Columbia Economics Review: Fall 2016

Columbia Economics Review

Food for Thought Growing Pains The Shock Doctrine Pay your Dues Take Me to Court Second-Wage Feminism

Vol. VII No. I Fall 2016

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COLUMBIA ECONOMICS REVIEW P U B L I C AT I O N I N F O R M AT I O N Columbia Economics Review (CER) aims to promote discourse and research at the intersection of economics, business, politics, and society by publishing a rigorous selection of student essays, opinions, and research papers. CER also holds the Columbia Economics Forum, a speaker series established to promote dialogue and encourage deeper insights into economic issues.

2016-2017 EDITORIAL BOARD EDITOR-IN-CHIEF

Carol Shou

JOURNAL SENIOR EDITORS

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STAFF EDITORS

Derek Li Jessica Bai Mitchell Zhang Shambhavi Tiwari

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Manuel Perez Archila

Alex Whitman Daniel JunYeol Kim Douglas DeJong Kelly Butler Michael Allen Chu Michael Crapotta Neel Puri Oi Lam Michelle Yan

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Printed with generous support from the Columbia University Program for Economic Research Columbia Economics Review

Fall 2016

TA B L E O F C O N T E N T S

Globalization and Food Security 6

Food for Thought

Evaluating the Historical Decline of the Agricultural Sector and Changes in Food Consumption in Puerto Rico

The Government's Role in Growth

12

Growing Pains

The Composition of Fiscal Adjustments; Economic and Social Implications

Electricity as a Commodity

18

The Shock Doctrine

Long Term Effects of Electricity: Evidence from Brazil

Labor Economics

26

Pay your Dues

The Effect of Right-to-Work Laws on Union Membership and Wages

Pharmaceutical Finance

38

Take Me to Court

Pharmaceutical Settlements under the Hatch-Waxman Act: A Stock Price Analysis of Generic Firms

Labor and Women's Health

53

Second-Wage Feminism

How Access to Contraceptives Affects Female Wages: An Irish Study

For a complete list of papers cited by our authors and a full version of all editorials, please visit our website at columbiaeconreview.com

Opinions expressed herein do not necessarily reflect the views of Columbia University or Columbia Economics Review, its staff, sponsors, or affiliates.

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COLUMBIA ECONOMICS REVIEW

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Columbia Economics Review

Fall 2016

A LETTER FROM THE EDITORS Dear readers, As the year ends, we are thrilled to present to you our Fall 2016 issue, which we have dubbed the Policy Edition. We think it comes at a crucial time. 2016 was a critical year in political and economic terms, both for the United States and the entire world. The national and international agendas were dominated by debates surrounding issues like the Syrian refugee crisis and the future of the European Union. With these subjects, this year saw a rise in populist and regressive discourses that attempt to divorce themselves from the reality of the world. To claim, as many do, that we have entered a post-factual society, where truth can be molded to one’s will, is not only foolish but plainly dangerous. Facts exist and ignoring them has real consequences on people’s lives. We must keep this in mind as we move on to an era that will likely be defined by discussions and arguments about policies.

It is our job as economists to go beyond gathering and modeling data. We should aim to understand the world and take action based on that understanding. Knowledge cannot stay within the walls of academia; it has to be applied in order to make a difference. Policy making is a way in which applied economic research has a real measurable impact. As such, it should be done in a sensible and conscientious manner. Responsible policy making must be guided by clear and objective studies rather than by ideology. Moreover, it is important that we turn our critical eye to the existing regulatory and policy frameworks. What have their impacts, intended and unintended, been? What have their costs been? How can we improve them? These are questions that concern us and that demand from us a deep engagement beyond the standard economic theory we learn and teach in classrooms.

This year we were lucky enough to receive some incredible submissions from across the nation. For their creativity, rigor and vision, we are proud to feature these papers in our Policy Edition. They all come from different branches of economics and use a wide array of methodologies. Nonetheless, they are all, in one way or another, motivated by a policy question. In some cases, the implications are clear. In others, the one clear conclusion is that further research needs to be done. We hope that providing these papers with a platform will serve to highlight the importance of economic research as a guide for policy making and evaluation, and that it will encourage further investigation in new directions.

One of the sectors in which policy has the most visible impact is that of the health services and products. With recent concern growing about the monopolistic and anticompetitive nature of many of these companies, it is imperative to look at the underlying structure of incentives that policy frameworks create. Columbia alumnus Siran Jiang does so in her awarded thesis, which we feature here (38). Fiscal adjustments are another area in which policy has deep and measurable impacts. We are glad to see that research has moved to critically evaluate the impact of fiscal spending, not only on economic growth, but also on inequality and social welfare, as illustrated by David Vilalta (12). And, though the Columbia Economics Review has featured labor economics research before, Benjamin Zhang’s piece (26) struck us as particularly pertinent, as its investigation of right-to-work laws serves to better understand the consequences of a very relevant form of policy.

We also decided to include papers that dealt with other, less studied branches of policy making around the world. The interplay of gender norms and labor economics, studied in the particular conjuncture of Ireland by Benjamin Reid (53), is a subject on which we would like to see more research. The rapidly changing landscape of the agricultural sector also invites us to reevaluate the impact that past policies and programs have had on the food and health sectors. In this case, the globalization, industrialization and urbanism phenomena might be of particular interest, as Adriana Aguayo points out in her paper (6). Finally, Stephanie Kestelman (18) explores the effects of electricity rationing on household consumption, a good illustration of how policies affect and even shape the decisions of ordinary people. Future researchers and policymakers might want to look at these dynamics if they want to better understand the consequences of their actions.

As we move into 2017, we at the Columbia Economics Review remain convinced that well-thought and structured research holds the key to better policies, and that better policies will, in turn, help shape a better world. We decided to highlight these papers because we believe they are the first step in this sequence and that they demonstrate how academia should remain engaged with the real world in an independent and critical way. We hope to continue this idea and to adhere to the principles that have made it possible for many students and economists to remain connected with the world of academic research to this day.

All the best, Manuel Perez SEAS ’18 | Managing Editor Carol Shou CC ’17 | Editor-in-chief Ben Titlebaum CC’19 | Publisher

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Palatino Food for Thought Evaluating the Historical Decline of the Agricultural Sector and Changes in Food Consumption in Puerto Rico Adriana Aguayo Barnard College Aguayo provides an ample literature through which she examines the effects of a number of determinants on the stark decline of Puerto Rico’s agricultural sector. In her examination of income, food security, urbanization, and imports, Aguayo sets the stage for a riveting debate on the efficiency of policy initiatives in combating Puerto Rico’s agricultural decline. The policies have direct effects on not only the health of the sector, but also the health of the island’s people. With far- implications ranging from employment to obesity rates, Aguayo’s research is both engrossing and inherently relevant to today’s world.

-M.V.C. Introduction The World Food Summit of 1996 defined food security as existing “when all people at all times have access to sufficient, safe, nutritious food to maintain a healthy and active life,” (World Economic Forum, 2016). This paper begins with background on the determinants of food insecurity and its connections to health.

It then examines the historical decline of the agricultural sector in Puerto Rico throughout the 20th century. After a literature review and research, the paper finds that the decline of the agriculture sector created a state of food insecurity on the island, with negative impacts on the nutritional health of the population.

The paper follows with an evaluation on current policy programs during the decline of the sector and current programs that promote growth. In light of the historical patterns that led to food insecurity, the paper concludes that policy programs that foster growth in Puerto Rico’s agricultural sector via increased interest in working in the industry and development of land for sustainable agriculture should be used in place of less effective, income-supplementary programs.

Background A. Food Insecurity and Health The World Health Organization defines food security using three characteristics: 1) availability: sufficient quantities of food available on a consistent basis; 2) access: having sufficient resources to obtain appropriate foods for a nutritious diet; 3) use: appropriate use based on knowledge of basic nutrition and

the decline of the agriculture sector created a state of food insecurity on the island, with

negative impacts on the nutritional health of the population Columbia Economics Review

care (World Health Organization, 2016).

Changes in an individual’s budget constraint for food (given change in income or changes in purchasing power given changes in food prices) can lead to health issues like malnutrition and micronutrient or protein-energy deficiencies if consumers have less to spend on the foods that they usually buy. In other instances, food insecurity might arise from lack of affordable, nutrition foods. Households change their consumption bundles and reallocate income, spending more money on cheaper, energy dense foods instead of fresh, nutritious food. This in turn can lead to health complications concerning obesity and being overweight (Cook, 1433, 2004).

B. Income and Food Security Income level may be one determinant of food security, as individuals with higher incomes have more resources available to access nutritious foods.

Cook and Frank examine “resourceconstrained” food insecurity by investigating whether children exposed to food insecurity experience worse health outcomes than children from food secure

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8 families in inner-city settings. The authors use measures from The U.S. Household Food Security Scale to determine a 3-category (food secure, food insecure without hunger, food insecure with hunger) food security status predictor variable. To measure health, they conduct a survey asking children’s caregivers to

The paper finds that the decline of the

agriculture sector created a state of food insecurity on the island, with

negative impacts on the nutritional health of the population comment on their child’s overall health as “poor, excellent, fair or good,” and indicate whether the child had been hospitalized since birth. Cook et al collapse this data into two outcome measures of health: poor/fair and good/excellent and find that children in households categorized as food insecure without hunger had higher odds of poor health than those in food-secure households.

Children in households that were food insecure with hunger had even higher odds of poor health than those in foodsecure households (Cook, 1435 & 1436, 2004). This study shows how income can indicate food security by availability of resources to allocate to food consumption. However, “resource-constrained” food insecurity is not the only explanation for food insecurity leading to poor health outcomes.

C. Agriculture and Food Security Because the status of food security is dependent on the sustainable supply of fresh, nutritious food, agricultural production is important for food security.

The World Economic Forum declares that in order to meet the 70% increase in global demand for food by a 2050 estimated population of 9 billion, improvements to the global food system that provide both livelihood for farmers and nutrition for consumers are dire. (World Economic Forum, 2016).

Shocks to food security through the deterioration of agricultural land can occur in various forms. For instance, an FAO report detailing the impact and consequences of natural disasters on the deterioration of agricultural lands found that US$11 billion in damage to agricultural land and production – caused by a 2011 drought crisis in Sub-Saharan Africa – led to lower exports, a 25% decline in food consumption and imposed food insecurity to 15.5 million people in the region (FAO, 39, 2015).

II. Historical Decline of Puerto Rico’s Agricultural Sector Economic expansionary interests that occurred before 1900 initiated the trend of declining local food production and corresponding changes in food consumption during the twentieth century.

The demand of global export markets and Puerto Rico’s inclusion in the U.S. protected market led to the expansion of sugar and coffee-producing haciendas that restricted small farmers’ access to land to produce local crops including fruits, corn, root and other vegetables.

In turn, dependency on imports for food consumption increased dramatically in the periods spanning 1940-1990 (CarroFigueroa, 83, 2002).

In the last century, the agricultural sector in Puerto Rico has declined significantly due to industry changes. According to the United States Department of Agriculture, 85 percent of food consumed on the island is imported, despite its tropical climate and availability of suitable soil for crop production (USDA, 2016) and land available for agricultural production has deteriorated by 70% since 1940 (Movimiento Jose Nim, 2012). Given the current challenges that Puerto Rico faces in import dependency and sustainable food supply, it is important to understand the patterns that have driven the decline of an agricultural industry to inform policy changes and decisions.

During the 1940s-1990s, patterns of urbanization, industrialization and globalization generated several effects that contributed to the overall decline of the agricultural sector. The changes in food consumption in each period indicate increasing levels of food insecurity corresponding with changes in nutritional health of the population over time.

A. Urbanization and Decrease in Available Farmland Beginning in the 1950s the growth of the manufacturing sector accelerated the urbanization process, which contributed Columbia Economics Review

significantly to loss of available farmland. Pares-Ramos and Gould attempt to understand the effects of a shift from an agriculture-based to manufacturing dependent economy on the local population and urban development by comparing data from studies conducted before 1990 to government census data and landcover classifications from 1991-2000. The authors report the most prevalent ruralurban migration movements in 1950, specifically on the coastal plains where agricultural land was the most abundant.

In later years they report significant overall suburban population growth on the

85 percent of food consumed on the

island is imported,

despite its tropical climate and availability of suitable soil for crop production outskirts of the San Juan Metropolitan Areas. (Pares-Ramos, 2008).

Lopez and authors similarly examine the rate of urban growth in Puerto Rico from 1977-1994 and its influence on potential agricultural lands. The authors found an increase of 27.4% in urban areas over this time period significantly related to elevation, in areas with mostly lowland regions on lower slope while areas of no urban change occurred at higher elevations with steeper slopes. The authors identified that lowland areas in general are more suitable for agricultural production, but threatened by urban use because of their vulnerability to conversion to nonfarm use (Lopez, 2001).

Initial success encouraged investment in land development for manufacturing purposes and growth for the Puerto Rican economy, but generated a general lack of concern for the farmlands being destroyed by urban spread (Carro-Figueroa, 81, 2002). 1960 industry shifts towards petroleum and chemicals – mainly capital-intensive industries –displaced many workers and left the state facing an urban population with a demand for food that the small number of remaining farmlands no longer had the capacity to meet. Over time consum-

Fall 2016 ers turned mainly to the consumption of imports in the absence of locally produced foods, which was made possible by subsequent increases in income (Figueroa, 2012).

Industrialization and Increase in Import Consumption Increases in food imports may be associated with food insecurity. According to the Asociacion de Agricultores de P.R. (The Agricultural Association of Puerto Rico), if import supply were to stop, the island’s supply of fresh food would be exhausted within ten days and preserved foods within four weeks (Govardhan, 2015).

Successful industrial movements that began in the 1950s continued through the 1970s and brought about significant changes in local food consumption; primarily through economic growth that generated higher middle class incomes.

Fernandez et al conducted a study to assess the nutritional status of Puerto Ricans in 1966 and compared socioeconomic and dietary changes from results of a previous survey in 1946. The authors found increases in population income since 1946 corresponding with the trends in industrialization: 44% of families reported annual incomes under $500 in 1946 and only 8.4% reported at this level in 1966 (Fernandez, 960 & 963, 1966).

In the same study Fernandez et al found that as income increased between 1946 and 1966 variety of diet increased, but to include less locally produced foods such as cassava, plantains and other root vegetables. Higher income levels made it possible to respond to the decline of local food production by spending more money on imported foods, but the island was approaching a state of food insecurity and import dependency that, despite increases in income, did not

necessarily result in healthier food consumption patterns. Consumers substituted these foods for processed and canned imports that generally lacked nutrients, were denatured and provided poor nutritional value (Govardhan, 2015). The authors conclude that “higher economic standards and greater food availability do not necessarily mean better nutrition,” (Fernandez, 62, 1966).

These changes in diet were associated with corresponding, poor nutritional health and increases in nutrient deficiencies in the urban population. During the 1960s, Puerto Rico’s main imports mainly consisted of animal proteins, fruits and vegetables, cereals and canned foods (Carro-Figueroa 86). Colon-Ramos show that in general, the middle class’s higher incomes, combined with lack of available fresh foods, specifically the decline of root vegetable crops, led to increased spending on canned, imported foods (Colon-Ramos, 6).

A small portion of the agricultural sector remained from 1974-1978, but lacked competitiveness in local and export markets given the high cost of land and labor generated by the decline itself.

Furthermore, “curtailing inputs and reducing costs” was the only way that farmers were able to survive in the declining industry, which generated higher costs of food (Carro-Figueroa, 92, 2002).

Given these trends, and despite increases in income levels across socioeconomic groups, high-priced imports were not viable substitutes for low income individuals who depended on farmers producing traditionally-consumed crops on small farms that had suffered the most from the urban growth on agricultural lands B. Globalization and Nutrition Transition

traditionally-

The historical agricultural decline positioned Puerto Rico to face a series of complicated health challenges amidst issues of food security during significant periods of globalization. Puerto Rico was recently declared to be in a state of nutrition transition – a trend many developing countries experience when they switch from consumption of locally produced foods to an energy-dense, highly processed food diet—which can correspond with increases in income and indicate rising levels of obesity (Bellido, 2014).

small farms

In response to high local demand for imports, government programs in the 1970s developed large supermarket food

high-priced imports were not viable

substitutes for low income individuals who depended on farmers producing consumed crops on

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Higher incomes

shifted consumer preferences towards more imported foods and generated a similar preference for fast foods chains that sold imported food at lower prices. Since then, large food retailers such as Walmart and Costco have dominated the market for imported foods (Papillo, 2015). This led to increased convenience and consumption of imported foods for people across most income groups (Carro-Figueroa, 83 & 95, 2002).

Higher incomes shifted consumer preferences towards more imported foods and generated a similar preference for fast foods; this popularized western food chains and caused significant changes in food consumption. In a study identifying socio-demographic, behavioral and health-related correlates of food groups, Colon-Ramos and Perez Cardona (2013) suggest that Puerto Rico is currently in a state where a healthful diet is limited by physical access to nutrient-rich foods.

They use data from a population-based study conducted in seven municipalities in the San Juan Metropolitan area to observe food consumption patterns in five categories: fruits, vegetables, tubers and starches, fried foods (mainly traditional Puerto Rican foods), and ultra-processed fast foods. Colon-Ramos and Perez find that greater incomes since the middle of the century increased consumption of ultra-processed fast foods – especially amongst higher income individuals – and decreased consumption of locally produced traditional foods. Despite the higher incomes, wealthier individuals did not consume more fruits and vegetables, which are relatively more expensive than fast food. Consumption of cassava and root vegetables was common amongst older adults with low incomes (Colon-Ramos, 6, 2013).

Lack of agricultural production imposed high prices on fresh produce imports, but the growing popularity of fast food chains and supermarkets driven by globalization makes these foods readily more available and affordable. Whereas higher incomes in the 1960s and 70s also

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10 led to more consumption of imports and processed (canned) foods, the current state of food insecurity in Puerto Rico limits the income effect (i.e. the ability to afford a more diversified diet) (ColonRamos, 6, 2014).

III. Policies to Address Food Insecurity and Health A. Income-Supplementing Programs Given the trends of the nutrition transition characterized by the lack of a strongly developed agricultural sector, policies to address the food security in the island should focus on fostering growth in the agricultural sector rather than supplementing income. Many government interventions tackle food shortages as issues of “resource-constrained” food insecurity, but this approach does not account for the challenges presented by the historical decline of agricultural production. One such program is the provision of food stamps or cash sup-

The historical

failure of farming is perpetuating food insecurity today plements. However, these programs increase consumer purchasing power, which exacerbates unhealthful food consumption given the rising popularity of supermarkets and the struggling agricultural sector (Thomas, 1981). In 1974, Puerto Rico was initiated into the U.S. National Food Stamp Program (FSP), which Carro-Figueroa and authors argue negatively affected the diet and nutritional status of the population (Carro-Figueroa, 85, 2002). The Food Stamp Program supplemented incomes during a period when incomes were already rising due to industrialization, and when land available for agricultural production was being deteriorated for urban use. The FSP expanded consumers’ purchasing power that led to more sales in supermarkets and imported food products (Thomas, 1981). Additionally, “local farmers [were] unable to capture the expanded demand produced by the FSP” and in turn “processed items and other foodstuffs, which were before purchased sparingly, began to account for a bigger proportion of family

expenditures (Carro-Figueroa, 85, 2002).

Though the FSP increased family food consumption as intended, it did not attempt to address nutrition or sustainability of food consumption and thus did not address food insecurity.

Puerto Rico’s agricultural sector still struggles today, and current policies like the Nutrition Assistance Food Program perpetuate the same challenges by attempting to address food insecurity via income assistance. The program provides approximately 1.3 million Puerto Ricans whose incomes fall below a certain level with assistance that is required to be spent 75% on food and 25 % as cash (Papillo, 2015). While the program might be effective to ensure that people have enough to eat, it does not ensure nutritional health. According to the Department of Agriculture and the Department of the Family Affairs, the program has the annual potential to generate $60 million if farmers were to sell their products directly to program participants (Papillo, 2015). However, farmers are generally unengaged in these programs as farming’s historical failure has made agriculture a largely unpopular occupation in Puerto Rico: since the 1980s people began to “look at farming as something no intellectual person would do” (Thomas, 1981). Furthermore, given the nutrition transition and growing popularity of fast food outlined by Colon-Ramos and authors, this program does not ensure that individuals would spend the additional income on healthful foods supplied b y farmers.

The program is also problematic because it creates a reliance on an unsustainable, supplemented income.

Since individuals who benefit from the program are unemployed or have low incomes, the supplemental income could provide disincentive to enter the labor market (Papillo, 2015). This is neither sustainable nor does it encourage a transition to healthful food choices.

The biggest issue with the program in addressing food security is that does not foster the growth of an agricultural sector in Puerto Rico. An agricultural sector is necessary for food security. As trends from the historical decline show, agricultural production and sustainable food supply supports job creation and employment, lower prices of local food production and could lead to improved health outcomes during a nutrition transition.

Columbia Economics Review

B. Agricultural Growth Programs In order for Puerto Rico to overcome its food insecurity, it can foster growth in the agricultural sector by using a combination of two types of programs: 1) Programs that encourage interest in agriculture-related occupations (i.e. crop production and farming) to increase local supply of fresh, healthful foods; 2) Programs that focus on the recovery and development of valuable land for agricultural use to drive down high production prices that generate high food prices. i. Cultivating Interest Puerto Rico’s Agriculture Secretary and head of the Nutrition Assistance Program, Myrna Comas Pagan, recently expressed how the historical failure of farming is perpetuating food insecurity today, as “parents pushed their children away from the farms,” telling them, “‘if you want to be a prosperous man, you will need to study medicine or engineering. Agriculture is for people that don’t have anything to do,’” (Allen & Penaloza, 2015). Currently, the Nutrition Assistance Program and the Department of Agriculture are collaborating on ways to incentivize agricultural activity in Puerto Rico. Ideas for possible growth include advertising the availability (and sometimes lower cost) of locally produced foods, and encouraging adolescents to participate in the agricultural industry in order to foster growth with a longer projected lifetime (Papillo, 2015).

These programs may be able to address the challenges presented by the dual threat of farming’s historical unpopularity and the lack of consumer preference for more healthful foods over imports.

In the town of Orocovis, for instance, Dalma Catagena teaches agricultural science to her elementary school students.

She emphasizes the value of sustainability in community-based food production to change the way students think about agriculture. Catagena’s grass-roots efforts may have contributed to the rise in the number of young people engaged in

The program is also

problematic because it creates a reliance

on an unsustainable,

supplemented income.

Fall 2016 agriculture, reflecting her broader goals to “make the island self-sufficient and rebuild Puerto Rico’s agricultural sector,” (Allen & Penaloza, 2015). According to Secretary Pagan, such a trend could help Puerto Rico double its food production within the next ten years, if it continues.

(Allen & Penaloza, 2015).

The Strategic Plan [...] directs resources

to create educational spaces for children,

teachers and society at large to engage in the discussion about food security and sustainability.

ii. Cultivating Land Programs that focus on agricultural land growth while maintaining consumers’ purchasing power at an adequate level may also be effective in changing food consumption patterns. Though the end of the twentieth century saw a significant decline the agricultural sector, the 1997 Agricultural Census of the USDA identified 864,478 existing plots of agricultural land and a series of available natural resources (climate, land and water) that can be used to cultivate fields and water systems for sustainable crop production (1997 Census Publications, Puerto Rico).

Given the factors that deteriorated the agricultural sector throughout the twentieth century, programs that drive growth in geographic areas with potential agricultural value and emphasize the use of natural resources for sustainability will be best suited to address the current state of food insecurity. According to a report from the College of Agricultural Sciences at the University of Puerto Rico, agricultural imports currently amount to $4 billion per year. Reducing these costs would allow for less money to be spent on importing raw materials, which would reduce the cost of production to farmers – a current barrier to food production (College of Agricultural Sciences, 8, 2001). The report suggests a Strate-

gic Plan to Foster Agriculture in Puerto Rico that could be expanded for statewide implementation to expand the agricultural sector. The plan focuses on key elements of development addressing the factors leading up to the decline of the agricultural sector and the status of food insecurity: 1) enable farmers to improve their living and working conditions 2) develop environmentally friendly, economically viable and sustainable agricultural systems 3) offer learning opportunities for students focused on sustainable agriculture (College of Agricultural Sciences, 4, 2001).

The Strategic Plan entails several policies intended to gather and disseminate information from existing literature and from experienced farmers’ knowledge and use of traditional farming on “feasible, sustainable agricultural practices” (College of Agricultural Sciences, 16, 2001). The information is available as a database and serves as a guide to workshops, demonstrations and university courses. New information is shared through newsletters, email and websites. Additionally, the program supports the development and extension of research projects conducted by public sector agents; entrepreneurs and nongovernmental organizations, and private entities; small farms and plant nurseries. To evaluate the economic viability of sustainable agricultural practices The Strategic Plan emphasizes the use of “soil and crop management practices that maintain or enhance soil fertility” and the use of beneficial, organic materials as “alternate methods to the use of pesticides,” (College of Agricultural Sciences, 16, 2001). (College of Agricultural Sciences, 15-17, 2001).

The Strategic Plan has the potential to improve on PR’s insecure food system by cultivating interest in agricultural occupations and sustainable land development. “To spread knowledge among Puerto Rico’s population about the importance and benefits of sustainable agriculture,” the plan directs resources to create educational spaces for children, teachers and society at large to engage in the discussion about food security and sustainability.

IV. Conclusion Patterns of urbanization, industrialization and globalization led to the decline of the Puerto Rican agricultural sector that spanned the twentieth century but had significant effects on food security in different periods since its start in 1950.

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11 Changes in food consumption patterns and diet reflected the status of food insecurity, indicating that the unstable supply of fresh, affordable and nutritious food puts people at risk of several health issues. As the island is currently undergoing a nutrition transition, these issues are not associated only with malnutrition and poverty, but could also indicate emerging obesity in concordance with rising incomes. The Kaiser Family Foundation reports that over 65% of adults in Puerto Rico are obese, making it one of the top 20 states and districts in the United States for high obesity prevalence (The Henry J. Kaiser Family Foundation, 2014).

According to the report by the College of Agricultural Science, population growth and deterioration of land available for agriculture will force the United

Over 65% of adults in Puerto Rico are obese, making it one of the top 20 states and districts in the United States for high obesity prevalence.

States to cease agricultural exports in order to meet its own local demand by 2025 (College of Agricultural Science, 6, 2001).

Given Puerto Rico’s import dependency and weak agricultural sector, these trends have serious implications for the population’s well-being. Government programs to address food insecurity as an issue of limited income fail to address the actual reasons for its existence: the lack of interest in working in agriculture and the lack of available lands for agricultural production. Meanwhile, policies such as The Strategic Plan emphasize sustainability, creation of agricultural jobs and research and development necessary for addressing food insecurity. Going forward, future policy programs should take into account the evidence of historically unsuccessful programs, patterns in the agricultural industry’s decline and emerging health trends to address the nutritional health of the population and obtain a sustainable food supply for the future. n

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Growing Pains The Composition of Fiscal Adjustments: Economic and Social Implications David Vilalta University of Warwick Governments have different methods of fiscal adjustments throughout history, but the most effective and efficient methods of reducing budget deficits have been widely contested. The following paper discusses the implications of addressing budget deficits through spending cuts or tax increases with regard to social inequality and overall economic effect. Existing approaches and theoretical possibilities are used to provide a contextual background on which the author builds his argument. We are especially excited about this paper as it is relevant to the many declining economies of today’s world. With an ever changing global structure, governments cannot rely on what has been done before, but must think of new methods that apply today.

-M.A.C, M.V.C. 1. Introduction The fiscal adjustments implemented in many countries since the 2008 financial crisis have become a major source of controversy. The governments responsible claim they were necessary to reduce the excessive budget deficits. In some cases they seem to be correlated with an increase in GDP growth. However, spending cuts and tax increases have had high social costs at the same time, such as heightened inequality and youth unemployment.

In this paper we attempt to focus on periods where governments have implemented measures of fiscal consolidation in recent years. Our goal is to analyze the effects of tax increases or spending cuts in two areas at the center of the debate: economic growth and inequality. We do not aim to make a point for austerity measures being implemented or not in response to economic distress.

2. Literature review This paper is related to two different lines of literature. The first is the litera-

ture on the impact and composition of fiscal adjustments. Early studies were carried out by Giavazzi and Pagano (1990 and 1996). They use country-specific case studies and cross-country evidence to show how fiscal consolidations can be associated with “non-Keynesian� expansionary effects (Feldstein, 1982). The first paper to analyze the composition of large fiscal adjustments, Alesina and

Our goal is to

analyze the effects of tax increases or spending cuts in two areas at the center of the debate:

economic growth and inequality.

Columbia Economics Review

Perotti (1995), argues in line with further evidence by the IMF (1996) that spendingbased fiscal adjustments are more effective in stabilising debt to GDP ratios and can have more expansionary effects than tax-based adjustments.

Several studies by Alesina and Ardagna (1998, 2010 and 2012) expand those analyses and share most of the previous conclusions. Most of the studies prior to 2010 use the cyclically adjusted primary balance as the main measure of fiscal consolidations, as proposed by Blanchard (1993).

The second line of literature englobes the studies relating episodes of fiscal adjustments to changes in inequality of income, suggesting a potential trade-off between growth and inequality. The existence of this trade-off was accepted in the early 20th century (Boix, 1996), until the rise of Keynesian economics, when new sets of policies that were positive for both inequality and growth were proposed.

Mulas-Granados (2003) argues that the neoclassical paradigm came back to dominance in the 70s. Mulas-Granados (2005) first studied the potential short-run trade-

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Overall, past

literature suggests that in the short run spending-based

adjustments lead to more economic growth but are also more harmful for inequality than tax-based

adjustments, therefore creating a trade-off.

off between growth and inequality. He shows that in the short term, spendingbased adjustments can be more expansionary than tax-based adjustments but at the same time lead to higher inequality.

Similarly, tax-based adjustments are less expansionary (or contractionary) but increase inequality by less.

The modern empirical literature on this subject is quite limited, although it has been expanded in the past few years. Recent evidence suggesting that spending cuts lead to more inequality than tax increases has been developed by Agnello and Sousa (2012) and Woo et al. (2013).

The Gini coefficient is broadly used to measure inequality in these studies. Ball et al. (2013) use the “narrative” approach to identify fiscal consolidations and reach similar conclusions. All of these studies focus on the short-run impact.

Overall, past literature suggests that in the short run spending-based adjustments lead to more economic growth but are also more harmful for inequality than tax-based adjustments, therefore creating a trade-off. This paper focuses on (i) analyzing whether this trade-off holds for our sample and (ii) investigating whether it holds in the long term.

3. Data, definitions and methodology 3.1 Data The growth data spans 30 OECD countries in the years 2000 to 2014. The inequality data is more restricted, spanning 28 OECD countries over the years 2000 to 2012. Further information about countries, time periods, definitions of variables and sources is included in the appendix. To measure economic growth we use the logarithm of real GDP per capita

to normalise the data, as per previous literature. The main measure of inequality used is the Gini coefficient multiplied by 100, also consistent with previous studies.

3.2 Definitions of fiscal adjustments In order to measure the impact of fiscal adjustments we use the cyclically adjusted primary balance (CAPB) as the measure of the government’s fiscal stance. The data from the “narrative” method mentioned previously is limited and not available for this analysis. CAPB is calculated by subtracting the effects of business cycle fluctuations from the primary budget balance, as calculated by the OECD. The main assumption is that once the primary balance is adjusted for business cycles, most of its fluctuations come from policy changes. Therefore, an increase in the CAPB would indicate a fiscal adjustment.

CAPB can lead to biased results as it may account for non-policy factors which are correlated with exogenous variables affecting inequality or growth (Romer and Romer, 2010). This can lead to an upwards biased estimate (IMF, 2011). CAPB may also suffer from measurement error if it omits periods during which fiscal adjustments were accompanied by offsetting adverse shocks.

Thus we will restrict the definition of fiscal adjustment to periods where the reduction can be considered too big to be “business as usual.” Past literature used definitions to consider only periods of fiscal adjustments where the reduction was in the range of 1-2 per cent. We adopt the following definitions: Definition 1. A period of fiscal consolidation is a year when the cyclically adjusted primary balance (CAPB) improves by 1% or more.

This allows us to ignore all periods where the change in CAPB is likely to be due to exogenous changes in other variables instead of policy changes. We do not aim to distinguish between discretionary and non-discretionary policies, and assume firms and households react to both in a similar way.

Definition 2. A tax-based fiscal adjustment is a period where CAPB improves by 1% or more and government revenues as % of GDP increase by 0.5% or more.

When estimating tax-based fiscal adjustments in the baseline equation we include Gross Fixed Capital Formation (GFCF) as a control variable. GFCF measures the value of net investment in fixed assets in an economy. This way we control for improvements in economic activity that could be biasing upwards part of Columbia Economics Review

13 the estimates.

Definition 3. A spending-based fiscal adjustment is a period where CAPB improves by 1% or more and government spending as % of GDP decreases by 0.5% or more.

When estimating spending-based adjustments in the main model we will include as a control variable the percentage of people who are not in the age of working. This way we control for changes in spending that need to be carried out as a response to demographic changes, and may be biasing the results.

Other variables included in all the baseline specifications are the exchange rate in the same period (controlling for currency fluctuations) and the short-term interest rate (controlling for changes in monetary policy). The log of per-capita GDP and its squared term are also included in regressions on inequality (see Barro, 2008).

3.3 Methodology In order to measure the effects of fiscal consolidations on growth and inequality we use the following baseline specification model:

where subscripts i and t index countries and years, Y is the dependent variable, CAPB is equal to one in periods of fiscal adjustments and zero otherwise, and X’ is a vector of control variables (see previous section). The error term µ contains country-specific fixed effects λ. Equation (1) is estimated over the sample by difference GMM (Arellano-Bond).

It is assumed that both real GDP and the Gini coefficient are dynamic variables, that is, they depend on their own past realizations. Following past analyzes (Ag-

The main assumption is that once the

primary balance is adjusted for business cycles, most of its

fluctuations come

from policy changes.

14 nello and Sousa, 2012, Alesina et al, 2015) we assume a linear functional relationship across time. The last assumption of this model is non-contemporaneity: due to long transmission mechanisms and fiscal policy lags, we assume changes in the CAPB take at least one period to have an impact on the dependent variables. This implies current decisions are based on past outcomes. Therefore, we will focus on analyzing the impact on adaptive expectations rather than rational expectations.

The aim of this study is to measure the short and long-run impact of a 1 percentage point change in CAPB on growth and inequality. Results are presented for the estimated cumulated responses on changes in CAPB at periods t+1, t+2, t+3 and the long-run effect. Robust standard errors of the impulse responses are calculated via the delta method (Alesina and Ardagna, 2012). Equation (1) is estimated separately for periods of spending- and tax-based fiscal consolidations (as per the previous definitions). Finally, the various specifications are estimated with other proxies for inequality and different control variables to ensure the main results are consistent and sound.

Several estimation problems may arise from equation (1). In a dynamic model, lags of the dependent variable will be correlated with the error term, which is a source of bias and autocorrelation. While by assuming non-contemporaneity the potential endogeneity problem from reverse causality is eliminated, independent variables are not likely to be strictly

Fall 2016 exogenous either. For instance, changes in CAPB are likely to be correlated with past realizations of the error (IMF, 2011). Fixed effects contained in the error term may be correlated with other endogenous variables too. Thus, OLS estimation would yield biased results.

Difference GMM (Arellano-Bond) uses first-differences to transform equation (1) into

and or

therefore removing fixed effects.

However, all variables on the right hand side of equation (1) are still endogenous because, for instance, the term in is correlated with the term in . Deeper lags can be used as instruments since they are correlated with the previous lag but not with the error. For instance, and are related to

but not to the error term .

Instruments can be assumed valid unless the errors are serially correlated (Roodman, 2006). Since is related to because of the shared term, negative first order serial correlation is likely to appear in the first differenced

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residuals. Therefore it is only required that there is no second order serial correlation (Arellano and Bond, 1991). Tests for second order autocorrelation in the first-differenced residuals are reported in all regressions, as well as Sargan tests for the joint validity of instruments.

4. Results We study whether spending-based adjustments increase both economic growth and inequality by more than taxbased adjustments, therefore creating a trade-off. We compare the findings in the short and long term. Table 1 shows the cumulated effect of a 1% improvement in CAPB on real GDP (columns 1-3) and the Gini coefficient (columns 4-6) after one, two and three years, and the long-run effect. Results are broken down into (i) all adjustments, (ii) spending-based adjustments and (iii) tax-based adjustments.

4.1 Growth Estimates in columns 1-3 show that fiscal consolidations have a statistically significant expansionary effect on GDP

The aim of this study is to measure the short

and long-run impact of

1 percentage point change in CAPB on

a

growth and inequality.

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both in the short and long run. This adds evidence to the hypothesis of expansionary fiscal adjustments as initially proposed by Giavazzi and Pagano (1990).

On average, a 1% fiscal adjustment is associated with an increase in GDP of 0.20.3 percent within three years and 1.1-1.6 percent in the long term. The magnitude of these results is similar to previous literature, including Mulas-Granados (2005) and Alesina and Ardagna (2012).

The long-run results suggest the effect of fiscal consolidations is persistent across time. This points to supply-side effects being the major driver of the impact, since they are more likely to be structural and have a higher longterm impact than demand-side effects.

Moreover, since this model is based on adaptive expectations, it is not likely to capture demand-side effects relying on rational expectations. Structural reforms that may accompany fiscal adjustments

are improvements in business capacity constraints and labour market reforms.

Its effects are likely to be persistent and take place in the medium term (Summers, 2012).

The overall direction of these effects

On average, a 1%

fiscal adjustment is associated with an increase in

GDP of

0.2-0.3 percent within three years and 1.11.6 percent in the long term.

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15

is invariant if they are divided between spending and tax-based adjustments (columns 2 and 3). However, spending-based adjustments have a higher expansionary effect than tax-based adjustments in most periods, with peak effects of 1.590 percent and 1.119 percent respectively in the long run. Therefore, results suggest that fiscal multipliers are negative, and are greater (in absolute terms) for spending-based consolidations than for tax-based consolidations.

Several studies including Alesina et al.

(2014) and Alesina and Ardagna (2012) support this evidence. We now analyze potential reasons for this effect.

Regarding spending-based adjustments, Guajardo et al. (2011) argue that this may be due to monetary easing accompanying large spending cuts. Yet, as previously mentioned, monetary policy is included as a control variable in the above regression. Lane and

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16

Estimates suggest that an improvement of

1% in CAPB increases inequality in all

[...] with an overall impact of 0.417 on the long-run Gini coefficient. periods

Perotti (1996), argue that a reduction in government employment and wages weakens the power of unions. It reduces labour demand and wages demanded by workers, and can increase long-term profitability and investment. This may be accounting for part of the long run expansionary effect captured in the results.

On the other hand, tax-based fiscal consolidations seem to have smaller effects on output. Romer and Romer (2010) show that permanent tax increases reduce general investment and consumption, mainly on durable goods.

Moreover, increases in income taxes decrease post-tax real wages (Alesina and Ardagna, 1997). In unionized imperfectly competitive labor markets, which is the case in OECD countries (Blanchflower, 1996), unions demand higher pre-tax real wages to reflect the higher taxes.

This may harm competitiveness and investment, and decrease output growth.

Therefore, this suggests the labour market effect from tax-based consolidations will be smaller in the long run.

4.2 Inequality Estimates suggest that an improvement of 1% in CAPB increases inequality in all periods (column 4), with an overall impact of 0.417 on the long-run Gini coefficient.

Comparing between spending and tax-based adjustments (columns 5 and 6), it can be observed how this effect varies across time, but always points to increases in inequality. analyzing the short-run results, particularly after two periods, spending-based adjustments seem to be more harmful than tax-based adjustments. Point estimates for the short-run effect on inequality of spending and tax-based consolidations are 0.147 and 0.139, respectively, both statistically significant. This is in line with the hypothesis of a short-term trade-off

between growth and inequality. Both the direction and magnitude are consistent with results by Agnello and Sousa (2012) and Ball et al. (2013).

Long-run estimates suggest that spending-based adjustments have a smaller impact on inequality than taxbased adjustments. The estimates are 0.381 and 0.613 respectively, both highly significant. Therefore, this suggests that in the long run spending-based adjustments increase inequality by less than tax-based adjustments. The short-run trade-off between growth and inequality seems to disappear in the long run.

This expands the scope of the previous literature, and points to the existence of different medium and long-term dynamics in the effects of tax increases and spending cuts.

To expand our results, we regress the baseline model on the share of income held by each quintile in society. We control for monetary policy, the percentage of population not in the age of working, the exchange rate, and the log of per-capita GDP and its squared term.

Results show that increases in CAPB raise the income share of the top 20% while decreasing the income share of the rest. The result is the same regardless of the design of the fiscal adjustment The statistically significant short-term results (period 2 for the first and third quintiles, and period 1 for the second quintile) suggest that spending-based adjustments increase the income share of the top 20% by more and decrease the income share of the rest by more than tax-based adjustments. This adds evidence to the short-run trade-off between inequality and growth.

However, the long-term results suggest that spending-based adjustments increase the income share of the top 20% by less and decrease the income share of the rest by less than tax-based adjustments. This adds further evidence to the existence of different medium and long-term dynamics in the impact of tax increases and spending cuts that eliminate the short-run trade-off. We now turn to investigate channels that explain this result.

We start by analyzing the effects of spending-based adjustments. The OECD (2012) argues that cuts in social transfers lead to effective fiscal consolidations, since they create disincentives to work.

Social transfers are mainly directed towards lower-income groups such as the unemployed and the disabled. These groups rely on such transfers as their

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primary source of income. Cuts in those areas will therefore increase inequality, as the higher-income groups are unaffected. Regarding the long-terms gains in incentives and productivity claimed by the OECD (2012), they could potentially be influencing the relative decrease in the long-term impact of spending cuts compared to tax increases.

Alesina and Perotti (1995) and MoralBenito (2012) show that cuts in public sector wages are one of the main areas where governments decrease expenditures when carrying out fiscal adjustments. Jenkins et al. (2011) show that the share of wages in the incomes of lowerincome groups is significantly higher than in the rest of groups. Therefore, wage decreases are likely to increase inequality in the short run, as these groups will see their main source of income decrease while the effect on other groups’ income will be relatively smaller. We previously suggested that as proposed

by Lane and Perotti (1996), decreases in public wages can create expansionary effects in the long run. If this leads to a reduction in unemployment, then the long-term impact of spending cuts on inequality may be smaller.

We now turn to the effects of tax-based adjustments. The IMF (1996) shows earning and corporate taxes have longer lags, so their biggest impact on inequality is felt in the long term, as reflected in the results. Multiple studies including the OECD (2012) argue that regressive taxes such as VAT have a much bigger impact on inequality than income and corporate taxes. Since such types of taxes are paid equally by everyone regardless of their wealth or income, the relative effect over an individual’s income is higher in lower-income groups.

wage decreases are likely to increase inequality in the short run Corporate taxes can also be considered as a source of inequality. As argued by Kotlikoff (2011), higher corporate taxes can lead to firm relocation and investment fleeing to look for higher returns.

This may create unemployment and leave the workers bearing the tax increase, instead of corporations. Increases

Fall 2016 in inequality from this rise in unemployment would be felt in the medium and long run given the time it takes for firms to relocate. Taxes on earnings are progressive so they tend to have a lower negative effect on inequality than regressive taxes (Woo et al. 2012).

Overall, our results show that in the short run, spending-based adjustments lead to higher growth and higher inequality than tax-based adjustments.

This is in line with the short run tradeoff proposed by Mulas-Granados (2005).

Results also suggest that this trade-off disappears in the long-run. Estimates for the long-run effect suggest spendingbased adjustments lead to higher growth and lower inequality than tax-based adjustments.

5. Robustness checks In this section we study alternative specifications in order to check the robustness of the previous analysis. Tables with results are included in the appendix (tables 4-11).

5.1 Growth In table 4 we add extra control variables to the GDP regressions, namely private consumption, exchange rate fluctuations in the same period and a year trend (columns 1-3). Results are consistent with our previous estimates. Adding the average growth of the G7 countries instead of private consumption (columns 4-6), tax increases become more expansionary than spending cuts in the long run, but results are not statistically significant.

Next, we modify the baseline equation to include the same independent variables in the equations for both spending cuts and tax increases, together with a year trend (Columns 7-9). Most results are significant and suggest spending cuts are more expansionary than tax increases in all periods except period 3.

Finally, in table 5, we include different sets of control variables than in the baseline specification. In columns 10-12, we control for exchange rate fluctuations in the same period, the long-term government yield and a year trend.

All results are smaller than in previous specifications. There is no statistically significant evidence that spending cuts are more expansionary than tax increases in the short run. In columns 13-15 we control for exchange rate fluctuations in the same period and government debt as a percentage of GDP. The magnitude of this results is similar to the initial one, and overall estimates are broadly

consistent with previous analysis.

5.2 Inequality In tables 6 and 7 we analyze the robustness of the results on the Gini coefficient. In columns 1-3 we include a time trend. In columns 4-6 we also include additional control variables, namely the unemployment rate and private consumption. Results are consistent with the previous estimates. Tax increases seem to be less harmful in the short run when estimates are statistically significant, but more harmful in the long run.

Moreover, we analyze the baseline regression using the same independent variables for both tax increases and spending cuts, and include a time trend.

Results are presented in columns 7-9.

Estimates are still consistent with the previous analysis. As an alternative set of control variables we use the average growth of G7 countries and the unem-

Long-run estimates

suggest that spendingbased adjustments are

more expansionary and increase inequality by less than tax-based adjustments.

ployment rate (columns 10-12). This alters the results significantly. The longrun effects of overall, spending- and taxbased consolidations drop from 0.417, 0.381 and 0.613 in the initial estimation to 0.379, 0.271 and 0.347, respectively.

However, the relative impact of spending and tax-based adjustments in the short and long run is unchanged.

Alternative specifications for the regressions on the income share held by each quintile of the population are presented in tables 8-9 and 10-11. In tables 8-9 we include a year trend instead of exchange rate fluctuations. In tables 1011 we include a year trend, the average growth of G7 countries and gross fixed capital formation, instead of short-term interest rates and the percentage of population not in the age of working.

Both estimations yield similar results to the ones previously obtained.

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17 6. Concluding remarks 6.1 Conclusion In recent years there has been a lively debate about the positive and negative impacts of austerity measures. In this paper we have studied the different impact that fiscal adjustments have on inequality and growth according to their composition. Results suggest there is a short-term trade-off between growth and inequality when implementing fiscal adjustments: in the short run, spendingbased adjustments increase economic growth by more than tax-based adjustments, but increase inequality by more as well. However, results suggest that in the long run this trade-off disappears. Long-run estimates suggest that spending-based adjustments are more expansionary and increase inequality by less than tax-based adjustments. This expands on previous literature and suggests the existence of different mediumterm dynamics in the impacts of fiscal policy.

Policy implications cannot be drawn without studying the specific areas in which spending cuts and tax increases are implemented. For example, spending cuts in disability benefits are likely to have a greater impact on inequality than any tax increase. Similarly, since higher levels of income tend to save more, taxing those savings is not likely to be as harmful for growth as VAT increases.

Further analysis should focus on providing more detailed estimates of which specific spending cuts and tax increases lead to better and worse outcomes.

6.2 Limitations The main limitations of this analysis are the small number of observations and our measure of fiscal adjustments. A larger dataset and the use of the “narrative� approach to calculating fiscal adjustments could improve the evidence presented. All regressions pass the test for second order serial correlation or can only be rejected at the 10% level.

Sargan tests reject the joint validity of instruments in some occasions, meaning that the lags of some variables used as instruments are correlated with the error term. This was expected since both GDP and inequality measures are affected by a large amount of factors that appear in the error term. As pointed out previously, the results of this analysis may have an upward bias. However, this is less relevant when analyzing the relative effect between tax and spending adjustments, assuming the magnitude and direction is the same for both. n

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The Shock Doctrine Long Term Effects of Electricity: Evidence from Brazil Stephanie Kestelman Swarthmore College

This paper was selected for publication because of its relevant policy implications. Kestelman uses rigorous statistical tests performed to control for bias. The paper reveals that an in-depth exploration of the inelasticity of energy demand could provide further insight regarding consumption patterns on a household level. Although the data used in the study were collected more than a decade ago, the results are still relevant to today’s readers––especially in light of the recent political environment and policy debate regarding sustainable energy.

-M.Y., K.B.

Introduction In the past few decades, climate change has prompted policymakers to reduce public demand for energy. However, demand for electricity is highly inelastic.

Few policies have had a long-term effect on energy consumption on the residential level, and most treated groups returned to pre-policy levels of consumption after a short period of time due to difficulty in sustaining behavioral changes (Allcott and Greenstone 2012; Costa 2012; Davis, Fuchs and Gertler 2012; Gerard 2013; Siqueira et al. 2006). Previous literature has not examined the Brazilian electricity rationing of 2001-02 as an example of how to induce conservation at the household level.

In 2001 and 2001, a severe drought affected parts of Brazil. The drought led to a decrease in the volume of water in hydroelectric plant’s reservoirs, an effect that was intensified due to inefficiency and inadequate infrastructure. In June 2001,

the Brazilian government implemented a rationing policy to lower residential demand for electricity and to reduce the risk of power shortages. From June 2001 to February 2002, households in 17 of the 27 Brazilian states had to reduce energy consumption by at least 20 percent.

Two types of incentives were used to encourage reductions in residential consumption of electricity: economic and social. Economic incentives included consumption ceilings and increases in tariffs––households that consumed an excessive amount were fined, and those with additional savings earned bonuses. Some even risked interruption of supply. The government also subsidized energy-efficient appliances. In this semi-voluntary system, households could decide whether they wanted to ration energy.

As a social incentive, the government established a national educational campaign, educating households across the country on ways to reduce consumption

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of water and electricity. Even states that were not under rationing were covered by the scope of the informational campaign.

The government appealed to Brazilian nationalism by forging a national commitment to conservation (Gerard 2013).

Other aspects of the campaign included appeals to the fact that energy is a public good, to the economics of rationing and to the moral argument that conserving is “the right thing to do.” The campaign also encouraged households to switch to more energy-efficient appliances. In February 2002, reservoirs were once again at safe levels because of rains and reduced consumption. The policy was lifted and the educational campaign ended. The rationing successfully led to reductions in consumption during the shortage.

The goal of this paper is to estimate the long run effects of the rationing and to examine the channels through which the rationing affected residential consumption of energy. There are two channels that

Fall 2016 can affect energy consumption: physical investments and behavioral changes (Gerard 2013). More energy-efficient appliances demand less energy, thus reducing consumption. The information campaign and subsidies may have led households to buy energy-efficient ap-

Gerard and Costa concluded that

social incentives, in the form of

information, could affect household’s consumption

patterns, potentially yielding long-term

behavioral changes.

pliances in order to reduce consumption of electricity. In contrast, behavioral changes can yield changes long-term consumption patterns (Costa 2012). The fine and quota might have acted as Pigouvian taxes, leading to internalization of the externalities of energy consumption. Meanwhile, the campaign might have provided the information to change households’ consumption patterns. It is more challenging to change behaviors than to increase physical efficiency, but the former can have more permanent effects.

Two economists have estimated the permanence effects of the rationing and found similar conclusions. Gerard (2013) used state-level data for 2000, 2003 and 2005 to analyze rationing-induced changes in residential consumption of electricity. He attributes changes in consumption to changes in household behavior and finds no effect of conservation through closure of the efficiency gap for domestic appliances. Gerard notes that “households reported systematic changes in the way they used domestic appliances and consumed electricity. Popular conser-

vation strategies during the crisis, unplugging freezers and avoiding standby power use, were still more prevalent [four years later] among households that had been subject to the conservation program” (p.3). He concludes that social incentives like the national educational can lead to medium run reductions in consumption. In contrast to Gerard’s statelevel data, Costa (2012) examined household-level data from the state of Rio de Janeiro (RJ) from 2000 to 2005. He also found evidence for changes in behavior, rather than the acquisition of more energy-efficient appliances. Both Gerard and Costa therefore concluded that social incentives, in the form of information, could affect household’s consumption patterns, potentially yielding long-term behavioral changes.

In the next sections I estimate the permanence effects and the role of different channels in changing consumption levels during the rationing. I describe my data sources and specification in sections 2 and 3, and the results in section 4. I offer policy recommendations in the conclusion.

Data I use state-level data from 2000 to 2011 to estimate the effects of the rationing policy on the entire country, rather than just one area. My main sources of data are listed below. Table 1 describes the variables used and Table 2 summarizes the data.

A. ANEEL: ANEEL (Agência Nacional de Energia Elétrica) is Brazil’s National Energy Agency. ANEEL publishes yearly reports on energy consumption with the Brazilian Ministry of Mines and Energy. The report divides consumption by state and sector. I collected state-level residential consumption data for 2000 to 2011 from the 2006 and 2014 “National Balance” reports. I also obtained yearly state-level data on energy tariffs by consumption category. Since ANEEL did not exist until 2003, tariff data from 2000 to 2002 was compiled from pieces of legislation approving changes to tariff rates in 2000, 2001 and 2002 (Law n˚ 10.483/2002, Resolution n˚ 91/2001, Resolution n˚ 485/2002).

B. IBGE and IPEA Data: The Brazilian Institute of Geography and Statistics is the national statistical agency. I collected survey micro-data from the 2000 and 2010 censuses and from the 2001-2009 and 2011 National Annual Domestic Survey (PNAD), which reports sample data for the country and its states. Economic

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19 data was collected from IPEA (Institute for Applied Economic Research).

One shortcoming of these data is that they were not all collected in the same way. Data from 2000 and 2010 were collected during the census, while data for all other years were estimated from samples of households. The possibility of measurement errors occurring is higher in the latter set of data. Additionally, information on tariffs was highly dependent on the availability of documentation for each state’s tariff resolutions for a given year, which may result in attenuation bias.

Empirical Model Kuziemko and Werker (2006) modeled the relationship between aid and membership in the Security Council, and used binary variables to account for preand post-membership years, as well as a country’s term in the council. I use their strategy to develop the specification below and use fixed effects estimation with standard errors clustered on state:

where ln_consumpit is the natural log of the amount of energy consumed by residences in the state i in year t, y1it and y2it equal 1 if state i was under rationing and the year was 2001 or 2002 respectively, yiit equals 1 in year i in states where rationing was implemented, appl_indexit is the index for sales of appliances in state i and year t, rationingi is a dummy variable that equals 1 if rationing was implemented in state i, and Υi and ηt are state and year fixed effects respectively. I also include a set of controls Xit for time-variant state characteristics, drawing from Gerard (2013).

This rationing policy can be considered a natural experiment. In 2001, 97 percent of Brazil’s electricity came from hydrological generation (Veja 2014). Any shock to the generation of hydroelectricity would imply a shock to aggregate supply of electricity of almost the same magnitude. Other sources of electricity were not meaningful enough to close the gap between supply and demand. Also, implementation of the policy depended on natural attributes of each state, such as pluviometric characteristics. Thus, the policy naturally generated a con-

20

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Fall 2016 trol and a treatment group, depicted in Figure 1. Nationwide infrastructure issues and inefficiency affected the country homogeneously. All states were also equally exposed to the national educational campaign. Finally, the shortage could not spillover from one state to another. The Brazilian electrical grid is partitioned into electric systems South, North, Southeast-Midwest and Northeast. Electricity cannot be transferred from one hydrological basin to the other and no states in the control group could help states under rationing manage the shortage. Residential consumption of electricity in a given state was therefore not correlated with that in states in a different treatment group. Thus, there can be no spillovers.

I test the claim that this constitutes a natural experiment using pre-drought data. Tables 2 and 3 provide evidence of the near-experimental assignment of the treatment and control groups. Only two of the control variables were statistically significantly different across groups for the year 2000: the Gini coefficient and the average age of the population. However, while statistically significant, these measures are small enough to lack economic significance. We can therefore infer a causal relationship between the rationing policy and changes in residential electricity consumption, given the specification above.

Results Figure 2 plots average residential consumption of electricity (log) by year for the treatment and control groups. The graph shows that between the years 2000 and 2001, average consumption in both treated and non-treated states declined and did not immediately return to prerationing levels. The group under the rationing policy shows a greater decline in consumption, which suggests that the policy was successful in promoting greater conservation. Moreover, the decline in the untreated group indicates that the policy had spillover effects. This is in line with previous findings, including those publicized by the Brazilian government during the period (Alkmin, Schmidt and Lima 2004). Average consumption had been increasing before 2000 for both groups, and started increasing again after 2002, which indicates that the trend was for consumption to continue to increase in 2001 and 2002 had there not been a rationing policy. The fact that the trend was broken in 2001 and 2002 suggests a causal relationship between

the rationing policy and the decline in residential consumption of electricity in both groups.

Table 4 presents the estimates for the empirical model listed above, using the natural log of residential consumption as the dependent variable. I estimate the effects of the rationing in equations (1) and (2), including state fixed effects in the second. The coefficients in (1) are statistically insignificant, while coefficients in (2) are significant at the 1 percent level, suggesting unobserved heteroskedasticity and supporting fixed effects estimation. The coefficients in equation (2) indicate that, in states where the rationing policy was implemented, residential consumption of electricity was 25.2 percent lower in 2001 than in 2000, and 27.2 percent lower in 2002. These findings are in line with the policy’s requirement that consumption decline at least 20 percent during the rationing period. Without controlling for anything other than the treatment itself in treated states, consumption fell more than was required. However, the decline is too large in magnitude given government reports.

Equation (3) controls for year fixed effects to estimate nationwide effects of the policy. Year dummy variables control for changes in consumption in the control states, as well as the upward trend found in Figure 2. We find that, in relation to pre-rationing levels, nationwide consumption was 7.9 percent lower in 2001 and 6.9 percent lower in 2002. These results are statistically significant at the 1 percent level. The rationing policy spilled over state borders to have nationwide effects, as can be observed in the decline in consumption for both groups in Figure 2. However, the coefficients for y1 and y2 suggest that the rationing policy has no statistically significant effect on consumption. That might be because of omitted variable bias. As we can see in figure 2, average consumption in treated states took longer to return to pre-treatment levels. The upward trend for residential consumption, on the other hand, returned once the rationing was lifted.

That means that the coefficients for the first couple of post-rationing years are expected to be negative and negatively correlated with y1 and y2. There could be positive bias in equation (3), causing the coefficients for y1 and y2, which are expected to be negative, to be biased towards 0.

Equation (4) addresses the omitted variable bias in equation (3) by controlling for the differences in the time it took Columbia Economics Review

21 for states to return to pre-rationing levels of consumption. The coefficients for y3 through y11 estimate the permanence effects of the rationing in treated states, or if and when the effects of the policy ends in states where rationing was implemented. Similarly, the coefficients for the year fixed effects estimate the permanence effects in the control group. Controlling for permanence and year fixed effects, I find that consumption in control states was 5.9 percent lower in 2001 and 5.0 percent lower in 2002 than in 2000.

These results are statistically significant at the 1 and 10 percent levels, respectively. Treated states, however, reduced consumption by even more. In relation to pre-rationing levels, consumption was 11.0 percent lower in 2001 and 10.7 percent lower in 2002, totaling a reduction of over 20 percent under the policy and suggesting that semi-voluntary policies can effectively achieve their conservation targets. These results are statistically significant at the 5 and 10 percent levels, respectively, indicating omitted variable bias in the estimation of the rationing effects in equation (3).

Equation (4) also shows there is no evidence for permanence effects. Year fixed effects are statistically insignificant in 2003 and 2004, but they are positive and statistically significant in 2005. This indicates that residential consumption in untreated states returned to pre-rationing levels soon after the policy was lifted and resumed the previous upward trend in two years. The coefficients for the interaction variables are not statistically significantly different from zero, with the exception of y6. An F-test indicated the other interaction variables, whose coefficients are negative but not statistically significant, are also not jointly significant. Therefore, there were no real differences in permanence effects between treated and untreated states. Costa (2012) and Gerard (2013) argue that households subjected to the rationing policy changed their behaviors in the long run, moving to a steady state of lower consumption.

I find that there were no such changes in steady state. In fact, reductions in consumption of electricity ended shortly after the end of the rationing policy in both treated and non-treated states. I look at the causal channels later in this section.

Note that the coefficient for y6 is negative and statistically significant. That is because a water shortage in 2006 affected many of the states treated in 2001-02. Officials had warned of another potential crisis back in 2002, when the crisis with

22 which this paper is concerned ended (La Insignia 09/02/2006). The government did not take the necessary measures to address another water crisis. Fortunately, the shortage of 2006 was not as drastic as that of 2001. Nonetheless, we see a significant reduction in consumption in treated states in 2006. This suggests that, while residences did not switch to a new steady state, as Costa and Gerard claim, they did learn to conserve energy in emergency situations.

Households are thus able to voluntarily reduce consumption in times of water shortage, even without a rationing policy. . Equations (5) and (6) estimate whether behavioral changes or physical investments drove reductions in consumption. I use the sales of appliances as a proxy for household investments in energy efficient appliances, since households would need to buy new items to replace the less efficient ones. In equation (6), I account for the possibility that channels of reduction were different across treatment groups by adding interaction variable between the appliances index and the rationing variable. The findings are similar to those of equation (5). The impact of physical investments is not significantly different from 0 at the 10 percent level in either equation, and the coefficients for y1 and y2 are statistically significant and negative, indicating that the decline in residential consumption of electricity under the rationing was due to causes other than the closure of the efficiency gap. Thus, like Costa and Gerard, I find that the conservation of electricity that took place in 2001 and 2002 was not due to physical investments, but rather to changes in behavior during the time.

Physical investments and behavioral changes are not completely independent, however. Davis, Fuchs and Gertler (2012) note that even efficient appliances might cause consumption of electricity to increase. It could be that households were conserving energy in other ways and believed they could use efficient appliances more intensively. In this case, consumption would have decreased because of behavioral changes and not because of the closure of the efficiency gap. This result may also suggest that the subsidies and information campaign only reached energy-efficient households. Allcott and Greenstone (2012) suggest that imperfect information is key determinant of electricity overuse, as well as efficiency gaps. They claim that both can be solved with information campaigns.

Energy inefficient households in treated states might have found it less costly to change their behaviors in the short run than to invest in new appliances. Once the

Fall 2016 rationing was lifted, the cost of consuming efficiently became too high. Since no physical investments had been made, long-term consumption was unaffected. This could explain the success of the policy in the short-term and the reversion to past consumption levels after a couple of years.

Additionally, equations (5) and (6) estimate that nationwide effects were shortlived, which indicates that the steady state of energy consumption did not change.

These findings are in line with those of equation (4). Controlling for physical investments, households in the control group reduced consumption by 10.3 percent on average, while households in the treatment group reduced consumption by 21.4 percent on average. Both groups returned to pre-treatment levels roughly three years after the policy was lifted. Similarly to (4), we find that even though households in the rationing group did not move into a new steady state of lower consumption, they remembered the behavioral changes made in 2001 and 2002 and used them to conserve electricity in 2006, during the other water crisis.

Semi-voluntary rationing programs are effective

in the short run, but do not affect consumption patterns permanently.

Table 5 addresses the robustness of the findings from Table 4. Equations (7) and (8) control for the logarithm of the yearly electricity tariff in each state, the logarithm of average household income, state population and poverty rate as a proxy for employment. The last three controls are not individually or jointly significant at the 10 percent level. However, I find that consumption is highly elastic to changes in the tariff rate: a 10 percent increase in the tariff rate (equivalent to R$2 for most states in 2011) yields an average reduction in consumption of 1.55-1.6 percent, or roughly one third of the overall reduction in 2001 under the rationing policy. Given the high statistical and economic significance of the tariff coefficient, we can argue that nationwide reductions in consumption are tied to the cost of electricity. Increases in tariff rate were therefore effective means of reducing household consumption.

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Additionally, residential consumption in treated states was 4.6 percent lower than the national average in 2001, controlling for physical investments and changes in the tariffs. We can therefore confidently argue that in 2001 the rationing affected residential consumption through behavioral means. Behavioral changes in treatment states can be attributed to both economic and social incentives, modeled by the tariff and the rationing variables y1 and y2. Note that in 2006, states affected by a new water shortage reduced consumption by 7.9 percent (significant at the 5 percent level), reinforcing the hypothesis that households learned to change their behavior and to conserve when needed.

Conclusion The paper finds no permanent effects of the rationing. Like previous literature, we find that the program was successful during the water shortage with spillover effects: national average consumption decreased during the drought, mostly due to the national information campaign and the tariff penalty. However, unlike Costa (2012) and Gerard (2013), I find no permanent effects in treated or untreated states. I also find that the efficiency gap does not account for most of the reduction, supporting Alcott and Greenstone (2012). Households voluntarily abided by the quota, changing their behavior in the face of shortage risks, but they did not make significant physical investments that would have affected consumption in the long run. The national education campaign was successful in promoted changes in behavior in the short run. Information policies can successfully means promote countywide conservation.

This paper’s findings suggest policy implications. Semi-voluntary rationing programs are effective in the short run, but do not affect consumption patterns permanently. A policy similar to the Brazilian rationing would be effective in an emergency situation. Short-term success depends on the semi-voluntary nature of the policy and on the information campaign. Reiss and White (2008) found that successful reduction in electricity consumption depends on voluntary conservation responses. Allcott and Greenstone (2012) argue that imperfect information functions as a key determinant of over consumption of electricity, and so educational campaigns inform households about how to conserve energy and lead energy-efficient lives.

Policies should also consider the interconnectedness of electricity with other public goods. For example, water availability in Brazil affects the availability of electricity.

Fall 2016 An understanding of how households view these relationships is key to creating a sense of urgency in conservation campaigns.

The Brazilian case also indicates that households are more responsive to tariff changes than the literature has led us to believe. High elasticity of electricity consumption with respect to changes in the cost of electricity itself suggests that new pricing policies for public goods can promote great conservation of natural resources. Haselhuhn et al. (2011) found that individuals are more likely to change their behavior when they have been fined and that risk-averse households reduce consumption in fear of the penalty. In the Brazilian case, households might have reduced consumption during the rationing so as to avoid paying fines, thus explaining the short run success of the semi-voluntary model with a loose quota and fines. As noted previously, reductions in consumption came from behavioral changes, and not physical investments, making long run changes more important to the sustainability of lower levels of electricity consumption.

Once the policy was lifted, individuals went back to their old patterns, as evidenced by the lack of permanence effects. Future research should look at the effects of increasing tariffs based on how quickly consumption has been rising, and verifying whether new pricing policies can yield long run reductions in consumption.

Finally, governments could implement a local or national permanent semivoluntary quota system modeled after the Brazilian rationing policy. There wouldn’t necessarily be an emergency component to the policy, which would undermine household’s willingness to conserve. However, a large enough penalty might incentivize households to change their consumption habits and decrease their baseline levels of energy consumption. This policy would not yield long-term changes in behavior, but it would reiterate the short run effects of the rationing year after year. Similarly, the government could use information campaigns to raise awareness about climate change and create a sense of urgency around that, promoting conservation effects similar to the one found in 2006 in treated states. Another possibility is to create an information campaign that does not rely on scarcity as a justification, focusing instead on other conveyed messages. Behavioral insights could be used to test the impact of different types

of messages. Policies like these might face political difficulties, but would address the main issue at hand: the need to reduce demand for energy and other natural resources, taking necessary steps

23 to mitigate climate change. n Figures and Tables

Figure 1: Map of Brazil, by States

Figure 2: Residential consumption of electricity by treatment group, 2000-2011

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24 Table 1: Description of the Variables

Table 2: Summary Statistics, year 2000 (pre-treatment)

Table 3: Natural Experiment Verification, pretreatment and post-treatment data

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Fall 2016 Table 4: Estimation Results, Permanence Effects, and Causal Channels

Table 5: Changes in residential consumption of electricity by state, with controls

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Pay your Dues The Effect of Right-to-Work Laws on Union Membership and Wages Benjamin Zhang Princeton University As authorized by the passing of the Taft-Hartley Act in 1947, Right to Work (RTW) laws affirm the right of every American to work for a living without being compelled to work for a union. Existing research that has been done regarding the use of RTW laws finds that its implications are far-reaching. In the following paper, the author investigates the enactment of RTW laws in Indiana and Michigan. Buoyed by robust statistical and econometric analysis, the author is able to draw comparisons and extract results about RTW and their effect on the wages and union membership. In a time where public and governmental policy regarding wages is being contested and debated over daily, the author’s paper provides a valuable, research centered approach to how to tackle this topic. The paper’s ambiguity of results characterizes it as a foundational work that calls for greater work and research into the intersection that exists between labor economics and law.

-R.S. Introduction To date, twenty-six states have adopted right-to-work laws as authorized by the Taft-Hartley Act of 1947. Formally titled the Labor Management Relations Act of 1947, this legislation permits states to outlaw union security agreements by passing right-to-work laws, so that private-sector unions cannot require union membership or payment of dues as a condition of employment. While many states enacted right-to-work laws immediately following the passage of the Taft-Hartley Act, three states have only recently done so.

These states are Indiana (March 2012), Michigan (March 2013), Wisconsin (March 2015), and West Virginia (July 2016).

One might expect that such legislation would decrease the proportion of privatesector workers in labor unions by limiting the ability of unions to maintain membership and collect dues, even from those covered by the union’s contract (“free riders”). One might also expect that by weakening the membership and bargaining power of labor unions, such legislation would result in decreased wages

earned by unionized workers. This effect could even extend to non-unionized workers, since employers would face a smaller threat of unionization, reducing the need to provide higher wages closer to the union wage (Farber 2005).

However, the negative effect of rightto-work laws on wages may not be so clear. By increasing employment, such laws may actually have the opposite effect. Companies may be attracted to states with right-to-work laws, since they would face weaker labor unions. The increased demand for labor that follows would then drive wages up. Nevertheless, I hypothesize that right-to-work laws do have a negative effect on both union membership and wages.

In this paper, I conduct an empirical investigation of the effect of recent rightto-work laws on both union membership and wages. I take care to consider the very real possibility of omitted-variable bias: both wages and the adoption of right-to-work laws could be correlated with underlying local economic trends.

A simple OLS regression could thus over-

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estimate the significance of right-to-work laws. By considering changes in certain variables during the years immediately surrounding enactment of right-to-work laws in Indiana and Michigan, using the difference-in-differences (DID) technique, it is possible to estimate the effect of rightto-work laws on these variables and minimize omitted-variable bias. I consider the fraction of private-sector workers in labor unions, the fraction of union workers who are free riders, the wages of union members, and the wages of non-union members, as well as the wages of union members compared to the wages of free riders.

Section 2 summarizes the existing literature on the effects of right-to-work laws.

Section 3 describes the data set being used and Section 4 describes the methodology being applied. Section 5 reports results, and Section 6 discusses and concludes.

Literature Review The literature on the effects of right-towork (RTW) laws gives mixed results.

Moore (1980) finds that RTW laws have no statistically significant effect on union

Fall 2016 membership after controlling for simultaneous equations bias. Farber (1983) also finds no effect on union membership, attributing the lower extent of unionization in states with RTW laws to lower demand for union representation. Ellwood and Fine (1983) find a 5–10% reduction in union membership immediately after the passage of a RTW law, based on examination of flows of workers organizing into unions rather than the total stock of union membership.

The effects of right-to-work laws on wages are similarly uncertain. Farber (2005) takes RTW laws as an exogenous decrease in the threat of unionization in his analysis of threat effects, controlling for individual demographic measures as well as time-invariant industry and state fixed effects. Using the examples of Idaho and Oklahoma, which enacted RTW laws in 1985 and 2001, respectively, he finds that non-union wages fell 4.2% after the passage of Idaho’s RTW law, but that Idaho union wages, Oklahoma non-union wages, and Oklahoma union wages all showed no statistically significant effect due to passage of RTW laws. Rinz (2015) focuses on the states that enacted RTW laws immediately after the passage of the Taft-Hartley Act in 1947, arguing that the timing of RTW legislation was exogenous in these cases. Using a differencein-differences model, and controlling for state, year, and census division by year fixed effects, he finds that the average effect of RTW laws on wages across all sectors is “small and slightly negative.”

Finally, Reed (2003), by controlling for initial economic conditions in these states at the time of passage of the RTW laws, finds that average wages are actually significantly higher in RTW states than in non-RTW states.

While the ambivalent state of the current literature is not particularly encouraging, examining the recent developments in Indiana and Michigan—which are relatively large states— would advance the literature by testing established methodology with new data and adding evidence either in favor of significant RTW effects or none at all. Given recent renewed public interest in right-to-work laws, this analysis would also be interesting to policymakers considering RTW legislation. In investigating whether the recent passage of RTW laws in these three states had significant impacts on union membership (both in terms of the fraction of workers unionized and the fraction of workers who are free riders) and wages (for both union and non-union workers),

the results will intrigue both economists and politicians alike.

Data My analysis uses data from the Current Population Survey (CPS), a monthly survey of households conducted by the United States Census Bureau for the Bureau of Labor Statistics. The CPS surveys households about employment, earnings, and other demographic characteristics.

Households in the survey are interviewed once a month for a four month period, then ignored for eight months, and then interviewed again for another four month-period. However, only households in the fourth and eighth months of their rotations are asked questions on usual weekly earnings and hours as well as union membership, which are essential to my analysis of right-to-work laws on wages. Therefore, the files actually employed in the regressions are extracts from the CPS containing only the households being surveyed in their fourth and eighth months. Termed “Monthly Outgoing Rotation Groups”, these files were compiled by the National Bureau of Economic Research. Since the CPS is conducted by the Census Bureau, a U.S. government agency specifically tasked with conducting surveys, it is reasonable to assume that the data is fairly reliable and complete.

I use data files from 2009 to 2015, a period of time beginning three years before passage of Indiana’s RTW law in 2012 and continuing to the latest data available. I restrict my attention to non-self-employed workers—the “eligible” universe in the data, for which union and earnings data are collected. I also limit my investigation to individuals employed in private, for-profit companies, the ones primarily affected by RTW laws. Out of 2,224,425 total observations from 2009 to 2015, 876,214 satisfy these two criteria.

A complicating factor in the data set is the procedure used when respondents do not answer the survey questions on wages. The Census Bureau and BLS use a process called “hotdecking” to estimate wages and hours of individuals who do not provide this information, based on demographic characteristics of similar individuals such as age, sex, and education.

However, the estimation process does not consider union status, so this “allocated” wage data will not produce reliable estimates for union and non-union workers separately. To this end, when working with wage data, I use allocation flags given in the data to drop 309,281 obser-

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27 vations with allocated wage data.

The important variables are described below. All variables whose descriptions begin with “indicates” are binary 0/1 indicator variables.

RTW Variables The right-to-work law (rtw) variable indicates whether an individual lives in a state with a right-to-work law at the time of the observation. This variable is 1 for residents of Indiana beginning in April 2012 and for residents of Michigan beginning in April 2013. For all other states, it is 1 if the state is a RTW state. Since all other RTW laws were passed before 2002 or after 2014, rtw is not time-dependent for states besides Indiana and Michigan.

The right-to-work state (rtw state) variable indicates whether an individual lives in a state that has ever had a rightto-work law.

Union Variables The covered by a union contract (unioncov01) variable indicates whether an individual is either a member of a union or a non-member covered by a union contract. I assume that all union members are covered by a union contract. This variable is generated from combining two variables in the data set: unionmme and unioncov, which indicate union members and non-union members covered by a union contract, respectively.

The union member (unionmme01) variable indicates whether an individual is a member of a union.

The free rider (unionfr01) variable indicates whether an individual is a “free rider”, defined as a worker who is covered by a union contract but is not a union member. To be explicit, the universe of this variable is covered workers: unionfr01 is 1 when a worker is covered by a union contract but not a union member; 0 when a worker is covered by a union contract and a union member; and [missing] when a worker is not covered by a union contract.

Table 1 illustrates the distinctions between union coverage, union membership, and free riders. Of the 876,214 observations in the period 2009–2015, all of the 57,393 union members are assumed to be covered by a union contract. Of the 818,821 non-members, 6,203 free riders are covered by a union contract.

Wage variables The hourly wage (wage) variable represents hourly wage, in dollars. Consistent with the recommendation of the

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NBER documentation, this is calculated by dividing weekly earnings (earnwke) by weekly hours (uhourse). earnwke is asked of non-hourly workers and computed for hourly workers as hourly earnings multiplied by weekly hours.

The log hourly wage (logwage) variable represents the natural logarithm of the hourly wage.

The allocation flag (alloc01) variable indicates whether either component of wage has been allocated: usual hours per week or usual earnings per week.

white, black, American Indian, Asian/ Pacific Islander, and other. For individuals of mixed race, if any of the races listed is “black”, I classify him/her as black; otherwise, if any of the races listed is “white”, I classify him/her as white; otherwise, if any of the races listed is “American Indian”, I classify him/her as American Indian; otherwise, if any of the races listed is “Asian/Pacific Islander”, I classify him/her as Asian/Pacific Islander. The remaining individuals are classified as “other.”

Fixed-Effect Variables The industry (industry) variable is an NBER-coded industry classification code with 51 categories.

The state (state) variable represents the individual’s state of residence via a unique numeric code for each state.

The year (year) variable represents the year in which the individual was surveyed.

Data Overview Summary statistics for these variables are given in Table 3. As usual, the mean of a binary 0/1 indicator variable represents the proportion of observations for which the variable equals 1.

Some comments concerning sample size are in order (recall that the full sample consists of 876,214 observations).

First, note that there are only 63,596 observations of unionfr01 because the universe of this variable is restricted to workers covered by a union contract, as explained above. Next, there are 58,299 missing values in the wage data, so wage has 817,915 observations. Of these, 1,339 observations have a value of 0, so logwage is defined for 816,576 of the nonmissing wage values. Finally, there are 7,501 missing values in the metropolitan status data, so metro01 has 868,713 observations.

Histograms for the wage and age variables were constructed. There exist 2,403 outliers below the federal minimum tipped wage of $2.13 and 79 outliers above $300 (in the latter case, because weekly hours were less than 10), but the number of outliers is relatively small.

The distribution of the hourly wage is roughly what one would expect, with most observations clustered around $10– $20 per hour and gradually tapering off at higher wages. The distribution of ages is also unremarkable: a sharp increase as young adults aged 16–25 enter the workforce, a plateau through the working years, and a gradual decline after age 55 as older adults retire.

Demographic Variables The age (age) and square of the age (agesq) variables represent the age and the square of the age of the individual, respectively.

The education (education) variable represents the education level of the individual. I recode this variable to have only five categories, represented by the numbers 1 through 5. In order from 1 to 5, these are: less than high-school (HS) education, HS education, less than 4 years of college, 4 years of college, and greater than 4 years of college.

The Hispanic (hispanic01) variable indicates whether the individual is Hispanic.

The male (male01) variable indicates whether the individual is male.

The marital status (marital01) variable indicates whether the individual is married with his or her spouse present.

The metropolitan (metro01) variable indicates whether the individual lives in a metropolitan area.

The race (race) variable represents the race of the survey respondent. I recode this variable to have only five categories:

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As a first step to understanding the data, I graph the evolution of the union membership and union free rider rates in Indiana and Michigan over time. My graphs plot monthly and yearly averages in the rates for each state. I expect that the unionization rate would decrease and the free rider rate would increase after the RTW law is introduced, but it is evident that the data are noisy: only the free-rider rate in Michigan seems to appreciably change after the introduction of the RTW law. Furthermore, the union free rider rate is calculated based on only 210 observed free riders over the 2009–2015 sample period, which is a very small number. This preliminary graphical analysis seems to suggest that my findings will be limited, both because of noise in the data and because of a small sample size in union members and free riders.

For a more formal statistical analysis of the union membership and union free rider variables in the above graphs, I run t-tests to analyze the difference in means before and after the introduction of the RTW law. The p-values imply that Michigan experienced a significant drop in union membership and a significant increase in union free riders after the introduction of its RTW law (at the 5% level), while Indiana did not.

Methodology The purpose of this paper is to study the effects of right-to-work laws. To this end, I consider the effects on five key variables: the fraction of all workers who are members of labor unions, the fraction of union workers who are free riders, the wages of workers who are covered by union contracts, the wages of workers who are not covered by union contracts, and the wages of union members compared to the wages of free riders.

OLS As a first step in examining the effect of RTW laws, I run OLS regressions of each dependent variable of interest on the regressor rtw.

The specifications have the following general form:

where i indexes individuals, j indexes industry, s indexes state, t indexes time, and rtwst indicates whether a state s has a RTW law at time t.

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30 Equation (1) is estimated with each of the following dependent variables Y: union membership (unionmme01); union free riders (unionfr01), over a sample of unioncovered workers; wages (logwage), over a sample of union-covered workers; and wages (logwage), over a sample of noncovered workers.

In addition, I estimate wages (logwage) with an additional regressor of unionmme over a sample of union-covered workers:

I use heteroskedasticity-robust standard errors, as I do not wish to make assumptions concerning the residuals.

To interpret the coefficient β1 in equation (1), recall that rtwst is a binary 0/1 indicator variable. I see that β1 represents the difference in the average value of the outcome variable Y in RTW states and the average value of Y in non-RTW states:

Therefore, β1 seems to represent the marginal effect of the right-to-work law on the outcome variable Y, as desired. However, the estimate of β1 is not causal; it does not represent the change in Y that would result from passing a right-to-work law in a given state. The simple OLS specification (1) can reasonably satisfy the OLS assumptions of random sampling and existence of fourth moments, by nature of the CPS survey process and the basic inspection of the data in Section 3, respectively. However, it almost certainly suffers from omitted variable bias, violating the exogeneity OLS assumption and rendering the estimates non-causal. Therefore, I improve upon my basic OLS specifications by using the difference-in-differences technique to mitigate omitted variable bias.

Difference-in-Differences The difference-in-differences (DID) technique attempts to isolate the effect of a treatment by controlling for fixed entity and time effects. In this case, I have data on outcome variables (union status and wages) for a treatment group of certain states (Indiana and Michigan) and a control group of other states, both before and after the treatment (the passage of an RTW law) is applied to the treatment states. I then assume the parallel trends assumption, which states that in the absence of the RTW law treatment, the treatment and control states follow similar trends in the outcome

Fall 2016 variables. These outcome variables are assumed to change by the same amount over time in both groups, therefore preserving any fixed state differences.

Formally, in the absence of the RTW treatment, the outcome variable is determined by a state effect and a year effect that are independent of each other:

where i indexes individual, j indexes industry, s indexes state, and t indexes time.

I then account for the RTW law treatment by including the dummy variable rtwst that is 1 when state s has a RTW law at time t:

The DID model examines the coefficient β on rtwst, which represents the amount by which the trend of the treatment group deviated from the trend of the control group.

Under the parallel trends assumption, this coefficient must therefore be the effect of the treatment. The coefficient β represents, in the treatment states after treatment, the difference between the observed average value of Y and the unobserved counterfactual average value of Y in the absence of treatment:

The regressions for the basic DID model have the following form: where i indexes individual, j indexes industry, s indexes state, t indexes time, rtwst indicates whether a state s has a rtw law at time t, treatments is a binary 0/1 variable indicating whether the individual resides in a treatment state, and aftert is a binary 0/1 variable indicating whether the individual was surveyed after the treatment was applied.

Equation (4) is estimated with each of the following dependent variables Y: union membership (unionmme01); union free riders (unionfr01), over a sample of unioncovered workers; wages (logwage), over a sample of union-covered workers; and wages (logwage), over a sample of non-

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covered workers.

In addition, I estimate wages (logwage) with an additional regressor of unionmme over a sample of union-covered workers:

The treatment group here consists of the states Indiana and Michigan, and the control group consists of all other states. The treatment variable rtwst is therefore equal to treatments* aftert. I use heteroskedasticity-robust standard errors, as I do not wish to make assumptions concerning the residuals.

The coefficients for equation (4) can be interpreted in terms of sample means of Yijst, as shown in the following table. For example, the average outcome of Yijst for individuals in control states before the treatment is applied is β0.

I take the difference-in-differences β1 to be the effect of the right-to-work law on Y, controlling for (binary) fixed state and time effects. Now, the estimate of β1 begins to take on a causal interpretation.

The interpretation of β1 as the differencein-differences of sample averages is consistent with the interpretation given in (3) as the difference between the observed average value of Y and the unobserved counterfactual average value of Y in the absence of treatment. First, note that by the parallel trends assumption,

that is, the unobserved counterfactual average value of Y in the treatment states is given by the observed average value of Y in the control states plus the time-invariant state effect, which is observed at t = 0 (before the treatment). Therefore,

Fall 2016 showing that the interpretation of β1 as the difference-in-differences of sample averages is the same as the interpretation (3), just using different notation.

With this model, it is evident why the recent changes in RTW laws are so important for analyzing the effect of the laws.

Without any changes in the identification of the rtwst variable over time in any state, the presence or absence of a rightto-work law is indistinguishable from a state fixed effect γs. Thus, the DID models would suffer from perfect multicollinearity. Furthermore, the simple OLS models in section 4.1 would then clearly suffer from omitted variable bias, as the rtwst variable simply represents fixed differences between two groups of states, not the effect of RTW laws themselves. Once I have a change in RTW status in certain states, I can use the DID models to control for state and time fixed effects to gain a more accurate estimate of the effect of RTW laws. In this case, the DID specification arguably mitigates omitted variable bias, because changes in the RTW status of Indiana and Michigan can be attributed to exogenous political factors, such as the conservative resurgence in the 2010 United States midterm elections, that are not correlated with the outcome variables.

Expanding Fixed Effects A natural extension of the DID model allows for more than two groups and time periods. I expand the difference-in-differences model by allowing for more fixed effects: instead of only two state groups and time periods, I include dummy variables for each state and year, to implement full state and time fixed effects. In addition, I add industry fixed effects as well. The regressions for the expanded DID model have the following form:

where i indexes individual, j indexes industry, s indexes state, t indexes time, rtwst indicates whether a state s has a rtw law at time t, δj represents industry fixed effects, γs represents state fixed effects, and λt represents time fixed effects.

Equation (6) is estimated with each of the following dependent variables Y: union membership (unionmme01); union free riders (unionfr01), over a sample of union-covered workers; wages (logwage), over a sample of union-covered workers; and wages (logwage), over a sample of non-covered workers.

In addition, I estimate wages (logwage) with an additional regressor of unionmme over a sample of union-covered workers:

The treatment group here consists of the states Indiana and Michigan, and the control group consists of all other states.

The interpretation of the coefficient β1 is the same as the interpretation (3) in the basic DID model. I use heteroskedasticity-robust standard errors as I do not wish to make assumptions concerning the residuals.

Adding Controls Finally, I supplement the difference-indifferences model by allowing for control variables. I add several demographic control variables: age, age-squared, education, ethnicity, marital status, metropolitan status, race, and sex.

The regressions for the final DID model have the following form:

where i indexes individual, j indexes industry, s indexes state, t indexes time, rtwst indicates whether a state s has a rtw law at time t, xi is a vector of individual demographic characteristics, δj represents industry fixed effects, γs represents state fixed effects, and λt represents time fixed effects.

Equation (8) is estimated with each of the following dependent variables Y: union membership (unionmme01); union free riders (unionfr01), over a sample of union-covered workers; wages (logwage), over a sample of union-covered workers; and wages (logwage), over a sample of non-covered workers.

In addition, I estimate wages (logwage) with an additional regressor of unionmme over a sample of union-covered workers:

The treatment group here consists of the states Indiana and Michigan, and the Columbia Economics Review

31 control group consists of all other states.

The interpretation of the coefficient β1 is the same as the interpretation (3) in the basic DID model. I use heteroskedasticity-robust standard errors, as I do not wish to make assumptions concerning the residuals.

Modifications and Robustness Checks I consider some variations to the final specification (8) to assess the robustness of my results and thus the internal validity of my analysis. In most cases, the interpretation of the coefficient on the rtw variable remains the same; see (3) above.

Heterogeneous Treatment Effects Originally, I pooled the states of Indiana and Michigan into one treatment group in order to obtain a larger sample size and reduce the standard errors.

However, it is possible that the treatment effects of the right-to-work laws in these states are heterogeneous: the effect in Indiana may be different from the effect in Michigan. Therefore, I estimate equations (8) and (9) twice more for each dependent variable: once with a treatment group of Indiana only and once with a treatment group of Michigan only. The control group, all other states excluding Indiana and Michigan, is unchanged.

Control Groups Originally, I used all states excluding Indiana and Michigan as a control group.

As a robustness check, I now estimate equations (8) and (9) twice more for each dependent variable: once with a control group of non-RTW states, and once with a control group of RTW states. The treatment group, Indiana and Michigan, is unchanged.

Probit Models Because the variables for union membership and free rider status are indicator variables, and an OLS regression estimates the expectation of the dependent variable conditional on the regressors, I am in effect estimating probabilities. That is, if Y is one of the indicator variables, then the OLS regression (1) estimates

Therefore, the OLS regressions for these indicator variables are actually linear probability models. As an alternative specification to (8), I run probit regressions as well. The probit model has the

32 advantage of varying the estimate of the treatment effect at different values of the dependent variable. Including the marginal effects of the treatment, the probability that the dependent variable equals 1 is restricted to lie in the interval [0,1].

I use this probit specification is when the dependent variable Yijst is a binary indicator variable: union membership (unionmme01) and union free riders (unionfr01), the latter over a sample of covered workers.

Here, the coefficient β1 still captures the effect of right-to-work laws on the outcome variable Y, but because I am dealing with a probit model, the marginal effect of RTW laws on Y is not β1 but rather

where ϕ is the probability distribution function of the standard normal distribution.

The specification (10) is similar to the models outlined in Farber (2005) that estimate the probability of unionization separately for each year. There, the probability of unionization is taken to be a measure of the threat of union organization, but RTW laws are not included as a regressor.

In fact, Farber (2005) takes RTW laws as an exogeneous decrease in the likelihood of union organization when analyzing the effect on wages. By including RTW laws in the regression, my probit models are essentially testing his assumption that RTW laws decrease the likelihood of union organization.

Union Membership vs. Union Coverage Originally, I analyzed the effect of rightto-work laws on the union membership rate and on the wages of union-covered and non-union covered workers. As a robustness check, I estimate equation (8) once more for these dependent variables: union coverage (unioncov01); wages (logwage), over a sample of union members; and wages (logwage), over a sample of nonmembers.

These estimates should not differ much from the estimates in Section 4.4, because the only difference between union mem-

Fall 2016 bership and union coverage is the population of free riders, which is relatively small in number.

Timing of RTW Changes As mentioned in footnote 5, Indiana’s right-to-work law took effect on March 14, 2012 and Michigan’s right-to-work law took effect on March 28, 2013. Therefore, as discussed in Section 3 I set rtw equal to 1 for residents of Indiana beginning in April 2012 and for residents of Michigan beginning in April 2013. However, these RTW laws are not retroactive: they only affect future union contracts, not existing ones. It is also conceivable that the possibility of an impending RTW law may affect negotiations of union contracts taking place shortly before the enactment of the law. Therefore, the effect of RTW laws may be diffused over a period of time as existing union contracts expire and are renewed. As a robustness check, I thus experiment with small adjustments to the coding of the rtw variable by changing the time at which Indiana and Michigan are indicated to have a RTW law. I estimate equations (8) and (9) for each dependent variable with alternative codings of the rtw variable, offset -3, +3, and +6 months from the original date.

Sample Size Originally, I used a sample consisting of the seven-year period 2009–2015. However, since 2009 was deep in the midst of the Great Recession, it makes sense to include earlier data so that the results would then be applicable in both periods of deteriorating labor markets and periods of recovering labor markets. As a robustness check, I therefore estimate equations (8) and (9) for each dependent variable over an expanded 14-year sample period of 2002–2015.

Outliers Finally, I analyze the robustness of my results to outliers. I estimate equations (8) and (9) twice more for each wage variable: once excluding the highest and lowest 1% of values and once excluding the highest and lowest 5% of values. The variables estimated are wages (logwage), over a sample of union-covered workers; wages (logwage), over a sample of non-covered workers; and wages (logwage), including the regressor (unionmme) over a sample of union-covered workers. The thresholds are 1.526056 < logwage < 4.278265 (4.60 < wage < 72.12) for a 1% trim, and 2.002481 < logwage < 3.912023 (7.41 < wage < 50.00) for a 5% trim.

Columbia Economics Review

Results The Methodology section above essentially outlines two series of specifications.

I now turn to the results of estimating these specifications.

One “baseline” set of regressions, given in Sections 4.1–4.4, begins with a simple OLS specification and builds up to a difference-in-differences model with full fixed effects and control variables. This series of regressions aims to investigate the effect of right-to-work laws on the various dependent variables considered: the union membership rate, the union free rider rate, the wages of union-covered workers, the wages of non-covered workers, and the wages of union members compared to the wages of free riders.

The second series of regressions, given in Section 4.5, consists of a battery of robustness checks to analyze the validity of the baseline regressions. I modify various aspects of the full baseline specifications (8) and (9) (with full fixed effects and control variables) one at a time and examine whether the baseline results are sensitive to these slight changes in model specification: heterogeneous treatment effects, control groups, probit models, union membership vs. coverage, timing of RTW laws, sample size, and outliers.

Summary The results indicate that for all variables, omitted variable bias in the OLS and the difference-in-differences models was a significant problem. Adding full industry, state, and year fixed effects leads to substantial changes in the estimated coefficients, demonstrating that it is important to control for these fixed effects in any estimate that I wish to interpret causally. Adding demographic control variables— age, age-squared, education, ethnicity, marital status, metropolitan status, race, and sex—does not further change the results by much.

I find that RTW laws decrease the unionization rate by 0.7 percentage points, significant at the 5% level. This finding is consistent with my hypothesis that RTW laws weaken unions. I also find that union members earn 6.18% more than free riders, significant at the 1% level. For the other variables, there is no definitive evidence, as the estimates are not statistically significant. The point estimate for the effect of RTW laws on the free rider rate (+1.3 percentage points) has a positive sign as expected, as RTW laws limit the ability of unions to maintain membership. However, the point estimates for the

Fall 2016 effect on both union wages (+2.17%) and non-union wages (+0.479%) also have positive signs, which is unexpected, because I expect that RTW laws decrease unions’ bargaining power and therefore both union and non-union wages as well.

The results are not robust to the choice of treatment group (except when considering the wages of union members compared to the wages of free riders, which makes sense since the right-to-work law is not the primary regressor of interest).

This indicates that the effect of right-towork laws is heterogeneous: it is different in Indiana and Michigan. The estimates for Michigan are more precise than those of Indiana, though this may just be a result of having more observations in Michigan. Unfortunately, while Michigan shows a statistically significant effect of RTW laws on the free rider rate of +2 percentage points, it also shows a statistically significant effect on union wages of +6%, which contradicts my hypothesis.

The results are generally robust to the other variations in model specification.

Union Membership The results show that controlling for industry, state, and year fixed effects led to a large change in the estimate, indicating substantial omitted variable bias in the simple OLS and DID specifications. Using the DID model with full fixed effects and demographic controls, RTW laws are estimated to decrease the union membership rate by 0.718 percentage points. This estimate is significant at the 5% level.

Such a result is consistent with the hypothesis that right-to-work laws diminish the ability of labor unions to enforce membership among an employer’s workers, so that the unionization rate falls when a RTW law is passed. However, the magnitude of the effect is relatively small in percentage terms: about 0.7 percentage points. Nonetheless, this still equates to about 50,000 workers, using a crude estimate of 7 million private-sector workers in Indiana and Michigan combined.

I report the results of the robustness checks for varying the treatment group and the control group. The baseline specification is identical to my last specification, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate the same baseline specification but with the treatment groups of Indiana only and Michigan only, respectively, as proposed in Section 4.5.1. This is achieved by excluding Michigan observations from the estimation and excluding Indiana observations

from the estimation. I estimate the same baseline specification but with the control groups of non-RTW states and RTW states, respectively, as proposed in Section 4.5.2. This is achieved by including non-RTW states, Indiana, and Michigan observations in the estimation and including RTW states, Indiana, and Michigan observations in the estimation.

The results indicate that the baseline estimate of a 0.7 percentage point decrease in the unionization rate is not robust to the choice of treatment group. The negative effect of RTW on unionization is estimated to be 1.1 percentage points in Michigan, significant at the 5% level, and 0.1 percentage point in Indiana, not significant even at the 10% level. However, the baseline estimate is relatively robust to the choice of control group, with the estimates varying between 0.6 and 0.9 percentage points and retaining significance at the 5% level.

I report the results of the probit model robustness check. The OLS specification in column is the specification given in Section 4.4. It is identical to the last specification, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate another specification, which includes the same regressors but uses a probit model instead of a linear model, as proposed in Section 4.5.3. I also estimate the average marginal effect of the rtw variable on the dependent variable unionmme01, as computed using the margins Stata command. This number represents the average marginal effect of the right-to-work law on the union membership rate under the probit model.

The result of the probit model is a 0.5 percentage point decrease in the unionization rate due to the RTW laws. This indicates that the baseline estimate of a 0.7 percentage point decrease in the unionization rate is fairly robust to the choice of a linear or probit model.

I report the results of the remaining robustness checks. I estimate the same baseline specification but with a dependent variable of union coverage (unioncov01) instead of union membership (unionmme01), as proposed in Section 4.5.4. I also estimate the same baseline specification but with slight changes in the coding of the rtw variable, as proposed in Section 4.5.5. The rtw variable is coded to change from 0 to 1 at three alternative times: 3 months before the effective dates of the RTW laws in Indiana and Michigan, 3 months after, and 6 months after.

I estimate the same baseline specification

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33 but with a larger sample size, including observations from 2002–2008 in addition to those from 2009–2015, as proposed in Section 4.5.6.

The results indicate that the baseline estimate of a 0.7 percentage point decrease in the unionization rate is fairly robust to the use of union coverage instead of union membership (0.65 percentage points) and to slight variations in the coding of the rtw variable (0.5–0.7 percentage points), though the significance of the result decreases under the rtw timing variations. However, the baseline estimate is not particularly robust to expansion of the sample size. The new estimate is a 1.8 percentage point decrease, which is significantly different from the baseline estimate, yet very precise because of the expanded 2002–15 sample period. Fortunately, this new estimate is of larger magnitude than the baseline estimate even with more observations, which strengthens the validity of the original result.

In summary, the estimated effect of RTW laws on the union membership rate is a 0.7 percentage point decrease, consistent with my hypothesis that RTW laws decrease union membership. This number is significant at the 5% level, but it is not robust to the choice of treatment group, meaning that the effect of the RTW law is different for Indiana and Michigan.

Indeed, the 0.7 percentage point decrease is a weighted average of a 0.1 percentage point decrease in Indiana and a 1.1 percentage point decrease in Michigan. The estimates are robust to the other modifications, and even increases in magnitude under a larger sample size.

Union Free Riders I report the results of estimating the baseline specifications. I estimate specifications (1), (4), (6), and (8), one by one, and successively add more control variables.

The results show that controlling for industry, state, and year fixed effects led to a large change in the estimate, indicating substantial omitted variable bias in the simple OLS and DID specifications. Using the DID model with full fixed effects and demographic controls, RTW laws are estimated to increase the union free rider rate by 1.27 percentage points. Such a result is consistent with the hypothesis that right-to-work laws diminish the ability of labor unions to enforce membership among an employer’s workers and allow workers to be covered by union contracts even if they are not members of the union, increasing the prevalence of free riders.

However, this estimate is not significant

Fall 2016

34 even at the 10% level, and the magnitude of the effect is relatively small in percentage terms: about 1 percentage point. It is difficult to separate this estimated effect from statistical noise.

I report the results of the robustness checks for varying the treatment group and the control group. The baseline specification is specification (8) given in Section 4.4. It is identical to the last specification estimated at the beginning of this section, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate the

In summary, I estimate that union members

earn

6.18% more than free riders.

same baseline specification but with the treatment groups of Indiana only and Michigan only, respectively, as proposed in Section 4.5.1. This is achieved by excluding Michigan observations from the estimation in one column of my results and excluding Indiana observations from the estimation in another column of my results. I estimate the same baseline specification but with the control groups of non-RTW states and RTW states, respectively, as proposed in Section 4.5.2.

This is achieved by including non-RTW states, Indiana, and Michigan observations in the estimation in column (4) and including RTW states, Indiana, and Michigan observations in the estimation in column (5).

The results indicate that the baseline estimate of a 1.3 percentage point increase in the free rider rate is not robust to the choice of treatment group. The effect is estimated to be a 2 percentage point increase in Michigan, significant at the 5% level, and a 0.1 percentage point decrease in Indiana, not significant even at the 10% level. The baseline estimate is also only somewhat robust to the choice of control group, as the estimate decreases to a 0.8 percentage point increase when using a control group of RTW states. It should be noted that the only statistically significant estimate occurs when using a treatment group of Michigan only.

I report the results of the probit model robustness check. The OLS specification is specification (8) given in Section 4.4. It is identical to the last specifica-

tion estimated at the beginning of this section, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate specification (10), which includes the same regressors but uses a probit model instead of a linear model, as proposed in Section 4.5.3.

I give the average marginal effect of the rtw variable on the dependent variable unionfr01, as computed using the margins Stata command. This number represents the average marginal effect of the right-to-work law on the union free rider rate under the probit model.

The result of the probit model is a 1.8 percentage point increase in the free rider rate due to the RTW laws. This indicates that the baseline estimate of a 1.3 percentage point increase is somewhat robust to the choice of a linear or probit model.

I report the results of the remaining robustness checks. The baseline specification in is specification (8) given in Section 4.4. It is identical to the last specification estimated at the beginning of this section, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate the same baseline specification but with slight changes in the coding of the rtw variable, as proposed in Section 4.5.5. The rtw variable is coded to change from 0 to 1 at three alternative times: 3 months before the effective dates of the RTW laws in Indiana and Michigan, 3 months after, and 6 months after. I estimate the same baseline specification but with a larger sample size, including observations from 2002–2008 in addition to those from 2009–2015, as proposed in Section 4.5.6.

The results indicate that the baseline estimate of a 1.3 percentage point increase in the free rider rate is fairly robust to slight variations in the coding of the rtw variable (1.0– 1.7 percentage points) and to expansion of the sample size (1.1 percentage points), even though the estimates are not statistically significant.

Increasing the sample size decreased the standard error enough to render the estimate of 1.1 percentage points significant at the 10% level, but this is still not a very convincing result.

In summary, the estimated effect of RTW laws on the union free rider rate is a 1.3 percentage point increase. While the sign of this estimate is consistent with my hypothesis that RTW laws increase the free rider rate, the number is not significant even at the 10% level. The estimate is not robust to the choice of

Columbia Economics Review

treatment group, meaning that the effect of the RTW law is different for Indiana and Michigan. Interestingly, the estimate becomes significant at the 5% level when considering only Michigan: a 2 percentage point increase in the free rider rate.

The estimates are fairly robust to the other modifications, but still not significant at the 5% level.

Union Wages I report the results of estimating the baseline specifications. I estimate specifications (1), (4), (6), and (8), respectively, with each column of my results successively adding more control variables.

The results show that controlling for industry, state, and year fixed effects led to a large change in the estimate, indicating substantial omitted variable bias in the simple OLS and DID specifications.

Using the DID model with full fixed effects and demographic controls, RTW laws are estimated to increase union wages by 2.17%, using the DID model with full fixed effects and demographic controls. This result is surprising, because I expect that right-to-work laws, by diminishing the ability of labor unions to enforce membership among an employer’s workers, would decrease the bargaining power of unions and lead to decreased union wages. However, this estimate is not significant even at the 10% level. Therefore, it is difficult to separate this estimated effect from statistical noise, and my hypothesis that RTW laws decrease union wages is not disproved.

I report the results of the robustness checks for varying the treatment group and the control group. The baseline specification is specification (8) given in Section 4.4. It is identical to the last specification estimated, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate the same baseline specification but with the treatment groups of Indiana only and Michigan only, respectively, as proposed in Section 4.5.1. This is achieved by excluding Michigan observations from the estimation in one column of my results and excluding Indiana observations from the estimation in another column of my results. I estimate the same baseline specification but with the control groups of non-RTW states and RTW states, respectively, as proposed in Section 4.5.2.

This is achieved by including non-RTW states, Indiana, and Michigan observations in the estimation in one column and including RTW states, Indiana, and Michigan observations in the other col-

Fall 2016 umn.

The results indicate that the baseline estimate of a 2.17% increase in union wages is not robust to the choice of treatment group. The effect of RTW on wages is estimated to be +6.66% in Michigan, significant at the 1% level, and -5.41% in Indiana, not significant even at the 10% level. The estimates in the two states have opposite signs! Surprisingly, the result for Michigan is significant at the 1% level, although with the exact opposite result in Indiana, I am hesitant to fully accept this highly statistically significant result. The results are somewhat robust to the choice of control group (1.9–2.7%), although without statistical significance.

I report the results of the remaining robustness checks. The baseline specification is specification (8) given in Section 4.4. It is identical to the last specification estimated, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimated the same baseline specification but with a sample size of union members instead of union-covered workers, as proposed in Section 4.5.4. I estimate the same baseline specification but with slight changes in the coding of the rtw variable, as proposed in Section 4.5.5. The rtw variable is coded to change from 0 to 1 at three alternative times: 3 months before the effective dates of the RTW laws in Indiana and Michigan, 3 months after, and 6 months after. I estimate the same baseline specification but with a larger sample size, including observations from 2002–2008 in addition to those from 2009–2015, as proposed in Section 4.5.6. I estimate the same baseline specification but exclude extreme values: later, I also exclude the highest and lowest 1% of values of logwage, and also exclude the highest and lowest 5% of values of logwage.

The results indicate that the baseline estimate of a 2.17% increase in union wages is somewhat robust to all of the variations considered, with all but one estimate falling in the range 1.4–2.6%.

Changing the sample to union members instead of union-covered workers increased the estimate to 3.4%, significant at the 10% level. None of the estimates are significant at the 5% level.

In summary, the estimated effect of RTW laws on union wages is a 2.17% increase. The sign of this estimate is surprising, because it implies that a law that decreases unions’ bargaining power would increase the wages earned by its members. Nonetheless, the number is not significant even at the 10% level, so

there is insufficient evidence to reject my hypothesis that RTW laws decrease union wages. The estimate is not robust to the choice of treatment group, meaning that the effect of the RTW law is different for Indiana and Michigan. Interestingly, the estimate becomes significant at the 1% level when considering only Michigan: a 6.66% increase in union wages.

The estimates are somewhat robust to the other modifications, but still not significant at the 5% level.

Non-Union Wages I report the results of estimating the baseline specifications. I estimate specifications (1), (4), (6), and (8), respectively, with each column successively adding more control variables.

The results show that controlling for industry, state, and year fixed effects led to a large change in the estimate, indicating substantial omitted variable bias in the simple OLS and DID specifications.

Using the DID model with full fixed effects and demographic controls, RTW laws are estimated to increase non-union wages by 0.479%, using the DID model with full fixed effects and demographic controls. This result is surprising, because I expect that right-to-work laws, by diminishing the ability of labor unions to maintain membership, would decrease the threat of unionization and enable non-union employers to pay lower wages without fear of unionization.

However, this estimate is not significant even at the 10% level. Therefore, it is difficult to separate this estimated effect from statistical noise, and my hypothesis that RTW laws decrease non-union wages is not disproved.

I report the results of the robustness checks for varying the treatment group and the control group. The baseline specification in column (1) is specification (8) given in Section 4.4. It is identical to the last specification estimated , which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate the same baseline specification but with the treatment groups of Indiana only and Michigan only, respectively, as proposed in Section 4.5.1.

This is achieved by excluding Michigan observations from the estimation in one column of my results and excluding Indiana observations from another column. I also estimate the same baseline specification but with the control groups of non-RTW states and RTW states, respectively, as proposed in Section 4.5.2.

This is achieved by including non-RTW Columbia Economics Review

35 states, Indiana, and Michigan observations in one estimation and including RTW states, Indiana, and Michigan observations in the another estimation.

The results indicate that the baseline estimate of a 0.479% increase in union wages is not robust to the choice of treatment group. The effect of RTW on wages is estimated to be a 0.79% increase in Michigan and a 0.0075% increase in Indiana, not significant even at the 10% level. The result is somewhat robust to the choice of control group (0.3–0.6%), although without statistical significance.

RTW laws are

estimated to increase non-union wages by

0.479% [...] However, this estimate is not

significant even at the

10% level.

I report the results of the remaining robustness checks. The baseline specification in is specification (8) given in Section 4.4. It is identical to the last specification estimated in the first part of this section, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate the same baseline specification but with a sample size of non-union members instead of noncovered workers, as proposed in Section 4.5.4. I estimate the same baseline specification but with slight changes in the coding of the rtw variable, as proposed in Section 4.5.5. The rtw variable is coded to change from 0 to 1 at three alternative times: 3 months before the effective dates of the RTW laws in Indiana and Michigan, 3 months after, and 6 months after.

I estimate the same baseline specification but with a larger sample size, including observations from 2002–2008 in addition to those from 2009–2015, as proposed in Section 4.5.6. I estimate the same baseline specification but exclude extreme values: I also exclude the highest and lowest 1% of values of logwage, while another column of my results excludes the highest and lowest 5% of values of logwage.

The results indicate that the baseline estimate of a 0.479% increase in union wages is somewhat robust to the use of union membership instead of union coverage and to slight variations in the

36 coding of the rtw variable, with estimates falling within 0.2–0.6%, and not very robust to trimming outliers, with estimates above 0.9%. Interestingly, expansion of the sample size revises the baseline estimate of the effect of RTW laws on nonunion wages to a 2.86% decrease, which is consistent with my hypothesis, and this estimate is significant at the 1% level.

In summary, the estimated effect of RTW laws on non-union wages is a 0.479% decrease. The sign of this estimate is surprising, because it implies that a law that decreases unions’ bargaining power would increase the wages earned by its members. Nonetheless, the number is not significant even at the 10% level, so there is insufficient evidence to reject my hypothesis that RTW laws decrease union wages. The estimate is not robust to the choice of treatment group, meaning that the effect of the RTW law is different for Indiana and Michigan. The estimates are somewhat robust to the other modifications, but still not significant at the 5% level. Interestingly, the estimate changes sign when considering a larger sample size: a 2.86% decrease in non-union wages, significant at the 5% level. This may suggest that right-to-work laws do decrease non-union wages, but only over a sufficiently long time horizon.

Union Member vs. Free Rider Wages I report the results of estimating the baseline specifications. I estimate specifications (2), (5), (7), and (9), respectively, successively adding more control variables.

The results show that controlling for industry, state, and year fixed effects led to a large change in the estimate, indicating substantial omitted variable bias in the simple OLS and DID specifications. Using the DID model with full fixed effects and demographic controls, I estimate that union members earn 6.18% more than nonmembers. This estimate is significant at the 1% level. It is an interesting result, but the implications are not obvious. Because labor unions are obligated to represent all workers—not just their members—when negotiating wages with employers, one might expect that free riders would not earn less than union members because they are still covered by union contracts.

The difference present in the data may be due to other benefits only available to union members, or some omitted variable bias in my model.

I report the results of the robustness checks for varying the treatment group and the control group. The baseline

Fall 2016 specification in this table is specification (9) given in Section 4.4. It is identical to the last specification estimated, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate the same baseline specification but with the treatment groups of Indiana only and Michigan only, respectively, as proposed in Section 4.5.1. This is achieved by excluding Michigan observations from one estimation and excluding Indiana observations from another estimation. I estimate the same baseline specification but with the control groups of non-RTW states and RTW states, respectively, as proposed in Section 4.5.2.

This is achieved by including non-RTW states, Indiana, and Michigan observations in the one estimation and including RTW states, Indiana, and Michigan observations in another estimation.

The results indicate that the baseline estimate of a 6.18% premium in union member wages is very robust to the choice of treatment group and significant at the 1% level. The result is somewhat robust to the choice of control group, with the estimates falling within 4.6–8.0% and retaining significance at the 1% level.

I report the results of the remaining robustness checks. The baseline specification is specification (8) given in Section 4.4. It is identical to the last specification, which includes full fixed effects and controls, a treatment group of Indiana and Michigan, and a control group of all other states. I estimate the same baseline specification but with slight changes in the coding of the rtw variable, as proposed in Section 4.5.5. The rtw variable is coded to change from 0 to 1 at three alternative times: 3 months before the effective dates of the RTW laws in Indiana and Michigan, 3 months after, and 6 months after. I estimates the same baseline specification but with a larger sample size, including observations from 2002–2008 in addition to those from 2009–2015, as proposed in Section 4.5.6. I estimate the same baseline specification but exclude extreme values: I exclude the highest and lowest 1% of values of logwage, and later I also exclude the highest and lowest 5% of values of logwage.

The results indicate that the baseline estimate of a 6.18% premium in union member wages is robust to all of the variations considered, and all estimates retain significance at the 1% level.

In summary, I estimate that union members earn 6.18% more than free riders.

This is a finding that is significant at the Columbia Economics Review

1% level and robust to slight variations in specification. While very convincing in a statistical sense, the real-world significance of this result is less clear: how can union members earn more than free riders if both are covered by the same union contract? There may be non-contract benefits of union membership that free riders do not receive, or there may be omitted variable bias present in my model.

Conclusion This paper examines the effect of recent right-to-work laws on labor unions and wages. The literature on these effects is mixed. Using recent data on Indiana and Michigan, which passed RTW laws in 2012 and 2013, respectively, I investigate whether these RTW laws have had any conclusive effects over the past few years. I focus on several key variables: fraction of workers unionized, fraction of free riders, wages of union workers, wages of non-union workers, and wages of union members compared to wages of free riders. I use a difference-in-differences model with industry fixed effects, state fixed effects, time fixed effects, and demographic controls in order to isolate the effect of RTW laws from other factors.

It may be the case that even though RTW laws are damaging to

unions, they may have only limited marginal effect on unions that are already weak from years of decline.

The results of my analysis are mixed. I find that union members earn about 6.2% more than free riders, significant at the 1% level. In addition, the effect of RTW laws is estimated to be statistically significant in decreasing the union membership rate. However, the magnitude of the effect—0.7 percentage points overall, 1.1 percentage points in Michigan—is small, and the result disappears when the treatment group is restricted to Indiana. RTW laws are also estimated to increase the free rider rate in Michigan only, by 2.0

Fall 2016 percentage points. The estimated effects on wages are not statistically significant, and they have positive signs, which is at odds with my hypothesis that rightto-work laws decrease wages. Overall, the effect of RTW laws is found to differ between Indiana and Michigan, but the results are generally robust to slight variations in model specification.

The lack of statistical significance in many specifications is worrying for the validity of my results. Our statistically significant results may simply be a byproduct of running many regressions under different specifications; after all, on average, 5% of them will be significant at the 5% level, even with random data.

As the graphs 3â&#x20AC;&#x201C;6 suggest, there is seemingly a good deal of statistical noise and a lack of causal effect between right-towork laws and the dependent variables.

In addition, a potential problem with my results concerns possible omitted variable bias. My difference-indifferences model accounts for fixed state and time effects, but does not correct for unobserved variables that may differ both across states and across time, and are correlated with both RTW laws and the outcome variables. Nevertheless, recent changes in RTW laws probably reflect idiosyncratic factors such as the rise of the Tea Party in American politics, so they are likely exogenous to factors driving wage and unionization changes. Omitted variable bias is therefore not a very pressing concern.

My results are consistent with the uncertainty of the existing literature examining the effects of right-to-work laws on unions. Though not very exciting, this fact also reflects a harsh reality for labor unions: with the private-sector unionization rate below 10%, it may be the case that even though RTW laws are damaging to unions, they may have only limited marginal effect on unions that are already weak from years of decline. Even though many of my results lack statistical significance, a silver lining presents itself: when I consider a larger sample size, I estimate a statistically significant 2.9% decrease in non-union wages. This suggest that further analysis focusing on larger sample sizes may be fruitful in uncovering the effects of right-to-work laws on labor unions. As time passes and more data becomes available on Indiana and Michigan after the passage of their RTW laws, it may be easier to separate the effects of right-to-work laws from statistical noise. n

Columbia Economics Review

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Fall 2016

38

Take Me to Court Pharmaceutical Settlements under the Hatch-Waxman Act: Stock Price Analysis of Generic Firms Siran Jiang Columbia University

Publicly traded pharmaceutical companies have been subject to heightened scrutiny in recent years, with seemingly-monopolistic drug manufacturers charging exorbitant prices for their medications. This paper offers an alternative vantage point, highlighting the profit-driven incentive structure created by patent rights. By focusing on the Hatch-Waxman Act’s legal framework for patent disputes, this paper highlights how public policy regulates industries to prevent anticompetitive practices. The piece specifically considers the anticompetitive increases in stock prices that may result from reverse payment settlements between firms. In analyzing a specific policy’s effect on pharmaceutical companies’ monopoly power, this paper brings new considerations to a turbulent political season in which the little man always appears to be losing.

-A.W.

I.1 Background Patents incentivize innovation by giving firms a period of market exclusivity during which they can earn returns to recover the high research and development (R&D) expenditures they incurred to develop their products. Market exclusivity describes the period of time in which a firm has a monopoly over its invention. In the pharmaceutical industry, patents play an especially central role because a significant portion of costs come from R&D in laboratory work, clinical trials, and other tests to prove safety and efficacy. After a drug’s composition is determined, the actual manufacturing costs are low compared to the R&D costs. After the inventing firm – which will be referred to as the “brand” firm – develops a drug without a patent, any other company can use this formula to manufacture and sell the drugs without costly R&D expenditures. These latter firms will be referred to as “generic” firms, as they manufacture generic versions of brand firm drugs. Sales lost

by a brand name company after generic entry are between 14%-41%, which represents $157 billion worth of industry-wide sales. In addition, prices fall an average of 85% after generic entry, with generic market penetration rates of around 90%.

Immediate generic competition implies that a brand company cannot maintain

Are less-

skilled workers disproportionately and negatively impacted by increased labor market competition from less-skilled immigrants?

Columbia Economics Review

the prices and market share needed to recover high R&D costs. Patents encourage companies to continue to invest millions of dollars into R&D and continue to innovate, giving brand firms a chance to recover some R&D costs before a generic manufacturer enters. Since the regulatory framework surrounding this topic is complex, the first section will outline how patents and patent challenges work under the Hatch-Waxman Act, the current legal framework for patents.

After obtaining promising laboratory results, a drug company will attempt to run clinical trials to prove that the new drug meets Food and Drug Administration (FDA) standards. After the company discovers promising information on a drug’s safety and efficacy in initial trials, it submits a New Drug Application (NDA) to the FDA. If the FDA approves the NDA, the company has the right to market the drug to the public, and to apply for a patent separately at the U.S. Patent and Trademark Office (USPTO). A patent is a

Fall 2016

investigating the labor market effects of immigration begs the question of how one should define the labor markets to be analyzed.

property right issued by the USPTO to an inventor to “exclude others from making, using, offering for sale, or selling the invention throughout the United States or importing the invention into the United States” for a set period of time. Generally, patents are granted for 20 years from the date on which the application was filed.

After the patent is approved, it is placed on the FDA’s Approved Drug Products with Therapeutic Equivalence Evaluations, or the “Orange Book”, which is a listing of drug products approved by the FDA on the basis of safety and efficacy and current standing patents.

A patent usually includes the specification of a certain compound, or pharmaceutical composition, in addition to a method of how to use the compound in the treatment or prevention of a disease.

A patent can be as broad as to protect the entire compound and its use in any way or as narrow as to protect only a small modification to an existing drug. For example, a company could patent an extendedrelease version of an existing compound or combine two successful compounds to market as a new drug, and the patent would only protect these modifications rather than the actual compound itself.

For racemate drugs that are compounds with multiple enantiomers (mirror-image molecules with the same chemical composition), companies often change the enantiomer and alter the chemical compound slightly, and some patents would only protect this new enantiomer modification. Companies can also patent new uses of existing compounds and market them as different drugs. The patent protection strength is a combination of the patent length and breadth of protection.4 Both of these components are included in the patent application that the company fills out, but ultimately determined by the

USPTO at the time of patent issuance.

An important aspect of USPTO patents is that the drug is not put under intense scrutiny before the patent is granted. The USPTO simply does not have enough resources to ensure that each patent granted has the length and strength that accurately reflects the novelty of the drug it protects. Therefore, patent litigation serves to discover and establish the optimal length of a patent. When a patent is challenged, the decision that results and the entry date that prevails should reflect the optimal amount of patent protection that balances incentives for innovation with the costs of temporary monopoly.

The importance of patent litigation can be seen in a Federal Trade Commission (FTC) study from 2002, where 73% of all patent cases that went to trial were won by the generic company. This statistic indicates that a larger number of patents issued by USPTO were given a stronger protective power than they should have been given, based on how beneficial the patented drug is to society. While settlements without payments may allow firms to reach a decision that would have been reached in court without costly litigation,5 they distort this optimality discovering process.

I.2 Intuitional Framework of the Hatch-Waxman Act The Drug Price Competition and Patent Term Restoration Act of 1984, known as the Hatch-Waxman Act (H-W), sets incentives for both brand and generic drug companies to obtain and challenge patents in the pharmaceutical industry.

Among many other policies, H-W outlines a cheaper and faster process for generic companies to enter the market, encouraging generic competition. This accelerated process begins with the generic filing an Abbreviated New Drug Application (ANDA) on a patented drug to the FDA. An ANDA allows a generic firm to utilize trials and data already compiled by the brand firm as long as they prove bioequivalence.6 It is much less costly to develop a new drug through an ANDA than an NDA, as the brand firm has already paid for the vast majority of R&D expenses when they file their NDA. However, for brand drugs that are patented, an ANDA is by definition an act of patent infringement. H-W specifies four special procedures to address ANDA-related patent disputes. Generic firms must prove one of the following about the patent that their ANDA may violate: (I) The patent has already expired (II) The patent has not yet been filed Columbia Economics Review

39 (III) The generic won’t market their drug until the patent expires (IV) The existing patent is invalid or not infringed In the last clause, proving a patent is “invalid” requires demonstrating that the patent should have never been issued in the first place because the invention is nonunique. Proving that a patent is “not infringed” by the ANDA generic drug involves demonstrating that the generic drug in question does not fall in the scope of exclusion specified by the patent.

Proving that a patent is either invalid or is not infringed allows the generic firm to enter the market immediately after the litigation is won. The last clause is called a Paragraph IV certification of the ANDA filing and usually results in patent litigation. This paper will primarily focus on these Paragraph IV patent disputes.

Drugs approved by the FDA are the

if migratory patterns attenuate the

estimate, then the

estimate should be larger in magnitude in larger geographic areas only products in which a competitor must resolve conflicting patent claims before entering the market. Therefore, after the Paragraph IV ANDA is filed, if the brand firm sues within 45 days, the FDA must wait until the earliest of the following three events before approving the generic firm’s ANDA: (1) The generic wins the patent trial in court by proving that the patent is invalid or that their generic drug does not infringe upon it (2) 30 months pass and no court decision has yet been made (3) The patent expires If (2) occurs and the FDA approves the ANDA without a court decision, then the generic may market their drug as “at risk,” which requires that they pay damages to the brand firm if a court eventually finds the patent valid or infringed by the generic drug. If the brand firm does not sue within 45 days, the FDA can approve the ANDA at any time, but the generic filer will be responsible for the costs of damages if the brand firm even-

40 tually sues and the patent is found valid or infringed by the generic drug. By the end of 2009, 55% of all approved brand name drugs (299 out of 692 total drugs) had Paragraph IV challenges, an increase from around 20% in 1984 when H-W was first passed.7 Paragraph IV ANDAs have become a central way in which generic firms raise patent challenges in the pharmaceutical industry.

As with any litigation, the parties can opt to “settle” on an agreed entry date before the actual hearing itself. This saves both the brand and generic firms costly litigation fees. However, in many ANDA Paragraph IV cases beginning in the 1990s, the brand firm made a payment to the generic firm as a stipulation of their settlements. These were deemed “reverse payments,” as the party suing pays the party being sued. These reverse payments have been accused by the FTC of being collusive, since the brand firm “pays for the delay” of the generic firm.

Reverse payment settlements could involve a cash payment, but more often involve some sort of business side deal.

These non-cash side deals fall into a number of categories: (1) Noncash business side deals: includes licenses from the brand firm to the generic to market/produce other drugs, supply of certain drugs to the generic firm, etc.

(2) No-AG clauses: authorized generics (AG) are the brand firm’s own generic version of their drug. The brand firm may market their AG or partner with a generic manufacturer to do so. AG’s are allowed during an ANDA filer’s 180-day exclusivity period, so agreeing not to market an AG sacrifices brand firm profits.

(3) Retained exclusivity: a third type of non-monetary “pay for delay” settlement that may not involve direct monetary payment, but involves the brand firm allowing the generic to maintain the 180-day exclusivity period by agreeing to drop the patent fight at a later date.

The generic first filer thus has a higher probability–essentially a sure chance–of receiving 180 days of exclusivity than if they go to court.

In a study conducted by Hemphill (2009), out of a dataset of 101 drugs with settlements, 51 (50%) drugs had settlements with payments and 48 (47%) had settlements without payments.8 Out of the 51 drugs with payments: five were cash (~10%), 16 involved side deals (~30%), and 25 only had the retained exclusivity agreement (~50%).9 Of the cash and side deal monetary payments, most generics were also guaranteed retained exclusivity as part of the settlement. Most

Fall 2016 deals in recent years involve complex side deal or retained exclusivity agreements.

These deals are difficult to estimate in value and therefore add more difficulty when litigating antitrust consequences of reverse payment settlements.

It is important to examine these reverse payment settlements and question whether or not they have anticompetitive effects through collusive entry deterrence. If weak patents were prolonged because the brand is paying the generic to stay out, these settlements would be extremely costly to consumers who must pay higher brand name prices for a longer period of time. Using a weighted average based on drug sales, the FTC (2010) estimates that settlements with payments have entry dates that are 17 months later than settlements without payments. They further project that these 17 months account for an additional $20 billion in sales of brand drugs. These massive welfare consequences make it crucial to examine these settlements in detail to examine their effect on innovation and competition.

terms between the brand and generic firms and serve as a proxy for the expected patent length from a trial (2) A positive abnormal stock return indicates that an anticompetitive settlement has taken place DSM’s results show that settlements with payments have a positive abnormal stock return while settlements without payments do not, which is constituent with the two assumptions that they make.

In addition, DSM find a significant difference between abnormal stock returns for payment and non-payment settlements in all event windows. From these results and the two assumptions above, DSM conclude that settlements with payments

II. Questions My paper builds upon empirical studies conducted by DSM by using stock price movements of generic firms to determine the presence of anticompetitive activities in reverse payment settlements.

My research is guided by three questions: I. Are there positive abnormal stock returns of generic firms in settlements with payments and settlements without payments from 1993 to 2015? Do these results suggest that the settlements are anticompetitive?

II. Do other factors in addition to indications of payments influence abnormal returns during settlements? Other factors that I investigate include the reputation of the generic firm characterized by how frequent they settle; the drug’s sales as a percentage of firm revenue III. How do the stock returns of generic firms differ from brand firms during settlements? How do these differences describe the anticompetitive and possibly collusive nature of reverse payment settlements?

Question I poses a similar question that DSM set out to answer for the brand firm in their 2013 study: whether there is a stock price jump in response to the settlement announcement in the news and whether this jump shows that the settlement is anticompetitive. DSM make two underlying assumptions in their study: (1) Settlements without payments are not anticompetitive because they represent a fair negotiation of the settlement

in a particular

Columbia Economics Review

a key dispute in the literature is whether one should define a labor market as a group of workers geographic area—say, a statistical area, or

a state—who compete

locally, or as a group of workers with

similar levels of skill and experience who

compete nationally. are anticompetitive while settlements without payments are not.

My initial hypothesis for Question I is that the generic firms’ stock returns will behave in a similar way, with positive abnormal returns for settlements with payments that are significantly different from no payment settlement stock returns in all windows. However, since my study explores generic settlements, I believe that assumption (1) no longer holds and will therefore answer Question I keeping assumption (2), but proposing a different interpretation of settlements without payments as assumption (1). This interpretation is based on the EHHS model.

Question II attempts to find different factors that influence stock price jumps at the time of settlement besides the announcement of a payment. This ques-

Fall 2016 tion originates from the recent string of settlements that involve complex side deals instead of simple transfers of cash.

This trend likely materialized as a result of close FTC antitrust scrutiny of cash payments. They may serve as a way to obscure large payments through complicated settlement terms. While most courts post-Actavis have treated side deals like cash payments,18 these deals add another layer of complexity to the Actavis Inference because courts have to value deals that may be worth different amounts depending on the business structure of the company involved. In addition, many deals in the last few years are announced as “confidential” instead of specifying payments or no payments. For a public company, the terms of the settlement constitute as material information that could significantly move the stock price but are obscured from shareholder knowledge. In light of these trends that add more layers of opacity to settlements, it is important to search for alternative means to gauge anticompetitive activity when payment and no payment terms and classifications are unclear.

A second component of Question II relates to investor conceptions of different types of deals. While this may involve using larger event windows, it would be interesting to evaluate whether there are certain settlements that the market takes longer to understand. As settlement terms get more and more complex, perhaps investors themselves do not truly understand the full effects of some deals right away. This would add valuable discussion to the methodology of short event study windows to determine whether there are anticompetitive effects of reverse payment settlements. I attempt to answer this by comparing the differences between stock returns on the event date and days after the event date to see if there’s a delay in responding to the settlement announcement.

To answer Question III, I compare my results qualitatively with DSM’s results for the brand firm. While there is current-

if migration rapidly equalizes wages

between areas, how does one explain

persistent inter-area wage variation?

41

Figure 1. Frequencies of Firm in Settlement Data ly no literature about the generic firm’s stock returns after reverse payment settlements, my initial hypothesis is that generic stock prices should also jump at news of settlement. If both the brand and generic stock prices jump at the news of a settlement with payment, it would further reinforce the collusive nature of these reverse payment settlements – they benefit both brand and generic firms at the cost of consumers. However, if the generic stocks do not jump when the brand stocks do for settlements with payments, it would mean that either: Settlements do not produce higher future profits for generic firms and therefore the benefits of settlements are asymmetrically distributed to brand firms.

Expectations of the settlements are better built into the generic’s stock prices prior to the settlement announcements.

Conversely, if stock returns of generic firms jump while brand firms do not in the case of settlements without payments, it may provide a different interpretation of how settlements without payments work for the generic firm than the brand firm. All three cases of empirical results provide insight for the interactions between the generic and brand firm during patent settlement and help add to the discussion of antitrust issues within reverse payment settlements. In analyzing stock prices, I attempt to examine which of the previous three causes produced the stock price jumps.

III. Data – Sample Categorization In Question I, I investigate whether settlements with payments and settlements without payments lead to positive abnormal stock returns by separating my data into “Payments” and “No Payments.”

However, in order to answer Question II and examine whether firm reputation or drug sales percentage plays a role in abnormal returns, I separated my data Columbia Economics Review

Figure 2. Subcategories and number of samples (N) in each group again into settlements by “frequent settlers” and “infrequent settlers” – referred to in this paper simply by “Frequent” and “Infrequent.” I define a “frequent settler” as a firm that settles more than 10% of all the settlements in the total sample. Firms in the Frequent group are Teva (TEVA), Actavis/Watson Pharmaceuticals (ACT/ WPI), Mylan (MYL), and Barr Laboratories (BRL). They collectively settle 54 out of 81 settlements, which constitutes around 66.67% of the data. Firms in the Infrequent group are Perrigo (PRGO), Impax Laboratores (IPXL), Novartis (NVS), Par Pharmaceuticals (PRX), Reddy Laboratories (RDY), GeoPharma (GORX), Merck (MRK), and Spectrum Pharmaceuticals (SPPI). The Infrequent group collectively settle 27 out of 81 settlements, or about a third of all settlements in the data set. Figure 1 displays the frequencies at which each firm settles within the entire data set (above).

While I could merely include dummy variables of “Payment/No Payment” and “Frequent/Infrequent Settler” in my regression of abnormal returns onto sales % to answer the second part of Question II, I decided to separate the data into four different groups to allow for interaction between the dummies (Payment/No Payment and Frequent/Infrequent Settler) and the continuous variable (Sales %). The following diagram represents the

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Immigrants may

also be attracted to areas with particular industry compositions breakdown of the four subcategories of my data: IV. Event Study Methodology Event studies examine the impact of an event on a company’s stock price to gauge whether the event had a significant effect on the company. All event studies assume that the stock market responds quickly to news of an event bearing on the expected profits of a firm. Changes in stock prices are expressed as stock returns, which is essentially defined as the percentage change of the stock price from the previous day. To obtain daily stock return data, I extracted the adjusted stock returns from the Center for Research in Security Prices (CRSP) database through the Wharton Research Data Services (WRDS). I imported the data into SAS with Eventus software to sort the data and calculate my performance variables based on different expected returns models. I will also use Eventus to conduct my hypothesis tests for Question I and I use base SAS without Eventus to conduct regressions for Question II. CRSP defines a stock return as the change in the total value of an investment in a security over some period of time per dollar of initial investment, calculated as:

[3]

pt = price of security i at time t, pt-1 = price of security i at time t-1, dt = dividend of security i at time t, ft = factor to adjust prices of security i based on any stock splits that may have occurred Abnormal returns in an event study are calculated as the difference between the actual daily stock return on a given day in the event window and the expected stock return on that day:

ARit = rit - E(rit)

[4]

where i is a given security and t is a given day in the event window. In my paper, the event date occurs on date t=0 when the settlement is first announced in the news, while negative values of t indicate days before the event date and positive

values of t indicate days after the event date. For example, t=-3 is the date that is three days before the event date.

Abnormal returns are often aggregated into “Cumulative Abnormal Returns” across “event windows”, which define the days across which the market is assumed to be responding to news of the event. It often takes multiple days to adequately capture the effects of an event because of differences in announcement time of day, news leakage, and imperfect news dissemination. To capture effects before and after the event date, I consider symmetric and asymmetric windows that begin (and end) one, two, and three day(s) before (and after) the event. For example, an event window (-3,0) represents the three-day period from t=-3 to t=0. My event windows are: (0,0), (-3,3), (-2,2), (-1,1), (-3,0),(-2,0),(-1,0), (0,1), (0,2), and (0,3). My windows are also intentionally similar to DSM’s windows in order to evaluate any differences between the generic and brand firm stock movements when answering Question III. While the abnormal return itself is calculated during the event windows, the expected stock return is calculated by inputting a market-wide return observation for date t into a model with coefficients that are estimated during the estimation period. These coefficients are estimated using the Ordinary Least Squares (OLS) method and the estimation period is typically the 120 days ending 30 days before the event date, t=0.

There are a number of different approaches used to estimate E(rit) with different estimation windows. I use the estimation window of 120-day period ending 30 days prior to the start of my event date. In this paper, date tE denotes a date in the estimation period while date t denotes a date in the event window(s).

My first model and the main model used in most event studies literature is the Market Model, in which OLS is used to estimate the coefficients of the regression of a security’s return on the market index return during the estimation period. These coefficient estimates are then used to calculate the expected return estimate E(rit) during the event window. I used the CRSP Equally Weighted index as my market index, which weights all stocks on the CRSP database equally, because it is a common index used in event studies and has been proven to be as effective as other popular market indices.

The Market Model describes the expected return of security i on date t as a function of the market index return on date t:

Columbia Economics Review

E(rit) = αˆ + βˆrmt

[5]

Where rmt is the daily market return for date t and αˆ and βˆ are the OLS estimates of the actual coefficients α and β, calculated over the estimation period. αˆ and βˆ from equation [5] are calculated by regressing ritEon the market index rmtEfor the 120 observations collected from the estimation window, tE1=-149 to tE2=-30:

rit = α+ βrmt +εit E

E

[6]

E

MacKinlay (1997) states that usually, adding additional factors to the market model does not increase the R2 and thus the explanatory power of the model. Brown and Warner (1985) have also stated the Market Model is well specified for an event study and under most conditions, relatively powerful in rejecting the null hypothesis that abnormal returns are equal to zero when abnormal returns are actually present. However, I add another popular event study model as a robustness check to the Market Model.

The Fama-French Model (Fama and French 1996) is the second expected returns model used, and adds two additional factors to the Market Model: the difference in returns between big-cap and small-cap stocks on date t and the difference between stocks with high and low book-to-market ratio on date t. The expected return from the Fama-French Model for security i on date t is calculated as:

E(rit)=αˆ+βˆi1rmt+βˆi2smbt+βˆi3hmlt [7] where rmt is the market return, using the CRSP Equally Weighted Index on day t and smbt (“small minus big”) is the difference in returns between big-cap and small-cap stocks on date t.hmlt (“high minus low”) is the difference between the returns of high book-to-market value stocks and low book-to-market value stocks on date t. Similar to the market model, coefficients αˆ, βˆi1, βˆi2, anβˆi3d are the OLS estimates of the coefficients in [8] below, calculated over the estimation period by regressing the stock return for firm i on date tE on the factors rmtE, smbtE, and hmltE on date tE:

rit = α + βi1rmt +βˆi2smbt +βˆi3hmlt + εit E

E

E

E

E

[8] The Fama-French model takes into ac-

Fall 2016 count the empirical observation that small-cap stocks and large book-to-market ratio (or “undervalued,” see footnote 27) stocks on average have a higher return than the market. In Buchheim et al.’s study, the R2 went up by nearly 25% when they used the Fama-French model instead of the Market Model. It is included as a robustness check to ensure that my results do not depend on the expected returns model used.

I provide the values of the OLS estimates for coefficients of factors in the Market Model and Fama-French Model for different subsets of the data and the R2 of both models. It also includes the mean squared error term. The FamaFrench model increases the R2 for every sample and subsample by an average of 0.0328, so I will include it as a robustness check for my abnormal returns calculations in my event studies. Since I separate my data into two samples “Payment” and “No Payment” and four subsamples “Payment – Frequent,” “Payment – Infrequent,” “No Payment – Frequent,” and “No Payment – Infrequent,” I also separate data into these six samples/subsamples when estimating the coefficients used to calculate E(rit).

IV.2 Event Study Methodology – Calculating Performance Variables After calculating the abnormal returns for each date t={-3,-2,-1,0,1,2,3} in the event windows from both the Market Model and Fama-French Model, I calculate three descriptive variables from these abnormal returns: (1) Average Abnormal Returns (AARt) (2) Cumulative Average Abnormal Returns (CAARt2-t1) and (3) Cumulative Abnormal Returns (CARi,t2t1). These will be referred to as “performance variables” throughout my paper.

Usage of these three variables is common in event studies (see Brown and Warner 1985, MacKinlay 1997, and Buchheim et al. 2001) because they take into account the change in stock returns of a given sample both across securities in the sample and across days of the event window.

The average abnormal returns (AARt) are the average daily returns of all stocks in a sample on date t in the event window. This is commonly called a cross-sectional return calculation in event study literature:

[11] where N is the number of securities in each given sample and ARit is the return of stock i on day t. The AARt is used to

43

calculate the Cumulative Average Abnormal Returns (CAARt2-t1) by summing the AARt’s across different event windows when they are more than one day long.

This allows us to capture the cross-sectional effects over the entire window:

[12]

where t1 to t2 represents event window (t1,t2) and AARt is the average abnormal return across securities in a sample on date t, as defined above. To answer Question I and determine if there is an abnormal return across days of the event window as a result of the settlement announcement, I test whether or not CAARt2-t1 is significantly greater than zero in different event windows. If there was no stock price jump as a result of the settlement announcement in a sample, then the performance variables AARt and CAARt2-t1 for the sample should equal zero. The Cumulative Abnormal Returns (CARi,t2-t1) are the daily returns of stock i summed over the event window:

[13]

where t1 to t2 represents event window (t1,t2) and ARit is the return of stock i on day t, as defined above. To answer the second part of Question II regarding the effect of drug sales percentage on abnormal returns, I regress CARi,t2-t1 onto each settlement’s drug sales percentage of generic firm annual sales.

V. Hypothesis Testing – t-test To answer Question I, I test whether or not the performance variable, CAARt2-t1, for each window (t1,t2) for each sample is significantly different from zero. I will use three parametric tests (t-test, Patell test, and BMP test) and two non-parametric tests (sign test and rank test) as a robustness to check to ensure that the significance of my results does not depend on the statistical test I choose. It is important to remember that parametric tests assume that the distribution stock returns rit and therefore ARit (ARit = rit - E(rit)) are independent and identically distributed (i.i.d.) random variables.

The first set of null and alternative hypotheses that I test relate to the variable CAARt2-t1, the cumulative average abnormal returns of all securities across my event windows: H0: CAARt2-t1 = 0 [14] H1: CAARt2-t1 > 0 Columbia Economics Review

Since CAARt2-t1 is constructed by summing AARt across event window(s) (t1,t2), as described in [12], I use the mean, variance, and distribution assumptions of AARt to construct the test statistics regarding CAARt2-t1. In Brown and Warner’s simulation (1985) of 250 samples with 50 securities in each sample, the abnormal returns for individual securities did not resemble a normal distribution, with a higher skewness and kurtosis than typically seen under normality. However, taking the sample means of the 250 samples, Brown and Warner (1985) found that “departures from normality are less pronounced for cross-sectional mean excess returns than for individual security excess returns, as would be expected under the Central Limit Theorem (CLT).”

The CLT states that if sample observations are i.i.d. with finite mean and variance, then the distribution of the sample mean converges to a normal distribution no matter what the underlying distribution of the data is, as long as the sample size is large enough. Therefore, the above H0 tests whether or not the sample mean across a window – the average abnormal return across all securities in a sample – is equal to zero and can be tested using typical t-test/z-tests as with any normal distribution. Assuming all of my sample sizes are large enough, the CLT allows us to assume that the distribution of CAARt2t1 follows a normal distribution, N(0, σ2(CAARt2-t2).

To construct the variance of cumulative average returns across window (t1,t2), σ2(CAARt2-t2)., I first construct the variance of AARt on date t. Since AARt is the cross-sectional mean of ARit, assuming that rit and therefore ARit is i.i.d. for large samples, the variance of AARt can be written as:

[15]

The actual variance σ2(ARit) can be approximated with the sample variance of ARit on date tE during the estimation period: SARitE2. The variance of AARt can therefore be estimated as:

[16]

where N is the number of observations in the sample and SARitE2 is the variance of the sample of stock returns over the estimation period. I acknowledge that there may

Fall 2016

44 be some additional variance in addition to the term above due to the sampling error of my E(rit) model and estimating coefficients, but if the estimation period is large enough, the sampling error should approach zero and can be ignored in the calculation of the test statistic (MacKinlay 1997). It is also possible to calculate the variance of AARt directly with the standard error of AARt observations over the estimation period. To calculate the standard deviation of the sample mean:

the sum of σ (AARt)across the event window (t1,t2), assuming that the ARit’s, and therefore AARt’s, are i.i.d: 2

[18]

The standard deviation of CAARt2-t1 can be written as (using the equation for σ(AARt) from above):

[17] where, , which is the average per-day abnormal return during the estimation period (average across all securities in a sample and average across all days of the estimation period) and SARitE is the average per-day standard deviation of the sample during the estimation period. This method calculates the variance of AARt based on its daily standard deviation from the mean of AARt across all days of the estimation period, using this standard error as a proxy for the true standard of the AARt distribution.

Buchheim et al. calls this the “time series method” of calculating variance.

Since CAARt2-t1 is the sum of the AARt terms across the days of the event window, the variance of CAARt2-t1 equals

counting for correlation between securities and cross-sectional dependence by using the averages of abnormal returns across all securities in a sample.

In addition, to test whether or not there is a significant difference in the CAARt2-t1 observations between two different samples, the second set of null and alternative hypothesis can be written as:

H0:CAARt2-t1,Sample 1–CAARt2-t1, Sample 2 =0 H1: CAARt2-t1,Sample 1–CAARt2-t1, Sample 2 > 0 [21] Assuming that the two samples are not correlated, the standard error of the difference of CAARt2-t1 between the two samples can be calculated as: σ(CAARt2-t1,Sample 1– CAARt2-t1, Sample 2) =S(CAARt2-t1,Sample1–CAARt2-t1,Sample 2)

[19] where (tE2-tE1+1) is the number of days in estimation window (tE1,tE2). I can write test statistic to test the null hypothesis regarding CAARt2-t1 in [14] as:

[20] This test is called the “Crude Dependence Adjustment” by Brown and Warner (1980) because it averages the abnormal return of all securities in a sample for a given day t, testing AARt, and thus ac-

[22]

where σ2(CAARt2-t1) for each sample is calculated in the same way as in [18] and [19]. The test statistic to test the difference in CAARt2-t1 between samples can be written as:

[23] Finally, to answer Question II regarding whether or not the drug sales percentage of annual firm sales at the time of settlement is significant on the abnormal returns after the announcement of a settlement, I regress the CARi,t2-t1 observations onto the drug sales percentage for each settlement:

CARi,t2-t1=β0+β1(Salest)+εi [24] Where Salest is equal to the percentage of the firm’s annual sales that the drug’s annual sales make up:

[25] OLS estimators, β0 and β1, are used to estimate the true coefficients, β0 and β1: The null and alternative hypotheses regarding whether the estimated coefficient of sales, β2, is significantly different from zero are: H0: β2 = 0 [26] H 1: β 2 > 0 The test statistic to test the hypotheses above can be written as:

[27]

Columbia Economics Review

Fall 2016 Where SE(β2) can be calculated as: [28]

VI.1 Results – Payment Group and Asymmetric Timing This section presents test statistics for the hypotheses described above. In addition to t-tests/z-tests, two other parametric tests, the Patell Test and BMP Test, and two non-parametric tests, the Sign Test and Rank Test, are included. Each test has certain advantages over the t-test and is included as a robustness check for the significance of the data.

I report the CAARt2-t1 values for the Payment group for all event windows, the standard error, and the test statistics/ p-values for all three parametric and two non-parametric hypothesis tests. The test statistics correspond to the null and alternative hypotheses from [14] adopted for the Payments sample: H0: CAARt2-t1, Payments = 0 H1: CAARt2-t1, Payments > 0

[29]

For every event window, the CAARt2-t1 is significantly different from zero to at least the 10% significance level for both the Market Model and the Fama-French Model. I can therefore reject the null from [14] and conclude that there is a significant stock price hike for settlements with payments. This is consistent with my initial hypothesis that settlements with a reverse payment are anticompetitive because the payment distorts the normal negotiation of the entry date.

However, a puzzling trend in my Payments sample is that the magnitude of the CAARt2-t1 values for windows (-3,0), (-2,0), and (-1,0) appear to be higher than the CAARt2-t1 values for windows (0,1), (0,2), and (0,3). On average between the Market Model and Fama-French Models, there is a 0.92% higher return in the window (-3,0) than the window (0,3), 0.49% higher return in (-2,0) than (0,2), and 0.33% higher return in (-1,0) than (1,0).

A difference in magnitude between preevent and post-event abnormal returns implies market anticipation prior to the announcement at t=0, as higher abnormal returns are appearing before the settlement is announced.

I display the differences between CAARt2-t1 observations for pre-event and post-event windows. For example, “3 days pre- / post-event” is the difference in CAARt2-t1 between the windows (-3,0) and (0,3). In order to formally statistically

test the differences between pre-event and post-event windows, I would not be able to use the standard error calculations from [22] because I cannot assume that the correlation between pre-event returns and post-event returns for the same sample of securities is zero. Therefore, to test whether the difference between pre- and post-event CAARt2-t1’s are significantly different from zero, the σ(CAARt2-t1, Sample 1 – CAARt2-t1, Sample 2) from the test statistic in [23] would have to be calculated as: σ(CAARt2-t1, pre-event – CAARt2-t1, post-event)= σ2(CAARt2-t1, pre-event)+σ2(CAARt2-t1, post-event) 2cov( CAARt2-t1, pre-event,CAARt2-t1, post-event) [30] To construct a test statistic for the difference between pre-and post-event CAAR’s, I would need an estimate for the covariance in [25] that is very difficult to mathematically write out. However, the magnitudes between pre- and post-event windows are noticeably different up to 0.94% for the 3 days pre-/post-event windows.

If the share of lowskilled immigrants

1 percentage point, lowskilled immigrants’ increases by

wages fall by about

0.15 percent, while low-skilled natives’ wages increase by

about

0.23 percent.

The asymmetric timing of abnormal returns can also be seen in the difference between the Payments and No Payments groups. I display the difference between the CAARt2-t1, Payments and CAARt2-t1, No Payments and test statistics to test the null hypothesis that the difference is equal to zero: H0:CAARt2-t1,Payments–CAARt2-t1,No Payments= 0 H1:CAARt2-t1, Payments–CAARt2-t1, No Payments > 0 [31] The difference between the Payments and No Payments sample is significant only in the windows prior to the event date, (-3,0), (-2,0), and (-1,0). These results Columbia Economics Review

45 suggest that the effect of a payment on the stock returns surrounding a settlement announcement is only significant prior to the actual settlement announcement date.

This result is unexpected, because if Payments had a positive impact on CAARt2-t1, it should be distributed through all event windows – a result that DSM found for the brand firm. Therefore, it seems that there is another factor that must be influencing investors’ reactions to the settlements before the terms are announced.

Reputation could be another factor influencing positive pre-event date abnormal returns surrounding settlements.

One main difference between brand firms and generic firms involved in Paragraph IV settlements is the frequency at which the firms settle: over 50 brand firms settled the 81 settlements but only 12 generic firms settled the 81 settlements in total.

This difference is significant in terms of the behavior of stock returns, because an important factor for how the stock market responds to a settlement is the reputation of the firm in terms of its propensity to settle. The Frequent and Infrequent characteristic of each settling firm serves as a proxy for this reputation/propensity to settle. I selected the firms that each settle more than 10% of the total dataset. Frequent settlers are TEVA, ACT/WPI, MYL, and BRL, which collectively settle 54 out of 81 settlements. I separated my dataset into four subgroups, Payments/Frequent (N=27), Payments/Infrequent (N=6), No Payments/Frequent (N=27), and No Payments/Infrequent (N=21), and repeated the calculations from the Event Study Methodology section for each subsample.

I then tested the same hypotheses in [14] to see if the CAARt2-t1 observations for each sample are significantly different from zero.

I show the CAARt2-t1 observations for settlements with and without payments settled by frequent settlers. The test statistics and p-values correspond to the null and alternative hypotheses from [14] for the samples Payment/Frequent settlers and No Payment/Frequent settlers.

I also include test statistics for the five different hypothesis tests that I use. The results suggest that I can reject the null that CAARt2-t1, Payments/Frequent = 0 in the Payments sample with frequent settlers for all windows. The results seem to mirror the results for the Payments sample as a whole, with CAARt2-t1 observations that are slightly higher in magnitude. I show some significant returns (-2,2), (-3,3), and (-1,1), at different levels of significant depending on whether the Market Model or Fama-French Model was used. These significant returns seem to be driven by

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returns in the windows, (0,1) and (0,2), after the event date. While settlements with payments settled by frequent settlers seem to generate very high abnormal returns in every window, settlements without payments seem to generate abnormal returns only in the windows following the event.

To examine whether the effect of Payments were similar for settlements settled by frequent settlers and settlements settled by infrequent settles, I tested whether the difference between Payment and No Payment is significant conditional on Frequent or Infrequent. Beginning with the frequent settlers, I tested the difference between CAARt2-t1, Payment/Frequent and CAARt2-t1, No Payment/Frequent:

I conducted a similar series of hypothesis tests to determine whether there is a significantly positive CAARt2-t1 in any of the event windows. The null and alternative hypotheses format again follows [14], and I specifically test:

H0: CAARt2-t1, Payments/Frequent – CAARt2-t1, No Payments/Frequent = 0 H1: CAARt2-t1, Payments/Frequent – CAARt2-t1, No Payments/Frequent > 0 [32] I can reject the null hypothesis in [32] for windows (-3,3), (-2,2), (-1,1), (-3,0), (-2,0), (-1,0) and (0,1). It seems that the abnormal returns in the former three windows are driven by the latter four.

Therefore, the effect of Payments within the Frequent group is significantly positive in the windows pre-event date. To check if this effect is present within the Infrequent group, I conducted a similar series of tests as in equations [14] and [21] to check if CAARt2-t1, Payments/Infrequent, CAARt2t1, No Payments/Infrequent, and the difference between them were statistically significant.

While there were some positive returns in windows (0,0) of the No Payments/Infrequent group (which will be discussed later in this section), there weren’t any positive returns in the Payments/Infrequent group. There were no statistically significant differences between Payments and No Payments settlements when settled by infrequent settlers, suggesting that both the effect of having a payment and the pre-event date timing of this effect are driven by settlements by the frequent settlers rather than the infrequent ones. Therefore, it seems that reputation of having a higher propensity to settle – tested by the variable, Frequent – influences (i) the positive abnormal returns of settlements with indications of payments and (ii) the asymmetric timing of abnormal returns occurring prior to the event date 0.

that inter-area wage

H0: CAARt2-t1, No Payments = 0 H1: CAARt2-t1, No Payments > 0

[33]

I use the same five hypothesis tests for both the Market Model and Fama-French

we find some evidence that is inconsistent with the hypothesis

differences are quickly arbitraged away by native migration Model abnormal returns. After conducting the event study and hypothesis tests, I determined that I can reject the null hypothesis that CAARt2-t1, No Payments = 0 for every window except the event date itself, (0,0), and (0,1). While I can reject the null hypothesis for window (0,1) using every statistical test for both the Market Model and Fama-French Model, I can only reject the null hypothesis for (0,0) using the t-test for both E(rit) models. This result suggests that there may be some abnormal stock return effect due to the event, because the windows (0,0) and (0,1) are the closest windows to the settlement announcement and capture any immediate positive returns due to trading. This is an unexpected result, because I did not expect settlements without payments to generate any positive stock price jumps.

In contrast, DSM’s event studies do not show any significant positive return in

Section VI.2 Results – Positive Returns in No Payment Group: For the sample of 48 settlements without an indication of reverse payment, Columbia Economics Review

brand firm’s stock for any windows following the announcement of a settlement without payment. They therefore concluded that settlements without payments are not anticompetitive, because investors don’t respond in a way that suggests belief of higher-than-expected profits. In addition, DSM assumes that settlements without payments are not anticompetitive because they represent the same negotiation that would occur inside a courtroom, without the distortion of a reverse payment.

However, I want to further investigate the assumption that settlements without payments are not anticompetitive. However, using the EHHS theoretical framework in Activating Actavis and The Actavis Inference: Theory and Practice, I work out the threshold of entry date E at which the generic is willing to settle.

Brand Firm (A) will settle if the following holds true (from Activating Actavis):

EMA+(T-E)DA-X>T[PMA+(1-P)DA]-CA [34] Simplifying Equation [34], we get the same equation as [1] from the Literature Review section:

[35]

Generic Firm (B) will settle if the following holds true:

(T-E)DB+X>T[(1-P)DB]- CB [36] Simplifying Equation [36], Equation [37] represents the maximum E at which the generic firm is willing to settle:

[37]

where (using the same definitions as EHHS in Activating Actavis): P = Probability that brand firm A will win litigation, T = Remaining patent lifetime, PT = Expected patent length that would

Fall 2016 prevail in court, E = Settlement Entry Date, MA = Monopoly profits for Firm A , DA = Duopoly profits for Firm A, DB = Duopoly profits for Firm B, CA/B = Litigation Costs for Firm A/B, X = Settlement payment size The left sides of equations [34] and [36] above represent the expected firm profits under a settlement with entry date, E. The right sides of the equations represent the expected firm profits under litigation.

The brand (Firm A) and generic (Firm B) will both opt for a settlement if the expected profits of a settlement exceeds the expected profits of litigation. The resulting E values in equations [35] and [37] therefore represent the thresholds of the entry date, E, under which both firms are willing to settle.

Figure 4 above shows a timeline of the dates in the model and the resulting monopoly/duopoly profits under the settled entry date, E. An assumption of the model is that after the generic enters, both the brand and generic firms compete in duopoly until the patent expiry date. In other words, there are no generic entrants that enter. As EHHS have described, this assumption is not always the case with reverse payment settlements. However, the only difference this makes for the model is the size of DA and DB. If we relax the assumption that duopoly results after entry and allow for multiple generic firms to enter, DA and DB decrease in size and the threshold E value for the brand firm gets closer to PT while the threshold E value for the generic firm gets even further away from PT. The generic will only settle if equation [37] holds true, and this settlement is anticompetitive if the entry date is greater than the expected patent length from a trial:

E >PT [38] Combining [37] and [38], we can obtain the range of E for which the generic will settle and the settlement obtained is anticompetitive:

[39]

However, because is always positive, the generic is always willing to settle at a threshold of E greater than PT. Even when there is no reverse payment

47

(X=0), E<PT+ and the threshold E is greater than PT. Therefore, it is possible for some settlements without payments to be anticompetitive because the generic firm is always willing to settle with values of E that are above PT. Figure 5 below shows the ranges of possible E that the generic firm (depicted in red) and the brand firm (depicted in blue) are willing to settle when there is no payment.

We can see in the above figure that there is a range of settlements without payments that are anticompetitive, represented by the region shaded both red and blue to the right of PT, that the generic and the brand firm are willing to settle.

While in the case of the brand firm, it is possible to obtain a threshold of settlements that are not anticompetitive and actually have a range of E below PT, the threshold at which generic firms are willing to settle is never below PT even when there is no payment.

In addition, if we combine the generic firm [37] and brand firm [35] decisions, we obtain a range of E for which they are both willing to settle:

[40] Subtracting PT from all sides, the time difference between the settled entry date E and the expected entry date from a trail falls in a range of:

[41] E – PT in equation [41] represents the additional delay from settlement rather than going to trial. It is therefore a measurement of how much more anticompetitive the settlement is than going to trial. As EHHS have explained, when the payment size, X, is lower than the brand firm’s litigation costs, CA, settlements may even result in a negative E – PT and be less anticompetitive than the expected outcome of a trial. However, there is no scenario when the upper bound of the additional delay from settling, E – PT, is not positive. Therefore, even when X=0, there is always a range of E – PT

Figure 5. Thresholds of entry date E for the Generic (red) and Brand (blue) firms for Settlements without Payments (X=0)

Columbia Economics Review

that is positive, which means that there is always a range of possible values for E that are higher than PT. Therefore, the assumption that settlements without payments never have anticompetitive effects may not be reasonable. This could be a theoretical argument as to why there are positive abnormal returns even in settlements without payments in the dataset of generic firm stock returns.

An alternative explanation to the theoretical argument presented above for the presence of positive abnormal results in windows (0,0) and (0,1) in the No Payments sample could also be firm reputation and market underestimation of settlement results. To formally test the effect of firm reputation in the No Payments sample, I examined the differences in CAAR’s of Frequent and Infrequent settlers conditional on No Payments. Out of the 48 No Payment settlements, 27 were settled by frequent settlers and 18 were settled by infrequent settlers. I conducted a similar series of statistical tests on the null hypothesis in [14] regarding whether CAARt2-t1, No Payments/Frequent and CAARt2-t1, No Payments/Infrequent were significantly greater than 0. The effect of Frequency in the No Payments group was not immediately clear, since there are some significant abnormal returns in windows near (0,0) and (0,1) for both groups: in windows (-3,0), (0,1), (0,2) for frequent settlers and in windows (0,0) and (0,1) for infrequent settlers. Many of these results also depended on which statistical test was used. Therefore, to test the effect of being a frequent settler on settlements without payments, I test the hypotheses: H0: CAARt2-t1, No Payments/Frequent – CAARt2-t1, No =0 H1: CAARt2-t1, No Payments/Frequent – CAARt2-t1, No Payments/Infrequent > 0 [42] Payments/Infrequent

I cannot reject the null in [42] for every window except (0,0) for both the Market and Fama-French Models. On the event date, (0,0), the CAARt2-t1 of the Infrequent group is actually higher than the CAARt2t1 of the Frequent group, so the p-value displayed is calculated from conducting a left-tailed test (denoted with the symbol, ^). This suggests that on the event date itself, there is a significantly negative effect of Frequent on abnormal returns of the No Payment group. This is an unexpected result, because I would expect that the settlements that are negotiated by firms that frequently settle would garner more confidence from investors. However, if we examine the settlement rates of fre-

Fall 2016

48 quent and infrequent settlers, we see that most of the settlements with payments are settled by frequent settlers: Since frequent settlers often seem to be involved with settlements with payments, perhaps the jump in stock prices for infrequent settlers of settlements without payments is due to a systematic underestimation of the Infrequent Settlers of settlements without payments before the official settlement announcement. The firm’s reputations as infrequent settlers coupled with the fact that these settlements don’t involve payments could cause the market to underestimate the terms of the settlement on the firm’s profits. On date (0,0), this market underestimation corrects when the actual terms of the settlements without payments are released. This explanation implies that the stock price jump is not necessarily a result of anticompetitive settlements without payments, but rather the correction of market underestimation due to the negative reputation of the firm in terms of its propensity to settle. The positive (0,0) returns of No Payment/Infrequent settlements due to underestimation could be an alternative explanation to the theoretical argument presented above for the presence of positive abnormal returns in the No Payments sample.

VI.3 Results – Effect of being a Frequent Settler While the impact of firm reputation as a Frequent or Infrequent settler has been discussed in the context of the effect of Payments, I also examine the two Frequent and Infrequent groups and the difference between them as a whole. The results only permit the rejection of the null that CAARt2-t1, Infrequent is not statistically significant for the windows (0,0) and (0,1). Interestingly, the positive abnormal returns present in the Frequent group resemble those in the Payment group . There are also pre-event date returns in windows (-3,0), (-2,0), and (-1,0) that seem slightly higher in magnitude than post-event date returns in windows (0,3), (0,2) and (0,1). At the same time, the Infrequent group observations are similar to the No Payment group observations, with significant abnormal returns only occurring in the windows (0,0) and (0,1), depending on which E(rit) model is used. These similarities will be explored further in detail later in this section in the context of possible correlation between Payment and Frequent, and No Payment and Infrequent.

To examine the significance of the effect of Frequent on abnormal returns, I take the difference between Frequent and

Infrequent settlers conditional on settlements with payments and settlements without payments. I display the difference between the Frequent and Infrequent groups conditional on Payments, as well as the test statistics to test the following hypotheses: H0: CAARt2-t1, Payments/Frequent – CAARt2-t1, = 0 H1: CAARt2-t1, Payments/Frequent – CAARt2-t1, Payments/Infrequent > 0 Payments/Infrequent

[43] The null above can be rejected at all the pre-event windows, (-3,0), (-2,0), and (-1, 0). Therefore, it seems that among settlements with payments, the reputation of the firm has a significant effect of abnormal returns in the windows prior to the event date 0. This result is again very similar to the results regarding the effect of Payment on abnormal returns, conditional on the settler being Frequent.

I display the difference in observations and the results from conducting the following hypothesis tests: H0: CAARt2-t1, No Payments/Frequent – CAARt2-t1, No = 0 H1: CAARt2-t1, No Payments/Frequent – CAARt2-t1, No Payments/Infrequent > 0 [44] The reputation of the firm as a frequent settler seems to have no effect on most windows for settlements without payPayments/Infrequent

ments except (0,0). On the event date, (0,0), Frequent actually seems to have a negative impact on abnormal stock returns. This could be due to the systematic underestimation of settlement terms when an infrequent settler is involved in a settlement without payment, as the frequent settlers tend to target the settlements with payments.

Therefore, after testing the effects of Frequent, I found results that were very similar to the effects of Payments on abnormal stock returns. The results from Frequent – Infrequent|Payment and Payment – No Payment|Frequent showed similar significant effects of Frequent and Payment in pre-event windows, (-3,0), (-2,0), and (-1,0). Additionally, it seems that the presence of positive abnormal returns in (0,0) and (0,1) of the No Payments are driven by the infrequent settlers of these settlements.

From these similarities in terms of both the presence of abnormal returns and the effects on abnormal returns between Payments and Frequent, it seems that the two variables may be correlated. To further investigate this idea, I tested the correlation between Payment and Frequent for all observations in my dataset. I display the correlation matrix between the variables Payment and Frequent, where correlation between Frequent and Payments, ρFreq,Pay is calculated

Figure 8. Market Model CAARt2-t1 Observations for All Event Windows

Columbia Economics Review

Fall 2016 Figure 9. Fama-French Model CAARt2-t1 Observations for All Event Windows

as:

[45]

The correlation between Frequent and Payment, ρFreq,Pay, is 0.2562. This is a moderate correlation coefficient that suggests there is some positive relationship between Payment and Frequent. To evaluate the significance of the positive relationship between Payment and Frequent, I tested the null hypothesis that this correlation coefficient is not significantly different from zero: H0: ρFreq,Pay = 0 H1: ρFreq,Pay > 0

[46]

After conducting a one-tailed t-test for the null hypothesis above, I found that I can reject the null to the 1.05%. These results imply that the variables Frequent and Payment are significantly correlated.

The correlation between Payments and Frequent is also expected in the context of Figure 6, as more than 80% of all settlements with payments are settled by frequent settlers. Therefore, while I do not test the effects of the two variables in a multiple regression model, the effect of multicollinearity is present within my difference in means tests to examine the effects of Payments and Frequent. The significant correlation between the two variables suggest that I cannot determine the isolated effects of either one sepa-

rately.

Figures 8 and 9 below summarize the CAARt2-t1 observations of the four data subgroups (Payment/Frequent, Payment/Infrequent, No Payment/Frequent, and No Payment/Infrequent) for each event window. Figure 8 shows the abnormal returns when the Market Model is used while Figure 9 shows the abnormal returns when the Fama-French Model is used to calculate the expected return.

As discussed above, it seems that that settlements with firms that are Frequent settlers almost always trigger positive stock returns, especially in the days right before the settlement announcement (t=0). While it seems that the Payment/ Infrequent group has negative abnormal returns in the event windows, these negative values are not significant and the small sample size (N=6) could be affecting the precision of the estimation. The No Payment/Infrequent group shows negative returns pre-event date and positive returns post-event date, suggesting that there may be a market underestimation of these settlements.

While the literature surrounding reverse payment settlements focus only on the presence of payments as an indication of anticompetitive activity, my study has shown that there may be an alternative explanation for the presence of abnormal stock returns surrounding settlements with payments. The reputation of the firm as having a high propensity to settle also seems to have a significant effect on Columbia Economics Review

49 the abnormal returns. Furthermore, the occurrence of significant stock returns only in the event windows before the actual event date suggests that reputation, and not the presence of payments alone, are influencing stock returns. This is due to the fact that while the terms of the settlement are theoretically not known until the event date itself, the reputation of the firm as a frequent settler is known as soon as patent litigation surrounding the drug is announced. At the same time, the two factors of the presence of a payment and the reputation of the settler as having a high propensity to settle seem to be significantly correlated and the effects from these two variables cannot be clearly distinguished. Therefore, these results challenge the conclusion that abnormal stock returns for settlements with payments prove that the settlements are anticompetitive, because these high stock returns could be due to the reputation of the firm itself. However, since payments and reputation are correlated, it is also difficult to reject the conclusion that high stock returns are caused by the presence of payments. Thus, in the case of the generic firm, high stock returns themselves are not enough to prove the presence of anticompetitive settlements.

high stock returns themselves are not enough to prove the presence of anticompetitive settlements.

VI.4 Results – Drug Percentage of Firm Sales In addition to the presence of a payment and the settling firm’s reputation, to answer Question II, I also test whether or not the percentage of firm annual sales that a drug’s annual sales comprises influences the abnormal return. Since the presence of a payment and whether the firm is a frequent settler are technically dummy variables, to avoid restricting my regression to have the same slope, I separated my data into the four subgroups mentioned in previous sections and then regressed the CARi,t2-t1, a firm-specific cumulative abnormal return, onto the percentage of total sales in year t that the annual sales of the drug in year t would

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Columbia Economics Review

Fall 2016 comprise: CARi,t2-t1=β0+β1(Salest)+εi

[24]

Details about the regression can also be found in Section VI. Hypothesis Testing – t-test. For each subgroup, I tested the null and alternative hypotheses regarding the coefficient, βˆ2: H0: βˆ2 = 0 H 1: β ˆ 2> 0

[26]

It seems that I can reject the null that βˆ2, the effect of drug sales percentage on abnormal returns, is zero for all windows prior to the event date for the Payment/ Frequent group and only the windows (0,2) or (0,3) (depending on whether the Market Model or Fama-French are used) for the Payment/Infrequent group.

Therefore, it seems that the relative sales of a drug also affects abnormal returns prior to the event date t=0 for settlements with payments that are settled by frequent settlers. The importance of the drug for the company’s revenue is therefore another factor that influences the presence of positive returns before the event date. If investors see that firms with a reputation for settling often are involved in a payment settlement, most of the positive effects on stock returns occur early on because investors don’t need to wait for the settlement to be officially published to begin trading at a higher price. The sales percentage of a drug playing a role in the pre-event date early stage therefore makes sense in this context, as most of the positive effects of settling have already occurred early on.

At the same time, it seems that the sales percentage of the drug does not play an important role in determining abnormal returns if the firm involved in the settlement does not have the reputation of being a frequent settler (the Payment/Infrequent group). This result is also expected, as there were no positive abnormal returns at all in the Payment/ Infrequent sample. These results suggest that perhaps frequency is a more important determinant for abnormal returns, as neither the presence of a payment nor the percentage of drug sales seem to affect or induce positive stock returns for the infrequent group.

I display the results of the regression and hypothesis test from [26] on the No Payment/Frequent and No Payment/ Infrequent group. It seems that I can reject the null hypothesis that βˆ2 is equal to zero for almost every window. For settle-

ments without payments settled by frequent settlers, the drug sales percentage influences the presence of abnormal returns for almost every window except the windows that include days further away from the event date, such as (-3,0), (0,2), and (0,3), depending on which expected returns model is used. While the actual returns for the No Payment/Frequent group are not statistically significant from zero except in the windows (0,0) and (0,1), the sales percentage has a sig-

These results suggests that the greater

the sales of a drug

relative to the firm’s annual sales, the

lower the abnormal returns are prior to the event date.

nificant effect on these abnormal returns for almost every window. This could be due to the fact that when a frequent settler enters into a settlement, whether this settlement involves a payment or not, investors will respond positively when the drug brings in a higher revenue.

However, the presence of the asymmetric timing of abnormal returns is not present here as it was in the Payment/Frequent group, because the positive returns are less “sure” or “expected” when the settlement does not involve a payment.

On the other hand, I show that for the No Payment/Infrequent group, the sales percentage positively influences abnormal returns on and after the event date in the windows (0,0), (0,1), (0,2), and (0,3).

However, sales percentage actually significantly negatively influences abnormal returns in the windows prior to the event date, (-3,0), (-2,0), and (-1,0). These results suggests that the greater the sales of a drug relative to the firm’s annual sales, the lower the abnormal returns are prior to the event date. Perhaps this result is due to the fact that when a drug has higher sales, and is therefore more important monetarily to a company, the market expects and wants the firm to enter into a settlement that involves a payment rather

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51 than one without a payment. This could be related to the possible market underestimation of the settlement seen in the alternative explanation to the presence of positive returns in the No Payments sample. However, once the terms of the settlement are officially announced, this market underestimation corrects and sales once again positively influences the abnormal returns.

VII. Comparison to DSM’s Brand Firm Returns While DSM did not divide their data into subgroups depending on whether the settlement involved a payment or not, I will analyze the Payment and No Payment samples of the generic firms in my dataset and compare them to the Payment and No Payment brand firms of DSM’s dataset. The first difference is that while it seems that the Payment groups of both the generic and brand firm involved significantly positive stock returns in all windows, the brand firm did not have the same pre-event date asymmetric pattern in their returns as the generics did.

In addition, while there were no positive abnormal returns for settlements without a reverse payment for the brand firm, there were significantly positive returns in windows (0,0) and (0,1) for the generic firms on the opposite side of those settlements. Finally, the third difference is that while DSM found significantly positive differences between the returns from settlements with payments and settlements without payments for the event date (0,0) and windows after the event date, (0,1), (0,2), and (0,3), I did not find significantly positive differences for the generic firms in these windows. In fact, I only found significantly positive differences between the stock returns for settlements with payments and settlements without payments in the windows before 11the event date, (-3,0), (-2,0), and (-1,0).

The first and third difference regarding the asymmetric timing of abnormal returns could be related to the reputation factor of generic firms. There are much fewer generic firms than brand firms that settle and therefore the firm’s reputation for having a high propensity to settle could be an important factor in the timing of abnormal returns. Both the effect of Payment on frequent settlers and the effect of Frequency on settlements with payments present an asymmetric timing of abnormal returns earlier than the event date. Therefore, the effect of reputation combined with the presence of a payment could be the reason for this asymmetric

52 timing in generic firms that is not present in brand firms.

The second difference, the presence of abnormal payments on dates (0,0) and (0,1) in no payment settlements, could be due to the generic entry date, E, threshold above the expected litigation entry date, PT. It is interesting to note that if generic firms are involved on the other side of these same settlements without payments, then this threshold E is similarly above PT for both the brand and generic firms and should represent higher-thanexpected profits for both. Therefore, it is unexpected that the market doesn’t react to these no payment settlements the same way for the brand and generic firm. This could be due to the fact that the market is more sensitive with the generic firm’s stock returns since it is the generic firm that establishes this threshold of E greater than PT. An interesting study could result from the investigation of the correlations between generic and brand firms, and the implications for anticompetitive activity from these interactions.

VIII. Conclusion This paper examines publicly available security price information for publicly traded generic firms involved in Paragraph IV ANDA settlements to (I) test how the settlement announcement affects the stock price of the generic firm and (II) examine what other factors besides the involvement of a payment in the settlement affect the generic stock prices. I found that on average, settlements with payments produce significantly positive abnormal stock returns of approximately 1.6% in windows before and approximately 1% in windows after the event date, =0. Settlements without payments produced positive abnormal returns only on the event date, =0, of around 0.5% and in the window, (0,1), of 0.9%. Similarly, settlements that were settled by frequent settlers, Teva, Actavis/Watson, Mylan, and Barr Laboratories, had a significantly positive abnormal return of approximately 1.2% before the event date and 0.9% after the event date. Settlements that were settlement by infrequent settlers resulted in positive abnormal returns also only in the windows (0,0) and (0,1) of approximately 1% and 1.1% respectively. The difference between abnormal returns from settlements with and without payments were significant only in the windows prior to the event date, (-3,0), (-2,0), and (-1,0), of approximately 1.7%. Similarly, the difference between abnormal returns generated from frequent and infrequent

Fall 2016 settlers were also only significant in the same pre-event date windows above of approximately 1.9%. My results question which factor, the presence of a payment or the reputation of the settling firm, is responsible for these positive abnormal returns. Most of the previous literature on this topic has focused on the following explanations for a stock price hike after the announcement of a reverse payment settlement: (i) The actual presence of an anticompetitive payment, , that causes the settled entry date, , to be greater than the expected entry date under litigation, (ii)The firm’s reputation that causes confidence in the terms of the settlement for the firm’s profit (iii)A systematic market underestimation prior to the announcement of the settlement and a subsequent correction once the settlement is announced Only the first explanation, (i), implies that a positive stock price hike actually signals the presence of anticompetitive activity. While I found positive abnormal returns from settlements both with and without payments that support explanation (i) that there may be anticompetitive activity present, my study also shows that explanation (ii) is another possible cause for positive stock returns through the similar effects and high correlation of Payment and Frequent. At the same time, (iii) could also be a factor when looking at the negative impacts of Frequent on abnormal returns in the sample of settlements without payments. Therefore, while the presence of anticompetitive activity could be indicated through the presence of significant abnormal stock returns in my study, it is not the only possible cause of these positive returns.

Furthermore, in regards to settlements without payments, I introduce a theoretical model building upon the EHHS model that shows that there is a range of equilibrium settlement entry dates, that are anticompetitive even when there is no payment involved in the settlement.

This is due to the fact that the maximum threshold that the generic is willing to accept is higher than, the expected patent length/generic entry date under litigation. In a large portion of Hatch-Waxman settlement literature, including the FTC v. Actavis case and the Actavis Inference that emerged from the Supreme Court opinions on the case, the expected outcomes from settlements without payments are assumed to be equivalent to the expected outcome from litigations.

While this may be the case for the brand

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firm, the Activating Inference theoretical model adapted for the generic firm tells a different story. Even when there are no payments, the generic is still willing to settle below a maximum threshold of that is above . Therefore, the theoretical model demonstrates that even settlements without payments can be anticompetitive.

This idea is supported in the data, as there are significantly positive abnormal returns in windows (0,0) and (0,1) for generic firms involved in settlements without payments.

At the same time, the percentage of a firm’s annual sales that the drug’s sales comprises is also an important factor that significantly influences the abnormal returns for settlements that are settled by frequent settlers, for settlements both with and without payments. While sales percentage is often thought of as positively influencing the anticompetitive effects of settlements with payments, its effects actually influences settlements settled by frequent settlers more so than merely settlements with payments. This is another indication of the importance of the reputation of the settling firm that is often ignored by literature regarding the anticompetitive effects of reverse payment settlements.

Therefore, when evaluating the anticompetitive implications of reverse payment settlements through stock return analysis, it is important to keep in mind that there are multiple other factors besides the presence of a reverse payment that could cause the stock price hike on announcement day. Some of these other factors, such as firm reputation and sales percentage of the drug, do not directly support the conclusion that these settlements are anticompetitive. However, since many of these predictors are correlated, it is often difficult to either reject or affirm that significant security returns reveals anticompetitive behavior. Finally, when examining the payments without settlements, the theoretical model that I propose adapted from EHHS suggest that we should not be looking at generic firms in the same way as brand firms, because generic firms are willing to accept an entirely different threshold of E. It is important to question the mere presence or lack of payment in these reverse-payment settlements as a direct indication of anticompetitive activity. n

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53

Second Wage Feminism How Access to Contraceptives Affects Female Wages: An Irish Case Study Benjamin E. Reid Oberlin College A woman's decision if and when to have children is a fundamental expression of her rights and autonomy. This has been made possible thanks, in part, to the expansion of access to contraceptives in the past century. The widespread use of contraceptives has in turn changed the dynamics of population growth and development. This paper analyzes some of the economic consequences of this change, looking at the effects on female wages in Ireland during the period of expansion of reproductive rights during the twentieth century. It sets a solid framework to analyze how the availability of different options to plan their pregnancies affect female labor outcomes. While there's still research to be done in this area, and economists must keep the limitations of their analyses in mind, we believe a better understanding of the forces at play in the female labor market will be crucial, especially in the contemporary world where issues such as the gender ay gap are as real as ever.

-K.B.

I. Introduction In this paper, I explore the extent to which access to contraceptives affects female wages. Numerous economists have studied the relationship between a woman’s fertility and labor market choices using life-cycle labor supply models that view a woman’s decision of when to start childbearing as an attempt to minimize the depreciation in human capital that she incurs when temporarily exiting the labor force after childbirth (Happel et al. 1984).

Past studies have generally found that contraceptives enable women to better control the timing of fertility, permitting them to more precisely minimize this loss in earnings potential and therefore attain higher lifetime wages (Hotz et al. 1997).

The resultant increase in lifetime returns to a career incentivizes more women to pursue a career in lieu of homemaking, thereby increasing labor force participa-

tion rates for women with access to contraceptives (Bailey 2006).

This study will examine the fertility and labor market effects of contraceptive ac-

Are less-

skilled workers disproportionately and negatively impacted by increased labor market competition from less-skilled immigrants?

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cess using Ireland in the period from 19731994 as a case study. Due to the country’s Roman Catholic leanings, Irish laws surrounding contraceptives such as condoms and spermicides have historically been very strict compared to other developed nations, until a series of three laws passed between 1973 and 1985 incrementally increased access to these devices, as outlined in Table 1 (Leridon et al. 2006). Birth rates soon fell while female labor force participation rates surged throughout the late 1970’s and into the 1990’s, and several economists have posited that the liberalization of contraceptive laws contributed to these demographic changes (Bloom et al. 2003).

As seen in Figure 1 below, the total Irish birth rate started to decline in 1974—the year after the Irish government legalized the import of contraceptives from Northern Ireland. The 1979 legalization of the

54

sale of contraceptives for family planning purposes appears to have had a larger effect, judging from the sharper drop in the fertility rate during the 1980’s and the concomitant steepening in the rate at which the labor force participation for women aged 25-34 was rising.

The distinct changes in contraceptive policy during this time, and the fact that changes in fertility and female labor market behavior closely followed these policies, make Ireland in this period a useful case study for this topic. Furthermore, each of the three policies had different implications for different subsets of women, facilitating the creation of control groups to determine if women who were more likely to have increased contraceptive access altered their fertility and human capital investments more than women who were less likely to have access.

Results indicate that access to contraceptives allowed for increased postponement of childbearing, as women with access had their first child at significantly later ages than did women without access. Furthermore, this postponement of maternity had a larger positive effect on female wages after the sale of contraceptives became legal. This suggests that as childbearing became increasingly controllable, the decision to postpone maternity became more closely tied to women’s labor force and human capital investment decisions, as predicted by life-cycle labor supply models, thereby having a larger marginal effect on their subsequent wages.

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is, the direct expenditure on goods and services that raising a child entails, as well as the opportunity cost of parental childcare. Minimization of this opportunity cost presents an interesting framework with which to analyze a couple’s fertility decisions as they relate to their life-cycle labor supply.

Life-cycle models generally assume that fertility is stochastic but controllable with the use of contraceptives. According to Hotz et al. (1997), most life-cycle fertility models assume that using contraception is costly, due to out-of-pocket costs for the contraceptives themselves or the travel expenses to obtain them, as well as psychological costs associated with the inconvenience or displeasure of use. While out-of-pocket costs for contraceptives are zero for all low-income Irish citizens who are covered by a medical card, those who do not have a medical card would have to pay for the contraceptives out of pocket.

It is also plausible that these psychological costs could play a particularly large role for religious Catholics in Ireland, as the staunch disapproval of birth con-

trol by the Catholic Church might have spawned social stigmatization surrounding contraceptive use. Given that Ireland was roughly 93% Catholic in this period, these psychosocial costs may have been significant for a large subset of the Irish population, potentially muting the effects of contraceptive access on the country as a whole (Census of Population, Volume 12 1971-1985). For this reason, religiousness will be controlled for in the regressions.

Life-cycle models of fertility present several factors as affecting a couple’s decision to have their first child. The most salient is how the maternal costs of raising children varies over the mother’s life cycle. According to Hotz et al. (1997), these models predict that only the timing of fertility demand responds to changes in income or the price of preventing childbirth, not the lifetime fertility demand. Indeed, Becker (1991) similarly argues that the ability of a woman to better control her fertility via contraception should not affect the total demand for fertility, which is empirically measured by completed fertility. As such, changes in income and prices at any point in a couple’s life cycle, including the price of preventing childbirth via availability of contraceptives, should not affect the total number of children that women eventually have, but should affect when they choose to start having them.

While Becker’s model (1960) and subsequent life-cycle labor supply studies such as Bailey’s (2006) predict that access to contraceptives should not change total demand for children, aggregate countrylevel data from Ireland during this time seem to contradict this assumption. After Ireland progressively increased access to

Figure 1: Birth Rate and Female Labor Force Participation 1971-1991 (source: Walsh 1993)

II. Literature Review Starting with Gary Becker’s work in the 1960’s, several economists have created models of a couple’s fertility choices as they relate to the mother’s life-cycle labor supply. In his landmark paper, Becker (1960) found that a couple’s decision to have a child depends on the family income as well as the cost of the child—that Columbia Economics Review

Fall 2016 contraceptives, the birth rate (number of children per 1000 women) for all age groups declined at an increasingly steeper rate (Figure 1), albeit faster for younger cohorts of women. Of course, even if contraceptives only incited a postponement of first maternity and not total fertility, the country’s birth rate would still be expected to fall initially as more women who would have otherwise started childbearing in these years would postpone their births to future years. However, if total fertility remained unchanged, the fertility rate should have subsequently risen, commensurate with the decrease from initial postponement, leaving total fertility unchanged in the long run. This did not occur in Ireland, as the birth rate continued to decline until the mid-1990s, at which point it remained at a persistently low level and did not return to initial rates.

While country-level data seem to contradict the assumption that total fertility does not respond to contraceptive access, regressions performed in this paper suggest that having access to contraceptives did not influence the total number of children that women had in Ireland during this time, as predicted by the lifecycle models. However, this might be due to truncation in the maximum age for women who had legal access in the dataset used (discussed further in section IV), as many women with contraceptive access may not have completed their life-

time fertility by the time they were interviewed in 1994. Since the available data is unable to precisely quantify changes in lifetime fertility, and since past literature assumes that lifetime fertility does not respond to contraceptive access, this paper will focus on age at first birth as the primary measure of fertility.

Another paper by Happel et al. (1984) models a couple’s decision of when to have their first child as dependent on the costs of childbearing throughout the life cycle. These costs include both direct expenditures on goods and services such as cribs and daycare, as well as loss of household income resulting from the mother’s temporary absence from the labor market to care for the newborn. The latter depends on the rate at which real earnings depreciate when the mother is absent from the labor force, as well as her initial wages at the start of the couple’s life cycle.

The driving factor affecting fertility timing in this model is the depreciation (γ) of the woman’s earning power due to time out of the labor market; if γ=0, then the woman, regardless of initial earnings status, would be indifferent towards having her child at an early or late age, as the loss to lifetime earnings would be constant throughout her life cycle for a given period out of the labor market. Indeed, the model predicts that women who work in less highly skilled professions where their skills are unlikely to depreciate over

Figure 2: Time path of wife’s earnings. Case I, no skill loss; Case II, partial skill loss; Case III, total skill loss. Source: Happel et al. 1984

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55 time (γ≈0) will tend to be indifferent to the timing of the birth of their children.

In Happel et al.’s model (1984), the wife’s earnings are expressed as, Y(t+ω) for 0 < t < T, and y{t + ω – τ – min(γτ, T+ω), for T+τ < t < L, where γ represents the rate of depreciation of job skills and earnings potential, and for each time period out of the labor force, γ periods of work experience are lost. ω is the amount of work experience or job training, measured in years, attained by the wife before marriage, and τ indicates the number of consecutive periods during which the wife is not in the labor market to take care of her child.

This model predicts three possible outcomes, depending on the value of γ and ω: Case I: If γ=0, there is no skill loss and the wife’s earnings when she re-enters the labor force are y(T+ ω), which is equal to her earnings before exiting the labor force at time T. Case II: If γ>0 and T+ ω > γτ, then the wife retains some of her initial skills and earnings potential when she is absent from the labor force. She then earns y(T + ω – γτ) when she returns to work.

Case III: If γ>0 and T+ ω ≤ γτ, then she loses all of her skills and initial earnings potential, and re-enters the labor force with a starting salary of y(0).

The time path of the woman’s earnings for each of these cases is diagrammed in Figure 2. According to this model, relatively unskilled women who start their marital life cycle with little or no earnings (ω0≈0) begin childbearing immediately after marriage because they do not have any human capital to lose from exiting the labor force after childbirth at this time, but they would in the future if they were to start their careers instead.

Alternatively, women with higher initial earnings, due to increased educational attainment or job training before marriage, would tend to postpone childbearing in order to minimize the number of years in their career that are affected by this loss in human capital.

This is consistent with O’Donoghue et al.’s (2010) finding that in Ireland throughout the 1970s and 1980s more highly educated women experienced a larger delay in first birth than their less educated counterparts. They attributed this to the likelihood that the human capital loss due to time out of the labor force might be substantially greater for highly skilled women, incentivizing them to start childbearing later in the life cycle

56 in order to minimize the number of years that are impacted by this potentially large reduction in earnings potential.

While many economists have constructed theoretical models relating fertility and female labor force choices, few have quantified the effect of contraceptive access on these outcomes. Martha Bailey (2006) measured this effect, exploring how the contraceptive pill, introduced in 1960, affected fertility as well as female labor force participation and wages after various state-level laws in the United States legalized “early access” to the medication for women aged 18 and over without the consent of their parents.

Using fixed effects regressions, Bailey found that early access to the pill increased female labor force participation and wages by reducing costs of preventing and timing pregnancies. She concludes that the pill increased women’s initial career investments, as women no longer expected to have as many unplanned spells out of the labor market due to an unintended pregnancy. As their future career paths became less uncertain, the lifetime returns to a career increased, incentivizing more women to enter the workforce in lieu of becoming homemakers.

While past studies by O’Donoghue et al. (2010) and Walsh (1993) suggested that the liberalization of contraceptive laws might have contributed to changes in fertility and female labor force behavior during this time in Ireland, neither of these papers explicitly analyzed and quantified these effects. This paper will expand on their studies by quantifying the effects of Ireland’s policy changes, and controlling for the differential effects that these policies had on different groups of women based on their exogenous characteristics—something Bailey did not consider in her 2006 paper. This paper will therefore combine the lifecycle labor supply model approach of O’Donoghue et al. (2010) and the targeted analysis of individual contraceptive policies as performed by Bailey (2006) to determine the extent to which contraceptive policy changes that took place in Ireland during this period altered female fertility behavior and lifetime wages.

III. Data This paper makes use of retrospective life history data from the 1994 Living in Ireland Survey, which was used in O’Donoghue et al.’s 2010 paper. The survey was conducted each year from 1994-2001 by the Economic and Social Research Institute in Dublin, beginning with

Fall 2016 Figure 3: Maximum ages at time of interview (1994) for women with contraceptive access (18 years or younger in policy year) via each policy

10,418 individuals in 4,048 households in 1994. The survey contains hundreds of variables detailing the employment and fertility history of each member over the age of 18 in every household, facilitating longitudinal analysis of individual women’s fertility and employment histories to detect connections between the two.

To determine the mechanism by which access to contraceptives affects fertility, I calculated various statistics for each of the 3,207 women who were listed as having children in the 1994 dataset, her age at each of her first six births, her age at marriage, whether or not she completed education and job training before marriage, her proximity to the Northern Ireland border, as well as many others.

IV. Truncation of Dataset: Implications for 1985 Policy Analysis The Living in Ireland Survey was conducted in 1994, leaving only nine years between the 1985 policy and the time of interview. For this reason, the number of women in the cohort that had legal access via this law and who started childbearing before 1994 was relatively low compared to the cohorts with access via the 1973 and 1979 policies. Furthermore, the maximum age at first birth for women with 1985 contraceptive access throughout their childbearing years (those who were 18 years or younger in 1985) was 27, resulting in an artificially low age at first birth for this cohort. These women also had relatively less work experience than those who did not have access and whose age was therefore unrestrained, resulting in commensurately lower wages for this Columbia Economics Review

cohort. For this reason, the models included in this paper cannot measure the effects of this policy on age at first birth (Model I) and wages (Model II).

While the 1985 policy could not be analyzed in these models, probit models that were not included in this paper measured the probabilities of giving birth by particular ages for all three laws to see if this policy impacted fertility decisions in a similar fashion to the 1973 and 1979 laws. Since these models compared the behavior of women with varying levels of access by certain ages, and therefore only analyzed completed fertility for all cohorts involved, they did not suffer the same truncation as Models I and II. Results from these probit models revealed that the 1985 policy significantly reduced the likelihood of young women having a child by each age between the ages of 23-27. As expected, since the 1985 policy legalized over-the-counter access to all women over the age of 18, its effect was seen for women at earlier ages than both the 1979 and 1973 policies, and was not influenced by a woman’s marital status as the 1979 policy was.

V. Empirical Design Model I: Age at First Birth The model on age at first birth (Age1i) takes the following specification: Age1i= β1la73i + β2la79i + β3yearbi + β4educi + β5religi + β6geoi + β7totalwagesi + β8educ_ complete + β9int_la73_geoi + β10int_la79_ marriedi + β11int_la79_religi + β12int_la79_ medcardi, r

Fall 2016 The variables of interest are la73i and la79i—dummy variables indicating whether woman i had legal access to contraceptives, via the 1973 or 1979 policies respectively, in the year that she had her first birth. These dummies answer the question: was the timing of first birth of woman i ostensibly planned using contraceptives? Variables controlling for a variety of characteristics of woman i were included.

Several of these controls—whether woman i had ever been married (evermarriedi), her religiousness (religi), and whether she possessed a medical card (medcardi), were interacted with the 1979 policy to determine if changes in these variables altered the effect that 1979 contraceptive access had on age at first birth. They were interacted with the 1979 policy since this policy likely increased access for the greatest number of women in Ireland, as this was the first policy that legalized the domestic sale of these devices in the Republic. The geographic proximity of woman i to the Northern Ireland border (geoi) was additionally interacted with the 1973 policy to determine if legalization of the import of contraceptives had a larger effect for women who lived closer to Northern Ireland, where these devices were legally purchasable. Additional variables controlling for year of birth, educational attainment, gross weekly wages, and whether or not education and job training were completed at time of marriage were included in the model.

Model II: Logarithm of Gross Weekly Wages The model for the log of gross weekly wages (Model II) is specified as follows: logwagesi= β1LA73i + β2LA79i + β3agei + β4educi + β5loghusbwagesi + β6managei + β7evermarriedi + β8age1over20i + β9int_ LA79_over20i +, r Where LA73i and LA79i are dummy variables indicating whether woman i had contraceptive access when she entered her childbearing years, taken here to be 18 years old, via the 1973 and 1979 policies respectively. A variable measuring the extent of maternity postponement (age1over20i) was added to the regression to determine the effect of this postponement on wages, and is measured as the number of years beyond age 20 that woman i gave birth to her first child. So, for a woman who had her first birth at age 26, age1over20i = 6. This variable is constrained to positive numbers, as I am only interested in whether postponing maternity positively affected wages, not whether failing

to postpone maternity reduced wages. An interaction term between this variable and the 1979 legal access dummy (int_ LA79_over20i) was included to determine if having contraceptive access had a larger effect on wages for women who used these devices to postpone their childbearing, which would be expected given that the hypothesized mechanism by which this access impacts wages is by facilitating maternity postponement. Additional variables controlling for other characteristics of women i were included.

The model on logwagesi defines the legal access dummies differently than the model on age1i, because it is testing whether the knowledge that contraceptives are an option—regardless of whether or not they were used—changed female labor market and human capital investment choices during the years that one often makes decisions regarding their future in the labor force. While the legal access dummies in the model for age1i indicate whether contraceptives were available when a woman had her first birth, the model on logwagesi explores whether the increased predictability of future childbearing increases lifetime returns to a career and therefore incentivizes increased human capital investment at a young age, or a decision to enter the labor force rather than become a homemaker as Bailey found in her study (2006). This would result in higher wages in the long run.

Furthermore, the issue that contraceptives might have become legal when a woman was, for example, 26 even though she started childbearing at age 28 does not present the same problem as it would have in the model on age1i. Many labor force decisions would have already occurred by the time the woman was 26 and even though her future first birth may be “planned” using contraceptives, this would not have affected decisions surrounding her future in the labor force that she already made before she knew her childbearing would be controllable.

The policy dummies in Model II therefore capture the woman’s expectations of how much control she will have over her future childbearing, which in turn affects her labor force decisions and human capital investments, resulting in higher lifetime earnings.

VI. Results Results from these models indicate that having contraceptive access enables women to postpone their childbearing longer and ultimately attain higher wages. Furthermore, this paper was the first to find that maternity postponement had Columbia Economics Review

57 a larger marginal effect on wages when it was achieved with the aid of contraceptives. This suggests that contraceptives allowed women to more precisely time their childbearing so as to minimize the loss in human capital that they experienced after childbirth, effectively making postponement less random and more closely tied to their labor supply and human capital investment decisions.

The coefficients on both la73i and la79i were statistically significant and positive, confirming the hypothesis that having contraceptive access enables women to postpone childbearing. Holding other regressors constant, the ability to obtain contraceptives from outside Ireland, via the 1973 law, increased age at first birth by 2.81 years. The marginal effect of the 1979 law resulted in an additional postponement of 2.81 years, such that a woman giving birth for the first time in 1980 Model I: Age at First Birth Table 2: Results for Model on Age1

58 would be 5.62 years older than an otherwise identical woman who gave birth for the first time in 1972. The interaction term between evermarriedi and la79i was positive and significant, indicating that the effect of the 1979 policy was greater for married women, who postponed their first births by an additional .97 years than unmarried women. This corroborates the commonly held notion that the Irish government’s 1979 legalization of the sale of contraceptives with a doctor’s prescription disproportionately increased access for married couples, as women had to prove to their doctor that they were using the devices for family planning purposes in order to receive a prescription.

Educi, a factor variable measuring the highest level of education completed, yielded a positive and significant coeffi-

Fall 2016 cient as well for all three levels of education. These results are consistent with Happel et al.’s model and O’Donoghue et al.’s study, as more highly educated women would be expected to postpone births longer to minimize the number of years that are affected by the reduction in earnings potential due to absence from the labor force, which might be very significant for women with high human capital prior to this absence. Likewise, women who had completed education or job training before marriage postponed their births by an additional 1.57 years.

This is also consistent with Happel et al.’s model, which predicts that women with higher initial human capital at the time of marriage start childbearing later in the life cycle.

The insignificant and positive coef-

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ficient on religi indicates that religiousness did have the stifling effect on contraceptive use that was expected given the Roman Catholic Church’s negative stance on birth control. However, much like the geoi variable and its associated interaction term, this finding should be viewed cautiously since this variable was defined very broadly, based only on the number of times per week a woman goes to church and not on religious affiliation or adherence to religious practices or values. This inconclusive result should therefore be attributed to the unfortunate dearth of questions included in the Living in Ireland Survey surrounding its subjects’ religious affiliation and involvement, necessitating the use of a different dataset in the future to draw conclusions on religion’s prohibitive effect on birth control use.

The regression on the log of gross weekly wages (Irish £/week) at the time of interview in 1994 yielded a negative and significant coefficient on the 1979 legal access dummy, suggesting that women with access to contraceptives throughout their childbearing years earned almost 35% less than women who did not have access. To check the robustness of this estimation, I removed LA73i from the regression, and the coefficient on LA79i (βLA79 = -.350) retained its sign, significance, and approximate magnitude. Likewise, when I excluded LA79i, the coefficient on LA73i remained highly insignificant with a p-value of .580, suggesting that these estimations—though initially counterintuitive—are not a result of collinearity between LA73i and LA79i.

While this seems to contradict the finding by Bailey (2006) that having access to contraception increases female wages, the interaction term between age1over20i and LA79i was positive and highly significant, indicating that for women who postponed maternity to age 24.8 or beyond ([20 + βint_LA79_over20] / βage1over20), having access to contraceptives during their childbearing years positively impacted their earnings. The effect of contraceptive access on wages therefore becomes larger as women postponed their births longer, such that a woman with legal access who started childbearing at age 29 would earn 30.1% more than a woman who did not have access but started childbearing at the same age.

These results indicate that while women who started childbearing later earned slightly more even before the 1979 policy (βage1over20 > 0), postponing maternity had a significantly larger effect on women’s

Fall 2016 wages afterwards—that is, when women achieved this postponement under less uncertainty with the aid of contraceptives. With an increased ability to plan the timing of childbirth, women and couples could ostensibly time their childbearing so as to minimize the mother’s loss of earnings potential, more closely approximating the theoretical decision-makers of Happel et al.’s (1984) model. Thus, as the timing of maternity became increasingly controllable, the decision to postpone childbearing became more closely tied to a woman’s labor force and human capital investment decisions, resulting in higher wages for those who postponed maternity using contraceptives. This suggests that simply having access to contraceptives did not change women’s labor force and human capital investment decisions, unless women actually used the devices to control their fertility.

VII. Conclusions Model II: Logarithm of Gross Weekly Wages Table 3: Regression results for Model II on logwagesi

This study reveals that access to contraceptives enables women to more precisely time childbirth and thereby minimize its negative impact on their lifetime earnings. Women with contraceptive access therefore started childbearing later, and this postponement of maternity by one year had a greater marginal effect on wages when women achieved it with the aid of contraceptives. For this reason, women with contraceptive access who used these devices to postpone maternity had higher wages at the time of interview compared to both women without access and to women who had access but did not postpone their childbearing.

While it is plausible that contraceptive access impacted wages by way of improving educational attainment prospects for women, a probit model on educi performed outside of this paper yielded highly insignificant results for all three levels of education. This indicates that the inclusion of educational attainment controls in these regressions did not interfere with the estimations of contraceptive access effects on age at first birth and wages. This further supports the conclusion that contraceptive access influenced wages by facilitating increased maternity postponement.

While results from this study point to the effect of contraceptive access on wages, it is unlikely that this was the only force behind the staggering labor force changes that took place for women during this time (Figure 1). For example, past work by Walsh (1993) found that several other changes significantly increased the

59 number of jobs available to women. These include the 1977 Employment Equality Act and expansion in both the retail distribution and professional services sectors, which were largely female-driven.

However, I argue that the contraceptive policies did not have an effect in spite of these other factors; rather, improvements in contraceptive access amplified the effects of these changes by enabling more women to pursue careers and thereby take advantage of the newfound opportunities that were afforded to them. Indeed, Bailey (2006) similarly argues that increased access to contraception in the United States might have had little or no effect on female labor force participation and wages without the concurrent changes in discrimination laws and labor market composition, which led to a growth in the number of job opportunities for women.

Ultimately, this paper contributes to the existing literature by employing both life-cycle labor supply models and targeted analysis of distinct policies to quantify the marginal effect of varying levels of contraceptive access on fertility and female wages. It also corroborates the commonly held notion that contraceptive access improves female labor market outcomes by facilitating maternity postponement, as it proves that maternity postponement has a larger positive effect on wages when it was achieved with the aid of contraceptives. n

Figure 4: Interaction Plot Illustrating Increased Effect of Maternity Postponement on log(wages)i for women with access to contraception in childbearing years (LA79i = 1)

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