill 101 by Sector of Work (Public Sector versus Private Sector) . . . . 172B.4 Robustness and Placebo Tests (Sample 3) . . . . . . . . . . . . . . . . . . . . . . 173B.5 Alternative Placebo Test Based on the Province of Ontario . . . . . . . . . . . . 175B.6 Alternative Measure of the Average Treatment Effects on the Treated . . . . . . . 176B.7 Bounded Main Estimates (Sample 3) . . . . . . . . . . . . . . . . . . . . . . . . . 177B.8 Effects on the Probability of Living Outside of Quebec in 1986 . . . . . . . . . . 178C.1 Effects of the ACES Initial Grant on Parents’ Saving Behaviour (with ControlVariables) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 179C.2 Effects of the ACES Initial Grant on Parents’ Saving Behaviour (with a TriangularKernel) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 180C.3 Effects of the CLB on Parents’ Saving Behaviour (with Control Variables) . . . . 180C.4 Effects of the CLB on Parents’ Saving Behaviour (with a Triangular Kernel) . . . 181D.1 Factors Associated with a Child’s Amount of RESP Savings . . . . . . . . . . . . 183D.2 Effect of RESP Savings on a Child’s Probability of Having Other Education Sav-ings (Estimated on the Restricted 1999-2007 Sample) . . . . . . . . . . . . . . . . 184D.3 Effect of the CESG Saving Incentive on a Child’s Probability of Having RESPSavings from Other Sources than Parents . . . . . . . . . . . . . . . . . . . . . . 185D.4 Effect of RESP Savings on Other Education Savings by Education Groups . . . . 186D.5 Effect of RESP Savings on Other Education Savings (with Additional ControlVariables . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 187D.6 Effect of RESP Savings on Other Education Savings (Estimated with the Alter-native IV) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 188D.7 Effect of RESP Savings on Other Education Savings Using an IV Specificationwith a Tobit First Stage . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 189D.8 Effect of RESP Savings on Academic Performance Using an IV Specification witha Tobit First Stage . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 190D.9 Effect of RESP Savings on Academic Performance (Using Binary Measures) . . . 190viiList of Figures2.1 Percentage of Elementary and Secondary School Students in Quebec Who Studyin French by Mother Tongue . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 432.2 Proportion of First- and Second-Generation Immigrants in Quebec Who SpeakFrench at Home (Sample 1) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 442.3 Proportion of First- and Second-Generation Immigrants in Quebec Who SpeakEnglish at Home (Sample 1) . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 442.4 Proportion of First- and Second-Generation Immigrants in Quebec Who UseFrench Most Often at Work (Sample 1) . . . . . . . . . . . . . . . . . . . . . . . 452.5 Proportion of First- and Second-Generation Immigrants in Quebec Who Use En-glish Most Often at Work (Sample 1) . . . . . . . . . . . . . . . . . . . . . . . . . 452.6 Quantile Triple Differences Estimates for Log Income from Wages . . . . . . . . . 462.7 Quantile Triple Differences Estimates for Log Total Income . . . . . . . . . . . . 462.8 Proportion of Children Without an Older Sibling Enrolled in School in 1977 byYear of Birth . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 473.1 Age Profiles of Average Yearly RESP Contributions by Birth Cohort . . . . . . . 923.2 Age Profiles of Average Yearly RESP Savings by Birth Cohort . . . . . . . . . . . 923.3 Average Age at RESP Creation by Date of Birth (ACES) . . . . . . . . . . . . . 933.4 Average RESP Contributions by Date of Birth (ACES) . . . . . . . . . . . . . . . 943.5 Average RESP Savings by Date of Birth (ACES) . . . . . . . . . . . . . . . . . . 953.6 Average Number of RESP Contributions by Date of Birth (ACES) . . . . . . . . 963.7 Percentage of Beneficiaries Residing in Alberta by Date of Birth (ACES) . . . . . 973.8 Average Age at RESP Creation by Date of Birth (CLB) . . . . . . . . . . . . . . 973.9 Average RESP Contributions by Date of Birth (CLB) . . . . . . . . . . . . . . . 983.10 Average RESP Savings by Date of Birth (CLB) . . . . . . . . . . . . . . . . . . . 984.1 Proportion of Children with Education Savings by Saving Vehicle over Time . . . 1364.2 Average Amount of Savings by Saving Vehicle Among All Children over Time . . 1374.3 Average Amount of Savings by Saving Vehicle Among Children with EducationSavings over Time . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 1374.4 Average Total Education Savings by Family Income (1999-2007) . . . . . . . . . . 1384.5 Average Total Education Savings by Parental Education Attainement (1999-2007) 1384.6 Reported Academic Performance of Children over Time . . . . . . . . . . . . . . 1394.7 Maximum Cumulative Nominal Amount of Basic CESG Elligble to Children byAge Group over Time . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 139viiiList of FiguresB.1 Proportion of First- and Second-Generation Immigrants in Quebec Who SpeakFrench at Home among Those Not Living with Their Parents (Sample 1) . . . . . 168B.2 Interprovincial Migration Patterns of Allophones and Francophones from 1966 to2006 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 169C.1 Histogram of the Number of Contributions to RESP Accounts Among A-CESGBeneficiaries in 2004 and 2005 . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 181ixAcknowledgementsI would not have completed this dissertation without the support and encouragement of manypeople around me. I would like to take the time to express my deepest gratitude to the severalpeople who made this project possible. I am particularly indebted to my supervisor, KevinMilligan, for his helpful advice, encouragement, patience, and interest in my research. Kevin isa kind teacher, an insightful researcher and an overall excellent advisor. I am also very gratefulfor the support and assistance provided by my other committee members: David Green andThomas Lemieux. They were not only generous with their time, but also insightful, and alwaysinterested in discussing research ideas, empirical techniques, and result implications. I thank youvery much.My research also greatly benefited from several discussions with Nicole Fortin, Craig Riddell, andthe participants of the UBC Public Finance research group: Daniel, Lori, Timea, Oscar, Tzu-Ting, and Joshua Gottlieb. I really appreciate your time and useful suggestions. Furthermore, Iwant to thank Ken Horricks, Martha Patterson, and Fernand Comeau at the Canada EducationSavings Program of Employment and Social Development Canada for their assistance, feedback,and for providing me with access to their database. I am especially grateful to Ken, who believedin my ideas, was enthusiastic about my work from the very beginning, and supported my researchambitions even when it seemed at times that all odds were against me. I acknowledge thefinancial support of the Fonds de Recherche du Québec - Société et Culture (FQRSC), the SocialSciences and Humanities Research Council (SSHRC), and the Canadian Labour Market andSkills Researcher Network (CLSRN). I also wish to thank Employment and Social DevelopmentCanada for financial support for the research presented in chapter 3.Completing this thesis was a professional challenge but also a personal one. I would like towarmly and sincerely thank my Vancouver family –Evan, Kiri, Dana, Jocelyne, Daniel, Colin,Elyse, Lori and Andy –with whom I learned, worried, laughed, and grew over the last five years.I am also very grateful to all my loyal and close friends in Montreal, particularly to Michèle, Caro,and Chloé, for their friendship, advice, and support – even when I was far away – and withoutwhom my life would neither be as rewarding nor as much fun.Most importantly, words cannot express how grateful I am to my parents, Carole Duhaime andChristopher Ross, who strongly believe that an education is not only one of the most useful toolsparents can provide to their child, but also one that no one can ever take away. My parents’xAcknowledgementsunconditional love, guidance, and encouragement throughout my life have made me the personthat I am today. I would not have succeeded without their advice and support. I consider themto be my role models in so many different ways. I am also extremely grateful to my loving andamazing sister, Arielle Duhaime-Ross, who is also my confidant and my very best friend. Arielle,you truly inspire me to be a stronger and better version of myself. I cannot believe how lucky Iam to have you in my life.Finally, I am immensely grateful to my partner, Eric Bond, who believed in me and supportedme every single step of the way throughout this challenging journey. My work greatly benefittedfrom his stylistic and grammatical revisions. More importantly, Eric, I would not have made itto the end without your patience, your reassurance, your encouragement, and your love. Thankyou.xiÀ mes parents, Chris et Carole, ainsi qu’à ma soeur Arielle.xiiChapter 1IntroductionEducation is central to economic, social and individual development. In economics, education isgenerally regarded as an investment in human capital, which increases workers’ productivity andbenefits the economy as a whole (theory of human capital). Education leads to both positiveindividual returns, such as increased lifetime earnings, as well as positive social returns, includinglarge positive externalities associated with schooling, such as production externalities, improvedcommunity health, higher civic involvement and reductions in crime. Capital market imper-fections, financial constraints, lack of information, and behavioural idiosyncrasies (e.g., myopicbehaviour or debt aversion) can, however, lead to individuals’ underinvestment in human capital.Most countries have thus introduced public policies to structure, encourage, support and financethe education of their citizens.1 It is essential to analyse the impacts of such policies in order togain economic insight into people’s behaviour as well as better understand the consequences andimprove the design of these policies.This dissertation evaluates the effects of various public policies related to language of instructionand saving incentive programs for post-secondary education in Canada. In chapter 2, I analysethe long-term effects of mandating immigrant children to attend school in the majority languageof the host region in terms of language use patterns, educational attainment, labour marketoutcomes, and choice of residential location. Using the 1977 introduction of Bill 101 in Quebec,a law that compelled children, with some exceptions, to attend primary and secondary school inFrench, I identify the long-term impacts of studying in French on first- and second-generationimmigrant children in Quebec. Specifically, I measure the effects of this law by exploiting theprecise implementation and exemption rules of the legislation through a triple differences frame-work. I find strong evidence that children who were mandated to attend school in French aremuch more likely than their peers to speak French at home and use French in their workplaceonce they have reached adulthood. I also estimate that the law led to a significant increase inthe probability of immigrants being employed or in school, being part of the labour force, andchoosing to live outside of the Montreal metropolitan area. In addition, the introduction of Bill101 caused some families to leave the province of Quebec so as to avoid sending their children to1For a review of studies on private and social returns to education, see Heckman, Lochner and Todd (2006),Lange and Topel (2006), Lochner (2011), and Oreopoulos and Petronijevic (2013). For a review of studies onfinancial or behavioural constraints in education and public interventions in education see Lochner and Monge-Naranjo (2012), Lavecchia, Liu and Oreopoulos (2014), and Kane (2006).1Chapter 1. Introductionschool in French. I perform a bounding exercise to account for the potential selection problemresulting from this increased interprovincial outmigration.The third and fourth chapters contribute to the literature on the financing of post-secondaryeducation by examining the effects of policies encouraging parents to save for their child’s highereducation in incentivised education savings accounts. In chapter 3, I study the effects of savingincentive programs (lump-sum subsidies and matching rates) on parents’ saving behaviour inCanadian Registered Education Savings Plans (RESPs). Specifically, I test the empirical predic-tions of three theoretical saving frameworks in the context of saving for a child’s post-secondaryeducation: the life-cycle saving model, the fixed-goal saving model, and the procrastination sav-ing model. Using regression discontinuity and panel data regression approaches, I evaluate theeffects of three Canadian education saving incentive programs on four outcomes: personal con-tributions, overall savings, the age of the child when the savings account was created, and thefrequency of contributions to the savings account. To measure these effects, I take advantage ofthe administrative database of the Canada Education Savings Program, which includes informa-tion on the education savings in RESPs between 1998 and 2012 of over 4.5 million children. Theresults suggest that the actions of parents are generally consistent with the behavioural procras-tination saving model when saving for their children’s post-secondary education in incentivisededucation savings accounts. I estimate that saving incentives, such as higher match rates oncontributions and initial subsidies, increased RESP contributions among lower-income familieswho applied for the programs. Furthermore, grants conditional on opening an account generallycaused all parents to start saving earlier for their child in RESPs.In chapter 4, I analyse the more general effects of education savings in incentivised educationsavings accounts on parents’ and children’s behaviour before they make the decision to attend acollege or university. In particular, I evaluate the causal impacts of education savings in RESPson children’s overall education savings as well as their academic performance. To identify theseeffects, I employ an instrumental variable approach that relies on the structure of Canadian savingincentives offered to parents for contributions to RESPs. Based on Canadian survey data, I findno effects of the saving incentives on parents’ decision to save for their child’s post-secondaryeducation in general; however, they have a strong positive effect on total education savings amongexisting savers, and on the use of RESPs as the vehicle for those savings. Among parents whosave, I estimate that for every additional dollar invested in a RESP, total education savingsincrease by 66 cents, suggesting a relatively small but significant crowding-out effect of RESPsavings on education savings in other types of saving vehicles. Finally, although RESP savingsand children’s academic grades are positively correlated, I find no evidence of a causal impactof savings in RESPs on children’s performance in school. Finally, in chapter 5, I summarisethe findings of this dissertation and present some overall conclusions and avenues for furtherresearch.2Chapter 2Does Schooling in the MajorityLanguage Matter? Evidence fromQuebec’s Bill 1012.1 IntroductionLearning the language of the majority is an important step towards the social and economic inte-gration of new immigrants in a region. In the case of immigrant children, numerous studies showthat majority language proficiency is strongly associated with higher educational attainment andfuture labour market success (Tainer, 1988; Dustmann and Soest, 2002; Bleakley and Chin, 2004;Chiswick, 2008; Akresh and Akresh, 2010; Lewis, 2011). Furthermore, there is some evidence,notably in the case of immigrants to the United States, that majority language influences otherimportant social and economic outcomes related to fertility, marriage, and residential location(Bleakley and Chin, 2010).In recent years, there has been significant interest in the language skills of immigrants dueto growing immigration in many countries, including Canada and the United States. As aresult of increased immigration, Canada has welcomed a growing number of elementary andsecondary level students for whom neither English nor French is a spoken first language (CanadianCouncil on Learning, 2008). In the United States, between 1992 and 2002, the number ofchildren with limited English proficiency in kindergarten through grade 12 increased 72% toreach approximately 8.4% of school-age children (Zehler et al., 2003). To address this concern,many schools offer bilingual education or English as a Second Language programs to help thesestudents improve their English language skills. Recently, certain states including California havemoved away from bilingual instruction towards English-only instruction (Zehler et al., 2003).There is, however, a considerable amount of variation in the implementation of these languageprograms and the circumstances under which they are offered. The estimated effects of thesevarious programs on student outcomes remain mixed (Durán, Roseth and Hoffman, 2010; Jepsen,2010; Chin, Daysal and Imberman, 2013).To ensure that new immigrant children learn the majority language, one approach is to require32.1. Introductionthat these children be educated in that language, thereby immersing them in the local environ-ment. If studying in the majority language increases the quality and number of employmentopportunities offered to immigrants, mandatory schooling in that language could increase im-migrants’ lifetime earnings as well as the quality of employer-employee matches in the labourmarket. On the other hand, if demanding that children study in a second or third language hasadverse effects on their academic performance, such a policy may increase barriers to achievinghigher levels of education, resulting in poorer economic outcomes. If that is the case, parentsmay perceive that the cost of learning the majority language exceeds the benefit for their child.In his paper on common culture and language, Lazear (1999) points out that, “Sometimes, poli-cies that subsidize assimilation and the acquisition of majority language skills can be sociallybeneficial”. He argues that trade between individuals, for example when negotiating a contract,may be facilitated when traders share a common language. However, learning an additionallanguage may be quite costly for immigrants (Lazear, 1999). Governments may be willing totolerate the social costs of mandatory majority language instruction in return for the perceivedsocial benefits. There exists, however, very little empirical evidence on the long-term individualeffects of implementing such policies, in terms of both economic benefits and costs.This paper explores the impact of such a policy by measuring the long-term effects of mandatingimmigrant children to study in the majority language of their host jurisdiction. Specifically, Ievaluate the effects of a law, introduced in 1977 in Quebec, that mandated most children beeducated in French, the majority language of this Canadian province. This law, The Charterof the French Language, also known as Bill 101, was implemented to promote and protect theFrench language in Quebec. One of the primary provisions of the law mandated all children livingin Quebec, with some exceptions, to attend school in French at the primary and secondary levels(kindergarten to grade 11).2 Prior to the introduction of Bill 101, most immigrant children inQuebec whose mother tongue was neither French nor English – referred to as Allophones – choseto study in English although the province was, and still is, largely Francophone.3 The legislationhad a major impact on Allophone children’s language of instruction. As Figure 2.1 shows, from1971 to 2006, the proportion of Allophone children enrolled in an elementary or secondary schoolwhere French was the language of instruction increased from 14.6% to 81.4% (Government ofQuebec, 2012). Although a few reports have documented the early education choices of the post-Bill 101 generation of immigrant children in Quebec (McAndrew, 2002; Paillé, 2002; Governmentof Quebec, 2012), to my knowledge, the long-run impacts of the law have not yet been examined.Using mainly Canadian Census data, I measure the long-term effects of mandatory schoolingin French due to Bill 101 on language use patterns in adulthood, as well as on the educational2In the interest of brevity, throughout this paper, the use of the term “Bill 101” refers to the section of thelegislation pertaining to the language of instruction although the law also addressed the use of French in otherdomains of society (see section 2.2.1 for details).3In this paper, I define Allophones as individuals whose mother tongue is neither French nor English. I defineFrancophones as those who include French as their mother tongue but not English.42.1. Introductionattainment, labour market outcomes, and residential location of Allophone immigrants in Que-bec, all of which are important dimensions of immigrants’ social and economic integration. Theidentification challenge is to evaluate the causal impact of language of instruction on variousindividual outcomes. This impact is generally difficult to measure since parents’ decision toeducate their children in a certain language is likely endogenous. If children who study in themajority language are unobservably different from those who study in another language due to,for example, parents’ preferences or their child’s perceived language acquisition abilities, then thedifference in outcomes between both groups of children will not be caused only by differences inlanguage of instruction. To address this concern, I exploit the strict applicability and exemptionrules of Bill 101 with respect to language of instruction in order to identify the causal impact ofthis law on various outcomes using a triple differences framework.In particular, I evaluate the effects of Bill 101 on first- and second-generation Allophone im-migrants since they were the main group targeted by the legislation.4 Among this group, Al-lophone children who were already enrolled in an English language school in Quebec prior toAugust 26, 1977 were exempt from the requirements of Bill 101. As a result, cohorts of childrenwho had started school before the implementation of the law in 1977 were allowed to study inEnglish, whereas younger cohorts were likely to be mandated to study in French. In addition,the law exempted all children with at least one parent who had studied in English in Quebecfrom mandatory schooling in French.5 I exploit this exception rule by using children with oneCanadian-born parent, thereby likely to have studied in English, as a comparison group for thosewith two foreign-born parents who were subject to the law. As an additional control group, Iuse Francophone immigrant children who presumably would have studied in French regardless ofthe law being in place. My empirical strategy is therefore rooted in comparing across Allophonesand Francophones the outcomes of pre- and post-Bill 101 school cohorts of immigrant children,with either one or two foreign-born parents.Bill 101 also exempted the younger siblings of children already enrolled in an English school in1977 from compulsory schooling in French. As a result, the proportion of Allophone childrentargeted by Bill 101 for which the law was actually binding (i.e., the proportion of “treated”children) varies across birth cohorts. I therefore estimate this proportion to recover estimates ofthe average treatment effect on the treated (ATT) from the main intent-to-treat (ITT) estimates.Furthermore, I assess the potential selection bias of my main estimates caused by children whowould have been affected by the new legislation being more likely to leave the province due tothe introduction of Bill 101 and being potentially different from those who remained in Quebec.4Following the 2006 Canadian Census definition, first-generation immigrants are defined as foreign-born indi-viduals who immigrated to Canada, whereas second-generation immigrants are individuals born in Canada withat least one parent who is a first-generation immigrant to Canada. Throughout the paper, I use the general term“immigrant” to refer to both first- and second-generation immigrants.5The exemption rule was subsequently modified as of 1983 by a ruling of the Canadian Supreme Court to“having one parent who studied in English in Canada”.52.1. IntroductionTo address this selection problem, I conduct a bounding exercise for the main effects of thelegislation in the spirit of Lee’s (2009) approach.I find that the introduction of Bill 101 caused a marked increase in the use of French amongtargeted Allophones once they reach adulthood. This increase was approximately 20 percentagepoints for both the probability of speaking French at home and at the workplace. Conversely,Allophones targeted by the law were approximately 26 percentage point less likely to speakEnglish at home and 15 percentage points less likely to use English at their workplace. I alsoestimate that the law was associated with an increase of 7 percentage points in the probabilityof female Allophone immigrants completing a post-secondary degree in Quebec. Furthermore,the results suggest that Allophone immigrants who were targeted by the law are less likelyto be unemployed and not attending school (by approximately 6 percentage points), as wellas being 8 to 9 percentage points more likely to be part of the labour force. The law alsoincreased the propensity of Allophone immigrants to reside outside of Montreal, the province’smain metropolitan area. I do not, however, find a significant impact of the law on earnings.Finally, I find strong evidence that Bill 101 caused up to 5.8% of Allophone families who weretargeted by the law to leave the province within a few years after its implementation so as to avoidsending their children to school in French. In addition, this outmigration was more concentratedamong highly educated and high-income families.The findings of this paper contribute to the existing literature in three ways. First, the intro-duction of Bill 101 in Quebec can be seen as a unique large natural experiment, which allowsfor a clear identification of the impact of requiring immigrant children to study in the majoritylanguage of a region. By taking advantage of the subtleties of the implementation and exemp-tion rules of the law and by comparing the long-term outcomes of Allophone children who weresubject to this law to those who were not, I obtain an estimate of the causal impact of com-pulsory schooling in French among Allophones on various outcomes of interest. Previous papersmeasuring the effects of majority language proficiency on earnings have generally either beendescriptive in nature or used an instrumental variable (IV) strategy to attempt to account forpotential endogeneity in the relationship between language and earnings (Chiswick and Miller,1995; Dustmann and Soest, 2002; Bleakley and Chin, 2010). However, none of these studies mea-sured the long-term effects of a policy change that aimed at increasing the majority languageproficiency of immigrants. The IV estimates may be very different from the average effects onthose targeted by such a policy depending on whose behaviour is affected by the instrumentused in the analysis. This paper exploits the variation in applicability rules of a sharp changein legislation, thereby providing estimates that pertain to an actual policy change, which aremeaningful, easy to interpret, and more likely to be externally valid and replicable in otherjurisdictions.Two previous papers have measured the impact of a large-scale national policy change affectingthe language of instruction of all children in a country, and the results were mixed (Angrist and62.1. IntroductionLavy, 1997; Angrist, Chin and Godoy, 2008). These papers, however, explore policy changesthat affected the entire student population of a country and not solely non-native speakers,making their results difficult to extrapolate to the case of immigrants. Lleras-Muney and Shertzer(2012) studied the impact of English-only school laws implemented in the U.S. between 1910 and1930 as part of the “Americanization movement” on immigrants’ education and labour marketoutcomes. They found modest positive effects of requiring English as the language of instructionon the literacy of foreign-born children, but no significant effects on educational attainmentor labour market outcomes. State level governments, however, often introduced these Englishschooling statutes at the same time as other compulsory schooling and child labour laws, makingit difficult to identify their effect independently from other major changes in the education systemat the time. In contrast, by using a control group within Quebec as part of the identificationstrategy, this analysis attempts to control for unobserved changes in the Quebec education systemover time, thereby isolating the effects on Allophone immigrants of mandatory schooling in themajority language.Second, this paper contributes to the literature by examining the long-term effects of mandatingmajority language schooling on a variety of different economic outcomes. The effects of sucha law are complex and relate to many dimensions that should be examined in order to havea more complete understanding of the impact of the policy. For example, acquiring majoritylanguage skills may increase immigrants’ internal mobility by lowering the cost of choosing toreside in regions where this language strongly dominates. In this way, such a language policycould improve the efficiency of the interregional allocation of workers. Many studies in theliterature focus solely on the effects of native language proficiency on immigrant wage gains,whereas this paper examines the impact of the legislation in terms of language use at home andat work, as well as on other outcomes such as educational attainment, employment, income,and sector of work (private or public).6 I also evaluate the effects of Bill 101 on immigrants’residential location as well as providing some evidence on which channels may explain the results.In addition, this paper is the first to address the impact of such a law on internal outmigrationand to bound the potential selection bias caused by this issue.Finally, studying the effects of Bill 101 provides a better understanding of long-run policy impli-cations. In the Canadian context, where the role of official languages is central to many policyquestions, this analysis will be useful in understanding the economic impact of this controversiallaw and in informing future decisions on the subject.7 In a general context, the results can in-form other governments investigating the implementation of similar policies related to languageof instruction, especially in the case of countries with a large proportion of non-native speakers6One notable exception is Bleakley and Chin (2010) who examine the effects of immigrants’ levels of Englishproficiency in the U.S. on earnings, marriage, fertility, and residential location.7See (Coleman, 1981) for a summary of the political context and reasons why the law was controversial at thetime.72.2. Institutional Background(such as the United States) or countries with multiple official languages.8The paper is structured as follows: Section 2.2 provides a description of the institutional back-ground of Bill 101. Section 2.3 discusses the empirical approach, including the data I use as wellas the identification strategy employed to measure the causal effects of the law. Some summarystatistics are also provided. Section 2.4 presents the main estimation results, including a dis-cussion of the selection problem resulting form interprovincial migration as well as the resultsof a bounding exercise. Robustness regressions and other limitations of the analysis are alsodiscussed. Section 2.5 offers concluding remarks.2.2 Institutional BackgroundThroughout this paper, I classify individuals into three groups based on their mother tongue:Allophones, Anglophones, and Francophones. The Canadian Census allows for individuals tostate more than one mother tongue. I define Allophones as individuals whose mother tongueis neither French nor English. I define Francophones as those who include French as theirmother tongue but not English and similarly, Anglophones as those who include English as theirmother tongue, but not French.9 This study focuses exclusively on Allophones and Francophonesin Quebec. Although Canada has two official languages, French and English, the country isprimarily Anglophone in all provinces except Quebec, where French is the most common languagespoken.10 In 2006, based solely on mother tongue, Quebec was composed of 79.6% Francophones,8.2% Anglophones, and 12.3% Allophones (Statistics Canada, 2012a). In the early 1970s, a fewyears before the introduction of Bill 101, the situation was similar. According to the 1971 Census,approximately 81% of Quebec residents were Francophone, 13% were Anglophone, and 6% wereAllophone. In addition, 88% of Quebec Allophones lived in Montreal, the largest metropolitanarea of the province (Bordeleau, 1973).The Quebec education system includes both English language and French language schools.11In the 1960s and early 1970s, the vast majority of non-Francophone immigrants in Quebecchose to send their children to English language schools as opposed to French language schools(McAndrew, 2002; Rocher, 2002). In 1971-1972, 85.4% of Allophone students studied in Englishin the province. In particular, among those who lived in the city of Montreal, 89.9% studied in8Examples of countries other than Canada with two or more official languages include Belgium, Bolivia, China,Finland, Haiti, India, Ireland, Peru, Singapore, South Africa, Switzerland, and Tanzania (Central IntelligenceAgency, 2014).9See Table B.1 in Appendix B for further details on mother tongue groups and the language variables used inthe analysis.10After Quebec, New Brunswick is the second province with the highest percentage of Francophones: approxi-mately 33% in 2011 (Statistics Canada, 2012a).11In 1976, 83.4 % of students in elementary and secondary schools in Quebec studied in French comparedto 16.6% who studied in English, excluding a small minority of students (less than 0.25%) who studied in anAboriginal language Government of Quebec (2012).82.2. Institutional BackgroundEnglish (Government of Quebec, 2012). During this period, Quebec’s shrinking French-speakingcommunity – in part due to the high enrolment of recent immigrant children in English languageschools – concerned many political leaders.12 As a result, the Government of Quebec implementedseveral laws to preserve and promote the French language in Quebec (Rocher, 2002; Governmentof Quebec, 1977).Prior to the implementation of The Charter of the French Language (Bill 101, 1977), the Gov-ernment of Quebec had introduced two other laws regarding the role of the French language inQuebec: The Law to promote the French language in Quebec (Bill 63, 1969) and The OfficialLanguage Act (Bill 22, 1974).13 Regarding the language of instruction in primary and secondaryschools, Bill 63 stated that the language of instruction in Quebec was French, but that childrenmay do their schooling in English if their parents or guardians had made a request at the timeof school enrolment. In contrast, Bill 22 was the first law that attempted to restrict access toEnglish language schools. Article 43 of the bill declared that students must have sufficient En-glish language skills to be allowed to study in English. To assess the level of English languageskills among children’s whose mother tongue was not English, the Quebec Ministry of Educationcould impose language knowledge tests. This verification process turned out to be ineffective andunpopular. Allophone parents who wished to enrol their children in English language schoolscould easily send their children to English language daycare centers or private kindergartens toprepare them for these language tests. Bill 22 thus failed to have an effect on the choice of thelanguage of instruction of Allophone and Anglophone children in Quebec (Paillé, 2002; Rocher,2002).2.2.1 Description of Bill 101On August 26, 1977, the province of Quebec adopted a new law, The Charter of the FrenchLanguage, also known as Bill 101. Similar to its two predecessors, this law was introducedto preserve the French language in the province of Quebec and, furthermore, to ensure thatFrench became and remained the common language of all Quebec residents. This law remains ineffect today, although over time there have been several amendments to the legislation. Bill 101proclaimed that French was the official language of Quebec and listed “fundamental languagerights”, such as the right of workers “to carry out their activities in French”, the right of consumersof goods and services “to be informed and served in French”, and the right of every person eligiblefor instruction in Quebec “to receive that instruction in French”. The law addressed the role ofthe French language in various domains of society: legislation and justice, civil administration,semi-public agencies, labour relations, commerce and business, and language of instruction.12The proportion of Francophones in Quebec decreased from 87.3% in 1951 to 84.4% in 1961, and reached82.5% in 1976 (Duchesne, 1980).13The French designations of Bill 63, Bill 22, and Bill 101 are respectively “La loi pour promouvoir la languefrançaise”, “La loi sur la langue officielle” and “La chartre de la langue française”.92.2. Institutional BackgroundOne of the principal components of the law, and the relevant component for this paper, concernedthe language of instruction in elementary and secondary schools in Quebec. This section ofthe law mandated immigrant children whose mother tongue was neither French nor English tocomplete their schooling in French while preserving the right of Anglophone residents of Quebecat the time, as well as their descendants, to obtain their education in English. Regarding languageof instruction, Bill 101 stated that all children living in Quebec, with some exceptions, mustreceive their elementary and secondary level instruction (Kindergarten to Grade 11) in French.14Children exempt from the law were allowed to attend an English language school at the requestof their parent or legal guardian. These children included the following:(a) A child who, in his last year of school in Quebec before the coming into force of the lawon August 26, 1977, was receiving his instruction in English, as well as the brothers andsisters of that child;(b) A child with at least one parent who completed their elementary instruction in English inQuebec;15(c) A child whose father or mother lived in Quebec on August 26, 1977 and received his or herelementary instruction in English outside Quebec.The last measure (part c) was put in place as a transitional measure for Anglophones livingin Quebec at the time and was removed from the legislation in 2010. In addition, childrenwhose mother tongue was an aboriginal language, those with learning disabilities, and temporaryresidents in the province were exempt from the law. One available avenue for parents who didnot qualify under one of the exception rules to avoid sending their children to school in Frenchwas to enrol their children in a non-subsidized English private school in Quebec. These schoolswere not subject to the legislation.16 In Quebec, however, the vast majority of children attendpublic or subsidized private schools. In 2005, less than 1% of Quebec students attended non-subsidized private schools, which are, in general, significantly more expensive (Marois, 2005).Between 1977 and 1989, of the children who started school after Bill 101 was introduced andwho were granted a certificate allowing them to study in English due to exemption rules of thelaw, 2% were exempt due to a learning disability, 7.3 % were exempt due to a temporary stay14Appendix A presents articles 72 and 73 of Bill 101 in their original form from the 1977 Statutes of Quebec.15Following a ruling from the Supreme court of Canada (The Canada Constitutional Act) this requirement waschanged in 1983 to read: “A child whose father or mother is a Canadian citizen and received elementary instructionin English in Canada, provided that that instruction constitutes the major part of the elementary instruction heor she received in Canada.” In addition, as of 1983, children who were previously enrolled in an English languageschool in another Canadian province before moving to Quebec were not required to attend school in French.16The Quebec education system includes publicly funded schools and subsidized private schools, which aresubject to provincial regulations (including Bill 101) and must follow the curriculum proposed by the QuebecMinistry of Education. The system also includes unsubsidized private schools, which are not subject to theseregulations. In 2005, 89.6% of students were enrolled in a public school compared to 9.55% in subsidized privateschools and less than 1% in unsubsidized private schools (Marois, 2005).102.2. Institutional Backgroundin Quebec and only 0.4% were exempt because they were attending a non-subsidized privateschool in English (Government of Quebec, 2012). These special exemption cases were thereforeuncommon and ignoring them should not significantly affect the results of the empirical analysis.By 2001, approximately 100,600 adults had completed their schooling in French rather than inEnglish because of Bill 101 since its introduction in 1977. This number represented 1.7% of theQuebec adult population (5.8 million adults) at that time (Paillé, 2002).The structure of the clauses of Bill 101 regarding mandatory schooling in French led to thegradual introduction of cohorts of Allophone children commencing primary school in the Frenchschooling system, which gave enough time to French instruction schools to prepare for the newinflow of Allophone students as of 1977. Bill 101 was introduced in a period of overall decliningfertility in Quebec. Between 1971 and 1998, both French and English language schools experi-enced a significant decrease in their enrolment, although English language schools experienced amore pronounced reduction, partly due to Bill 101 compelling the majority of new Allophone im-migrants to attend French language schools instead of English ones (McAndrew, 2002).17 Frenchlanguage schools in Quebec were thus likely not capacity constrained before the law was intro-duced. They were therefore able to easily accommodate the gradual increase in enrolment ofAllophone students following Bill 101 with their existing infrastructure.During this period, since the majority of Allophone children resided in Montreal, the changesover time in the ethnic composition of students enrolled in French language schools due to Bill101 mostly occurred in Montreal. In 1969, prior to Bill 101, French language schools in Montrealintroduced a system of “welcome classes” (translated from the French “classes d’accueil”) fornon-Francophone students.18 The goal of these “welcome classes” was to immerse the studentsin a French language environment so that they could acquire age-appropriate French languageskills that would facilitate their transition to the regular system and encourage the developmentof a positive attitude towards the Francophone community (Armand, 2005, 2011). These “wel-come classes” consisted of smaller groups of students than regular classes and students usuallyparticipated in these classes for a period of 10 months before transitioning to the regular schoolsystem. With the implementation of Bill 101 in 1977, the system of “welcome classes” becamemore wide-spread and still functions today in Quebec (St-Germain, 1981; Armand, 2011).17Between 1971 and 1997, enrolment in Quebec French langue schools decreased by 25% from 1,378,788 to1,033,879 students. In contrast, during the same period, enrolment in Quebec English language schools decreasedby 55% from 256,251 to 114,267 (Government of Quebec, 1999).18Several other countries, including France and Switzerland, have similar programs for immigrant children wholack the language skills needed to enter the regular school system (Government of the Republic and Canton ofGeneva, 2011; Government of France, 2012).112.3. Empirical Approach2.3 Empirical Approach2.3.1 DataThe paper is based on four data sources: the 1981, 1986, and 2006 cycles of the Canadian Censusand the 2011 National Household Survey. The main empirical analysis relies primarily on dataprovided by the long-form of the 2006 Canadian Census, which represents a cross-section of 20%of the Canadian population. To complement the main results, I use the 2011 National HouseholdSurvey (NHS) to examine the evolution of the long-term effects of the law between 2006 and2011.19 In addition, using the 1981 and 1986 Censuses, I measure the early interprovincialmigration patterns that resulted from the introduction of the law in 1977. I also employ theseearlier Censuses to bound my main estimates and to recover the average treatment effect onthe treated (ATT) estimates from the intent-to-treat (ITT) estimates. The Canadian Censusprovides a rich enough set of variables to identify, among first- and second-generation immigrants,who was likely to be subject to the law and who was likely to be exempt from it. Furthermore,the 2006 Census provides detailed information on various measures of language use at homeand in the workplace, which is essential to assess the direct impact of the law (see Table B.1 inAppendix B for a description of these language variables). This census also offers informationon many labour market outcomes, educational attainment, and residential location.The primary population of interest is composed of first- and second-generation Francophone andAllophone immigrants living in Quebec in 2001 and 2006, who were born between 1962 and 1981.They were thus between the ages of 25 and 44 in 2006. This birth cohort window correspondsto 10 years before and after the cut-off birth date for determining whether children were likelyto be subject to Bill 101, which was October 1, 1971 (these children would start school at age5 in September 1977 shortly after the law came into effect). Among that age group, these first-and second-generation Francophone and Allophone immigrants represent 20% of the Quebecpopulation. Furthermore, I restrict first-generation immigrants (i.e., who were born outside ofCanada) to those who immigrated to Canada before the age of 6. This age limit ensures thatthese young immigrants would have completed all of their elementary and secondary schooling inCanada. Unfortunately, the Census does not provide information on their province of arrival, so Iassume that the majority of first-generation immigrants arrived directly to Quebec and thereforedid their schooling in Quebec. This assumption seems reasonable since generally, Canadianimmigrants tend to remain in the province in which they first settled (Okonny-Myers, 2010).2019The National Household Survey (NHS) replaced the Canadian Census in 2011. The NHS is not directlycomparable to the previous Censuses as it was administered as a voluntary survey, resulting in a non-responserate of 31.4 %.20According to a report completed by Citizenship and Immigration Canada, the majority of immigrants whofirst settled in a province between 1991 and 2006 were still residing in that province in 2006. Among those who lefttheir province of arrival, the great majority of immigrants did not, however, move to Quebec. Ontario, BritishColumbia, and Alberta received the highest proportion of immigrants originally destined for other provinces(Okonny-Myers, 2010).122.3. Empirical ApproachIn the case of second-generation immigrants, I restrict the sample to those born in Quebec withat least one parent born outside of Canada. In addition, in all my analyses, I remove from thesample self-reported aboriginals because the law did not apply to aboriginal children since theywere allowed to study in their native aboriginal tongue. I also exclude from the sample individualswho reported using sign language as their mother tongue as well as temporary residents and non-permanent residents living in Quebec in 2006. The resulting sample, which represents the mainsample of analysis (Sample 1), comprises 24,090 people.In addition to this main sample, I perform the analysis on two more restrictive subsamplesin order to obtain robust estimates. First, because one may be concerned about a sampleselection problem arising from the composition of immigrants being different prior to and afterthe introduction of Bill 101 in 1977, I restrict first-generation immigrants in Sample 2 to those whoarrived prior to 1977. Second, because I cannot identify from the Census if these first-generationimmigrants resided exclusively in Quebec once they arrived in Canada (I am assuming they did),the third and most restrictive sample of analysis consists solely of second-generation immigrantsborn in Quebec (Sample 3). I assume that if these individuals were born in Quebec and stillreside in Quebec in 2006, it is very likely that they spent their entire life in Quebec. Table 2.1provides a description of the three samples as well as their relative sample sizes, which rangefrom 24,090 (Sample 1) to 20,740 individuals (Sample 3).2.3.2 Identification Strategy and EstimationAlthough Bill 101 affected both Allophone children and some Anglophone children living inQuebec, who, by and large, studied in English prior to the law being in place, this paper focusessolely on the effect of the law on Allophone children for three reasons. First, the law was intendedprimarily to mandate Allophone immigrants to adopt French instead of English when they firstarrived to Quebec; therefore, evaluating the effect of the law on its primary target group seemslike a natural first step. Second, as a consequence of this primary goal, the law was muchmore restrictive for Allophones than Anglophones. Through its various exemption rules, Bill 101allowed the majority of Anglophone children living in Quebec at the time of its implementation toattend school in English, whereas this was not the case for Allophone children. As a consequence,focusing only on Allophones allows for a cleaner identification strategy, as I can exploit threedistinct margins of variations to identify whether individuals were likely mandated to study inFrench or exempt from the law. Lastly, by focusing on Allophone immigrants in Quebec, theestimated effects may be more externally valid and thus relevant to the situations of immigrantsin other countries. The position of Anglophones in Quebec is less common, as they are a minoritylanguage group in Quebec while being part of the majority language group in Canada as a whole.This context may affect the interpretation of the potential effects of the law in their case.As mentioned briefly earlier, it is generally difficult to identify the causal economic impact of132.3. Empirical Approachchildren studying in a certain language due to potential omitted variable biases. The challengeis to isolate the effect of language of instruction from the presence of other unobserved factorscorrelated with both the outcomes of interest and the choice of language of instruction in orderto obtain unbiased results. To evaluate the causal effects of schooling in French on Allophoneimmigrants, I use the introduction of Bill 101 as a natural experiment. The law was introducedquickly after the unexpected election of a political party in November 1976.21 Furthermore, thestrict exemption rules of the legislation were chosen for administrative ease and to remove anyambiguities that occurred following previous language laws (Rocher, 2002). Due to these circum-stances, the implementation process and applicability rules of Bill 101 are arguably exogenous tothe outcomes examined. To measure the long-term effects on language use patterns, educationalattainment, residential location and labour market outcomes of being required to study in Frenchfor Allophone immigrants living in Quebec, I therefore exploit the introduction of Bill 101 aswell as its precise implementation and applicability rules. To identify, among Allophones andFrancophones, individuals who were likely to be subject to or exempt from Bill 101, I use threevariables present in the Census: their date of birth, their mother tongue and whether one or bothof their parents were born outside of Canada. Table 2.2 summarises my classification strategy.First, consider the case of Allophones. All those born on or prior to October 1, 1971 presumablystarted school by 1976, prior to this law being in place, and were thus allowed to continue studyingin English. October 1st is the relevant cut-off date since it is the day used by the Quebec Ministryof Education to determine whether a child is old enough to enter kindergarten (Government ofQuebec, 1965). Next, I use the parents’ place of birth as an indicator for their language ofinstruction. Ideally, I would like to be able to identify each person’s language of instructionas well as their parents’ language of instruction. Unfortunately, the Census does not providethis information. Among Allophones born after October 1, 1971, I assume that those with bothparents born outside of Canada were likely mandated to study in French by Bill 101 since theirparents probably did not study in English in Canada.22 In contrast, I assume that Allophonechildren with only one foreign-born parent were exempt from Bill 101 regardless of their birthdate since their Canadian-born parent probably studied in English in Canada, resulting in thembeing allowed to attend an English-language school.23 This assumption seems reasonable since,21The law was introduced by the “Parti Québécois”, a political party led by René Lévesque who first came intopower on November 15, 1976.22Using the 1981 Census, I estimate that the great majority (over 85%) of Allophone children likely to besubject to Bill 101 using this classification approach had foreign-born parents who immigrated after the age of10, making it very unlikely that they would have completed their elementary schooling in English. Among thosewith parents who arrived at an early age to Quebec, it could be the case that they attended an English languageelementary school in Quebec. It would then, however, be more likely that they would speak English with theirchildren, thus resulting in their children being classified as Anglophones, not Allophones, and being excluded fromthe sample.23Although the exemption rule of the law was originally restricted to children who had one parent who studiedin English in Quebec, if one parent completed his elementary schooling outside of Quebec in English but residedin Quebec on August 26th 1977, the child was also exempt from the law. As a consequence, the vast majority ofchildren with one Canadian-born parent who studied in English in Canada, regardless of the province of study,142.3. Empirical Approachhistorically, the vast majority of Allophones living in Quebec attended English language schools(Bordeleau, 1973; Government of Quebec, 2012).Thus, considering Allophones only, a simple difference-in-differences estimation strategy wouldinvolve estimating the difference in outcomes for birth cohorts of immigrants with two foreign-born parents (the treatment group targeted by the law) who started school before and after Bill101 was introduced relative to the same difference in outcomes for pre- and post-Bill 101 cohortsof immigrants with only one foreign-born parent (the control group exempt from being mandatedto study in French). The identifying assumption of this approach would be that the birth yearcohort trends in outcome variables of Allophones with two foreign-born parents and those withone foreign-born parent would have been the same (i.e., parallel trends) in the absence of thelaw being implemented. Such an approach, however, would not account for unobserved shocksor factors differentially affecting the outcomes of interest of certain birth cohorts of immigrantswith one Canadian-born parent relative to those with two foreign-born parents. For example, onepossible concern could be that the quality of education in French language schools was affectedby the unexpected inflow of Allophone students in these schools due to the introduction of Bill101. If for example, class sizes in French language schools increased during the first few yearsof implementing this law relative to pre-Bill 101 classes of students, this could affect students’academic performance and later labour market outcomes. As a second example, suppose thatindividuals with one Canadian-born parent have an unobservable advantage in the labour marketover those with two foreign-born parents due to stronger Canadian business connections in thelabour market or a larger knowledge of Canadian cultural customs. If this advantage were eitherlarger or smaller for post-Bill 101 birth cohorts due to factors other than attending school inFrench, this would also be cause for concern. In both these cases, the difference-in-differencesestimation would provide biased estimates because the gap in outcomes between Allophonessubject to and those exempt from the law could not solely be attributed to the effect of studyingin French due to Bill 101.To address concerns of this nature, I use an additional comparison group. Among first- andsecond-generation immigrants in the province, Francophones constitute a natural control groupfor Allophones, since presumably they would have attended a French language school in Quebecregardless of whether the law was in place. I therefore use a triple differences estimation relyingon three sources of variation: year of birth, parental birthplace, and mother tongue. UsingFrancophone immigrants as an additional control group allows me to difference out the effect ofunobserved factors that are invariant to mother tongue, but influence first- and second-generationimmigrant children differently across those with one foreign-born parent and those with twoforeign-born parents before and after the cut-off birth date. Furthermore, by employing thistriple differences strategy, I can evaluate the specific effects of the section of the law pertainingwere exempt from being mandated to study in French. In this way, the assumption for the classification approachis reasonable.152.3. Empirical Approachto language of instruction since other components of the law affected both the treatment andcomparison groups.The standard triple differences (DDD) framework in this context is as follows.24 Let Yi be theobserved outcome of individual i. Individuals are classified according to their parents’ place ofbirth, their mother tongue, and their date of birth. Let Gi ∈ {0, 1} denote parental origingroups, where Gi = 1 if the individual has two foreign-born parents and Gi = 0 if the individualhas only one foreign-born parent. Let Li ∈ {0, 1} denote mother tongue groups, where Li =1 for Allophones and Li = 0 for Francophones. Furthermore, individuals belong to one oftwo birth cohort groups, denoted by Ti ∈ {0, 1}, where Ti = 1 if the individual was bornas of October 1, 1971 and Ti = 0 if the individual was born prior to October 1, 1971. Eachindividual i can therefore be characterised by the following combination of observed variables:(Yi, Gi, Li, Ti). Following the treatment effect literature (Angrist and Krueger, 1999; Imbens andWooldridge, 2009), in this context, treatment assignment, denoted by Di ∈ {0, 1}, is defined asbeing mandated to study in French. Finally, let Y 0i denote the potential outcome for an individualwho does not receive the treatment and Y 1i denote the potential outcome for an individual whorecieves the treatment. Then, for each individual, either Y 0i is observed if the individual didnot receive treatment (Di = 0) or Y 1i is observed if the individual received treatment (Di = 1).As a simplification, at this point, I assume that all Allophone individuals with two foreign-bornparents born after October 1, 1971 received treatment whereas all other individuals did not,implying that Di = Gi × Li × Ti.25 I will relax this assumption later. The observed outcome Yiof an individual can be expressed as:Yi = Y0i (1−Di) +DiY1i = Y0i +Di(Y1i − Y0i ) where Di =1 if Gi × Li × Ti = 10 otherwise(2.1)In absence of treatment (i.e., in absence of being mandated to study in French), the potentialoutcome for individual i is modeled as the following:Y 0i = β0 + β1Gi + β2Li + β3Ti + β12GiLi + β13GiTi + β23LiTi + εi (2.2)In this framework, β1 corresponds to the parental group specific component, invariant across birthcohort and mother tongue groups, β2 corresponds to the mother tongue group specific component,invariant across parental group and birth cohort groups, and similarly, β3 represents the birthcohort group specific component, which is common to all parental and mother tongue groups of24See Meyer (1995), Angrist and Krueger (1999), and (Imbens and Wooldridge, 2009) for an overview of themethodology and other applications.25Although the rules of Bill 101 also applied to Francophones, for the purposes of the analysis, they are notclassified as receiving the treatment (being mandated to study in French) since they would have attended schoolin French regardless of the law being introduced. Francophones are thus only viewed as a control group.162.3. Empirical Approachindividuals. In this way, β12, β13, and β23, correspond to the second-level interactions betweenthese components. The term εi represents the unobserved characteristics of the individual,which are assumed to be independent of mother tongue, birth cohort, and parental groups, thatis εi ⊥ (Gi, Li, Ti) and is normalized to have mean zero. The goal is to estimate the effect ofbeing mandated to study in French on Allophones (i.e., the average effect of treatment on thetreatment group), which is given by:τ = E[Y 1i − Y0i |Di = 1]= E[Y 1i |Gi = 1, Ti = 1, Li = 1]−E[Y 0i |Gi = 1, Ti = 1, Li = 1](2.3)However, the last term, E[Y 0i |Gi = 1, Ti = 1, Li = 1], is unobserved since it is a measure of theaverage outcomes of Allophones in the treatment group had they not been treated. I thereforeestimate τ using the the standard difference-in-difference-in-differences estimator τDDD definedas follows:τDDD ={(E [Yi|Gi = 1, Ti = 1, Li = 1]− E [Yi|Gi = 1, Ti = 0, Li = 1])−(E [Yi|Gi = 0, Ti = 1, Li = 1]− E [Yi|Gi = 0, Ti = 0, Li = 1])}(2.4)−{(E [Yi|Gi = 1, Ti = 1, Li = 0]− E [Yi|Gi = 1, Ti = 0, Li = 0])−(E [Yi|Gi = 0, Ti = 1, Li = 0]− E [Yi|Gi = 0, Ti = 0, Li = 0])}In this setup, to identify the effect of treatment using the DDD estimator (i.e., for τ = τDDD), onekey assumption (known as the Unconfoundness Assumption) must hold: assignment to treatmentmust be unrelated to unobservable characteristics, that is: Di⊥(Y oi , Y1i ) | Gi, Li, Ti.26 In otherwords, being subject to treatment does not depend on potential outcomes after controlling forthe variation in outcomes induced by differences in observable characteristics.27 Under thisassumption and assuming that E(Y 1i −Y0i |Gi, Li, Ti) is constant, I obtain the following standardtriple differences regression model by combining equations 2.1 and 2.2:Yi = β0 + β1Gi + β2Li + β3Ti + β12GiLi + β13GiTi + β23LiTi + τDDDGiLiTi + εi (2.5)The coefficient of interest is τDDD, the coefficient on the triple interaction term GiLiTi, whichcaptures the variation in outcomes specific to those with two foreign-born parents (relative tothose with one foreign-born parent) among Allophones (relative to Francophones) and among26This assumption is often referred to as the Unconfoundness Assumption or the Conditional IndependenceAssumption. More generally, this assumption can be extended to Di⊥Y oi |Gi, Li, Ti, Xi if we add other observablecharacteristics Xi to equation 2.2.27This implies the following, which is often referred to as the “Common Trends” assumption:{(E[Y 0i |Gi = 1, Ti = 1, Li = 1]− E[Y 0i |Gi = 1, Ti = 0, Li = 1])− (E[Y 0i |Gi = 0, Ti = 1, Li = 1]− E[Y 0i |Gi = 0, Ti = 0, Li = 1])}={(E[Y 0i |Gi = 1, Ti = 1, Li = 0]− E[Y 0i |Gi = 1, Ti = 0, Li = 0])− (E[Y 0i |Gi = 0, Ti = 1, Li = 0]− E[Y 0i |Gi = 0, Ti = 0, Li = 0])}It is then straightfoward to show that the average treatment effect on the treated is equal to the triple differencesestimator (i.e., τ = τDDD).172.3. Empirical Approachpost-1971 birth cohorts (relative to pre-1971 birth cohorts). In this simple framework, theOrdinary Least Squares (OLS) estimator τˆDDD is in fact identical to the sample analog of thepopulation means in equation 2.4.For additional precision, I extend this standard model to include multiple birth cohorts (instead oftwo groups of individuals born either before or after October 1, 1971) as well as other covariates tocontrol for additional observable characteristics. These control variables are included even if theintroduction of Bill 101 is independent of these covariates, as they may improve the precision ofthe estimates if there were some compositional changes in these dimensions present across certainspecific groups. For the triple differences identification strategy to hold, one must thereforeassume that the difference in birth cohort trends in the outcome variables between Allophonesand Francophone across those with two foreign-born parents and those with one foreign-bornparents would have been the same over time (i.e., fixed group differences) in absence of thelaw being implemented. Figures 2.2 to 2.5 provide some evidence that this “Common Trends”assumption seems to hold by comparing pre-Bill 101 group specific birth cohort trends (seediscussion in section 2.4.1). Therefore, in order to identify the effect of mandating Allophonechildren to study in French, through Bill 101, on various outcomes of interest measured in 2006,the main triple differences estimation equation (using a more context-specific notation) is thefollowing:Yi = β0 + γBill 101i + βlAllophonei + βgTwoforeignparentsi +1981∑t=1963βtyobt,i+1981∑t=1963βltyobt,i ×Allophonei +1981∑t=1963βgtyobt,i × Twoforeignparentsi+ βlgAllophonei × Twoforeignparentsi +Xiα+ εi(2.6)where Bill 101i = bornpost1971i ×Allophonei × TwoforeignparentsiIn this equation, Yi is the outcome of interest of person i. The various outcomes examined aremeasured in 2006 and include language use, labour market outcomes, post-secondary educationcompletion, and residential location. The variable Twoforeignparents refers to whether bothparents were born outside of Canada (Twoforeignparents = 1) or only one parent was bornoutside of Canada (Twoforeignparents = 0). The variable Allophone refers to whether thechild’s mother tongue was a language other than French or English (Allophone = 1) or French(Allophone = 0). The variable yobt refers to year of birth t cohort fixed effects, whereas thebinary variable bornpost1971 indicates whether an individual was born after October 1, 1971.The main parameter of interest is γ, the coefficient on the binary variable Bill 101. The latter isequal to 1 for individuals who were likely to be mandated to study in French as a result of this law:Allophone individuals born after October 1, 1971 with both parents born outside of Canada. Asmentionned earlier, the model presented in equation 2.6 is rich enough to control for unobserved182.3. Empirical Approachcohort fixed effects, parent group (one or two foreign-born parents), and mother tongue group(Francophone or Allophone) fixed effects as well as all possible two-way interactions betweenthese three dimensions. The estimation equation also comprises individual control variablesXi, which include dummy variables for gender, ethnic groups, and for being a first-generationimmigrant.28In practice, this model (equation 2.6) constitutes a linear probability model or an OLS model,depending on whether the outcome of interest is a binary variable or a continuous variable.Standard errors are clustered at the year of birth level to account for their potential correlationwithin birth cohorts. All regressions are weighted using Census weights. In addition, throughoutmy analysis, the variable “year of birth” used to identify birth cohorts is calculated based on theacademic enrolment cut-off of October 1st each year.29 Another valid approach to measure theeffect of Bill 101 on Allophones would be to exploit the October 1, 1971 cut-off in a regressiondiscontinuity (RD) design based on the date of birth of the individual. Due to the limited samplesize of Allophone immigrants born near this date of birth cut-off, however, the triple differencesstrategy is more appropriate in this case.30By employing this triple differences estimation strategy, I am able to address various sourcesof concern when attempting to measure the impact of mandatory schooling in French. First, itallows me to identify specifically the impact of the section of Bill 101 on language of instruc-tion. Although Bill 101 also included other policies to protect the French language in Quebec,these policies affected all individuals in the sample (both in the control and treatment groups),and their effects would therefore not be picked up by the triple differences estimator, whichrelies on differences across birth cohorts. Furthermore, suppose the introduction of the law hadother indirect consequences on the labour market, such as causing some businesses to leave theprovince after its introduction, an increase in the returns to French language skills over time, ora decrease in the returns to English language skills. By using control groups in the estimationstrategy, whose members were also subject to these indirect consequences, the estimated impactsof mandatory schooling in French remain unbiased.28Specifically, I control for the most common ethnic groups in the sample: French, other European (Italian,Greek and Portuguese), Haitian, Chinese, Vietnamese, North African, and mixed (individuals belonging to morethan on ethnic group). The omitted category includes all other ethnic origins.29In Quebec, children must be 5 years old on October 1stof a certain year to be allowed to begin kindergarten inSeptember of that year (Ministère de l’éducation, règlement numéro 1, 1965). Because Bill 101 allowed childrenwho had already commenced school before September 1977 to continue studying in English regardless of theirparents’ language of instruction, the October 1st year of birth cut-off is the relevant cut-off (as opposed to theusual January 1st calendar year cut-off) to identify birth cohorts likely to be subject to or exempt from the law.In this paper the term “year of birth” therefore runs from October 1st to September 30thof the following year. Forexample, a child born in on September 15, 1971 would have been 5 years old on October 1, 1976 and thereforestarted school in 1976. The would be classified as part of the 1971 “year of birth” cohort. In contrast, a childborn on October 15, 1971 would only be 4 years old on October 1, 1976 and would therefore be forced to startschool a year later (at age 6). His or her “year of birth” cohort would be 1972.30Because of the grandfathering clause exempting the younger siblings of children enrolled in an English languageschool in 1977 from Bill 101, one would have to use a fuzzy RD design, which usually requires an even largersample size than a sharp RD design to obtain precise estimates.192.4. Empirical ResultsUntil this point, I have assumed that Bill 101 was binding for everyone targeted by the law,implying that all Allophones with two foreign-born parents born after October 1, 1971 completedtheir schooling in French due to Bill 101 (i.e., all of them were “treated”). I will now relax thisassumption to account for the portion of Allophones in this group who were allowed to studyin English due to the grandfathering clause of Bill 101. Under this clause, younger siblings ofchildren already enrolled in an English language school in 1977 were exempt from having toattend a French language school regardless of when they themselves commenced school. Thisparticular rule implies that the impact of the law, obtained from estimating the triple differencesmodel (equation 2.6), is not uniform across birth cohorts; rather, it increases as cohorts’ year ofbirth increase. One can therefore interpret the triple differences estimator, γ, as the “intent-to-treat” (ITT) estimator as opposed to the average treatment effect on the treated (ATT) estimator(see section 2.4.6 for details on obtaining the ATT).2.3.3 Summary StatisticsTable 2.3 presents the summary statistics measured using the 2006 Census for the main sampleof my analysis (Sample 1). For comparison purposes, panels A and B provide summary statisticson Allophone and Francophone immigrants respectively. In both panels, individuals are classifiedinto four groups based on their parents’ place of birth and whether they were born prior to orafter October 1, 1971. The characteristics of the group subject to Bill 101 are presented in thethird column of panel A.First-generation immigrants account for less than 25% of Sample 1, which is a relatively smallnumber because these individuals had to have arrived to Canada prior to age 6 to be includedin the sample. There are some ethnic group composition differences between the various groupsin the analysis. For example, although Allophones subject to or exempt from Bill 101 arepredominantly from a White heritage, there is a larger proportion of Asians among those subjectto the law. In addition, among Francophones with two foreign-born parents, the proportionof Black immigrants is 41% for post-Bill 101 individuals compared to only 8.5% for pre-Bill101 individuals. To account for these differences, I control for ethnic group, gender and first-generation immigrant status in all of the regressions.2.4 Empirical ResultsSections 2.4.1 to 2.4.3 describe the main results of the analysis (the intent-to-treat (ITT) effects),based on the 2006 Census, evaluating the effect of mandatory schooling in French for Allophoneindividuals on various outcomes measured in 2005 or 2006. I present some robustness regressionsand falsification tests in section 2.4.4 followed by some evidence on the evolution of the effectsover time based on the 2011 National Household Survey (section 2.4.5). I then recover the average202.4. Empirical Resultstreatment effects on the treated (ATT) in section 2.4.6. Finally, section 2.4.7 presents the resultsof a bounding exercise to address the potential selection bias problem due to the introduction ofBill 101 increasing interprovincial outmigration.2.4.1 Language UseFirst, I examine the effect of mandatory schooling in French for Allophone children on adulthoodpatterns of language use at home and at the workplace. This initial step has two purposes. First,it evaluates the impact of Bill 101 in terms of its primary aim, which was to ensure that newimmigrants to Quebec learned and used French. More than 95% of people in the sample reportedknowing French when asked about their knowledge of Canadian official languages, regardless ofwhether they were Allophone or Francophone.31 The Census does not require people to reporttheir level of language proficiency, so the answer to this question is quite subjective. Therefore,in my empirical analysis, I rely on measures of language use such as what language is frequentlyspoken at home or used at work (see Table B.1 in Appendix B for details). These measures arelikely to be highly correlated with language proficiency since individuals with higher skills in alanguage are more likely to use that language in various contexts. Second, this step providesevidence that the empirical strategy accurately identifies which individuals were likely to besubject to the law. If it were the case that I found no effect on whether Allophones affectedby Bill 101 used French at home and at work, then it would be difficult to argue that theidentification strategy upon which my analysis is based is correct. On the contrary, I find verylarge effects of the law on French language use among this group.Figure 2.2 presents the birth cohort trends in the proportion of first- and second-generationimmigrants who spoke French at home in 2006 among several groups of individuals in Sample1.32 As expected, nearly all Francophone immigrants spoke French regularly at home, regardlessof their birth cohort or whether they have one or two parents born outside of Canada. AmongAllophones, only those born after 1971 and with two foreign-born parents were likely to besubject to Bill 101. It is clear from Figure 2.2 that these individuals experienced an increasein their propensity to speak French at home, whereas those with one parent born in Canada,and therefore exempt for the law, saw a decrease in this measure. The marked decrease after1977 in French language use among Allophones with one foreign-born parent can be explained inpart by an increase in the proportion of these individuals still living at home with their parents.Compared to Allophones with two foreign-born parents, younger cohorts of Allophones with oneforeign-born parent are more likely to live with their parents (who probably have limited French31The Census enquires about whether individuals are able to conduct a conversation in an official language.Choices include French, English, both French and English or neither language.32To provide a more complete picture, the figures are based on an extended version of Sample 1, which includesindividuals born between 1960 and 1983 inclusively. The main regression results are based on the narrower1962-1981 birth cohort sample.212.4. Empirical Resultsskills), thereby explaining why they are less likely to speak French at home.33 Figure 2.3 presentsthe analogue to Figure 2.2 for the use of English at home. The opposite pattern is observed. Inthe case of Allophones, the proportion of those who spoke English at home significantly decreasedfor those born after 1971 with two foreign-born parents (subject to Bill 101), whereas it remainedrelatively constant over the years for those with one Canadian-born parent (exempt from Bill101). These findings suggest that the “Bill 101 generation” of Allophones, in contrast to earliergenerations, are much more inclined to use French and less inclined to use English at home.The regression analysis results confirm the home language use patterns observed in Figures 2.2and 2.3. Panel A of Table 2.4 presents the estimation results of the triple differences approach(equation 2.6) for speaking French at home (columns 1, 2, 3) and for speaking English at home(columns 4, 5, 6) for each of the three samples. The table displays the coefficient on the keyvariable, Bill 101, as well as on certain other variables of interest. For both home languageusage measures, the results are consistent across all three samples. Being mandated to studyin French due to Bill 101 led to an increase of 18 to 21 percentage points in the probabilityof speaking French at home and a decrease of 26 to 28 percentage points in the probability ofspeaking English at home.34 It is important to note that speaking French or English at home arenot mutually exclusive outcomes. As a consequence, the effect of Bill 101 on speaking French athome is not the inverse of its effect on speaking English at home, as some individuals use bothlanguages at home.When examining language use in the workplace, Bill 101 also seems to have had a large positiveimpact on the use of French at work and a large negative impact on the use of English atwork. Figures 2.4 and 2.5 show that the pattern for language use at work is similar to thatfor language use at home. Although they are somewhat noisier due to the smaller sample sizeresulting from considering only individuals in the workforce, these figures clearly suggest thatAllophones targeted by the law (i.e., those born after October 1, 1971 with two foreign-bornparents) were more likely to use French and less likely to use English at work than their peersexempt from the law. The regression results for language use at work, presented in panel B ofTable 2.4, are consistent with the figures. Bill 101 increased the probability of speaking Frenchat work by 18 to 20 percentage points and, conversely, decreased the probability of speakingEnglish in the workplace by approximately 15 to 16 percentage points. The results are similar33Figure B.1 in Appendix B presents the same trends as Figure 2.2 on the restricted sample of individuals whowere not living with their parents. The sharp decrease in the propensity of Allophones with only one foreign-bornparent to speak French at home after 1977 is no longer present. In addition, when estimating the baseline model(equation 2.6) on this restricted sample, the effects of Bill 101 remain the same.34In an extended empirical analysis of the effects of Bill 101 (the results of which are not included in the paper),I found no significant effects of Bill 101 on Allophones’ propensity to marry or become common-law partners withFrancophones. This result suggests that Allophones being more likely to speak French at home at adulthoodis not simply a consequence of them marrying Francophones, but rather it is likely a result of two Allophonepartners within a household being more inclined to speak French together at home. I did not include the resultsof this additional analysis in the paper because some individuals in the sample may still be too young (in their20s and early 30s) to have chosen a lifetime partner, thus possibly affecting the validity of the estimates.222.4. Empirical Resultsin magnitude and statistically significant across all three samples. The results of Table 2.4 alsoconfirm that as a general rule, compared to Francophones, Allophones are significantly less likelyto use French and more likely to use English both at home and at work than Francophones.In addition, on average, immigrants with two foreign-born parents compared to those with oneforeign-born parent are also more likely to choose English over French regardless of their mothertongue. These patterns are consistent with expectations.Based on this analysis, it is clear that Bill 101 had a significant impact on Allophones’ choice oflanguage at home and at work. Less than 40% of Allophones born after 1971 and exempt fromthe law (those with one foreign-born parent) used French at home and close to half of them usedFrench at work. In comparison, the effects of being mandated to study in French on language useamong those subject to Bill 101 – an increase of approximately 20 percentage points in Frenchusage both at home and in the workplace – are therefore quite large. The law mandated these“children of Bill 101” to complete their elementary and secondary education in French, therebypresumably greatly improving their French language skills compared to their peers who attendedschool in English. This was likely to have resulted in increased use of French both at homeand in the workplace, as well as decreased use of English. Although English language schoolsoffered French-as-a-second-language courses, being immersed in an entirely French environmentis more likely to result in better language proficiency (Cummins, 1998; Genesee, 2012). Thesefirst results pertaining to language use provide some confidence that the estimation strategy isidentifying the correct groups of individuals targeted by or exempt from the law.In addition, Figures 2.2 to 2.5 provide some visual evidence on the validation of the identificationassumption, as trends in language use appear to be approximately parallel for cohorts born priorto 1972, the birth year of the first cohort of Allophone children with two foreign-born parentsexposed to the law. As of this cut-off year, the trends begin to diverge. In none of the fourfigures is there a clear jump at the cut-off year of birth. This can be explained by the factthat some children who were part of school cohorts targeted by the law were exempt from itbecause they had an older sibling enrolled in an English language school prior to the law beingintroduced. The use of this exemption rule is likely to be less common in cohorts for later birthyears, thus explaining the constant increase in French language use over birth cohorts following1971. Finally, the figures present the same pattern when based on Samples 2 or 3 instead ofSample 1 (which, in the interest of brevity, are not shown here).2.4.2 Education and Labour Market OutcomesWhen Bill 101 was first introduced, many parents of Allophone children subject to the lawwere concerned that they would not be able to help their children with school assignments orexam preparations if they themselves did not have the French skills required to do so. They wereconcerned that, as a result, their children would suffer academically in the long term. To examine232.4. Empirical Resultsthe impact of Bill 101 on Allophones’ educational attainment, Table 2.5 presents the effects ofthe law on completing a post-secondary education degree across the three samples.35 Althoughthe overall effects are positive but not significant, there is evidence of a differential impact ofBill 101 on post-secondary educational attainment for men and women. Whereas females werebetween 4 to 7 percentage points more likely to complete a post-secondary degree, the effectsare significantly smaller and statistically insignificant for males. The positive effects for femalesare larger and only significant for samples 1 and 2, suggesting that first-generation immigrantsmay be driving the results. One explanation for this gender difference may be that boys do notperform as well when immersed in a second language at school (Baker and MacIntyre, 2000).With respect to labour market outcomes, the introduction of Bill 101 had some positive effects interms of labour force participation and employment (Table 2.6). Among those living in Quebecin 2006, Table 2.6 presents the estimates of the impact of Bill 101 on the probability of beingunemployed and not attending school (panel A), being part of the labour force (panel B), beingunemployed among those in the labour force (panel C), and working in the public sector (panel D).Columns 1 to 3 show the overall effects of Bill 101 for each of the three samples. Being mandatedto study in French as a result of Bill 101 is associated with a 6 to 7 percentage point decreasein the probability of being unemployed and not attending school; although when restrictingthe sample to those in the labour force, the effect on unemployment is smaller (3.5 percentagepoints) and only significant for second-generation immigrants. Because the sample contains someindividuals between the ages of 25 and 45, a substantial portion of individuals in the sample werestill in school and may not yet have entered the labour force. In fact, approximately 25% of thesample attended school (full-time or part-time) in the year preceding the Census survey. Forthis reason, the effects of the law on being both unemployed and not in school (Panel A) may bemore reliable than those on the traditional unemployment measure (panel C). In addition, thelaw caused a striking 7.5 to 9 percentage point increase in Allophones’ probability of being inthe labour force. Generally, being proficient in the language of the majority is likely to increasethe number and quality of employment opportunities offered to immigrants (Bleakley and Chin,2004), which may be driving these results. Recent evidence suggests that French language skillsare positively related to immigrants’ success in Quebec’s labour market (Nadeau, 2010; Grenierand Nadeau, 2011). Finally, among second-generation immigrants, the law was associated witha 5.6 percentage point increase in the probability of working in the public sector, although thiseffect is not significant when including first-generation immigrants. Most of the public sectoremployment opportunities require excellent knowledge of French, which may be why the law hadan impact on this dimension.Using the mean in the outcome variables of post-1971 cohorts of Allophones with one foreign-35I did not measure the impact of Bill 101 on Allophone immigrants’ field of study since the Census only providesinformation on the field of study of a person’s highest completed post-secondary degree. Due to missing values,the analysis would therefore have to be performed on a sample excluding all individuals without a post-secondarydegree, which could lead to an issue of sample selection bias.242.4. Empirical Resultsborn parent as a benchmark (they are arguably the most comparable group to those subjectto Bill 101), these effects are substantial: a 48% to 60% decrease in the probability of beingunemployed and not in school and a 9% to 11% increase in labour force participation dependingon the sample of analysis. In addition, among second-generation Allophones (Sample 3) in thelabour force, Bill 101 led to a striking 87% decrease in their probability of being unemployed andincreased their probability of working in the public sector by more than two-fold.Because the effects of Bill 101 on post-secondary educational attainment vary by gender, I alsoexplore the impact of the law on employment outcomes by gender (Table 2.6, columns 4 to 6).The much stronger effects of Bill 101 for women on post-secondary educational attainment donot seem to translate to the various employment measures examined. Both men and womenexperience similar effects of Bill 101 in terms of the probability of being unemployed and notenrolled in school, being part of the labour force, and working in the public sector.Next, to evaluate the labour market effects of Bill 101 on the intensive margin, Table 2.7 displaysthe estimated effects of the law on income among positive income earners. Panel A presents theresults of the estimation for income from gross wages and salaries earned in 2005 before incometax, employment insurance and pension deductions. Panel B presents the results for total incomereceived in 2005 including wages and salaries, self-employment income, government benefits,retirement pensions as well as investment income.36 Although positive, the point estimates ofthe overall effects of Bill 101 on the income measures examined (columns 1 to 3) are not estimatedprecisely enough to distinguish them from zero. However, columns 4 to 6 show that the effectsof Bill 101 on total income seem to be significantly higher for women compared to men, whichmay be caused in part by women’s higher educational attainment among Allophones subject tothe law.37To explore further whether the law had heterogeneous effects on income across individuals withdifferent income levels, I estimate an unconditional quantile triple differences (QDDD) model.This approach, based on an estimation technique developed by Firpo, Fortin and Lemieux (2009),evaluates the effect of the law on the entire unconditional (marginal) income distribution ofAllophones targeted by the law in Quebec. More specifically, the approach uses the pre- andpost-Bill 101 income distributions of the control groups to estimate what would have been the“counterfactual” income distribution of Allophones in the treatment group in absence of the lawbeing implemented. The entire procedure, which involves running a regression of the recenteredinfluence function (RIF) of the unconditional quantile of the outcome variable on the explanatory36These income measures are generally reliable and precise. The great majority (82.4%) of 2006 Census respon-dents granted permission to Statistics Canada to retrieve income information directly from their tax records asopposed to self-reporting their income (Statistics Canada, 2006).37I also estimated the effects of Bill 101 on the entire sample (including individuals with no income) and usingthe inverse hyperbolic sine transformation for log income measures (Burbidge, Magee and Robb, 1988). Theoverall results remained unchanged. The differential effects on income from wages by gender are, however, nolonger significant when including individuals with zero earnings in the analysis.252.4. Empirical Resultsvariables, is bootstrapped to obtain consistent standard errors. It is then possible to estimatewhether the impact of the law was constant across Allophones targeted by Bill 101 or whetherit varied depending on individuals’ level of income. Figures 2.6 and 2.7 present the results ofthe estimation across income quantiles for log income from wages and for log total income for allthree samples. The continuous line represents the estimated unconditional quantile treatmenteffects over the distribution whereas the dashed lines trace the 95% confidence intervals. Thefigures show that there does not seem to be much heterogeneity of the effects of Bill 101 acrossincome quantiles. Although the effects are generally positive, they are mostly insignificant acrossthe entire wage income and total income distributions.Over the past few decades, the average labour market performance of first-generation immigrantsin Quebec has been deteriorating over time relative to Quebec-born individuals. In Quebec, boththe earnings gap and the employment gap between first-generation immigrants and the rest ofthe active population have increased in recent years, and moreover, at a faster rate than the gappresent in the rest of Canada (Boudarbat and Boulet, 2010; Nadeau and Seckin, 2010).38 Forexample, in 2006, the unemployment gap between first-generation immigrants and native-bornindividuals in Quebec was considerably larger (6 percentage points) than the Canadian averagegap (1.4 percentage points).39 It is important to underline, however, that immigrants whoarrived to Quebec at an adult age are driving this pattern. The gap disappears when restrictingfirst-generation immigrants to those who arrived as children to Quebec (Boudarbat and Boulet,2010). Based on the estimated effects of Bill 101 on labour market outcomes, one contributingfactor to the better performance of immigrants who arrived at an early age could be the strongerFrench language skills of the members of this group who more than likely completed all of theirschooling in French in Quebec due to Bill 101, compared to non-French speaking immigrantswho immigrated to Quebec as adults. First-generation immigrants in Quebec who are fluentin French are significantly more likely to work full-time than those with limited or no Frenchlanguage skills (Grenier and Nadeau, 2011). Among newly arrived first-generation immigrants inQuebec in 2008, however, approximately 80% of them immigrated after the age of 15 and nearly40% did not know any French (Boudarbat and Boulet, 2010).2.4.3 Regional Choice of Residential LocationIndividuals choose their residential location by weighing the costs and benefits of various locationoptions. In the case of immigrants, limited majority language skills can significantly increase thecosts of choosing to reside in regions where that language heavily dominates. As such, learning38Generally, in Canada, second-generation immigrants perform in the labour market as well as third-or-highergeneration Canadian residents (Picot and Hou, 2011).39In 2006, the unemployment rate of first-generation immigrants in Quebec was 11.2% compared to 5.2% forQuebec-born individuals. In comparison, for Canada as a whole, the unemployment rate of first-generationimmigrants was 6.5% compared to 5.1% for the rest of the population (Boudarbat and Boulet, 2010).262.4. Empirical Resultsthe language of the majority may therefore increase immigrants’ internal mobility. Previousresearch has shown that the linguistic abilities of immigrants strongly influence their locationdecisions within their host country. Generally, immigrants with limited majority language skillstend to reside in areas with a high concentration of immigrants of similar ethnicity and language(Lazear, 1999; Bauer, Epstein and Gang, 2005). In the context of internal migration explainedby a Search and Matching model, a policy aimed at lowering the relocation costs of workers couldincrease the efficiency of employer-employee matches in the labour market by reducing frictions.In this way, such a policy could help improve the efficiency of the interregional allocation ofhuman capital (Kennan and Walker, 2011; Molloy, Smith and Wozniak, 2011; Beaudry, Greenand Sand, 2014; Buchinsky, Gotlibovski and Lifshitz, 2014). I therefore examine next whethermandatory schooling in French had an impact on the regional choice of residential location ofAllophones in Quebec once they reach adulthood, as well as what possible channels may explainthis effect.Similar to other major cities in Canada such as Vancouver and Toronto which attract a largenumber of immigrants, the majority of immigrants who choose to reside in Quebec live in itslargest metropolitan area: Montreal. In 2006, 86.9% of first-generation immigrants in Quebeclived in Montreal (Government of Quebec, 2011). Different reasons may explain this pattern.Many new immigrants choose their destination location within Canada based on partners, family,and friends already living in that location, resulting in an agglomeration of immigrants generallyin larger urban areas (Grenier, 2008). Another factor could be that job prospects are perceivedto be better in larger cities. In Quebec, according to a study performed using the LongitudinalSurvey of Immigrants, the second most common reason for choosing to settle in Montreal, afterhaving family or friends that already live there, is language (Chui, 2003). Although Montreal is afairly bilingual city in French and English, French strongly dominates in the rest of the province.For Allophone immigrants who have no knowledge or a limited knowledge of French, settling inMontreal may be easier, especially initially.If Allophone immigrants acquire strong French language skills as children, however, then thisis likely to lower their cost of moving to another region of the province later in life, therebyincreasing their likeliness of living outside Montreal.40 Table 2.8 presents the estimated effectsof Bill 101 on the probability of living in Montreal among the entire population (columns 1 to 3)and among non-students (columns 4 to 6). The results suggest that Allophones targeted by Bill101 are significantly less likely to reside in Montreal, especially when they are no longer students.This probably follows from the fact that post-secondary education students are more likely tolive in Montreal, which offers the largest variety of post-secondary educational institutions in theprovince. The law is associated with a 5.8 to 8.7 percentage points decrease in the probability40I focus mainly on the impact of Bill 101 on Allophones’ propensity to live in Montreal versus other regionswithin Quebec. Due to sample size limitations, I am unable to study the effects of the law on Allophones’ choiceto reside in ethnic enclaves within the Montreal region.272.4. Empirical Resultsof living in Montreal among non-student Allophone immigrants. Using Allophones with oneforeign-born parent as a comparison group, these effects correspond to an approximate 6.7% to9.2% decrease in the propensity of non-student Allophones to live in Montreal.Various channels could explain why Allophone immigrants mandated to study in French due toBill 101 are more likely to choose to live outside of Montreal once they reach adulthood. To gainadditional insight on these possible channels, I examine how Bill 101 differentially affected thelabour market outcomes of those who chose to live in regions other than the Montreal metropoli-tan region compared to those who did not. Although the estimates cannot be interpreted as truecausal effects because the decision to move outside of Montreal is affected by the introductionof Bill 101 and therefore endogenous, the patterns observed are nevertheless very informative.Table 2.9 presents the results of estimating equation 2.6 on labour market outcomes when addingan additional interaction term between the Bill 101 treatment variable and living in Montreal.41The estimates suggest that Allophones targeted by the law were approximately 10 percentagepoints more likely to work in the public sector when residing outside of the Montreal region,while these effects were negligible for Montreal residents. In addition, Allophones likely subjectto Bill 101 residing outside of Montreal generally benefited from a much higher total income:between 35 and 40 percent higher on average than those who were not subject to Bill 101. Theeffect of Bill 101 on total income is half the size and insignificant for those who chose to live inthe Montreal region. I find no significant differential effects of the law by residential location onemployment and labour force participation.These results are consistent with the explanation that obtaining strong French language skillsdue to Bill 101 reduced the cost of moving outside of Montreal and opened the door for Allo-phones to seek higher paying employment outside of Montreal, particularly in the public sector.42Whereas it is possible to work solely in English in certain institutions in Quebec such as in En-glish language education institutions or small businesses, working in the provincial public sectorrequires high levels of proficiency in the French language. It is also advantageous to be fluentin French for several positions in the federal public sector (Coleman, 1981; Vaillancourt, Lemayand Vaillancourt, 2007; Nadeau, 2010). If the law resulted in higher French language skills, thismay explain why Allophone immigrants who were likely to be subject to the law are more likelyto obtain a public sector job compared to those who were not subject to it. In Quebec, approx-imately 20% of workers are part of the public sector. Of this group, two-thirds are employedby the provincial or federal public sector (Palacios and Clemens, 2013), with offices generallylocated outside of the Montreal region (the provincial capital is located in Quebec City). Being41I also include a binary indicator for living in Montreal as an additional control variable in the estimationequation.42One could be concerned about general equilibrium effects resulting from the inflow of Allophones due to Bill101 into regions who generally do not attract many immigrant workers. This is not a major concern here since theproportion of Allophones in regions outside of Montreal, although affected by Bill 101, remains relatively smallcompared to Francophones.282.4. Empirical Resultssubject to Bill 101 increased Allophones’ propensity to live in Quebec City, where the majorityof provincial public sector jobs are located, by approximately 3 to 5 percentage points (TableB.2 in Appendix B), which validates this possible explanation further.43 Furthermore, as is alsothe case in Canada, Quebec public sector workers benefit from higher compensation and betterbenefits than private sector workers (Gunderson, Hyatt and Riddell, 2000; Palacios and Clemens,2013).To further verify the plausibility of this explanation channel for the differential labour marketeffects across Montreal and non-Montreal residents, I re-estimate the effects of Bill 101 amongindividuals in the labour force by sector of work (Table B.3 in Appendix B). Several results areworth highlighting. First, the effects of Bill 101 on language use, unemployment, and residentiallocation still hold conditional on working in the private sector, which is the case for approximately95% of individuals in the sample. Second, compared to private sector workers, the effects ofBill 101 on language use at home are approximately twice as large for public sector workers. Inaddition, I find no significant impact of Bill 101 on language use in the workplace for public sectorworkers, which is consistent with French being the only language used in this setting. Third,although workers in both sectors are more likely to live outside of Montreal, the magnitudes of theeffects are considerably larger for public sector workers. Finally, the effects of Bill 101 on incomeare not significantly different between Montreal residents and non-Montreal residents within theprivate sector, but they remain much higher for public sector workers outside of Montreal thanthose residing in Montreal, which implies that public sector employment was driving the incomedifferences measured on the entire sample.44 These results therefore provide further support forthe hypothesis that one of the main reasons Allophones subject to Bill 101 are more likely tochoose to live outside of Montreal is the better public sector employment opportunities locatedoutside of Montreal, which require excellent French language skills.2.4.4 Robustness and Falsification TestsThe previous estimation results are highly robust to many robustness tests, including alterna-tive specifications and sample definitions, which are presented in Table 2.10. For comparisonpurposes, column 1 presents the main estimates obtained from estimating the triple differencesmodel (equation 2.6) on Sample 1. For brevity, all robustness regression results are presentedsolely using the principal analysis sample, Sample 1 (or its equivalent), which includes both43One concern could be that the results regarding Allophones’ propensity to live outside of Montreal are drivenby better economic and labour market prospects in other regions than Montreal, for instance Quebec City, whichas seen important economic growth in recent years (Government of Quebec, 2014b). If this were the case, however,all groups of immigrants in the analysis would be more inclined to leave Montreal to benefit from these betterlabour market opportunities. Consequently, by using comparison groups, the triple differences strategy shouldcontrol for this possible confounding factor.44The effects are larger in magnitude but not as significant as those estimated on the entire sample, probablydue to the much smaller sample size of public sector workers.292.4. Empirical Resultsfirst and second-generation immigrants. The results of these tests are, however, very similarwhen performed on Samples 2 and 3 (see Table B.4 in Appendix B for robustness and placeboregressions performed solely on second-generation immigrants (Sample 3)).First, I test whether the results for binary outcomes are sensitive to using a non-linear modelspecification. Column 2 presents the estimates of the marginal effects obtained using a Probitmodel, which are very similar to the linear probability models used for the baseline model (column1), both in terms of magnitude and significance of the effects estimated.45 Second, I test whetherthe results are robust to the choice of sample, by varying the length of the birth year windowaround the 1971 cut-off included in the sample. The baseline model (equation 2.6) is estimated onindividuals born within 10 years of the October 1, 1971 cut-off date (i.e., between 1962 and 1981).Columns 3 and 4 respectively present the results of estimating the baseline model specification(equation 2.6) on the extended sample of individuals born within 15 years of the cut-off date(between 1957 to 1986) and on the restricted sample of individuals born within 5 years of thecut-off date (between 1967 and 1976). In both cases, the estimated effects are very similar to theestimates of the baseline triple differences model presented in column 1, although, as expected,some estimates obtained based on the restricted sample (column 4) lose their significance due tothe smaller size of the sample used. In addition, the restricted sample coefficients are generallysmaller in magnitude than the extended sample estimates, which is consistent with the varyingproportion of individuals for which the law was binding across post 1971 cohorts (see section2.4.6 for further details).I also estimate two different simple difference-in-differences models as opposed to the baselinetriple differences model. First, column 5 presents the results of estimating the impact of Bill 101based solely on the subsample of Allophone and Francophone individuals with two foreign-bornparents. Equation 2.7 presents the corresponding two-way difference-in-difference model. In thisempirical approach, the Bill 101 variable is equal to one for Allophone individuals born afterOctober 1, 1971 and zero otherwise.Yi = β0 + γBill 101i + βlAllophonei +1981∑t=1963βtyobt,i +Xiα+ εi (2.7)where Bill 101i = bornpost1971i ×AllophoneiNext, I estimate the impact of Bill 101 based on solely on the subsample of first- and second-generation Allophone individuals. Francophones are therefore excluded from the sample. Equa-tion 2.8 presents the difference-in-difference model used in this case, where the Bill 101 variable45I chose to estimate a Linear Probability Model in the case of binary outcome variables as my main specification,as opposed to a Probit or Logit model, to maintain the linear framework of the difference-in-differences empiricalapproach (equation 2.4). In addition, fixed effects Probit estimators and their corresponding average marginaleffects are likely to be inconsistent, an issue often referred to as the incidental parameter problem (Neyman andScott, 1948; Lancaster, 2000). In this case, the Probit marginal effects are very similar to the LPM estimates,which mitigates this concern somewhat.302.4. Empirical Resultsis equal to 1 for individuals with two foreign-born parents born after October 1, 1971 and zerootherwise. Column 6 of Table 2.10 presents the results.Yi = β0 + γBill 101i + βlTwoforeignparentsi +1981∑t=1963βtyobt,i +Xiα+ εi (2.8)where Bill 101i = bornpost1971i × TwoforeignparentsiFor both models, the estimates obtained, shown in columns 5 and 6, fluctuate somewhat in mag-nitude but generally remain comparable in terms of sign and significance to estimates obtainedfrom the baseline model. The main triple differences model is more robust to unobserved diverg-ing trends over birth cohorts in outcome variables across mother tongue groups or parental origingroups. The fact that the estimates of both simple difference-in-differences (DD) approaches aresimilar to the triple differences (DDD) estimates is nevertheless reassuring, as this implies thatthe results obtained are mainly driven by changes in the outcomes of the treatment group (Al-lophones subject to Bill 101) as opposed to variations in the outcomes of either control group(Francophones or Allophones with one-foreign born parent). In this way, the similarities betweenthe DDD estimates and the DD estimates could be seen as the analog of an overidentificationtest in this context, the idea being to difference out an entire “control/placebo experiment” (theDD estimation based on Francophone immigrants only) from the “experiment of interest” (theDD estimation based on Allophone immigrants only).Finally, column 7 of Table 2.10 presents the results of a falsification test in which I estimatea difference-in-differences model on the sample of Allophone and Francophone individuals withtwo foreign-born parents born between 1952 and 1971, who had thus all started school prior toBill 101 being introduced.46 The estimation is thus similar to the one performed in equation2.7, but using a sample composed of earlier birth cohorts. For this falsification test, I choose1962 as the placebo cut-off date of birth in order to include in the regression individuals bornwithin 10 years of this cut-off as is the case in my main estimation. As expected, generally, noimpacts were found. One exception to this is the significant differential effect for the probabilityof obtaining a post-secondary degree across men and women. This implies that there may havebeen a pre-existing differential trend in the educational attainment of men and women specificto Allophones with two foreign-born parents, which could potentially bias the estimates. Thislimitation should be kept in mind. When adding control variables for educational attainmentin the baseline model, however, all of the results presented earlier still hold. This suggests thatthe possible presence of pre-existing trends in educational attainment among Allophones is notdriving the other effects measured by the triple differences estimation.I also perform an alternative placebo test by estimating the baseline model (equation 2.6) on46For this placebo test, I chose to estimate a simple difference-in-differences model instead of a triple differencesmodel because very few Allophones had only one foreign-born parent among those born prior to 1962.312.4. Empirical Resultsthe analogous sample to sample 3, but basing the analysis on second-generation Anglophonesand Allophones living in the province of Ontario who were born between 1962 and 1981. Ionly include second-generation immigrants born in Ontario to avoid including individuals whomight have lived in Quebec before moving to Ontario. For this test, I use Anglophones as thecomparison group since English is the majority language in Ontario. Table B.5 in Appendix Bpresents the results. Once again, as expected, I find no significant effects of the placebo policyvariable, except for a negative effect on post-secondary educational attainment, which seems tobe driven by men.2.4.5 Effects measured in 2011To explore the evolution over time of the effects of being mandated to study in French, I usethe 2011 National Household Survey (NHS) to supplement the 2006 Census results. In 2006,individuals in the main sample of analysis were between the ages of 25 and 45. In particular,those targeted by Bill 101 were between 25 and 34 years old inclusively. In 2011, they werebetween 30 and 39 years old, resulting in them being more likely to have finished school and bepart of the labour force. This older age bracket could thus improve the precision of the labourmarket estimates. Using a sample obtained by pooling the 2006 Census and the 2011 NHS, Ievaluate the differential impacts of Bill 101 in 2006 and in 2011.It is important to note, however, that the 2011 NHS is not a Census; it is a voluntary nationalsurvey that was administered in 2011 by Statistics Canada in lieu of the long-form of the Census.Because of the survey’s low response rate (68.6%) and its different sampling methodology than theCensus, the results may not be as reliable as the 2006 Census results. With this caveat in mind,it is nonetheless informative to examine the estimates obtained (Table 2.11) from estimating thefollowing pooled regression model:Yi = β0 + β1I {Y ear = 2011}+ γ1Bill 101i × I {Y ear = 2006}+ γ2Bill 101i × I {Y ear = 2011}+ βlAllophonei + βgTwoforeignparentsi +1981∑t=1963βtyobt,i +1981∑t=1963βtyobt,i × I {Y ear = 2011}+1981∑t=1963βltyobt,i ×Allophonei +1981∑t=1963βgtyobt,i × Twoforeignparentsi+ βlgAllophonei × Twoforeignparentsi +Xiα+ εi(2.9)In equation 2.9, Bill 101i = bornpost1971i×Allophonei×Twoforeignparentsi and the controlvariables Xi include gender, ethnic groups, first-generation immigrant status, and age. Theregression model also includes a binary variable I {Y ear = 2011}, which is equal to one foroutcomes measured in 2011 and zero otherwise. In this specification, year of birth fixed effects322.4. Empirical Resultsare time-specific (i.e., they are allowed to vary across 2006 and 2011) to control for the age ofthe individual within each cohort. The estimated effects of Bill 101 in 2011, captured by γ2, arevery similar to the 2006 effects, captured by γ1, both in magnitude and significance, suggestingpersistent effects of the law over time (Table 2.11). Because the results are consistent over timeand due to the higher reliability of the Census data, the next sections will focus solely on themain 2006 Census estimates.2.4.6 Recovering the Average Treatment Effect on the Treated (ATT)The main estimates presented in sections 2.4.1 to 2.4.3 can be viewed as the “intent-to-treat”(ITT) effects of the law on the ten birth cohorts following the introduction of the law. The intent-to-treat effects represent the full impact of the law on the main group of interest targeted byBill 101: Allophone children without a parent having studied in English in Canada, regardlessof whether some children in this group were exempt from the law due to the grandfatheringmeasure in place. The average treatment on the treated (ATT) estimate may be of greaterinterest to policy makers, as it provides an estimate of the impact of the law on those whoactually completed their schooling in French because of the law (i.e., the “treated”) among this“intent-to-treat” group. I use the 1981 Census to estimate the proportion of children who did nothave an older sibling already enrolled in school in 1977 by birth cohort (i.e., the proportion oftreated children) among this group. As expected, this proportion increases steadily over the yearsfrom 44% for those born in 1972 to 95% for those born in 1981 (Figure 2.8).47 This increasein the proportion of treated children with later birth cohorts explains why Figures 2.2 to 2.5depict a gradual increase in French language use and gradual decrease in English language usefor Allophones subject to the law (those born after 1971 with two foreign-born parents) insteadof a clear jump as of 1971.For each outcome of interest, to recover the ATT estimate of Bill 101, θˆ, I divide the main ITTestimate, γˆ, obtained in equation 2.6, by the overall proportion of treated individuals in the“intent-to-treat” group, which varies between 70% and 73% depending on the sample (equation2.10). This overall proportion is equal to the average of the proportion δt of children in eachbirth cohort t who did not have an older sibling already enrolled in school in 1977, weighted bythe proportion pt of individuals in the sample born in year t, for t ≥ 1972.θˆ =γˆ∑1981t=1972 ptδˆt(2.10)One advantage of examining the ITT instead of the ATT is that it captures spillover effects toother groups who were not targeted by the law due to, for example, peer effects. Peer effects47Figure 2.8 provides estimates of the proportion of treated children by year of birth in Sample 1. The estimatesfor Samples 2 and 3 are very similar.332.4. Empirical Resultscould occur if Allophone children mandated to study in French interacted with other Allophonechildren who were allowed to study in English, and this interaction affected the latter group’slong-term outcomes in some way. Recovering the ATT from the ITT using a scaling factorrelies on two assumptions. The first assumption is that the law was perfectly binding for allthose without an older sibling already enrolled in school in 1977 in the “intent-to-treat” group.This would imply that the all Allophone children in the group who did not have an older siblingalready enrolled in school when Bill 101 was passed attended school in French without exception.The law was strongly enforced, but there still may have been a few parents who found a wayto avoid sending their children to the French schooling system, for example, by sending theirchildren to unsubsidized private English schools. This is not, however, a major concern as only0.4% of exempt children between 1977 and 1989 did so by attending a non-subsidized Englishlanguage private school (Government of Quebec, 2014a). The second assumption is that allAllophone children exempt from having to study in French were in no way affected by the law.This assumption could be violated due to peer effects, as mentioned previously, or if, for example,parents of exempted children modified their behaviour and chose to send their children to schoolin French even if the law did not mandate them to do so. According to official statistics fromthe Ministry of Education of Quebec, 97% of exempted Allophone children were enrolled in anEnglish language school in the early 1980s and this proportion remains over 90% today. Thisvery high proportion suggests that most parents of children who were exempted from the lawdid not modify their behaviour once Bill 101 was introduced (Government of Quebec, 2014a).Assuming these two assumptions hold, then scaling the ITT effects by the inverse of the averageproportion treated in the group targeted by the law would provide a valid ATT estimate of Bill101.Table 2.12 presents ATT estimates calculated as shown in equation 2.10 as well as the previ-ous ITT estimates for comparison purposes. Being mandated to study in French among thosefor which Bill 101 was binding is associated with a 25 to 30 percentage point increase in thepropensity to use French at home and at work. Conversely, Allophones in this group are 36to 38 percentage points less likely to speak English at home and approximately 20 percentagepoints less likely to use English at their workplace. I also estimate that the effect of the lawon the probability of completing a post-secondary education degree among female Allophoneimmigrants who studied in French due to Bill 101 increased by 5 to 10 percentage points. Fur-thermore, the ATT estimates suggest that Allophone immigrants who were mandated to attendschool in French are less likely to be unemployed and not attending school by approximately8 to 10 percentage points, as well as being 10 to 13 percentage points more likely to be partof the labour force. Finally, the ATT effects of Bill 101 on the probability of living outside ofMontreal are estimated to be 4 to 8 percentage points among all Allophones and 8 to 12 percent-age points among non-student Allophones. If we compare these labour market and residentiallocation effects to the mean outcomes of Allophones with one foreign-born parent who were born342.4. Empirical Resultsafter 1971, which is arguably the most comparable group to those subject to Bill 101, these ATTestimates are quite large. They represent approximately a 75% decrease in the probability ofbeing unemployed and not in school, a 12% increase in labour force participation, and 4.5% to13% increase in their propensity to live outside of Montreal (depending on the sample used).An alternative approach to calculate the ATT estimates is to exploit the cohort specific pro-portion of treated children in the “intent-to-treat” group. This technique relies on calculatinga weighted average of the birth cohort specific Bill 101 ITT effects γt multiplied by their corre-sponding scaling factor given by the inverse of the proportion δt of children in each birth cohortt who were actually treated.Yi = β0 +1981∑t=1972γtBill 101i × yobt,i + βlAllophonei + βgTwoforeignparentsi+1981∑t=1963βtyobt,i +1981∑t=1963βltyobt,i ×Allophonei +1981∑t=1963βgtyobt,i × Twoforeignparentsi+ βlgAllophonei × Twoforeignparentsi + αXi + εi(2.11)θˆ =1981∑t=1972ptθˆt =1981∑t=1972ptγˆtδˆt(2.12)In equations 2.10 to 2.12, θˆ is the estimate of the average treatment effect on the treated (ATT)which is equal to the average of all cohort specific ATT estimators θˆt, for t ≥ 1972, weightedby pt, the proportion of individuals in the sample born in year t. Similarly, one can obtain anestimate of the ITT by averaging the cohort specific treatment effects γt without the scalingfactors δt. Table B.6 of Appendix B presents the estimates of the ITT and ATT effects obtainedin this way, which are generally comparable to the previous ones. A few of the estimates of theeffects of Bill 101, notably those on post-secondary educational attainment and log wage income,are however very different from those presented in Table 2.12, probably due to the cohort specificBill 101 estimated effects, γˆt , being much noisier and less precisely estimated than the overallaverage effect gamma γˆ used in the first approach (equation 2.10).2.4.7 Addressing the Potential Selection Bias ProblemOne limitation of the empirical strategy used for the analysis stems from the Census’ lack ofinformation on individuals’ migration patterns over their lifetime. The 2006 Census only providesinformation on individuals’ province of residence at the time of the Census (in 2006) and 5 yearsprior (in 2001). As a result, the sample of analysis includes individuals who were residents ofQuebec both in 2006 and in 2001, but may be missing some people who left the province before352.4. Empirical Results2001. According to interprovincial migration estimates by mother tongue groups, there doesseem to have been a marked exodus of people who left Quebec in the late 1970s during theperiod when Bill 101 was introduced (see Figure B.2 in Appendix B). To the extent that thedecision of movers to leave Quebec was independent of whether children were mandated to studyin French due to the introduction of Bill 101, this would not bias the estimates of the effectsof the law. It is, however, possible that the introduction of Bill 101 resulted in families withchildren affected by this law to be more likely to move out of the province, and that those wholeft were different than those who stayed. This would result in a selection problem due to theviolation of the Unconfoundness Assumption of the triple differences estimation. To address thisissue, I use the 1981 Census to measure, among all children of parents living in Quebec in 1976,the impact of Bill 101 on the probability of having left the province by 1981. Most families wholeft Quebec due to the law did so within four years after the law was introduced (see the end ofthis section for evidence that this is the case). I thus estimate the following selection equation:Mi = β0 + λBill 101i + βlAllophonei + βgTwoforeignparentsi +1981∑t=1963βtyobt,i+1981∑t=1963βltyobt,i ×Allophonei +1981∑t=1963βgtyobt,i × Twoforeignparentsi+ βlgAllophonei × Twoforeignparentsi +Xiα+ εi(2.13)In equation 2.13, Bill 101i = bornpost1971i ∗ Allophonei ∗ Twoforeignparentsi and Mi is abinary variable equal to one if a child whose parents were living in Quebec in 1976 was livingin another province than Quebec in 1981. This analysis provides an estimate of the severity ofthe selection problem due to interprovincial migration when the law was introduced. The resultsin panel A of Table 2.13 indicate that Allophone children who would have been subject to thelaw had they stayed in Quebec were 6 to 7 percentage points more likely to leave the provincethan other children. This is a very large effect considering that nearly 6% of Allophone childrensubject to the law left the province between 1976 and 1981. The results thus suggest that Bill101 explains most of the behaviour of children who left the province among this group.Next, to evaluate, among those who would have been subject to Bill 101, whether the childrenwho left by 1981 were observably different from those who remained, I estimate the differentialimpact of parents’ education, parents’ income and the child’s ethnic group on the probabilityof leaving Quebec among this group. By interacting the Bill 101 variable with various familyincome, parental education level and ethnic groups, I obtain the results presented in panelsB, C, and D of Table 2.13.48 They clearly indicate that children who left the province due48Parents’ education levels are defined as the highest educational attainment of both parents according tothe following categories: high school degree or less (omitted group), college degree or some university (level 2),university Bachelor degree (level 3), and university post-graduate degree (level 4). Parents’ income groups aredefined according to the four quartiles of the family income distribution.362.4. Empirical Resultsto Bill 101 generally had more highly educated and higher-earning parents. They were alsodisproportionately more likely to be from a Chinese background relative to those who stayed.Children with at least one parent who obtained a postgraduate degree (education level 4) were18 percentage points more likely to leave Quebec due to Bill 101 compared to 5 percentage pointsfor those with parents without a post-secondary degree (education level 1). Similarly, whereasAllophone children subject to Bill 101 in the bottom family income quartile were 5 percentagepoints more likely to leave, those in the top income quartile were 12 percentage points morelikely to move out of the province. These findings suggest that my main estimates of the impactsof Bill 101 are likely to be biased due to this selection problem. Families who left the provinceto avoid having to send their children to school in French were observably different from theaverage family mandated to enrol their children in a French language school who chose to remainin Quebec. One approach to address this problem would be to control for parents’ characteristicsin my main analysis. These variables are not present in the 2006 Census, making this impossible.In general, there is strong evidence that children of highly educated parents and high-incomefamilies tend to be highly educated and high-income earners themselves (Lee and Solon, 2009;Turcotte, 2011). If we assume that the children of the families who left Quebec who would havebeen subject to Bill 101 would have attained high levels of education and above average labourmarket outcomes had they stayed in Quebec, then this would be evidence of a negative selectionbias for the main education and labour market estimates. In other words, the estimates forthe positive effects of Bill 101 on post-secondary educational attainment and on employmentmeasures could be seen as a lower bound of the true effects of the law.However, this assumption is fairly strong. It may also be the case that there were some unobserv-able differences between families likely to be affected by Bill 101 who left the province and thosewho remained. To account more formally for this potential selection bias problem, I perform abounding exercise. Specifically, I bound the main estimates based on a technique in the spirit ofLee (2009) and similar to the one used by Scott-Clayton (2011). To understand how selectionmay bias the findings presented earlier, suppose that we could observe the outcomes of the chil-dren who left as a consequence of Bill 101 if they had instead chosen to remain in Quebec. Then,consider the following equation estimated on the entire sample of first- and second-generationAllophones and Francophones who lived in Quebec in 1976 before the law was introduced:Yi = β0 + γ˜Bill 101i+piSi + βlAllophonei + βgTwoforeignparentsi+1981∑t=1963βtyobt,i +1981∑t=1963βltyobt,i ×Allophonei +1981∑t=1963βgtyobt,i × Twoforeignparentsi+ βlgAllophonei × Twoforeignparentsi +Xiα+ εi(2.14)In equation 2.14, Si is an indicator variable equal to 1 if a person is part of the group who wouldhave chosen to leave Quebec because of Bill 101 and zero otherwise. If we could estimate the372.4. Empirical Resultsfollowing model on all children living in Quebec prior to Bill 101 being introduced (includingthose who did leave), we could measure the extent of the bias. The coefficient pi would provideus with an estimate of the difference in the impact of Bill 101 between the children who left andthose who stayed in Quebec. The concern is that those who left the province are unobservablydifferent from those who stayed (pi different from zero). If this were the case, then the estimatedeffect γˆ obtained by estimating equation 2.6 on the sample of individuals living in Quebec in2006 would not converge to the true effect of Bill 101. Assuming that the assumptions of thetriple differences model hold and that Si is orthogonal to all other variables in the model, thenthe size and direction of the bias thus depends on the fraction of children who left the province asa consequence of Bill 101 and who would have stayed had the law not been introduced, capturedby [Pr (Si = 1) |Bill 101 = 1], as well as how different their outcomes would have been if theyhad remained in Quebec from the outcomes of those who did stay in the province (measured bypi).It is impossible to identify in the 2006 Census data precisely which individuals left Quebecbecause of Bill 101 and what their outcomes would have been had they stayed. In order tobound the potential bias due to this selection problem, I could use the parameter λˆ (obtainedfrom estimating equation 2.13), which provides a causal estimate of the additional probability ofAllophone children targeted by the law leaving the province due to Bill 101 above and beyondthe usual propensity of children in this group to migrate out of the province. This estimate is,however, higher than the actual percentage of children among this group who left the province.For example, in Sample 1, 5.8% of Allophone children targeted by the law (born after October 1,1971 with two foreign-born parents) left the province by 1981 whereas the estimate of the effectof Bill 101 on their propensity to leave is 7.2 percentage points. I therefore use the estimate of 5.8percentage points for [Pr (Mi = 1) |Bill 101 = 1].49 By using this value, I make the assumptionthat all children within the group likely to be subject to Bill 101 were induced to leave dueto Bill 101 being introduced, which implies that the counterfactual assumption is that none ofthem would have left Quebec had the law not been introduced. This is a strong assumption,considering that all of the other control groups in the estimation experienced some degree ofoutmigration, which renders my bounds quite conservative.50Next, following a technique similar to Lee’s (2009) approach, for the purposes of the boundingexercise, I make the extreme assumption that these individuals who left the province representeither the top 5.8% of values for a given outcome to obtain an upper bound or the bottom 5.8% tocalculate a lower bound on my main estimates. Lee’s (2009) technique relies on the MonotonicityAssumption, which states that the treatment assignment (i.e., whether a child was mandatedto study in French because of Bill 101) can only affect sample selection in one direction.51 Inother words, I must assume that all children mandated to study in French through Bill 101 were49This proportion is very similar for children in Samples 2 and 3 respectively.50Between 1976 and 1981, 2.3% of children who were not targeted by the law left the province (Sample 1).51Another assumption needed is the Independence assumption, which states that the “potential” outcomes of382.4. Empirical Resultseither equally likely or more likely to leave Quebec than those not affected by Bill 101. I mustalso assume that the law did not cause other children (Francophones and Allophones exemptfrom the law) to leave the province nor did it affect the inflow of migrants to Quebec. There isno way to directly test these assumptions, although they are likely to hold since the legislationonly restricted the choice of language of instruction offered to children who were targeted byBill 101. Other children did not experience a change in their schooling choices. I discuss theseassumptions further at the end of this section.Hence, to bound the main results of this paper, I re-estimate the effects of Bill 101 by artificiallyadding to the treatment group (i.e., those with Bill 101 = 1) the missing 5.8% of childrenwho left the province due to Bill 101 and assigning to them extreme values of the dependentvariables.52 Specifically, to obtain a lower bound for each of the main estimates of interest,I re-estimate the effects of Bill 101 for each outcome after adding to the treatment group anartificial 5.8% of lowest possible outcome values. Conversely, to obtain an upper bound, I usethe same technique, but adding to the treatment group an artificial 5.8% of the highest possiblevalue of each dependent variable. In the case of binary outcome variables, 0 and 1 correspond totheir lowest and highest possible values. In the case of the continuous income variables, I boundthe effect of the law on the median of the income distribution (as opposed to the mean) becauseof the high sensitivity of the mean to extreme values of the distribution. I therefore performthe bounding exercise by calculating the unconditional quantile effect of Bill 101 on the medianof the income distribution by adding either 5.8% of top or bottom values to the distribution tothe treatment group. The results of the bounding exercise are shown in Table 2.14 (Sample 1).Columns 1 to 3 provide the estimates as well as the upper bounds and lower bounds for the ITTwhereas columns 4 to 6 provide the upper and lower bounds of the ATT. To bound the ATT, Isimply scale the bounds of the ITT estimates by the inverse of the weighted average proportionof treated individuals living in Quebec in 1976 in the sample.53 The magnitudes of all of thebounded effects remain above zero, except in the case of the effects of the law on the probabilityof being unemployed (conditional on being part of the labour force), for which the bounds are nolonger informative. For the most part, the main effects of Bill 101 therefore remain significanteach child as well as their parents’ “potential” decision to move out of the province had they been subject or notto Bill101 is independent of whether they were actually subject to Bill 101. This assumption holds if the necessaryassumptions for the triple differences model hold.52Lee’s (2009) bounding technique involves trimming the outcome distribution of the group that did is mostfrequently observed after the selection occurred. In the context of this paper, this would imply trimming thedistribution of all the children who were not affected by the law since they were more likely to stay in theprovince. Because it is not clear if all or only some of the distributions of the outcome variables of the variouscomparison groups used in the triple differences framework should be trimmed, I instead add to the distributionof the treatment group who experienced a loss of individuals due to Bill 101. This technique can easily beimplemented since the distribution of the majority of the outcome variables considered are bounded due to thefact that they are binary outcome variables.53To scale the upper and lower bound of the ATT, I use the proportion of children who were living in Quebecin 1976 before the law was introduced without an older sibling already enrolled in school in 1977, which was 0.73for Sample 1 and 0.71 for Sample 3.392.4. Empirical Resultswhen accounting for the potential selection bias due to families leaving the province because ofthe introduction of this law. The results are robust to performing this bounding exercise for themain effects of Bill 101 estimated using only second-generation Allophones (Sample 3) (see TableB.7 in Appendix B).One concern with this bounding exercise could be that the migration induced by Bill 101 persistedafter 1981, which would imply that the previous technique underestimates the percentage ofchildren who left the province due to the law. Using the 1986 Census, I estimate the effect of Bill101 on the propensity of Allophones to leave the province by 1986 among those who remainedin Quebec in 1981 (Table B.8 in Appendix B). I find no significant impact of Bill 101 on theseindividuals, suggesting that the outmigration caused by Bill 101 took place entirely within 4 yearsfollowing the introduction of the legislation. As a result, this bounding exercise should capturethe extent of the selection problem caused by the interprovincial outmigration of families withchildren subject to Bill 101.Another concern could be that Bill 101 had an impact on in-migration to Quebec. WithinCanada, it could be the case that a few families or young adults who did not yet have childrenwere less inclined to move to Quebec from other provinces due to Bill 101, but it seems as thoughthese would have been marginal cases, as there was no decrease in in-migration to Quebec amongAllophones following the introduction of Bill 101 (see Figure B.2 for some statistics on the Quebecinterprovincial migration patterns of Francophones and Allophones over time). In addition, asof 1983, it is unlikely that the law affected in-migration from other provinces since children whostudied in English in another Canadian province prior to moving to Quebec were exempted frommandatory schooling in French.In terms of international immigration to Quebec, there were some compositional changes in theorigin of immigrants during the 1970s and 1980s. Prior to 1976, the vast majority of immigrantswho arrived to Quebec were originally from Europe (67.6%), followed by North or South America(15.2%), and a minority of immigrants from Asia (9.1%) and Africa (6.8%). After 1976, theproportion of European immigrants dropped significantly, whereas more and more immigrantsarrived from Asian countries. Between 1976 and 1985, approximately 35% of immigrants arrivedfrom Asia, 30% from the American continent (mainly from the Caribbean), 27% from Europe and8% from Africa (Boudarbat and Boulet, 2010). Although it is possible that Bill 101 had an effecton the type of immigrants who arrived to Quebec as of 1977, the rest of Canada also experiencedsignificant changes in the composition of its immigrants during this period, suggesting that otherfactors were also at play. Nevertheless, these important differences could affect the results ofthe estimation. I address this concern by restricting first-generation immigrants in samples 2and 3 to individuals who arrived prior to the introduction of the law. The main effects arefairly consistent across all three samples. It is, however, possible that the parents of a fewsecond-generation immigrants arrived in Quebec after the introduction of the law. However, thefact that the main results remain approximately the same when restricting the sample to those402.5. Conclusionborn between 1967 and 1976, before the law was introduced, provides some evidence that thesepotential issues related to interprovincial and international in-migration are unlikely to affect theconclusions of this paper.Finally, one could be concerned that Bill 101 had an affect on individuals’ propensity to leavethe province once they reach adulthood after completing their schooling in Quebec, resulting inanother source of selection bias in addition to the one addressed previously using the boundingexercise. This last point is more difficult to address since the Census does not provide enoughinformation to follow individuals throughout their lifetime. When estimating, among all second-generation immigrants born in Quebec across Canada, the effect of the law on the probability ofliving outside of the province in 2006 and 2011, the effects are not larger than those obtained onthe probability of leaving the province by 1981. I therefore conclude that most of the outmigrationfrom Quebec due to Bill 101 occurred very shortly after the law was introduced.2.5 ConclusionBill 101 was, at the time of its introduction in 1977, a controversial law in Quebec and it remainsso today. Proponents of mandatory schooling in French saw this law as a way to promote andprotect the French language and culture of Quebec. Opponents argued for freedom of choicegranted to all parents, not only to children of Anglophones born and raised in Quebec (Cole-man, 1981). Few empirical studies to date have documented the long-term effects of mandatoryschooling in the majority language.This paper provides a first examination of the causal economic impact of mandating first-and second-generation Allophones in Quebec to study in French, the majority language of theprovince. By exploiting the timing of the implementation and the exemption rules of Bill 101regarding mandatory schooling in French, I identify the effects of the law on language use athome and at work, on post-secondary education and labour market outcomes, as well as onchoice of residential location. Among those living in Quebec in 2006, the law had a major im-pact on immigrants’ propensity to use French both at home and in the workplace: an increase ofapproximately 20 percentage points. In addition, in terms of educational attainment and labourmarket outcomes, the law does not appear to have had any adverse effects. Among Allophones, Iestimate that the law was associated with an increase in their propensity of females to completea post-secondary degree, but I find no significant effects for males. The results also suggest thatAllophones mandated to study in French were more likely to participate in the labour force by 8percentage points and less likely to be unemployed and not in school by 6 percentage points. Inaddition, they were more mobile than their peers, which resulted in them being more likely tolive outside of Montreal, the main metropolitan area of the province. I provide suggestive evi-dence that the residential location results are consistent with these individuals being more likely412.5. Conclusionto choose to live in other regions than Montreal in order to be employed in higher paying jobs,such as employment opportunities in the public sector, which require an excellent knowledgeof French. Bill 101, however, also caused some families to leave the province shortly after itsintroduction to avoid sending their children to school in French, especially families with highlyeducated and high-income parents. As a result, nearly 6% of Allophone children targeted bythe law left Quebec by 1981 because of this law. Despite the potential for selection bias due tothis increased outmigration, a bounding exercise shows that the estimated impacts on languageuse, education, labour market outcomes, and regional location choices among those who stayedin Quebec remain significant even in the presence of extreme assumptions about the type ofindividuals targeted by the law who left the province.Understanding the long-term impacts of the law can help evaluate the costs and benefits of sucha policy from an economic point of view. The results of this study are potentially informativeto other jurisdictions in terms of the implications of implementing similar policies related tothe language of instruction in primary and secondary education. The French-speaking cantonof Jura in Switzerland and, more recently, the country of Latvia have respectively consideredand adopted very similar language policies based on Quebec’s Bill 101 (Schmid, Zepa and Snipe,2004; Cotelli, 2013).54 In addition, the state of California enacted Proposition 227 in 1998, whichrequired public schools to favour English-only classes over bilingual classes as a way of teachinglimited English proficiency children (García and Curry-Rodríguez, 2000). The results of thisstudy could, for example, help develop information campaigns for parents who are concernedabout enrolling their child in school that offers instruction in a language that they may notmaster themselves. The results also highlight that policies related to language of instructionmatter enough for certain families to move out of an area in order to avoid being subject to suchpolicies.For the findings of the paper to be externally valid in other contexts, however, certain factorsshould be considered. First, the empirical approach used in this study relies on a partial equi-librium framework. Since Allophone immigrants in Quebec represent a small percentage of thepopulation, it is unlikely that a policy affecting their labour market outcomes would have majorrepercussions on the labour market outcomes of other members of the population. If anotherjurisdiction considers implementing a similar policy to Quebec’s Bill 101 on a group representinga very large fraction of the population, the same conclusions may not apply because of generalequilibrium effects. Furthermore, although prior to the implementation of the law, Allophonefamilies in Quebec were much more likely to speak English at home compared with French (inaddition to their mother tongue), making English a much more familiar language to Allophonechildren than French before they entered school, both English and French remain languages54In 1999, Latvia adopted the Latvian Language Law, which was based mostly on Bill 101. This law restrictedaccess to English and Russian language schools to protect and promote the Latvian language (Schmid, Zepa andSnipe, 2004). The Latvian context is very similar to the Quebec context since a small population who speaks theLatvian language is surrounded by a larger population who speaks Russian.422.6. Figuresother than their mother tongue. In this way, the choice of language of instruction in Quebecfor Allophones prior to the law being implemented was between two “second languages”, neitherof which was the child’s mother tongue. The results of this paper may thus be more closelyapplicable to immigrants in countries trying to preserve one of many official languages than tocountries offering special schooling programs in the mother tongue of immigrants.Overall, this paper highlights some of the economic effects of mandatory schooling in the majoritylanguage on immigrants. While this study only examines very specific economic outcomes, amore complete picture of the long-term effects of such a policy could be obtained through furtherexamination of other socio-economic outcomes, such as the impact of the law on family structure,psychological well-being and on immigrants’ cultural capital loss or accumulation.2.6 FiguresFigure 2.1: Percentage of Elementary and Secondary School Studentsin Quebec Who Study in French by Mother Tongue020406080100Percentage1971 1976 1981 1986 1991 1996 2001 2006Academic yearFrench English OtherSource: Government of Quebec. 2012. Indicateurs linguistiques dans le domaine del’education 2011. Ministère de l’Éducation, du Loisir et du Sport.432.6. FiguresFigure 2.2: Proportion of First- and Second-Generation Immigrants inQuebec Who Speak French at Home (Sample 1)Source: 2006 Canadian Census. Note: Individuals are classified as speaking French athome if they include French when reporting the languages they speak most often or speakon a regular basis at home. The figure presents estimated trends calculated using a locallinear polynomial approximation and its corresponding 95% confidence interval.Figure 2.3: Proportion of First- and Second-Generation Immigrants inQuebec Who Speak English at Home (Sample 1)Source: 2006 Canadian Census. Note: Individuals are classified as speaking English athome if they include English when reporting the languages they speak most often or speakon a regular basis at home. The figure presents estimated trends calculated using a locallinear polynomial approximation and its corresponding 95% confidence interval.442.6. FiguresFigure 2.4: Proportion of First- and Second-Generation Immigrants inQuebec Who Use French Most Often at Work (Sample 1)Source: 2006 Canadian Census. Note: Individuals are classified as using French atwork if they include French when reporting the languages they use most often atwork. The figure presents estimated trends calculated using a local linear polynomialapproximation and its corresponding 95% confidence interval.Figure 2.5: Proportion of First- and Second-Generation Immigrants inQuebec Who Use English Most Often at Work (Sample 1)Source: 2006 Canadian Census. Note: Individuals are classified as using English atwork if they include English when reporting the languages they use most often atwork. The figure presents estimated trends calculated using a local linear polynomialapproximation and its corresponding 95% confidence interval.452.6. FiguresFigure 2.6: Quantile Triple Differences Estimates for Log Income from Wages-1-.50.51Effect of Bill 1011 10 20 30 40 50 60 70 80 90 99Income PercentileSample 1-1-.50.51Effect of Bill 1011 10 20 30 40 50 60 70 80 90 99Income PercentileSample 2-1-.50.51Effect of Bill 1011 10 20 30 40 50 60 70 80 90 99Income PercentileSample 3Note: This figure presents the quantile triple difference estimates using the Firpo, Fortin andLemieux (2009) method. The dotted lines represent the 95% confidence intervals.Figure 2.7: Quantile Triple Differences Estimates for Log Total Income-1-.50.511.52Effect of Bill 1011 10 20 30 40 50 60 70 80 90 99Income PercentileSample 1-1-.50.511.52Effect of Bill 1011 10 20 30 40 50 60 70 80 90 99Income PercentileSample 2-1-.50.511.52Effect of Bill 1011 10 20 30 40 50 60 70 80 90 99Income PercentileSample 3Note: This figure presents the quantile triple difference estimates using the Firpo, Fortinand Lemieux (2009) method. The dotted lines represent the 95% confidence intervals.462.6. FiguresFigure 2.8: Proportion of Children Without an Older Sibling Enrolled in School in1977 by Year of Birth (Among Allophones Targeted by Bill 101 in Sample 1)0.440.470.610.700.81 0.810.860.900.910.950.1.2.3.4.5.6.7.8.911972 1973 1974 1975 1976 1977 1978 1979 1980 1981Year of birthSource: 1981 Canadian Census. Note: The red line segments represent the 95% confidence intervals.472.7. Tables2.7 TablesTable 2.1: Description of the Three Main Samples of AnalysisFirst-generation Second-generationimmigrants living in Quebec immigrants living in Quebec Sample size(i.e. born outside of Canada) (i.e. born in Canada)Sample 1Includes those whoimmigrated to Canadabefore the age of 6Includes those born inQuebec24,090Sample 2Includes those whoimmigrated to Canadabefore the age of 6 and priorto 1977Includes those born inQuebec22,760Sample 3 ExcludedIncludes those born inQuebec20,740Note: The number of observations are based on the 2006 Canadian Census. They are unweighted and rounded tothe nearest multiple of 5. All samples include Allophones and Francophones born between 1962 and 1981 inclusively.First-generation immigrants are defined as foreign-born individuals who immigrated to Canada, whereas second-generation immigrants are individuals born in Canada with at least one parent who is a first-generation immigrantto Canada.Table 2.2: Rules of Applicability of Bill 101Mother tongue Parents’ place of birthBorn before or onOctober 1, 1971Born afterOctober 1, 1971Allophone(Mother tongueother than Frenchor English)One foreign-bornparentTwo foreign-bornparentsExemptExemptExemptBill 101Francophone(French mothertongue)One foreign-bornparentTwo foreign-bornparentsControl groupControl groupControl groupControl group482.7. TablesTable 2.3: Descriptive Statistics (Sample 1)Born prior to Oct. 1, 1971 Born after Oct. 1, 1971Two foreign- One foreign- Two foreign- One foreign-born parents born parents born parents born parentsMean S.D. Mean S.D. Mean S.D. Mean S.D.Panel A: AllophonesAverage age 39.0 (2.9) 39.2 (3.0) 29.2 (2.9) 27.8 (2.7)Female 0.487 (0.250) 0.548 (0.248) 0.503 (0.250) 0.586 (0.243)White 0.930 (0.065) 0.889 (0.099) 0.724 (0.200) 0.903 (0.088)Asian 0.035 (0.034) 0.020 (0.020) 0.148 (0.126) 0.016 (0.016)Black 0.009 (0.009) s s 0.027 (0.026) s sOther 0.026 (0.025) s s 0.101 (0.091) s sFirst-generation immigrant 0.165 (0.138) 0.095 (0.086) 0.194 (0.156) 0.075 (0.069)Observations (weighted) 32,650 995 30,140 1,865Percentage among Allophones 49.7 % 1.5 % 45.9 % 2.8 %Panel B: FrancophonesAverage age 38.9 (3.0) 39.1 (2.9) 28.6 (2.8) 28.8 (2.9)Female 0.479 (0.250) 0.490 (0.250) 0.485 (0.250) 0.504 (0.250)White 0.867 (0.115) 0.948 (0.049) 0.438 (0.246) 0.893 (0.250)Asian 0.036 (0.035) 0.038 (0.037) 0.094 (0.085) 0.083 (0.076)Black 0.085 (0.078) 0.010 (0.010) 0.411 (0.242) 0.018 (0.018)Other 0.036 (0.035) 0.038 (0.037) 0.094 (0.085) 0.083 (0.076)First-generation immigrant 0.242 (0.183) 0.024 (0.023) 0.161 (0.135) 0.034 (0.033)Observations (weighted) 8,320 14,945 15,700 19,700Percentage among Francophones 14.2 % 25.5 % 26.8 % 33.6 %Source: 2006 Canadian Census. The table presents the means and standard deviations (S.D.) in parentheses. Thenumbers of observations are weighted and rounded to the nearest multiple of 5. The symbol s denotes cells thatwere suppressed to meet the confidentiality requirements of the Statistics Act of Statistics Canada.492.7. TablesTable 2.4: Effects on Language Use at Home and at WorkBaseline modelFrench English(1) (2) (3) (4) (5) (6)Sample 1 Sample 2 Sample 3 Sample 1 Sample 2 Sample 3Panel A: Language spoken at homeBill 101 0.212∗∗∗ 0.183∗∗∗ 0.213∗∗∗ -0.280∗∗∗ -0.262∗∗∗ -0.263∗∗∗(0.064) (0.062) (0.065) (0.043) (0.041) (0.043)Allophone -0.473∗∗∗ -0.471∗∗∗ -0.463∗∗∗ 0.463∗∗∗ 0.456∗∗∗ 0.514∗∗∗(0.023) (0.023) (0.024) (0.026) (0.026) (0.025)Two foreign-born parents -0.063∗∗∗ -0.058∗∗∗ -0.030∗∗∗ 0.063∗∗∗ 0.053∗∗∗ 0.000(0.005) (0.006) (0.004) (0.006) (0.005) (0.004)Mean 0.39 s 0.37 0.76 s 0.78Observations 24,090 22,760 20,740 24,090 22,760 20,740R2 0.404 0.418 0.437 0.329 0.340 0.356Panel B: Language used most often at workBill 101 0.186∗∗∗ 0.177∗∗∗ 0.197∗∗∗ -0.160∗ -0.145∗ -0.163∗(0.063) (0.062) (0.067) (0.079) (0.077) (0.078)Allophone -0.218∗∗∗ -0.214∗∗∗ -0.201∗∗∗ 0.304∗∗∗ 0.301∗∗∗ 0.316∗∗∗(0.032) (0.031) (0.028) (0.053) (0.053) (0.049)Two foreign-born parents -0.064∗∗∗ -0.059∗∗∗ -0.051∗∗∗ 0.112∗∗∗ 0.106∗∗∗ 0.085∗∗∗(0.006) (0.005) (0.007) (0.010) (0.009) (0.011)Mean 0.54 s 0.53 0.55 s 0.55Observations 20,920 19,820 18,080 20,920 19,820 18,080R2 0.143 0.149 0.157 0.185 0.194 0.202Note: The table presents the Linear Probability Model coefficients of regressions based on the 2006 CanadianCensus. Standard errors are clustered by year of birth and are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗denote statistical significance at the 1, 5, and 10 percent levels. Sample 1 is the main analysis sample including first-and second-generation Francophone and Allophone immigrants. Sample 2 restricts first-generation immigrantsto those who immigrated to Canada prior to 1977. Sample 3 only includes second-generation immigrants. Allregressions include year of birth fixed effects, all possible two-way interactions between year of birth, two foreign-born parents and Allophone, and control variables for gender, ethnic groups and being a first-generation immigrant.The mean refers to the average of the dependent variable among Allophones born after October 1, 1971 with oneforeign-born parent. The symbol s denotes cells that were suppressed to meet the confidentiality requirements ofthe Statistics Act of Statistics Canada.502.7. TablesTable 2.5: Effects on Post-Secondary Education AttainmentBaseline model Model with gender interactions(1) (2) (3) (4) (5) (6)Sample 1 Sample 2 Sample 3 Sample 1 Sample 2 Sample 3Having a postsecondary education degreeBill 101 0.043 0.045 0.015 0.070∗ 0.070∗ 0.038(0.039) (0.038) (0.035) (0.038) (0.038) (0.036)BIll101×Male -0.055∗∗∗ -0.052∗∗∗ -0.045∗∗∗(0.010) (0.014) (0.014)Male -0.085∗∗∗ -0.084∗∗∗ -0.088∗∗∗ -0.072∗∗∗ -0.072∗∗∗ -0.078∗∗∗(0.010) (0.010) (0.010) (0.010) (0.010) (0.010)Mean 0.75 s 0.76Mean (females only) 0.80 s 0.81Observations 24,090 22,760 20,740 24,090 22,760 20,740R2 0.025 0.024 0.024 0.026 0.025 0.024Note: The table presents the Linear Probability Model coefficients of regressions based on the 2006 CanadianCensus. Standard errors are clustered by year of birth and are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗denote statistical significance at the 1, 5, and 10 percent levels. Sample 1 is the main analysis sample including first-and second-generation Francophone and Allophone immigrants. Sample 2 restricts first-generation immigrantsto those who immigrated to Canada prior to 1977. Sample 3 only includes second-generation immigrants. Allregressions include year of birth fixed effects, all possible two-way interactions between year of birth, two foreign-born parents and Allophone, and control variables for gender, ethnic groups and being a first-generation immigrant.The table also presents the mean of the dependent variable among all Allophones born after October 1, 1971 withone foreign-born parent as well as the corresponding mean for females only. The symbol s denotes cells that weresuppressed to meet the confidentiality requirements of the Statistics Act of Statistics Canada.512.7. TablesTable 2.6: Effects on Labour Market OutcomesBaseline model Model with gender interactions(1) (2) (3) (4) (5) (6)Sample 1 Sample 2 Sample 3 Sample 1 Sample 2 Sample 3Panel A: Being unemployed and not in schoolBill 101 -0.058∗ -0.064∗∗ -0.072∗∗ -0.071∗∗ -0.074∗∗ -0.082∗∗∗(0.029) (0.029) (0.026) (0.029) (0.030) (0.027)Bill101×Male 0.026∗∗ 0.020 0.021(0.012) (0.013) (0.013)Mean 0.12 s 0.12Observations 24,090 22,760 20,740 24,090 22,760 20,740R2 0.014 0.014 0.015 0.014 0.015 0.015Panel B: Being part of the labour forceBill 101 0.091∗∗∗ 0.085∗∗∗ 0.075∗∗∗ 0.098∗∗∗ 0.093∗∗∗ 0.083∗∗∗(0.024) (0.025) (0.022) (0.026) (0.026) (0.023)Bill101×Male -0.014 -0.016 -0.018(0.013) (0.014) (0.014)Mean 0.86 s 0.87Observations 24,090 22,760 20,740 24,090 22,760 20,740R2 0.015 0.015 0.015 0.015 0.015 0.015Panel C: Being unemployed (among those in the labour force)Bill 101 -0.021 -0.024 -0.035∗∗ -0.027∗∗ -0.026∗ -0.035∗∗(0.013) (0.015) (0.014) (0.013) (0.014) (0.014)Bill101×Male 0.012 0.003 0.001(0.008) (0.010) (0.010)Mean 0.04 s 0.04Observations 20,920 19,820 18,080 20,920 19,820 18,080R2 0.008 0.007 0.007 0.008 0.007 0.007Panel D: Working in the public sector (among those in the labour force)Bill 101 0.039 0.035 0.056∗∗ 0.037 0.032 0.053∗(0.025) (0.025) (0.026) (0.025) (0.026) (0.026)Bill101×Male 0.004 0.006 0.006(0.006) (0.007) (0.008)Mean 0.02 s 0.02Observations 20,920 19,820 18,080 20,920 19,820 18,080R2 0.013 0.013 0.015 0.013 0.013 0.015Note: The table presents the Linear Probability Model coefficients of regressions based on the 2006 Canadian Census.Standard errors are clustered by year of birth and are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statisticalsignificance at the 1, 5, and 10 percent levels. Sample 1 is the main analysis sample including first- and second-generation Francophone and Allophone immigrants. Sample 2 restricts first-generation immigrants to those whoimmigrated to Canada prior to 1977. Sample 3 only includes second-generation immigrants. All regressions includeyear of birth fixed effects, all possible two-way interactions between year of birth, two foreign-born parents andAllophone, and control variables for gender, ethnic groups and being a first-generation immigrant. The mean refersto the average of the dependent variable among Allophones born after October 1, 1971 with one foreign-born parent.The symbol s denotes cells that were suppressed to meet the confidentiality requirements of the Statistics Act ofStatistics Canada.522.7. TablesTable 2.7: Effects on IncomeBaseline model Model with gender interactions(1) (2) (3) (4) (5) (6)Sample 1 Sample 2 Sample 3 Sample 1 Sample 2 Sample 3Panel A: Log Wages IncomeBill 101 0.046 0.054 0.117 0.121 0.115 0.176(0.112) (0.116) (0.121) (0.114) (0.118) (0.122)Bill101×Male -0.150∗∗∗ -0.125∗∗ -0.120∗∗(0.051) (0.051) (0.055)Mean $29,773 s $29,508Observations 18,945 17,930 16,395 18,945 17,930 16,395R2 0.066 0.062 0.064 0.067 0.063 0.065Panel B: Log Total IncomeBill 101 0.204 0.197 0.179 0.273∗ 0.256∗ 0.235∗(0.137) (0.138) (0.133) (0.131) (0.131) (0.126)Bill101×Male -0.140∗∗∗ -0.119∗∗∗ -0.113∗∗(0.034) (0.038) (0.041)Mean $28,578 s $28,528Observations 23,940 22,620 20,615 23,940 22,620 20,615R2 0.055 0.051 0.054 0.056 0.051 0.054Note: The table presents the OLS coefficients of regressions based on the 2006 Canadian Census.Standard errors are clustered by year of birth and are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗denote statistical significance at the 1, 5, and 10 percent levels. Sample 1 is the main analysis sampleincluding first- and second-generation Francophone and Allophone immigrants. Sample 2 restrictsfirst-generation immigrants to those who immigrated to Canada prior to 1977. Sample 3 only includessecond-generation immigrants. All regressions include year of birth fixed effects, all possible two-wayinteractions between year of birth, two foreign-born parents and Allophone, and control variables forgender, ethnic groups and being a first-generation immigrant. The mean refers to the average of theincome measures among Allophones born after October 1, 1971 with one foreign-born parent. Thesymbol s denotes cells that were suppressed to meet the confidentiality requirements of the StatisticsAct of Statistics Canada.532.7. TablesTable 2.8: Effects on the Probability of Living in MontrealBaseline model Baseline Model(among non-students)(1) (2) (3) (4) (5) (6)Sample 1 Sample 2 Sample 3 Sample 1 Sample 2 Sample 3Living in MontrealBill 101 -0.029 -0.040 -0.056∗ -0.058∗ -0.065∗∗ -0.087∗∗(0.033) (0.032) (0.030) (0.031) (0.030) (0.030)Mean 0.90 s 0.92 0.86 s 0.95Observations 24,090 22,760 20,740 19,880 18,920 17,140R2 0.148 0.152 0.157 0.158 0.164 0.169Note: The table presents the Linear Probability Model coefficients of regressions based on the 2006Canadian Census. Standard errors are clustered by year of birth and are reported in parentheses.Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percent levels. Sample 1 is themain analysis sample including first- and second-generation Francophone and Allophone immigrants.Sample 2 restricts first-generation immigrants to those who immigrated to Canada prior to 1977.Sample 3 only includes second-generation immigrants. All regressions include year of birth fixed effects,all possible two-way interactions between year of birth, two foreign-born parents and Allophone, andcontrol variables for gender, ethnic groups and being a first-generation immigrant. The mean refers tothe average of the dependent variable among Allophones born after October 1, 1971 with one foreign-born parent. The symbol s denotes cells that were suppressed to meet the confidentiality requirementsof the Statistics Act of Statistics Canada.542.7. TablesTable 2.9: Effects on Labour Market Outcomes by Residential LocationBaseline model Model with location interactions(1) (2) (3) (4) (5) (6)Sample 1 Sample 2 Sample 3 Sample 1 Sample 2 Sample 3Being unemployed and not in schoolBill 101 -0.058∗ -0.064∗∗ -0.072∗∗ -0.076∗ -0.082∗∗ -0.084∗∗(0.029) (0.029) (0.026) (0.038) (0.037) (0.034)Bill101×Montreal 0.019 0.018 0.012(0.020) (0.020) (0.020)Being part of the labour forceBill 101 0.091∗∗∗ 0.085∗∗∗ 0.075∗∗∗ 0.112∗∗∗ 0.080∗ 0.065(0.024) (0.025) (0.022) (0.044) (0.046) (0.030)Bill101×Montreal -0.022 0.005 0.009(0.021) (0.035) (0.037)Being unemployed (among those in the labour force)Bill 101 -0.021 -0.024 -0.035∗∗ -0.005 -0.022 -0.035(0.013) (0.015) (0.014) (0.026) (0.027) (0.029)Bill101×Montreal -0.017 -0.003 -0.001(0.022) (0.018) (0.019)Working in the public sector (among those in the labour force)Bill 101 0.039 0.035 0.056∗∗ 0.092∗∗∗ 0.098∗∗∗ 0.119∗∗∗(0.025) (0.025) (0.026) (0.030) (0.034) (0.035)Bill101×Montreal -0.059∗∗ -0.069∗∗ -0.069∗∗(0.027) (0.032) (0.033)Log wage incomeBill 101 0.046 0.054 0.117 0.073 0.155 0.218(0.112) (0.116) (0.121) (0.167) (0.164) (0.169)Bill101×Montreal -0.015 -0.092 -0.091(0.106) (0.082) (0.087)Log total incomeBill 101 0.204 0.197 0.179 0.400∗∗ 0.384∗∗ 0.352∗∗(0.137) (0.138) (0.133) (0.161) (0.163) (0.161)Bill101×Montreal -0.202∗∗ -0.191∗∗ -0.176∗(0.071) (0.082) (0.087)Note: The table presents the Linear Probability Model coefficients (binary outcomes) and OLS coefficients (incomemeasures) of regressions based on the 2006 Canadian Census. Standard errors are clustered by year of birth andare reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percentlevels. Sample 1 is the main analysis sample including first- and second-generation Francophone and Allophoneimmigrants. Sample 2 restricts first-generation immigrants to those who immigrated to Canada prior to 1977.Sample 3 only includes second-generation immigrants. All regressions include year of birth fixed effects, all possibletwo-way interactions between year of birth, two foreign-born parents and Allophone, and control variables forgender, ethnic groups, being a first-generation immigrant and living in Montreal.552.7. TablesTable 2.10: Robustness and Placebo Tests (Sample 1)(1) (2) (3) (4) (5) (6) (7)Baseline Probit Baseline Baseline DD among DD among Placebomodel model model on model on two foreign- Allophones test1957-1986 1967-1976 born parentsPanel A: Language useFrench at home 0.212∗∗∗ 0.142∗∗∗ 0.335∗∗∗ 0.083 0.110∗∗∗ 0.205∗∗∗ -0.005(0.064) (0.045) (0.050) (0.071) (0.017) (0.059) (0.011)English at home -0.280∗∗∗ -0.337∗∗∗ -0.274∗∗∗ -0.285∗∗∗ -0.182∗∗∗ -0.207∗∗∗ -0.019(0.043) (0.048) (0.035) (0.070) (0.025) (0.039) (0.019)French at work 0.186∗∗∗ 0.148∗∗∗ 0.223∗∗∗ 0.098 0.100∗∗∗ 0.162∗∗∗ 0.022(0.063) (0.052) (0.046) (0.056) (0.021) (0.056) (0.029)English at work -0.160∗ -0.151∗ -0.197∗∗∗ -0.161 -0.127∗∗∗ -0.109 -0.016(0.079) (0.077) (0.059) (0.110) (0.024) (0.065) (0.026)Panel B: Post-secondary education degreeOverall effect 0.043 0.042 0.031 0.095∗ 0.002 0.054 0.027(0.039) (0.039) (0.033) (0.042) (0.017) (0.032) (0.021)Effect for females 0.070∗ 0.070∗ 0.057 0.119∗∗ 0.034∗ 0.091∗∗ 0.054∗∗(0.038) (0.037) (0.034) (0.045) (0.019) (0.033) (0.025)Differential effect -0.055∗∗∗ -0.059∗∗∗ -0.053∗∗∗ -0.047∗∗∗ -0.064∗∗∗ -0.075∗∗∗ -0.051∗∗for males (0.010) (0.012) (0.013) (0.010) (0.011) (0.016) (0.024)Panel C: Residential locationLiving in Montreal -0.029 -0.054 -0.055∗∗ -0.065∗ -0.070∗∗∗ -0.032 0.004(0.033) (0.043) (0.024) (0.032) (0.015) (0.026) (0.020)Living in Montreal -0.058∗ -0.085∗∗ -0.061∗∗ -0.098∗∗ -0.065∗∗∗ -0.054∗∗ 0.010(for non-students) (0.031) (0.042) (0.028) (0.032) (0.016) (0.025) (0.021)Panel D: Labour market outcomesUnemployed and -0.058∗ -0.061∗∗ -0.032 -0.091∗ -0.011 -0.049∗ 0.035not in school (0.029) (0.025) (0.026) (0.047) (0.016) (0.028) (0.023)In labour force 0.091∗∗∗ 0.081∗∗∗ 0.120∗∗∗ 0.090∗ 0.043∗∗∗ 0.069∗∗ -0.032(0.024) (0.021) (0.020) (0.043) (0.015) (0.026) (0.020)Unemployed -0.021 -0.033∗∗∗ -0.005 -0.031 -0.005 0.001 -0.002(0.013) (0.013) (0.018) (0.027) (0.009) (0.014) (0.009)Public sector 0.039 0.052 0.039∗ 0.073∗∗ 0.009 0.042∗ 0.018(0.025) (0.038) (0.020) (0.031) (0.011) (0.023) (0.015)Log wage 0.046 - 0.042 -0.017 0.018 -0.047 0.038income (0.112) (0.107) (0.091) (0.066) (0.105) (0.105)Log total 0.204 - 0.233∗∗ 0.288 0.099∗ 0.088 -0.041income (0.137) (0.105) (0.255) (0.050) (0.119) (0.072)Note: The table presents in column 2 the marginal effects calculated at the mean for discrete changes of dummy variablesfrom 0 to 1. The other columns of the table present Linear Probability Model or OLS coefficients. All regressions are basedon the 2006 Canadian Census. Standard errors are clustered by year of birth and are reported in parentheses. Symbols ∗∗∗,∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percent levels. All estimates are based on the main analysis sample(Sample 1), which includes first- and second-generation Francophone and Allophone immigrants. All regressions in panels Ato D include control variables for gender, ethnic groups, and being a first-generation immigrant.562.7. TablesTable 2.10 (Continued): Robustness and Placebo Tests (Sample 1)(1) (2) (3) (4) (5) (6) (7)Baseline Probit Baseline Baseline DD among DD among Placebomodel model model on model on two foreign- Allophones test1957-1986 1967-1976 born parentsPanel E: Labour market outcomes with residential location interactionsUnemployed and not in schoolBill 101 -0.076∗ -0.076∗∗ -0.056∗ -0.125∗∗ -0.022 -0.056 0.044(0.038) (0.030) (0.029) (0.049) (0.029) (0.051) (0.047)Bill 101×Montreal 0.019 0.021 0.025∗ 0.036 0.012 0.008 -0.009(0.020) (0.021) (0.014) (0.024) (0.024) (0.037) (0.038)In the labour forceBill 101 0.112∗∗∗ 0.098∗∗∗ 0.168∗∗∗ 0.107∗ 0.061∗∗ 0.109∗ -0.033(0.044) (0.028) (0.034) (0.053) (0.029) (0.053) (0.038)Bill 101×Montreal -0.022 -0.027 -0.050∗∗ -0.018 -0.019 -0.040 0.002(0.021) (0.026) (0.020) (0.018) (0.024) (0.037) (0.029)Unemployed (among those in the labour force)Bill 101 -0.005 -0.028∗ -0.013 -0.042 0.017 0.036 -0.011(0.026) (0.016) (0.024) (0.045) (0.025) (0.030) (0.013)Bill 101×Montreal -0.017 -0.008 0.008 0.011 -0.023 -0.036 0.009(0.022) (0.011) (0.016) (0.022) (0.023) (0.023) (0.013)Public sector (among those in the labour force)Bill 101 0.092∗∗∗ 0.101∗∗ 0.091∗∗∗ 0.101∗ 0.047 0.087∗∗∗ 0.042(0.030) (0.043) (0.028) (0.048) (0.033) (0.028) (0.032)Bill 101×Montreal -0.059∗∗ -0.031∗∗∗ -0.057∗∗ -0.035 -0.045 -0.051∗ -0.024(0.027) (0.008) (0.022) (0.040) (0.031) (0.029) (0.026)Log wage incomeBill 101 0.073 - 0.111 0.045 0.011 0.041 0.095(0.167) (0.137) (0.134) (0.132) (0.159) (0.122)Bill 101×Montreal -0.015 - -0.061 -0.044 0.016 -0.072 -0.065(0.106) (0.074) (0.127) (0.110) (0.114) (0.061)Log total incomeBill 101 0.400∗∗ - 0.458∗∗∗ 0.387 0.256∗∗ 0.396∗∗ -0.096(0.161) (0.143) (0.267) (0.091) (0.184) (0.141)Bill 101×Montreal -0.202∗∗ - -0.230∗∗∗ -0.096∗ -0.161∗ -0.314∗∗ 0.058(0.071) (0.065) (0.050) (0.080) (0.130) (0.130)Observations 24,090 24,090 36,145 10,310 16,890 12,780 12,505Note: The table presents in column 2 the marginal effects calculated at the mean for discrete changes of dummy variablesfrom 0 to 1. The other columns of the table present Linear Probability Model or OLS coefficients. All regressions are basedon the 2006 Canadian Census. Standard errors are clustered by year of birth and are reported in parentheses. Symbols ∗∗∗,∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percent levels. All estimates are based on the main analysis sample(Sample 1), which includes first- and second-generation Francophone and Allophone immigrants. All regressions in panel Einclude control variables for gender, ethnic groups, being a first-generation immigrant, and living in Montreal.572.7. TablesTable 2.11: Pooled 2006 and 2011 ResultsSample1 Sample 2 Sample 32006 2011 2006 2011 2006 2011Panel A: Language useFrench at home 0.160∗∗∗ 0.188∗∗∗ 0.133∗∗ 0.159∗∗∗ 0.171∗∗∗ 0.193∗∗∗(0.050) (0.048) (0.049) (0.047) (0.052) (0.048)English at home -0.241∗∗∗ -0.231∗∗∗ -0.223∗∗∗ -0.216∗∗∗ -0.265∗∗∗ -0.257∗∗∗(0.047) (0.049) (0.047) (0.049) (0.047) (0.048)French at work 0.083 0.107∗ 0.070 0.096∗ 0.096∗ 0.096∗(0.052) (0.053) (0.050) (0.052) (0.055) (0.057)English at work -0.132∗∗ -0.142∗∗ -0.114∗ -0.131∗ -0.140∗∗ -0.154∗∗(0.060) (0.064) (0.060) (0.065) (0.062) (0.067)Panel B: Post-secondary education degreeOverall effect 0.035 0.027 0.036 0.026 0.013 0.009(0.025) (0.027) (0.025) (0.028) (0.023) (0.026)Effect for females 0.063∗∗ 0.037 0.063∗∗ 0.042 0.036 0.025(0.027) (0.027) (0.027) (0.026) (0.026) (0.025)Differential effect -0.057∗∗∗ -0.021 -0.054∗∗∗ -0.032∗ -0.047∗∗∗ -0.031∗for males (0.011) (0.015) (0.014) (0.018) (0.014) (0.018)Panel C: Residential locationLiving in Montreal -0.057∗∗ -0.042 -0.065∗∗ -0.047∗ -0.090∗∗∗ -0.067∗∗(0.027) (0.027) (0.024) (0.026) (0.024) (0.024)Living in Montreal -0.067∗∗ -0.058∗∗ -0.073∗∗∗ -0.063∗∗ -0.105∗∗∗ -0.087∗∗∗(among non-students) (0.025) (0.026) (0.025) (0.026) (0.024) (0.025)Panel D: Labour market outcomesUnemployed and -0.028 -0.040∗ -0.033 -0.043∗ -0.047∗ -0.060∗∗not in school (0.023) (0.021) (0.025) (0.023) (0.025) (0.023)In labour force 0.069∗∗∗ 0.060∗∗ 0.068∗∗ 0.059∗∗ 0.066∗∗ 0.061∗∗(0.023) (0.021) (0.024) (0.022) (0.027) (0.026)Unemployed -0.020 -0.025 -0.023 -0.025 -0.035∗ -0.037∗∗(0.017) (0.015) (0.018) (0.015) (0.017) (0.016)Public sector 0.014 0.004 0.011 -0.001 0.027 0.013(0.018) (0.017) (0.018) (0.016) (0.018) (0.016)Log wage income 0.102 0.085 0.109 0.078 0.147 0.120(0.103) (0.104) (0.105) (0.105) (0.113) (0.111)Log total income 0.100 0.049 0.098 0.028 0.119 0.049(0.090) (0.088) (0.091) (0.087) (0.094) (0.090)Note: The table presents the Linear Probability Model or OLS coefficients of regressions based on a pooled sampleof the 2006 Canadian Census and the 2011 National Household Survey. Standard errors are clustered by yearof birth and are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and10 percent levels. Sample 1 is the main analysis sample including first- and second-generation Francophone andAllophone immigrants. Sample 2 restricts first-generation immigrants to those who immigrated to Canada priorto 1977. Sample 3 only includes second-generation immigrants. All regressions in panels A to D include yearspecific birth cohort fixed effects, all possible two-way interactions between year of birth, two foreign-born parentsand Allophone, and control variables for gender, ethnic groups, being a first-generation immigrant, age, and adummy variable for outcomes measures in 2011.582.7. TablesTable 2.11 (Continued): Pooled 2006 and 2011 ResultsSample1 Sample 2 Sample 32006 2011 2006 2011 2006 2011Panel E: Labour market outcomes with residential location interactionsUnemployed and not in schoolBill 101 -0.041 -0.057∗ -0.044 -0.074∗∗ -0.056 -0.093∗∗∗(0.036) (0.029) (0.035) (0.034) (0.036) (0.030)Bill 101×Montreal 0.014 0.017 0.012 0.031 0.009 0.035(0.019) (0.024) (0.019) (0.032) (0.019) (0.028)Being in the labour forceBill 101 0.094∗∗∗ 0.080∗∗∗ 0.066 0.087∗∗ 0.062 0.098∗∗∗(0.032) (0.024) (0.045) (0.033) (0.050) (0.031)Bill 101×Montreal -0.024 -0.022 0.002 -0.029 0.004 -0.038(0.020) (0.026) (0.036) (0.035) (0.038) (0.027)Unemployed (among those in labour force)Bill 101 0.003 -0.022 -0.017 -0.027 -0.031 -0.036∗(0.030) (0.018) (0.026) (0.018) (0.027) (0.019)Bill 101×Montreal -0.024 -0.004 -0.007 0.001 -0.004 -0.000(0.021) (0.011) (0.015) (0.011) (0.017) (0.013)Public sector (among those in labour force)Bill 101 0.047 0.083∗∗∗ 0.056 0.091∗∗ 0.068∗∗ 0.112∗∗(0.031) (0.032) (0.033) (0.039) (0.035) (0.042)Bill 101×Montreal -0.040 -0.088∗∗∗ -0.052 -0.100∗∗ -0.050 -0.109∗∗(0.025) (0.029) (0.030) (0.036) (0.031) (0.039)Log wage incomeBill 101 0.114 0.211 0.194 0.260∗ 0.247 0.344∗∗(0.156) (0.134) (0.146) (0.142) (0.150) (0.127)Bill 101×Montreal -0.001 -0.123∗ -0.076 -0.181∗∗ -0.090 -0.223∗∗∗(0.104) (0.066) (0.079) (0.076) (0.084) (0.055)Log total incomeBill 101 0.294∗∗ 0.269∗∗ 0.284∗∗ 0.311∗∗∗ 0.304∗∗ 0.357∗∗∗(0.112) (0.096) (0.113) (0.091) (0.116) (0.084)Bill 101×Montreal -0.197∗∗∗ -0.229∗∗∗ -0.187∗∗ -0.294∗∗∗ -0.185∗∗ -0.317∗∗∗(0.068) (0.062) (0.077) (0.044) (0.082) (0.054)Observations 50,505 47,870 43,535Note: The table presents the Linear Probability Model or OLS coefficients of regressions based on a pooled sampleof the 2006 Canadian Census and the 2011 National Household Survey. Standard errors are clustered by yearof birth and are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and10 percent levels. Sample 1 is the main analysis sample including first- and second-generation Francophone andAllophone immigrants. Sample 2 restricts first-generation immigrants to those who immigrated to Canada priorto 1977. Sample 3 only includes second-generation immigrants. All regressions in panels A to D include yearspecific birth cohort fixed effects, all possible two-way interactions between year of birth, two foreign-born parentsand Allophone, and control variables for gender, ethnic groups, being a first-generation immigrant, age, and adummy variable for outcomes measures in 2011.592.7. TablesTable 2.12: Estimates of the Average Treatment Effects on the TreatedITT ATT(1) (2) (3) (4) (5) (6)Sample 1 Sample 2 Sample 3 Sample 1 Sample 2 Sample 3Panel A: Language useFrench at home 0.212∗∗∗ 0.183∗∗∗ 0.213∗∗∗ 0.290 0.251 0.304(0.064) (0.062) (0.065)English at home -0.280∗∗∗ -0.262∗∗∗ -0.263∗∗∗ -0.384 -0.359 -0.376(0.043) (0.041) (0.043)French at work 0.186∗∗∗ 0.177∗∗∗ 0.197∗∗∗ 0.255 0.242 0.281(0.063) (0.062) (0.067)English at work -0.160∗ -0.145∗ -0.163∗ -0.219 -0.199 -0.233(0.079) (0.077) (0.078)Panel B: Post-secondary education degreeOverall effect 0.043 0.045 0.015 0.059 0.062 0.021(0.039) (0.038) (0.035)Effect for females 0.070∗ 0.070∗ 0.038 0.096 0.096 0.054(0.038) (0.038) (0.036)Differential effect -0.055∗∗∗ -0.052∗∗∗ -0.045∗∗∗ -0.075 -0.071 -0.064for males (0.010) (0.014) (0.014)Panel C: Residential locationLiving in Montreal -0.029 -0.040 -0.056∗ -0.040 -0.055 -0.080(0.033) (0.032) (0.030)Living in Montreal -0.058∗ -0.065∗∗ -0.087∗∗ -0.079 -0.089 -0.124(among non-students) (0.031) (0.030) (0.030)Panel D: Labour market outcomesUnemployed and -0.058∗ -0.064∗∗ -0.072∗∗ -0.079 -0.088 -0.103not in school (0.029) (0.029) (0.026)In labour force 0.091∗∗∗ 0.085∗∗∗ 0.075∗∗∗ 0.125 0.116 0.107(0.024) (0.025) (0.022)Unemployed -0.021 -0.024 -0.035∗∗ -0.029 -0.033 -0.050(0.013) (0.015) (0.014)Public sector worker 0.039 0.035 0.056∗∗ 0.053 0.048 0.080(0.025) (0.025) (0.026)Log wage income 0.046 0.054 0.117 0.063 0.074 0.167(0.112) (0.116) (0.121)Log total income 0.204 0.197 0.179 0.279 0.270 0.256(0.137) (0.138) (0.133)Note: All estimates are based on the 2006 Canadian Census. Standard errors are clustered by year of birth andare reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percentlevels. Sample 1 is the main analysis sample including first- and second-generation Francophone and Allophoneimmigrants. Sample 2 restricts first-generation immigrants to those who immigrated to Canada prior to 1977.Sample 3 only includes second-generation immigrants.602.7. TablesTable 2.13: Effects on the Probability of Living Outside of Quebec in 1981(among those living in Quebec in 1976)(1) (2) (3)Sample 1 Sample 2 Sample 3Panel A: Baseline modelBill 101 0.072∗∗∗ 0.068∗∗∗ 0.056∗∗∗(0.023) (0.023) (0.016)Panel B: Model with parental education group interactionsBill 101 0.050∗∗ 0.047∗∗ 0.034∗∗(0.022) (0.022) (0.015)Bill 101×Education Level 2 0.023∗∗∗ 0.023∗∗ 0.025∗∗(0.008) (0.009) (0.010)Bill 101×Education Level 3 0.075∗∗∗ 0.086∗∗∗ 0.091∗∗∗(0.019) (0.018) (0.020)Bill 101×Education Level 4 0.131∗∗∗ 0.130∗∗∗ 0.156∗∗∗(0.012) (0.012) (0.010)Panel C: Model with parental income quartile interactionsBill 101 0.050∗∗ 0.049∗∗ 0.041∗∗(0.023) (0.023) (0.017)Bill 101×Income Quartile 2 0.009 0.006 -0.000(0.009) (0.009) (0.010)Bill 101×Income Quartile 3 0.036∗∗∗ 0.032∗∗∗ 0.025∗∗(0.010) (0.010) (0.011)Bill 101×Income Quartile 4 0.067∗∗∗ 0.063∗∗∗ 0.057∗∗∗(0.013) (0.012) (0.014)Note: The table presents the Linear Probability Model coefficients of regressions based on the 1981Canadian Census. Standard errors are clustered by year of birth and are reported in parentheses.Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percent levels. Sample1 is the main analysis sample including first- and second-generation Francophone and Allophoneimmigrants who were living in Quebec in 1976. Sample 2 restricts first-generation immigrants tothose who immigrated to Canada prior to 1977. Sample 3 only includes second-generation immigrants.All regressions include year of birth fixed effects, all possible two-way interactions between year ofbirth, two foreign-born parents and Allophone, and control variables for gender, ethnic groups andbeing a first-generation immigrant. Parents’ education levels are defined as the highest educationalattainment of both parents according to the following categories: high school degree or less (omittedgroup), college degree or some university (level 2), university Bachelor degree (level3), and universitypost-graduate degree (level 4). Parents’ income groups are defined according to the four quartiles ofthe family income distribution.612.7. TablesTable 2.13 (Continued): Effects on the Probability of Living Outside of Quebecin 1981 (among those living in Quebec in 1976)(1) (2) (3)Sample 1 Sample 2 Sample 3Panel D: Model with ethnic group interactionsBill 101 0.093∗∗∗ 0.090∗∗∗ 0.083∗∗∗(0.024) (0.024) (0.018)Bill 1011×Haitian -0.054∗∗∗ -0.033∗∗ -0.064∗∗∗(0.007) (0.013) (0.007)Bill 101×Italian -0.042∗∗∗ -0.045∗∗∗ -0.050∗∗∗(0.007) (0.009) (0.010)Bill 101×Greek -0.036∗∗∗ -0.037∗∗∗ -0.040∗∗∗(0.009) (0.010) (0.011)Bill 101×Jewish -0.037∗∗∗ -0.034∗∗∗ -0.040∗∗∗(0.011) (0.010) (0.011)Bill 101×Portuguese -0.047∗∗∗ -0.042∗∗∗ -0.049∗∗∗(0.011) (0.014) (0.014)Bill 101×North African -0.048 -0.051 -0.062(0.047) (0.053) (0.058)Bill 101×Chinese 0.175∗∗∗ 0.181∗∗∗ 0.202∗∗∗(0.031) (0.033) (0.036)Bill 101×Vietnamese 0.016 -0.019∗ -0.017(0.026) (0.010) (0.022)Mean 0.04 s sObservations 23,785 21,830 21,400Note: The table presents the Linear Probability Model coefficients of regressions based on the 1981Canadian Census. Standard errors are clustered by year of birth and are reported in parentheses.Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percent levels. Sample 1 is themain analysis sample including first- and second-generation Francophone and Allophone immigrantswho were living in Quebec in 1976. Sample 2 restricts first-generation immigrants to those whoimmigrated to Canada prior to 1977. Sample 3 only includes second-generation immigrants. Allregressions include year of birth fixed effects, all possible two-way interactions between year of birth,two foreign-born parents and Allophone, and control variables for gender, ethnic groups and beinga first-generation immigrant. The mean refers to the average of the dependent variable amongAllophones born after October 1, 1971 with one foreign-born parent. The symbol s denotes cells thatwere suppressed to meet the confidentiality requirements of the Statistics Act of Statistics Canada.622.7. TablesTable 2.14: Bounded Main Estimates (Sample 1)ITT ATT(1) (2) (3) (4) (5) (6)Lower Effect Upper Lower Effect Upperbound bound bound boundPanel A: Language useFrench at home 0.184∗∗∗ 0.212∗∗∗ 0.242∗∗∗ 0.252 0.290 0.332(0.063) (0.062) (0.063)English at home -0.316∗∗∗ -0.280∗∗∗ -0.259∗∗∗ -0.433 -0.384 -0.355(0.043) (0.041) (0.043)French at work 0.152∗∗ 0.186∗∗∗ 0.209∗∗∗ 0.208 0.255 0.286(0.062) (0.063) (0.062)English at work -0.191∗∗ -0.160∗ -0.134∗ -0.262 -0.219 -0.184(0.076) (0.079) (0.076)Panel B: Postsecondary education degreeOverall effect 0.000 0.043 0.058 0.000 0.059 0.079(0.041) (0.039) (0.041)Effect for females 0.023 0.070∗ 0.081∗∗ 0.032 0.096 0.111(0.038) (0.038) (0.038)Panel C: Residential locationLiving in Montreal -0.084∗∗ -0.029 -0.027 -0.115 -0.040 -0.037(0.032) (0.033) (0.033)Living in Montreal -0.115∗∗∗ -0.058∗ -0.056∗ -0.158 -0.079 -0.077(among non-students) (0.031) (0.031) (0.031)Panel D: Labour market outcomesUnemployed and -0.065∗∗ -0.058∗ -0.008 -0.089 -0.079 -0.011not in school (0.029) (0.029) (0.029)In labour force 0.040 0.091∗∗∗ 0.098∗∗∗ 0.055 0.125 0.134(0.024) (0.024) (0.024)Unemployed -0.024∗ -0.021 0.033∗∗ -0.033 -0.029 0.045(0.014) (0.013) (0.014)Public sector 0.037 0.039 0.095∗∗∗ 0.051 0.053 0.130(0.025) (0.025) (0.025)Log wage income (median) 0.064 0.142∗ 0.200∗∗∗ 0.087 0.195 0.273(0.078) (0.073) (0.075)Log total income (median) 0.058∗ 0.068 0.140 0.079 0.092 0.192(0.087) (0.081) (0.082)Note: All estimates are based on the main analysis sample (Sample 1) of the 2006 Census, which includes first-and second-generation Francophone and Allophone immigrants. Standard errors are clustered by year of birth incolumn 2 and bootstrapped in columns 1 and 3. They are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denotestatistical significance at the 1, 5, and 10 percent levels.63Chapter 3Parents’ Savings for their Child’sPost-Secondary Education: WhichIncentives Work and Why?3.1 Context and MotivationThe concern that many households save too little has motivated a number of public policy inter-ventions over the past several decades in Canada, the U.S., and many other countries (Crossley,Emmerson and Leicester, 2012). Several governments offer saving incentive programs to encour-age individuals to accumulate savings, mainly for their retirement. For example, tax-deductibleretirement savings accounts are present in Canada, the U.S., Denmark, and the U.K (Chettyet al., 2012; Crossley, Emmerson and Leicester, 2012). The rationale for these policies is thatby offering higher saving incentives, such as tax-favoured returns on savings or saving subsidies,individuals will increase their saving stock and saving flows and thereby avoid under-saving fortheir retirement.Understanding how individuals respond to saving incentives is thus crucial in order to evaluatewhether these policies attain their goal of increasing savings. Multiple studies have examinedhow individuals respond to retirement saving incentives (Engen, Gale and Scholz, 1996; Poterba,Venti and Wise, 1996; Bernheim, 2002; Benjamin, 2003; Gelber, 2011; Chetty et al., 2012);however, very little research has examined people’s saving behaviour in the context of parentssaving for their child’s post-secondary education. This paper attempts to fill this gap in theliterature by testing the empirical predictions of three theoretical saving frameworks in thisparticular context: the neoclassical life-cycle saving model, the fixed-goal saving model, and theprocrastination saving model. To differentiate between the predictions of each saving model, Ievaluate the effects of three Canadian saving incentives for children’s post-secondary educationon four outcomes: personal contributions, overall savings, the age of the child when the savingsaccount was created, and the frequency of contributions to the savings account. To measurethese effects, I take advantage of the administrative database of the Canada Education SavingsProgram (CESP), which includes information on the savings in Registered Education SavingsPlans (RESPs) between 1998 and 2012 of over 4.5 million Canadian children (Employment643.1. Context and Motivationand Social Development Canada, 2014b). Under this program, parents can accumulate savingsfor their child’s post-secondary education in RESPs, which are incentivised education savingsaccounts.55 The CESP offers saving incentives in the form of matching rates on contributionsor subsidies when opening an account, many of which are targeted specifically at low-incomefamilies. Using a regression discontinuity design and a panel data regression approach, I evaluatethe effects of three Canadian education saving incentive measures on parents’ saving behaviourin RESPs. I compare the predictions of the models with the empirical effects of each savingincentive and assess their effectiveness in increasing savings in education savings accounts.The contributions of this study are twofold. First, this paper contributes to the existing literatureby providing evidence on the most useful saving model for thinking about how parents save fortheir child’s post-secondary education, and in light of this model, which saving incentives are themost effective. Whereas numerous studies have modelled and examined the saving behaviourof individuals with respect to retirement savings or lifetime precautionary savings (see Crossley,Emmerson and Leicester (2012) for a summry), very few studies have focused on the savingbehaviour of parents for their child’s post-secondary education. Parents’ saving behaviour inthis context may differ from other contexts for various reasons: parents who save for their child’shigher education are not saving directly for themselves, the saving horizon for education savingsis generally shorter and more likely to be known to the savers than the horizon for retirementsavings, and parents may have a better idea of how much they need to save for their child’s post-secondary education in contrast to lifetime precautionary or retirement savings, which involvemore unknowns. Because of these particularities, traditional saving models may not apply tothis particular setting.Second, there is evidence that the presence of liquidity constraints is an important factor lim-iting access to post-secondary education, especially among low-income families, due to eitheractual credit constraints or debt aversion (Lochner and Monge-Naranjo, 2012; Lavecchia, Liuand Oreopoulos, 2014). Education saving incentive programs may be one approach to decreaseyoung adults’ financial burden through transfers from their parents (via education savings) andthus prevent youth from low-income families from underinvesting in their education. By evalu-ating the impact of various saving incentive programs, especially those targeted at low-incomefamilies, this study evaluates whether the incentives are effective and attain their primary goalof increasing the education savings of children in targeted education savings accounts.56 Theresults of such an evaluation are thus useful to inform policymakers who create and design edu-cation saving incentive programs with the goal of promoting education savings. In the Canadian55For simplicity, throughout this paper, I assume that the contributors to RESPs are the parents of the RESPbeneficiary; however, anyone may contribute to a child’s RESP. This simplification does not affect the conclusionsof the paper.56This chapter focuses on education savings specifically in RESPs. The next chapter will provide some evidenceon crowding-out effects of RESP savings on other types of education savings and thus provide a more generalassessment of the effects of incentivised savings accounts, such as RESPs, on overall education savings.653.2. Institutional Background: Education Saving Incentive Programs in Canadacontext, given the recent introduction of education saving incentives in Canada (see section 3.2for details), little empirical research has been conducted to study the effects of these incentiveson parents’ saving behaviour in RESPs. The results of this paper will help fill this gap.Overall, the results of this study suggest that the actions of parents seem to generally be consis-tent with the procrastination saving model, as developed in the behavioural economics literature(see section 3.3.2), when saving for their child’s post-secondary education. This behaviour is es-pecially pronounced among modest-income families. I estimate that a $500 grant conditional onopening an account generally causes both the RESP take up rate to increase and parents to startsaving earlier in RESPs for their child (by approximately 1 year). Among low-income familiesspecifically, I find evidence that higher matching rates on contributions and grants conditionalon opening an account increased parents’ contributions and thus overall savings in RESPs.The rest of the paper is organised as follows. In section 3.2, I describe the various saving incentiveprograms in Canada. Section 3.3 depicts the three theoretical saving models I consider in thisstudy, as well as their predictions regarding the individual agent’s response to lump-sum subsidiesand increased returns on savings. In section 3.4, I describe the administrative database used forthe empirical analysis. I present the methodology and empirical results in section 3.5. Finally, Idiscuss the implications and limitations of the results in section 3.6 and offer overall conclusionsin section 3.7.3.2 Institutional Background: Education Saving IncentivePrograms in CanadaIn Canada, both federal and provincial public education saving incentive programs are currentlyoffered to encourage parents to save for their child’s post-secondary education. The main federalsaving incentive program, the Canada Education Savings Program (CESP) consists of one savingvehicle, the Registered Education Savings Plan (RESP), and two saving incentives, the CanadaEducation Savings Grant (CESG), in the form of a matching rate on contributions, and theCanada Learning Bond (CLB), a subsidy to the RESP accounts of children in low-income families.Provincial programs provide additional saving incentives, which are also based on RESPs. Dueto data limitations on some of the provincial programs as well as their very recent introduction,this paper will focus solely on the Alberta saving incentive.57 Sections 3.2.1 to 3.2.4 provide adescription of the various saving incentive programs analysed in this paper.57The provincial programs were introduced more recently than the federal incentives (1998) in the provinces ofAlberta (2005), Quebec (2007), Saskatchewan (2013) and British Columbia (2015).663.2. Institutional Background: Education Saving Incentive Programs in Canada3.2.1 Registered Education Savings Plans (RESPs)Registered Education Savings Plans (RESPs) are education saving vehicles registered with thegovernment of Canada and provided by the majority of financial institutions and financial serviceproviders (Employment and Social Development Canada, 2015). They were first created in 1974,but they only started being extensively used after their 1997 and 1998 reforms (Milligan, 2005).Contributors to the RESP, who are typically parents of the child beneficiary (but who canalso be other relatives or family friends), may contribute up to a lifetime limit of $50,000 perbeneficiary.58 Although contributions to RESPs are made out of after-tax income, all earnings onfunds in RESPs remain tax free until withdrawn for the beneficiary’s post-secondary education.If enrolled in a qualifying educational program, the beneficiaries of RESPs are eligible to makewithdrawals from their RESP savings, which include contributions to the RESP, investmentreturns on these contributions, and additional federal and provincial education saving incentives,which I describe in sections 3.2.2 to 3.2.4. When withdrawn, earnings on contributions aretaxable, but they are treated as income to the beneficiary in the year of withdrawal (Employmentand Social Development Canada, 2015). Most full-time students do not pay any income taxeson these amounts because of the typically low income they obtain from other sources and theincome tax credits they are entitled to as students (Milligan, 2005).Qualifying educational programs include those offered by colleges, CEGEPs, trade schools, col-leges and universities.59 These programs may be full-time or part-time. Where the beneficiary ofthe RESP chooses not to pursue post-secondary studies, another beneficiary may be designatedwithout any tax consequences if the replacement beneficiary is a sibling under the age of 21 (Em-ployment and Social Development Canada, 2015).60 Alternatively, the contributor to the RESPmay withdraw savings from the RESP if the beneficiary is 21 years or older or if the RESP wascreated at least 10 years prior to this withdrawal. The withdrawals on investment earnings arethen treated as taxable income to the contributor and are subject to a 20% additional penaltytax (Knight, Waslander and Wortsman, 2008). Since 1998, assets in RESPs have grown consid-erably over the years, reflecting their increasing popularity. In 2012, the total value of assets inRESPs in Canada reached $35.6 billion (Employment and Social Development Canada, 2014b).This increase in take up is more than likely mainly due to the federal government’s introduction58From 1998 to 2006, RESP annual contributions were capped at $4,000 in addition to being subject to amaximum lifetime contribution limit of $46,000. As of 2007, there are no annual contribution constraints and thelifetime contribution limit is $50,000 per beneficiary (CESP user guide 2015).59CEGEPs are publicly-founded colleges in the province of Quebec. The acronym CEGEP stands for “Collèged’enseignement général et professionnel”, which translates in English to “General and Vocational College”. Theyoffer either a pre-university 2-year program required for entry in university or a 3-year vocational program.60Parents who have more than once child may choose to contribute to a family RESP plan instead of multipleindividual RESP plans. Any beneficiary named in the RESP may use the earnings and publicly offered grantsand bonds (such as the CESG, the A-CESG and the CLB) accumulated in the family plan. The possibility oftransferring RESP funds between siblings without penalties mitigates the risk of losing the amounts obtainedthrough the various government programs if, for instance, one child in the household chooses not to pursue apost-secondary education degree.673.2. Institutional Background: Education Saving Incentive Programs in Canadaof education saving incentives, which are described in the next section.3.2.2 The Canada Education Savings Grant (CESG)In 1998, the Canadian government introduced the Canada Education Savings Grant (CESG)in order to encourage the use of RESPs for post-secondary education savings. The CESG is amatching rate equal to a percentage of the contributions made to the RESPs of beneficiaries aged17 years or less. In order to receive the grant, the beneficiary of the RESP must be a Canadianresident at the time of the contributions to the RESP, must have a social insurance number, andmust be aged 17 years or under (CESG user guide 2015). The CESG includes both the basicCESG grant, which has been available to all Canadian children since 1998, and the additionalCESG (A-CESG), which was introduced in 2005 for low- and middle-income families. The basicCESG is equivalent to a 20% matching rate on contributions. The annual limit in contributionseligible for the basic CESG was $2,000 between 1998 and 2006 and increased to $2,500 in 2007,which remains the current annual limit today.61 Grant room (unused basic CESG amounts)accumulates for a child until the end of the calendar year in which the child turns 17, even ifthe child is not a beneficiary of an RESP. Unused basic CESG amounts can therefore be carriedforward for possible use in future years (Employment and Social Development Canada, 2015).For contributions made as of January 1, 2005, the additional CESG (A-CESG) provides anadditional 10% or 20% matching rate on the first $500 invested yearly in the child’s RESPdepending on their family income (see Table 3.1). In addition to the 20% matching rate offeredby the basic CESG to everyone, children from low-income families are eligible for an extra 20%matching rate, while those from middle-income families are eligible for an extra 10% matchingrate. Yearly RESP contributions beyond the first $500 or contributions to RESPs of children fromhigher income families are only eligible for the 20% basic CESG. Unused A-CESG amounts cannotbe carried forward for use in future years. The maximum lifetime CESG amount, including thebasic CESG and the A-CESG, that a beneficiary can receive is $7,200 (Employment and SocialDevelopment Canada, 2015). Approximately 70% of families were eligible for the A-CESG eachyear since the introduction of this grant in 2005 (Employment and Social Development Canada,2014a).3.2.3 The Canada Learning Bond (CLB)In 2004, the Canadian government introduced an additional incentive to encourage savings forpost-secondary education among modest-income families: the Canada Learning Bond (CLB).61The great majority of RESP beneficiaries have annual amounts of RESP contributions below the cap oncontributions eligible for the basic CESG. This limits the scope of the analysis if I were to attempt to measurethe effect of this increase in contribution limit on parents’ saving behaviour. I therefore chose not to exploit thischange in the program to study parents’ saving behaviour in this paper.683.2. Institutional Background: Education Saving Incentive Programs in CanadaUnder this policy, the Government of Canada makes a $500 contribution to the RESP of eachchild of eligible families during the first year. The child also receives $100 per year for eachsubsequent year he or she remains eligible, up to the age of 15 years for a lifetime maximumcontribution of $2,000. To be eligible, the child must be the beneficiary of an RESP account, thechild must have been born as of January 1, 2004, and the primary caregiver of the child mustreceive the National Child Benefit Supplement, which, in 2012, applied to families whose netannual income was $42,707 or less.62 The CLB may be obtained retroactively, in which case itsamount would depend on the number of years of eligibility of the child. With the exception of thebasic CESG grant which applies to all RESP holders, all other saving incentive programs – theA-CESG, the CLB, and the provincial programs – require that RESP contributors apply for them(Employment and Social Development Canada, 2015, 2013).Overall, the Canada Education Savings Program, which includes the Canada Education SavingsGrant (CESG) and the Canada Learning Bond (CLB), is one of the main programs to supportpost-secondary education in Canada. In 2012, CESG and CLB payments totalled $852 million(Employment and Social Development Canada, 2014b). In comparison, the Canada Student LoanProgram paid out a total of $698.2 million in grants and forgiven student loans in the 2012-2013academic year (Employment and Social Development Canada, 2014b). Table 3.2 presents therecent performance of the CESG and CLB programs. Among all education saving incentivesoffered to RESP contributors, the CESG is Canada’s principal program. It is important bothin terms of population participation rates and public costs. As of December 31, 2012, 45.4%of Canadian children had received the CESG through an RESP compared with 39.7% in 2008.The Government of Canada contributed approximately $7.2 billion in CESG to the RESPs ofCanadian children since the program’s inception in 1998. In 2012 alone, the Government ofCanada paid out $753 million in CESG. Although receiving the CLB subsidy does not requireany contributions to the child’s RESP and is thus free of cost, the take up rate of this programhas been relatively low among eligible children. In 2012, only 27.5% of eligible children hadreceived the CLB, which is still significantly higher than the CLB participation rate of 16.3%in 2008. In 2012, the government of Canada paid $99 million in CLB to reach a total cost of$398 million dollars since the program was introduced in 2004 (Human Resources and SocialDevelopment Canada, 2009, 2011; Employment and Social Development Canada, 2014b).3.2.4 The Alberta Centennial Education Savings (ACES) PlanIn 2005, the Alberta provincial government introduced the Alberta Centennial Education Savings(ACES) Plan to further encourage Albertan families to save for their child’s post-secondary62For children whose primary caregiver is a public agency, the child is eligible for the CLB if the agencyreceives payments under the Children’s Special Allowances Act (CSAA) for a child in care (Employment andSocial Development Canada, 2015)693.3. Theoretical Saving Models and Predictionseducation.63 As part of this program, the Alberta government contributes $500 to the RESP ofchildren born or adopted by its residents as of January 1, 2005. To receive the grant, parentsmust apply for the initial $500 ACES grant before the child’s sixth birthday. Furthermore,a $100 Alberta Centennial Education Savings (ACES) Grant is available for students enrolledin an Alberta school (or homed-schooled for their primary school education) who received acontribution the year before and who have turned 8 years, 11 years or 15 years in 2005 or later(Employment and Social Development Canada, 2015). Currently, according to the governmentof Alberta, the annual cost of the program is approximately $19 million (Government of Alberta,2015).3.3 Theoretical Saving Models and PredictionsThere exist many theoretical frameworks that attempt to explain why and how individualsgenerally accumulate savings. Three important models are: i) the neoclassical life-cycle model,ii) the fixed-goal saving model, and iii) the procrastination saving framework, each of which Iwill describe in turn.3.3.1 The Neoclassical Life-Cycle Saving ModelThe standard neoclassical life-cycle saving model was first proposed by Modigliani and Brumberg(1954).64 According to this model, agents are forward-looking, risk averse and have stable time-consistent rational preferences. They optimise their consumption and savings in order to “smoothconsumption” over their life-cycle; in other words, agents want to equalise their marginal utilityof consumption across periods. This generally means that individuals will save more whentheir income is high, expected returns to savings are high, and their consumption needs are low(Bernheim, 2002; Attanasio and Wakefield, 2008; Madrian, 2012).Under this framework, if the expected returns to savings rise (e.g., if there is an increase in amatching rate on contributions), there are two competing effects on savings: a substitution effectand an income effect. The substitution effect is caused by consumption in the future becomingless costly relative to present consumption; in this way, individuals will tend to save more in thepresent in order to consume more in the future. The income effect arises from individuals nowhaving a higher expected lifetime income, thereby causing an increase in consumption across63The Alberta Centennial Education Savings (ACES) Plan will be terminated in the 2015-2016 fiscal year. Allchildren born after March 31, 2015 will no longer be eligible for the program (Government of Alberta, 2015).64Another well-known neoclassical theory of saving is the Permanent Income Hypothesis (Friedman, 1957),which assumes that long-term income is the primary determinant of consumption. Under this theory, householdswill respond to changes in permanent income (the present value of lifetime income), but not transitory income(difference between current income and permanent income). The implications of this model are similar to thelife-cycle model (Beverly and Sherraden, 1999; Crossley, Emmerson and Leicester, 2012).703.3. Theoretical Saving Models and Predictionsall time periods and lowering current savings. The overall effect of an increase in returns onindividual contributions to a savings account is therefore ambiguous and depends on the relativemagnitude of the substitution and income effects (Bernheim, 2002; Attanasio and Wakefield,2008; Madrian, 2012). In the case of a money transfer at one point in time, however, the life-cycle model predicts that overall savings will increase. For example, if an individual is offereda lump-sum subsidy when opening an education savings account, this increases present income,and one would therefore expect both savings and consumption to increase in all future periods.In this case, the parents’ contributions to the account would decrease somewhat (to reflect anincrease in consumption), but overall savings (including the subsidy) would increase. Also, themodel assumes that there are no information or adjustment costs, and therefore everyone shouldrespond to incentives. This assumption also implies that, in theory, everyone should save andconsume in every period and thus saving incentives should affect neither the timing of savingcontributions nor the timing of when individuals begin to save (Bernheim, 2002).If we relax the assumption that everyone saves in every period, the theoretical impact on savinglevels of an increase in returns to savings is ambiguous for people who were already accumulatingsavings, but is unambiguously positive for those who were not saving prior to this increase.We would thus expect a positive impact on participation in a savings plan adding matcheson contributions or increasing the matching rate (Madrian, 2012). We would also expect anincrease in participation following a government transfer to a savings plan due to a pure incomeeffect. In evaluating how matching incentives affect individuals’ saving behaviour for retirement,the empirical evidence is mixed. The results of several studies suggest that matching ratescause higher participation in retirement saving plans (Choi et al., 2002; Choi, Laibson andMadrian, 2004; Duflo et al., 2006; Engelhardt and Kumar, 2007; Huberman, Iyengar and Jiang,2007; Madrian, 2012). A few studies demonstrated that, conditional on participation, matchingincentives increased contributions moderately, with this effect being generally more pronouncedfor high-income participants (Duflo et al., 2006; Engelhardt and Kumar, 2007; Madrian, 2012).Other studies, however, found no effects or a negative effect of matching incentives on retirementsavings (Kusko, Poterba and Wilcox, 1998; Mitchell, Utkus and Yang, 2007; Han and Sherraden,2009).To summarize, the theoretical implications of the life-cycle saving model generally seem consis-tent with individuals’ behaviour regarding the accumulation of precautionary lifetime savings orlong-term retirement savings.65 There are, however, three key differences between individualsaccumulating lifetime or retirement savings and parents saving for their children’s post-secondaryeducation. First, when parents save for their child’s post-secondary education, they are not sav-ing directly for themselves. Although some may argue that parents increase their utility from65Browning and Crossley (2001) present an overview of studies demonstrating that lifetime saving patterns canbe empirically explained by the predictions of this model; however, other empirical studies have found that certaincharacteristics of lifetime/retirement savings are inconsistent with the life-cycle saving model (see Bernheim (2002)for a summary).713.3. Theoretical Saving Models and Predictionsinvesting in their child’s human capital, not everyone may share this view: some degree of altru-ism or varying preferences across parents may explain variations in their behaviour. Second, thesaving horizon for education savings is quite specific, which can matter a lot in explain savingbehaviours (Fisher and Montalto, 2010). Saving for a child’s post-secondary education spans aperiod of approximately 18 years or less, depending on when parents start saving, whereas savingfor one’s retirement is usually subject to a much longer time frame and involves some uncertaintyrelated to the timing of the retirement decision. Third, compared to lifetime/retirement savings,which involve more unknowns, parents may have a better idea of how much they need to save fortheir child’s post-secondary education. In the case of education savings for their child, parentsmay have a fixed saving goal in mind or may use some kind of reference point or “rule of thumb”.3.3.2 Behavioural Economics Saving ModelsThe second and third saving models originate from behavioural economics, a more recent strandof literature that uses insights from psychology and economic experiments in order to better un-derstand economic decision-making (Mullainathan and Thaler, 2000). According to behaviouralsaving theories, there are many saving behaviour concepts to consider: bounded rationality, men-tal accounting, loss aversion and reference points, and issues of time-inconsistency and self-control(Mullainathan and Thaler, 2000; Choi et al., 2002; Benartzi and Thaler, 2007; Crossley, Emmer-son and Leicester, 2012; Madrian, 2012). These concepts stem from the idea that individualstend to take reasoning shortcuts when making decisions such as consumption or saving decisions,and these shortcuts may sometimes lead to suboptimal decision-making. As a consequence, in-stitutional features such as saving incentives, program characteristics, and the structure of thesaving choices available to individuals matter greatly in explaining people’s behaviour (Beverlyand Sherraden, 1999; Choi et al., 2002; Schreiner and Sherraden, 2007; Card and Ransom, 2011).For example, program design features such as opting-in versus opting-out of a program havebeen shown to have a tremendous impact on household saving choices (Choi et al., 2004; Carrollet al., 2009; Chetty et al., 2012). Another example could arise from parents viewing increases inpublicly offered incentives as a signal from the government underlying the importance of themsaving more for their child’s education. Certain incentives may also be seen as saving targets.For example, incentivised education savings accounts often offer matching rates on savings upto a maximum contribution amount and parents may perceive this limit as the optimal amountto save. These matching limits are sometimes referred to “threshold cues” (Choi et al., 2002,2012; Madrian, 2012). Certain incentives may therefore facilitate the development of rules-of-thumb for saving, which are not necessarily consistent with rational saving behaviour (Beverlyand Sherraden, 1999). In this way, relying solely on individuals being “rational agents”, as is thecase in the traditional life-cycle model, is not enough to explain their behaviour. Policies andinstitutions shape the costs, incentives, and consequences of saving decisions (Choi et al., 2002;Schreiner and Sherraden, 2007; Carroll et al., 2009; Han and Sherraden, 2009).723.3. Theoretical Saving Models and PredictionsThe Fixed-Goal Saving ModelAligned with the idea of using reference points or rules-of-thumb, the second saving frameworkconsidered in this paper thus focuses on the idea of fixed-goal savings and is sometimes referredto as the “Target Saving Model”. If individuals target a fixed amount of savings, as may be thecase for a child’s education savings, then there may be a “fixed-goal effect” at play. Accordingto this model, people wish to save a certain amount (no more, no less), and higher real interestrates, for example, simply allow individuals to reach their saving target with lower contributions(Berheim and Shoven, 1988; Samwick, 1998; Guha and Guha, 2008). Target saving behaviour isnot easily generated from standard utility functions; however, Guha and Guha (2008) show thatit can be modelled theoretically using specific time-varying values of risk aversion parameters.Using the 1992 Survey of Consumer Finances, Samwick (1998) presents some descriptive evidencethat certain consumers present a fixed-goal saving behaviour for explicit saving targets suchas a home purchase or family transfers, largely for their education. This result relies on thebehavioural economic assumption that individuals perform mental accounting (Thaler, 1990),implying that savings are not “fungible” and people mentally divide their income or assets intovarious categories.66In the education savings context, the fixed-goal model predicts that parents target a certainsaving goal to pay for their child’s higher education in the future. Higher returns to savings andpositive income shocks will decrease parents’ contributions by the additional income, therebykeeping overall savings constant. According to this model, one would thus expect lower con-tributions to a child’s education savings account in response to subsidies or higher matchingrates (resulting in constant overall savings) among those who a priori intended to save a cer-tain fixed amount. Assuming parents save following a rule-of-thumb (for example, by saving afixed amount each month to reach a specific long-term goal), additional saving incentives suchas lump-sum grants or higher matching rates should not affect when they begin to save or thetiming of contributions.The Procrastination Saving ModelThe final saving model that I consider in this paper focuses on time-inconsistencies and self-control behavioural concepts (Thaler and Shefrin, 1981; Benhabib and Bisin, 2005; Gathergoodand Weber, 2014). Certain individuals may procrastinate by consuming more today and savinglittle, with the assumption that they will save more in the future. Even among those with highlevels of savings, there is a strong tendency for individuals to wait until the end of the taxyear to make contributions to targeted savings accounts (Bernheim, 2002). One explanation for66In the neoclassical life-cycle saving model, money is assumed to be fungible. This “fungibility” assumptionimplies that money has no labels and individuals make no distinctions between the various components of wealthor expenditures (Thaler, 1990).733.3. Theoretical Saving Models and Predictionsthis procrastination behaviour is to model individuals’ actions using a hyperbolic time discountfunction instead of the standard constant discount rate (Laibson, 1998; O’Donoghue and Rabin,1999; Thaler and Benartzi, 2004; Caliendo and Findley, 2014). A hyperbolic discount functionimplies that preferences are dynamically inconsistent: people heavily discount the near future,but discount the distant future less. They thus perceive themselves as being more patient in thefuture than in the present, causing them to procrastinate.In the case of parents procrastinating with regards to saving for their child’s education, conferringa grant immediately when opening an education savings account could encourage them to openan account earlier and to commit to saving, thereby addressing the self-control/procrastinationproblem. In other words, a strong incentive in place early on may kick-start their savings, withthe hope that parents will continue to save regularly afterwards and end up contributing more totheir child’s education savings in the long run. Education savings accounts with such incentivesshould therefore help parents act according to their “true” long-term preferences by encouragingthem to begin saving immediately (Benhabib and Bisin, 2005; Crossley, Emmerson and Leicester,2012). In this way, according to the procrastination saving model, an initial grant when openinga savings account will thus cause savers to open the account earlier and to contribute more tothe account over time, thereby increasing total lifetime savings. Under this model, an initiallump-sum grant would not affect the frequency of contributions since parents are only requiredto apply for the grant at one point in time when creating the account. Matching rates onyearly contributions up to a certain maximum amount should also increase contributions bycreating a yearly reminder or yearly commitment mechanism. We would therefore expect yearlycontributions and possibly the frequency of these contributions to increase because of the strongincentives for individuals to commit to saving regularly (Madrian, 2012).67The life-cycle saving model, the fixed-goal saving model, and the procrastination saving frame-work have distinct predictions with regards to the potential effects of different saving incentives.Furthermore, people’s response to saving incentives may be heterogeneous across certain char-acteristics, notably across income groups (Beverly and Sherraden, 1999; Dworak-Fisher, 2008;Chetty et al., 2012). As previously mentioned, there is a large literature on retirement savingsthat has demonstrated that tax incentives, matching rates, contribution limits, and other formsof subsidies can strongly influence people’ saving behaviour (Choi et al., 2002; Milligan, 2003;Saez, 2009; Burman et al., 2012). There is also strong evidence that other institutional factors,such as default rules, commitment mechanisms, financial education and framing effects may havean even larger effect on people’s retirement saving behaviour than traditional saving incentives(Carroll et al., 2009; Choi et al., 2002; Duflo et al., 2006; Crossley, Emmerson and Leicester, 2012;Madrian, 2012). Little is known, however, about the effects of saving incentives in the context ofeducation savings. Evaluating the responses of individuals to various education saving incentives67In the case of the A-CESG, this effect could be reinforced by the fact that this additional matching ratecannot be carried forward from one year to the next if it is not used.743.4. Datawill therefore contribute to the literature by assessing which framework seems to best capturethe saving behaviour of parents for their child’s post-secondary education. In particular, in thisstudy, parents’ saving behaviour is characterised by the amounts of contributions and resultingtotal savings in education savings accounts (including subsidies and matching funds), parents’decision regarding when to open the account, as well as the frequency of their contributions.Specifically, I exploit the introduction of three Canadian education saving incentive programsto study how parents react to subsidies and higher matching rates on contributions. Table 3.3summarises the hypotheses that can be drawn and empirically tested from each theoretical sav-ing model in this context. Furthermore, some of the Canadian education saving incentives aretargeted specifically at low-income households, which will allow the analysis of parents’ savingbehaviour among this group, members of which are generally less likely to accumulate savings(Beverly and Sherraden, 1999; Dynan, Skinner and Zeldes, 2004; Duflo et al., 2006).3.4 DataThe empirical analysis is based on data from the administrative database of the Canada Ed-ucation Savings Program (CESP), a program run by the Employment and Social DevelopmentCanada Department of the Government of Canada. This administrative dataset provides preciseinformation on savings in RESPs of all Canadian RESP holders between 1998 and 2012. Inparticular, the database identifies each beneficiary’s gender, postal code, urban/rural living area,province, date of birth, the timing and size of contributions to RESPs over the years, as wellas the grants and bonds allocated to the eligible children. The downside of using this admin-istrative dataset is that it only contains information on the beneficiaries of RESPs and not onchildren without RESP accounts. Also, it is important to note that the database contains noinformation on education savings in vehicles other than RESPs, nor on the household incomeof RESP beneficiaries, which limits the extent of the analysis. I discuss these limitations andpossible solutions to address these concerns in section 3.6.2. For the purposes of this study, Iuse a 10% random sample of all Canadian beneficiaries of RESPs aged 17 or less as of July 1,2012.68 The final sample size is 466,423 RESP beneficiaries.I measure the four dependent variables examined in the empirical analyses in the following way:i) savings correspond to total RESP savings including contributions as well as all grants andbonds,69 ii) contributions correspond to the total amount deposited in the RESP account bythe contributors, iii) the amount of time before opening an account is measured by the age of68A 10% random sample was used instead of the entire database due to hardware limitations. Twenty childrenwere considered outliers because they had yearly contributions to their RESP account of more than $20,000. Theywere excluded from the final sample.69Specifically, the value of RESP savings includes RESP personal contributions as well as all government offeredincentive amounts from the CESG, the A-CESG, the CLB and the ACES grant. RESP savings do not, however,include investment earnings such as interest or dividends.753.4. Datathe beneficiary when the RESP account was opened, and iv) the frequency of the contributionscorresponds to the total number of contributions since the RESP account was opened.70 Allof these variables are measured conditional on having an RESP account on July 1, 2012, sincethe data provides no information on children without RESPs. For simplicity, throughout thepaper, I refer to parents as the contributors of RESPs, but other individuals, such as friends orother relatives, may also contribute to a child’s RESP. This simplification does not affect theinterpretation of the results of the paper.Tables 3.4 and 3.5 present a breakdown of the value of these saving outcomes by calendar yearand by year of birth of the beneficiary respectively. Total contributions, total savings, andtotal number of contributions are adjusted for the age of the beneficiary by dividing their valueby the age of the child.71 Contributions and savings are expressed in constant 2002 dollars.72Conditional on having an RESP account, contributions, savings, and the number of contributionshave increased steadily over time, whereas the average age of the child at the creation of theRESP account has declined over the years (see Table 3.4). Generally, after adjusting for theirage, younger children tend to have higher contributions, higher savings, and a larger number ofcontributions (see Table 3.5). Figures 3.1 and 3.2 show the evolution of yearly contributions andyearly savings as children age by birth cohort. For every birth cohort, both yearly contributionsand yearly savings increase as children age. It is also clear from both graphs that children inmore recent cohorts have higher average levels of yearly contributions and higher savings at everyage.73 Among all RESP beneficiaries aged 17 or less in 2012, average lifetime contributions were$8,178, and average overall savings were $9,920. These amounts were marginally lower in Alberta:$8,046 and $9,857 respectively. Tuition costs vary substantially across provinces in Canada. Forthe 2012-2013 academic year, the average cost of tuition for a full-time undergraduate studentwas $5,581 in Canada, but this ranged from $2,520 in the province of Quebec to $6,815 in theprovince of Ontario. The average undergraduate tuition fees in Alberta, $5,663, were quite closeto the Canadian average (Statistics Canada, 2012e)70These definitions generally hold throughout the paper except when measuring the impact of the A-CESGon parents’ saving behaviour. In that case, I study yearly amounts of contributions, savings and number ofcontributions instead of lifetime amounts.71I divide these values by the age of the child instead of dividing them by the number of years elapsed sincethe creation of the child’s RESP to take into account the absence of RESP savings before the child’s RESP wascreated. It is important to note, however, that I only have data on savings in RESPs as of 1998.72The nominal values were adjusted for inflation using a province specific CPI index based on a basket of generalconsumption goods (Statistics Canada, 2012d).73One noticeable pattern in Figures 3.1 and 3.2 is the flattening of the RESP contribution and saving trendsacross the majority of cohorts (except the 1998 cohort). For each cohort, the trend starts to flatten at theage of the child corresponding to the years 2008 and 2009, which coincide with a Canadian recession. Furtherinvestigation would need to take place to confirm that the recession was indeed the cause of this marked reductionin the growth of RESP contributions.763.5. Empirical Strategy and Results3.5 Empirical Strategy and ResultsTo evaluate the effects on parents’ saving behaviour in RESPs of an initial subsidy or highermatching rate on contributions, I take advantage of the introduction of three saving incentivepolicies in Canada: the ACES, the CLB, and the Additional CESG programs. Specifically, tomeasure the effects of these programs on the four saving behaviour outcomes, I exploit the preciseeligibility rules of each program. I estimate the impact of the ACES and the CLB on lifetimesavings, lifetime contributions, total number of contributions, and the age of the beneficiarywhen opening an RESP account using a regression discontinuity design. I measure the impact ofthe A-CESG on yearly savings, yearly amounts contributed and yearly number of contributionsby exploiting the longitudinal structure of the data and using an individual fixed effect model.Sections 3.5.1 and 3.5.2 describe the empirical approach I employ as well as the empirical resultsI obtain when measuring the effects of each program.743.5.1 Subsidy Conditional on Opening an AccountI first examine the effects of offering a grant conditional on opening an RESP on parents’ savingbehaviour. The ACES subsidy, which was offered to all residents of Alberta regardless of income,allows the measurement of its overall effects among children of all family income levels. Incontrast, the CLB, which was offered in every province, but only to low-income families, allowsthe examination of the effect of the grant on this subgroup of the population.Overall Effects on Saving Behaviour: Evidence from the Alberta CentennialEducation Savings (ACES) Initial GrantFirst, to estimate the effect of the ACES initial grant on various saving outcomes, I use a sharpregression discontinuity (RD) design based on the beneficiary’s date of birth (measured in thenumber of days since January 1, 2005). The main idea of the RD design is that assignment totreatment is determined completely by the value of a specific variable (referred to as the “forcingvariable”) being on either side of a fixed threshold. In this case, treatment is defined as beingeligible for the ACES $500 initial grant, and the forcing variable is the date of birth of thechild since only children born on or after January 1, 2005 are eligible for the grant. The forcingvariable may be correlated with the outcome of interest, but the relationship between both ofthese variables is assumed to be continuous. For example, savings in RESPs tend to increaseas children grow older, but there is no reason to believe that this increase is discontinuous at74Unfortunately, I was unable to identify siblings in the dataset due to data limitations and the high costs ofmatching children by home address. I therefore measure the effect of each saving incentive program on the savingoutcomes associated with each individual RESP beneficiary instead of the outcomes measured at the family level.As a result, I cannot exploit within family variations in program eligibility.773.5. Empirical Strategy and Resultsany specific date of birth. If there is a discontinuity in the dependent variable at the threshold(January 1, 2005 in this case), we can interpret this as evidence of the causal effect of thetreatment (Imbens and Lemieux, 2008). The average treatment effect of the ACES grant onoutcome Y is given by:TE = limd↓0E [Y |d]− limd↑0E [Y |d] (3.1)In equation 3.1, d denotes the number of days separating the date of birth of the child and January1, 2005. I estimate the two limits on the right-hand side using a local (linear or quadratic)polynomial regression, allowing for different polynomials on either side of the threshold (i.e.,using a spline).75 Equation 3.2 presents the local linear regression used to measure the effectof the ACES initial grant on the dependent variable, which is estimated by the coefficient δ onthe treatment variable. This regression model is estimated using only observations for whichd ∈ (−h, h) where h is the size of the rectangular kernel bandwidth used. In other words, thebandwidth is the span of days on either side of January 1, 2005 (d = 0), the date of introductionof the incentive.Yi = β0 + β1d+ δTREATid + γd · TREATid + εi (3.2)where TREATid =1 if child i is born on January 1, 2005 or later (d ≥ 0)0 if child i is born earlier than January 1, 2005 (d < 0)In equation 3.2, i denotes the child and d denotes the number of days separating the date ofbirth of the child and January 1, 2005. Also, Yi is the dependent variable, TREATid is thebinary treatment variable indicating if the child is eligible for the program or not (i.e., if thechild is born as of January 1, 2005 or not), and εi is the error term. A local linear regressionprovides a nonparametric way of consistently estimating the treatment effect in an RD context,which is estimated by the parameter of interest δ. Although a linear regression specification isused, the results are consistent for any arbitrary and unknown shape of the relationship betweenthe outcome variable Y and the running variable d (Lee and Lemieux, 2010). The size of thebandwidth h, however, matters greatly for the estimation. A larger bandwidth increases theprecision of the estimates due to the increased sample size, but a smaller bandwidth reduces thepotential bias of the estimates by relying solely on observations that are very close to the pointof discontinuity. Keeping the bandwidth sizes relatively small to emphasise the “local” aspect75The RD design requires a regression estimation at the threshold point, thereby causing a “boundary problem”when using non-parametric standard kernel regressions, potentially resulting in biased estimates. One solution tothis problem is to use a local linear regression estimated on observations very close to the cut-off point to reducethe importance of the bias (Hahn, Todd and der Klaauw, 2001; Lee and Lemieux, 2010).783.5. Empirical Strategy and Resultsof the estimation, I vary the size of bandwidth in different specifications of the regression toensure that the results are robust to this choice (Lee and Lemieux, 2010).76 To further test thesensitivity of the results, I also estimate a quadratic local polynomial regression specification,which is presented in the next equation.77Yi = β0 + β1d+ β2d2 + δTREATid + γd · TREATid + λd2 · TREATid + εi (3.3)where TREATid =1 if child i is born on January 1, 2005 or later (d ≥ 0)0 if child i is born earlier than January 1, 2005 (d < 0)The intuition behind the regression discontinuity identification strategy is that individuals closeto the threshold are quasi-randomly assigned as being eligible for treatment or not. Just assubjects in control and treatment groups in randomized experiments should have similar baselinecharacteristics, this should also be the case for children born immediately before and after thethreshold. For example, there is no reason to believe that children born before and after acertain date in Canada differ systematically with regards to province, gender, or rural/urbanclassification. One approach to provide evidence for this is to verify that characteristics of children(in this case province of origin, gender, and rural/urban classification) are the same for thoseborn before and after the threshold date; however, because the database only contains recordsfor children with RESP accounts and because the policies in place (e.g., the ACES programs)may affect RESP participation rates and therefore whether children are in the database, I cannottest for this without having data on the entire population of children in Canada.To interpret the RD estimates as the causal effect of the ACES subsidy, one must assume that,in absence of the program, the distribution function of the dependent variable conditional on theforcing variable is continuous at the threshold (Imbens and Lemieux, 2008). I gather evidence onthis by examining the relationship between the saving outcomes and the date of birth of the childin the rest of Canada, a natural control group since the policy only applies to Alberta. If there areno discontinuities in the rest of Canada, we can be fairly confident that any discontinuities at theJanuary 1, 2005 threshold in Alberta are caused by the implementation of the ACES program.Furthermore, the RD estimate also relies on the assumption that parents cannot manipulatethe date of birth of their child. In particular, I need to assume that certain parents did not,for example, postpone the birth of their child to be eligible for this policy or move to Albertafrom another province only to benefit from this particular policy. Although these behaviours are76I chose h = 100 as the optimal bandwidth. This value is close to the estimated bandwidth value obtained fora sharp RD design based on the technique developed by Imbens and Kalyanaraman (2012). I then also estimatedthe model on half the size (h = 50) and double the size (h = 200) of this bandwidth.77I use a local linear or quadratic polynomial in the RD estimation framework since estimators of causal effectsusing high-order polynomial regressions may be misleading due to poor inference properties (Gelman and Imbens,2014).793.5. Empirical Strategy and Resultspossible, they are fairly unlikely since the program was announced during the Alberta Speechfrom the Throne on February 17, 2004, a little more than nine months before the implementationof the program, giving people little time to modify their plans (Government of Alberta, 2004).Table 3.6 presents the RD estimates of the effects of the ACES initial grant in Alberta onfour saving outcomes: total savings, total contributions, the age of the child when their RESPaccount was created, and the number of transactions per year, all of which are conditional onhaving opened an RESP account. Columns 1 to 3 of the table present the RD results using alocal linear specification and various bandwidth sizes, whereas columns 4 to 6 present similarresults obtained using a quadratic specification. For example, the first column presents theresults obtained using a local linear regression for children born in the interval consisting of 50days before and after January 1, 2005. Panel A presents the results of the RD regressions forAlberta (treatment group), whereas panel B presents the results of the same regressions for therest of Canada (control group).The results suggest that the presence of the ACES initial grant in Alberta had a large negativeeffect on the age of the child when opening the RESP account, but no significant effect on lifetimesavings, lifetime contributions, or the number of contributions to the RESP account. Childrenincluded in the regression were born around January 1, 2005, making them 7 years old in July2012 (when outcomes were measured). On average, the ACES grant reduced the age at whichchildren obtained an RESP account by approximately one year, which constitutes a reduction of43%. That there is no such effect for RESP beneficiaries in the rest of Canada further validatesthe causal negative effect of the Albertan program on the age at which the RESP accounts wereopened. Figure 3.3 plots the average age at which RESP accounts were opened against thedate of birth of the child for Alberta and the rest of Canada. The two graphs also presents thelinear trend on either side of the January 1, 2005 threshold to help visualise whether there is adiscontinuity in the trend. There is a clear jump at January 1, 2005 in the case of Alberta, but nosuch discontinuity in the rest of Canada, graphically confirming the causal impact of the ACESgrant on the timing of the RESP account opening. Figures 3.4 to 3.6 present the relationshipbetween a beneficiary’s date of birth and total RESP contributions, total RESP savings, andnumber of contributions respectively. Although some of these figures seem to suggest a slightdiscontinuity at the cut-off date of birth in the case of Albertan RESP holders, the effects aretoo noisy to be statistically significant.78 In Figures 3.3 to 3.6, the trends for the age of thechild at RESP creation, RESP contributions, and RESP savings are decreasing as the date ofbirth of the child becomes more recent. These downward-sloping trends are to be expected since,78In the case of the graphs showing the relationship between saving outcomes and the date of birth of thebeneficiary for non-Alberta residents, the linear trend on the left hand side of the threshold seems to be system-atically marginally higher than the trend on the right hand side of the threshold. This apparent discontinuityis, however, statistically insignificant regardless of the model specification (linear or quadratic local polynomial)and the choice of the kernel used (uniform or triangular), suggesting that the absence of an effect in the rest ofCanada is a robust result (see Table 3.6 and Table C.2 in Appendix C).803.5. Empirical Strategy and Resultsgenerally, younger children (with more recent dates of birth) tend to have smaller amounts ofcontributions and thus less savings, as well as a lower average age at RESP creation comparedto older children.In theory, if the assumptions for the RD design hold, there is no need to add control variablesother than the forcing variable in the regression, as an RD estimation can be seen as a quasi-natural experiment that is “as good as randomized” in the local neighbourhood of the threshold.In practice, adding additional covariates to the basic RD specification may increase the precisionof the estimate without changing the identification strategy (Imbens and Lemieux, 2008). I findthat the estimates are robust to the inclusion of the following control variables: gender, medianfamily income in the household’s geographic area, and rural/urban living area classification(Table C.1 in Appendix C).79,80 Furthermore, the results are also very similar when using atriangular kernel instead of a rectangular kernel in the local linear regression estimation. (TableC.2 in Appendix C).81To further understand the impacts of the subsidy, I next examine whether there were any effectsof the ACES grant on parents’ decision to start saving in an RESP. To measure the effectsof the grant on this extensive margin, I estimate the RD model on the proportion of childrenin the database residing in Alberta. This strategy relies on the assumption that there was nodiscontinuous enrolment of children born before and after January 1, 2005 in other provinces,which is likely to hold since no other saving incentive programs were introduced based on thiscriterion. I find a significant increase in the proportion of RESP beneficiaries residing in Albertaborn as of January 1, 2005 (Figure 3.7 and Table 3.7). The most conservative estimates suggesta 2.2 percentage point increase in RESP take up due to this policy, which represents a sizeable18% increase, compared with the proportion of RESP beneficiaries residing in Alberta before thepolicy was introduced (11.7%).82 The policy therefore caused more parents to open RESPs fortheir children, and they did so much earlier in their child’s life. These new RESP beneficiaries,79The limited information on children’s and parents’ characteristics in the database restricts the nature of thecontrol variables that I can include in the analysis. For example, there is evidence that Canadian immigrantfamilies are approximately 8 percentage points more likely to use RESPs than non-immigrant families (Milligan,2005), but due to data limitations, I cannot control for immigrant status in the analysis. In theory, however, thedistribution of immigrant families should be smooth at the threshold used in the RD design, thereby not affectingmy results.80Because I do not have information on each child’s family income in the database, I use the median familyincome in the household’s geographic area from the 2006 Canadian Census as a proxy for family income. Thegeographic unit used is the “forward sorting area” (FSA), which is defined by the first three digits of a household’spostal code. Canada is divided into 1,577 FSAs. In 2006, the number of families per FSA varied between 65 and38,720 with an average number of families of 5,563 Statistics Canada (2006).81Fan and Gijbels (1996) have demonstrated that a triangular kernel is optimal for estimating local linearregressions at the boundary. In practice, however, using a triangular kernel involves estimating a weightedregression (instead of an un-weighted regression when using a rectangular kernel), which weighs observationsclose to the cut-off more heavily. Reducing the size of the bandwidth when using a linear kernel produces thesame effect (Lee and Lemieux, 2010). I nevertheless include the triangular kernel regressions for completeness.82For this calculation to be correct, the proportion of Albertan births relative to other Canadian provincesmust have remained relatively constant between July 2004 and July 2005, which was the case (Statistics Canada,2012b).813.5. Empirical Strategy and Resultshowever, do not seem to benefit on average from significantly different contributions or savingsthan their peers who were not subject to this $500 subsidy. This absence of a significant impact,however, could also be the result of a composition effect. It could be the case, for example, thatparents who were induced to open an RESP because of the ACES saving incentive contributeless to their child’s RESP than parents of recipients of the ACES grant who would have usedRESP regardless of the grant being offered, resulting in a net zero effect. It could also simplybe the case that the variance of the estimates is too large to detect an effect on the amount ortiming of contributions.Effects on the Saving Behaviour of Low-Income Families: Evidence from theCanada Learning Bond (CLB)To examine whether the impact of a subsidy differs for children from low-income families, I nextexamine the effects of the CLB on parents’ saving behaviour. To be eligible for the subsidy,children from low-income families must be born on or after January 1, 2004. Since the datadoes not provide any information on the income levels of RESP contributors, it is not possibleto identify with precision the group of low-income families targeted by the CLB. To addressthis problem, I perform the analysis on the restricted sample of RESP beneficiaries who havereceived the 20% Additional CESG (A-CESG) at least once, implying that they have been inthe low-income group at least once since 2005. Since the low-income cut-off is the same for bothprograms, among this group, all children born as of January 1, 2004 were also eligible for theCLB. The fact that receiving the A-CESG is conditional on making contributions whereas theCLB is independent of whether parents contribute to the child’s RESP is not a major concernsince close to 95% of children who receive the CLB have positive RESP contributions (Table 3.2).I therefore use a sharp RD design based on the January 1, 2004 date of birth cut-off to estimatethe impact of the CLB on this subsample of children, which I will refer to as the “subgroupA-20”.There are, however, two issues to consider with this approach. First, the amount of CLB forwhich an individual is eligible depends on the number of years for which the child qualified (i.e.,the number of years for which the child’s family was under the low-income cut-off). Childrenare eligible for a $500 initial grant and a $100 for every year following this grant in which theyqualify for the program until age 15. This yearly qualification rule thus affects the intensity oftreatment as parents’ income may fluctuate over the years, thus affecting the number of years ofCLB eligibility for their child. Generally, income mobility among low-income families is relativelylow, thereby mitigating the importance of this issue. Among all children born in 2004 who hadbeen eligible for the CLB at least once by 2012, they were on average eligible for the CLB 79%of their life. Approximately half of the children were eligible for the CLB every year since birth.The second concern stems from the fact that not everyone who is eligible for the A-CESG823.5. Empirical Strategy and Resultsapplies for this grant, and therefore beneficiaries in the subgroup A-20 are only a subsampleof children from low-income families who are eligible for the CLB. This sample selection mayresult in a positive selection bias problem, where, for example, only those aware of the A-CESGor only keen individuals are included in the subgroup A-20. Keeping this important limitationin mind, the results are nonetheless informative of the saving behaviour among parents whoare aware of the programs targeted at low-income families and who apply for them. The RDresults should thus be interpreted as estimates of the average treatment effect among that specificpopulation and not the average treatment effect among all children targeted by the policy (i.e.,children in low-income families). These two treatment effects may be very different. In 2012, thetake-up rate of the A-CESG among all eligible children in Canada was 28.1%. Among RESPbeneficiaries who received the basic CESG and who were eligible for the A-CESG, only two-thirdsof children applied for this additional grant, suggesting that a third of parents may not be awareof the program (Employment and Social Development Canada, 2014a). Similarly, 27.5% of allCanadian children eligible for the CLB actually benefited from the program. (Employment andSocial Development Canada, 2014b). Among RESP beneficiaries, about 23% of eligible childrendid not apply for the CLB (Employment and Social Development Canada, 2014a). Although theparticipation rates of both programs are relatively low, they are also quite similar, suggestinga large overlap in participation. The RD estimation strategy relies on the assumption that, inabsence of the date of birth eligibility criterion for the CLB, all families who applied for theA-CESG would have also applied for the CLB. This assumption is likely to hold since bothprograms target the same low-income families and require parents to actively apply for them.Table 3.8 presents the results of the sharp RD regressions on the sample of beneficiaries whohave received at least once the 20% A-CESG matching rate by 2012, and who have thereforebeen in the low-income group (subgroup A-20). Children included in the regression were bornaround January 1, 2004, and were therefore 8 years old by July 2012. Among those not eligiblefor the CLB, the average age when opening an account is 3.5 years and their average lifetimecontributions to their RESPs are $5,600, which translates into average lifetime savings of nearly$7,000 when the incentives are included. The results demonstrate that, among the A-20 subgroup,the CLB reduced the average age at which the RESP accounts were opened by approximately6 months in addition to increasing both overall contributions and overall savings significantly.According to the most conservative estimates obtained, lifetime average contributions increasedby $686, whereas lifetime average savings increased by $1,704. Since the CLB offers $500 to everyeligible child when opening an RESP account and $100 for every following year the child is eligible,these estimates seem reasonable. I do not find evidence that the CLB affected the frequency ofcontributions to the RESP account of children in the A-20 subgroup. One explanation for thisresult is that many parents from low-income families enrol their children in RESPs offered bygroup scholarship providers. The use of these group scholarship plans is higher among the low-income population since the group scholarship plan companies actively target and recruit low-833.5. Empirical Strategy and Resultsincome clients (Knight, Waslander and Wortsman, 2008). In 2012, 35.1% of CLB payments weredone through group scholarship trust plans (Human Resources and Skills Development Canada,2012). These plans generally require fixed RESP contribution schedules, which may explainthe absence of an effect of the CLB on the frequency of contributions (Knight, Waslander andWortsman, 2008).Figures 3.8 to 3.10 present graphic representations of the discontinuities at January 1, 2004in the age of the child when opening the account, in savings, and in contributions, respectively.Confirming the regression estimates, there is a jump in the saving behaviour measured at January1, 2004 in all three cases, although the jump is sharper in the case of RESP savings and theage of the child when opening the account than for RESP contributions. Tables C.3 and C.4 inAppendix C present the results of the same RD regressions adding gender, rural/urban livingarea classification, median family income in the household’s geographic area, and province ofresidence as control variables, as well as using a triangular kernel in the local linear regression.In both cases, the results are very similar to the baseline estimates.Another estimation strategy to measure the effects of the CLB on parents’ saving behaviourwould be to use a fuzzy RD design on the entire population of RESP holders. A fuzzy RDdesign, as opposed to a sharp one, is used when the probability of being eligible for the programincreases significantly at the discontinuity threshold, but does not change exactly from 0 to 1at the threshold (Imbens and Lemieux, 2008). The idea behind the fuzzy RD design is to scalethe estimate obtained by the difference in probability of being eligible for the CLB before andafter the threshold. Due to the small percentage of children who qualify for the CLB in thepopulation (17.7% in 2012) as well as the even smaller take up rate of the CLB among them(27.5% in 2012), however, the results based on this approach were too imprecisely estimated tobe informative.83 Finally, because this program was introduced for all low-income children inCanada, I cannot measure the impact of the CLB on a child’s probability of having an RESPusing the same technique that I employed in the case of the ACES subsidy. The saving behaviourof parents induced to open an RESP due to the CLB may be different from the behaviour ofparents who would have used RESP regardless of the CLB being in place. I cannot disentanglethese effects due to the limitations of the data.Due to the potential for large gains that the CLB can provide to children’s RESPs at no financialcost to the parents (since the program is independent of contributions), one could wonder whythe participation rate of the program among eligible families is so low. Different explanations areplausible. First, not all parents from low-income families may be aware of the existence of theprograms. Second, although the programs do not require personal contributions from the parents,they may nevertheless incur time and psychological costs caused by having to apply for a socialinsurance number of their child, visit a bank or financial institution offering RESPs and complete83These statistics were provided or derived from the 2012 CESP annual review (Human Resources and SkillsDevelopment Canada, 2012).843.5. Empirical Strategy and Resultsan application form. Finally, the penalties on withdrawals for purposes other than paying forthe beneficiary’s post-secondary education may increase the risk associated with contributing toRESPs if parents are not certain that their child will eventually attend a university or college,or they feel they may need access to the funds for emergency purposes.84 Using another savingvehicle with no restrictions on withdrawals may be more appealing. One could thus explain thelow participation rate by the behavioural concept of “loss aversion”, which describes people’stendency to strongly prefer avoiding losses to acquiring gains (Kahneman and Tversky, 1979,1991).3.5.2 Increase in the Matching Rate on ContributionsAccording to the saving models considered in this study, parents’ response to an increase in thereturns to savings may be very different from their response to pure income shock such as asubsidy independent of contributions. I therefore evaluate next the effect of an increase in thematching rate on RESP contributions by exploiting the introduction of the A-CESG program in2005.Effects on the Saving Behaviour of Low- and Middle-Income Families: Evidencefrom the Additional Canada Education Savings Grant (A-CESG)The A-CESG program was implemented differently than the previous two programs examined.All contributions made to RESPs of children in low- and middle-income families in Canada as ofJanuary 2005 were eligible for the A-CESG, regardless of the date of birth of the child. Specifi-cally, since 2005, children of low-income families and middle-income families benefit respectivelyfrom a matching rate of 40% or 30% instead of the basic CESG 20% on the first $500 contributedeach year to their RESP. All subsequent contributions up to $2,500 per year are subject to thebasic CESG 20% matching rate. To measure the impact of the higher matching rate providedby the A-CESG, I estimate an individual fixed effect model exploiting the panel data structureof the observations. I restrict the sample to beneficiaries who opened an RESP prior to 2005,the year in which the A-CESG was introduced. The identification of the effects of the A-CESGtherefore relies on comparing for each child, the saving behaviour of his contributors pre- andpost-2005. I measure the impact of the A-CESG on yearly contributions, yearly savings, and theyearly number of contributions. I cannot measure the effect of the policy on the age of the childwhen opening the account since all accounts considered were opened prior to the policy beingintroduced.The idea behind using a panel data estimation approach is to control for individual heterogeneityof the contributors to the RESP accounts. We assume that the unobserved characteristics of each84It is, however, possible for parents to transfer RESP funds from one child to another, which reduces the risksomewhat in this context.853.5. Empirical Strategy and Resultschild, such as having parents that are well informed of policies or very responsive to incentiveprograms, are constant over time and controlled for using individual fixed effects.Yit = αi + δACESG20it + γACESG10it + β1ageit + β2age2it + λt + εit (3.4)Equation 3.4 presents the regression model estimated, where Yit is the dependent variable forchild i in year t, ACESG20it and ACESG10it are the binary treatment variables indicating ifthe child i received the A-CESG 20% or 10% rates respectively in year t. The specification alsoincludes linear and quadratic controls for the age of the child (in years), as well as individual fixedeffects, ai, and year fixed effect, λt, which capture year specific shocks to the saving behaviourof parents (common to all individuals in that year), such as changing economic conditions orincreases in the contributions limits subject to the basic CESG as of 2007. All dollar amountsare expressed in constant 2002 dollars.The effects of the additional 20% and 10% matching rates on the first $500 contributed are mea-sured by the coefficients δ and γ on the dummy variables ACESG20 and ACESG10 respectively.These effects, however, are measured on RESP beneficiaries who applied for the higher A-CESGrate as opposed to being measured on all RESP beneficiaries eligible for the program. Thisimplies that the coefficients δ and γ are capturing the average treatment effects on the treated(ATT) and selection into treatment is likely to be endogenous, for example, due to differences incontributors’ knowledge about the program.85 Among eligible RESP beneficiaries, the A-CESGtake up rate is approximately two-thirds (Employment and Social Development Canada, 2014a).With this limitation in mind, the effects of the 40% and 30% A-CESG matching rates on the first$500 invested per year in RESPs are presented in Table 3.9. I estimate that, among RESP holderswho applied for the program, the 10% A-CESG matching rate increased, on average, yearlycontributions by $188, yearly savings by $260, and the yearly number of contributions by 2.5.In comparison, the 20% A-CESG matching rate increased, on average, yearly contributions by$261, yearly savings by $385, and the yearly number of contributions by 2.3 among its applicants.Since the A-CESG is added to the basic CESG matching rate, the first $500 in contributions issubject to a 30% or 40% return, making the estimated effects on yearly savings relative to theones on yearly contributions reasonable.86 It may, however, be the case that only very specifictypes of parents in middle- and low-income families chose to save in RESPs and applied for the85If we define "treated” children as children who received the A-CESG, then following the literature on treatmenteffects (Angrist and Krueger, 1999; Imbens and Wooldridge, 2009), the estimates obtained measure the averagetreatment effect on the treated (ATT), that is the average impact of the A-CESG on eligible children who appliedfor the A-CESG. In this context, the average treatment effect (ATE) would be the effect of the A-CESG on alleligible children for the program.86If an increase of $188 in contributions due to the 10% A-CESG is subject to a 30% return (20% from thebasic CESG and 10% from the A-CESG), then one would expect an increase in total savings of 1.3×$188 = $244,which is close to $260. Similarly, an increase of $261 in contributions due to the 20% A-CESG would be subjectto a 40% return (20% from the basic CESG and 20% from the A-CESG), suggesting an increase in savings of1.4× $261 = $365, which is also very close to $385.863.6. DiscussionA-CESG. These parents may be much more responsive to higher matching rates than the averageparent in the subgroups of the population, causing a positive sample selection bias. If the sampleincluded the entire population of children (including those without RESP savings), the measuredeffects would likely be smaller in magnitude. These results should therefore be seen as an upperbound on the estimated effects. Nevertheless, the fact that the higher matching rate of 40%had a stronger effect on contributions than the 30% rate is quite remarkable since families thatbenefit from the highest matching rate also dispose of the lowest income.One concern may arise from the fact that the A-CESG was announced in March 2004, but onlyimplemented in 2005 for contributions made as of 2005 (Human Resources and Skills DevelopmentCanada, 2010). This could cause an overestimation of the effects of the A-CESG on contributionsif eligible parents stopped contributing to their RESP accounts to wait until 2005 to obtain ahigher match rate on their contributions. This behaviour would bias the effects of the programupwards. Figure C.1 in Appendix C presents a histogram of the number of contributions toRESP accounts, opened prior to 2005, that benefited from the A-CESG per thirty-day period in2004 and 2005. According to this figure, there is no evidence of a significant drop in the numberof transactions after March 2004. In addition, estimates are based on panel data spanning anumber of years around 2005 and therefore this anticipated effect, if present, should be mitigatedby averaging out effects over multiple years.3.6 Discussion3.6.1 Empirical Results Compared to the Model PredictionsBased on the estimated effects of the three saving incentive programs on the four outcomesexamined (see Table 3.10 for a summary), the majority of the results point to the behaviouralprocrastination saving model as being the most consistent with parents’ saving behaviour for theirchild’s post-secondary education, especially among low-income families. First, I find no evidencethat either the CLB or the ACES initial grant reduced contributions to the RESP accounts,which should be the case according to the life-cycle and fixed-goal models. The procrastinationmodel, however, predicts that these two subsidy programs should instead cause contributions toincrease (by creating a kick-start effect), which seems to be the case for low-income families whoreceived the CLB. RESP contributors from lower income families may respond more strongly toincentives compared to those in higher income families, thus explaining why the average effectof the ACES plan on all children in Alberta is not significant. The A-CESG higher matchingrate increased contributions, which is inconsistent with the fixed-goal model, but consistent withboth the procrastination model as well as the life-cycle model if we assume in the latter case thatthe substitution effect resulting from the higher matching rate is stronger than the income effect.873.6. DiscussionThe effects of the three programs on contributions are thus most aligned with the procrastinationsaving model predictions.The estimated effects of each program on overall savings are, however, somewhat contradictoryand inconsistent with one theory being the best explanation. I find no evidence that the ACESinitial grant had an effect on lifetime savings, which may be consistent with the fixed-goal savingmodel; however, that the ACES grant did not cause contributions to decrease significantly goesagainst this conclusion. At first glance, an absence of significant effects on both savings andcontributions seems contradictory, but this is likely caused by both estimates being very noisy.In addition, a $500 subsidy may seem like quite a small amount compared to average lifetimeRESP contributions and savings in Alberta, the province with the highest average family incomelevel in Canada (Statistics Canada, 2012c). Among the A-20 subgroup of beneficiaries, the CLBseems to have increased savings by more than the amount of the subsidy, a result that is onlyconsistent with the procrastination model. Finally, the A-CESG caused an increase in savingsamong those who applied for the program, which can be explained by both the procrastinationmodel as well as the life-cycle model (if the substitution effect outweighs the income effect).Lastly, the life-cycle and fixed-goal models predict no effect on the timing of the account creationor frequency of contributions to the account. That I find that certain saving incentives had largeimpacts on these two dimensions is therefore aligned with the procrastination saving model.According to this model, an initial subsidy when opening the savings account should reduceprocrastination by diminishing the time parents take to start saving. This is clearly demonstratedby the CLB and ACES initial grants considerably reducing the average age of the child whentheir RESP accounts were created. In addition, I find that the A-CESG increased the numberof transactions, possibly due to the policy acting as a yearly reminder to contribute to theaccount, which is once again only consistent with the procrastination model. This effect isprobably exacerbated by the fact the A-CESG is the only saving incentive that cannot be obtainedretroactively (i.e., the A-CESG room cannot be carried forward), thus creating an incentive tocontribute every year.In light of these results, the procrastination model seems to generally be the most useful in ex-plaining RESP contributors’ saving behaviour. This conclusion is consistent with the findings ofother recent studies that have examined the saving behaviour of individuals in the context of re-tirement savings (Choi et al., 2002; Madrian, 2012) or lifetime precautionary savings (Gathergoodand Weber, 2014). The CLB and A-CESG, the two programs targeted at low- or middle-incomefamilies, appear to be the most effective saving incentive programs if we measure their effective-ness by motivating parents to contribute larger amounts to their child’s RESP account. I find noevidence that any of the programs caused parents to save less than they otherwise would have.It is important to remember, however, that all the results obtained are conditional on childrenhaving an RESP account, which was the case for slightly less than half of children in Canadain 2012 (Table 2). Furthermore, the effects obtained in the case of the CLB and A-CESG were883.6. Discussionmeasured among RESP contributors who signed up for these programs, as opposed to beingmeasured on all eligible children. They should therefore be interpreted as an upper bound of theeffects on all eligible children. The following section describes in detail some of the limitationsof the empirical results and possible strategies to address them.3.6.2 Limitations of the AnalysisThe Canada Education Savings Program (CESP) database offers many advantages as a datasource, such as a very large number of observations and detailed information on the exact timingand amounts of RESP contributions and savings of each beneficiary, which eliminates any mea-surement error issues. This very rich dataset, however, also has important limitations resultingin three potential concerns regarding the results of this paper.First, the absence of information on children without an RESP account restricts the measure-ment of the impact of the programs on RESP take-up. From a policy perspective, it is importantto know whether these saving incentives encourage new parents to start using RESPs (exten-sive margin) or simply affect the saving behaviour of individuals who would have used RESPsregardless of the policies being in place (intensive margin). Although I was able to present someevidence that the ACES initial grant significantly increased Albertan children’s probability ofhaving a RESP account by age 7, I wasn’t able to asses the impact of the CLB or the A-CESGon this extensive margin. It is likely that the most important factor to influence RESP take uprates was the introduction of the basic 20% CESG grant for all children, which I do not studyin this paper due to the absence of data on RESP beneficiaries prior to its introduction in 1998.Since the program’s inception, the CESG participation rate grew from 9.7% of children in 1998to 45.1% in 2012 (Human Resources and Skills Development Canada, 2010; Employment andSocial Development Canada, 2014b).Second, the absence of information on family income levels in the database limits the preciseidentification of individuals eligible for the CLB and the A-CESG, the two programs targeted atlow- and middle-income families. The database only presents information on A-CESG and CLBparticipation once a beneficiary has applied for them. As a consequence of this, I can only analyseprecisely the effects of these two saving incentives on individuals who applied for the programs,which causes selection bias concerns. If the behaviour of these individuals is representative ofthe behaviour of all low-income families, then the results may not be biased, but this is fairlyunlikely.Third, and most importantly, the data provides no information on education savings in othertypes of saving vehicles. If it is the case that higher contributions result from parents simplyshifting their contributions from another saving vehicle to an RESP account for their child, thenoverall education savings may not actually be increasing. In addition, the database presentsno information on other types of savings such as retirement savings, which may also be subject893.7. Conclusionto crowding-out effects caused by increased education savings. This is less of a concern, as Ma(2004) found no evidence that higher education savings offset other household savings in the U.S.Furthermore, using Canadian survey data, Benjamin and Smart (2011) have shown that there isno crowding-out effect between RESP savings and savings in Canadian tax-favoured retirementsaccounts known as Registered education savings plans (RRSPs).One solution to address all three of these issues is to find a data source that contains theinformation needed in order to obtain a more complete picture of parents’ saving behaviourfor their child’s post-secondary education. In the next chapter, I study this topic by usingCanadian survey data that offers information on education savings of all children in Canada,not only RESP holders, between 1999 and 2012. In particular, the dataset, although muchsmaller, contains reported information on RESP savings and education savings in other savingvehicles, as well as demographic characteristics of each child, such as family income and parents’education attainment. I am therefore able to explore the impact of the combined saving incentiveprograms (mainly driven by the basic 20% CESG) on the overall take-up rate of RESPs as wellas the crowding-out effects of RESP savings on other types of education savings. I also explorewhether these effects vary across family income and parental educational attainment groups. Theresults of the next chapter therefore complement the conclusions of this chapter by providinganswers on questions that could not be addressed using the administrative database of the CESP.Whereas this chapter evaluates the precise effects of specific saving incentive programs on RESPsavings, the next chapter offers more general conclusions regarding parents’ education savingbehaviour.3.7 ConclusionThis study measures the effects of three education saving incentive programs and compares theresults to the empirical predictions of three theoretical saving models in the context of savingfor a child’s post-secondary education: the life-cycle saving model, the fixed-goal saving model,and the procrastination saving model. Specifically, I evaluate the effects of three Canadiansaving incentive programs on parents’ saving behaviour in Registered Education Savings Plans(RESPs). Despite certain data limitations, several findings are worth highlighting. The resultsindicate that parents’ actions are most consistent with the procrastination behavioural savingmodel when saving in RESPs, especially in the case of low-income families who applied forthe incentive programs. Among this low-income group, saving incentives, such as initial grantsupon opening an RESP or higher matching rates on contributions, significantly increased parents’contributions to the account, resulting in larger overall savings. In addition, regardless of income,I find that an initial $500 grant given to RESP beneficiaries reduced parents’ procrastinationby increasing their likelihood of opening an RESP for their child and significantly decreasingthe average wait time before opening the account, as measured by the age of the child when903.7. Conclusionthe RESP was created. These findings therefore suggest that such a subsidy is successful inmotivating parents to start saving earlier in incentivised education savings accounts. To obtaina more complete picture of the saving behaviour of parents for their child’s education, the nextchapter measures crowding out effects of RESP savings on other types of education savings.In presenting evidence that the procrastination saving model best explains parents’ behaviourin RESPs, the results of this paper open the door to many policy implications. In addition tomatching rates and subsidies when opening the account, other kinds of incentives could haveimportant effects on parents’ behaviour and reduce procrastination. How the programs areadvertised, how the programs are explained to parents, and the complexity of the enrolmentprocess itself are dimensions worthy of careful consideration. For example, presently the parentof a child from a low-income family in Alberta who wishes to benefit from the ACES, CLB,and A-CESG must first obtain a social insurance number for their child and then apply toeach of the these three programs, which may seem quite tedious and time consuming to somepeople. Simplifying the application process, such as automatically obtaining the A-CESG oncontributions to the RESPs of eligible children, could increase participation rates, encourageparents to start saving earlier, and possibly even increase overall contributions and savings.Another policy intervention could be to remind parents who receive a tax refund that some oftheir refund could be used to expand their child’s RESP, similar to Canadian income tax noticesof assessments that currently remind taxpayers of unused RRSP contribution room. These areresearch avenues to explore further in the context of publicly offered education savings programs.Ultimately, the objective of all financial support programs for post-secondary education is toincrease or at the very least maintain access to higher education. To fully evaluate the long-termeffects of education saving incentive programs to this end, future research should be conducted onwhether RESP savings have a causal impact on post-secondary enrolment and completion ratesin Canada. Only then could one perform a cost-benefit analysis in order to evaluate whethersuch a program is worth its public costs (see Table 2). If RESP savings do help alleviate youngadults’ financial constraints to post-secondary education attainment, the benefits could includeincreased tax revenue from higher educated and thus higher income workers, but also positivesocial returns to education such as health benefits, improved civic involvement (e.g., voting),and spillover effects of highly educated workers on other workers’ wages (Milligan, Moretti andOreopoulos, 2004; Moretti, 2004; Hout, 2012; Lochner, 2011; Oreopoulos and Petronijevic, 2013).This paper should therefore be seen as the first building block in such an evaluation.913.8. Figures3.8 FiguresFigure 3.1: Age Profiles of Average Yearly RESP Contributions by Birth CohortNote: All values are in constant 2012 dollars.Figure 3.2: Age Profiles of Average Yearly RESP Savings by Birth CohortNote: All values are in constant 2012 dollars. Amounts of RESP savings include RESPcontributions and all additional grants and subsidies offered by the government.923.8. FiguresFigure 3.3: Effect of the ACES grant: Average Age at RESP Creationby Date of Birth of the BeneficiaryNote: Dots represent the average age of beneficiaries at RESP creation measured in July2012 within ten day bins.933.8. FiguresFigure 3.4: Effect of the ACES grant: Average RESP Contributionsby Date of Birth of the BeneficiaryNote: Dots represent the average cumulative contributions of beneficiaries by July 2012within ten day bins.943.8. FiguresFigure 3.5: Effect of the ACES grant: Average RESP Savingsby Date of Birth of the BeneficiaryNote: Dots represent the average cumulative savings of beneficiaries by July 2012 withinten day bins.953.8. FiguresFigure 3.6: Effect of the ACES grant: Average Number of RESPContributions by Date of Birth of the BeneficiaryNote: Dots represent the average cumulative number of contributions of beneficiaries byJuly 2012 within ten day bins.963.8. FiguresFigure 3.7: Effect of the ACES grant: Percentage of Beneficiaries Residingin Alberta by Date of Birth of the BeneficiaryNote: Dots represent the average proportion of beneficiaries residing in Alberta byJuly 2012 within ten day bins.Figure 3.8: Effect of the CLB: Average Age at RESP Creation by Date ofBirth of the Beneficiary (for the Subgroup A-20 of Beneficiaries)Note: Dots represent the average age of beneficiaries at RESP creation by July 2012within ten day bins.973.8. FiguresFigure 3.9: Effect of the CLB: Average RESP Contributions by Date ofBirth of the Beneficiary (for the Subgroup A-20 of Beneficiaries)Note: Dots represent the average cumulative contributions of beneficiaries by July2012 within ten day bins.Figure 3.10: Effect of the CLB: Average RESP Savings by Date ofBirth of the Beneficiary (for the Subgroup A-20 of Beneficiaries)Note: Dots represent the average cumulative savings of beneficiaries by July 2012within ten day bins.983.9. Tables3.9 TablesTable 3.1: Value of the Canada Education Savings Grant (CESG)per Family Income Level and Contribution Level to the Child’s RESPAnnual value of the CESG(including the basic CESG and the additional CESG)Family net incomelevel (in 2012)*First $500 contributedeach yearContributions beyond thefirst $500 each year$42,707 or less 40 cents per dollar1 20 cents per dollar$42,708 to $85,414 30 cents per dollar2 20 cents per dollar$85,415 and above 20 cents per dollar 20 cents per dollar*Family net income cut-offs are adjusted every year according to the rate of inflation.1 The grant includes 20 cents from the basic CESG and an additional 20 cents from the A-CESG.2 The grant includes 20 cents from the basic CESG and an additional 10 cents from the A-CESG.Source: Employment and Social Development Canada (2013)Table 3.2: Recent Performance of the Canada Education Savings Program (CESP)Saving incentive 2008 2010 2012Panel A: RESPsTotal value of assets ($ billion) 22.6 27.6 35.6Annual RESP contributions ($ billion) 3.1 3.39 3.75Average annual amount of RESP withdrawalfor post-secondary educ.($)6,474 6,680 7,235Panel B: CESG (basic and A-CESG)Total CESG payments since 1998 ($ billion) 4.46 5.75 7.24Annual CESG Payments ($ million) 603 667 753CESG Participation Rate 39.7% 42.8 % 45.4%Average age of new CESG beneficiaries 3.87 3.6 3.54Panel C: CLBTotal CLB payments since 2005 ($ million) 98 220 398Annual CLB Payments ($ million) 47 65 99Average annual contribution perCLB beneficiaries ($)921 843 1,013CLB Participation Rate (%) 16.3% 21.8% 27.5%Percentage of CLB beneficiarieswho have ever made a contribution (%)94.2% 94.8% N.A.Source: Human Resources and Social Development Canada, 2009, 2011; Employment and Social DevelopmentCanada, 2014b. Dollar amounts are in nominal values. The abbreviation N.A. denotes information that was notavailable in that year.993.9. TablesTable 3.3: Model Predictions for Each Saving Incentive ProgramACES initial grant CLB Additional-CESGLump-sum subsidyoffered toresidents of AlbertaLump-sum subsidyoffered tolow-income familiesHigher matching rateoffered to low- andmiddle-incomefamiliesPanel A: Life-Cyle ModelOverall savings Increase byless than subsidyIncrease byless than subsidyAmbiguous effectContributions Decrease byless than subsidyDecrease byless than subsidyAmbiguous effectAge at RESP creationNo effect No effect N.A.Contribution frequencyNo effect No effect No effectPanel B: Fixed-Goal Saving ModelOverall savingsConstant Constant ConstantContributions Decrease bythe subsidy amountDecrease bythe subsidy amountDecrease bythe extra revenueAge at RESP creationNo effect No effect N.A.Contribution frequencyNo effect No effect No effectPanel C: Procrastination Saving FrameworkOverall savingsIncrease Increase IncreaseContributionsIncrease Increase IncreaseAge at RESP creationDecrease Decrease N.A.Contribution frequencyNo effect No effect IncreaseNote: Overall savings refer to the sum of contributions and the saving incentive amounts (subsidies and returnsto contributions). Contributions refer to parents’ contributions to their child’s RESP. Age at RESP creationrefers to the child’s age when the RESP was first opened. Contribution frequency refers to the number ofcontributions in the child’s RESP account. The abbreviation N.A. indicates cases when measuring the effectof the policy on this dimension is not applicable.1003.9. TablesTable 3.4: Saving Outcome Measures over TimeTotal savings/age Total Age at RESP Number ofcontributions/age creation contributions/agemean median mean median mean median mean median1998 546.53 382.66 460.30 321.49 8.59 8.62 3.9 1.21999 561.93 392.13 472.77 328.95 8.22 8.17 4.1 1.42000 575.95 400.69 484.13 335.75 7.89 7.74 4.3 1.52001 589.52 409.94 495.15 343.29 7.58 7.29 4.5 1.72002 602.19 419.12 505.43 350.75 7.30 6.86 4.7 1.82003 616.30 429.38 515.93 358.11 6.98 6.34 4.9 2.02004 629.64 439.56 524.93 364.83 6.72 5.90 5.0 2.22005 643.52 450.11 533.99 371.28 6.45 5.44 5.1 2.32006 656.69 459.80 542.55 376.88 6.21 5.00 5.3 2.42007 669.36 468.24 550.74 381.87 5.98 4.58 5.4 2.62008 679.72 475.74 556.93 385.45 5.77 4.18 5.5 2.72009 688.79 482.09 561.92 387.35 5.58 3.84 5.6 2.82010 694.70 485.62 563.86 386.54 5.41 3.53 5.6 2.92011 690.81 479.46 559.46 381.23 5.31 3.36 5.6 2.9Note: Savings refer to the sum of contributions and the saving incentive amounts (subsidies and returnsto contributions). Contributions refer to parents’ contributions to their child’s RESP. Age at RESPcreation refers to the child’s age when the RESP was first opened. Contribution frequency refers tothe number of contributions in the child’s RESP account. Contributions and savings are expressed inconstant 2002 dollars.1013.9. TablesTable 3.5: Saving Outcome Measures by Year of Birth of the RESP BeneficiaryTotal savings/age Total Age at RESP Number ofcontributions/age creation contributions/agemean median mean median mean median mean median1995 710.67 535.02 594.04 444.47 6.56 5.47 5.6 3.31996 716.64 525.77 598.56 437.00 5.98 4.72 5.9 3.51997 738.69 529.58 616.67 439.48 5.15 3.79 6.3 3.81998 746.36 534.27 622.41 443.555 4.21 2.73 6.8 4.31999 750.91 535.28 625.85 444.16 3.70 2.11 7.1 5.02000 764.18 538.70 636.65 446.10 3.44 1.88 7.2 5.12001 785.82 560.75 654.53 463.31 3.10 1.74 7.3 5.52002 800.48 574.25 666.17 474.55 2.86 1.72 7.3 5.82003 816.72 581.15 679.02 477.97 2.66 1.77 7.3 5.92004 850.41 620.52 677.58 484.21 2.43 1.73 7.3 5.92005 869.71 649.02 680.48 483.59 1.98 1.27 7.5 6.22006 905.17 677.72 704.88 493.69 1.69 1.02 7.5 6.42007 929.42 682.68 721.56 491.53 1.39 0.90 7.7 6.62008 919.31 693.11 705.73 493.26 1.18 0.82 7.6 6.72009 912.19 679.26 690.24 470.85 0.90 0.64 7.6 6.72010 886.24 636.70 650.73 402.51 0.65 0.49 7.5 6.42011 605.67 397.87 399.87 76.03 0.41 0.33 6.3 5.0Note: Savings refer to the sum of contributions and the saving incentive amounts (subsidies and returnsto contributions). Contributions refer to parents’ contributions to their child’s RESP. Age at RESPcreation refers to the child’s age when the RESP was first opened. Contribution frequency refers tothe number of contributions in the child’s RESP account. Contributions and savings are expressed inconstant 2002 dollars.1023.9. TablesTable 3.6: Regression Discontinuity Estimates of the Effects of the ACES Initial Granton Parents’ Saving BehaviourSpecification Linear QuadraticBandwidth 50 100 200 50 100 200Mean (1) (2) (3) (4) (5) (6)Panel A: Alberta (eligible for the ACES grant)Total savings $7,947 -95.8 646.0 773.6 -1,821.5 54.31 770.7(1063.0) (776.0) (540.4) (1583.8) (1108.0) (801.6)Total contributions $6,381 -421.7 208.9 355.6 -1,789.5 -2,90.3 312.9(903.4) (659.2) (465.4) (1348.0) (938.7) (687.6)Age at RESP creation 2.29 years -0.75∗∗ -1.11∗∗∗ -1.00∗∗∗ -0.47 -0.97∗∗∗ -1.20∗∗∗(0.34) (0.24) (0.16) (0.54) (0.36) (0.25)Number of contributions 54.25 8.86 10.77 10.49∗∗ -19.83 16.72 13.65∗(10.59) (6.97) (4.95) (17.74) (11.47) (7.72)Observations 605 1,274 2,754 605 1,274 2,754Panel B: Rest of Canada (control group)Total savings $8,305 218.0 -11.2 -193.2 17.75 460.2 -23.60(417.1) (290.6) (203.8) (632.1) (438.3) (307.2)Total contributions $6,626 185.2 -87.1 -163.0 -18.69 387.3 -6.08(357.2) (249.1) (174.8) (540.0) (374.8) (263.2)Age at RESP creation 2.35 years -0.21∗ -0.02 -0.06 -0.17 -0.21 -0.06(0.12) (0.08) (0.06) (0.20) (0.13) (0.09)Number of contributions 57.23 1.69 -1.87 -1.69 2.99 1.28 -1.07(4.15) (3.05) (2.20) (6.21) (4.54) (3.09)Observations 4,247 8.845 18,314 4,247 8,845 18,314Note: The regression results are based on a 10% random sample of the Canada Education Saving Program database.Robust standard errors are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5,and 10 percent levels. All specifications use a rectangular kernel and the bandwidth is measured in number of days.The mean was calculated on the sample of children who were born within 200 days prior to January 1, 2005.1033.9. TablesTable 3.7: Regression Discontinuity Estimates of the Effectsof the ACES Initial Grant on RESP Take UpSpecification Linear QuadraticBandwidth 50 100 200 50 100 200Mean (1) (2) (3) (4) (5) (6)Proportion of beneficiaries 0.117 0.046∗∗ 0.019 0.022∗∗ 0.065∗∗ 0.048∗∗ 0.024∗residing in Alberta (0.019) (0.013) (0.009) (0.029) (0.020) (0.014)Observations 4,851 10,118 21,063 4,851 10,118 21,063Note: The regression results are based on a 10% random sample of the Canada Education Saving Programdatabase. Robust standard errors are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significanceat the 1, 5, and 10 percent levels. All specifications use a rectangular kernel and the bandwidth is measured innumber of days. The mean was calculated on the sample of children who were born within 200 days prior toJanuary 1, 2005.Table 3.8: Regression Discontinuity Estimates of the Effects of the CLB onParents’ Saving Behaviour (Estimated on the Subgroup A-20 of Beneficiaries)Specification Linear QuadraticBandwidth 50 100 200 50 100 200Mean (1) (2) (3) (4) (5) (6)Total savings $6,962 2,695.2∗∗∗ 2,054.6∗∗∗ 1,703.8∗∗∗ 2,685.3∗∗ 3,125.6∗∗∗ 2,198.6∗∗∗(768.7) (544.7) (385.9) (1170.1) (831.0) (577.0)Total contributions $5,592 1,494.7∗∗ 1,004.9∗∗ 685.9∗∗ 1,458.6 1,846.3∗∗∗ 1,122.1∗∗(636.1) (452.0) (321.1) (968.5) (690.9) (478.4)Age at RESP creation 3.54 -0.52∗ -0.46∗∗ -0.48∗∗∗ -0.86∗ -0.55∗ -0.46∗∗years (0.29) (0.20) (0.14) (0.45) (0.31) (0.21)Number of 55.84 -7.50 1.29 2.56 -10.71 -4.09 2.56contributions (8.63) (5.82) (3.95) (13.31) (9.15) (6.23)Observations 1,185 2,472 4,860 1,185 2,472 4,860Note: The regression results are based on a 10% random sample of the Canada Education Saving Program database. Thesubgroup A-20 refers to RESP beneficiaries who have received the 20% Additional CESG (A-CESG) at least once since 2005.Robust standard errors are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10percent levels. All specifications use a rectangular kernel and the bandwidth is measured in number of days. The mean wascalculated on the sample of children who born within 200 days prior to January 1, 2004 (i.e., not elligible for the CLB).1043.9. TablesTable 3.9: Panel Data Estimates of the Effects of the A-CESGon Parents’ Saving BehaviourOutcome: Yearly Yearly Yearly numbercontributions savings of contributions(1) (2) (3)A-CESG20 261.3∗∗∗ 385.1∗∗∗ 2.33∗∗∗(11.02) (13.3) (0.14)A-CESG10 188.2∗∗∗ 260.7∗∗∗ 2.52∗∗∗(7.7) (9.3) (0.17)Age 62.54∗∗∗ 75.42∗∗∗ 1.30∗∗∗(1.30) (1.54) (0.02)Age squared -2.00∗∗∗ -2.42∗∗∗ -0.05∗∗∗(0.09) (0.11) (0.00)Individual fixed effects yes yes yesYear fixed effects yes yes yesMean outcome before 2005 $443 $528 4.03Mean outcome as of 2005 $826 $1018 7.34Observations (individual×year) 2,644,117 2,644,117 2,644,117Note: The regression results are based on a 10% random sample of the Canada EducationSaving Program database restricted to individuals with RESP accounts created prior to2005. Standard errors are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statisticalsignificance at the 1, 5, and 10 percent levels. The table presents the means of the dependentvariables prior to 2005 and as to 2005. All regressions includes year fixed and individualfixed effects. Contribution and saving amounts are expressed in constant 2002 dollars.1053.9. TablesTable 3.10: Summary of the Empirical Results ObtainedACES initial grant CLB Additional-CESGSubsidy offered toresidents of AlbertaSubsidy offered tolow-income familiesHigher matching rateoffered to low- andmiddle-incomefamiliesOverall savingsNo significant effectIncrease by morethan the subsidyIncreaseContributionsNo significant effect Increase IncreaseAge at RESP creationDecrease Decrease N.A.Contribution frequencyNo significant effect No significant effect IncreaseNote: Cells in bold are consistent with the procrastination saving model. Overall savings refer to the sumof contributions and the saving incentive amounts (subsidies and returns to contributions). Contributionsrefer to parents’ contributions to their child’s RESP. Age at RESP creation refers to the child’s age when theRESP was first opened. Contribution frequency refers to the number of contributions in the child’s RESPaccount. The abbreviation N.A. indicates cases when measuring the effect of the policy on this dimension isnot applicable.106Chapter 4The Effects of Incentivised EducationSavings Accounts on Children’sEducation Savings and AcademicPerformance4.1 IntroductionPost-secondary education is crucial for many employment opportunities in addition to beinglinked to public economic benefits such as innovation, increased tax revenues, and civil engage-ment. Access to post-secondary education, however, is not universal. There is generally a strongpositive relationship between family income and post-secondary education enrolment in manycountries, including the United States and Canada (Carneiro and Heckman, 2002; Corak, Lippsand Zhao, 2003; Belley, Frenette and Lochner, 2014). Although not the only factor, one elementthat may limit access to post-secondary education for individuals from low-income families is thehigh cost associated with obtaining such an education. Recent evidence suggests that credit andincome constraints have become more salient in limiting higher education attainment in recentyears (Lochner and Monge-Naranjo, 2012).To increase post-secondary education’s accessibility for all, many countries subsidise higher ed-ucation through programs such as student loans, tax credits, caps on tuition fees, and merit-or need-based scholarships. An alternative approach to decrease the financial burden of post-secondary education on students and their families is to encourage parents to save early on fortheir child’s higher education needs. Several countries, including the United States, the UnitedKingdom, Singapore, Hong Kong, South Korea, and Canada, have established national policies topromote and increase children’s education savings, primarily through targeted education savingsaccounts and saving incentive measures (Loke and Sherraden, 2009).87For example, the U.S. government currently offers 529 College Savings Plans, which are tax-favoured accounts intended for parents to accumulate savings for their children’s college costs.87The UK Child Trust Fund program was abolished in 2010.1074.1. IntroductionThe earnings on savings in a 529 plan grow tax deferred, and, when the beneficiary of the planis enrolled in an educational institution, qualified withdrawals are tax-free. There is, however,no consensus on whether these accounts are a useful tool to encourage parents to help financetheir children’s higher education. If these targeted savings accounts are effective in increasingchildren’s college savings, especially among those from middle- and lower-income families, thensuch a policy could help increase college enrolment rates in the U.S. by alleviating financialconstraints. In contrast, Sandy Baum from the Urban Institute recently argued that these plans“primarily provide a subsidy to people who would save in other forms regardless” (The New YorkTimes, January 22nd, 2015). On January 20th, 2015, the Obama administration put forward aproposal to end the ability to withdraw investment earnings from 529 plans tax-free, which wassubsequently retracted a week later following general public outrage (The Guardian, February5th, 2015).In Canada, the federal government introduced in 1998 the Canada Education Savings Program(CESP) to encourage parents to save for their child’s post-secondary education. The CESP relieson one main saving instrument, the Registered Education Savings Plan (RESP), a tax-advantagedsavings account registered with the Government of Canada and similar in nature to the U.S. 529plan. The main difference with the U.S. program is that in addition to the tax advantages of theRESP, the CESP offers saving incentives such as matching rates on contributions and lump-sumsubsidies when opening an RESP, some of which are targeted specifically at low-income families.88Given the recent development of the incentives offered by the CESP in Canada, however, littleempirical research has been conducted to study the specific effects of these incentives on children’slevels of education savings.This paper attempts to contribute to the current policy debate as to whether incentivised edu-cation savings accounts can be effective in increasing education savings, especially among lower-income families. Studying parents’ saving behaviour in the context of saving for their child’spost-secondary education relies on the behavioural assumption that parents use a system of“mental accounts” (Thaler, 1990). This assumption implies that parents make a distinction be-tween education savings for their child and other types of household savings, such as retirement orprecautionary lifetime savings (see section 4.2 for a discussion on this assumption). Specifically,this study has two research objectives. The first objective is to measure the effects of increasedsavings in RESPs due to the saving incentives offered by the Canada Education Savings Program(CESP) on other types of education savings. Do savings in RESPs crowd-out education sav-ings in other saving vehicles, and if so, what is the extent of this crowding-out effect? In otherwords, are parents simply shifting contributions from traditional investment vehicles to incen-tivised education savings accounts or are they actually saving larger amounts due to the savingincentives associated with these accounts? To obtain a more complete picture of parents’ saving88While a few U.S. states offer savings incentives tied to their 529 plans, the CESP presents an opportunity toexamine a universal, nation-wide intervention.1084.1. Introductionbehaviour, I also explore whether these crowding-out effects are heterogeneous across parentalincome groups. The second goal of this paper is to examine the relationship between savings intargeted education savings accounts and children’s level of preparation for college. In particular,do education savings create an extra incentive for children to perform well in school in order tolater attend a post-secondary institution? To answer this question, I will evaluate the effects ofchildren’s savings in RESPs on their elementary and secondary academic performance.The key empirical challenge of this analysis is to measure the causal impact of RESP savings onthese different outcomes. Parents’ decision to use RESP accounts is likely to be endogenous toparents’ general saving behaviour in other saving vehicles if, for example, certain types of peoplehave a strong preference for saving in general. Furthermore, individuals’ saving behaviour istypically highly correlated with their educational attainment and income levels (Dynan, Skinnerand Zeldes, 2004; Lusardi and Mitchell, 2007), characteristics which, in the case of parents, arelikely to be also be strongly related to their child’s performance in school (Dahl and Lochner,2012). To address these endogeneity concerns, I use an instrumental variable (IV) regressionmodel to measure the causal impact of savings in RESPs on other types of education savings andon children’s academic outcomes. More specifically, I instrument savings in RESPs with eachchild’s maximum amount of grant offered by the federal government based on the main savingincentive of the Canada Education Savings Program (CESP). This main incentive, the CanadaEducation Savings Grant (CESG), is offered to RESP holders in the form of a matching rate oncontributions and its amount varies across cohorts and over time. By exploiting the exogenousintroduction of this education saving incentive, I am therefore able to measure the impacts ofRESP contributions on parents’ saving patterns and children’s performance in school prior tomaking the decision to attend a post-secondary institution.Using Canadian survey data, the empirical results of this paper suggest that RESP accountsand their related saving incentives do not affect parents’ overall decision to save for their child’spost-secondary education (versus not save at all). Among education savers, however, they ledto a large increase in the overall amount of average education savings per child, although thereis evidence of some crowding-out between RESP savings and other types of education savings.Among children with education savings, for every dollar saved in a RESP account, other typesof education savings decrease on average by 34 cents. This crowding-out effect appears to beslightly larger for high-income families (approximately 42 cents) than for lower-income families(approximately 34 cents). In addition, although children’s RESP savings are strongly positivelycorrelated with their academic performance, the IV model results fail to confirm that there existsa causal impact of RESP savings on children’s grades in primary and secondary school.The remainder of the paper is structured as follows. Section 4.2 discusses the contributions of thepaper and its link to the existing literature. Section 4.3 provides an overview of the educationsaving incentive programs present in Canada, and section 4.4 presents the details of the empiricalapproach used in the paper, including a description of the data sources and the identification1094.2. Contribution and Related Literaturestrategy. Finally, the empirical results of the paper are presented in section 4.5, while section4.6 offers concluding remarks.4.2 Contribution and Related LiteratureThis study makes important contributions to the existing literature on post-secondary educationfinancing. Recent evidence indicates that the presence of liquidity constraints is an importantfactor limiting access to post-secondary education, especially among low-income families, due toeither actual credit constraints or debt aversion (Lochner and Monge-Naranjo, 2012; Lavecchia,Liu and Oreopoulos, 2014). Much of the literature on the financing of higher education has,however, focused largely on the effects of scholarships, bursaries, student loans, and lower tuitionfees on access to post-secondary education as opposed to parental transfers and education savings(Nielsen, Sørensen and Taber, 2010; Turner, 2011; Dynarski and Scott-Clayton, 2013; Cohodesand Goodman, 2014; Lochner and Monge-Naranjo, 2015). The introduction of tax-favoured edu-cation savings programs constitutes another approach to help young adults both face the costs ofhigher education and prevent them from underinvesting in their education, particularly membersof low-income families. This approach moves away from directly subsidizing post-secondary insti-tutions and needs-based financial aid towards encouraging long-term savings. Education savingincentive programs can thus be viewed as an advantageous way for parents to transfer wealthto their children to finance their higher education. The first step to understanding whetherthese education saving policies are effective in improving access to post-secondary education isto evaluate whether they lead to an increase in overall education savings.As a first objective, this paper therefore evaluates the crowding-out effects of savings in incen-tivised education savings accounts on education savings in other saving vehicles, which is animportant dimension to consider when implementing such programs. If crowding-out effectsare small, total education savings will greatly increase due to the saving incentives in place. Ifcrowding-out effects are large, then such a policy may not be worth the public costs of the sav-ing incentives. Ideally, in addition to measuring crowding-out effects within education savings,I would also more generally like to measure the offsetting effects of increased savings in tar-geted education savings accounts on all types of household savings, including retirement savings,precautionary savings, etc. To achieve this, one could measure the impact of increased educa-tion savings on total household investments or alternatively, on total household consumption.If household consumption decreases in response to larger savings for children’s post-secondaryeducation, this is a strong indication that education savings lead to increased total householdsavings. Due to data limitations, however, I am unable to address this question and I will thusfocus on measuring crowding-out effects within overall parental education savings.Standard neoclassical economic theory makes the assumption that all savings are fungible, that is1104.2. Contribution and Related Literaturethat money has no labels and individuals make no distinctions between the various componentsof wealth or expenditures.89 This “fungibility assumption” implies that various forms of wealth(both present and future) are perfectly substitutable for one another and therefore any changesin one form of savings should be completely offset by other types of savings. The empiricalinvestigation of the validity of this assumption has led to a large public finance literature oncrowding-out effects, which has focused mainly on estimating such effects in retirement savingsaccounts such as individual retirement accounts (IRAs) and 401(k) plans in the U.S. Followingthe influential work by Cagan (1965), the results of many studies in the 1980s and 1990s, mostlybased on saving model simulations, suggest that various types of wealth such as retirementsavings, home equity, and future income, are generally poor substitutes. Some studies foundmarginal or no crowding-out effects between pension savings and other types of savings (Ventiand Wise, 1995; Poterba, Venti and Wise, 1996). In contrast, other studies have found someevidence of substantial crowding-out effects across wealth categories (Gale and Scholz, 1994;Engen, Gale and Scholz, 1996; Gale, 1998). Although it is likely that some of the disparitiesbetween the results of these studies follow from different econometric assumptions (Hubbard andSkinner, 1996), this debate has yet to be resolved. Some later studies on this topic also offermixed evidence on whether increases in IRA or 401(k) savings represent increases in total savingor simply transfers from other accounts (e.g., Gelber (2011), Benjamin (2003), and Engelhardtand Kumar (2007)).More recently, the focus of this literature has shifted to using a behavioural economics approachto explain crowding-out effects, examining concepts such as framing, default options, and mentalaccounting (Madrian and Shea, 2001; Thaler and Benartzi, 2004; Chetty et al., 2012). In par-ticular, it is now well documented that people generally tend to spend and save using “mentalaccounts”, where mental accounting refers to the psychological differentiating of wealth betweenvarious economic categories (Shefrin and Thaler, 1988; Thaler, 1990; Winnett and Lewis, 1995;Antonidesa, de Grootb and van Raaijc, 2011; Card and Ransom, 2011; Hastings and Shapiro,2012). Furthermore, crowding-out effects tend to vary greatly across levels of household wealthand education. The effects are generally larger for more educated and wealthier households whotend to be more financially sophisticated (Gale, 1998; Chetty et al., 2012). Based on the resultsof these recent papers, it is likely that education savings are imperfect substitutes for other typesof household investments, such as retirement savings, due to “mental accounting”, although ev-idence to this effect is beyond the scope of this paper. This imperfect substitution is especiallylikely since education savings are intended for parents’ children, whereas other types of householdsavings are intended for parents’ own direct benefit.90 In support of this hypothesis, Benjaminand Smart (2011) find no evidence that increased RESP savings lead to a decrease in savings89According to the neoclassical life-cycle model, the marginal propensity to consume all types of wealth suchas current income, assets, or future income, is equal assuming no transactions costs (Thaler, 1990).90One exception to this statement would be the case where parents accumulate lifetime or retirement savingswith the hopes of giving a portion of these savings to their children through an inheritance or bequest.1114.2. Contribution and Related Literaturein Registered Retirement Savings Plans (RRSP), tax-deferred retirement savings accounts inCanada. Their results were, however, inconclusive in the case of other types of wealth or debtaccumulation.Among the few researchers who have specifically studied parental savings for education, evi-dence on the effects of incentivised education savings accounts is mixed. Ma (2004) found thatparents who contributed to tax-favoured education savings accounts, such as the 529 plans andCoverdell accounts in the U.S., were motivated to save more overall than they normally wouldwithout them. Attempting to control for saver heterogeneity by using a propensity score method,her results suggest that education savings did not simply offset other forms of household savings,but that in fact, education savings seemed to constitute additional household savings. Dynarski(2004) argues, however, that the use of these tax-advantaged education savings accounts dis-proportionately benefits families with higher levels of income due to the higher marginal taxrates higher-income families face, tax penalties if savings are not used in their intended way,and interactions with other college financial aid options. In Canada, Lefebvre (2004) found thatchildren with siblings, higher family income, higher academic ability, and who participated inextracurricular activities generally had significantly more education savings in RESPs put asidefor them by their parents than other children. The same held for children whose parents weremore educated and thus had higher post-secondary education aspirations for them. Milligan(2005) studied the use of RESPs prior to their reform in 1998 and also found that their use wasconcentrated mainly among highly educated parents and high-income families. Parents’ expecta-tions for their children’s educational attainment as well as the initial fixed costs of setting up anRESP account were some of the key factors that could have explained the limited use of RESPsamong low-income families. With the exception of Benjamin and Smart (2011), these studies,however, do not fully address the important concern of the presence of other unobserved factorsaffecting the use of education savings accounts, such as parents’ saving preferences, which couldpotentially bias their results if interpreted as causal estimates.This paper will therefore contribute to the existing literature by using a credible identificationstrategy in order to evaluate the causal effects on children’s overall education savings of ed-ucation savings in incentivised education savings accounts. Using an IV strategy, I measurewhether saving incentives generally increase the overall education savings of a child or parents’savings in RESPs simply constitute a shift in the type of savings for the child’s post-secondaryeducation. Furthermore, since enrolment rates in post-secondary institutions are so closely re-lated to family income, I also evaluate whether parents’ behaviour varies across income groups.Evaluating parents’ saving behaviour in this context is primordial to assess the impact of publicpolicies promoting education savings and understand how targeted education savings accountsmay help attenuate children’s financial constraints and potentially lead to increased access topost-secondary education.In addition, the results of this study provide some evidence on one possible non-financial channel1124.2. Contribution and Related Literatureby which savings intended for post-secondary education could increase college and universityeducation participation. In contrast to other financial aid strategies, which are generally onlyoffered to young people at the time when they make their post-secondary enrolment decisions,one appeal of promoting savings in targeted education savings accounts stems from the long-termaspect of this approach and its link to expectations (Elliot III, Destin and Friedline, 2011). Itis likely that parents who have saved for their child’s education over many years inform theirchildren of these savings and their purpose. If children view their education savings as a concretedemonstration of their parents’ expectations for their child’s higher educational attainment,higher education savings could translate into higher academic performance in preparation forcollege or university. In contrast, students may view their parents’ savings for their education asa disincentive to perform well in school since their need to obtain a performance-based scholarshipto finance their university or college is reduced. Based on U.S. survey data, Elliot III (2009) andElliot, Jung and Friedline (2010) find evidence that child development savings accounts, definedas incentivised savings accounts generally intended for post-secondary education, are positivelycorrelated with children’s math scores.91 They estimate that relative to those without a savingsaccount, children with a savings account score on average close to 9% higher in mathematics.Furthermore, this pattern is stronger for children from high-wealth families than those fromlow-wealth families (Elliot III, 2009; Elliot, Jung and Friedline, 2010). In order to confirmtheir results, I document the correlation between education savings and school grades usingCanadian survey data. Pushing the analysis further, I also test whether there is a causal impact ofeducation savings in RESPs on school achievement using the IV identification strategy. Anothercontribution of this study is therefore to examine whether parental education savings could notonly help alleviate students’ monetary costs of higher education, but also have an impact onchildren’s degree of preparation for post-secondary education, which, to my knowledge, is achannel that has not been examined before.Overall, this paper provides important policy-relevant insight on parents’ behaviour in responseto education saving incentives as well as the effects of education savings on children’s preparationlevels for post-secondary education (as measured by their academic grades). The results canhelp inform policy makers who design education saving policies, which are becoming increasinglypopular in many countries. In particular, in the Canadian context, although 47.1% of childrenin 2013 were the beneficiaries of the CESG through an RESP account, very little research hasbeen conducted on the effects of this major education savings program. (Employment andSocial Development Canada, 2014b) The results of this paper will thus allow the Canadiangovernment to make more informed recommendations regarding future measures to encourageparental savings for Canadian children’s university and college education.91Child development accounts are publicly offered incentivised savings accounts intended for long-term invest-ments, usually for higher education, but also for home ownership, business ownership, or retirement (Elliot, Jungand Friedline, 2010).1134.3. Institutional Background: Education Saving Incentive Programs in Canada4.3 Institutional Background: Education Saving IncentivePrograms in CanadaIn Canada, both federal and provincial public education saving incentive programs are currentlyoffered to encourage parents to save for their child’s post-secondary education. The main federalgovernment program, the Canada Education Savings Program (CESP), consists of one savingvehicle, the Registered Education Savings Plan (RESP), and two saving incentives, the CanadaEducation Savings Grant (CESG), in the form of a matching rate on contributions, and theCanada Learning Bond (CLB), a subsidy to the RESP accounts of children in low-income families.Provincial programs provide additional saving incentives, which are also deposited into RESPs.4.3.1 Registered Education Savings Plans (RESPs)Registered Education Savings Plans (RESPs) are education saving vehicles registered with theGovernment of Canada and provided by the majority of financial institutions and financial serviceproviders (Employment and Social Development Canada, 2015). They were first created in 1974,but they only started being extensively used after their 1997 and 1998 reforms (Milligan, 2005).Contributors to the RESP, who are typically parents of the child beneficiary but who can also beother relatives or family friends, may contribute up to a lifetime limit of $50,000 per beneficiary.92Although contributions to RESPs are made out of after-tax income, all earnings on funds inRESPs remain tax free until withdrawn for the beneficiary’s post-secondary education. If enrolledin a qualifying educational program, the beneficiaries of RESPs are eligible for withdrawalsfrom their RESP savings, which include contributions to the RESP, investment returns on thesecontributions, and additional federal and provincial education saving incentives, which I describein sections 4.3.2 and 4.3.3. When withdrawn, earnings on contributions are taxable, but theyare treated as income to the beneficiary in the year of withdrawal (Employment and SocialDevelopment Canada, 2015). Most full-time students do not pay any income taxes on theseamounts because of the typically low income they obtain from other sources and the income taxcredits they are entitled to as students (Milligan, 2005).Qualifying educational programs include those offered by colleges, CEGEPs, trade schools, col-leges and universities.93 These programs may be full-time or part-time. Where the beneficiaryof the RESP chooses not to pursue post-secondary studies, another beneficiary may be desig-nated without any tax consequences if the replacement beneficiary is a sibling under the age of92From 1998 to 2006, RESP annual contributions were capped at $4,000 in addition to being subject to amaximum lifetime contribution limit of $46,000. As of 2007, there are no annual contribution constraints and thelifetime contribution limit is $50,000 per beneficiary (Employment and Social Development Canada, 2015).93CEGEPs are publicly-founded colleges in the province of Quebec. The acronym CEGEP stands for “Collèged’enseignement général et professionnel”,which translates in English to “General and Vocational College”. Theyoffer either a pre-university 2-year program required for entry in university or a 3-year vocational program.1144.3. Institutional Background: Education Saving Incentive Programs in Canada21 (Employment and Social Development Canada, 2015). Alternatively, the subscriber of theRESP may withdraw savings from the RESP if the beneficiary is 21 years or older or if theRESP was created at least 10 years prior to this withdrawal. The withdrawals on investmentearnings are then treated as income to the subscriber. They are taxable and subject to a 20%additional penalty tax (Knight, Waslander and Wortsman, 2008). Since 1998, assets in RESPshave grown considerably over the years, reflecting their increasing popularity. In 2013, the totalvalue of assets in RESPs in Canada increased $4.9 billion over the 2012 level to reach $40.5billion (Employment and Social Development Canada, 2014b). This increase in take up is morethan likely mainly due to the federal government’s introduction of education saving incentives,which are described in the next section.4.3.2 The Canada Education Savings Grant (CESG)In 1998, the Canadian government introduced the Canada Education Savings Grant (CESG) inorder to encourage the use of RESPs for post-secondary education savings. The CESG was setup as one of the measures of the Canadian Opportunities Strategy introduced in the 1998 federalbudget. The goal of this strategy was as follows:“The Canadian Opportunities Strategy will help ensure that all Canadians – espe-cially those with low and middle incomes – have an equal opportunity to participatein the changing economy. It will do so by reducing financial barriers and other ob-stacles that stand in the way of acquiring skills and knowledge. By expanding accessto opportunity, the government is building a stronger economy and a more securesociety” (Department of Finance, Canada, 1998).The CESG includes both the basic CESG, which has been available to all Canadian childrensince 1998, and the additional CESG (A-CESG), which was introduced in 2005 for low- andmiddle-income families. The basic CESG, which remains today the main RESP saving incentive,is equivalent to a 20% matching rate on the contributions made to the RESPs of all beneficiaries.In order to receive this grant, the beneficiary of the RESP must be a Canadian resident at thetime of the contributions to the RESP, must have a social insurance number, and must be aged17 years or under. The annual limit in contributions eligible for the CESG was $2,000 between1998 and 2006 and increased to $2,500 in 2007, which remains the current annual limit today.Since 1998, RESP beneficiaries were therefore eligible for a maximum yearly basic CESG amountof $400 prior to 2007 and $500 as of 2007 (Employment and Social Development Canada, 2015)In 2005, the additional CESG (A-CESG), was introduced to further encourage low- and middle-income families to save in RESPs. For contributions made as of January 1, 2005, the A-CESGprovides an additional 10% or 20% matching rate on the first $500 invested yearly in the child’s1154.3. Institutional Background: Education Saving Incentive Programs in CanadaRESP. Eligibility for the A-CESG depends on the child’s level of family income in a year. Childrenfrom low-income families are eligible for an additional 20% matching rate while those from middle-income families are eligible for an additional 10% matching rate.94 Yearly RESP contributionsbeyond the first $500 or contributions to RESPs of children from higher income families areonly eligible for the basic 20% CESG (Employment and Social Development Canada, 2015). Themaximum lifetime CESG amount, including the basic CESG and the A-CESG, that a beneficiarycan receive is $7,200 (Employment and Social Development Canada, 2015).The CESG is Canada’s main education saving incentive program. It is important both in terms ofpopulation take-up rates and public costs. As of December 2013, 47.1% of Canadian children hadreceived the CESG through an RESP. Since the program’s inception in 1998, the Governmentof Canada contributed more than $8 billion in CESG to the RESPs of Canadian children asof December 2013. In 2013 alone, the Government of Canada paid out $782 million in CESG(Employment and Social Development Canada, 2014b).4.3.3 Additional Education Saving IncentivesThe Canada Learning Bond (CLB)In 2004, the Canadian government introduced an additional incentive to encourage savings forpost-secondary education among modest-income families: the Canada Learning Bond (CLB).Under this policy, the Government of Canada makes a $500 contribution to the RESP of eachchild of eligible families during the first year. The child also receives $100 per year for eachsubsequent year he or she remains eligible, up to the age of 15 years for a lifetime maximumcontribution of $2,000. To be eligible, the child must be the beneficiary of an RESP account, thechild must have been born as of January 1, 2004, and the primary caregiver of the child mustreceive the National Child Benefit Supplement, which, in 2013, applied to families whose netannual income was $43,561 or less (Employment and Social Development Canada, 2013, 2015).95Although receiving the CLB subsidy does not require any contributions to the child’s RESP (incontrast to the CESG), the take up rate of this program has been relatively low among eligiblechildren. In 2013, 29.4% of eligible children had received the CLB. The government of Canadapaid $101 million in CLB in 2013 to reach a total cost of $499 million since the program wasintroduced in 2004 Employment and Social Development Canada (2014b).94In 2013, to be qualified as a low-income family, a family’s income had to be below $43,561. To qualifyas a middle-income family, a family’s income had to be between $43,561 and $87,123 (Employment and SocialDevelopment Canada, 2013). These income thresholds are adjusted every year for inflation.95For children whose primary caregiver is a public agency, the child is eligible for the CLB if the agencyreceives payments under the Children’s Special Allowances Act (CSAA) for a child in care (Employment andSocial Development Canada, 2015).1164.4. Empirical ApproachProvincial Education Saving Incentive ProgramsIn addition to the federal education saving incentives, several Canadian provinces offer their ownsaving incentive programs based on RESPs to further encourage their families to save for theirchild’s post-secondary education. These provincial programs were introduced more recently thanthe federal incentives in the provinces of Alberta (2005), Quebec (2007), Saskatchewan (2013) andBritish Columbia (2015). With the exception of Quebec, the government of Canada administersthese programs on behalf of the provinces.The province of Alberta introduced in 2005 the Alberta Centennial Education Savings (ACES)Plan, under which the Alberta government contributes $500 to the RESP of children born oradopted by its residents as of January 1, 2005.96 In 2007, the government of Quebec introducedthe Quebec Education Savings Incentive (QESI). Under this program, Quebec children are eligiblefor a 10% matching rate on contributions up to $250 per year as well as an extra amount of upto $50 for children of low- and middle-income families. The QESI is paid out to the RESP ofthe child in the form of a refundable tax credit for parents. Saskatchewan later implemented asimilar program, the Saskatchewan Advantage Grant for Education Savings (SAGES) in 2013,which offers a 10% matching rate on yearly contributions up to $250 made as January 1, 2013.Finally, the province of British Columbia initiated the British Columbia Training and EducationSavings Grant (BCTESG) under which children born as of January 1, 2007 are eligible for aone-time subsidy of $1,200 to their RESP when the child turns 6. These subsidies will onlybe paid out as of August 2015 (Employment and Social Development Canada, 2015; RevenuQuébec, 2015).4.4 Empirical ApproachTo evaluate the impact of savings in incentivised education savings accounts on overall educationsavings and children’s academic performance, I use an empirical approach that relies on Canadiansurvey data.4.4.1 DataThis study is based on four cross-sectional Canadian survey data sources: the 1999, 2002, and2013 cycles of the Survey of Approaches to Educational Planning (SAEP) and the 2008 Accessand Support to Education and Training Survey (ASETS), which replaced the SAEP in 2008. Foreach survey, parents (or guardians) provided information about themselves and about one child96The ACES Plan will be terminated in the 2015-2016 fiscal year. All children born after March 31, 2015 willno longer be eligible for the program (Government of Alberta, 2015).1174.4. Empirical Approachchosen at random in their household.97 To perform the empirical analysis, I pool together thesefour repeated cross-sectional datasets into one large sample. The unit of analysis is the child.The resulting sample includes children aged 0 to 17 years at four points in time (1999, 2002, 2008and 2013) across the ten provinces of Canada.98 The pooled dataset contains information onchildren’s own characteristics (age, gender, province of residence, performance in school), on theirfamily characteristics (parents’ educational attainment, family income level, family structurevariables, etc.) and on their parents’ saving behaviour for their post-secondary education (typesof saving vehicles used and amount of savings). I exclude from the final sample children with thetop 2% of values for total education savings in order to remove implausibly large values of thesesaving amounts, which could strongly bias the results.99 The sample size of the final pooleddataset is 42,503 children, which includes 18,699 children from the 1999 SAEP, 9,571 childrenfrom the 2002 SAEP, 5,738 children from the 2008 ASETS, and 8,495 children from the 2013SAEP.Throughout the paper, all dollar amounts including income levels, saving amounts, tuitionamounts, and saving incentive amounts are expressed in constant 2012 dollars for comparisonpurposes. Saving amounts include parents’ contributions, investment income, and in the case ofRESP savings, all grants and subsidies provided by the government. The 1999 and 2002 SAEPprovide parents’ reported savings in the year the survey was administered. In the case of the2008 ASETS and 2013 SAEP, general demographic variables were measured at the time of thesurvey, but parents were asked about their income levels and saving amounts on last day ofthe previous calendar year. As a consequence of this, reported amounts of savings in the 2008ASETS were measured at the end of 2007 and reported amounts of savings in the 2013 SAEPwere measured at the end of 2012. Despite the published dates of the surveys, the data thereforereflects saving outcomes in 1999, 2002, 2007, and 2012, which are the four reference years that Iuse throughout the analysis.Table 4.1 provides a summary of the demographic characteristics of all children in each cross-section of the pooled sample. Overall, the various cross-sections are relatively similar. Thedistribution of children across provinces is comparable over time. The average age of childrenin the sample is 8 years and approximately two thirds of them have parents who own their97One exception to this is the 1999 SAEP where parents provided information on all children present in theirhousehold.98The target population of the surveys did not include children living in the three territories of Canada, but allprovinces were included.99The top 2% was chosen as a cut-off since the main analysis estimates were very sensitive to removing theseextremely large values from the dataset, but they were not sensitive to removing the next 1% of values. I choseto drop observations with extremely large values of education savings since they were mostly driven by amountsof RESP savings well above the overall RESP contribution limit set by the government ($50,000). These amountsmade me question whether individuals really understood the question that was asked in the survey. In addition,since information on overall education savings is unavailable in 2013, I also removed the top 1% of RESP savingsin that cross-section in order to drop unusually large values of savings and make the amounts comparable toRESP savings in previous years. The yearly average amounts are very similar to the ones calculated using theadministrative database of the CESP.1184.4. Empirical Approachhome. As one would expect, parent’s income and educational attainment slowly increase overtime. One limitation of the data is that the 2008 ASETS dataset contains an unusually largenumber of missing values for income levels of single-parent families, resulting in an abnormallylarge number of children with two-parent households in the 2007 cross-section. To address thisissue, I include in all the regression estimations a control variable indicating whether a child isliving with both his parents as opposed to only one parent. I also perform the analysis on thesubsample of households with two parents present as a robustness test (see section 4.5.4).A second drawback of the data stems from missing variables on certain saving measures. Due tosome inconsistencies across the four datasets in key outcome variables, three different samplesare considered throughout the analysis. The full sample includes all four cross-sections. Someof the empirical analyses are performed on a restricted sample, which excludes the 2012 cross-section because unfortunately, it does not contain any information on the amount of savingsparents have accumulated in saving vehicles other than RESPs. Finally, when examining therelationship between RESP savings and academic performance, the sample is restricted to school-age children (age 6 and above) across all four cross-sections.Figure 4.1 provides an overview of the evolution of the proportion of children with educationsavings over time. Between 1999 and 2012, the proportion of children with education savingsincreased from 41% to 62%. Over this sample period, this increase in children’s propensity tohave education savings was driven by both an increase in the proportion of children with RESPsavings (from 17% to 45%) and in the proportion of children with other types of savings (from30% to 41%).100 Other types of education savings include savings in bank accounts or in-trustaccounts, term deposits, guaranteed investment certificates (GICs), saving bonds, RegisteredRetirement Savings Plans (RRSPs), mutual funds, investment funds, publicly traded stocks notin RRSPs or RESPs, or any other type of saving vehicle.Since the number of years of eligibility for most saving incentive programs increased over time,thereby creating stronger incentives to save in RESPs in recent years, one would expect theaverage amount of RESP savings to also increase over time. Figures 4.2 and 4.3 provide evidencethat this was the case. Among children with education savings, the average amount of RESPsavings was $1,793 in 1999, compared with $6,169 in 2012. In contrast, average amounts of othereducation savings were relatively constant in 1999 and 2002 (approximately $4,000 per childwith education savings), but these amounts then decreased significantly by 25% in 2007. Thesame patterns are observed when comparing the distributions of savings in RESPs to savings100According to calculations performed by the Canada Education Savings Program (CESP), the proportion ofchildren with RESP savings was 15.6% in 1999, 26.2% in 2002, 37.8% in 2007 and 45.4% in 2012. These numbersare comparable to the estimates I obtain based on the survey data, with the exception of the 2007 value, whichis slightly lower than my estimate (0.43). This discrepancy is probably due to the very high number of missingobservations for single-parent families in the 2008 ASETS dataset, affecting the sample selection of that cross-section (Human Resources and Social Development Canada, 2009; Human Resources and Skills DevelopmentCanada, 2010; Employment and Social Development Canada, 2014b).1194.4. Empirical Approachin other types of education savings over time (Table 4.2). In addition to evolving over time,children’s amounts of education savings are strongly related to parents’ level of income andparents’ educational attainment (Figures 4.4 and 4.5). I therefore explore in the analysis ofparents’ saving behaviour whether the effects measured are heterogeneous across family incomegroups and parents’ educational attainment groups.This study also examines the link between children’s academic performance and RESP savings.Academic performance is measured based on parents’ reported assessment of their child’s per-formance in school.101 Unfortunately, the performance scale is not consistent across all datasets.In the 1999 SAEP, parents were asked whether their child’s performance in school was belowaverage, average, or above average. In the three other surveys, parents were asked to report theirchild’s average performance in school according to letter grades.102 For consistency, I convertedthe letter grades to the same scale as the 1999 SAEP. Although imperfect, this approach allowsthe inclusion of all four datasets in the analysis on schooling outcomes.103 Figure 4.6 provides anoverview of school-aged children’s average performance over time, as reported by parents, whichseems to increase as of 2008.4.4.2 Identification StrategyI use an instrumental variable (IV) identification strategy to identify the causal impact of a child’ssavings in RESPs on other types of education savings and the child’s academic performance.The idea underlying this strategy is to instrument a child’s cumulative amount of RESP savingswith the level of saving incentives faced by his or her parents based on the structure of theCanadian education saving incentive programs. By exploiting the exogenous variation in thesaving incentives, I am able to obtain causal estimates of the effects of RESP savings on differentdimensions. More specifically, by adopting this IV technique, I address two potential commonissues: omitted variable biases and measurement error biases.The first issue is that ordinary least squares (OLS) or maximum likelihood estimation modelestimates (e.g., Probit, Tobit, and Ordered Logit models) are likely to provide biased estimatesof the effect of RESP savings on the outcomes studied due to the presence of unobserved variablescorrelated both with RESP savings and these outcomes. For example, when attempting tomeasure crowding-out effects of RESP savings on other types of education savings, it is likelythat parents who tend to save for their child’s post-secondary education in other saving vehicleswould also tend to use RESPs due to their general preferences for saving. These parents may101The question asked to parents is the following: “Based on your knowledge of (name of child)’s schoolworkand report cards, how did (he/she) do overall in school?”.102The choice of letter grades in the 2002 SAEP, the 2008 ASETS, and the 2013 SAEP surveys was as follows:A+ (or 90%-99%), A or A- (or 80%-89%), B (or 70%-79%), C (or 60% to 69%), D (or 50 %-59%), or E, F, or R(Below 50%).103The results are similar when removing from the sample the 1999 SAEP data, but I include the 1999 SAEPin the final sample to maximise the number of observations and the predictive power of the instrument.1204.4. Empirical Approachinherently be very active savers or they may simply value education savings more for otherunknown reasons than parents who do not tend to save at all. Furthermore, although I controlin all regressions for parents’ education levels and annual family income, the data presents noinformation on family wealth levels, which is likely to also affect parents’ saving behaviour. Inall of these examples, the estimates would suffer from an omitted variable bias and more thanlikely underestimate crowding-out effects between both types of education savings. This issue ofomitted variables may also lead to biased estimates of the impact of RESP savings on academicachievement. It is likely that other unobservable factors such as, for example, the degree to whichparents care about post-secondary education, may be correlated with both their saving behaviourand how much effort they put into making sure that their children perform well in school, therebyresulting in biased estimates. One solution to this issue is to employ an instrumental variableapproach.Measurement error is another important concern when estimating the effects of reported RESPsavings on various outcomes. Because this analysis is based on survey data, it is likely that theamount of education savings reported by parents, both in RESPs and in other saving vehicles,suffers from measurement error caused by self-reporting. Parents may not remember the preciseamount of savings they have accumulated for their child at the time of the survey, causing inexactreported amounts. Under the Classic Measurement Error (CME) model, which assumes thatmeasurement error is independent of the true value of the variable or has zero mean conditionalon the true value, this issue creates an attenuation bias (i.e., a bias towards zero). Furthermore,although classical measurement error alone in the dependent variables does not lead to biasedestimates, if it is correlated with measurement error in the explanatory variable, it may affectthe estimation results considerably (Hyslop and Imbens, 2001).104 Such a situation could occurwhen measuring crowding-out effects between RESP savings and other types of education savingsif parents report both types of savings with similar measurement error. Finally, in additionto potential measurement error in reported saving amounts, the variable used to measure achild’s academic performance is not based on an objective academic test score, but on parents’reported school performance of their child, potentially leading to measurement error in thisdimension as well. One approach to correct for measurement error bias on the estimated effectsof RESP savings is to use an instrumental variable strategy. Under the classical measurementerror framework and the assumption that the instrument is orthogonal to the measurementerror of RESP savings, the linear IV approach provides unbiased results (Bound, Brown andMathiowetz, 2001).105104In this case, the bias cannot generally be signed without information on the correlation between both measure-ment errors. If the correlation between the measurement error on the dependent variable and the measurementerror on the independent variable is close to 1, the bias will be upwards, but if it is close to -1, the bias will bedownward (Hyslop and Imbens, 2001).105The orthogonality assumption is likely to hold since the instrument I employ is based on the exogenousintroduction of a saving incentive program. It is, however, possible that the amount of measurement error onRESP savings is correlated with the true value of RESP savings, thereby violating the Classical Measurement1214.4. Empirical ApproachBearing in mind these two important concerns and the goal of obtaining plausible causal estimatesof the impact of RESP savings, I instrument a child’s cumulative amount of RESP savings withthe level of education saving incentives faced by the child’s parents. There exist numerousways of capturing this level of saving incentive. In the main analysis, I use as an instrumentthe maximum cumulative amount of basic CESG available to a child in the survey year. Thisinstrument relies solely on the basic CESG as the measure of saving incentive for three reasons.First, the basic CESG is the main education saving program and provides the largest potentialamount of incentive compared to other saving incentives. Second, whereas the basic CESG is afunction of the child’s age and the year of the survey, the other saving incentive programs rely onthe child’s current and past province of residence and family income levels. Due to the fact thatI only have access to current measures of these variables, a child’s eligibility amount of the othersaving incentives is not as exact as for the basic CESG. Third, the instrument including onlythe basic CESG as a measure of saving incentive performs the best in terms of predictive powerfor the cumulative amount of RESP savings (i.e., has the strongest first stage results). It is alsoimportant to point out that the instrument does not reflect the tax advantages of investing inan RESP as opposed to other saving vehicles, since these tax advantages did not vary over thesample period and thus present no additional source of exogenous variation.The maximum cumulative amount of CESG for which a child is eligible varies across both agegroups and time as the number of years of exposure to the CESG program depends on both thesemargins (see Figure 4.7). Specifically, within a given age group, the level of saving incentive variesover time. For example, a twelve-year-old in 2012 was eligible for 12 years of CESG basic grantcompared with 10 years for a twelve-year-old in 2007, 5 years for a twelve-year-old in 2002 and2 years for a twelve-year-old in 1999. This variation comes from the fact that years of eligibilityfor the CESG correspond to either the number of years since 1998 (for children born prior to theprogram’s implementation in 1998) or to their age (for those born after 1998). In addition, thecontribution limit for yearly contributions eligible for the 20% CESG matching rate increasedfrom $2,000 to $2,500 in 2007, which adds another margin of variation. Equation 4.1 presentsthe formula of the maximum nominal CESG amount for a child of age j in year t, where j rangesfrom 0 to 17 and t is either 1999, 2002, 2007, or 2012.106MaxCESGjt =[t+ 1−max(t− j, 1998)]× 0.2× 2, 000 if t ≤ 2002[t+ 1−max(t− j, 1998)]× 0.2× 2, 000 + [t+ 1−max(t− j, 2007)]× 0.2× 500 if t ≥ 2007(4.1)There is one exception to this formula. Children aged 17 years in 1999, one year after theError assumption and making it difficult to get a sense of the direction of the measurement error bias. In thiscase, using an IV strategy would not necessarily provide unbiased estimates of the effects of RESP savings.106The year t corresponds to the year of measurement of the saving amounts: 1999 for the 1999 SAEP, 2002 forthe 2002 SAEP, 2007 for the 2008 ASETS, and 2012 for the 2013 SAEP.1224.4. Empirical Approachprogram was introduced, were not eligible for the CESG except under very stringent criteria.107Because of this exception, I make the assumption that they were not eligible for the basic CESGand thus their assigned amount is zero.For a child to receive the amount of basic CESG calculated in equation 4.1, parents must havemade the maximum RESP contribution – $2,000 per year from 1998 to 2007 and $2,500 in 2007or later – in every year of eligibility. The majority of children benefits from considerably lowercontributions than these amounts. It is important to note that the instrument does not dependon the amount of CESG received by the child, but on the potential amount that a child couldreceive if parents maxed out their RESPs. The instrument thus captures the potential levelof saving incentive and not the realised amount of incentive. In addition, the CESG incentiveamount obtained in equation 4.1 is adjusted for inflation and is expressed in constant 2012 dollarsto obtain the instrumental variable Incentivejt.The baseline specification of the instrumental variable (IV) approach is linear, which I estimateusing a Two-Stage Least Squares (2SLS) model. The first stage of this technique, presentedin equation 4.2, models RESP savings as a linear function of the instrument and various de-mographic characteristics of the child. The second stage (equation 4.3) models the outcome ofinterest as a linear function of the predicted value for RESP savings obtained in the first stageand the same demographic characteristics in the following way:RESPsavingsijtp = αo + γIncentivejt +XitjpA+ ωtp + νj + µijtp (First stage) (4.2)Yijtp = βo + θRESP ̂savingsijtp +XitjpB + ωtp + νj + εijtp (Second stage) (4.3)In equations 4.2 and 4.3, indices i represents the child, j stands for the age of the child (0 to 17),t stands for the year (1999, 2002, 2007, 2012), and p for the province. The variable Incentivejt,defined above, refers to the maximum cumulative real amount of basic CESG the governmentcan contribute to a child’s RESP. The variables Yijtp and RESPSavingsijtp refer respectivelyto the outcome of interest and the amount of cumulative real RESP savings for the child. Allregressions include year by province fixed effects ωtp, age fixed effects νj , as well as controlvariables Xijtp, which include the gender of the child, family income levels, parents’ combinedhighest level of educational attainment, whether parents own their home, the number of childrenin the household, whether the child lives with both parents, the child’s province of residence,and the average provincial university tuition in the child’s year of birth.108 All dollar amounts107The criteria were as follows. Sixteen or seventeen year olds were only eligible for the basic CESG if they hadat least 4 years of minimum annual contributions of $100 to an RESP before the calendar year they turned 15 orif they had a minimum of $2,000 in RESP contributions before the calendar year they turned 15 (Employmentand Social Development Canada, 2015).108In the regression model, I cannot include year, age, and cohort fixed effects because these three variables areperfectly collinear (age = year − year of birth). An alternative model specification would be to include cohortfixed effects instead of age fixed effects. I chose to use age fixed effects due to the nature of the dataset. Thefour repeated cross-sections included children aged 0 to 17 at four points in time, providing me with four different1234.4. Empirical Approachused in the regressions are expressed in units of thousands of constant 2012 dollars.In equation 3, the variable RESP ̂savingsijtp refers to the predicted value of RESP savingsobtained from estimating the first stage of this approach (equation 4.2). Standard errors areclustered at the age level to account for any within age group correlation. The parameter ofinterest, θ, provides an estimate of the local average treatment effect: the causal impact ofRESP Savings on the outcome Yijtp among parents whose saving behaviour was affected by theCESG saving incentive. The main outcomes examined in the analysis include the probabilityof having other types of education savings, the amount of other education savings, the amountof total education savings and parents’ reported measure of the academic performance of theirchild (below average, average, or above average).For the IV strategy to be valid, the instrument must satisfy two conditions: the relevance con-dition and the exogeneity condition. The relevance condition, which is empirically testable,requires that the instrument Incentivejt be a strong significant predictor of RESP savings(i.e., Cov [Incentivejt, RESPsavingsijtp|Xijtp, ωtp, νj ] 6= 0). The results presented in section4.5.2 confirm that this condition holds. The exogeneity condition requires that the instrumentIncentivejt is uncorrelated to the error term (i.e., Cov [Incentivejt, εijtp|Xijtp, ωtp, νj ] = 0).This condition, which can not be empirically tested, relies on the assumption that the introduc-tion of the CESG program was exogenous and the child’s maximum amount of eligible CESG isuncorrelated to the outcomes of interest (other education savings and the child’s performance inschool) other than through increased RESP savings after conditioning on the control variablesand fixed effects in equation 4.3.In the context of this analysis, the exogeneity condition is likely to be satisfied for three reasons.First, the CESG program was announced in 1998 and implemented immediately for contributionsto RESPs made as of 1998. One could be concerned that if parents anticipated the introduction ofthe CESG incentive, they could have modified their behaviour prior to the grant being introduced.For example, parents could have waited until the program was in place to have a child or to startsaving for their child’s post-secondary education. Because of its unexpected announcement,however, the CESG incentive can arguably be seen as an exogenous shock to the saving incentivesoffered to parents. Second, the criteria for CESG eligibility rely in a specific nonlinear way onthe year of birth of the child, as well as the time elapsed since its implementation in 1998 andits contribution limit increase in 2007 (measured here by the reference year of the survey), whichare two dimensions that are very difficult for parents to manipulate. Finally, in addition todemographic control variables, I include age fixed effects and province by year fixed effects inthe specification. This ensures that I control for other possible confounding factors commonto all children that vary by province over time, such as economic conditions or the politicalclimate, as well as factors that vary by age group such as school curriculum or time to highyears of observations within each age group. If I had instead used birth cohort fixed effects, the overlap of birthcohorts over time would have been unbalanced and much more limited.1244.4. Empirical Approachschool graduation.The identification of the effects of RESP savings thus relies on the nonlinear structure of theCESG saving incentive after purging out age specific and year specific level effects of the CESGincentive. In other words, I exploit, within a specific age group, the pattern of increased amountof eligible CESG eligibility over time after removing general effects common to children within aprovince in a certain year (see Figure 4.7). Based on this pattern, the amount of CESG incentivefaced by a child’s parents should only affect the child’s amount of other education savings oracademic grades due to increased RESP savings, thus satisfying the exogeneity assumption ofthe instrument. Following the treatment effect literature (Imbens and Angrist, 1994; Imbens andWooldridge, 2009), the IV approach provides causal estimates of the local average treatment effect(LATE); that is, the effect for individuals whose saving behaviour was modified by the instrument(the compliers). In other words, under the assumption that the instrument is exogenous, the IVestimates are picking up the effects of increased RESP savings solely due to the compliers reactingto the incentives induced by the basic CESG. Among the compliers, this increase is thereforeindependent of parents’ underlying saving preferences or other unobserved factors. Due to thestructure of the CESG incentive, the compliers are more likely to be parents of younger children,which experience the highest variation in basic CESG over time after removing age-specific andyear-specific level effects of the CESG. The first stage results confirm that the instrument isstronger for these individuals (see section 4.5.2). Section 5.4 provides a further discussion ofthe possible threats to the validity of the exogeneity assumption and other limitations of theanalysis.In the main specification, the first stage of the IV empirical approach is always modeled linearlyby regressing the CESG incentive on RESP savings using an OLS specification. The secondstage specification, however, may not be linear and varies according to the outcome measured.For example, in the case of a binary dependent variable, such as a variable indicating the use ofother types of education saving vehicles, the second stage is also modelled using a Probit modelin addition to using a linear probability model. When the second stage is non-linear, I use amethodology based on a control function approach in order to obtain consistent estimates for thenonlinear IV case (Smith and Blundell, 1986; Newey, 1987; Rivers and Vuong, 1988; Wooldridge,2010). This technique is also known as a two-stage residual inclusion approach (Terza, Basu andRathouz, 2008). Using the example of the Probit model, the procedure is as follows.I first regress RESP savings on the instrument Incentivejt as well as the other control variablesusing an OLS regression. This step is identical to the first step of the Two-Stage Least Squares(2SLS) approach presented previously in equation 4.2.RESPsavingsijtp = αo + γIncentivejt +XitjpA+ ωtp + νj + µijtp (First stage) (4.4)I then estimate the OLS residual µˆijtp of equation 4.4 by subtracting the predicted amount of1254.5. Empirical ResultsRESP savings from the actual amount of RESP savings for each child.µˆijtp = RESPsavingsijtp −RESP ̂savingsijtp (4.5)Next, to model the binary outcome of interest Yijtp, I estimate a Probit model using a maxi-mum likelihood estimation, which includes the estimated residual µˆijtp obtained from estimatingequation 4.4. Under this Probit specification, the probability that Yijtp = 1 is modelled in thefollowing way:P (Yijtp = 1) = Φ (βo + θRESPsavingsijtp + λµˆijtp +XitjpB + ωtp + νj + εijtp) (Second stage) (4.6)where Φ(.) is the standard normal distribution.Finally, I use a bootstrap resampling scheme on this two-step procedure in order to obtainconsistent estimates of the standard errors of my estimates. I also use this control functionapproach in the case of the outcome of interest being modelled in the second stage using a Tobitmodel or an Ordered Logit model.1094.5 Empirical Results4.5.1 The Extensive Margin: The Effects of Education Saving Incentives onParents’ Decision to SaveAs a first step, I estimate whether parents are more likely to start saving for their child’s post-secondary education due to the saving incentive provided by the CESG. I find no evidence of aneffect of the CESG incentive on this extensive margin. The estimated effects of a $1,000 increasein eligible CESG on a child’s probability of having education savings are very small in magnitudeand mostly statistically insignificant across both samples considered throughout the analysis aswell as across income groups (Tables 4.3 and 4.4).The results presented in Table 4.3 also clearly demonstrate that several demographic factors areassociated with a significantly higher probability of a child having education savings. Childrenin families with higher income levels, with highly educated parents, with parents who own theirhome, and in families with fewer children are significantly more likely to have education savingsthan other children. For example, compared to a child with both parents who have not completedhigh school, a child with at least one parent who has completed a post-secondary degree is 16to 19 percentage points more likely to have education savings. Similarly, a child with parentswhose combined income is above $104,800 is 28 percentage points more likely to have some109For a further discussion of the control function procedure applied to each model, see Wooldridge (2010,585–594) for the Probit case, Wooldridge (2010, 681–685) for the Tobit case and Wooldridge (2010, 660–662) forthe Ordered Logit case.1264.5. Empirical Resultseducation savings compared to a child from a family with an income level below $13,100. Overall,these various socio-economic factors are also associated with parents’ saving behaviour in RESPsspecifically, which is consistent with the findings of previous studies (Lefebvre, 2004; Milligan,2005).1104.5.2 The Intensive Margin: The Effects of RESP Savings on OverallEducation SavingsThe Effects of the Saving Incentives on RESP Savings (First Stage Results)Although the CESG saving incentive does not seem to have had an effect on parents’ generaldecision to save for their child’s higher education, it may still influence the type of saving vehicleparents choose to use for education savings. I therefore evaluate next whether it has an impact onparents’ take-up rate of RESPs specifically. I find that children eligible for higher CESG amountsare significantly more likely to have an RESP account (Table 4.5). Specifically, I estimate that anincrease of $1,000 in eligible CESG causes a 2 percentage point increase in a child’s propensity tohave an RESP account overall and a 3.7 percentage point increase among those with educationsavings. These effects translate into a 6 % increase in RESP take up rate when compared to theaverage proportion of children with RESPs. In terms of percentage increase, the results suggestthat the effect of the incentive on the use of RESPs is similar for children in low-income families(income less than $65,500), who are generally less likely to use RESPs, compared to those inhigh-income families (income greater than $65,500).In addition to encouraging parents to use RESPs to accumulate education savings for their child,the CESG also has a considerable impact on the amount of savings in a child’s RESP account.Table 4.6 presents the estimated effects of the CESG saving incentive on a child’s amount ofRESP savings across all three estimation samples and by family income groups. Based on theentire sample, a $1,000 increase in eligible CESG is associated with a $716 increase in RESPsavings among all children and a $1,059 increase in RESP savings among children with educationsavings of any kind. These effects are very large in comparison to the average amount of RESPsavings among all children ($2,413) and among those with education savings ($4,561). The resultsin panels B and C suggest that the CESG incentive has heterogeneous effects across incomegroups: a $1,000 increase in eligible CESG is associated with an increase in RESP savings ofapproximately $367 for all children from lower-income families compared with a $898 increase forall those from higher-income families. In addition, the estimates based on the restricted sample(1999-2007) are similar in magnitude, although the ones based solely on school-aged children aremuch lower, suggesting that the CESG incentive had a larger impact on younger children than110See Table D.1 in Appendix D for the regression coefficients associated with these demographic controls whenmodelling savings in RESPs specifically.1274.5. Empirical Resultson older ones.111As well as being informative about parents’ saving response to the CESG incentive, the resultsin Table 4.6 also represent the first stage estimation of the IV strategy employed in this study(equation 2). Based on the entire sample (1999-2012) and the restricted sample (1999-2007),the predictive power of the CESG incentive is very strong both overall and by income groups,with F-statistics ranging from 22.2 to 184.5 (columns 1 to 4). Using the CESG incentive as aninstrumental variable for RESP savings therefore satisfies the instrument relevance condition.112The third sample, which includes only school-aged children (ages 6 to 17), is used later in theanalysis to examine the impact of RESP savings on children’s school grades in section 4.5.3(columns 5 and 6). When estimating the first stage equation on this sample, the predictivepower of the CESG incentive is reduced, indicating that its effect is much stronger for youngerchildren than for school-aged children. Due to the poor performance of the CESG incentiveby income group on this sample, I do not perform subgroup analyses by family income whenstudying the relationship between RESP savings and academic outcomes.Crowding-Out Effects of RESP Savings on Other Education SavingsFrom a policy perspective, measuring the effect of the CESG incentive on RESP savings isuseful, but understanding how it affects overall education savings is the more relevant questionto accurately evaluate the impacts of the program. I therefore examine next the crowding-outeffects of increased RESP savings due to the CESG incentive on other types of education savings.As a first step, I examine whether RESP savings have an impact on a child’s likelihood of havingsavings in other types of saving vehicles.113 Columns 1 and 2 of Table 4.7 show that there isa positive correlation between the use of RESPs and the use of other types of saving vehiclesamong all children. In contrast, the IV estimates in columns 3 and 4 suggest a negative impactof RESP savings on a child’s probability of having other types of education savings. Amongall children, a $1,000 increase in RESP savings causes on average a 1.6 to 1.8 percentage pointdecrease in the use of other saving vehicles. Combining this result with the increased take up ofRESPs identified earlier, this suggests that parents are switching from using other types of savingvehicles to RESPs in response to higher RESP saving incentives. When restricting the sample to111One concern could be that the costs of raising a child increase as children grow older. This would imply thatthe portion of the family budget available for RESPs may decline with the age of the child, which could bias theresults. I address this concern by including age fixed effects in the model specification.112As a general rule of thumb, an instrument is strong enough (i.e., satisfies the relevance condition) if it has anF-statistic above 10 (Staiger and Stock, 1997). More recently, Stock and Yogo (2002) proposed a more stringenttest of the strength of the instrument based on the maximum Wald test size distortion. The values of the F-statistics in Table 4.6 exceed the Stock and Yogo (2002) critical value of 16.38 for all samples, except for thesample of school-aged children.113The estimation is based on the entire sample (1999-2012). I also present the estimated effects of RESP savingson the use of other types of education saving vehicles based the restricted sample (1999-2012) in Table D.2 ofAppendix D. The results are similar.1284.5. Empirical Resultschildren with education savings, evidence of this switching behaviour is even stronger. Amongthis group, children are 3.4 percentage points less likely to have other types of education savingsfor every $1,000 increase in RESP savings (Table 4.7, panel A, columns 7 and 8).114 Furthermore,the results in panels B and C of Table 4.7 indicate that both low- and high-income families areless likely to use other types of education savings in response to RESP savings, with somewhatlarger effects among low-income families. It is noteworthy to point out that the opposite signof the LPM/Probit (in columns 1 and 2) and IV estimates (in columns 3 and 4) suggests thatinterpreting the LPM or Probit results as causal estimates without using an instrument wouldlead to erroneous conclusions. This is probably due to an omitted variable bias resulting, fromfor example, parents who use RESPs being likely to also use other types of saving vehicles dueto their general strong preferences for education savings.To further explore the extent of crowding-out effects between RESP and other types of educationsavings, I also evaluate the effects of RESP savings on a child’s amount of other education savings(Table 4.8). This analysis is solely performed on the sample restricted to pre-2012 data due tomissing information on a child’s amount of other savings in 2012. The estimation results indicatean overall slight negative correlation between RESP savings and other savings when using anOLS or Tobit model (panel A, columns 1 and 2) but no significant crowding-out effects whenusing an IV approach (panel A, columns 3 and 4). When restricting the sample to children witheducation savings, I find strong evidence of crowding-out effects. For every dollar invested in achild’s RESP account, a child’s average amount of other savings is reduced by 28 to 34 centsdepending on the specification.One might find the absence of statistically significant IV estimates of crowding-out effects mea-sured on all children, including those without education savings, mighty strange (Table 4.8,columns 3 and 4). This insignificant effect is probably due to the fact that 50% of children haveneither RESP savings nor other education savings, leading to an estimate of zero crowding-outfor those children and greatly affecting the overall results. In addition, when including both chil-dren with and without savings in the sample, the strength of the instrument is reduced, leadingto larger standard errors. Although restricting the sample to children with education savings isbased on an endogenous criterion – because the instrument could theoretically affect the sampleselection – I believe that the results are still informative since I showed in Table 4.3 that theCESG has no effect on this extensive margin.Based on the point estimates in columns 7 and 8, crowding-out effects seem slightly larger forchildren from high-income families (between 33 and 42 cents) than for children from low-income114Making the effects comparable in terms of the CESG incentive, they translate into children with educationsavings being approximately 3.6 percentage point less likely to have other savings compared to 3.7 percentagepoint more likely to have RESP savings for every $1,000 in CESG incentive. These estimates are based on i)the 0.037 estimate of the effect of a $1,000 in CESG on RESP take up (Table 4.5, panel A, column 3), and ii)the reduced form estimate of the effect of a $1,000 in CESG on other saving take up. The latter is obtained bymultiplying -3.4 (Table 4.7, panel A, column 7) by 1.059 (Table 4.6, panel A, column 2), which equals -3.6.1294.5. Empirical Resultsfamilies (approximately 34 cents), which is consistent with the patterns found by Gale (1998) andChetty et al. (2012), although this difference is not statistically significant due to large standarderrors. One possible explanation for these heterogeneous effects is that since high-income familiestend to save larger amounts regardless of the incentives in place, it is easy for them to switchsavings from one account to another in order to meet the annual RESP contribution limit subjectto the CESG. On the other hand, if modest-income families did not save much prior to theintroduction of the CESG, then this new incentive is more likely to create additional savings.One concern is that the empirical results may underestimate the crowding-out effects betweenRESP savings and other types of education savings due to the mechanical 20% increase in RESPsavings resulting from the CESG saving incentive. For example, if parents simply transfer con-tributions from a non-RESP account to an RESP account without making any adjustments tothe amount of contributions, then other savings would mechanically decrease to 83.3% of RESPsavings due to the 20% basic CESG added to RESP contributions.115 In terms of parents’ contri-butions, however, the crowding-out effect should be equal to 100%. Under the assumption thatparents do not reduce their contributions to RESPs in response to the incentive, the estimatedcrowding-out effects in Table 4.8 should therefore be seen as a lower bound to account for the ad-ditional 20% basic CESG.116 To obtain estimates of crowding-out effects based on contributions,one should multiply all estimates in Table 4.8 by 1.2. Even when accounting for this possiblebehaviour, however, the measured crowding-out effects of other savings are far from being largeenough to completely offset savings in RESPs.Finally, an alternative approach to analyse crowding-out effects in this context is to measure theimpact of RESP savings on total education savings (Table 4.9). In accordance with the resultspresented in Table 4.8, I find that that among children with education savings, a $1 increasein RESP savings leads to a $0.66 increase in total savings. This suggests some crowding outof other types of education savings due to RESP savings, but nevertheless a significant positiveeffect of the CESG saving incentive on total education savings among savers.4.5.3 The Effects of RESP Savings on Children’s Academic PerformanceBecause encouraging savings in education savings accounts constitutes a long-term approach topost-secondary education financing, RESP savings could have an early impact on children before115The value of 83% is obtained as follows. When transferring an amount x from other savings to an RESPaccount (up to the contribution limit), other savings decrease by x whereas RESP savings increase by x + 0.2x.The “mechanical” crowding-out effect is thus equal to −x/(x+ 0.2x) = −0.833.116According to neoclassical economic theory, parents may reduce their contributions to RESPs in response to a20% return on contributions if the income effect of this increased return on savings is larger than the substitutioneffect. According to the results of the previous chapter, however, it is unlikely that parents would decrease theirRESP contributions due to the basic CESG. The results suggest that parents are likely to have a “behaviouralresponse” and may actually increase their RESP contributions due to a higher matching rate on contributions(see chapter 3 of this dissertation).1304.5. Empirical Resultsthey make the decision to attend a college or university. To examine whether RESP savings affectchildren’s level of preparation for post-secondary education, I measure their effect on children’sperformance in school. Although not the only contributing factor, academic performance is animportant factor that influences whether students are accepted in a higher education programonce they finish high school. As a measure of school performance, I use parents’ reported measureon whether their child’s grades are below average, average, or above average. Estimating anOrdered Logit model, I find a small, but significantly positive relationship between a child’samount of RESP savings and academic performance (Table 4.10). A $1,000 increase in RESPsavings is associated with a 0.3 percentage point decrease in a child’s likelihood of being belowaverage and a 0.6 percentage point increase in a child’s likelihood of being above average.117 Inorder to understand whether this relationship is causal, I use an Ordered Logit IV estimationstrategy based on the control function approach described in section 4.4.2.118 The results aregenerally noisy, rendering all estimates insignificant. I therefore cannot conclude that RESPsavings have an impact on children’s academic performance at the elementary and secondarylevels.4.5.4 Limitations of the Analysis and Potential Threats to IdentificationThe estimation results are generally robust to the choice of specification and sample selection,although they are subject to certain data limitations. This section explains these limitations andaddresses several concerns including potential threats to identification. Appendix D presents theresults of various robustness tests for the main results of the paper, both for crowding-out effectsof other education savings due to RESP savings (Tables D.4 to D.7) and the effects of RESPsavings on children’s academic achievement (Tables D.8 and D.9).A first limitation of this analysis stems from the data only providing information on a child’samount of parental education savings. Some children may also have education savings fromsources other than their parents such as other relatives or friends, which could create a problemif the effects of the CESG saving incentive on RESP savings vary by contributor type. Forexample, if parents respond to this incentive more strongly than other contributors, there couldbe some crowding-out of education savings across contributor types instead of solely across typesof saving vehicles. This situation could bias my results due to the lack of information on non-parental savings. The IV estimates therefore rely on the assumption that the CESG incentiveaffected all types of contributors in the same way, regardless of whether they were the parents,friends or other relatives of the child. Although the data does not provide any information on117The positive correlation between RESP savings and grades is not simply due to grade inflation over time.I include year by province fixed effects in the regression model in order to control for the possibility of thisconfounding factor, which would be correlated with increased CESG incentive amounts over time.118The results are very similar when using Ordered Probit and IV Ordered Probit models instead of OrderedLogit and IV Ordered Logit models to study the relationship between RESP savings and children’s academicperformance.1314.5. Empirical Resultsthe amount of education savings from sources other than parents, it does provide an indicatorvariable for whether the child has education savings from other sources. I find very little impactof the CESG incentive on this extensive margin, which provides some evidence that the crowding-out effects are not simply a reflection of changes in the type of contributors to the child’s RESP(Table D.3 in Appendix D).Second, although I examined whether crowding-out effects are heterogeneous across incomegroups, these effects may also vary in other dimensions. For example, parental education isanother important factor that is strongly related to both children’s levels of education savingsand children’s propensity to pursue post-secondary studies. If parents’ own levels of educationalattainment affect how much they value higher education for their child, evaluating how theirsaving behaviour differs across this margin may be useful to understand, for instance, a po-tential cause of limited intergenerational education mobility. I therefore examine whether thecrowding-out effects of RESP savings on other education savings are heterogeneous across par-ents’ educational attainment. I separate the sample into two categories: children with parentswho do not have a post-secondary education degree (the lower educated group) and childrenwith at least one parent who completed a post-secondary education degree (the highly educatedgroup). The results of this exercise presented in Table D.4 are very similar to the heterogeneouseffects measured by family income groups, which is not surprising since parents’ education isstrongly related to family income. Probably due to much smaller sample sizes, the instrumentis quite weak among children with lower-educated parents. Within this group, the first stageF-statistics are smaller than 10, which can lead to inconsistent IV estimates (Staiger and Stock,1997). The IV estimates for children of lower-educated parents should thus be interpreted withcaution.A third concern stems from potential threats to the validity of the instrument. As previouslydiscussed, the instrumental variable (IV) approach employed in this study relies heavily on theassumption that the instrument (the CESG saving incentive) is related to the outcome examined(other education savings or the child’s academic performance) solely through increased RESPsavings. If this exogeneity assumption is violated, than the estimated causal impacts of RESPsavings may be biased. This assumption could be violated if other unobserved factors are relatedto the saving behaviour of parents or to their child’s school performance vary in the same manneras the CESG amounts over time and across birth cohorts. For example, one could imaginethat parents’ saving behaviour is strongly influenced by their perceived or predicted cost ofpost-secondary education once their child reaches young adulthood. This perceived cost couldincrease over time across cohorts in a way that is correlated with the increasing amounts ofCESG, thereby confounding the results. To address this concern, I include in all specificationsa control variable for the average provincial tuition of an undergraduate university degree wheneach child was born, which is presumably a good proxy for parents’ predicted costs of their child’shigher education degree.1324.5. Empirical ResultsParents’ change in employment status could constitute another possible confounding factor. Onecould be concerned that parents’ employment status varied over time and children’s age groups inthe same pattern as CESG amounts. Although this variation would be partly reflected in familyincome, which I control for in the main analysis, it could also impact parents’ saving behaviourthrough other channels such as their level of risk aversion. Furthermore, some studies have foundthat a mother’s educational attainment is a better predictor of a child’s educational attainmentthan the father’s educational attainment (Chevalier, 2004; Bingley, Christensen and Jensen,2009). If this affects the saving behaviour of parents or the child’s academic performance, thencontrolling separately for each parents’ educational attainment instead of using a single indexfor both parents would control for any important changes in mothers’ educational attainmentover the last 15 years. To mitigate these concerns and test that the results are robust to a moredemanding model specification, I preform the analysis including additional control variablesto the baseline specification. This specification includes each parent’s educational attainment,parents’ unemployment status, an indicator variable for whether a child spoke a language otherthan an official language at home, and a variable indicating if the family resides in a ruralarea.119 These additional variables were not included in the original specification due to theirlarge number of missing values. In order to allow the inclusion of both parents’ educationalattainment separately instead of using their combined highest educational attainment, I restrictthe sample to children in two-parent households. This sample restriction renders the four cross-sections more comparable across all years since the 2008 ASETS data contains an unusually largenumber of two-parent households due to missing values. Table D.5 presents the main estimatedeffects on parents’ saving behaviour, which are not sensitive to this different specification andsample definition.Another potential issue with the main analysis results stems from the definition of the instrument,which relies only on the basic CESG. The instrument therefore does not pick up all of the otherRESP saving incentives, which may also affect parents’ investment decisions in RESPs. To theextent that these other incentives are positively correlated to the basic CESG and that all theincentives affect the saving behaviour of parents in the same direction (none of them decreasea child’s expected amount of savings in RESPs), which is very likely to be the case, then usingonly the basic CESG as an instrument should provide valid causal estimates.120 Nonetheless, toverify that the results are not sensitive to this choice of instrument, I also perform the analysisusing a different incentive measure as the instrument, which includes all federal and provincial119Milligan (2005) presents evidence that immigrant status is a strong indicator of RESP participation in Canada.Unfortunately, information on immigrant status is not consistently available in all four datasets. As a proxy, Iinclude in this specification a variable indicating if the child spoke a language other than French or English athome.120The IV approach provides causal estimates of the local average treatment effect (LATE), that is the effectfor the compliers whose behaviour was modified by the instrument (Imbens and Angrist, 1994; Imbens andWooldridge, 2009). If the compliers among parents adjust their saving behaviour in RESPs in the same directionfor both measures of the incentive (i.e., the effect of the two saving incentive measures on RESP savings ispositive), then both IV definitions should be valid.1334.5. Empirical Resultssaving incentives. Specifically, this alternative instrument includes the basic CESG, the A-CESGfor low- and middle-income families, the CLB for low-income families, as well as the Alberta andQuebec incentives.121 The advantage of this measure is that it relies on additional sources ofvariation based on the child’s province of residence, the year and family income. This is alsoa disadvantage since eligibility for the programs varies over time due to potential migrationbetween provinces and variations in family income. To identify each child’s exact amount ofeligible saving incentive, I would therefore ideally need information on where each child has livedsince birth as well as information on the child’s past yearly values of family income, which is arenot available in the data. To assign values of each saving incentive to each child, I assume thatchildren living in a certain province at the time of the survey remained in that province theirentire lives and that children’s family income was relatively constant over their lifetime. Due tothese two fairly strong assumptions, the values of this second instrument are thus noisier, whichmay explain why the first stage estimates based on this instrument are slightly weaker than thosebased on the original instrument. The IV estimates of this third robustness test based on thisalternative instrument definition are comparable to the baseline estimates (Table D.6).Finally, I also use a different IV model specification to ensure that the results are not driven bythe baseline choice of functional form. Up until this point, I used an OLS specification as thefirst stage of the IV empirical approach. Because a large number of children have zero RESPsavings, using a censored regression model may better capture the impact of the incentive on achild’s amount of RESP savings. As a final robustness test, I therefore use a Tobit model insteadof an OLS model for the first stage regression of the IV estimation. This technique is analogousto the control function approach presented in section 4.4.2 with the only difference being thatthe residuals are calculated based on the Tobit estimates obtained in the first stage regression.The results in Table D.7 present evidence that the estimated crowding-out effects are also robustto this exercise.The smaller number of school age children in the data limits the estimation of the impact ofRESP savings on children’s academic outcomes. Due to this smaller sample, which often leads toweak IVs, I cannot perform the same specification and sample selection modifications as the oneson the first set of results. Table D.8 presents the IV results using a Tobit model as the first stageand an Ordered Logit model as a second change. The results remain noisy and insignificant. Toobtain the estimates presented in Table D.9, I use a different model to measure the impact ofRESP savings on academic performance. I evaluate the impact of RESP savings on a child’sprobability of being above average (columns 1 to 4) and on a child’s probability of being belowaverage (columns 5 to 8) using Linear Probability and Probit models. Once again, the resultsshow a correlation between RESP savings and academic achievement, but no evidence of a causalimpact.121The provinces of Saskatchewan and BC only introduced their saving incentive programs as of 2013, which isoutside of the sample period in this study.1344.6. Conclusion4.6 ConclusionIt is widely believed that one of the main factors limiting universal access to post-secondaryeducation is its high cost at a time when young adults usually have limited means. One approachto address this issue is to motivate parents to help their children financially by encouragingparents to start saving early on for their children’s post-secondary education. Few empiricalstudies to date have evaluated the effectiveness of such a policy.A first step in this evaluation is to measure the extent of crowding-out effects in the context ofparents saving for their child’s post-secondary education. In this paper, I analyze these effectsby exploiting the Canadian introduction of a policy that encourages parents to contribute totargeted education savings accounts by offering saving incentives. Based on an instrumentalvariable approach, the results of the analysis are clear. I do not find any evidence that tax-favoured education savings accounts offering saving incentives, such as a 20% matching rate oncontributions, affect parents’ decision on the extensive margin to save for their child’s education.Among parents who do choose to save, however, I find that savings in incentivised educationsavings accounts only partially crowded out other types of education savings, implying thatchildren benefit from up to 66% higher total education savings due to these incentives. Moreover,these positive effects on the intensive margin are observed for both low- and high-income families.Compared with other post-secondary education financing strategies, one of the advantages ofencouraging education saving is the long-term aspect of this approach, which could induce chil-dren to better prepare for post-secondary education if they are aware of their parents’ efforts.Although children with savings in targeted education savings accounts generally perform betterin school, I find no evidence of a causal relationship between education savings and children’sacademic grades in elementary and secondary school.The results of this study are informative, as they clearly show that incentivised education savingsaccounts such as RESPs can be very effective in increasing overall education saving amountsamong parents inclined to save. In particular, in light of these results, the effects of the CLBsubsidy and the higher A-CESG matching rate estimated in the previous chapter likely increasedoverall education savings through higher RESP contributions among those who applied for theseprograms. To fully evaluate the performance of such policies, however, future research shouldbe conducted on measuring the long-term consequences of increased education savings on post-secondary enrolment and completion rates.Such a comprehensive evaluation should include studying the interactions between the CanadaEducation Savings Program and other publicly offered education financing policies, such as theCanada Student Loans Program, Canada Student Grants, education income tax credits, as wellas other provincial financial support programs for post-secondary education. If, for example,children from low-income families with a certain level of RESP savings are no longer eligible for1354.7. Figuresuniversity or college need-based bursaries, this could create a disincentive for low-income familiesto accumulate RESP savings. In Canada, the implications of RESP withdrawals on students’eligibility for financial aid programs vary substantially across provinces (Essaji and Neill, 2012).Furthermore, in addition to potentially affecting the demand for higher education, subsidisingpost-secondary education through saving incentive programs could have consequences on thesupply of education by institutions, resulting in, for example, higher tuition fees. Between theinception of the CESP in 1998 and 2008, real tuition fees have risen by 26 percent on averageacross Canada. When accounting for large expansions in tax credits (both at the federal andprovincial level) and increases in student aid over the same period, however, net tuition fees haveincreased much less (Usher and Duncan, 2008; The Canada Millennium Scholarship Foundation,2009). Overall, it is therefore crucial to consider the long-term effects of policies encouragingparental education savings on post-secondary education participation in conjunction with otherfinancial assistance programs and the response of institutions to such policies.4.7 FiguresFigure 4.1: Proportion of Childrenwith Education Savings by Saving Vehicle over Time0.170.300.410.270.380.500.430.370.610.450.410.620.00.20.40.60.81.0Proportion of children1999 2002 2007 2012RESP savings Other savings (non-RESP)Any type of education savingsNote: The proportions of children with RESP savings and with other types of savingsare not mutually exclusive, which explains why they do not add up to the proportion ofchildren with overall education savings of any type.1364.7. FiguresFigure 4.2: Average Amount of Savingsby Saving Vehicle Among All Children over Time8111,8311,6642,1173,4031,9334,13201,0002,0003,0004,0005,0006,0007,0008,0009,000Average amount of savings (in constant 2012 dollars)1999 2002 2007 2012RESP savings Other savings (non-RESP)Note: The data provides no information on other types of savings (non-RESP savings)in 2012.Figure 4.3: Average Amount of Savings by Saving VehicleAmong Children with Education Savings over Time1,7934,1583,0684,0245,2623,0666,16901,0002,0003,0004,0005,0006,0007,0008,0009,000Average amount of savings (in constant 2012 dollars)1999 2002 2007 2012RESP savings Other savings (non-RESP)Note: The data provides no information on other types of savings (non-RESP savings)in 2012.1374.7. FiguresFigure 4.4: Average Total Education Savings by Family Income (1999-2007)01,0002,0003,0004,0005,0006,0007,0008,0009,00010,00011,000Amount of savings (in constant 2012 dollars)0.00.10.20.30.40.50.60.70.80.91.0Proportion0-13,09913,100-19,64919,650-26,19926,200-39,29939,300-52,39952,400-65,49965,500-78,59978,600-104,799104,800 or moreProportion of children with education savingsAmount of education savings (among those with savings)Note: The numbers are based on the restricted sample (1999-2007) because informa-tion on total savings is not available in 2012.Figure 4.5: Average Total Education Savingsby Parental Education Attainement (1999-2007)01,0002,0003,0004,0005,0006,0007,0008,0009,00010,000Amount of savings (in constant 2012 dollars)0.00.10.20.30.40.50.60.70.80.91.0ProportionLess than high school High School Some post-sec. Post-sec. degreeProportion of children with education savingsAmount of education savings (among those with savings)Note: The numbers are based on the restricted sample (1999-2007) because informa-tion on total savings is not available in 2012.1384.7. FiguresFigure 4.6: Reported Academic Performance (School Grades)of Children over Time0.080.460.460.180.360.460.130.290.580.090.290.610.00.20.40.60.81.0Proportion of children1999 2002 2008 2013Below average Average Above averageFigure 4.7: Maximum Cumulative Nominal Amountof Basic CESG Elligble to Children by Age Group over Time01,0002,0003,0004,0005,0006,0007,000Amount of basic CESG0 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17199901,0002,0003,0004,0005,0006,0007,000Amount of basic CESG0 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17200201,0002,0003,0004,0005,0006,0007,000Amount of basic CESG0 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 17200701,0002,0003,0004,0005,0006,0007,000Amount of basic CESG0 1 2 3 4 5 6 7 8 9 10 11 12 13 14 15 16 1720121394.8. Tables4.8 TablesTable 4.1: Demographic Characteristics of Children in the Sample by Cross-Section1999 2002 2007 2012 Overallmean s.e. mean s.e. mean s.e. mean s.e. mean s.e.Age 8.8 (0.048) 8.9 (0.073) 8.1 (0.084) 8.4 (0.081) 8.6 (0.036)Female 0.490 (0.005) 0.486 (0.007) 0.491 (0.008) 0.487 (0.008) 0.488 (0.004)Two-parent household 0.828 (0.004) 0.778 (0.006) 0.987 (0.002) 0.787 (0.006) 0.837 (0.003)Province of residenceNewfoundland & Lab. 0.017 (0.001) 0.016 (0.001) 0.014 (0.001) 0.014 (0.001) 0.015 (0.000)Prince Edward Island 0.005 (0.000) 0.005 (0.000) 0.004 (0.000) 0.004 (0.000) 0.005 (0.000)Nova Scotia 0.030 (0.001) 0.029 (0.001) 0.026 (0.002) 0.024 (0.001) 0.027 (0.001)New Brunswick 0.024 (0.001) 0.023 (0.001) 0.019 (0.001) 0.021 (0.001) 0.022 (0.001)Quebec 0.234 (0.004) 0.228 (0.007) 0.227 (0.007) 0.229 (0.007) 0.230 (0.003)Ontario 0.384 (0.005) 0.398 (0.007) 0.410 (0.008) 0.392 (0.008) 0.395 (0.004)Manitoba 0.038 (0.001) 0.038 (0.002) 0.036 (0.002) 0.038 (0.002) 0.038 (0.001)Saskatchewan 0.036 (0.001) 0.034 (0.002) 0.029 (0.002) 0.034 (0.002) 0.034 (0.001)Alberta 0.106 (0.003) 0.108 (0.004) 0.110 (0.005) 0.127 (0.005) 0.113 (0.002)British Columbia 0.126 (0.003) 0.122 (0.005) 0.125 (0.006) 0.117 (0.005) 0.122 (0.002)Number of children in the householdOne child 0.209 (0.004) 0.230 (0.005) 0.156 (0.005) 0.238 (0.005) 0.211 (0.002)Two children 0.457 (0.005) 0.472 (0.004) 0.495 (0.008) 0.464 (0.008) 0.471 (0.004)Three children or more 0.334 (0.005) 0.299 (0.007) 0.349 (0.008) 0.297 (0.008) 0.318 (0.004)Parents’ highest education attainmentLess than high-school 0.091 (0.003) 0.083 (0.004) 0.010 (0.002) 0.052 (0.004) 0.062 (0.002)High-school degree 0.144 (0.003) 0.145 (0.005) 0.086 (0.005) 0.099 (0.005) 0.121 (0.002)Some post-sec. educ. 0.075 (0.002) 0.196 (0.006) 0.047 (0.003) 0.138 (0.005) 0.118 (0.002)Post-secondary degree 0.689 (0.004) 0.576 (0.576) 0.858 (0.006) 0.710 (0.007) 0.699 (0.003)Parents own their home 0.744 (0.004) 0.739 (0.007) 0.860 (0.006) 0.747 (0.767) 0.767 (0.003)Family income (constant 2012 dollars)$0 - $13,099 0.019 (0.001) 0.033 (0.003) 0.013 (0.002) 0.031 (0.003) 0.024 (0.001)$13,100 - $19,649 0.059 (0.002) 0.066 (0.004) 0.010 (0.002) 0.031 (0.003) 0.044 (0.001)$19,650 - $26,199 0.064 (0.002) 0.062 (0.004) 0.023 (0.003) 0.056 (0.004) 0.053 (0.002)$26,200 - $39,299 0.105 (0.003) 0.125 (0.005) 0.063 (0.004) 0.091 (0.005) 0.098 (0.002)$39,300 - $52,399 0.139 (0.003) 0.114 (0.005) 0.085 (0.005) 0.110 (0.005) 0.114 (0.002)$52,400 - $65,499 0.117 (0.003) 0.106 (0.004) 0.126 (0.005) 0.096 (0.005) 0.111 (0.002)$65,500 - $78,599 0.154 (0.003) 0.108 (0.004) 0.091 (0.005) 0.080 (0.004) 0.110 (0.002)$78,600 - $104,799 0.163 (0.003) 0.177 (0.006) 0.206 (0.006) 0.190 (0.006) 0.182 (0.003)$104,800 or more 0.181 (0.004) 0.209 (0.006) 0.383 (0.008) 0.315 (0.008) 0.264 (0.003)Observations 18,699 9,571 5,738 8,495 42,503Source: 1999, 2002 and 2013 cycles of the Survey of Approaches to Education Planning and the 2008 Accessand Support to Education Survey. Means and standard errors were calculated using the survey weights. Thelast row of the table presents the unweighted number of observations.1404.8. TablesTable 4.2: Statistics on Saving Amounts for Children in the Sample (1999-2012)1st 25th 75th 99thMean Percentile Percentile Median Percentile PercentilePanel A: Savings Statistics in 1999RESP savingsAmong all children 811 0 0 0 0 11,528Among those with RESP savings 4,902 110 1,886 3,396 6,288 23,056Other savingsAmong all children 1,831 0 0 0 1,310 23,580Among those with other savings 6,0691 131 1,703 3,930 7,860 30,130Total savingsAmong all children 2,641 0 0 0 3,275 26,200Among those with education savings 6,478 131 1,965 4,585 8,515 28,820Panel B: Savings Statistics in 2002RESP savingsAmong all children 1,664 0 0 0 730 18,255Among those with RESP savings 6,127 162 2,434 4,868 8,519 30,425Other savingsAmong all children 2,117 0 0 0 1,704 24,340Among those with other savings 5,588 122 1,217 3,043 6,694 30,425Total savingsAmong all children 3,781 0 0 0 5,111 30,425Among those with education savings 7,578 122 2,286 5,111 10,953 35,293Panel C: Savings Statistics in 2007RESP savingsAmong all children 3,403 0 0 0 4,366 27,288Among those with RESP savings 7,881 327 2,183 5,458 10,915 32,745Other savingsAmong all children 1,933 0 0 0 1,637 21,830Among those with other savings 5,193 109 1,092 2,729 5,458 32,745Total savingsAmong all children 5,336 0 0 2,182 7,641 32,745Among those with education savings 8,721 218 2,401 5,458 12,007 32,745Panel D: Savings Statistics in 2012RESP savingsAmong all children 4,132 0 0 0 5,000 35,000Among those with RESP savings 9,156 300 2,800 6,0000 12,000 40,000Source: 1999, 2002 and 2013 cycles of the Survey of Approaches to Education Planning and the 2008 Accessand Support to Education Survey. All statistics are calculated using the survey weights. All dollar amountsare expressed in constant 2012 dollars.1414.8. TablesTable 4.3: Effect of the CESG Saving Incentiveon a Child’s Probability of Having Education SavingsEntire sample Restricted sample(1999-2012) (1999-2007)LPM Probit LPM Probit(1) (2) (3) (4)Incentive 0.006 0.005 0.007 0.006(0.005) (0.005) (0.011) (0.010)Average provincial tuition -0.002 -0.001 -0.000 -0.000(0.008) (0.008) (0.008) (0.008)Female 0.010∗ 0.010∗ 0.106∗∗∗ 0.105∗∗∗(0.005) (0.005) (0.010) (0.010)Two-parent household 0.006 0.006 0.003 0.003(0.012) (0.012) (0.013) (0.014)Parents own their home 0.109∗∗∗ 0.106∗∗∗ 0.106∗∗∗ 0.105∗∗∗(0.010) (0.009) (0.010) (0.010)Number of children in the householdTwo-children household -0.022∗∗ -0.023∗∗∗ -0.023∗∗ -0.025∗∗∗(0.008) (0.008) (0.010) (0.009)Three-or-more-children household -0.085∗∗∗ -0.085∗∗∗ -0.097∗∗∗ -0.098∗∗∗(0.014) (0.014) (0.016) (0.016)Parents’ education attainmentHigh school degree 0.078∗∗∗ 0.095∗∗∗ 0.064∗∗∗ 0.085∗∗∗(0.020) (0.023) (0.021) (0.025)Some post-secondary education 0.078∗∗∗ 0.095∗∗∗ 0.060∗∗∗ 0.080∗∗∗(0.017) (0.021) (0.019) (0.024)Post-secondary education degree 0.179∗∗∗ 0.192∗∗∗ 0.161∗∗∗ 0.179∗∗∗(0.016) (0.019) (0.017) (0.021)Family income$13,100 - $19,649 -0.011 -0.019 -0.016 -0.025(0.022) (0.026) (0.018) (0.023)$19,650 - $26,199 0.013 0.014 0.002 0.003(0.021) (0.025) (0.024) (0.030)$26,200 - $39,299 0.050∗∗ 0.056∗∗ 0.043 0.051∗(0.021) (0.023) (0.025) (0.028)$39,300 - $52,399 0.089∗∗∗ 0.093∗∗∗ 0.090∗∗∗ 0.098∗∗∗(0.023) (0.024) (0.024) (0.026)$52,400 - $65,499 0.153∗∗∗ 0.152∗∗∗ 0.141∗∗∗ 0.145∗∗∗(0.022) (0.024) (0.025) (0.027)$65,500 - $78,599 0.140∗∗∗ 0.139∗∗∗ 0.141∗∗∗ 0.145∗∗∗(0.023) (0.024) (0.025) (0.027)$78,600 - $104,799 0.211∗∗∗ 0.202∗∗∗ 0.222∗∗∗ 0.217∗∗∗(0.027) (0.028) (0.028) (0.029)$104,800 or more 0.288∗∗∗ 0.280∗∗∗ 0.287∗∗∗ 0.280∗∗∗(0.024) (0.025) (0.025) (0.027)Proportion of children with savings 0.529 0.497Observations 42,503 34,008Note: The table presents the Linear Probability Model coefficients and the average marginal effects of the Probitregressions. Standard errors are clustered by age group and are reported in parentheses. Symbols ∗∗∗, ∗∗, and∗ denote statistical significance at the 1, 5, and 10 percent levels. All regressions include demographic controlvariables, age fixed effects, and year*province fixed effects. The incentive amount is expressed in units of thousandsof constant 2012 dollars.1424.8. TablesTable 4.4: Effect of the CESG Saving Incentive ona Child’s Probability of Having Education Savings by Income GroupEntire sample Restricted sample(1999-2012) (1999-2007)LPM Probit LPM Probit(1) (2) (3) (4)Panel A: Overall effectsIncentive 0.006 0.005 0.007 0.006(0.005) (0.005) (0.011) (0.010)Proportion of children with savings 0.529 0.497Observations 42,503 34,008Panel B: Effects for low-income families (Income<$65,500)Incentive 0.002 0.002 0.017 0.015(0.007) (0.006) (0.012) (0.010)Proportion of children with savings 0.388 0.359Observations 20,537 16,976Panel C: Effects for high-income families (Income>=$65,500)Incentive 0.009∗ 0.008 0.002 0.001(0.005) (0.005) (0.011) (0.011)Proportion of children with savings 0.642 0.610Observations 21,966 17,032Note: The table presents the Linear Probability Model coefficients and the average marginaleffects of the Probit regressions. Standard errors are clustered by age group and are reportedin parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percentlevels. All regressions include demographic control variables, age fixed effects, and year*provincefixed effects. The incentive amount is expressed in units of thousands of constant 2012 dollars.1434.8. TablesTable 4.5: Effect of the CESG Saving Incentive on a Child’s Probability ofHaving RESP SavingsEntire sample (1999-2012) Restricted sample (1999-2007)All children With educ. All children With educ.savings savingsLPM Probit LPM Probit LPM Probit LPM Probit(1) (2) (3) (4) (5) (6) (7) (8)Panel A: Overall effectsIncentive 0.020∗ 0.024∗∗∗ 0.037∗∗ 0.034∗∗∗ 0.012 0.017∗ 0.024∗∗ 0.021∗∗(0.010) (0.008) (0.013) (0.013) (0.014) (0.009) (0.009) (0.010)Proportion with RESP 0.321 0.607 0.277 0.557Observations 42,503 21,534 34,008 16,337Panel B: Effects for low-income families (Income<$65,500)Incentive 0.013 0.017∗∗ 0.040∗∗∗ 0.040∗∗∗ 0.018 0.022∗∗∗ 0.039∗∗∗ 0.039∗∗∗(0.009) (0.007) (0.013) (0.013) (0.011) (0.007) (0.012) (0.012)Proportion with RESP 0.200 0.514 0.167 0.465Observations 20,537 7,564 16,976 5,950Panel C: Effects for high-income families (Income>=$65,500)Incentive 0.025∗ 0.029∗∗∗ 0.035∗∗ 0.031∗∗ 0.009 0.014 0.017 0.013(0.012) (0.011) (0.015) (0.015) (0.016) (0.014) (0.014) (0.015)Proportion with RESP 0.418 0.651 0.368 0.602Observations 21,966 13,970 17,032 10,387Note: The table presents the Linear Probability Model coefficients and the average marginal effects of the Probit regressions.Standard errors are clustered by age group and are reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statisticalsignificance at the 1, 5, and 10 percent levels. All regressions include demographic control variables, age fixed effects, andyear*province fixed effects. The incentive amount is expressed in units of thousands of constant 2012 dollars.1444.8. TablesTable 4.6: Effect of the CESG Saving Incentive ona Child’s Amount of RESP Savings (First Stage Results)Entire sample Restricted sample School-age children(1999-2012) (1999-2007) (1999-2012)All With educ. All With educ. All With educ.children savings children savings children savingsOLS OLS OLS OLS OLS OLS(1) (2) (3) (4) (5) (6)Panel A: Overall effectsIncentive 0.716∗∗∗ 1.059∗∗∗ 0.713∗∗∗ 1.044∗∗∗ 0.447∗∗∗ 0.718∗∗∗(0.074) (0.078) (0.097) (0.127) (0.129) (0.178)Mean RESP savings 2.413 4.561 1.829 3.689 2.974 5.552F-stat on Incentive 93.1 184.5 53.9 67.1 12.1 16.3Observations 42,503 21,534 34,008 16,337 26,597 13,551Panel B: Effects for low-income families (Income<$65,500)Incentive 0.367∗∗∗ 0.760∗∗∗ 0.422∗∗∗ 0.763∗∗∗ 0.119 0.496∗∗(0.066) (0.081) (0.090) (0.144) (0.133) (0.199)Mean RESP savings 1.155 2.978 0.850 2.367F-stat on Incentive 31.1 87.8 22.2 28.0 0.8 6.2Observations 20,537 7,564 16,976 5,950 12,415 4,526Panel C: Effects for high-income families (Income>=$65,500)Incentive 0.898∗∗∗ 1.148∗∗∗ 0.787∗∗∗ 1.086∗∗∗ 0.630∗∗∗ 0.786∗∗∗(0.093) (0.108) (0.137) (0.185) (0.150) (0.233)Mean RESP savings 3.415 5.323 2.641 4.326F-stat on Incentive 92.8 113.5 33.1 34.5 16.6 11.4Observations 21,966 13,970 17,032 10,387 14,182 9,025Note: The table presents the coefficients of the OLS regressions. Standard errors are clustered by age group andare reported in parentheses. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percentlevels. All regressions include demographic control variables, age fixed effects, and year*province fixed effects.Amounts of incentive and RESP savings are expressed in units of thousands of constant 2012 dollars.1454.8. TablesTable 4.7: Effect of RESP Savings on a Child’s Probability of Having Other Education Savings(Estimated on the Entire 1999-2012 Sample)All children Children with education savingsLPM Probit 2SLS IV Probit LPM Probit 2SLS IV Probit(1) (2) (3) (4) (5) (6) (7) (8)Panel A: Overall effectsRESP savings 0.005∗∗∗ 0.004∗∗∗ -0.016∗∗ -0.018∗∗ -0.020∗∗∗ -0.018∗∗∗ -0.034∗∗∗ -0.035∗∗∗(0.001) (0.001) (0.006) (0.007) (0.001) (0.001) (0.006) (0.007)Prop. with other savings 0.365 0.690Observations 42,503 21,534Panel B: Effects for low-income families (Income<$65,500)RESP savings 0.011∗∗∗ 0.009∗∗∗ -0.037∗∗∗ -0.041∗∗ -0.025∗∗∗ -0.023∗∗∗ -0.060∗∗∗ -0.060∗∗∗(0.002) (0.002) (0.014) (0.017) (0.002) (0.002) (0.011) (0.012)Prop. with other savings 0.275 0.709Observations 20,537 7,564Panel C: Effects for high-income families (Income>=$65,500)RESP savings 0.003∗∗∗ 0.003∗∗∗ -0.012∗ -0.013 -0.018∗∗∗ -0.017∗∗∗ -0.028∗∗∗ -0.029∗∗∗(0.001) (0.001) (0.007) (0.008) (0.001) (0.001) (0.007) (0.007)Prop. with other savings 0.437 0.681Observations 21,966 13,970Note: The table presents the Linear Probability Model and Two-Stage Least Square coefficients as well as the average marginal effectsof the Probit and IV Probit regressions. All standard errors are clustered by age group and are reported in parentheses. Standard errorsfor the IV Probit model are bootstrapped. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percent levels. Allregressions include demographic control variables, age fixed effects, and year*province fixed effects. Amounts of incentive and RESPsavings are expressed in units of thousands of constant 2012 dollars.1464.8. TablesTable 4.8: Effect of RESP Savings on a Child’s Amount of Other Education Savings(Estimated on the 1999-2007 Restricted Sample)All children Children with education savingsOLS Tobit 2SLS IV Tobit OLS Tobit 2SLS IV Tobit(1) (2) (3) (4) (5) (6) (7) (8)Panel A: Overall effectsRESP savings -0.061∗∗∗ -0.017∗∗ 0.039 -0.027 -0.278∗∗∗ -0.317∗∗∗ -0.340∗∗∗ -0.282∗∗∗(0.012) (0.007) (0.063) (0.054) (0.021) (0.015) (0.103) (0.105)Mean other savings 1.962 3.951Observations 34,008 16,337Panel B: Effects for low-income families (Income<$65,500)RESP savings 0.011 0.031∗∗∗ 0.216 0.047 -0.234∗∗∗ -0.307∗∗∗ -0.338 -0.336∗∗(0.013) (0.008) (0.185) (0.140) (0.020) (0.024) (0.209) (0.167)Mean other savings 1.256 3.219Observations 16,976 5,950Panel C: Effects for high-income families (Income>=$65,500)RESP savings -0.083∗∗∗ -0.038∗∗∗ -0.136 -0.107 -0.290∗∗∗ -0.322∗∗∗ -0.417∗∗∗ -0.317∗∗(0.013) (0.010) (0.109) (0.117) (0.023) (0.019) (0.152) (0.152)Mean other savings 2.630 4.308Observations 17,032 10,387Note: The table presents the Linear Probability Model and Two-Stage Least Square coefficients as well as the average marginaleffects for the expected value of the dependent variable of the Tobit and IV Tobit regressions. All standard errors are clusteredby age group and are reported in parentheses. Standard errors for the IV Tobit model are bootstrapped. Symbols ∗∗∗, ∗∗, and∗ denote statistical significance at the 1, 5, and 10 percent levels. All regressions include demographic control variables, agefixed effects, and year*province fixed effects. Amounts of RESP savings and other education savings are expressed in units ofthousands of constant 2012 dollars.1474.8. TablesTable 4.9: Effect of RESP Savings on a Child’sAmount of Overall Education Savings(Estimated on the 1999-2007 Restricted Sample)All children With educ. savingsOLS 2SLS OLS 2SLS(1) (2) (3) (4)Panel A: Overall effectsRESP savings 0.939∗∗∗ 1.039∗∗∗ 0.722∗∗∗ 0.660∗∗∗(0.012) (0.063) (0.021) (0.103)Mean total savings 3.791 7.634Observations 34,008 16,337Panel B: Effects for low-income families (Income<$65,500)RESP savings 1.011∗∗∗ 1.216∗∗∗ 0.766∗∗∗ 0.662∗∗∗(0.013) (0.185) (0.020) (0.209)Mean total savings 2.006 5.585Observations 16,976 5,950Panel C: Effects for high-income families (Income>=$65,500)RESP savings 0.917∗∗∗ 0.864∗∗∗ 0.710∗∗∗ 0.583∗∗∗(0.013) (0.109) (0.023) (0.152)Mean total savings 5.271 8.634Observations 17,032 10,387Note: The table presents the Linear Probability Model and Two-Stage Least Square co-efficients. Standard errors are clustered by age group and are reported in parentheses.Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percent levels.All regressions include demographic control variables, age fixed effects, and year*provincefixed effects. Amounts of RESP savings and total education savings are expressed in unitsof thousands of constant 2012 dollars.1484.8. TablesTable 4.10: Effect of RESP Savings on a Child’s Academic Performance(Estimated on the Sample of School-Aged Children (1999-2012))Dependent variable: Categorical measure of academic performanceOrdered Logit IV Ordered LogitBelow Average Above Below Average Aboveaverage average average average(1) (2) (3) (4) (5) (6)Panel A: All childrenRESP savings -0.003∗∗∗ -0.003∗∗∗ 0.006∗∗∗ 0.016 0.019 -0.035(0.000) (0.000) (0.001) (0.059) (0.065) (0.125)Proportion in each category 0.121 0.358 0.522 0.121 0.358 0.522Observations 26,597 26,597Panel B: Children with education savingsRESP savings -0.001∗∗∗ -0.002∗∗∗ 0.004∗∗∗ 0.005 0.009 -0.014(0.000) (0.001) (0.001) (0.010) (0.018) (0.028)Proportion in each category 0.088 0.321 0.591 0.088 0.321 0.591Observations 13,551 13,551Note: The table presents the average marginal effects of the Ordered Logit and IV Ordered Logit regressions.The dependent variable is a categorical measure of performance (above average, average, below average). Allstandard errors are clustered by age group and are reported in parentheses. Standard errors for the IV OrderedLogit model are bootstrapped. Symbols ∗∗∗, ∗∗, and ∗ denote statistical significance at the 1, 5, and 10 percentlevels. All regressions include demographic control variables, age fixed effects, and year*province fixed effects.Amounts of RESP savings are expressed in units of thousands of constant 2012 dollars.149Chapter 5ConclusionThis dissertation contributes to the literature on the economics of education by analysing theconsequences of the introduction of public policies related to language of instruction and savingincentives for post-secondary education in Canada. Chapter 2 provides a first examinationof the causal economic impact of requiring that immigrant children obtain their primary andsecondary education in the language of the majority. In particular, I study the effects of theimplementation of Bill 101 in Quebec, a law that compelled most children to attend primaryand secondary school in French. On the one hand, the results suggest that individuals who weremandated to attend school in French are much more likely than their peers to use French at homeand in their workplace. I estimate that the law led to a significant increase in the probabilityof immigrants being employed or in school, being part of the labour force, and choosing to liveoutside of the Montreal metropolitan area. On the other hand, Bill 101 also caused some familiesto leave the province shortly after its introduction to avoid sending their children to school inFrench, especially families with highly educated and high-income parents. The province as awhole therefore lost some highly skilled workers to other provinces, while the economic prospectsof the children of immigrant families choosing to remain in Quebec improved.In chapters 3 and 4, I evaluate various saving incentive programs on parents’ saving behaviourfor their child’s post-secondary education. I take advantage of the introduction of federal andprovincial Canadian saving incentive programs that aim to increase savings in incentivised tax-favoured education savings accounts known as Registered Education Savings Plans (RESPs). Inchapter 3, I establish that saving incentives can lead to additional savings in RESPs, especiallyamong low-income families. Furthermore, initial subsidies to the account led to parents startingto save earlier for their child in RESPs. Overall, parents’ behaviour is generally consistent withthe predictions of the procrastination saving model from the behavioural economics literature.The research in chapter 4 complements the work in chapter 3 by measuring the crowding-outeffects of savings in RESPs on other types of education savings. Although I find no effects ofincentives on parents’ decision to start saving for their child’s education, among parents whodo save for this purpose, I find that RESP savings increase total education savings by up to66%, suggesting the presence of a small but significant crowding-out effect. I find, however, noevidence of a causal impact of RESP savings on children’s level of preparation for post-secondaryeducation, as measured by their academic grades in elementary and secondary school.150Chapter 5. ConclusionOverall, the three essays of this dissertation emphasize the importance of parents’ role in makingchoices for their child’s education. Parents make decisions such as the language in which theirchild will attend school or how much they save for their child’s college or university education. Ipresent compelling evidence that public policies can greatly influence these decisions, which mayhave huge impacts both in the short run and the long run. Evaluating the effects of these policiesin terms of both their intended and unintended consequences is thus crucial to obtain a compre-hensive understanding of their implications for parents, their children, and society as a whole.Furthermore, from a practical point of view, this dissertation also highlights the importanceof the empirical instruments and techniques needed for empirical economic policy evaluations.Throughout this thesis, I use a variety of data sources and econometric techniques to obtaincausal estimates of the effects of such policies. Whereas the empirical analyses in chapter 2 relyon Census data, those in chapter 3 are based on an administrative dataset, and I use survey datain chapter 4. The empirical approaches that I employ include difference-in-differences designs,regression discontinuity designs, panel data regressions and instrumental variable techniques, allof which are useful tools in empirical microeconomics and public economics research.Finally, the findings of this thesis lead to important avenues for future research. First, to drawa more complete picture of the long-term effects of mandatory schooling in the language of themajority, one could examine the impacts of Bill 101 on other socio-economic outcomes, suchas family structure, social networks, and immigrants’ cultural capital loss or accumulation. Inaddition, this law may have repercussions for third and fourth generation immigrants in Quebec,which could also be assessed in a few years. Second, to fully evaluate the costs and benefits ofeducation saving incentive programs, further research should be conducted on whether RESPsavings have a causal impact on post-secondary enrolment and completion rates in Canada. IfRESP savings alleviate the financial constraints faced by young adults with respect to post-secondary education attainment, the program could be an effective way to help families financepost-secondary education. Another potential research avenue would be to analyse the interac-tions between RESP savings and other education financial support policies such as student loans,scholarships, and bursaries. Public policies are rarely implemented in isolation and it is impor-tant, in this case, to take into consideration other policies already in place that could impactpost-secondary education in Canada. 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