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The Yale Journal of Economics Spring 2013
Volume 1, Issue 1
Staff Editor in Chief David Burt Managing Editor Antonia Woodford Associate Editors Jimin He Isaac Park Moss Weinstock Copy Editor James Austin Schaefer Production and Design Editors Baobao Zhang Yoonji Woo Publishers James Lu Iva Velickovic
The Yale Journal of Economics Spring 2013 Volume 1, Issue 1 New Haven, Connecticut Website: http://econjournal.sites.yale.edu/
Table of Contents Editorsâ€™ Note
Geoffrey A. Barnes (Yale)
Formal Education as a Determinant of Rural Out-migration: Evidence from Rural India
Jenny Shen (MIT)
Does the Availability of Music Streaming Products Decrease Rates of Music Piracy? Evidence from Google Trends
Noam Angrist (MIT)
Does Merit Pay Pay? The Impact of Tipped Minimum Wage Shifts on Earnings, Employment, and Incentives
Jasmine Barrett (Yale)
An Economic Analysis of Intermarriage between American Indian Women and European Fur Traders
Lauren Zumbach (Princeton)
Do Laptops Improve Student Performance?
Marc Beck (Yale)
Exploring the Essentiality of the Essential Air Service (EAS): Federally Subsidized Flights and Their Effects on Rural Property Values and Per Capita Income
This journal is published by Yale College students and Yale University is not responsible for its contents.
Editors’ Note At the end of every semester, undergraduates spend countless hours poring over literature, considering methodologies, and honing arguments to produce final economics papers. Then, their papers are read by a single professor, after which they gather dust in forgotten piles or occupy space on overloaded hard drives. But many of these papers contain original insights of interest to other students, professors, and professionals. The Yale Journal of Economics provides a forum for students’ innovative ideas to contribute to the economic discourse both at Yale and in the larger academic community. Our inaugural issue contains six essays — three by Yale students and three by students from other universities — that offer original analyses in different areas of economics. In a contribution to the development economics literature, Geoffrey Barnes explores how education affects the propensity of people to migrate from rural India. Jenny Shen analyzes how the adoption of Spotify affects rates of music piracy, raising questions that are becoming increasingly important as the information economy expands. Noam Angrist looks into whether changes in tipped minimum wages affect the behavior of waiters and waitresses. Lauren Zumbach investigates whether the provision of laptops in schools improves academic performance. In the field of economic history, Jasmine Barrett examines the incentives that drove marriages between American Indian women and European fur traders. Finally, Marc Beck analyzes how federal airline subsidies change communities’ economic outcomes. We selected these papers from a strong pool of submissions from students at Yale and other universities. We thank all those who submitted and all professors who nominated the best papers in their classes for our consideration. Additionally, we thank the professors who helped selected authors revise and prepare their essays for publication. In future semesters, we invite students who write papers that make them proud, as well as professors who read papers that impress them, to reach out to us at the Yale Journal of Economics. Unlike graduate students or professors, undergraduates 4
are just beginning to develop their research skills. But undergraduates have a certain freshness and daring that can yield thought-provoking conclusions and also motivate further research. This inaugural issue of the Yale Journal of Economics will be the first of many that showcase this type of exciting undergraduate scholarship.
Formal Education as a Determinant of Rural Out-migration Evidence from Rural India Geoffrey A. Barnes, Yale University1 Abstract. This paper employs two-stage tobit and probit models to explore how formal schooling affects out-migration in rural India. Fitted values of formal schooling are obtained using first stage ordinary least squares regressions with variables measuring the supply and cost of credit and formal schooling as explanatory variables. Second stage results indicate that formal schooling increases migratory distance and the propensity to leave home for males while decreasing migratory distance and the propensity to leave home for females. Keywords: migration, India, education
1 Geoffrey A. Barnes graduated from Yale University in 2012 with a BA in economics. This senior essay won the Charles Heber Dickerman Memorial Prize. The author would like to thank his senior essay advisor, Professor Mark Rosenzweig, for the many insights he contributed to this project. He would also like to thank Professor Timothy Guinnane for years of help with statistical programming and empirical research.
“Our towns are already large beyond precedent, and yet they continue to grow at an alarming rate. Nevertheless, the indigent rural poor are almost bound to drift into them. And their doing so is, in regard to the social questions of the day, like a rush of steam into the pipes of a boiler.” — Peter Anderson Graham (1892) Brain drain — the out-migration of highly skilled and productive individuals — has long been a contentious topic in the literature on development economics. As the typical brain drain story goes, especially skilled individuals from rural areas who face better earnings opportunities elsewhere and relatively poor earnings opportunities at home engage in mass flights away from their birthplaces. Their birthplaces, in turn, incur large gross economic costs due to the outflow of valuable human capital. Without the ability to retain skilled workers, they have poor prospects of economic growth, which serves to perpetuate the brain drain problem. A sizeable body of research demonstrates that people with large human capital endowments in the form of education indeed tend to move away from rural areas. Lucas (1985) finds that in rural Botswana the more educated are more likely to move into more modernized towns. Likewise, T. Paul Schultz (1982), using data from rural Venezuela, concludes that more educated men leave their birthplaces more frequently, more educated people migrate over greater distances, and out-migration is more common in locales with higher school attendance. Carrington and Detragiache (1999) present evidence of selection for the highly educated in international migration. Excepting Mexico and Central American nations, emigration rates to the United States from least developed countries were higher for individuals with higher education in 1990. In order to discern the net effect of outmigration that selects for individuals with large human capital endowments, one must consider remittance flows alongside the loss of a skilled workforce. Money sent home by migrants is a major component of many developing nations’ economies. According to a recent report by the International Fund for Agricultural Development, 8
an estimated 150 million out-migrants sent an amount in the order of $300 billion to their families in developing nations in 2006. If the benefits from remittances sent home outweigh the costs incurred from the loss of human capital, then perhaps the mass rural out-migration of skilled workers is not categorically bad for migrants’ home villages. Adelman et al. (1988) present evidence of remittances’ importance, finding that in Mexican villages 40 percent of remittance income came from educated internal migrants and that a $100 decrease in remittances from the U.S. amounted to a $178 decline in village income — suggesting the existence of a “remittance multiplier” of sorts. Such questions surrounding brain drain and the net returns rural areas accrue from human capital investment motivate this paper. I investigate the causal relationship between the supply and cost of schooling and out-migration in rural India to arrive at novel conclusions regarding how formal schooling affects outmigration decisions. The well-documented positive relationship between formal education and the propensity to out-migrate arises at least partially because of ex-ante sorting. Individuals who know they will eventually seek employment away from home may be inclined to pursue more education, or individuals with low risk aversion may pursue both education and migration as a result of their preferences. By isolating how the supply and cost of schooling impact rural out-migration, I seek to determine whether there exists an expost effect — that is, whether more schooling as a result of lower costs or higher supply of schooling increases the propensity to migrate independently. This paper uses panel data from rural India to investigate the question of how formal schooling affects migration and is structured as follows: Section 2 develops a theoretical framework that informs my empirical analysis. Section 3 describes the data I use in my analysis. Sections 4 and 5 discuss my empirical design for estimates of how formal schooling affects out-migration and the results thereof. Section 5 concludes, summarizing the implications of my results while suggesting avenues for improvement and future work.
As described by Williamson (1988), the literature on labor markets and demography in developing countries groups the forces driving rural out-migration into two broad categories: push and pull factors. Push factors are unfavorable conditions at home such as relatively low wages and high unemployment, agricultural land shortages driven by Malthusian forces, war, drought, and famine. Pull factors, as the name suggests, describe favorable conditions elsewhere that “pull” migrants in: higherpaying jobs, abundant employment opportunities, relatively low costs of living, and relatively good infrastructure. Intuitively, obtaining formal education should affect out-migration through both pathways. Ceteris paribus, an individual with more years of formal schooling is more likely to possess specialized, highlevel skills for use in “modern sectors” such as technology and manufacturing. Jobs in these sectors are generally scant in rural areas and offer higher wages than typical rural employment.2 Denizens of rural villages with the requisite education may therefore find that their skill sets are more lucrative elsewhere (pull) while the limited economic opportunities at home do not allow them to realize their earnings potential (push). These intuitions form the basis of a stylized model I use to describe the rural out-migration decision, following standard models of human capital investment cum out-migration such as those laid out by Todaro (1969) and Rosenzweig (1988). Let Li denote a vector of economic conditions at geographical location i, Yit denote an individual’s earnings over a fixed period t in location i, s denote an individual’s formal schooling, c denote the costs an individual incurs by migrating, and dim denote the distance between a location i and another location m. An individual’s decision to migrate from his initial (home) location j to another location k rests on the following objective function M, which describes the expected gains from migration: M=
t =0 2 See
� E[Ykt (s( L j ), Lk ) − Yjt (s( L j ), L j )] − E[c(d jk , L j )]
Harris and Todaro (1970) for the seminal treatment of urban-rural wage differentials in developing countries.
Here, schooling depends on economic conditions in the initial location j, many of which fall under the influence of public policy. Earnings in each location are a function of schooling and that location’s economic conditions. The cost of migration is a function of conditions in the home location j and the distance between j and k. ∂c/∂d jk > 0 so that, all else being equal, migrating over a longer distance is always more costly. An individual faces the migration decision at time t = 0 and considers income for each successive period until exiting the labor force T periods later. Imposing the strong assumption of full rationality for the sake of mathematical exposition, whatever alternative location k maximizes the expected differential between future earnings in k and future earnings in j minus the expected cost of migrating from j to k will be where an individual chooses to relocate. If no location k returns a positive value for the objective function M, the individual chooses to remain in the home location j. Calculating how schooling affects the expected gain from migrating from j to k amounts to computing the partial derivative of equation (1) with respect to s( L j ). The above design, while a sound starting point, is naïve in that it does not consider schooling’s simultaneity with migration. Consider now a parameter p that captures a certain “propensity to invest,” essentially the inverse of the rate at which an individual discounts his future consumption and/or income. Broadly speaking, an investment may be defined as anything that involves present loss with the hope or expectation of future gain. Both formal schooling and outmigration, under this definition, are investments. In relatively poor rural areas of developing countries, families and pupils incur large opportunity costs when pupils attend school. Agricultural families often depend on children to help tend to land and livestock.3 A child’s regular absence from home, in such cases, is money lost. Moreover, children who contribute to rural households’ workloads learn valuable practical skills that may have more immediate payoffs than formal education, especially in the context of their home villages. Extended to include p, equation (1) is now rewritten as: 3 See
Rosenzweig and Evenson (1977) and Cain (1977) for more information.
� �� � �� E Ykt (s( L j , p), Lk ) ∗ f ( p) − Yjt (s( L j , p), L j )
E[c(d jk , L j )] f ( p)
where ∂s/∂p > 0 and f ( p) is monotonically increasing in p. When using data and specifications based on the design in equation (1), disregarding the partial effect from p may cause the partial derivative of the objective function with respect to s( L j ) to be calculated as positive when it is in fact negative or zero — a classic case of omitted variable bias. Because p correlates positively with both schooling and the objective function M, one may conclude erroneously that more educated individuals are, all else being equal, more likely to migrate when in actuality people with a higher propensity to invest (or lower discount rate) based on individual and family characteristics happen to pursue both schooling and migration. Simply attempting to control p away presents a whole host of empirical problems as constructing a meaningful and accurate measure of propensity to invest is extremely difficult, if not impossible, using any available data from rural India. The main empirical challenge of this study is thus isolating the partial effect of s( L j ) on the migration decision by capturing the portion of formal schooling that varies with L j while remaining independent from the unobservable parameter p. The components of L j I focus on in this study are the supply and/or cost of schooling in j and the supply and/or cost of credit in j. Both can be readily observed with empirical data and are well within the purview of public policy. I hypothesize that, in line with basic economic theory, a greater supply of formal schooling will lead to more formal schooling being pursued. Formal schooling’s costs should be thought of primarily as opportunity costs: the amount of income pupils’ families forgo when they attend school. A farther away school means more travel time to and from school, and hence less time working at home. I follow Shrestha et al. (1986) in also considering the manner in families’ income portfolios affect the opportunity cost 12
of schooling. Whereas a family with its largest earner working in a non-agricultural field stands to lose little from having children away, one that depends heavily on agricultural income and the contributions of children may stand to lose quite a bit and thus have its children spend less time at school. How the supply and cost of credit might affect the schooling decision is more ambiguous a priori. In rural areas of developing countries, credit can act as an income smoothing mechanism. On the one hand, this means that families whose children contribute to household income could buffer themselves against lower income with steady streams of borrowing while school is in session, and then pay loans back during more bountiful periods when children remain at home. In this respect, a greater supply of creditors and lower interest rates could allow such families to mitigate the opportunity costs of schooling and have their children spend more time in school. Conversely, easy credit could increase the opportunity cost of schooling by raising the benefit of activities that preclude pupilsâ€™ attendance at formal schools. The aforementioned consumption smoothing mechanism also applies to the purchase of farming implements, highly productive seed varieties, and other fixed investments that increase the productivity of childrenâ€™s labor at home. A family with easy credit may choose to pursue such investments using loans with the expectation of being able to pay their loans back using the additional future income that the investments will bring. The purchase of the investments, in turn, makes a childâ€™s presence at home relatively more valuable and his or her attendance at school relatively less valuable. Using data on the supply and cost of schooling and credit allows estimation of the function s( L j ), and in turn estimation of how s( L j ) affects M without noise from the unobservable parameter p. Should the portion of s determined by these components of L j have a positive and statistically significant effect on the propensity to out-migrate, then formal schooling may truly be considered to cause migration. The discussion to this point regarding the partial effect of s( L j ) on the objective function M faces one large caveat: in all likelihood, it does not apply to women at all in the context of this study. Consequently, all of my empirical analysis is performed on 13
male and female subsamples separately. For women in rural India, one of the most important determinants of migration is what has been termed the “marriage market.” Rosenzweig and Stark (1989) find that the out-migration of daughters from households in South Indian villages is a function of interfamilial marriage arrangements, which serve as “interhousehold contracts” with the purpose of consumption-smoothing. Marriage between individuals from two villages with “spatial income risks” and high costs of information pools risk between their families via inter-household sharing arrangements. As their model and results demonstrate, rural Indian females’ outmigration achieves its goal of reducing consumption variability. The manner in which s( L j ) affects women’s migration decisions, then, may depend on its indirect effect on them through the marriage market. If rural females’ formal schooling significantly impacts the nature of their households’ marriage contracts in order to make them more (less) marriageable, then formal schooling will increase (decrease) their propensity to outmigrate. If, on the other hand, formal schooling has a small or negligible effect on interfamilial marriage contracts, it may not affect out-migration by women. The exact manner in which females’ formal schooling enters the marriage contract function is not a subject of great import in this paper, as marriage contracts cum out-migration constitute a topic sufficient in breadth to warrant study in its own right. Section 5 does, however, present suggestive results regarding formal education’s effect on women’s marriageability — a fruitful starting point for potential future research. With data described in Section 3 and econometric techniques outlined in Section 4, I isolate the portion of the schooling decision that, independent from p, varies with the supply and cost of credit and formal schooling. The manner in which that portion of the schooling decision impacts out-migration for men should motivate academic and policy discussion regarding returns to formal schooling and the impacts of education and credit policy in rural India. The manner in which it impacts out-migration for women may offer tantalizing insights into the interplay between cultural and economic factors vis-à-vis Indian demography.
Sample Design and Data
I use data from the Additional Rural Incomes Survey and Rural Economic and Demographic Survey databases (henceforth ARISREDS) compiled by India’s National Council of Applied Economic Research (henceforth NCAER). Created in order to “constitute a nationally representative rural sample of Indian households,” the ARIS-REDS data report extensive economic and demographic information at the individual, household, and village levels. They were first collected in 1969, with later progressively more detailed surveys with larger samples undertaken in 1970, 1971, 1982, and 1999. While drawing upon data from all five rounds would be ideal, the surveys from 1969-71 were considerably less comprehensive than those from the latter two years and had far smaller sample sizes. Including only individuals associated with families surveyed in all five ARIS-REDS rounds in the analysis would have thus limited the amount of usable data. With this in mind, my sample utilizes data from the 1982 and 1999 rounds alone. The ARIS-REDS data are organized in an upward hierarchy from individual to household to village. In each data round, an individual’s affiliated household and village are those in which his or her head of household (almost invariably the father) lives. While households and villages can be matched between data rounds using identifier variables, no identifier exists to do the same with individuals. That is, given a person in the 1999 dataset, it is possible to determine that person’s 1982 household and village characteristics, but not his or her 1982 individual characteristics. Consequently, variables from the 1982 round used in the final analysis can only draw upon household and village data. My final sample consists of 15,815 individuals — 8,963 males and 6,852 females. All are listed as sons or daughters of heads of household in the 1999 data and have some matching household and village data available from the 1982 ARIS-REDS data round. As of the 1999 data-round, males in my sample were between 16 and 41 years of age while females were between 14 and 37 years of age. I use these age ranges because of the distribution of the ages at which sons and daughters leave their households. 15
Figures 1 and 2, using a sample not restricted by age, show histograms of the age at departure of sons and daughters who live away from their households as of 1999. The peak age ranges for outmigration are the twenties for males and the late teens to mid-twenties for females. The age ranges 16-41 for males and 14-37 for females thus capture a large swath of individuals who actually faced the migration decision between 1982 and 1999. Very few people, as the histograms show, leave during early childhood or old age. Extending the age ranges to their maximum values includes individuals who were in or around the peak age ranges for migration prior to 1999, as far back as 1982.
Figure 1: Histogram of ages when sons leave their home household
15 20 25 30 35 40 45 50 Sonsâ€™ ages as of moving away from home household
While a full list of variables used in the analysis is provided in Appendix A, a few particularly important and/or problematic ones merit special attention.4 I provide shorthand notation for each, used in the forthcoming sections on empirical analysis, 4 Appendix A is available at the Journalâ€™s website: http://econjournal. sites.yale.edu/
Figure 2: Histogram of ages when daughters leave their home household
10 15 20 25 30 35 40 Daughtersâ€™ ages as of moving away from home household
in parenthesis. First and foremost is individuals’ educational attainment. The 1999 individual-level data include two different measures of education. The first is simple: total years of formal schooling taken (schoolyrs). In addition, there is a softer, more descriptive measure (educationlevel) that places individuals in one of twenty-one educational categories such as “Illiterate,” “Above Primary but below Middle,” “Pre-University,” and “PostGraduate.” The former is more easily interpreted and holds more empirical relevance for the purposes of this paper. However, a non-negligible portion (8.5 percent) of the individuals in the final sample does not have educationlevel reported in the raw ARISREDS data. Fortunately, 38 percent of the final sample report both measures, enough to get a meaningful idea of how the descriptive variable corresponds to years of formal schooling and fill in missing values accordingly. When schoolyrs is missing in the raw data and education equals a value x, schoolyrs is inferred to equal the mode of schoolyrs over all observations for which both measures are reported and education equals x. The original ARIS-REDS 1999 data also have two different measures of migratory distance. One is the distance in kilometers that an individual lives from his or her affiliated household (distance f rom), with those remaining in their home households reported as living zero kilometers away. The second is another discrete, descriptive variable with eight categories such as “same village”, “town of other state”, and “village/town of other country” pertaining to where individuals live in relation to their home households (currentlocation). The categories in the latter variable give a rather poor picture of actual migratory distances and the costs incurred in migration. Migrating to neighboring Pakistan or Bangladesh, for instance, is considered statistically equivalent to migrating to the United States. Furthermore, continuous regression techniques may not produce meaningful results using a dependent variable with only seven values. I therefore use the distance in kilometers from home household as my primary measure of migratory distance, electing to winsorize its values at a maximum of 3,000 kilometers because of a handful of troublesome outliers reported as 9,999 kilometers. Dummy variable regressions using the descriptive measure of migration could, however, be of some interest despite their statistical 18
shortcomings and are therefore presented in Appendix B with a brief write-up on the results.5 Obtaining measures of the supply and cost of schooling and credit proved difficult because of the paucity of information regarding either in the 1982 ARIS-REDS data and the uncertainty that arises due to the large temporal gap between the 1982 and 1999 data rounds. The NCAER went above and beyond in compiling data on schooling and credit constraints for the 1999 ARIS-REDS set. Each village has information on every school with pupils from the village in attendance, including but not limited to the year it was founded, the type of school it is, its number of instructors, its instructors’ level of educational attainment, whether its instructors have received formal teaching training, and whether it offers amenities such as books, school-provided lunches, clean drinking water, and a library. Information on schools in the 1982 data, however, is limited to whether the village had a primary school, middle school, and high school that year, and if not, what the distance to the nearest one of each was. Ideally, this study would be able to include an entire vector of school characteristics akin to those in the 1999 ARIS-REDS data. The quality of schooling rural children receive, as measured through teachers’ education and training and the availability of educational tools, should serve as an excellent measure of schooling’s opportunity costs. Ceteris paribus, higher quality schools increase the expected future gain from formal education and therefore decrease the opportunity cost of attendance. Accordingly, school quality should vary positively with school attendance. Indeed, Shrestha et al. (1986) find that in rural Nepal, teacher qualification and experience have positive and significant effects on pupils’ school attendance, with somewhat ambiguous results regarding how the quality of schools’ facilities affects attendance. The nature of the data, though, prevents these measures from being used. While the 1999 ARIS-REDS data provide a good idea of what school an individual attended in his or her youth based on when it was founded, whether it was closest to the village, and whether he or she was allowed to attend based on gender requirements, they do not give us any information 5 Appendix B is available at the Journal’s website: http://econjournal. sites.yale.edu/
on school characteristics in any year prior to 1999. Because we know nothing about the exact schooling conditions encountered by anyone who surpassed the age of matriculation before 1999, using the full detail of the 1999 school data would be valid only after imposing the strong assumption that school quality remains roughly constant over time. The only plausible measure of the cost of schooling using the ARIS-REDS data is a vector of dummy variables describing the supply of schooling for each individual — that is, whether he or she was able to attend each level of schooling (primary, middle, and secondary) when he or she was at the age appropriate to that level. An individual is considered “able to attend” a gender- and age-appropriate school if children from his or her home village attended that school as of 1999 and it was established before he or she reached the minimum age for enrollees. I constructed these dummies by cross-referencing birth years, school establishment years, school levels, the age range of pupils attending schools, and the genders allowed into schools as reported in the 1999 ARISREDS data. Data on the supply and cost of credit present a similar obstacle, as the 1999 village-level data contain a wealth of information on lending institutions that would be of use were it only recorded in earlier data rounds as well. The 1999 data separate lending institutions into types — cooperatives, banks, post offices, and rural Gramya banks — reporting the year of establishment, distance from the village and interest rate for the closest of each institution type to each village. Because previous ARIS-REDS rounds make no mention of lending institutions’ interest rates, taking full advantage of the 1999 data’s detail would once again require a strong assumption: that rates remain roughly constant over time. Using a procedure analogous that used in constructing the aforementioned variables measuring the supply of schooling, I constructed four binary variables to measure the supply of credit. Each equals one if an institution of the corresponding type existed less than one kilometer away from an individual’s home village before he or she turned sixteen and zero otherwise. Alternative measures that account for the nature of credit rather than the nature of credit institutions exist in both the 1999 and 1982 ARIS-REDS data. Both years’ data contain binary 20
variables describing whether credit was “available” for a number of purposes: irrigation, purchasing seed, buying agricultural equipment, improving land, and setting up small businesses among them. I choose to forgo any use of these variables in the main analysis because the definition of credit’s so-called “availability” is never made clear in ARIS-REDS documentation. What exactly makes a line of credit tailored to a certain purpose? How close must institutions offering such credit be to villages for the credit to be considered available? Does the definition of availability depend on interest rates? Nonetheless, these variables could capture variation that the aforementioned measures of the supply of credit institutions gloss over. As suggested in Section 2, easy credit for agricultural activities may increase the opportunity cost of children’s formal schooling for families that gain income from agricultural activities to which children can contribute. Having measures of credit specifically for agricultural activities allows me to test this hypothesis. I therefore also run auxiliary regressions using these data rather than the data on the supply of credit institutions. Results, which must be approached with a healthy dose of skepticism because of the variables’ underlying ambiguity, are presented in Appendix C.6 Remaining variables include an agricultural income dummy (agrincome), equaling one if the highest earning member of an individual’s household in 1982 belonged to the category “farmers, fishermen, hunters, loggers, and related workers” and zero otherwise, an individual’s birth order (birthorder), the income in thousands of Indian rupees of an individual’s household as of 1982 (hhincome82), and an individual’s age as of 1999 (age).
To reiterate, I attempt to capture only the portion of the schooling decision determined by the supply and cost of schooling and credit. Doing so ensures that additional formal schooling itself, independent from “propensity to invest,” drives migration decisions. Moreover, such a design leaves my results within the 6 Appendix
C is available at the Journal’s website: http://econjournal. sites.yale.edu/
purview of public policy. While local and national governments can alter the supply and cost of formal schooling and credit in rural areas, the manner in which investment decisions such as schooling and out-migration enter individuals’ utility functions is more so a topic of academic curiosa. To isolate the desired portion of the schooling decision I use a two-stage approach. I first run ordinary least squares regressions of schooling on the variables measuring the supply and cost of schooling and credit plus a number of controls. I then use the resultant fitted values of schooling as variables explaining outmigration. The first stage specification to obtain fitted values of schooling for sons and daughters is as follows. Note again that variable abbreviations and descriptions are in Appendix A. The subscripts i, h, and v denote variables that apply to the individual, household, and village levels, respectively. schoolyrsi = β 0 + β 1 primaryv + β 2 middlev + β 3 secondaryv + β 4 agrincomeh + β 5 cooperativev + β 6 gramyav + β 7 posto f f icev + β 8 bank v + β 9 birthorderi + β 12 hhincome82h + β 13 agei + β 14 agei2 + error I include birth order, household income in 1982, age, and age squared as control variables. All else being equal, higher household income should lower the opportunity cost of schooling and thus increase educational participation. Birth order accounts for any tendency for children born later to be more or less educated then their siblings. Age and age squared control for age cohorts within the sample, as schooling conditions and preferences for schooling may differ between generations. Ordinary least squares (OLS) regressions run using this equation � which are then used for two second obtain fitted values schoolyrs stage regression designs, the first of which is:
� i + γ2 agrincomeh + distance f romi = γ0 + γ1 schoolyrs γ3 cooperativev + γ4 gramyav + γ5 posto f f icev + γ6 bank v + γ7 birthorderi + γ8 hhincome82h + γ9 agei + γ10 agei2 + error I estimate this specification for sons and daughters using a tobit model. A tobit is ideal when dealing with a dependent variable with a corner solution, meaning that while above (or 22
below) a certain value c the dependent variable’s distribution is more or less continuous, it equals c for a substantial portion of the sample.7 In this case, c equals zero, as 69.64 percent of the sample consists of individuals who still lived in their � is home households as of 1999. If the coefficient on schoolyrs positive and statistically significant for sons, then I can reject the null hypothesis that, independent from my model’s p, formal schooling does not increase males’ expected gains from outmigration and hence the distance over which they are willing to migrate. Note that I include the dummy variables measuring the supply of credit in both second stage specifications. I elect to do so because credit could feasibly allow consumption smoothing for migrants and their families that facilitates out-migration. 1982 household income, birth order, age, and age squared are once again introduced as controls. In addition, I estimate two-stage instrumental probits using the same explanatory variables and a binary dependent variable that equals one if an individual lives outside of his or her home household (if the distance variable is recorded as greater than zero):
� i + π2 agrincomeh + P(distance f romi > 0) = π + π1 schoolyrs π3 cooperativev + π4 gramyav + π5 posto f f icev + π6 bank v + π7 birthorderi + π8 hhincome82h + π9 agei + π10 agei2 + error While the tobit regressions answer the question of whether additional formal schooling causes individuals to migrate farther away, the probits address how formal schooling affects the binary decision of whether or not to leave the household. A positive and significant coefficient on schoolyrs for sons here means that, independent from my model’s p, more educated sons are more likely to leave their home households. 7 For
a more detailed discussion of the mathematics behind tobit models, see Wooldridge (2009).
Results First Stage OLS
First stage results for sons and daughters of heads of household are reported in Table 1. Here, my hypotheses regarding how the variables would affect the schooling decision have mixed success. For both sons and daughters, coefficients on dummies measuring the supply of secondary and middle schools are positive and significant, but the coefficient on the primary school dummy is statistically indistinguishable from zero. These results likely arise because secondary and middle schooling are more discretionary than primary schooling. The magnitudes of the coefficients on all three schooling dummies are higher for daughters than for sons, suggesting that the supply of formal schooling affects females’ educational participation more than it does males’ educational participation. Regrettably, the credit variables give rather ambiguous results, perhaps because they fail to capture aforementioned nuances such as interest rates and what credit is used for. The coefficient on supply of a post office is positive and significant for sons while statistically insignificant for daughters, while the opposite is true for the supply of a Gramya bank. For both groups the supply of a bank has a negative and significant effect on years of formal schooling. The supply of a cooperative has a positive and significant effect on daughters’ educational participation and no statistically significant effect on sons’ educational participation. As mentioned in Section 3, the ARIS-REDS data include unspecific measures of the availability of credit for certain purposes, which are included in regressions in Appendix C. As expected, being affiliated with a household that depended primarily on agricultural income in 1982 decreases formal schooling while higher household income in 1982 increases formal schooling for both groups. A family with a higher percentage of its income coming from agricultural activities likely relies more on children being put to work, and thus faces a larger opportunity cost of formal schooling. All else being equal, families with more income face a lower opportunity cost of formal schooling. The model is a far better fit for daughters than for sons, as its R2 when fit to the daughters’ data is .186 versus .108 when fit to the sons’ 24
Table 1: First stage OLS regressions Dependent variable: Years of formal schooling taken as of 1999 Sons Daughters (1) (2) Primary School Dummy .199 .212 (.163) .268∗
Middle School Dummy
Secondary School Dummy
Agricultural Income Dumy
Gramya Bank Dummy
Obs. R2 F statistic
HH Income in 1982
Post Office Dummy
6993 .108 42.709
5357 .185 63.482
Robust standard errors clustered by household identifiers reported in parenthesis. ***,**,* indicates statistical significance at the 1%, 5%, and 10% level, respectively.
Two-Stage Tobit Estimates
Table 2 reports results from two-stage tobit models explaining migratory distance using the fitted values of schooling from the first stage OLS estimates. Coefficients on these fitted values suggest that more educated sons move farther away whereas more educated daughters stay closer to home. Both are significant at the .1% level. Independent from my model’s p, then, schooling indeed increases the propensity to migrate over long distances for men. For women, however, the inverse holds. Independent of p, more formal schooling decreases their migratory distances. The coefficient on household income in 1982 also differs between sons and daughters. For sons, it’s negative and significant; sons from wealthier households are less likely to move far away. For daughters, on the other hand, it’s positive and significant, implying that daughters from wealthier families move farther away. The mechanism for such disparities may lie in the marriage market, a possibility I explore in brief at the end of this section. The credit variables perform poorly in this second stage as well, as none are statistically significant. Note that the table reports a value labeled “Wald p.” This is the p value from a Wald test of exogeneity, which tests the null hypothesis that the instrumented explanatory variable (in this case years of formal schooling) is exogenous. Given the low values of Wald p for both sons and daughters, one can reject formal schooling’s exogeneity for sons at the 5% level and for daughters at the 10% level. Using IV estimates for schooling, then, was the correct decision as formal school is likely endogenous as suspected.
Two-Stage Probit Estimates
Results from two-stage probits are reported in Table 3 and for the most part are similar to the tobit results. The coefficient on years of formal schooling is once again positive and significant for sons and negative and significant for daughters. Males with more formal education are more likely to leave their households whereas females with more formal education are less likely to do 26
Table 2: Two-stage tobits Dependent variable: distance in kilometers an individual lives fro his or her home household as of 1999 Sons Daughters (1) (2) ∗∗ Years of Schooling 101.801 -5.813∗∗ Agricultural Income Dumy
Gramya Bank Dummy
Post Office Dummy
HH Income in 1982
6993 -25428.09 53.372 .022
5357 -33832.4 92.912 .074
Obs. Log Likelihood χ2 statistic Wald p
Robust standard errors clustered by household identifiers reported in parenthesis. ***,**,* indicates statistical significance at the 1%, 5%, and 10% level, respectively.
so. Agricultural income has a negative effect on the probability of daughters leaving their home households and no significant effect on the probability of sons leaving. Higher household income negatively impacts the probability of sons leaving and positively impacts the probability of daughters leaving. The coefficient on birth order is positive and significant for sons, so sons born later are more likely to move away from home. The Wald test once again rejects the exogeneity of formal schooling and hence confirms the appropriateness of an instrumental variables approach.
Exploring the Marriage Market Hypothesis
I surmise that the negative effect formal schooling has on outmigration for females could be a result of formal schooling decreasing their marriageabiity, and hence their opportunities to out-migrate and live with husbands away from home. Table 4 reports the results of two preliminary regressions supporting this hypothesis, both using only data from daughters. The first, in column 1, is a probit using as its dependent variable the aforementioned dummy variable for whether individuals lived away from their home households in 1999 and using a dummy variable equaling one if a woman was married as of 1999 and zero otherwise as an explanatory variable. Column 2 reports a two-stage instrumental probit using the marriage dummy as its dependent variable, the fitted value of school years from the first stage as an explanatory variable, and the same controls I introduced into my previous tobit and probit specifications. Being married indeed has a positive effect on daughtersâ€™ probability of moving out of their home households, as the coefficient on the marriage dummy is positive and highly statistically significant. Instrumented formal schooling has a negative and significant effect on the probability of marriage in the second regression while household income has a positive significant effect. Both variablesâ€™ effects on the probability of marriage match their effects on the probability of moving away from home, suggesting that their indirect effects through the marriage market may in fact play a large part in determining whether daughters out-migrate.
Table 3: Two-stage probits Dependent variable: binary variable equaling 1 if an individual lives away from his or her home household as of 1999 Sons Daughters (1) (2) Years of Schooling .139∗∗∗ -.107∗∗∗ (.035)
Agricultural Income Dumy
Gramya Bank Dummy
Birth Order HH Income in 1982
(.109) (.165) (.128)
Post Office Dummy
Obs. Log Likelihood χ2 statistic Wald p
6993 -22018.98 369.914 .006
5357 -17744.81 1531.619 .004
Robust standard errors clustered by household identifiers reported in parenthesis. ***,**,* indicates statistical significance at the 1%, 5%, and 10% level, respectively.
Table 4: Marriage market probit (1) 2.409∗∗∗
Years of Schooling
Agricultural Income Dumy
Gramya Bank Dummy
(.146) -.211∗ (.118)
Post Office Dummy
HH Income in 1982
(.179) (.139) (.017) (.004)
Age Squared Const.
(.214) (.154) (.010) (.004)
5357 -1935.139 770.832
5357 -17491.58 1271.725 .02
Obs. Log Likelihood χ2 statistic Wald p
Column 1: Depvar — Whether Out of Household in 1999 Column 2: Depvar — Whether Married in 1999 Robust standard errors clustered by household identifiers reported in parenthesis. ***,**,* indicates statistical significance at the 1%, 5%, and 10% level, respectively.
Conclusions and Next Steps
My results for sons of heads of household contribute to the scholarship on returns to human capital in developing countries by highlighting one unfortunate consequence of policies aimed at increasing human capital: they can induce an ex-post brain drain in which educated individuals from rural areas move away from home en masse. Both two-stage designs using the ARISREDS data point to additional formal schooling in rural India increasing malesâ€™ propensity to out-migrate. If this is the case, then the benefits of policies that increase the supply and decrease the cost of schooling in rural India may not be realized entirely by the locales in which they are implemented. Rural men to whom formal schooling imparts valuable knowledge and skills are more likely to put their skills to use elsewhere. Once they leave home, their villages will have devoted considerable labor and capital to teaching them. Whether their home villages receive a corresponding return to investment is a topic that requires further study. While the out-migration of educated men certainly lowers villagesâ€™ returns to human capital investment, remittance flows increase returns. If educated out-migrants sent remittances home with benefits outweighing the benefits they would have given their home villages had they remained at home, then the rural out-migration caused by human capital investment is a net positive rather than an unfortunate side effect. I hope to explore this question in greater depth in future research. The results for daughters of heads of household are fascinating starting points for further study on the culture of Indian marriage arrangements and the economics of Indian inter-household marriage contracts. Many women leave their households because of marriage arrangements, whereas the vast majority of men remain at home. In my final sample, 53% of women lived away from their home households as of 1999 compared to only 7.5% of men. That the minority of women who live at home have more formal education than their peers who leave flies in the face of my model and other conventional models of human capital investment cum out-migration. The reason for this deviation from theoryâ€™s predictions most likely lies in the nuances of the marriage 31
market. Going forward, re-estimation of similar specifications using more extensive data is an avenue I would like to explore. A panel of data collected in smaller intervals with detail rivaling that of the 1999 ARIS-REDS set would allow the estimation a first stage regression that better accounts for how the supply and cost of credit and the quality of supplied schools affect schooling decisions in rural India. Further, data on where educated migrants relocate to would give a better picture of how my empirics conform to theory. Given my current data, I can estimate the effect of education on rural out-migration, but not necessarily rural outmigration to urban areas. Additionally, such information would provide insight into what factors pull educated migrants into their eventual destinations.
References Adelman, Irma, J. Edward Taylor & Stephen Vogel. 1988. “Life in a Mexican village: A SAM perspective.” Journal of Development Studies 25(1):5–24. Cain, Mead T. 1977. “The Economic Activities of Children in a Village in Bangladesh.” Population and Development Review 3(3):201–227. Carrington, William J & Enrica Detragiache. 1999. “How extensive is the brain drain?” Finance and Development 36:46–49. Harris, John R. & Michael P. Todaro. 1970. “Unemployment and Development: A Two-Sector Analysis.” The American Economic Review 60(1):126–142. Lucas, Robert E. B. 1985. “Migration Amongst the Batswana.” The Economic Journal 95:358–382. Rosenzweig, Mark R. 1988. Labor Markets in Low-Income Countries. In Handbook of Development Economics, ed. Hollis Chenery & T.N. Srinivasan. Vol. 1 Elsevier chapter 15, pp. 713–759. Rosenzweig, Mark R. & Oded Stark. 1989. “Consumption Smooting, Migration, and Marriage: Evidence from Rural India.” Journal of Political Economy 97(4):905–926. Rosenzweig, Mark R. & Robert Evenson. 1977. “Fertility, Schooling, and the Economic Contribution of Children of Rural India: An Econometric Analysis.” Econometrica 45(5):1065–1079.
Schultz, T. Paul. 1982. “Lifetime Migration within Educational Strata in Venezuela: Estimates of a Logistic Model.” Economic Development and Cultural Change 30(3):559–593. Shrestha, Gajendra Man, Sri Ram Lamichanne, Bijaya Kumar Thapa, Roshan Chritrakar, Michael Useem & John P. Comings. 1986. “Determinants of Education Participation in Rural Nepal.” Comparative Education Review 30(4):508–522. Todaro, Michael P. 1969. “A Model of Labor Migration and Urban Unemployment in Less Developed Countries.” The American Economic Review 59(1):138–148. Williamson, Jeffrey G. 1988. Migration and Urbanization. In Handbook of Development Economics, ed. Hollis Chenery & T.N. Srinivasan. Vol. 1 Elsevier chapter 11, pp. 425–461. Wooldridge, Jeffrey M. 2009. Introductory Econometrics: A Modern Approach. Mason, OH: South-Western Cengage Learning.
Does the Availability of Music Streaming Products Decrease Rates of Music Piracy? Evidence from Google Trends Jenny Shen, Massachusetts Institute of Technology1 Abstract. In 2008, the Swedish company Spotify began rolling out its music streaming product, which rapidly gained popularity, filling a gap in consumer demand for cheaper alternatives to services such as iTunes, Amazon, and CD albums. I exploit the intertemporal variation in Spotifyâ€™s introduction into new countries to examine the impact that Spotify has on music piracy rates and use Google Trends search data to proxy for Spotify usage rates, music piracy rates, and an additional control variable. I find that once I control for country-specific time trends in music piracy rates, the introduction of Spotify does indeed reduce rates of music piracy, albeit temporarily. These results are robust to different measures of music piracy and Spotify, as well as a control for Grooveshark user volume. However, the statistical significance of these effects is uncertain. Keywords: music piracy, natural experiment, technology, event study, time series
1 Jenny Shen is a senior economics major at the Massachusetts Institute of Technology. The author wants to thank Professors Heidi Williams and Christopher Palmer for their guidance and insight in this process. She also wants to thank her classmates in â€œResearch and Communication in Economics" for their helpful input.
The music industry has long been plagued by a high incidence of music piracy. The law and, more seriously, enforcement tactics to ensure compliance with music copyright laws have been slow to catch up with music piracy techniques. Many believe that the law and law enforcement techniques will never outmatch those who pirate music, a group which is much more technologically sophisticated and much more nimble than most, if not all, governments and government agents.2 Some of the motivation behind music piracy is a reluctance to pay the (perceived) high cost associated with paying for ownership of each song (as is the case with many current business models, such as iTunes or Amazon) or with purchasing CDs. Some have pursued other avenues to avoid directly paying for music by using modes such as radio, internet radio, other musicsharing websites, and YouTube. According to The Economist, “The past year [2008-2009] has seen rapid growth of digital music services that accept the post-Napster consensus that music should be free, or at least appear to be free.” The article further notes that one of the tactics that the music industry has been embracing in order to reduce the incidence of music piracy has been to support the spread of these “free” music services.3 Among these free music services is Spotify, which has been rapidly gaining popularity around the world, particularly through a close partnership with Facebook. In this paper, I explore whether Spotify has reduced the incidence of music piracy. Spotify may reduce the incidence of music piracy by converting “marginal” consumers who are reluctant to download music illegally but are unwilling to pay for music through conventional legal channels to listen to music using Spotify. On the other hand, Spotify’s introduction of listening limits or its insistence on payment for use of its mobile app (i.e. consumers are not able to listen to music on phones or 2 See,
e.g., Nick Bilton, “Internet Pirates Will Always Win,” The New York Times, August 4, 2012, Accessed October 28, 2012, http://www.nytimes.com/2012/08/05/sunday-review/internet-pirates-willalways-win.html. 3 “Singing a different tune.” The Economist, November 12, 2009. Accessed November 17, 2012. http://www.economist.com/node/148450987.
iPods unless they pay for the Premium package), may have an ambiguous effect on music piracy or may even exacerbate rates of music piracy. I investigate this question by taking advantage of intertemporal variation in Spotifyâ€™s introduction to new countries and by relying on search data from Google Trends. This intertemporal variation in the Spotify introduction dates allows us to test whether Spotify truly does have an impact on music piracy. Nevertheless, these introductions are likely not exogenous and are due to such factors as (1) company strategy to test its product in smaller markets first, (2) difficulty in negotiating licensing agreements with music labels, or (3) expansion into countries that the company is most familiar with. I address the potential endogeneity of Spotifyâ€™s decisions to expand using an event study and find that Spotify does indeed reduce the incidence of music piracy when first introduced to a country but the effect is only temporary. The existing literature seems not to have addressed the question of whether Spotify has reduced incidence of music piracy. Some papers have looked at the impact of iTunes on music piracy. For example, Waldfogel (2010) has argued that when CDs were the primary mode of music listening, people resorted to music piracy to avoid having to buy an entire CD to listen to a single song that they liked. Similarly, others have attempted to identify the impact of iTunes on rates of music piracy through survey data, sales data, or data on specific music downloads. It does not appear that the existing literature has looked into the question of whether Spotify and other music streaming sites such as Grooveshark have impacted music piracy. The existing literature has not reached much of a consensus on the impact of music piracy on sales. Waldfogel (2010), for example, uses survey data from undergraduate students and finds that an additional song stolen through illegal downloads displaces between 1/3 and 1/6 of a legally purchased song, a rate that accords with pre-internet rates of music piracy. On the other hand, Oberholzer-Gee and Strumpf (2007) use a comprehensive panel of sales data and do not find evidence that illegal music downloads have caused decreased sales volume over time. Finally, Hammond (2012) has found that illegal file sharing of music albums leaked 36
before official release helps sales, but only for popular artists. In my study, I find that Spotify decreases the incidence of music piracy in a country, once I control for country and time fixed effects, as well as country-specific time trends. Moreover, these results are robust to other measures of music piracy and Spotify usage. The results hold when I control for country-specific time trends, when I use different measures of music piracy, and when I look at Spotify introduction instead of Spotify usage rates. However, while I find that these results are statistically significant at the 0.1% level when I use heteroskedastic-robust standard errors, I find instead that the results are statistically insignificant when I use clustered standard errors. Moreover, I conduct an event study and find that Spotifyâ€™s impact on music piracy is only temporary: While music piracy does decrease in the quarters immediately following Spotifyâ€™s introduction into a country, it quickly rebounds after a few quarters. The remainder of the paper proceeds as follows: Section 2 provides some institutional background on Spotify, Section 3 provides an overview of data, Section 4 details the main regression specifications, and Section 5 interprets the main results. Section 6 delineates and discusses the various robustness tests employed, and Section 7 concludes.
Spotify was founded in 2006 by Daniel Ek and Martin Lorentzen in Sweden, and now has over 15 million active users. Users have three options to listen to music: (1) Free, (2) Unlimited, and (3) Premium. Under the free version, users do not explicitly pay for the music they listen to; the cost of the music is supported by advertising that users must listen to every few songs. In some countries, Spotify places limits on the amount of music that listeners can consume. With the unlimited version, users pay $5 per month and enjoy ad-free listening but do not have the option to listen to Spotify on mobile phones. Under the premium option, users pay $10 per month, enjoy ad-free listening, are permitted to listen to music on a mobile device using the Spotify app, and can listen to music without an internet connection. Spotify is currently available in 15 countries, including the 37
United States, the United Kingdom, Australia, New Zealand, Switzerland, and many other European countries. The company began with a trial version only available through invitation and formally launched its product in 2008 in Finland, France, Norway, Spain, Sweden, and the UK, expanding to other countries in the years since 2012.4 . It is currently in the process of expanding to countries in Asia and South America5 Spotify has many other competitors, including companies such as Grooveshark, Rdio, 8Tracks, Google Music, and Deezer. Nevertheless, as these companies attempt to expand to new countries, they must cross a key hurdle of negotiating with music record labels to allow their company to stream the label’s music in each country.6 . Spotify, however, appears to be the most popular among music streaming services7 In particular, its popularity is a result of intelligent strategy in forming a close partnership with Facebook to propagate its product.8
Data and Methodology Data
Data for this analysis are all taken from Google Trends, which provides aggregate measures of search volume for all phrases searched for. Google Trends breaks down its data at the weekly and country level – sometimes with more granular geographic breakdowns (e.g. at the state level in the United States) – and spans from January 2004 to October 2012.9 A data download for a given search term yields data for all 4 Noble, Tom. ”Spotify Fast Facts.” Spotify, Aug 22, 2012. Accessed Sept 27, 2012. https://spotify.box.com/s/159e804367f0224d38cd 5 Grundberg, Sven. “Spotify to Launch in Canada.” The Wall Street Journal, August 22, 2012. Accessed December 1, 2012. 6 Pfanner, Eric. “French Music Streaming Service Is Taking On the World, but Omitting America.” The New York Times, October 21, 2012. Accessed December 1, 2012. 7 Imam, Jareen. “Young listeners opting to stream, not own music.” CNN, June 16, 2012. Accessed November 1, 2012. 8 Olanoff, Drew. “Why Spotify and Facebook are Apple’s iTunes worst nightmare and the record label’s best friend.” The Next Web, October 22, 2011. Accessed December 2, 2012. 9 This paper was written in December 2012.
searches that contain the given term. For example, search volume data for “Spotify” includes all searches for “Spotify,” as well as searches for “download Spotify,” “What is Spotify?” and other similar queries. What is particularly convenient about this feature is that most of the relevant search terms (in particular, “Spotify,” “MP3,” and “Torrent”) for this analysis are the same in every language. Thus, a download of data for searches containing the word “Spotify” would include the analogous queries in Spanish, French, German, and the relevant languages used in the countries in which Spotify operates. The main problem presented with Google Trends data is that the tool only provides relative search volume over a specified time period and within a specified geographic region. That is, Google Trends normalizes the minimum search volume to 0 and the maximum search volume to 100 over a given time period and within a specified region. As noted in Stephens-Davidowitz (2012), this normalization can be denoted as follows:
= 100 · �
[Spotify Search Query] j �
Google searches including the word “Spotify” Total Google searches j
Google searches including the word “Spotify” Total Google searches max
I download data at the country level, so each of the variables that I look at is normalized across 2004-2012 and within each country. 3.1.1
Spotify and Grooveshark
I use Google Trends search volume to proxy for Spotify usage rates, music piracy rates, and Grooveshark usage rates (a control variable). Underlying this method is a key assumption that a significant proportion of the population uses Google to access websites rather than typing in the URL directly. So long as this population is the same as the population that accesses these services directly, the analysis validly predicts the effect of Spotify on music piracy correctly. Nevertheless, that these populations are different in systematic ways that may bias the estimates of the analysis is a valid concern. 39
As suggested previously, I proxy for Spotify and Grooveshark use by looking at searches that contain “Spotify” and “Grooveshark,” respectively. I use Grooveshark as a variable to control for the impact that existing music streaming services have on music piracy rates. Nevertheless, it may not be a very good control for this purpose, for two reasons. First, Grooveshark users may substitute towards Spotify once it is available for use. (I test this later in the paper and find that this is not a significant effect.) Second, Grooveshark is different from Spotify in several respects, and, in particular, does not appear to be used in the same way that Spotify or other music streaming services are used. While Google Trends data can plausibly proxy for usage rates for Spotify users, Grooveshark users, and users who pirate music (with differing degrees of measurement error), exactly what the search volume measures differs in meaningful ways. In particular, Spotify’s service is not provided through an internet browser (as is the case with Grooveshark). Rather, users visit the Spotify website and download a separate software that, after installation, can be accessed without going through an internet browser – more specifically, it is accessed without the user having to search for Spotify through Google. Thus, distinctions between the flow of new Spotify users and the stock of new Spotify users are meaningful to look at: It may be the case that the total volume of Spotify users is what has an impact on music piracy rates, rather than the volume of new Spotify users each week.
Following Oberholzer-Gee and Strumpf (2007), I identify music piracy within Google Trends search data that may be motivated by a search for an illegal download. I use this method to look at two measurements of music piracy. The first of these methods is to look at Google searches that contain the phrases “mp3” or “torrent.” This data would, for example, yield searches for “Adele Rolling in the Deep MP3” or “Adele Rolling in the Deep Free MP3 Download,” and the analogous searches for torrent downloads. It is possible that these searches include people who are looking to buy mp3s and those looking to download other types of files (such as movies) through torrent. Thus, I introduce a
second measure of piracy, looking specifically at search queries for “free mp3 download.” This measure more precisely captures the rates of music piracy in a given country, but likely excludes a large number of people who are illegally downloading music. Summary statistics are presented in Table 1.
I take advantage of the staggered introduction of Spotify to measure its impact on rates of music piracy. Specifically, I create a dummy variable equal to one if Spotify is available for use in a given country at a given time, and control for unobserved characteristics using country and time fixed effects. Because of the possibility that countries may have specific time trends that cannot be captured by separate country and time fixed effects, I look also at a specification that controls for these trends. Specifically, I look at six different specifications, which are all variations of the following general form and differ only in the types of fixed effects included: ln( MusicPiracyit ) = β 0 + β 1 Spoti f yit + αi + γt + δi∗t + ε
MusicPiracyit is an aggregate measure of music piracy in a given country. In my baseline regressions, I rely only on the first measure of music piracy, total searches that include either “mp3” or “torrent.” I expand upon this in my robustness tests. Spoti f y is a dummy variable for whether or not Spotify has been introduced in the country. Again, I look only at this discontinuity in my baseline regressions but expand to look at other measures of Spotify usage in my robustness tests. αi are country fixed effects, and γt are time fixed effects. These time fixed effects are measured at the annual level and at the quarter (i.e. 2004Q1, 2004Q2, etc.) level. Finally, δi∗t are variables that capture country-specific time trends. For a given country, they are equal to the year or quarter of each observation in that country; otherwise, they are equal to 0. Results are presented in Table 2. I look first at a regression without any fixed effects (Regression 1). Next, I add country 41
10.81757 918.2367 16.5932 39.77659 39.80345 39.1446 7296
20.16852 2163.008 26.08069 17.27099 15.0646 16.78556
0 0 0 13 0 0
100 10380 100 100 100 100
Table 1: Summary Statistics
Spotify search volume (Flow) Spotify search volume (Stock) Grooveshark search volume Mp3 search volume Torrent search volume Free Mp3 Download search volume Observations
1. Source: Google Trends 2. Data covers 2004-2012 for all countries in which Spotify currently provides its service and is broken down at the weekly level. 3. All measures are normalized to max=100 and min=0, except for “MP3” search volume and “torrent” search volume, which together are normalized to max=100 and min=0. This means that the minimum value for (mp3, torrent) is normalized to zero and the maximum value for (mp3,torrent) is normalized to 100. 4. Spotify search volume (Stock) is generated by summing all of the search volume for Spotify in all previous periods. Thus, its maximum value is significantly greater than 100.
fixed effects (Regression 2) and then add time fixed effects, of which I use two measures â€“ year and quarter (Regressions 3 and 4). Finally, I look at country-specific time trends at both the year and quarter level (Regressions 5 and 6). Because Google Trends normalizes its data within countries, I look at the logs of the relevant variables. In my baseline regressions, I use the log of my music piracy measure as my dependent variable. In my robustness tests, I also take the logs of my measures of Spotify and Grooveshark to account for the fact that search data are normalized. In particular, looking at logarithms allows us to look at changes in the dependent variable that are induced by changes in the independent variable, thus allowing us to circumvent the normalization of the search data. Country fixed effects may also control for the underlying country specific factors and allow us instead to examine only the changes in the relevant variables that are induced by the independent variable. These country fixed effects also control for underlying factors that do not change between 2004 and now, which would be important even absent the normalization of the data. For example, there may be some underlying cultural attitudes towards piracy that affect the adoption of Spotify and Grooveshark, as well as music piracy rates. Such factors would be controlled for by country fixed effects. What is probably not controlled for by country fixed effects is the underlying legal environment or the strength of the music industry, which probably has changed significantly between 2004 and now. I also include time fixed effects in my regressions. The effects controlled for by time fixed effects are factors that affect all countries equally in the year, quarter, or month of concern. For example, with the torrent searches, there may be some periods of time in which a legal injunction shut down the servers for the website for some time, dampening overall torrent searches, or for more popular piracy services for those who downloaded mp3 files. As discussed in Bertrand, Duflo, and Mullainathanâ€™s (2002) study, differences-in-differences studies often suffer from autocorrelation across time that is not controlled for, which potentially may cause the analysis to produce statistically significant but spurious relationships. In particular, they 43
construct placebo state-level laws on female wages and perform difference-in-difference regressions on CPS data. Despite the placebo nature of the laws, they find significant results for up to 45% of the placebo laws that they construct. As such, they conclude that using heteroskedastic-robust standard errors grossly underestimates the true standard errors of the estimate and suggest using clustered standard errors to control for possible autocorrelation of error terms across time. Nevertheless, KĂŠzdi (2004) shows that 50 clusters is sufficient for clustered standard errors to be roughly equal to true standard errors, but that a smaller number of clusters has a higher probability of producing incorrect results. To take into account that shifts in Spotify usage and piracy rates are not random within a country, I cluster my standard errors at the country level, addressing some of the concerns raised by Bertrand, Duflo, and Mullainathan (2002). Nevertheless, since I look at a relatively small number of states (15 total), the clustered standard errors may not allow us to draw accurate conclusions â€“ that is, estimates that use clustered standard errors may produce estimates that are not close to their theoretical values. Thus, I look at both heteroskedastic-robust standard errors as well as clustered standard errors. 3.3.2
In order to test the robustness of the results obtained by the baseline regressions, I expand upon the baseline regressions in three ways: (1) I look at a different measure of music piracy, (2) I look at two different measures of Spotify usage rates, and (3) I add in a control variable to account for the possibility that other music streaming services account for changes in music piracy rates, rather than Spotify itself. I obtained data only for one possible substitute: Grooveshark, a similarly popular music streaming service that aims to change the way that music is listened to in such a way that diminishes music piracy rates. As discussed in section 2, Spotifyâ€™s impact on music piracy may not necessarily be its introduction into a country but rather the volume of new Spotify users. Thus, I look also at two other measures of the variable Spotify: (1) the flow of new Spotify users,
and (2) the stock of total Spotify users. In doing so, I assume that each search for the term “Spotify” is roughly equal to a new user looking to download Spotify. Note that search volume for the term “Spotify” includes also searches for terms that contain the word “Spotify,” such as “Download Spotify.” On the other hand, Grooveshark users and those who download music illegally must do so through a browser each time they (1) wish to use the service (in the case of Grooveshark) or (2) wish to download a song (in the case of illegal downloads). Finally, I also use a different measure of music piracy (searches for “free MP3 download” instead of searches for either “mp3” or “torrent”) in a third set of regressions. Thus, in my robustness tests, I expand upon my baseline specification in one respect, but look at different measures of the variables in the baseline specification. In particular, I examine regressions of the form: ln( MusicPiracyit ) = λ0 + λ1 ln(Spoti f yit ) + λ3 ln( Grooveshark it ) + αi + γt) + δi∗t + ε
MusicPiracyit is an aggregate measure of music piracy in a given country. I use two measures: (1) Google searches for “MP3” and “Torrent”, and (2) Google searches for “free MP3 downloads.” Spoti f yit is a measure of Spotify usage rates, rather than just simply its introduction. I use two measures: (1) the flow of new Spotify users and (2) the stock of total Spotify users. Grooveshark it is a control variable that, as previously discussed, controls for the impact that substitutable music streaming products have on piracy rates. αi are country fixed effects, and γt are time fixed effects. These time fixed effects are measured at the annual level and at the quarter level. Finally, δi∗t are variables that capture country-specific time trends. For a given country, they are equal to the year or quarter of each observation in that country; otherwise, they are equal to 0. 3.3.3
Spotify’s expansion into new countries is likely not entirely exogenous. For example, Spotify may identify the countries where people especially do not like paying for music using the iTunes 45
or Amazon business model as places where their product would be most popular and expand to those countries first. In addition, Spotify has to negotiate licenses to stream music with major music labels before offering its product (or at least gaining a critical mass of popular music to offer to their customers). Countries with particularly strong music labels may be more difficult for Spotify to enter and also plausibly may have been able to take more action against those who pirate music. Moreover, Spotify may have wanted to test out its products in smaller markets before expanding to larger markets. Finally, Spotify may only expand music to countries that are relatively similar to Sweden (where the product was first created). It has only thus far expanded to western countries (e.g. France, UK, Spain, USA, New Zealand, Australia, etc.). In order to test whether Spotify’s expansion was truly endogenous, I conduct an event study. In particular, I run the following regression: ln( Piracyit ) = η0 + η1 · ln( Grooveshark it )αi + γt + ∑ 1τ =t� + ε it
where, as before, Piracy is a measure of music piracy rates, Grooveshark is used as a control variable to control for the impact that existing music streaming services have on music piracy rates, αi are country fixed effects, γt are calendar week fixed effects, and 1τ =t� are dummy variables for an alternative measure of time (denoted as t� ) – a normalized measure of time that is set to zero for the week before Spotify is introduced into a country. These differ systematically from the calendar date fixed effects since Spotify was introduced in different countries at different times. In addition to conducting an event study for music piracy, I also conduct an event study to see if Spotify has a statistically significant impact on Grooveshark use. The concern is that Grooveshark may not be a good control variable because people may alter their use of Grooveshark once Spotify is made available.
I run a similar regression as above: ln( Grooveshark it ) = η0 + αi + γt + ∑ 1τ =t� + ε it
Results from the event studies are presented as graphs at the end of the paper.
Overall, I find that Spotify’s introduction reduces the incidence of music piracy in my baseline regressions. In the expansions upon the baseline regressions (i.e. the robustness tests), a general trend emerges: I find that Spotify usage decreases the incidence of music piracy only when I control for quarter-level country-specific time trends. In the remaining robustness tests, I find that Spotify actually increases the incidence of music piracy. Moreover, while my baseline regressions generally find that the impact of Spotify introduction on music piracy is significant, I find mostly that the impact is significant when I use heteroskedastic-robust standard errors but insignificant when I use clustered standard errors.
Table 2 presents the results from my baseline regressions. Absent any fixed effects, I find that the introduction of Spotify – across all 15 countries – decreases rates of music piracy by 13%, a result which is significant at the 0.1% level with heteroskedastic-robust standard errors and significant at the 5% level with clustered standard errors. When I include country fixed effects (column 2), I find this effect to be stronger: Controlling for factors that are constant in a country over the 2004-2012 period, Spotify decreases incidence of music piracy by 15.7%. Nevertheless, when I control for time fixed effects in addition to country fixed effects (columns 3 and 4), I find the effect to be relatively smaller but still negative (a decrease of 4.4% and 6.1% with year and quarter fixed effects, respectively). Finally, I find the impact of Spotify introduction on music piracy to be much smaller when I control for countryspecific time trends in addition to country and time fixed effects (columns 5 and 6). The effect is significant only with quarter-level 47
country-specific time trends and heteroskedastic-robust standard errors.
Table 3 presents the results from my robustness tests. In order to minimize the results presented, I look only at models that control for quarter-level country-specific time trends. Columns 1 and 2 use the broader definition of music piracy that looks at searches that include the phrases “MP3” or “torrent,” and columns 3, 4, and 5 use the narrower definition of music piracy that looks at searches that include the phrase “free mp3 download.” Overall, I find that the effects are not significant when I use clustered standard errors. Moreover, the broader definition of music piracy (columns 1 and 2) does not find any significant impacts of Spotify on music piracy rates. However, once I look at the stricter definition of music piracy, I find a negative and statistically significant impact of Spotify on music piracy rates (using heteroskedastic robust standard errors). Specifically, I find that the introduction of Spotify reduces music piracy by 5.4% when controlling for country-specific time trends. Moreover, a 1% increase in total Spotify users decreases music piracy by 2.8%, an effect that is statistically significant at the 0.1% level using heteroskedastic robust standard errors. Finally, a 1% increase in new Spotify users induces a 1.4% decrease in music piracy, an effect which is statistically significant at the 1% level using heteroskedastic-robust standard errors. In addition to the robustness tests, I conduct two event studies to examine two different hypotheses: (1) whether Spotify’s expansion is endogenous and (2) whether Grooveshark is an adequate control variable. The results are presented in Figures 1 and 2. I find that Spotify’s introduction significantly reduces the incidence of music piracy, but this effect quickly rebounds about eight quarters after Spotify is introduced into a country. With the Grooveshark event study, I find that Spotify’s introduction has no impact on usage rates for Grooveshark, and, thus, that Grooveshark is a valid control variable in that it is not affected by the introduction of Spotify into a country.
ln_piracy -0.155 0.00577*** 0.0441**
ln_piracy -0.128 0.00645*** 0.0331** 4.397 No No No No 7296 0.062
Spotify Introduction Heteroskedastic-Robust Standard Errors Clustered Standard Errors
Country fixed effects Year fixed effects Quarter fixed effects Country-specific time trends
Yes No No No
Yes Yes No No
ln_piracy -0.0436 0.00692*** 0.0427
Yes No Yes No
ln_piracy -0.0604 0.00695*** 0.0478
Table 2: Spotify Introduction and Music Piracy
Yes Yes No Yes
ln_piracy 0.0044 0.00657 0.0251
Yes No Yes Yes
ln_piracy -0.015 0.0071 0.0316
0.0363 0.00617*** 0.0425
0.0397 0.00633*** 0.0434
Yes Yes Yes
0.0375 0.00624*** 0.0439
-0.0539 0.0125*** 0.0775
-0.00159 0.00278 0.0107 0.0153 0.00370*** 0.0252
Yes Yes Yes
Table 3: Spotify and Music Piracy (Robustness Tests)
Spotify Introduction Heteroskedastic-Robust Standard Errors Clustered Standard Errors
ln(Total Spotify Users) Heteroskedastic-Robust Standard Errors Clustered Standard Errors
0.0152 0.00370*** 0.0247
Yes Yes Yes
-0.0145 0.00485** 0.0276
ln(Grooveshark Use) Heteroskedastic-Robust Standard Errors Clustered Standard Errors
Yes Yes Yes
0.000904 0.00261 0.0112
Yes Yes Yes
ln(New Spotify Users) Heteroskedastic-Robust Standard Errors Clustered Standard Errors
Country fixed effects Quarter fixed effects Country-specific time trends
-0.0284 0.00604*** 0.0383
Figure 1: Event Study
In this paper, I examined the impact of a new popular music streaming service, Spotify, on music piracy rates. Overall, consumers seem to prefer not to have to pay explicitly for music, with many people opting to download music illegally rather than to pay for it. As noted in The Economist, music distribution services seem to be headed in the direction of providing services that do not require explicit payment for listening to music. Thus, these music streaming services, which offer a legal and ethically cleaner alternative to illegal music piracy, could plausibly decrease rates of music piracy in the countries where they are available. In this paper, I used Spotifyâ€™s staggered introduction of its product into new countries to look at its impact on music piracy rates in the 15 countries where it is currently available. Overall, I found that once I controlled for a granular country-specific time trend, Spotify decreased rates of music piracy. Nevertheless, whether or not this impact is statistically significant is still unclear. My results yielded two opposite extremes: With heteroskedastic51
robust standard errors, I generally found results that were statistically significant at the 0.1% level, but with clustered standard errors, I generally found results that were statistically insignificant. I suspect that the impact is relatively small, negative, and statistically significant at a less strict significance level. The reason for this suspicion is that additional controls generally decreased the magnitude of Spotify’s impact on music piracy and decreased its magnitude. On the subject of statistical significance, the results do not seem to paint a very clear picture. In this paper, I also conducted an event study to get a more robust look at the impact of Spotify introduction on music piracy. The event study appears to indicate that Spotify does indeed reduce the incidence of music piracy, but only temporarily. Nevertheless, as Spotify continues to change and improve its product to reflect consumer tastes, Spotify’s impact on music piracy may be different if this analysis is repeated with the countries that Spotify plans on expanding to. Future research on this subject may expand in many meaningful ways. First, the use of Google Trends data to proxy for rates of music piracy and Spotify usage was imperfect, and, while data on music piracy may be difficult to obtain, usage statistics for Spotify and other music streaming products may be able to be obtained directly from the company and may offer a clearer picture of how people listen to music. Moreover, controlling for Grooveshark instead of other music streaming services was purely out of convenience and the omission of a more robust estimate of existing music streaming use in a country was not done for any particularly meaningful reason. As such, future research may also aim to better control for usage rates of similar music streaming services.
References Bertrand, Marianne, Esther Duflo & Sendhil Mullainathan. 2002. “How much should we trust differences-in-differences estimates?” National Bureau of Economic Research. Hammond, Robert G. 2012. “Profit Leak? Pre-Release File Sharing and the Music Industry Supplementary Appendix.” Manuscript.
Kézdi, Gábor. 2004. “Robust Standard Error Estimation in Fixed-Effects Panel Models.” Hungarian Statistical Review pp. 95–116. Oberholzer-Gee, Felix & Koleman Strumpf. 2007. “The effect of file sharing on record sales: An empirical analysis.” Journal of Political Economy 115(1):1–42. Stephens-Davidowitz, Seth. 2012. “The Effects of Racial Animus on a Black Presidential Candidate: Using Google Search Data to Uncover What Traditional Surveys Miss.” SSRN 2050673 . Waldfogel, Joel. 2010. “Music file sharing and sales displacement in the iTunes era.” Information Economics and Policy 22(4):306–314.
Does Merit Pay Pay? The Impact of Tipped Minimum Wage Shifts on Earnings, Employment, and Incentives Noam Angrist, Massachusetts Institute of Technology1 Abstract. Since its inception in 1938, the United States minimum wage has been controversial because it aims to boost overall standards of living but might lead to unemployment. In this paper, I explore this tradeoff and analyze the precise impact of the minimum wage on income and employment. To this end, I use a natural experiment: the implementation of the Fair Minimum Wage Act (FMWA) of 2007, which increased the minimum wage by $2.10 over the course of two years. This approach allows me to draw on state-by-state wage differences as well as the exogenous FMWA policy shift to make causal conclusions about the effects of the minimum wage. I focus my analysis on waiters and waitresses, who earn tipped minimum wages, which are lower than regular minimum wages. My estimates suggest that higher tipped minimum wages have no effect on the employment or earnings of waiters and waitresses. A reason for this might be that waiters display targeting behavior, working fewer hours with less effort to earn the same amount. Keywords: labor economics, minimum wage, natural experiment, instrumental variable
1 Noam Angrist is a senior economics and mathematics major at the Massachusetts Institute of Technology. The author would like to thank Professor Sara Ellison for excellent guidance and advising as well as Jonathan Tebes for help compiling the legal tipped minimum wage data. He would also like to thank Eliana Schleifer for helpful comments.
The minimum wage and tipped minimum wage have significant policy implications. In theory, minimum wages raise overall earnings and protect against inflation by ensuring a higher baseline real salary. On the other hand, they artificially boost wages above the market-clearing level and potentially leave some employees without a job. Overall, minimum wages lead to higher average earnings, but fewer employees benefit from those earnings as unemployment rises. This argument holds both for the regular minimum wage and the tipped minimum wage, which is generally lower in absolute terms and leaves more room for merit-based pay in the form of tips. This paper sheds light on the tradeoff between high and low levels of regular and tipped minimum wages to help inform the minimum wage policy debate. There are also econometric motivations for this paper. First, the variation in tipped minimum wages across states allows for differences-in-differences and state fixed effects analyses. For example, Californiaâ€™s tipped minimum wage is $8.00 per hour, while Massachusettsâ€™ is only $2.63 per hour. Thus, Massachusetts waiters make a significantly larger portion of their salary from tips relative to guaranteed income. These differences abound across states, a natural variation I take advantage of in making causal conclusions. Second, I use an exogenous policy shift, the Fair Minimum Wage Act of 2007, which raised minimum and tipped wages in tandem across the United States by $2.10 over two years. I examine employment and earnings before and after this shift. Some states were unaffected by this shift since their initial minimum wages were higher than the final mandated wage of $7.25, so I considered these states as controls. The combination of state-by-state wage variation and a discrete policy shift allows for causal interpretations of my results. My basic ordinary least squares (OLS) results show that there is no effect of an increase in the tipped minimum wage on employment, while there is an effect on earnings. When I employ a state fixed effects model and examine the FMWA policy shift, however, I see no effect of higher tipped minimum wages on either employment or earnings. A possible explanation is that the 55
tipped minimum wage is so low that it does not induce employers to hire or fire waiters since waiters’ labor is a small fraction of their overall cost. Furthermore, these results indicate that waiters might display “targeting” behavior; as their guaranteed income increases, they work fewer hours or less hard to earn the same amount. This paper is organized as follows. Section 2 provides a review of the relevant literature. Section 3 explains the construction and details of the data used in this paper. Section 4 describes the empirical strategy. Section 5 presents my results. Section 6 concludes.
Since the minimum wage was first implemented in 1938, a large body of literature about its effects has emerged. In 1975, when more than 90 percent of the workforce in America was covered by the federal minimum wage, Congress established the Minimum Wage Study Commission (Brown 1999). Three economists on the commission – Charles Brown, Curtis Gilroy, and Andrew Kohen – conducted a literature review and stated that “time-series studies typically find that a ten percent increase in the minimum wage reduces teenage employment by one to three percent” (Brown, Gilroy & Kohen 1982). New literature emerged in the 1990s, which primarily used times-series or cross-state variation approaches. The conclusions from this research vary widely, and so much of the minimum wage literature is inconclusive. Neumark and Wascher (2006) showed disemployment effects similar to those comprising the earlier consensus of the Congressional commission. Other results indicate no effect on employment (Card 1992), while still others give evidence of a positive effect of the minimum wage on employment (Katz & Krueger 1992). One landmark study on the minimum wage is Card and Krueger (2000). Card and Krueger conducted surveys of fastfood restaurants in February 1992, roughly two months before the April 1992 increase in the New Jersey minimum wage to $5.15 per hour, and repeated their surveys in November of that year. They constructed a wage gap for New Jersey and included a control group of restaurants in eastern Pennsylvania, where the minimum wage did not change. Their results implied that the 56
increase in New Jerseyâ€™s minimum wage raised employment in that state with an estimated elasticity of .73, a sharp departure from expected behavior in the fast-food industry. While there has been much research on the effect of the minimum wage on employment and earnings, little research has been conducted on the tipped minimum wage. In addition, substantial research exists on sub-populations, such as low-wage workers and the fast food industry, yet only sparse research exists on tipped employees. A paper by Camerer, Babcock, Loewenstein, and Thaler (1997), showed that New York City taxi drivers display targeting behavior, where they aim to earn a particular amount and adjust their hours and effort according to their hourly wage. Thus, taxi drivers set a loose daily income target and stop working once they reach this target. This behavior has been documented in a variety of other contexts (Farber 2003, Chou 2002). In this paper, I explore the possible incentive effects of merit pay, a question that, to the best of my knowledge, has never before been analyzed in the context of waiters and waitresses.
The database in this paper is, to the best of my knowledge, the first panel data set created on the tipped minimum wage. My sample, which spans from 2004 to 2010, consists of 32 states, Guam, and the District of Columbia. I exclude states that have tipped minimum wage structures that are not compatible with my subject of analysis: the average waiter in a given state in a given year. The first exclusion I make is for states that subdivide waitersâ€™ minimum wages by the location of their tipped encounter, including restaurant work versus hotel work versus bar work, since I cannot separate out my dependent variables by restaurant versus hotel earnings. I further exclude states that subdivide the tipped minimum wage by groups of employees, since I cannot easily conclude if they were affected by a federal minimum wage policy shift between 2007 and 2009. Finally, I exclude states that base their tipped minimum wage on employer gross sales, since this presents an endogeneity problem. I include the District of Columbia and Guam in my analysis since waiters and waitresses in these districts are subject to unique tipped 57
minimum wage laws and also have earnings and employment data. Although these districts do not share certain characteristics with recognized states, their variation in legal tipped minimum wages is informative. See Table 1 for a list of the variables I use and their summary statistics. The variable LOGTOTEMP is the log transformation of total number of waiters employed in a given state in a given year. I compile these data for waiters and waitresses by state by year from the Bureau of Labor Statisticsâ€™ â€œOccupation Employment Statistics.â€? I then take the log transformation for simple interpretation of my coefficients. Furthermore, the log transformation of employment results in a similar R-squared value, such that the log transformation fits the data. The variable LOGHMEAN is the log transformation of the hourly earnings for the average waiter in a given state in a given year. This variable is likely misreported, since waiters and waitresses generally do not fully report cash tips. This in itself would not introduce an error in variable bias, unless this misreporting was related to time or state-varying characteristics. One case where this might be true is if credit cards have become more prevalent over time. Since it is impossible to underreport credit card tips, this could increase observed hourly earnings. As a result, LOGHMEAN might be higher in year 2009 due to increased credit card usage as opposed to shifting state tipped minimum wages. While this bias might indeed be present, it is unlikely that it shifts discontinuously with the FMWA, so I can still employ my instrumental variable to determine causal effects of an increase in the tipped minimum wage. The variable MINTIPWAGE is the independent variable. I use the variable MINREGWAGE to link the FMWA exogenous shift to changes in tipped minimum wages as described in section 4. To obtain data on both of these measures, I compile data from the Bureau of Labor Statistics to create a panel data set of regular and tipped minimum wages across states between the years 20042010. These data are based on legal cutoffs and therefore have no other bias except potential state factors that contribute to the setting of tipped minimum wages as well as state-specific waiter employment or earnings. In order to control for certain variables, I compile demographic 58
data by state from the Census Bureau. I obtain over 30 different variables from the Census Bureau ranging from gender to distance of commute to ethnicity. Ultimately, I use a fixed effects model to take into account unobserved characteristics. Below, I include a table with basic summary statistics on those variables included in my analysis: Tables 1 and 2 indicate the variation of the tipped minimum wage, which I employ to analyze the effects of higher minimum wages on my outcome variables. This cross-sectional and timeseries variation is essential to the econometrics techniques I utilize throughout this paper. Table 2 displays all of the unique tipped minimum wages across all states and over a seven year time period. Table 1: Summary Statistics Variable
LOGTOTEMP TOT_EMP LOGHMEAN H_MEAN MINREGWAGE MINTIPWAGE MEDINCOME SALESFOODSERV STATEINCTAX
238 238 238 238 238 238 238 238 238
10.15779 45191.22 2.155336 8.766513 6.343508 3.514916 52251.82 11500000 0.0430983
1.050375 54232.62 0.1745677 1.606015 1.200963 1.835767 7866.42 15700000 0.025206
8.180321 3570 1.83418 6.26 2.575 1.59 38380 1214201 0
12.42304 248460 2.660259 14.3 8.55 8.55 70647 80900000 0.09
The figures in the Appendix have some missing values for two reasons: First, if the state is below the federal cutoff, then the federal cutoff applies and the state value is missing; second, if the tipped minimum wage is the same as the regular minimum wage in that state, then they take on one anotherâ€™s value, so one might be missing in the table. In the data set, I inputted variables into these missing values according to these guidelines.2 2 The Appendix is available at the Journalâ€™s website: http://econjournal. sites.yale.edu/
Table 2: The Tipped Minimum Wage, 32 states, DC and Guam, 2004-2010 MINTIPWAGE ($)
1.59 2.13 2.23 2.33 2.38 2.57 2.575 2.58 2.63 2.65 2.77 2.83 2.89 3.09 3.13 3.3 3.35 3.45 3.77 4.12 5.15 6 7.05 7.15 7.16 8
1 9 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1 1
2.94 26.47 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94 2.94
2.94 29.41 32.35 35.29 38.23 41.17 44.11 47.05 49.99 52.93 55.87 58.81 61.75 64.69 67.63 70.57 73.51 76.45 79.39 82.33 85.27 88.21 91.15 94.09 97.03 99.97
In order to estimate the effects of higher tipped minimum wages on my two outcome variables (LOGTOTEMP and LOGHMEAN), I break up my analysis in three phases, each technique yielding progressively more causal results. First, I first use a standard OLS regression. This approach can be modeled using the following equation: Yi = α + β 1 Xi + ui
Second, I capitalize on the massive variation of legal wage structures. To this end, I use a state and time fixed effects model. I employ this specific model in my analysis across 32 states and 2 districts across the years 2004-2010. The fixed effects equation is modeled as follows: Yi = αi + λt + ρDit + ε it
where • Yit = (1) LOGTOTEMP, (2) LOGHMEAN; • Dit = instrumental variables; dummy variable indicating whether a state was affected • ρ = causal effect of interest • αi = state fixed effect • λt = year fixed effect Third, I employ an instrumental variables (IV) approach to determine causality. The passing of the FMWA in 2007 served as an exogenous shock to certain states, which previously had minimum wages below the new federal levels. This federal shift increased regular minimum wages at varying levels for states across the country. In order to relate this to the tipped minimum wage, I run a first-stage regression using a fixed effects model to establish a positive correlation between an increase in the regular minimum wage and an increase in the tipped minimum wage. This is likely, since as the legal wage is shifted up, states tend to 61
boost their standard of living for all low-wage workers and thus adjust their tipped minimum wage as well. Since this relationship between tipped and regular wages holds, the exogenous shift in the regular minimum wage can be used credibly to instrument for the effect of increasing tipped wages on employment and wages. Thus, the conditions for an IV are satisfied, since the FMWA changes regular and tipped minimum wage structures but is not itself correlated with employment and earnings. I construct this IV by creating a dummy variable and setting it equal to one if a state has a lower regular minimum wage in time t than the federal minimum wage in time t + 1, when the FMWA shifted from 2007 to 2008. I set this dummy to equal one if, when the FMWA again shifted from 2008 to 2009, the state minimum wage in t was below the destined federal minimum wage in t + 1. Once a state is affected by at least one shock, it is considered affected, and takes on the value one for the dummy AFFECTED. This IV is robust, since 24 of 34 states and districts were affected by the federal shift at least once, and therefore provide a statistically significant treatment sample, in addition to an existing and significant control group of unaffected states. In my final analysis I add an interaction term, AFFECTEDxTOTDIFF, since each state was affected differentially by the federal minimum wage shift depending on its pre-shift minimum wage. The AFFECTEDxTOTDIFF term is cumulative and reflects the additive shift from each federal shock to the state tipped minimum wage. The following equation includes my interaction term so as to reveal the effect of the degree of an exogenous shock: Yit = αi + λt + ρ ∗ AFFECTEDxTOTDIFFit + ε it
In effect, my strategy is twofold. First, I treat all changes in the tipped minimum wage as exogenous and run a fixed effects regression of wages on minimum wage controls and of employment on minimum wage controls. Second, I recognize that changes in the tipped minimum wage might very well be endogenous, so I restrict my sample to states where the tipped minimum wage was changed by a shift in the national laws. This empirical strategy allows me to discern the effect of tipped minimum wage structures on earnings and employment. 62
OLS Estimates on employment and earnings Employment
I examine the effects of higher tipped minimum wages on employment. In theory, higher tipped minimum wages would make it more expensive for a firm to hire waiters, and therefore employment would decrease. However, there may be positive effects on employment if a higher tipped minimum wage induces more people to enter the waiting profession as the guaranteed income increases. Column 1 of Table 3 reports the estimation results using the following basic OLS regression of tipped minimum wage on employment: LOGTOTEMPit = α + β 1 TIPMI NWAGEit + uit
The results of this regression indicate that, for each dollar increase in the tipped minimum wage, waiters’ employment increases by 3.8%, although not at a statistically significant level. This result – that an increase in the tipped minimum wage has no significant effect on employment – is surprising. One explanation is that the tipped minimum wage is so small that, even when the tipped minimum wage increases, it does not affect employers’ decision making, and so waiter employment is unaffected. Alternatively, opposing effects might be perfectly canceling each other out. That means that, as tipped wages are increased and waiters become more expensive to hire, employers fire the same amount of waiters as are induced to enter into the now higher-paid waiting profession. These results align with my final conclusion after multiple causal analyses.
Table 3: Basic OLS Regression – The effect of the tipped minimum wage on employment LOGTOTEMP – % Change in the employment (1)
Column 1 contains the results from the OLS regression Column 2 contains the reuslts from the OLS regression, clustering standard errors Column 3 contains the results from the OLS regression of the tipped minimum wage controlling for median household income between 20062010, for the sales in the food insustry in the year 2007 Column 4 contains the results from the OLS regression of the tipped minimum wage controlling for median household income between 20062010, for the sales in the food insustry in the year 2007 and for the stateincometax ***,**,* indicates statistical significance at the 1%, 5%, and 10% level, respectively.
Next, I examine the effects of higher tipped minimum wages on earnings. Higher tipped minimum wages would in theory lead to a higher direct revenue stream for waiters, and thus higher earnings. However, the higher the tipped minimum wage, the more the waiter earns from a guaranteed income as opposed to tips. This might mean that an increasing share of a waiter’s income is coming from non-merit based pay, thus stifling a waiter’s incentive to work hard and earn more. In this scenario, the higher tipped wage could result in a lower than expected increase in overall earnings. Column (1) of Table 4 reports the estimation results using the following basic OLS regression of tipped minimum wage on earnings: LOGHMEANit = α + β 1 TIPMI NWAGEit + uit
The results of this regression indicate that for each dollar increase in the tipped minimum wage, waiters’ earnings increase by 4.67% at a highly significant level. This would indicate that the immediate effect of greater tipped minimum wages is a guaranteed larger income stream for waiters. These results, however, are likely biased by unobserved factors, since they do not ultimately align with my most rigorous causal analysis using an IV, which indicates that increased minimum wages have no effects on earnings.
Table 4: Basic OLS Regression - The effect of the tipped minimum wage on earnings Panel A: LOGHMEAN - % Change in the earnings (1)
Column 1 contains the results from the OLS regression Column 2 contains the reuslts from the OLS regression, clustering standard errors Column 3 contains the results from the OLS regression of the tipped minimum wage controlling for median household income between 2006-2010, for the sales in the food insustry in the year 2007 Column 4 contains the results from the OLS regression of the tipped minimum wage controlling for median household income between 2006-2010, for the sales in the food insustry in the year 2007 and for the stateincometax ***,**,* indicates statistical significance at the 1%, 5%, and 10% level, respectively.
Fixed Effects Model
To obtain more precise estimates, I next address the omitted variable biases across states by employing a fixed effects model. This approach allows me to control for cross-state and time variation. Specifically, I control for characteristics across the 32 states and 2 districts in my sample between 2004 and 2010. These estimates would indicate the true effects of changes in the tipped minimum wages, not driven by state or time-varying characteristics. I employ the following regression, as outlined in Section 4: Yit = ﾎｱi + ﾎｻt + ﾏ．it + ﾎｵ it
My estimates indicate that a one-dollar increase in the tipped minimum wage results in .26% more employment, although not at a statistically significant level. This result confirms my analysis using the basic OLS regression. I conduct the same exercise for earnings and find a .47% increase in earnings, although also at an insignificant level. This result varies from my OLS estimates, indicating that, when I employ a fixed effects model, I am able to account for state and time variation. In this case, when I employ a more causal analysis, I show that higher tipped minimum wages have no effect on earnings. This might be the case if waiters display targeting behavior, where as their guaranteed income rises, they make less effort to earn more through tips. These results ultimately correspond to my most rigorous analysis using an IV and differences-in-differences approach.
Table 5: Fixed Effects, IV – The effect of the tipped minimum wage on employment Panel A: LOGTOTEMP – % Change in the earnings (1)
Column 1 describes the results of the state-fixed effects when we regress the mincashwage on earnings Column 2 describes the results when we use the IV affected Column 3 describes the results when we incorporate the IV affected into the fixed effects model Column 4 describes the results of the regression when we incorporate the interaction term affectedxtotfiff into the fixed effects model
Table 6: Fixed Effects, IV - The effect of the tipped minimum wage on earnings Panel A: LOGHMEAN – % Change in the earnings (1)
0.009878 [ .0102991]
Column 1 describes the results of the state-fixed effects when we regress the mincashwage on earnings Column 2 describes the results when we use the IV affected Column 3 describes the results when we incorporate the IV affected into the fixed effects model Column 4 describes the results of the regression when we incorporate the interaction term affectedxtotfiff into the fixed effects model
A Difference-in-Difference Approach
I next employ a differences-in-differences approach in combination with an IV. A discrete, exogenous policy shift allows me to conclude that any changes in employment and earnings are a result of the changes in tipped minimum wages. To this end, I analyze the effect of the FMWA, which occurred between 2007 and 2009. I segment time into two periods: a preFMWA period and a post-FMWA period. I further aggregate the degree to which the FMWA shifted state minimum wages after each of the two shifts. Depending on a stateâ€™s minimum wage in the pre-FMWA period, multiple states could have experienced an exogenous shift if their pre-FMWA period minimum wage was lower in time t than the FMWA wage in time t+1. As an example, Idaho had a minimum wage of $5.15 in 2007. The first FMWA shift moved the federal minimum wage up from $5.15 to $6.55 from 2007 to 2008. Thus, the Idaho minimum wage was pushed up to $6.55. California, on the other hand, had a minimum wage of $8.00 in 2007 and therefore saw no exogenous push to its minimum wage. In my sample, 22 out of 32 states and 2 districts experienced an exogenous increase in their regular minimum wage between the years 2007 and 2009. This in itself, however, is not enough to determine the effect of tipped minimum wages on earnings and employment. Thus, I employ the shift in the regular minimum wage as an exogenous variable only if shifts in the regular minimum wage are directly correlated to an increase in the tipped minimum wage, independent of state and time characteristics. To test this, I run a first-stage regression for the variable AFFECTED on the MINREGWAGE to verify that my IV is credible. This result shows that when a state is affected by the federal minimum wage shift between 2007 and 2009, the regular minimum wage increases by $1.08 at a statistically significant level. Next, I run a fixed effects model to verify that when the regular minimum wage increases, so does the tipped minimum wage, exclusive of other individual state and time-varying factors. This first-stage regression reveals that, when the regular minimum wage shifts by one dollar, the tipped minimum wage increases by 8 cents. This result is significant at the 10% level and indicates that AFFECTED can be used as a credibly exogenous 69
push to the tipped minimum wage. Next, I utilize my instrumental variable in my fixed effects model to run the following regression: Yit = αi + λt + AFFECTED + ε it
My results indicate that there is a 1.5% increase in employment when the tipped minimum wage increases by one dollar, though not at a statistically significant level. Thus, there is no effect of an increase in the tipped minimum wage on employment. When I run the same regression on earnings, the effect of a one-dollar increase in the tipped minimum wage increases earnings by 0.3% at an insignificant level. I further indicate the effect of the degree of the policy shift by including the interaction term AFFECTEDxTOTDIFF and running the following regression: Yit = αi + λt + AFFECTEDxTOTDIFIT + ε it
My estimates show that, for each dollar increase in the tipped minimum wage, earnings increase by 2.3%, with no significance. The effect of a tipped minimum wage increase on earnings also has no effect, with an insignificant .98% increase in earnings. These results are consistent with my fixed effects model. These results are surprising because they indicate that as one’s guaranteed income rises, one’s earnings remain the same and employment is unaffected. As discussed earlier, one reason why this might be true is that the tipped minimum wage is so low to begin with that a rise in this wage has no significant effect. This theory is hard to believe in the context of a typical lowwage worker, since even a 50-cent increase in one’s guaranteed income can translate to $1,460 more earnings a year if one works 8 hours a day. In the context of tipped employees, such as waiters, however, this theory is viable. Waiters, who earn a portion of their income from merit pay, might compensate for a higher guaranteed income by working fewer hours or less hard, thus earning the same amount they earned before. An explanation for why higher tipped minimum wages might affect employment could be the low absolute level of the guaranteed tipped minimum. Hiring waiters is not a huge cost for employers, and so increases in this 70
low cost do not induce employers to higher or fire waiters. Table 7: First Stage Regression Regular Minimum Wage (1) 1.083774 [.1641671]***
Table 8: First Stage Regression, fixed effects Tipped Minimum Wage (1) 0.088811 [.0523243]*
Regular Minimum Wage
In this paper, I examine the effects of the tipped minimum wages on earnings and employment using the FWMA as a quasi-experiment. I further examine a sub-section of the lowwage working population, which includes tipped workers. My results show that there is no employment effect of higher tipped minimum wages, consistent with the Card and Krueger (2000) results for the regular minimum wage. This result is surprising, though it might make sense specifically in the context of tipped employees, because tipped employees receive much lower wages than low-wage workers. Thus, employers might not hire or fire waiters since the cost of hiring a waiter is relatively low. Additionally, earnings might not change as waiters revert to â€œtargetingâ€? behavior. In this scenario, waiters compensate for a higher guaranteed salary by working fewer hours or working less hard. Further analysis could include the effect of the rising tipped minimum wage on hours worked. Additional research could also utilize Yelp reviews to indicate waiter effort levels through customer reviews. Linking Yelp-rated effort levels to
overall earnings would shed more light on the effect of merit pay on tipped employees.
References Brown, Charles. 1999. “Minimum wages, employment, and the distribution of income.” Handbook of labor economics 3:2101–2163. Brown, Charles C, Curtis Gilroy & Andrew I Kohen. 1982. The Effect of the Minimum Wage on Employment and Unemployment: A Survey. Cambridge, MA: National Bureau of Economic Research. Camerer, Colin, Linda Babcock, George Loewenstein & Richard Thaler. 1997. “Labor supply of New York City cabdrivers: One day at a time.” The Quarterly Journal of Economics 112(2):407–441. Card, David. 1992. “Using regional variation in wages to measure the effects of the federal minimum wage.” National Bureau of Economic Research. Card, David & Alan B Krueger. 2000. “Minimum wages and employment: a case study of the fast-food industry in New Jersey and Pennsylvania: reply.” The American Economic Review 90(5):1397– 1420. Chou, Yuan K. 2002. “Testing alternative models of labour supply: Evidence from taxi drivers in Singapore.” The Singapore Economic Review 47(01):17–47. Farber, Henry. 2003. “Is tomorrow another day? the labor supply of New York cab drivers.” National Bureau of Economic Research. Katz, Lawrence F & Alan B Krueger. 1992. “The effect of the minimum wage on the fast food industry.” National Bureau of Economic Research. Neumark, David & William Wascher. 2006. “Minimum wages and employment: A review of evidence from the new minimum wage research.” National Bureau of Economic Research.
An Economic Analysis of Intermarriage between American Indian Women and European Fur Traders Jasmine Barrett, Yale University1 Abstract. Through a detailed application of Beckerâ€™s Theory of Marriage to historical scholarship on the Canadian fur trade, this paper shows that marriages between European fur traders and American Indian women were economically efficient for both parties involved. Becker (1988) suggests that the decision to marry is made by analyzing the marginal costs and benefits of the potential union as well as the availability of desirable traits in the marriage market. It appears that fur traders who married American Indian women and thus adopted a new household division of labor were more economically successful than those who did not. Keywords: Indians
marriage, fur trade, Western Canada, American
1 Jasmine Barrett is a senior economics major at Yale University. The author would like to thank James and Ann Palmer.
During the seventeenth and eighteenth centuries, powerful fur trade companies were established in Western Canada that accelerated globalization and formed the basis for interactions between Europeans and American Indians in Western Canada. The most notable fur trade companies were the English Hudsonâ€™s Bay Company and the French North West Company. While the English established a line of trade posts along the shore of the Hudson Bay and rarely traveled inward, the French moved west and created vital trade links through their relations with American Indians that allowed them to set up posts along the Saskatchewan River, effectively diverting trade from the bay (Van Kirk 1983). While the importance of American Indian communities to the fur trade has been studied by scholars of economic history, the specific role that American Indian women played is rarely discussed. Understanding the nature of relationships between European men and Native women is key to understanding the inner workings of the fur trade. While trade was ultimately powered by large companies that seized the world market from the Russians and became dominant in the exploitation of beaver fur, the men who worked as the brute strength for this larger goal were ordinary, working-class men with lives that needed to be sustained on a domestic level (Innis 1999). In order to help cope with the harsh Canadian terrain and provide the prized beaver fur that made British and French companies so prominent, these men formed alliances with Native communities through marriages to Native American women. Gary S. Beckerâ€™s famous Theory of Marriage model provides insight into why these marriages would occur. Becker (1973) argues that the decision to marry is made by analyzing the marginal costs and benefits of the potential union as well as the availability of desirable traits in the marriage market. In an application of Beckerâ€™s model, this paper analyzes the inner workings of these marriages through a microeconomic framework.
Becker’s Theory of Marriage includes two primary assumptions: 1) The decision to marry is voluntary, and 2) the competition among men and women for mates creates a market for viable marriage partners (Becker 1973). Among Western Canadian tribes, these assumptions generally hold. In the majority of Native societies, the marriage of a daughter to a fur trader brought prestige and the promise of security to her family and thus was highly encouraged (Van Kirk 1984). Chiefs were said to have often “offered their daughters as a token of friendship,” and, sometimes believing that the fur traders who arrived in their territory were demi-gods, hoped that “they might bear children by such valorous men and bring into the world a new warrior caste” (O’Meara 1968, 19). American Indian women themselves were voluntary participants in the marriage market as well. Prominent scholars suggest that American Indian women sought relationships with European fur traders not only to benefit their families through the lasting trade partnerships that resulted, but also for the benefits of a much easier lifestyle at the trading posts (Van Kirk 1983). The life of an Indian woman was extremely difficult. European traders who observed the labor these women engaged in believed that they were treated like “drudges,” “pack animals,” and “slaves” by their Indian husbands (O’Meara 1968, 47). Women were expected to perform arduous tasks such as chopping wood and building large structures like canoes, in addition to the more traditional duties of cooking and cleaning (O’Meara 1968). American Indian men, on the other hand, were only responsible for hunting. In Europe, the concept of women performing such tasks was virtually unheard of. The Hudson’s Bay Company Factor Matthew Cocking observed that American Indian women were only given a few hours after childbirth to recover and then were expected to return to their laborious everyday duties. Naturalist John Bradbury wrote that Sioux and Cree women “frequently” hung themselves from trees in order to “escape a life of pure misery” and would sometimes kill their young female children as well “to save their babies from the same fate” (O’Meara 1968, 45). Marriages to fur traders offered American Indian women the 75
opportunity to live much more comfortably on the trade posts. Van Kirk (1983) points out that upon the return of an American Indian woman’s husband to Europe, she and her children would often either remain on the trading post grounds and be cared for by the company or remarry another trader. Native women often did not want to return home after becoming adjusted to life on the trade posts. Evidence suggests that the fur traders also entered into marriages voluntarily. James Isham, a prominent eighteenthcentury North West Company trading post governor, declared that marriage alliances created a “firm friendship” with the Indians and were a “great help in engaging them to trade” (Van Kirk 1983, 45). It was clear to tradesmen of all ranks that alliances with American Indian women would help them to compete against rival trade companies by establishing exclusive trade rights with various tribes (Brown 1980). In this sense, mini-monopolies on fur sources were created through marriage. Additionally, traders were much less likely to be ambushed, killed, or robbed in the forest if they were aligned with the Indians who occupied the territory (O’Meara 1968). In contrast to the North West Company, the Hudson’s Bay Company forbid intermarriage with Native women. Intermarriages still occurred, however, indicating that the gains from these marriages were enough to outweigh the costs of potential fines or punishment through the English court system (Van Kirk 1983). Furthermore, these laws were rarely enforced due to the distance between law enforcers in England and traders in Western Canada. Henry Kelsey, an explorer famous for his thousand-mile-long excursions westward, defied the governor of York and the laws prohibiting American Indian women from entering the trade post by declaring, “Either my wife comes in with me, or I’ll go and live with her people.” After consideration, Kelsey and his wife were allowed to enter (O’Meara 1968, 18). The competition among European men for Native women was certainly strong and created a viable marriage market, satisfying Becker’s second assumption. The desire of Native women to have a less strenuous lifestyle also led them to compete for potential partners. Trader Pierre Antoine-Tabeau observed that Cree women “were not unconscious [of] their deplorable state and 76
made efforts to escape it — preferably by running off with a white man.” European men demonstrated the value they placed on companionship by allocating their wages in a manner that would secure their relationships with American Indian women, even before marriage became a possibility. Trading officer Alexander Henry the Younger wrote of a man who paid the vast majority of his savings for “one single touch [of] a slave girl.” Additionally, Henry speaks freely in his accounts of many men who, despite being in debt, would offer their services in the form of indentured servitude, so long as they would be given clothes, lodging, and permission to marry American Indian women they had “fallen in love with” (O’Meara 1968, 18).
Comparing Utilities: Costs and Benefits of Intermarriage
Becker’s Theory of Marriage suggests that in order to understand why a male and a female would want to become betrothed, one must compare married life to the alternative: remaining single. He considers two parties as married if they share the same household, and asserts that marriage occurs “if and only if, both [the male and female] are made better off — that is, [they] increase their utility” by being together (Becker 1973, 301). For American Indian women, the alternatives to marrying a European fur trader did not offer comparable levels of utility. Her options were either to marry an American Indian man or to remain single in the home of her family. In both cases, life in Indian Country required women to balance domestic duties with the production of commodities such as clothing, moccasins, blankets, and tools needed on hunts for fur. Although American Indian women sacrificed proximity to their families and were sometimes the victims of racism in their lives on trade posts, the utility gained from a lighter workload was high enough to incentivize them. Even for the lowest ranking engages, living quarters were warm and relatively spacious, and tasks could be performed with relative ease. For Native women who married high-ranking officers, life was even more comfortable. Hired help performed the tasks of cooking and cleaning, and wives enjoyed fine feasts
and imported wine with their husbands and other members of the bourgeoisie (O’Meara 1968). Although most scholars agree that the quality of life for American Indian women generally improved drastically after marriage to a fur trader, Bourgeault (1983) suggests that Native women who stayed in their communities retained a wider array of valuable skills, while Native wives at trade posts became increasingly specialized in fur trade related tasks and could not develop skills necessary to be self-sufficient in their Native communities. Daily tasks for American Indian women living within their Native communities were changing also, however, as local markets became increasingly focused on the fur trade. In either case, skills related to the fur trade became an integral part of daily life, making a move to a trade post even desirable (O’Meara 1968, Bourgeault 1983). It is paramount to note however, that the Indian wives of fur traders relinquished some duties because of the structure of the trade posts themselves, rather than because they no longer had the necessary skills. European men took on duties such as gathering firewood so that Native American women could spend their time cleaning the pelts of beavers their husbands had killed and cooking meals. Wives of fur traders were intimately involved in the business of their husbands and established strong relationships with fellow married American Indian women. Indian wives at the trade posts worked together to produce snow shoes that traders used and preserved fat from meat called Pemmican, which traders would eat while out on hunts (O’Meara 1968). For the fur traders themselves, the gains from marriage were also readily apparent. Traders gained the sexual gratification and companionship they desperately desired on the womanless frontiers. They often commented on the “physical and sexual attractiveness of many of the Indian women” in their journals, and American Indian chiefs often remarked on lusty attitudes of the “sex-hungry frontiersmen.” While it is true that a fur trader could have found sexual gratification in the arms of “squaw prostitutes,” he would not be able to simultaneously gain an experienced business partner who was skillfully trained in housekeeping, cooking, and fur trade related tasks, as well as an exclusive trade relationship with an American Indian tribe (O’Meara 1968, 201). 78
Hunting was a time-consuming, dangerous business that required much of the husband’s time (Van Kirk 1983). The potential economic gains from hunting and killing game were much higher than those from allocating the same portion of time to building the tools necessary to hunt. It was essential for these men to have companions with the skills necessary to perform tasks such as making hunting tools and snowshoes (since they were frequently broken or lost), as well as cleaning beaver pelts. For a fur trader, the cost of hiring an American Indian woman to make these tools, while lower than the cost of making them himself, was higher than that of taking on a wife. Further, if a fur trader did not have a wife to prepare food, he would have to buy it from hostesses along the trading posts.
Becker’s analysis of “assortative mating” states that the “likes” (that is, qualities that both the male and female share) between couples decrease in importance if the “unlikes” (the qualities on which the male and female differ) are ones which maximize total household commodity output over the course of the marriage. Optimal sorting occurs when males and females share “likenesses” to each other in key categories such as intelligence, race, and religion (Becker 1973, 303). For American Indian women and European men, differing in key “likes” such as race and religion actually contributed to the success of their unions. Due to cultural differences, European men seemed much more willing to make the Native woman’s workload balanced, and the organization of the fur trade companies brought a new sense of order and structure to the lives of American Indian women. Many traders described American Indian women’s temperaments as agreeable and conducive to long lasting partnerships (O’Meara 1968). Native women appreciated the comfort they experienced while living with their husbands at the trade posts. Additionally, Native American women, who were hard workers and had been trained in many tasks, were able to produce commodities that enriched the lives of the traders.
Utility depends in part on the commodities produced by each household, according to Becker (1973). American Indian women used spices and alcohol they purchased in trade post markets, along with berries and other leafy edibles that they collected themselves, to cook meals for their families. Husbands hunted animals both for trade and for family consumption, and wives used the skins and bones to create moccasins and tools that the husband then reused for hunting. The quality of meals certainly improved for fur traders, as single traders were known for eating only fish and occasionally larger game and drinking brandy. Native women, who had both the time and skill to produce higher quality meals, provided the variety that traders needed in their diets. Ojibwe women, for example, mixed “pounded hazelnuts into their maize cakes to give them a buttery taste,” and “thickened their soups with swan potatoes, fried pumpkin blossoms, and trout herb” (O’Meara 1968, 246). Native women’s cooking not only provided their husbands with the variance in diet that was needed to prolong their lives but also with the calories necessary for long hours of hunting in the cold Canadian terrain. Living at trade posts and having access to the goods necessary to produce household commodities benefited American Indian women as well. Instances of starvation were much less frequent at the trade posts than in Indian communities. Having to spend less time gathering food meant that women had more time to produce items such as woven blankets, which were sold on the market and contributed additional income to the household (O’Meara 1968). For these families, utility as defined by commodities produced was high, further indicating that the total utility in a married household on the Western Canadian frontier was generally much higher than the sum of the utilities of individuals who did not intermarry.
Becker’s marriage model postulates that an important beneficial role of marriages between men and women is to raise children. He argues that other desirables such as sexual gratification, housekeeping, cooking, and other services can be purchased, 80
but children cannot (Becker 1973). Within the context of the Western Canadian fur trading frontier, this is certainly true. Many European men, particularly those in the French North West Company, had à la facon du pays marriages, which translates to “in the manner of the country” (Van Kirk 1983). Europeans adopted Native customs in these marriages, which tended to be rather informal by European standards. Indian chiefs freely offered their daughters to European men in a “pleasant gesture of hospitality.” The simplicity of Indian marriage arrangements were “much to the taste of fur traders,” who readily adapted to the customs of the tribes even, in some cases, to the extent of taking brides of nine or ten years old. In Huron communities, a “young couple lived together for a week or two, and if it did not work out, each felt free to try again with another mate.” Fur traders appreciated the ease with which they could divorce, as they were able to “cast [their] wives à la facon du pays adrift” once they were ready to return to Europe (O’Meara 1968, 246). Despite the informality of these marriages, many unions provided both fur traders and Native women with children. From the standpoint of Becker’s Theory of Marriage, investment in family life by adding children and love “into the equation” increases the utility of the marriage. As this investment increases, changing spouses becomes more costly relative to marginal utility. Optimal utility occurs when the husband or wife in question loves his family just as much, if not more, than he loves himself (Becker 1973). The personalities of the individuals within the family unit are unique and not interchangeable, and a child that a specific man and woman produce together is not interchangeable for another child. While it is possible that each parent could have other children, a child possessing the same qualities could not have been produced by any other union. Fur traders demonstrated their love for their half-Indian children by paying for their formal education and including them in their wills. Their mixed-race daughters commonly attended finishing schools where they were taught “European virtues” and prepared for marriage to new fur traders arriving from Europe. These women became the ideal wives for fur traders due to their skill in fur trade related labor and their knowledge of European customs (Van Kirk 1983). 81
While some historians claim that polygamy was rare among traders on the fur trade frontier because of Englishmen’s “morale and sense of gentlemanliness,” it is more likely that monogamous marriage was motivated by the benefits it provided (Brown 1980, 5). Since fur traders and American Indian women were viewed as interchangeable on the marriage market, the law of “diminishing returns” as proposed by Becker incited traders to remain monogamous (Becker 1973, 303). Adding wives to a household would likely diminish efficiency, since there was a finite amount of food to prepare and a limited number of tools that needed to be made for the one husband to hunt. Further, household income restricted the amount of market goods that could be purchased at one time. Additional wives would not have helped to run the household any more efficiently, and in most cases, would have actually impeded it. There would have been more mouths to feed without the additional income needed to supplement them.
Becker’s Theory of Marriage argues that the gains from marriage must be balanced against the costs to determine whether marriage is worthwhile. In the case of Euro-Indian marriages, the gains from marriage far outweighed the costs for both parties. Becker’s model, though constructed in the late twentieth century, applies directly to the marriage activities on the Western Canadian frontier during the seventeenth and eighteenth centuries. The key incentives and marriage markets that formed on fur trade territories provided a pivotal foundation that would help sustain the trade for centuries.
References Becker, Gary S. 1973. “A Theory of Marriage: Part I.” Journal of Political Economy 81(4):813–46. Bourgeault, Ron G. 1983. “The Indians, the Metis and the Fur Trade: Class, Sexism and Racism in the Transition from “Communism" to Capitalism.” Studies in Political Economy 12:45–80.
Brown, Jennifer SH. 1980. Strangers in blood: fur trade company families in Indian country. Vancouver: University of British Columbia Press. Innis, Harold Adams. 1999. The fur trade in Canada: An introduction to Canadian economic history. Toronto: University of Toronto Press. O’Meara, Walter. 1968. Daughters of the country: the women of the fur traders and mountain men. New York: Harcourt, Brace & World. Van Kirk, Sylvia. 1983. Many tender ties: Women in fur-trade society, 16701870. Norman: University of Oklahoma Press. Van Kirk, Sylvia. 1984. “The role of Native women in the fur trade society of western Canada, 1670-1830.” Frontiers: A Journal of Women Studies 7(3):9–13.
Do Laptops Improve Student Performance? Lauren Zumbach, Princeton University1 Abstract. Increasingly, schools are turning to technology in the hopes of improving student performance while realizing the productivity gains technology has brought to other sectors. But despite the enthusiasm for technologyâ€™s potential to play a role in education reform, research into the actual effects of classroom technology on student achievement has lagged behind introduction of such programs. This paper examines what is currently the largest one-to-one technology program, the Maine Learning Technology Initiative, using a difference-in-difference approach to test whether providing all students with individual laptops translates into higher test scores. Empirical analysis using Maine Department of Education data shows that the introduction of laptops is associated with lower test scores in all subjects, particularly in small schools in which classroom technology may be a particularly large financial burden. This suggests that despite classroom technologyâ€™s great potential, it is not a quick fix for struggling schools. Keywords: technology, education, natural experiment
Zumbach is a senior economics major at Princeton University. The author would like to thank her independent work advisor, Professor Ilyana Kuziemko, and Xiaotong Niu, for their invaluable guidance throughout her research process.
As personal computing technology increases in power and decreases in cost, schools are increasingly turning to technology as a way to not only prepare students for a world in which technology skills are essential, but also in hopes of realizing the productivity gains technology has brought to other sectors (Gulek & Demirtas 2005). Classroom technology used to consist of a single computer or school-wide computer lab used only infrequently and had little impact on day-to-day classroom instruction (Cuban & Cuban 2003), but there are now many a large number of one-to-one computing initiatives that provide every student with a laptop computer for use in the classroom and at home. Advocates of one-to-one technology programs argue that laptops can increase productivity in the education system through increased engagement and learning without increasing the primary input, teachers’ labor (Penuel 2006). However, existing research has shown mixed and even contradictory results, with critics suggesting that laptops may be little more than a costly distraction that promotes a passive learning style (Angrist & Lavy 2002). This paper examines Maine’s statewide one-to-one laptop initiative to test whether the assumed benefits of classroom technology improve student learning outcomes and translate into higher test scores and reduced absenteeism. Maine’s Learning Technology Initiative presents a unique opportunity to evaluate the impact of classroom technology on student achievement because 55% of high schools chose to adopt the laptop initiative, which allows me to compare student performance between laptop and non-laptop districts. Evidence of tangible benefits of such programs, or lack thereof, should lead to a better understanding of classroom technology’s impact on student learning and whether the benefits justify the significant costs. The remainder of the paper proceeds as follows. Section 2 reviews related literature on classroom technology and one-to-one laptop initiatives. Section 3 describes the Maine Department of Education (DOE) data and outlines my empirical strategy. Section 4 provides results, with analysis in Section 5. Section 6 concludes. 85
The theoretical framework for one-to-one laptop programs, often drawing on psychological research, generally supports the idea that one-to-one computing programs enhance student learning outcomes by using technology to create new learning opportunities. Lage, Platt and Tueglia (2000) both found that incorporating technology and online resources increased student engagement, and Gulek (2005) found that when students are more engaged in school, they tend to improve more. Zurita and Nussbaum (2004) argue that networked devices and new media facilitate collaborative learning, with Wilensky and Stroup (2000) adding that simulations, an example of collaborative learning, allow students to experience complex systems directly and better understand them. Gulek and Demirtas (2005) note prior findings that students with their own laptops spend more time in collaborative work, participate in more in-depth projects, report more active learning strategies, and improve research and analysis skills. Critics, however, argue that laptops may be more of a distraction than a benefit and may promote more passive forms of learning (2002). Windschitl and Sahl (2002) found that extensive support and training for teachers is crucial for these programs to succeed, and that teacher attitudes towards technology have a significant impact on both a program’s success and whether adding technology has an impact on classrooms. Gritter (2005) found that teachers’ feeling of preparedness — affected by how much training was provided — in turn affected how much they used technology in class. Surprisingly, though one-to-one laptop programs have rapidly grown in popularity, empirical evaluations have not kept pace. Though a preponderance of existing literature seems to favor oneto-one laptop programs, empirical evidence thus far is mixed and even contradictory. I have chosen to focus on Maine’s one-to-one laptop program, as it has, thus far, the most extensive one-to-one computing program in the United States and possibly worldwide (2006). In 2002, the state piloted the Maine Learning Technology Initiative, which had a goal of providing every middle school and, 86
eventually, high school student in the state with a personal laptop for use in class and at home. The pilot program gave every seventh grader in a single middle school a laptop; the following year, every public school seventh grader in the state received one. In 2009, the program expanded to the high school level; however, while middle schools received laptops for free, high schools had to absorb some of the cost and as such participation was voluntary. 55% of high schools chose to join the Maine Learning Technology Initiative (Silvernail et al. 2008). Decisions on how to work laptops into the curriculum were left to individual teachers, but at the middle school level, over 80% of students reported using the laptops in language arts, social studies, and science classes, and 64% reported using them in math classes.2 Teachers attributed the gap to greater ease in finding quality online resources related to writing, history, and science. I focus on potential improvements in student achievement in subjects that are part of the standard curriculum. Gulek and Demirtas (2005) and Silvernail and Gritter (2007) find evidence that one-to-one laptop programs improve students’ writing ability. Silvernail and Gritter’s results were based on surveys given to teachers of Maine middle schoolers. However, they do not consider other subjects, and only Gulek and Demirtas look at students’ test scores in addition to more qualitative selfassessments from surveyed students. When Gulek and Demirtas (2005) looked at test scores in subjects other than writing, however, they did not see clear gains. In addition to score benefits that vary by subject, researchers have found varying performance based on students’ socioeconomic background. Muir, Knezek and Christensen (2004) found that at-risk or low-achieving students benefited most from laptop programs, estimating the laptop program they studied put the students two months further ahead in math, science, and the visual and performing arts than they would have been in a traditional classroom setting. However, most of the quantitative studies focus on individual 2 Maine Education Policy Research Institute. 2003. The Maine Learning Technology Initiative: Teacher, Student, and School Perspectives Mid-Year Evaluation Report. Gorham, ME: Maine Education Policy Research Institute, Center for Education Policy Applied Research, and Evaluation, University of Southern Maine.
schools or districts, or even a subset of students within a single school, and they compare mean test scores before and after laptops were introduced. This method fails to separate the impact of laptops from any broader trend in scores. Focusing on single schools or districts also makes it very difficult to generalize the results of the past studies. The way a particular school designs and implements a program — how much professional development and support is available to teachers, how extensively laptops are used in class, etc. — all significantly affect a program’s success (Penuel 2006), and make it quite likely that individual schools will see very different outcomes. While there will still be variation in how teachers use laptops in the Maine program, the Maine DOE did develop statewide programs to help teachers integrate the laptops into the curriculum. Each school, for example, selected a teacher to be their Technology Leader, someone comfortable with the laptop technology who could mentor less-experienced colleagues. Content Mentors were chosen to help teachers identify online resources specific to their subject and give them ideas for incorporating the laptops into the curriculum.3 While the results of this paper will still be strongly influenced by the specific implementation strategy Maine chose, it is unique in that it is the only example of what a one-to-one laptop program looks like when implemented by the state public school system. In assessing the potential impact of large-scale classroom technology programs, it would seem more reasonable to generalize from results of a statewide program like Maine’s, rather than those of a single experimental school or district. Even though there has been research on the Maine Learning Technology Initiative, to the best of my knowledge this paper is unique in its examination of the high school program as a natural experiment, comparing average changes in score before and after the laptop program was introduced between laptop and non-laptop districts. 3 See the Maine Learning Technology Initiative: Teacher, Student, and School Perspectives Mid-Year Evaluation Report (2003).
Data and Methodology
I analyze data from Maine’s Department of Education (DOE), which collects standardized test score data at the school and district level, as well as basic demographic data, attendance and school finance data. I use the Maine High School Assessment (MHSA), given yearly at the 11th grade level. The MHSA score data are consistent, since the test itself is the nationwide SAT test along with a supplemental science test, and it is available for several years before and after the Maine Learning Technology Initiative was introduced at the high school level. I specifically consider MHSA score data for Maine 11th graders for the 20052006 through 2010-2011 academic years.4 Test score summary statistics are displayed in Table 2. There is a clear gap between laptop and non-laptop schools, with a statistically significant difference between the groups in average total score and in all subject scores. In these figures, 2010 (corresponding to the 2009-2010 school year) is the first year in which students receiving laptops would have been tested. It appears that average total scores, weighted by enrollment, increase fairly steadily for non-laptop districts while performance for laptop districts is flatter, producing a larger performance gap at the end of the period. The gap in science scores appears to stay fairly constant, while gaps in math, reading and writing appear to increase over time. The difference is small — less than two points for any given subject — but statistically significant. The Maine DOE also collects information on basic demographics, which is useful in accounting for the impact of underlying district characteristics on differing achievement levels across districts. Including demographic data in the regression also allows analysis of differences in the way the laptop program impacts particular groups of students — for example, Knezek and Christensen (2004) found that students 4 For
each subject, possible scores range from 1120 to 1180 (11 is a prefix signifying grade 11, while 20-80 corresponds to the first two digits of the student’s score on that section of the SAT). I define the total score as the sum of a student’s math, reading, and writing subject scores for a possible range of 3360 to 3540.
Mean Median Std. Dev. Variance Skew N Min Max
Mean Median Std. Dev. Variance Skew N Min Max
Table 1: District Characteristics Summary Statistics Total Score
Per Pupil Expenditure
371.39 219 399.6 159654.7 1.45 843 0 2488
Percent Disadvantaged Students
10486.64 9883.08 3061.14 9370571 3.007 881 3553.17 36853.8
92.13 92.27 2.828 7.998 -0.367 327 82.29 100
Percent English Learners
0.43 0.45 0.191 0.036 -0.277 843 0 1
3420.3 3418 13.48 181.66 1.014 789 3375 3486
0.01 0 0.049 0.002 9.61 842 0 0.85
Table 2: Test Score Summary Statistics
Mean Median Std. Dev. Variance Skew N Min Max
3420.3 3418 13.48 181.66 1.01 789 3375 3486
1140.5 1140 4.07 16.58 1.24 789 1127 1162
1140.2 1140 5.03 25.3 0.94 789 1124 1164
1139.5 1139 4.96 24.58 0.76 789 1123 1161
1140.3 1140 3.64 13.24 0.87 571 1125 1163
from low-income families derived greater benefit from laptop program, possibly because they did not have access to a computer at home and the new program made it easier for them to work on assignments outside the classroom. On the district level, the relevant demographic factors for this paper will be the percentage of students qualifying as â€œdisadvantaged,â€? the percentage of English language learners in grades 9-12 and the districtâ€™s average enrollment and expenditure per student. Summary statistics for demographic data are displayed in Table 1. The enrollment data are averages of enrollment figures taken throughout the year, which explains why enrollment is not a whole number. The percentage of disadvantaged students refers to the percentage of students in a district qualifying for free or reduced-price lunches through the National School Lunch Program based on household income. Per pupil operating cost includes all expenditures and revenues each district reports to the DOE annually. As with test score data, there are statistically significant differences, across demographic characteristics, between the districts that chose to purchase laptops and those that did not. Laptop districts tend to have larger average and median enrollments. Laptop districts also have, on average, about 4% more students qualifying for federal subsidies than non-laptop schools, and also have higher per pupil expenditures. The difference between laptop and non-laptop schools in average enrollment, per pupil expenditures, and percentage of students qualifying for subsidies is statistically significant, while the gap 91
between average attendance and percentage of English language learners is not statistically significant. Although there are differences in pretreatment characteristics between laptop and non-laptop districts, these variables are relatively constant over time. Lack of significant changes in the control variables over the period studied means observed changes in the difference in scores between laptop and non-laptop districts can reasonably be attributed to the factor that did change, the laptop initiative. The one exception is the percentage of students qualifying for federal subsidies, which rose for both groups of districts following the 2008 financial crisis.
I used a difference-in-differences approach and regression analysis of the Maine DOE data to test whether implementation of the Maine Learning Technology Initiative has an effect on 11th grade studentsâ€™ MHSA scores and attendance rates, using panel data from each school year between 2005-06 and 2010-11. I use difference-in-differences analysis to compare the change in districtsâ€™ mean scores from the pre-laptop policy period to the years following the introduction of laptops at the beginning of the 2009-2010 school year, using the schools that never adopted the laptop program as the control group. Since participation in the laptop program was self-selected and therefore nonrandom, there will be selection bias. However, by including additional regressors for underlying district characteristics I can explicitly control for some of the factors that are correlated with both likelihood of adopting the laptop program and student achievement, and differences-in-differences will eliminate pretreatment differences between districts that adopted laptops and those that did not to the extent that underlying differences between districts are relatively constant over time â€” a reasonable assumption given that most reflect demographic characteristics that are do not vary significantly year-to-year. Because this model looks at changes over time, any additional difference in scores can be attributed to the primary factor that changed during the time period I examine, the laptop program.
Before estimating the main regression, since the assignment of the “treatment” — participation in the laptop program — was nonrandom, I model the determinants of districts’ participation in the laptop program using a logit regression to see which, if any, of the pretreatment district characteristics predict participation: Pr ( Laptopi = 1| Enroll, Disad, Budget, pELL, ScoreZ )
= Φ( β 0 + β 1 Enrolli + β 2 Disadi + β 3 Budgeti + β 4 ScoreZi )
Laptop is an indicator variable that takes the value 1 for districts that adopted the laptop program and 0 for districts that did not. Enroll is a district’s average yearly enrollment. Disad is the percentage of a district’s students whose family income qualifies them for free or reduced price lunches through the National School Lunch Program. Budget is the budgeted operating cost per pupil the district reported to the DOE. ScoreZ is the Z score for a given district’s total MHSA score. Since this regression assesses pretreatment characteristics for possible sources of omitted variable bias and nonrandom selection, I use only data from the years before laptops were introduced. My main regression equation analyzes the impact of the laptop policy on MHSA scores and daily attendance. I test whether schools with laptop programs experienced a statistically significant change in average test scores in the years following the introduction of the laptop program. Scoredt = β 0 + β 1 Laptopd + β 2 A f ter09t
+ β 3 Laptopd ∗ A f ter09t + β 4 Enrolld + β 5 Disadd + β 6 pELLd + β 7 Budgetd + β 8 Postmergerd + udt
Scoredt is a district’s average total MHSA score. The regression is repeated for a series of Score variables corresponding to subject areas — ScoreMathdt , ScoreReaddt , ScoreWridt , ScoreScidt — since previous studies found that laptop programs affected student performance differently in different subjects. Laptopd is the same indicator variable described above, and A f ter09t is an indicator variable that takes on the value 1 if the data was collected after the 93
laptops were introduced in the 2009-10 school year. Postermergerd is an indicator variable that takes the value 1 if the district was one of the 15 formed by joining smaller districts in 2009. Laptopd ∗ A f ter09t is an interaction term of two indicator variables, and takes on the value 1 for data collected in districts that adopted laptop programs during the years the program was in place. In this regression, β 0 is the average test score for non-laptop districts prior to 2009, when the laptop program was implemented. β 1 is an estimator of the difference between the laptop and non-laptop districts in the period before the laptops were actually introduced. β 2 estimates the difference between average test scores before and after the laptop program’s implementation among the control districts, and β 3 , the coefficient on the interaction between the indicator variable for adoption of a laptop program and a year following the program’s introduction, is the estimator of the change in mean score attributable to a district’s adopting a laptop program. I run one version of this regression with an additional set of variables to test whether the effects of a laptop program vary with certain district characteristics and to examine possible sources of bias: Scoredt = β 0 + β 1 Laptopd + β 2 A f ter09t
+ β 3 Laptopd ∗ A f ter09t + β 4 Enrolld + β 5 Disadd + β 6 pELLd + β 7 Budgetd + β 8 HighDisadd + β 9 HighDisad ∗ Laptopd + β 10 HighDisad ∗ A f ter09d + β 11 HighDisad ∗ Laptop ∗ A f ter09d + β 12 Smalld + β 13 Small ∗ Laptopd + β 14 Small ∗ A f ter09d + β 15 Small ∗ Laptop ∗ A f ter09d + udt
HighDisad is an indicator variable that takes the value 1 if a district’s percentage of students qualifying for federal subsidies is in the top 25% of all Maine districts. HighDisad ∗ Laptop ∗ A f ter09 is an interaction term of three indicator variables and its coefficient, β 9 , is an estimator of the change in mean score attributable to a district’s adopting a laptop program in districts with a high percentage of disadvantaged students. Small is an 94
indicator variable that takes the value 1 if a district is in the smallest 25% of all Maine districts. Similarly, Small ∗ Laptop ∗ A f ter09 is an interaction term of three indicator variables and its coefficient, β 15 , estimates the change in mean score attributable to a district’s adopting a laptop program in small districts. To examine possible sources of bias due to school spending and budgetary considerations, I also run a regression on per student spending to test whether any district characteristics affect per-student spending. Variables are the same as in the regressions described above. Budgetdt = β 0 + β 1 Laptopd
+ β 2 A f ter09t + β 3 Laptopd ∗ A f ter09t + β 4 Enrolld + β 5 Disadd + β 6 pELLd + udt
Results Logistic Regression
The linear probability model predicting which district characteristics influence a district’s decision whether to adopt a laptop program gives results consistent with the observed differences between laptop and non-laptop districts. Per pupil expenditure has a small but statistically significant positive contribution, indicating that higher-spending districts are more likely to incur the additional expense to purchase laptops. The final characteristic that affects the probability of a district participating is its performance relative to other districts on standardized tests. Lower-performing districts were significantly more likely to choose to participate, perhaps because they saw it as an opportunity to catch up. The pseudo R-squared for the logistic model is still quite low, at 0.0894.
Performance — Test Scores
Table 5 and 6 display regression results where the dependent variable is the district’s total MHSA score, and Table 7 shows regressions for individual subject areas. All regressions use 95
Table 3: Logistic Regression Predicting Laptop Program Participation Dependent Variable:
Pr(laptop = 1) 1
Pr(laptop = 1) 2
Enroll (Std error) % Disadvantaged (Std error) Total MHSA Score (Z score) % English learners (Std error) Per Pupil Expenditures (Std error) Intercept (Std error) N Pseudo - R-squared
0.000604 ** 0.000276 -0.214 0.844 -0.345 ** -0.161
0.000644 ** 0.000278 -0.186 0.845 -0.352 ** -0.162 -2.364 2.643 0.000332 *** 5.82E-05 -3.989 *** 0.743 413 0.0894
0.000326 *** 5.73E-05 -3.915 *** 0.735 413 0.0895
balanced samples. For total test scores, the significant factors are sensitive to the particular specification. The coefficient on A f ter09 is statistically significant, indicating an upward trend in scores over time. Using data weighted by enrollment, post-2009 scores are approximately 2 points higher than pre-2009 scores, while unweighted data show an average gain of approximately 5 points across districts. The impact of the laptop program, as measured by Laptop âˆ— A f ter09, is significant at the 5% level, robust to the inclusion of control variables and equivalent to a 4 to 6-point decline in average total score, but only before weighting the data by district enrollment. The fact that significance depends on whether or not data are weighted suggests that the impact of laptops may vary by district size, or that there is another factor that determines how laptops affect student performance that is also related to school size. There is one other variable, per pupil expenditures, for which the effect on student test scores varies depending on whether weighted or unweighted data are used. When weighted by enrollment, expenditures are significant at the 1% level, with a one-point increase in average total score for a $1,000 increase 96
Table 4: Linear Regression of Per Student Spending Dependent Variable: Per Pupil Expenditure Laptop (Std error) After09 (Std error) Laptop_After (Std error) Enrollment (Std error) % English Learners (Std error) % Disadvantaged (Std error) Intercept (Std error) Weighted? Fixed Effects? N R-Squared
2194.4** (308.5) 550.2** (258.7) 445.3 (657.7) -1.796*** (0.33) 8814.4** (4019.8) -543.9 (957.1) 10637.2*** (464.5) No No 673 0.18
702.3*** (158.2) 667.4*** (219) -159 (408) -1.399*** (0.181) 17197.3*** (2798.6) -535.7 (447.7) 10870.6*** (239.7) Yes No 673 0.174
338.9*** (130.7) 456.9 (305.7) -6.495*** (1.432) 24032.2*** (2614.5) 1244 (1114.8) 12382.7*** (768.3) No Yes 673 0.842
340.5*** (110.1) -85.4 (271.9) -7.980*** (1.641) 16845.2*** (4955.2) 3043.9** (1403.9) 15186.5*** (1439) Yes Yes 673 0.807
***,**,* indicates statistical significance at the 1%, 5%, and 10% level, respectively.
Table 5: Linear Regression of Test Scores, Part A Dependent Variable: Total MHSA Score Laptop (Std error) After09 Laptop*After Enrollment
-2.843 ** (1.188) 5.331 ** (2.151) -6.286 ** (2.767)
-3.611 *** (1.241) 2.527 (2.17) -2.134 (2.71)
2.121 *** (0.692) -1.467 ** (0.954)
No No 521 0.036
Yes No 521 0.033
Yes Yes 521 0.911
% English Learners Per Pupil Expenditures % Disadvantaged Post-merger High Disadvantaged
4 -1.063 (0.912) 5. 523 *** (1.652) -4.157 ** (2.031) -0.001 (0.001) -17.84 ** (8.409) 0.0001 (0.0002) -47.70 *** (3.635) -5.035 *** (0.873)
High Disad * Laptop High Disad * After High Disad * Laptop*After Small Small*Laptop Small*After Small*Laptop *After Weighted? Fixed Effects? N R-Squared
No No 521 0.47
Table 6: Linear Regression of Test Scores, Part B Dependent Variable: Total MHSA Score Laptop (Std error) After09 Laptop*After Enrollment % English Learners Per Pupil Expenditures % Disadvantaged Post-merger High Disadvantaged
-1.274 (0.817) 3.199 ** (1.372) -1.175 (1.664) -0.0007 (0.001) -1.972 (11.26) 0.0008 ***
-1.986 ** (0.951) 2.14 (1.705) -0.071 (2.001) -0.0005 (0.001) 13.8 (12.56) 0.0010 ***
3.697 *** (1.104) -4.284 *** (1.33) -0.0133 (0.0112) -15.61 (32.58) -0.00003
2.223 *** (0.72) -1.453 (0.933) 0.0075 (0.0092) 8.951 (16.66) 0.0010 ***
1.742 ** (0.806) -0.684 (1.046) 0.0078 (0.009) 8.106 (15.6) 0.0001
(0.0002) -53.94 *** (2.838) -5.247 *** (0.841)
(0.0002) -57.29 *** (3.62)
(0.0004) -8.882 (9.941)
(0.0002) 1.936 (6.704)
(0.0002) 3.419 (7.533)
High Disad*Laptop High Disad*After High Disad*Laptop*After Small Small*Laptop Small*After Small*Laptop*After Weighted? Fixed Effects? N R-Squared
Yes No 521 0.616
(1.786) 1.562 (2.33) -4.986
(2.269) 0.635 (1.794) -0.784
(3.752) -2.129 (1.557) -2.88 (1.925) 7.273 (4.535) -8.648 (5.675) Yes No 521 0.599
(2.892) -2.81 (4.488) 16.17 *** (5.415) 8.666 *** (2.746) -12.00 *** (3.618) Yes Yes 521 0.914
No Yes 521 0.843
Yes Yes 521 0.911
in per-student spending, using the weighted, fixed-effects model with all controls except HighDisad, Small, and the interactions with those variables. This model, (8) in Table 6, is the model with the lowest root mean squared error, or standard deviation of the regression, and therefore the specification with the best fit. Enroll has a very small, not significant but consistently negative effect on scores. The percentage of students learning English is statistically significant if Disad, the percentage of students qualifying for federal subsidies is left out of the model but is not significant if Disad is included. The change in the significance of the percentage of English language learners (pELL) is likely because there is a statistically significant correlation between the variables and the magnitude of the coefficient on the percentage of disadvantaged students was much greater, so the variation in score attributed to pELL in models (3) and (4) may reflect the fact that these students were more likely to qualify for federal subsidies as well. The varying magnitude, significance, and even sign on the pELL coefficient is likely due to the fact that Maine has so few English language learners that it would be very difficult to draw any meaningful conclusions from the data. In the specifications including triple interaction terms testing for differential effects on small districts and districts with a large percentage of disadvantaged students, the coefficient estimating the additional difference in the impact of the laptop program on average test scores in districts with the highest percentage of students on subsidies is negative but not statistically significant, which fails to support Muir, Knezek and Christensenâ€™s (2004) hypothesis that low-income students would gain more than the average student. The coefficient estimating the effect of the laptop program on the change in scores for the smallest 25% of districts is negative and, in the fixed effects specification, statistically significant at the 1% level. For individual subjects, the various models are quite similar to the total score regressions, so I have included the most complete and best fitting versions of the model from Table 5 and 6, using enrollment-weighted data and the fixed-effects model for each subject, displayed in Table 7. As with total scores, in all subjects the laptop program has a statistically significant impact only in the unweighted model. The coefficient on Laptop âˆ— A f ter09 is still 100
negative but smaller in magnitude, which is logical given that the total score is simply a sum of these individual scores.
Results of the per-student spending regression analysis are displayed in Table 4. Laptop districts spend $700 more per student than non-laptop districts in the specification weighted by enrollment. However, the coefficient on Laptop âˆ— A f ter, which estimates the difference in per student spending between laptop and non-laptop districts after districts would have begun purchasing laptops, is not statistically significant and negative in the weighted regression. This is an unexpected result, as I would expect purchasing laptops to increase rather than decrease school spending. The other significant result from this regression concerns enrollment and spending. The coefficient on enrollment is statistically significant at the 1% level and negative, so although laptop districts tend to be larger and spend more than non-laptop districts, on the whole increasing enrollment by ten students is estimated to reduce per student spending by $79.80.
Discussion Logistic Regression
The logistic regression supports initial observations from the summary statistics that larger, higher-budget but underperforming districts are disproportionately likely to implement laptop programs. Ideally, none of the district characteristics would be significant determinants of participation in the laptop program. However, even though there are significant differences, since the gaps between laptop and non-laptop schools for all characteristics are relatively constant over time, any change in the gap in scores can be attributed to the laptop program and the estimator overcomes much of the selection bias. While there still may be unobserved heterogeneity in district characteristics for which data are not available, this evidence supports treating districts as though they were randomly selected in the main 101
Dependent Variable: After09 (Std error) Laptop_After Enrollment % English Learners Per Pupil Expenditures % Disadvantaged Intercept Weighted? Fixed Effects? N R-Squared
1.357 *** (0.323) -1.173 *** (0.412) -0.0019 (0.0031) -14.96 ** (6.904) 0.0001
(0.0001) 1.127 (2.153) 1134.7 *** (2.444) Yes Yes 521 0.911
0.991 *** (0.209) -0.343 (0.284) 0.0048 ** (0.0023) 2.889 (4.434) 0.0001 *
(0.0002) -1.502 (4.164) 1145.1 *** (3.676) No Yes 521 0.807
1.431 *** (0.464) -1.676 *** (0.531) -0.0088 * (0.0047) 12.02 (14.42) -0.0001
(0.0001) 4.039 (2.966) 1138.6 *** (4.333) Yes Yes 521 0.878
0.726 ** (0.321) -0.623 (0.4) -0.0005 (0.0045) 18.11 * (9.548) 0.0001
(0.0002) -6.612 * (3.924) 1144.3 *** (3.747) No Yes 521 0.823
0.909 ** (0.403) -1.434 *** (0.51) -0.0027 (0.0044) -12.67 (16.64) -0.0001
(0.0001) -3.229 (2.757) 1139.8 *** (3.503) Yes Yes 521 0.898
0.506 * (0.281) -0.486 (0.373) 0.00328 (0.0034) -12.05 ** (5.869) -0.0001
(0.0001) -0.379 (3.619) 1143.08 *** (3.428) No Yes 415 0.814
1.014 *** (0.344) -1.147 *** (0.445) -0.0017 (0.0053) -19.036 * (11.028) -0.0002
(0.0001) -4.348 (3.105) 1137.03 *** (4.1) Yes Yes 415 0.866
0.7223 *** (0.263) -0.189 (0.342) 0.0077 * (0.0043) -27.545 * (15.605) -0.0001
Table 7: Linear Regression of Test Scores by Subject
(0.0001) -0.768 (2.899) 1140.7 *** (2.224) No Yes 521 0.851
regression. The fact that underperforming schools are disproportionately likely to purchase laptops seems reasonable given that schools bore the majority of the cost of the laptops, so already highachieving schools would have less incentive to participate given the high cost. However, although schools that spent more per student are significantly more likely (at the 1% level) to participate in the laptop program, Table 4 show that laptop districts did not increase per pupil spending after implementing the laptop program, which suggests that laptop districts either spent less on existing programs, or that all districts increased expenditures but non-laptop districts decided to invest in other programs.
Performance — Test Scores
Contrary to my hypothesis given the evidence from existing literature, laptop programs are associated with lower test scores across all subjects and in all specifications of the model. While the negative coefficients are not always statistically significant, they are consistently significant at the 5% level for unweighted data and robust to the inclusion of control variables, a finding that holds for performance on individual subject tests as well. The results suggest that Maine’s laptop program may indeed have a negative impact on student performance on standardized tests, but that the impact is greater in smaller districts and less noticeable or nonexistent in larger districts.5 To interpret this result, I look to per-student spending, another factor that affects performance that is correlated with both the likelihood that a district purchased laptops and the district’s size. Per pupil expenditures are negatively correlated with enrollment, a relationship that is statistically significant at the 1% level. As enrollment increases, per pupil expenditures decrease, which can be explained by economies of scale if schools tend to have high 5 This explanation is supported by the linear regression analysis of total scores that tests the impact of a laptop program on the smallest 25% of schools with the triple interaction variable Small ∗ Laptop ∗ A f ter09 (Table 5). Among the smallest schools, the estimated difference in the change in average scores after implementing a laptop program is 12 points in the weighted, fixed effects specification. Not only does this represent a larger gap in the change in scores than is observed across all districts, it is statistically significant at the 1% level.
fixed costs that large schools can spread over more students. Since the gap in per pupil expenditures did not increase after laptop programs were introduced even though schools absorbed the cost of laptops, it seems reasonable to conclude that spending on laptops replaced spending on other programs. If smaller schools have less room to cut variable, per-student spending, laptops may have replaced other programs that were more beneficial to student performance, resulting in greater drops in scores at small schools with laptops. This explanation would also account for the fact that per pupil expenditures only have a significant positive effect on scores (at the 1% level) when data are weighted by enrollment, suggesting a greater impact of increased spending at larger schools, because small schools tended to have higher perstudent spending to begin with because of fixed costs.6 The relationship between enrollment, per student spending, and performance indicates that district finances are a likely source of omitted variable bias. Although I control for per-student spending, as explained above the relevant factor seems to be the degree to which spending on laptops force cuts in other areas. If the cuts have a negative effect on student performance, they would make laptops appear to me more harmful to studentsâ€™ performance than they truly are, since the coefficient for the effect of a laptop program on the change in test scores reflects not only the effect of the technology itself, but the effect of whatever cuts were made in order to purchase them. While analyzing the effect of a laptop program along with any other spending decisions that accompanied it might be valuable knowledge from a practical perspective as schools will always be forced to make choices in how they allocate funding, doing so makes it difficult to assess the effect of technology on its own merits by negatively biasing changes in scores. Contrary to findings in Muir, Knezek and Christensen (2004), laptop programs did not significantly increase or decrease the change in scores for districts with a high percentage of students on federal subsidies. Prior research found evidence 6 As
an alternative possible explanation, small schools may have less infrastructure to support laptops or fewer teachers with the necessary technical background, thus rendering laptops more of a distraction, but there is currently no evidence to support that theory.
that students’ socioeconomic status makes a difference in the effectiveness of a laptop program, with those from more disadvantaged backgrounds experiencing greater gains when laptops are introduced. In my analysis, however, there is no significant difference in the change in score for laptop districts with the highest percentage of students on subsidies. Researchers in the prior study attributed the differential impact across socioeconomic status to the fact that wealthier students are more likely to have access to computers at home even before receiving a laptop in school. However, in the years since that study technology prices have declined significantly, increasing access even for disadvantaged students, which may reduce the benefits of additional access through classroom laptop programs.
Though I expected to find that laptop programs had varying effects across subjects based on Gulek and Demirtas (2005) and Silvernail (2007), the subject-specific regressions follow the same pattern as the total score regression. Across subjects laptop districts’ scores were lower by 1 to 1.5 points, a statistically significant results only in the unweighted specification. While it seems unlikely that all subject matter would be equally conducive (or not conducive) to a curriculum integrating laptops and online resources, it is possible that the universal declines have more to with the short time frame of the study. It may be that two years is not enough time for teachers to figure out how to utilize laptops most effectively. This finding would be promising for follow-up research to see whether the direction and magnitude of laptop programs’ impact changes over time, as teachers learn how best to integrate laptops into the curriculum.
Enthusiasm for classroom technology programs has outstripped the pace of research examining the effectiveness of such programs, particularly one-to-one laptop initiatives like Maine’s. What is clear is that laptop programs are not the panacea technology advocates have argued they can be, nor are they a quick fix 105
for struggling schools. Although I do not believe that these results indicate that laptops cannot be used effectively to increase productivity in the classroom and help students learn through an innovative, technology-supported curriculum, the open-ended and decentralized approach Maine chose has not yet produced the desired results, suggesting that more evaluation of laptop programs and their implementation is needed before they can be endorsed as a tool whose benefit justifies the cost. Further econometric analyses should attempt to resolve some of the uncertainties to determine whether there is a way to design and implement one-to-one laptop programs such that they can fulfill what has been portrayed as technology’s great potential to transform the education system. A particular area of interest is whether the negative effects observed here persist when schools are not responsible for the cost of laptops and do not need to sacrifice other programs, and whether effects change as the program matures. Some limitations could be addressed by gathering additional data on the laptop program and others like it that would allow comparisons of versions of the one-to-one model — or other classroom technology models — to test which characteristics make some more effective than others. In particular, there is a need for a framework for evaluating classroom technology initiatives that goes beyond the binary technology/no technology model. It may also be worth considering broadening our understanding of academic achievement so that we can evaluate these and other programs along the criteria that best assess whether students are acquiring the skills they need to succeed. If policymakers are considering technology as a strategy for education reform, these findings suggest a need to take a step back from the rhetoric lauding high-tech classrooms and to examine technology’s effectiveness, as well as the features and program design that most effectively harnesses technology’s potential to improve the productivity and quality of education. This examination is an initial step towards understanding how technology affects student performance and the true costs and benefits of the digital classroom.
References Angrist, Joshua & Victor Lavy. 2002. “New Evidence on Classroom Computers and Pupil Learning.” The Economic Journal 112(482):735– 765. Cuban, Larry & Larry Cuban. 2003. Oversold and underused: Computers in the classroom. Cambridge, MA: Harvard University Press. Gritter, Aaron. 2005. “Belief drives action: How teaching philosophy affects technology use in the classroom.” Annual meeting of the New England Educational Research Organization, Northampton, MA. Gulek, James Cengiz & Hakan Demirtas. 2005. “Learning with technology: The impact of laptop use on student achievement.” Journal of Technology, Learning, and Assessment 3(2):1–39. Lage, Maureen J, Glenn J Platt & Michael Treglia. 2000. “Inverting the classroom: A gateway to creating an inclusive learning environment.” The Journal of Economic Education 31(1):30–43. Muir, Matthew, G. Knezek & R. Christensen. 2004. “The Power of One-to-One: Early Findings from the Maine Learning Technology Initiative.” Learning and Leading with Technology 32(3):6–11. Penuel, William R. 2006. “Implementation and effects of one-to-one computing initiatives: A research synthesis.” Journal of Research on Technology in Education 38(3):329. Silvernail, David L & Aaron K Gritter. 2007. Maine’s middle school laptop program: Creating better writers. University of Southern Maine. Gorham, ME: Maine Education Policy Research Institute. Silvernail, David L, Dorothy Small, Leanne Walker, Richard L Wilson & SW Wintle. 2008. “Using technology in helping students achieve 21st century skills: A pilot study.” Center for Education Policy, Applied Research, and Evaluation. Wilensky, Uri & W Stroup. 2000. “Networked gridlock: Students enacting complex dynamic phenomena with the HubNet architecture.” Fourth international conference of the learning Sciences. Windschitl, Mark & Kurt Sahl. 2002. “Tracing teachers’ use of technology in a laptop computer school: The interplay of teacher beliefs, social dynamics, and institutional culture.” American Educational Research Journal 39(1):165–205.
Zurita, Gustavo & Miguel Nussbaum. 2004. “Computer supported collaborative learning using wirelessly interconnected handheld computers.” Computers & Education 42(3):289–314.
Exploring the Essentiality of the Essential Air Service (EAS) Federally Subsidized Flights and Their Effects on Rural Property Values and Per Capita Income Marc Beck, Yale University1 Abstract. This paper explores the economic impact of the Essential Air Service (EAS) program, which was established after airline deregulation in 1978 in order to guarantee the continuation of commercial air service to isolated communities in the United States through federal subsidies. I use a difference-in-difference estimator to investigate the programâ€™s effects using median housing value and per capita income as economic indicators, taking advantage of two policy changes: the implementation of the program in 1979 and the elimination of subsidies in the 1990s due to budget cuts and new eligibility requirements. I find that changes in housing value due to a gain or loss of EAS subsidies depended on the attractiveness of alternative airports. Per capita income was not affected by the presence of EAS flights and only depended on the attractiveness of alternative airports, suggesting that the subsidies are not important to a communityâ€™s economic vitality. Keywords: airline, federal subsidies, housing value, income
Beck graduated from Yale in 2012 with a BA in economics. This senior essay won the Ronald Meltzer and Cornelia Awdziewicz Prize. The author would like to thank his adviser, Professor Dan Keniston, for his endless guidance and support throughout the process of putting this project together. He is also deeply appreciative of the many hours Librarian for Government Information Julie Linden and Data Librarian Michelle Hudson dedicated to helping him locate data and government records related to the Essential Air Service Program.
History of the Essential Air Service
The Essential Air Service program (EAS) was implemented after the U.S. airline industry was deregulated in 1978 and provides federal subsidies for airlines to offer service to rural communities across the United States — communities that would otherwise be unprofitable for airlines and would remain without service.2 The history of the program dates back to the era of airline regulation in the U.S. Under this regulatory regime, airlines were required to submit an application to and gain approval from the Civil Aeronautics Board (CAB), which oversaw airline regulation, before entering or exiting a market. The application process was often lengthy and the CAB would both force airlines to serve smaller markets, as well as limit the number of airlines serving each route. One notable example is Delta’s arduous journey in obtaining the rights to fly from Atlanta to New York, a route on which Eastern Airlines enjoyed a monopoly throughout the 1940s and for the first half of the 1950s. The CAB denied Delta Air Lines’ application to fly the route in 1948 and only granted the rights to the Atlanta-based airline in 1955 after it had reapplied in 1954 (Lewis & Newton 1979). Moreover, route approvals were often contingent on the airline serving smaller communities along the way: Delta’s route from Atlanta to Cincinnati was forced to make stops in Chattanooga and Knoxville, Tennessee, as well as Lexington, Kentucky. The airline desired more routes to major cities in order to make up for the “heavy expenses of serving so many smaller communities on relatively unprofitable short hops” (Lewis & Newton 1979). Thus, it was not surprising that when the government was on track to deregulate the U.S. airline industry, allowing airlines to freely enter and exit markets without intermediate stop requirements, smaller communities were afraid that airlines would drop service to their airports completely in favor of more profitable routes such as New York to Chicago, potentially crippling their economic development. Because of those concerns, the government added 2 Office
of Aviation Analysis. “What is Essential Air Service?” U.S. Department of Transportation, 11 Apr. 2009, http://ostpxweb.dot.gov/ aviation/rural/easwhat.pdf
section 419 to the Federal Aviation Act of 1958 in order to ensure that air service was maintained to smaller communities, establishing what is now known as the Essential Air Service program.3 Section 419 mandated that the federal government establish minimum service levels in terms of number of roundtrips and seats at eligible rural airports around the nation. Eligibility for section 419 was based on prior service criteria: • Airports that were on airline certificates4 prior to airline deregulation and had no service or service from just one airline on the date of the act’s passing were eligible for consideration. • Any airports that had two or more airlines prior to deregulation and subsequently found themselves with no service after deregulation were also eligible, as well as communities that previously appeared on an airline’s certificate but were deleted within the ten year period prior to the passing of deregulation. • If air service drops below the established minimum service levels determined, the federal government provides subsidies to ensure that those service levels are maintained. When a carrier receiving subsidies wants to leave a market, it must first notify the government 90 days before its desired date of exit, during which time the government would attempt to find a replacement carrier. Should the government not find a replacement carrier within 90 days, the government would continue to provide subsidies to the exiting carrier, as well as funds to cover the airline’s losses from continuing service beyond the desired date of exit. Almost a decade later, the government restricted eligible points to those that were 45 miles or more from the nearest large or medium hub airport with the passing of the Airway 3 Office
of Aviation Analysis, “What is Essential Air Service?” (2009) CAB issued certificates to airlines prior to deregulation in order to regulate safety and designate which routes an airline was allowed to fly. 4 The
Safety and Capacity Expansion Act of 1989.5 In 1990, insufficient funding for the increased minimums mandated by the Airway Safety and Capacity Expansion Act of 1989 forced the Department of Transportation (DOT) to eliminate service to 26 communities that were less than 70 miles from the nearest large or medium airport, less than 55 miles from the nearest small hub airport, or less than 45 miles from the nearest non-hub airport that boarded more than 100 passengers daily, though state capitals and various other cities, perhaps due to political reasons, were exempted from the act.6 In 1993, Public Law 103-122 codified the requirement that eligible points be at least 70 miles from the nearest large or medium hub airport and an additional 11 communities had their subsidies eliminated.7 Congress reduced appropriations to the Essential Air Service program by $10.8 million in 1996, forcing the Department of Transportation to reduce subsidies across all communities rather than cut off subsidy support completely. Because of the uniform reduction, minimum service levels no longer included weekend service, more than two round trips on weekdays, or service to more than one hub. In 1998, Congress removed the 1998 termination date of the Essential Air Service subsidies, making the program permanent.8 Supporters of the EAS program argue that the presence of air service in a community is essential for its economic development. Nevada Senator and Senate Majority Leader Harry Reid, speaking about the EAS subsidies for Ely, Nevada said in February 2011: “Airports themselves create jobs...people don’t make location decisions about industry based on going someplace in a bicycle 5 The
FAA defines a large hub airport as one that handles one percent or more of the nation’s total air traffic, a medium hub airport as one that handles at least 0.25 percent but less than one percent, a small hub airport as one that handles at least 0.05 percent but less than 0.25 percent, and non-hub airports as those that handle at least 10,000 passengers but have a share less than 0.05 percent of the nation’s total air traffic. 6 Office of Aviation Analysis, “What is Essential Air Service?” (2009). Also see Annual Report of the Regional Airline Industry (1989). 7 Office of Aviation Analysis, “What is Essential Air Service?” (2009). 8 Ibid. Also see Appendix for a timeline of the Essential Air Service program. The Appendix is available at the Journal’s website: http://econjournal.sites. yale.edu/
or a car.”9 In a congressional hearing discussing the effect of airline deregulation on the rural economy in 1987, Dean Schofield, director at the office of planning of the South Dakota Department of Transportation, said that air service to Brookings, South Dakota, subsidized by the EAS program, was a major consideration for 3M in deciding to set up a medical products division in the town, generating 650 jobs and $14 million in annual payroll.10 But the EAS program has not been without controversy. Critics of the program maintain that the subsidies are a waste of taxpayers’ money because many of the EAS flights are underutilized. Until 2010, Macon Airport in Georgia received subsidies for flights to Atlanta, 75 miles away. The route averaged less than one passenger per flight. Many of them were departing empty, causing Oklahoma senator Tom Coburn to call the EAS program “the most wasteful government spending.”11 Ely airport, one of the most isolated of the EAS airports in the contiguous United States — 183 miles from the nearest hub airport, Salt Lake City — had an even lower average load per flight at 0.78 passengers and received $1.8 million in subsidies in 2010 for flights to Denver. Johnstown Airport in Pennsylvania, located 75 miles from Pittsburgh, received $1.4 million in subsidies for flights to Washington’s Dulles International Airport in 2010 and averaged 7.5 passengers per flight on a 34-seat Saab 340.12
Grubesic and Matisziw (2011) study the potential market leakage away from EAS airports to alternative airports, which may be causing the dismal load factors on many EAS flights. They 9 Demerjian,
Karoun. “Senate bill would prop up rural air service in Nevada.” Las Vegas Sun. 1 Feb. 2011. 10 United States, Committee on Small Business, Hearing, the Effect of Airline Deregulation on the Rural Economy (Washington: GPO, 1987) 19. 11 Kelly Yamanouchi, “Regional flights could lose subsidies.” The Atlanta Journal Constitution, 8 Mar. 2011 12 Office of Aviation Analysis. “U.S. Subsidized EAS Report” U.S. Department of Transportation, 1 May 2010, http://ostpxweb.dot.gov/aviation/x-50% 20role_files/100501nonalaska.xls. Also see Bureau of Transportation Statistics. (2011) Passengers – All Carriers, All Airports. Retrieved 11/16/2011 from http://www.transtats.bts.gov/Data_Elements.aspx?Data=1
show that it may be useful for the government to consider small hub and non-EAS commercial airports rather than just medium and large hub airports when determining EAS eligibility. While just 64 percent of the U.S. population lives within 70 miles of a medium or large hub airport, under the EAS minimum standard, 96 percent live within the same distance when all small hub and non-EAS commercial airports are included. Only 0.007 percent of the population does not live within 180 miles of any commercial airport, excluding airports receiving subsidies under the EAS program. Thus, while EAS airports may provide some benefits for the communities they serve, those benefits may be undermined as travelers from those communities drive to nearby non-EAS airports that offer more convenient schedules and service to a greater variety of destinations. Widely-accepted theories of air transport demand support this hypothesis. Douglas and Miller (1974) argue that passengers do not simply want to minimize total travel time, but also the time between their preferred departure and arrival times and their actual scheduled times, as well as monetary costs — those associated with traveling to and from the airport and the airfare. In this framework EAS airports are less desirable to customers because they have fewer direct flights to popular destinations. For example, a passenger living in an EAS community might arrive at her destination at 12 p.m. if she chose to fly out of the EAS airport. If the nearest hub airport offers a flight that will arrive at the passenger’s destination at 10:30 a.m., the value of the 1.5 hour difference between arrival times may outweigh the monetary and time costs of driving farther to the hub airport. Douglas and Miller (1974) call the average of the difference between preferred departure or arrival time and actual scheduled departure or arrival time the “convenience of schedule” in a market. A hub airport will likely be able to support greater route frequencies than an EAS airport because of its larger catchment population, and thus have higher schedule convenience. William Fruhan (1972) and other economists have shown that airlines that have high frequencies, and thus high capacity in a market, tend to carry a disproportionately greater share of the traffic due to a greater chance of minimizing a passenger’s measure of schedule inconvenience, creating an S114
curve relationship between capacity share and market share. Many of those passengers come to expect that the airline with the highest frequency will minimize the difference between the preferred and scheduled departure and arrival times and will tend to only consider that airline when making future bookings (Fruhan 1972). Because EAS communities support low frequencies, passengers may find that schedules at their local EAS airport are consistently inconvenient and stop considering it an option altogether, opting for an alternative airport instead. Additionally, the value of time saved driving from using the EAS airport could be diminished because service is limited to one or two hubs, limiting the number of destinations one can reach requiring only one connection. For example, a passenger today flying from Ely, Nevada to Hartford, Connecticut would be forced to make two connections to reach his or her destination as there is currently no nonstop service between Denver, Colorado (the designated hub for Ely’s EAS service) and Hartford on an airline with interline agreements.13 Moreover, even if Denver had nonstop service to Hartford on such an airline, it is possible that the low frequency of EAS service would make a connection to the Hartford flight impossible or would require a substantial layover. Because non-EAS airports are more likely than EAS airports to have service to multiple hubs, the number of destinations reachable within one connection is higher, making them more attractive. The type of aircraft used on EAS routes could also be a driver of market leakage. The routes are largely operated by Beech 1900 Turboprops, which seat 19 passengers and may drive customers away from EAS airports towards hubs that operate jet service, commonly perceived to be more comfortable and safer, even though this may not be the case in reality (Clark 2007).14 Moreover, aircraft with 19 or fewer passengers are not required to have a flight attendant on board, and thus the perceived quality of service is likely to be lower on these flights. If passengers’ 13 Southwest
Airlines operates nonstop service from Denver to Hartford, but does not currently have any interline agreements with other airlines, severely diminishing the attractiveness of connections. Without interline agreements, passengers must retrieve their checked baggage, recheck them for their next flight, retrieve their ticket for their next leg and re-clear security. 14 Sparks, Evan. “Unfree as a Bird,” The American, 3 Jan. 2007. http://www. american.com/archive/2007/january/unfree-as-a-bird/.
perceptions of an airline’s fleet and service are low, the route will suffer as high-yielding business traffic is driven to alternate airports (Holloway 2008). Therefore, the time convenience of the local EAS airport or fare decrease must be sufficient to outweigh this “cost” of having to endure lower service standards. Furthermore, before deregulation, U.S. airlines’ domestic networks were linear in nature and largely did not concentrate traffic at a few hubs as we see today. Airlines have increasingly embraced the hub-and-spoke system after deregulation was passed in the United States and many medium and small hubs, as well as non-EAS commercial airports, can support multiple daily frequencies to the large hubs because of the sheer number of connecting opportunities which facilitate increased density on spoke to hub routes (Holloway 2008). Because of the concentration of traffic at the hub, airlines can use larger aircraft, which generally have lower costs per seat mile than smaller counterparts, thus maximizing profit. With deregulation, airlines have been able to organize their networks freely into this structure, rather than having to wait years for government approval, as was the case during regulation (Morrison & Winston 1986). Airlines’ vastly increased usage of regional jets (aircraft with more than 19 seats but less than 100) in the U.S. domestic market has amplified the benefits that hub and spoke networks have had for non-large hub airports. After the introduction of the Bombardier Canadair Regional Jet (CRJ) in 1992, the number of regional jets in the country has seen a rapid increase. The Canadian-built plane, and other regional jets that are popular in the U.S. domestic market, are less risky to deploy than larger jets, despite their higher unit costs as a smaller airplanes, because fewer passengers are needed to reach a profitable load factor. This decreased risk has allowed airlines the ability to increase frequencies at small hub airports and begin service at many more. In fact, in 2001, the General Accounting Office has found that 41 percent of all regional jet route deployments have started new routes.15 Additionally, Scott and Savage (2004) have found that only three percent of regional jet deployments can be classified as hub by-pass routes and nearly all route deployments have been to 15 U.S. General Accounting Office, “Regional Jet Service yet to Reach Many Communities,” GAO-01-344. Washington DC: General Accounting Office, 2001.
or from large hub airports. In Figure 1, we can see the effect that regional jets have had on small hub airports. The average number of seats per flight at those airports has decreased 37 percent between 1990 and 2009 from 94 seats to 59 seats, compared to 18 and 25 percent at medium and large hub airports, respectively. The larger drop in seats per flight at large hub airports in comparison to medium hub airports adds support to the claim that regional jets were largely deployed between small and large hub airports. Figure 1: Average Seats per Flight by Hub Status, 1990-2009 $&"#
Data from the Bureau of Transportation Statistics
In Figure 2, we can see that the number of small hub airports in the U.S. has increased from 87 to 111, a 27.5 percent increase, which follows from the GAO study that found that regional jets have allowed airlines the opportunity to enter into new markets. Medium hub airports saw an increase of 13.6 percent over the same 19 year period, while large hub airports saw a 12.5 percent decrease, from 32 to 28 airports. The large hub 117
airports that saw a downgrade to medium hub airports were Portland, Pittsburgh, Raleigh-Durham, and San Diego. Delta, US Airways, and American pulled their hubs at Portland, Pittsburgh, and Raleigh-Durham, respectively, as they consolidated flights into a small number of hubs over the 19-year period. San Diego International Airport, meanwhile, fell just under the cutoff in 2009 for large hub airports with 0.97 percent of the national total departures. Figure 2: Number of Airports by Hub Status, 1990-2009
&))'# %&# %)# &!#
Data from the Bureau of Transportation Statistics
Figure 3 shows that the number of departures has increased across all classifications from 1990 to 2009. Even large hub airports saw a 32 percent increase in number of departures despite its numbers falling from 32 to 28 as seen in Figure 2, suggesting that airlines consolidated some of those flights into a smaller number of hubs during the 1990s. The increased densities at the remaining large hubs, along with the increased usage of regional jets as discussed above, all have helped airlines sustain higher 118
frequencies to more small hub airports. In fact, even though the number of small airports increased from 87 to 111, as seen in Figure 3, the average number of daily flights at small hub airports increased from approximately 19 in 1990 to 28 in 2009. The increased frequencies at these â€œspokesâ€? may have further increased the attractiveness of using alternatives to EAS airports, and thus lowered the perceived value of EAS flights.
Figure 3: Number of Departures by Hub Status, 1990-2009
+"!&% +"$'% '"
$"$&% !"('% !"#$%
Data from the Bureau of Transportation Statistics
Lastly, EAS airports, which offer subsidies to just one airline, might suffer from lack of competition. While a passenger travelling from an EAS community to a point beyond the designated hub could choose among multiple competing airlines for connections to his or her destination at the hub, the overall itinerary price could be relatively high because of the monopoly on the EAS airport to hub airport route. Therefore, the value of time saved from using the local EAS airport over driving to a hub airport must be sufficiently high to outweigh the fare premium. In 119
the case of the hub airport, an airline flying nonstop to a certain destination not only faces competition from other airlines flying that route nonstop, but also airlines that flow traffic between the hub airport and that destination over one or more of their hubs, leading to relatively lower fares. An interesting question related to pricing in EAS markets is why airlines do not lower fares in order to increase demand for its EAS flights considering that the marginal cost of the extra passenger is low. This is a valid question if the airline is looking to maximize profits on a singular route; however, airlines make pricing decisions in order to maximize profits of the network as a whole. Since most EAS passengers are likely going to destinations beyond the hub, the opportunity costs of the EAS passenger taking a seat on the second beyond hub flight must also be taken into account. For the reasons mentioned above, EAS passengers are likely low yielding and would need a low enough fare to outweigh the inconveniences of an EAS routeâ€™s poor schedule and service. An EAS passenger may displace another passenger coming from a business center such as Los Angeles on the second beyond hub flight, and thus the cost of carrying the EAS passenger is the marginal cost plus the difference in fare between her and the higher yielding passenger. Rasker, Gude, Gude and van den Noort (2009) study the economic importance of air travel in the rural west, and find that longer travel times to large airports are associated with a lower per capita income and a lower amount of diversification of industries. The study, however, does not find causal evidence linking access to air travel to increased economic vitality as it could be the case that large airports are built in areas that already had high economic activity. This paper builds on the Rasker and Grubesic and Matisziw studies by exploring the actual economic effects of the Essential Air Service on the communities it serves, using property values and per capita income as economic indicators, seeking to find a causal link between air service and those indicators. Changes in property values over time should approximate the value a community places on the convenience of having local air service, while changes in per capita income should give some insight as to whether subsidized flights have increased the welfare of a given county. I explore the effect of subsidized 120
air service on housing value and per capita income using a difference-in-difference estimator, taking advantage of two public policy changes mentioned above: the implementation of EAS in 1978 which mandated service to cities that appeared on airline certificates but had suspended service, and the elimination of subsidies in 1990s to 38 communities based on distance minimums. Following from the theory laid out above, we should expect that the effect of EAS flights on housing value and per capita income has decreased over time as airlines add more frequencies and convenient connections at alternative airports with the adoption of hub and spoke networks and lower fares as a result of more competition among U.S. airlines.
Methodology Difference-in-difference Estimator
The original guidelines of the EAS program stated that all airports on an air carrier certificate but that are served by none or one airline would receive an Essential Air Service determination within one year of the passing of the Airline Deregulation Act. Therefore, all communities that had no service prior to airline deregulation likely received subsidies for air service once the act was passed, while airports with one carrier received subsidies depending on whether the airlines serving them exited in favor of the trunk routes. If airports that had one airline prior to deregulation required subsidies to maintain minimum service throughout the following decade, it could be the case that those routes were unprofitable during regulation and had similar characteristics to airports with no service. Thus, in order to investigate the economic effects of the implementation of the EAS program, we can use a difference-in-difference estimator where airports that had no service prior to airline deregulation can be used as the treatment group, while those that had one airline prior to airline deregulation and retained that service after its passing, and maintained its subsidy eligibility, can be used as the control group, with housing value and per capita income as the dependent variables. Investigating the effect of the 1990 subsidy cuts will provide 121
a more up-to-date picture of EAS effects on the economies of small communities with the changes in airline network decisions discussed in the previous section. The control group in this case would be those communities that retained their subsidies in the 1990s, while the treatment would be those which lost them. Let hsgns1980 and hsgs1980 represent housing values in 1980 for airports that had no service prior to the introduction of the EAS program and airports that did have service prior to EAS, respectively, and let hsgns1980 and hsgs1980 represent housing values in 1990 for the aforementioned groups. Similarly, let hsgls1990 and hsgs1990 represent housing values in 1990 for counties that lost service between 1990 and 2000 and counties that retained service, respectively, and let hsgls1990 and hsgs1990 represent housing values in 2000 for the same groups. The difference-in-difference estimator for both scenarios is then: � � δ = (hsgns1980 − hsgs1980) − hsgns1980 − hsgs1980
� � ∆ = (hsgls1990 − hsgs1990) − hsgls1990 − hsgs1990
where δ and ∆ are the difference-in-difference estimators and can be derived from the following equation: loghsgi,t = α + βyear + γcounty + δgainEASi,t
+∆lostEASi,t + θ popi,t + λt_atti,t +φt_atti,t ∗ gainEASi + θt_atti,t ∗ lostEASi + µi + ε i,t
The dependent variable loghsg is the log of the median housing value in each county i and year t: 1980, 1990, 2000, and 2009. The independent variables are year, a vector of indicator variables for the years 1990, 2000, and 2009; county, a vector of indicator variables for all counties in the sample; gainEAS, a dummy variable equal to one if an airport did not have service prior to implementation of the EAS program for the years 1990, 2000, and 2009 and 0 otherwise; lostEAS, a dummy variable equal to one if an airport lost service after 1990 for the years 2000 and 122
2009 and 0 otherwise; pop, the population in tens of thousands in each county and year; µ, a vector for all characteristics of each county that are time invariant and can be controlled through county fixed effects; and t_att, the sum of the attractiveness of the nearest small hub airport, nearest medium hub airport, and nearest large hub airport for each airport and year, where attractiveness of alternatives is defined by the following equation: √ DEP ∗ 100 (4) ATT = DIST 2 DEP is the number of departures at the nearby airport and DIST is the distance of that airport from the EAS airport in question. This equation is a slight variation of the attractiveness variable Kaemmerle (1991) uses in a model of demand for small community air service. Kaemmerle uses DIST 2 because as distance increases an increasingly greater number of flights are needed in order for that airport to hold the same √ attractiveness level. However, this paper differs in that I use DEP instead of DEP because for a given distance, potential passengers should value each additional departure less than the previous one. As an example, someone living 50 miles away from Atlanta’s HartsfieldJackson International Airport, the world’s busiest airport, should not value it much more than living 50 miles from Chicago’s O’Hare International Airport, the second busiest airport, even though Atlanta had a 107,836 departure advantage in 2009. The resulting value is multiplied by 100 so that the coefficient is easier to interpret. One limitation of the t_att variable is that some airports may have more than one viable alternative in each hub classification. I use the interactions t_att ∗ gainEAS and t_att ∗ lostEAS in order to investigate the impact of attractiveness on effects of gainEAS and lostEAS on housing values. The coefficients of interest are δ, ∆, λ, φ and θ, where δ is the fractional change in median housing value associated with gaining subsidized flights after the initial deregulation; ∆ is the fractional change in median housing value associated with losing subsidized flights in the 1990s; λ is the fractional change in median housing value associated with a one point increase in total attractiveness of alternative airports; φ is the change in impact of gainEAS on median housing value associated with a one point 123
increase in total attractiveness of alternative airports; and φ is the change in impact of lostEAS on median housing value associated with a one point increase in total attractiveness of alternative airports. I use the same equation to investigate the EAS program’s effect on per capita income: logpcinci,t = α + βyear + γcounty
+δgainEASi,t + ∆lostEASi,t + θ popi,t + λt_atti,t +φt_atti,t ∗ gainEASi + φt_atti,t ∗ lostEASi + µi + ε i,t
which has similar interpretations.
The dataset for this paper was created from three different sources: median housing value, per capita income and population by county from the U.S. Census Bureau, departures by airport from the U.S. Bureau of Transportation Statistics, and latitude and longitude coordinates for all public-use airports in the United States from the National Transportation Atlas Database. Information on airports receiving subsidies in different years was gathered from the Annual Report of the Regional Airline Industry as well as the Department of Transportation’s Essential Air Service web page and was manually entered as a dummy variable into the dataset. There were 120 airports that received subsidized flights under EAS in the 1980s. However, only those airports that saw subsidized service throughout the 1980s were considered in this paper, shrinking the number of airports in the data set to 90. As discussed in Section 1, some small communities lost service simply because airlines were shifting their fleets to trunk routes in order to maximize profitability, but saw service return once fleets caught up with airline’s post deregulation network decisions. Such airports would not be comparable against those airports which remained unprofitable (and thus kept subsidies) throughout the decade. Of the 90 airports remaining, Massena and Ogdensburg, New York were omitted as they are both located 124
in the same county: St. Lawrence. Since the data in this paper is at the county level, St. Lawrence County would not be comparable to the other counties as it would have double the frequencies of subsidized flights stipulated by the EAS guidelines. Blythe, California was also omitted as it is located in the same county as Ontario International Airport, a small hub. Distances from each EAS airport to the nearest small, medium, and large hub airports were calculated by first finding the nearest airport by straight line distance using ArcGIS, and then using Stata to calculate the road distance between it and the EAS airport in conjunction with Google Maps.
Results of the effect of flights subsidized under the Essential Air Service program on housing values are reported in Table 2. The first column shows the coefficients for the basic model, which does not include controls for attractiveness of alternative airports. The coefficient on gainEAS (0.092) is positive, as expected, and is significant at the five percent level. The coefficient on lostEAS (0.056) is significant at the 10 percent level, but is also positive. We would expect that a loss of air service to a county would have a negative effect on housing value, which suggests that the coefficient is positively biased. I add a control for attractiveness of alternatives, t_att, in the second column. Its coefficient is small (.008) and insignificant, suggesting that it does not have much effect on housing values. With the control, the effect of a loss of EAS subsidies has fallen slightly (.051) and remains positive but is now statistically insignificant. However, when we look at the third column, total attractiveness is negative when interacted with gainEAS (-0.023) and positive when interacted with lostEAS (0.02). These are significant to the ten and one percent levels, respectively. The coefficient on lostEAS is now negative (-0.067) though not significant, but because of its relatively large magnitude, it should not be discounted. The coefficient on gainEAS is now much larger with the added controls (0.189) and is significant at the five percent level. The effect of t_att for airports that already had 125
Table 1: Means and Standard Deviations of Selected Variables for All Counties, 1980-2009 County Variable
median housing value
-941 6398 -76 53887 -8394 –
-1833 11043 -147 62429 -13860 7780
-2574 17033 -224 72809 -18201 8716
-5621 21751 -299 85265 -25536 10771
departures at nearest medium hub
departures at nearest large hub
distance from nearest small hub
distance from nearest medium hub
distance from nearest large hub
attractiveness of nearest small hub
attractiveness of nearest medium hub
attractiveness of nearest large hub
total attractiveness of alternative airports
per capita income population departures at nearest small hub
Distance in miles n=87
Table 2: Regression Coefficients on Housing Value Dependent Variable: log(hsgvalue) Independent Variables
0.092** (0.044) 0.056* (0.032) 0.039*** (0.009) –
t_att * gainEAS
.089** (0.045) 0.051 (0.032) 0.039*** (0.009) 0.008 (0.015) –
t_att * lostEAS
year dummies county dummies
0.189** (0.075) -0.067 (0.057) 0.042*** (0.008) 0.009 (0.015) 0.023* (0.007) 0.02*** (0.053) Yes Yes
Column 1: Basic Model Column 2: Model with Attractiveness of Alternatives Column 3: Model with Attractiveness and EAS Interactions Significance at the one percent level denoted by ***; significance at the five percent level denoted by **; significance at the 10 percent level denoted by *
service prior to deregulation and did not lose their EAS subsidies remains small and insignificant (0.009). The directions of the coefficients on the total attractiveness interaction variables are as expected and agree with the theory of air transport demand laid out in Section 3.1. We should expect that an increased number of departures at alternative airports would increase their convenience, thus increasing housing value as people tend to prefer to live in areas with ease of access to the air transport network. Increased frequencies at nearby airports and the available choices of scheduled departure and arrival times will minimize the difference between preferred and scheduled departure or arrival times. As follows, t_att ∗ gainEAS should be negative as we would expect that as the attractiveness of alternatives increases, a community will rely decreasingly on the subsidized service, and the increase associated with the gain of subsidized flights to housing value should not be as large. Likewise, t_att ∗ lostEAS should be positive. A community that has convenient alternative airports nearby should not see as large of an impact should EAS flights be discontinued, while a community with few feasible alternative airports that relies heavily on its subsidized service should see a bigger impact. Additionally, from Table 1, we can see that total attractiveness has increased by .545 from 1990 to 2009 on average, which suggests that the impact of a gain or loss of EAS is diminishing over time. Small hub airports accounted for 0.237 of that increase, or 43.5 percent. According to the regression, the average county in 1980 would have seen an 11.1 percent increase in housing value with a gain in subsidized flights under EAS, while the average county in 1990 would have seen essentially no loss in housing value with the loss of service. The difference in the baseline effects — that is, the effects when total attractiveness of alternatives is zero — can be reconciled by the fact that in 1996, Congress cut the number of weekly flights that the EAS program would support, decreasing the attractiveness of EAS routes. Additionally, companies may have been attracted to an EAS county initially because of the subsidized flights, as 3M did in Brookings, South Dakota, which provides the county with higher paying jobs, but when those communities subsequently lost service, the costs of moving out of 128
the community may have been too high to outweigh the benefit of relocating to a location with easier access to the U.S. air transport system. Thus, the effect on housing value of losing subsidized flights should not be as large in magnitude as the gain. Moreover, since counties that lost service no longer had money tied up in keeping their airport operational for commercial service, they could now redirect those funds to other programs that may have increased the quality of life for its residents, softening the impact of the loss of subsidized flights. The larger magnitude of the coefficient on t_att âˆ— gainEAS over that on t_att âˆ— lostEAS is contrary to what we would have expected. With the changing dynamics of the airline industry since deregulation, namely the tendency for airlines increasingly to utilize the hub and spoke network in the U.S. air transport market and the increasing popularity of regional jets, the value of one point of attractiveness of alternative airports should be higher today than in prior years. Those two factors have been the driving force behind increased frequencies at small and medium hub airports and have increased the attractiveness of alternative airports in two ways. First, the increased amount of connecting opportunities as airlines consolidate their operations into a few large hubs can increase the amount of passengers per flight over those that rely solely on origin and destination (OandD) traffic when in a pure point-topoint network. This has given airlines the ability to support more frequencies to smaller markets and allow more passengers to reach their destination in one connection or less. Second, the hub and spoke network has increased competition between airlines. A passenger who needs to get from spoke A to spoke D can choose between airline X from A to hub B to D, and airline Y from A to hub C to D. The increased competition over itineraries, rather than routes, because of the hub and spoke system, has lowered air fares dramatically since deregulation. These two effects have likely changed the value of a point in attractiveness, as defined in this paper in section 2.1, over time. The value of one extra departure would not be as high as it is today if the fares on that departure were higher and if that flight did not connect into a large bank of flights that allowed the passenger to get to her destination in one stop. We may have seen a much smaller coefficient had county 129
level data been available for years between 1980 and 1990 and if departure data on the airport level had been recorded prior to 1990. The comparison between 1990 and 1980 had to be made because of the limitations of our data, but the move towards hub and spoke networks had been well underway by 1990. Table 3 shows the results of the analysis of the effects of EAS flights on per capita income. In all three regressions, EAS has no statistically significant effect on per capita income, even after controlling for attractiveness of alternatives. The coefficient on t_att in the second regression (0.008) is statistically significant at the five percent level. Attractiveness of alternatives has no impact on the effect of EAS on per capita income, as seen in the third regression. In the second regression, because the coefficients on gainEAS and lostEAS are statistically insignificant while that on t_att is statistically significant, this suggests that the economic well being of a community depends primarily on alternative airports rather than on EAS service. While some leaders have said that EAS service was a key factor in luring businesses to their communities, it seems that the low frequency of EAS routes and low service quality have, in general, not been successful in attracting much business traffic.
Table 3: Regression Coefficients on Per Capita Income Dependent Variable: log(pcinc) Independent Variables
0.036 (0.026) 0.026 (0.017) -0.006*** (0.002) –
t_att * gainEAS
0.033 (0.026) 0.021 (0.017) -0.006*** (0.002) 0.008** (0.004) –
t_att * lostEAS
year dummies county dummies
0.033 (0.035) -0.038 (0.027) -0.007*** (0.002) 0.011 (0.008) 0 (0.008) 0.003 (0.003) Yes Yes
Column 1: Basic Model Column 2: Model with Attractiveness of Alternatives Column 3: Model with Attractiveness and EAS Interactions Significance at the one percent level denoted by ***; significance at the five percent level denoted by **; significance at the 10 percent level denoted by *
In this paper, I argue that the value of subsidized flights to rural communities in the United States through the Essential Air Service has diminished since the programâ€™s inception. Hub and spoke networks, which have become the ideal network type for U.S. airlines since deregulation, have increased competition, lowered fares, and decreased the inconvenience of flying by reducing the number of stops needed to reach oneâ€™s destination. They, in conjunction with the regional jet, have also increased the number of frequencies that non-EAS airports are able to support, increasing schedule convenience for their passengers and making them more attractive alternatives to those in EAS communities. The evidence I present in Section 4 of this paper has shown that, indeed, the value of federally subsidized flights depends greatly on the attractiveness of alternative airports, a function of departures and distance. However, the government currently does not take into account the absolute number of departures at alternative airports when considering whether a community should be cut from EAS subsidies. It only stipulates that a community be located 70 miles or more from a large or medium hub airport, where distinctions about the size of the hub are based on the relative number of departures to the national total. While this rule may have made sense in the late 1980s, when it was implemented, it now discounts the growing importance and convenience of small hub airports throughout the country. A better approach would be to develop an attractiveness scale, as this paper has, and weight departures at given alternative airports according to their distance from a given community, rather than setting a fixed absolute distance and restricting alternative airports to just medium and large hubs. And even if an attractiveness scale is developed, the changing dynamics of the airline industry needs to be monitored in order to assess how the value of attractiveness of alternatives changes over time. This paper also shows that the opportunity costs of federally subsidized flights can be quite large. Counties that lost EAS subsidies in the 1990s saw an increase in housing value (5.6 percent) after losing federally subsidized service, suggesting that counties took funds previously used for airport upkeep and spent 132
them on other programs that were of greater economic benefit than commercial air service directly to said communities. In fact, the average community would have seen an increase in housing value if its subsidy allotment under EAS were cut. Still, politicians continue to rally to keep alive the EAS program, which cost the government $158,124,582 in 2010.16 Congressman Brian Higgins of New York recently wrote a letter to a Congressional Committee overseeing the reauthorization of the Federal Aviation Administration (FAA) to petition to keep EAS service in Jamestown, New York despite the fact that Jamestown Airport is located just 75 miles from Buffalo/Niagara Falls International Airport — an airport with 106 daily departures (as of 2009). He states that the “Chautauqua County community relies on the service provided...at Jamestown Airport for life quality and economic development purposes.”17 Perhaps politicians like Higgins continue to fight for service as a matter of pride for the communities they serve, because the evidence presented in this paper suggests that the economic value of the EAS program is minimal.
References Clark, Paul. 2007. Buying the big jets: Fleet planning for airlines. Burlington, VT: Ashgate Publishing Company. Douglas, George Warren & James Clifford Miller. 1974. Economic regulation of domestic air transport: Theory and policy, Vol. 10. Washington, DC: Brookings Institution. Fruhan, William E. 1972. The fight for competitive advantage: A study of the United States domestic trunk air carriers. Cambridge, MA: Harvard University. Grubesic, Tony H & Timothy C Matisziw. 2011. “A spatial analysis of air transport access and the essential air service program in the United States.” Journal of Transport Geography 19(1):93–105. 16 Office
of Aviation Analysis, “Subsidized Essential Air Service Outside of Alaska,” U.S. Department of Transportation, January 1 2010. 17 Higgins, Brian, “Congressman Higgins Fights to Keep Jamestown Airport Eligible For Federal Program,” Official Website of Congressman Brian Higgins (NY-27), January 27, 2012.
Holloway, Stephen. 2008. Straight and level: practical airline economics. Burlington, VT: Ashgate publishing. Lewis, Walter David & Wesley Phillips Newton. 1979. Delta: The history of an airline. Athens, GA: University of Georgia Press. Morrison, Steven & Clifford Winston. 1986. The economic effects of airline deregulation. Washington, DC: Brookings Institution Press. Rasker, Ray, Patricia H Gude, Justin A Gude & Jeff van den Noort. 2009. “The economic importance of air travel in high-amenity rural areas.” Journal of Rural Studies 25(3):343–353. Savage, Ian & Burgess Scott. 2004. “Deploying regional jets to add new spokes to a hub.” Journal of Air Transport Management 10(2):147–150.
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Published on Mar 28, 2013