Based on the legislative history, I restrict the analysis to births occurred in years 1982 to 1986. This reflect a period when the Medicaid expansions focused primarily on the categorical eligibility rules. Specifically, the pre-policy period includes years 1982 to 1984. I use January 1985 as the first month of post-policy period, as this coincide with the state legislature convene timing of calendar year 1985 for most of the states. I end the post-policy period by December 1986 for two reasons. First, starting in April 1987, a subsequent policy change - the Omnibus Budget Reconciliation Act of 1986 (OBRA86) – was effective. The OBRA86 permitted states to increase income threshold for pregnant women to up to 100% of the poverty line. Variation occurred across states in adopting the expansion. On the other hand, the timing and generosity of state level expansions are potentially correlated with other state level unobserved attributes. To avoid state level legislative endogeneity concern, I exclude from the analysis sample births occurred after OBRA86 became effective. Second, I further exclude birth occurred in the first three month of 1987, to ensure that both pre-policy and post-policy sample are evenly distributed over the months of the year. Buckles and Hungerman (2013) documents substantial seasonality pattern of maternal characteristics.
policy in a non-microfounded linear Rational Expectations model, where the gov- ernment’s information set is a subset of the private sector’s information set. They show that, even though the “separation principle” fails because of asymmetric infor- mation, there is a suitable modification of the standard Kalman filter that works, thanks to linearity and additively separable shocks. Moreover optimal policy has the “certainty equivalence” property: under Partial Information the government applies the Full Information policy to its best estimate of the state. In our setup, because of non-linearity, both the “separation principle” and “certainty equivalence” fail. Aoki (2003) applies these results to optimal monetary policy with noisy indicators on out- put and inflation. Nimark (2008) applies them to a problem of monetary policy where the central bank uses data from the yield curve while at the same time understanding that it is affecting them.
But even if the quality of the road surface can be measured satisfyingly, there is a mech- anism that puts the results of efficiency analyses using only these data into question. A lower quality of a road may be a result of the aging process of roads such that higher maintenance costs arise without any inefficient use of public funds. Therefore, I propose the development of a third generation of efficiency analyses that also consider the age of the foundation of the road network. The mechanical process that describes the deterio- ration of the surface (and thus the quality of roads and increasing maintenance costs) can be separated into two categories (Habiballah and Chazallon 2005): first, the short-term mechanical process (horizontal stress), which is activated by vehicle use (the effect of this process is usually very small and reversible) and second, the long-term mechanical pro- cess (vertical stress), which is caused by ground water flows, creep processes in the clay, or long-term settlement after a large amount of vehicle use. Regarding vertical stress, a permanent deformation in the foundation leads to a modification of any layer above it (the unbound base and the pavement) and eventually results in a deformation (also per- manent) of the surface (see Werkmeister 2003, Habiballah and Chazallon 2005 and Fig- ure 13). Pavement tests show that 30 to 70% of surface rutting is attributed to this long- term mechanical process (Little 1993).
This version of the paper focuses on men, since early retirement rules differ for men and women. Results for women are available upon request and yield a qualitatively sim- ilar picture. We select all male UI-entries between 1980 and 2010 who qualify for their age-specific maximum PBD based on their working histories. This leaves a five year win- dow before the first year in the data (1975) and a three year window after the last (2013), allowing us to calculate UI eligibility for all individuals and unemployment durations for up to three years after UI entry. Since some of the requirements for maximum PBD eli- gibility, such as the duration over which claims could be accumulated, changed over the study period, the restrictions set on this duration differ slightly over time. We summarize these restrictions in Appendix Table B.4. Additionally, we exclude mining and steel con- struction from our analysis, since both sectors are known to have specific early-retirement rules for at least some of the periods. For other specific subgroups which face some, but less clear or pronounced early retirement rules we do not exclude cases a priori, but ad- dress them throughout the analysis. For the selected individuals, we construct detailed biographical information such as experience tenure or past exposure to unemployment.
While mounting evidence documents the impact of neighborhood violence on children’s performance on standardized tests, less is known about the underlying mechanisms driving this effect. One leading hypothesis is that exposure to violence increases absenteeism, forc- ing kids to miss critical instruction and reducing their performance on subsequent stan- dardized tests. There is, however, little evidence documenting a causal link between neigh- borhood violence and absenteeism due in part to a dearth of appropriate data. In this paper we exploit daily absenteeism data for NYC public school children, combined with detailed, blockface-level crime data, to estimate the impact of exposure to neighborhood violence on absenteeism. Our results provide credible causal estimates of the impact of neighborhood violence on absenteeism, contributing both to the ongoing debate about how neighborhoods affect kids’ outcomes and to the growing literature on the causes of school absenteeism.
The results presented here show that, in some areas, the BRAC 2005 announcement had effects quite similar to those reported in studies of prenatal stress and natural or man-made disasters. In a few communities that were projected to lose 10–20 percent of employment due to BRAC, the DoD announcement was associated with a significant decrease in mean gestational age. Gestational age trended downward in the months preceding the announcement, and the effect reached a peak just after the announcement of the BRAC list. The month of the announcement and the following month show a brief, sharp drop in gestational age of about 1.5 days in magnitude. The drop is characterized by a shift in births from 39 weeks and above to 37–38 weeks, a period called early- term and associated with long-lasting, negative effects on health and cognitive function. This result is supported by auxiliary, individual-level analyses using a full-term exposure instrument (Currie and Rossin-Slater 2013a), which reveal a strong negative link between expected gestational age and BRAC exposure during the third trimester. Over the key period between the DoD announcement and the commission’s decision, the mean gestational age was about half a day lower. These results are robust to many alternative specifications of the control group. The effects on the mean birth weight are more difficult to estimate but are consistent with the effects seen in gestational age. These results suggest that researchers and officials should pay greater attention to the negative psychological and health effects of major policy announcements.
Our dependent variable, the number of rms, accounts for the total number of rms at the municipal level and ranges from a minimum of 1 rm in few small localities to a maximum of more than 26,000 in the city of Zürich. Unlike recent papers that have focused on rm births or entry, our dependent variable is given by the stock of rms. Let us spend a few lines on this choice. The main argument given by studies using new rms data is that they control (although imperfectly) for the potential simultaneity bias that might arise because of local rms inuencing the tax setting process through the tax base. In other words, entrants are supposed to be more unlikely to signicantly inuence pre-existing local tax rates. However, even if this argument holds, we have decided to consider the stock of rms for several reasons. First of all, working with the whole sample considerably increases our number of observations. Second, it is worth mentioning that in Switzerland there is a large number of new rms that disappear after the rst years of activity. The magnitude of this share goes from 20% after the rst year of activity to 50% after ve years of activity, might be an issue in order to identify the medium and long- term impacts of the scal policy. 10 Finally, the fact of new rms being less likely to inuence
With public attitude toward obesity ranging from viewing it as a stigmatized difference to being a character flaw, U.S. law and publicpolicy have struggled with how to respond to the statistical discrimination against the obese in the markets. Sometimes obesity is viewed as an affliction, and sometimes as a personal choice. In 2002, the IRS recognized obesity as a medical condition, allowing tax deductions for certain medical expenses. Yet, in 2005, the House of Representatives passed the Personal Responsibility in Food Consumption Act to protect the fast food industry from legal liability (although the bill did not pass the Senate vote). In 2006, changes to the Health Insurance Portability and Accountability Act (HIPAA) paved the way for group health plans to charge lower premiums to the non-obese. In response, the State Employees’ Insurance Board of Alabama, for example, approved a policy under which obese employees will have to pay an additional $25 per month in health insurance beginning in 2011 if they do not make sufficient progress toward lowering their BMI. There has also been renewed interest in levying a tax on fatty foods and sugary drinks.
This paper is embedded in a growing body of work on the political economy of finance. My first contribution is to show that elections influence discretionary changes to financial regulation, in particular macroprudential (and microprudential) tools. As such, I provide some empirical evidence to suggest that political limitations are a po- tential weakness of the post-crisis consensus on how to address the build-up of sys- temic risk. My second contribution is to examine the circumstances in which political interference may impact regulation. I show that stronger central bank independence – and institutional frameworks more broadly – have very limiting moderating effects. At the same time, central bank independence is an important moderator for political cycles in monetary policy. The electoral cycle I document is also uncorrelated with proxies of the market power of financial institutions. Taken at face value, this sug- gests that it is not driven by powerful special interests exerting power over politicians. Consistent with theories of opportunistic regulatory cycles, I find that benign eco- nomic conditions characterized by higher economic and credit growth drive an easing of financial regulation prior to elections.
rates, job separation and job finding rates across workers of different age groups. The unemploy- ment rate faced by young workers is substantially higher than that of older age groups. Moreover, job separation rate for young workers is higher than the other two groups. The decomposition of the youth unemployment show that reduced level of job finding contributes more to their higher un- employment level as compared to the other two age groups. One reason for why young workers and less educated workers have higher incidence of job losses in the estimations is that they are assumed to be low skilled by employers. When the crisis hit and as a result the firms decide to downsize their number of employees to cut their costs, these workers are generally among the first group of people to lose employment. They have the highest probability of job loss over the years as compared to other groups. Bertola (2006) highlights that expenditure on active labour market policies (ALMPs) tends to increase the job finding especially among the young less educated workers as this group generally seeks help from public offices in finding employment. The strictness of Employment Pro- tection Legislation (EPL) tends to decrease the transitions from employment to unemployment for young workers. Hence provision of Public Employment Services (PES), such as job search assistance and Vocational Education and Training (VET), including apprenticeships can be a key to lowering youth unemployment and facilitating youth job finding rates. Policy-makers should enhance VET programs in order to provide an attractive alternative to general upper-secondary and tertiary ed- ucation and in order to better meet the skill requirements of the labour market. This could play an increasingly crucial role in the policy response to youth unemployment, in particular in the longer term.
when many SBHCs opened. Many centers opened in the mid-1990s (Figure 1), a time period in which welfare programs were reformed, the EITC was expanded, and many states were expanding public health insurance programs. The state- year fixed effects should account for these policy changes if they affected teen birth rates in all counties similarly in a state and year. But these policies dispro- portionately affected low-income communities, so they may have dispropor- tionately affected teen birth rates in these communities. Table 7 shows several robustness checks to compare with the results from Table 3. Columns (i) and (ii) of Table 7 reveal that the results are robust to controlling for state-year-median income fixed effects by allowing the state-year fixed effects to differ based on whether a given county’s median income in 1990 was in the bottom half of all counties in that state. Columns (iii) and (iv) of Table 7 show that the results are also robust to controlling for both state-year fixed effects and differential year fixed effects among the bottom 20% of counties in the US according to 1990 me- dian earnings. The estimates in columns (i) through (iv) are similar to those in Table 3, with somewhat larger estimates for the IV models. Table 7 thus sug- gests that our main results are not upwardly biased by state or national policies aimed at lower-income communities.
Table 1.7 provides some robustness checks for the prefered specification across both the control groups. Weighting the regression by 2 digit trade shares for ex- porter country in 2003 reduces the size of the coefficient and increases the standard errors, hinting that trade with smaller nations maybe driving the results 14 . Next, I test for whether the results are being driven by the fall in the positive gap or by a fall in the negative gap, by censoring the negative values to zero and the positive values to zero respectively. There are some puzzling aspects to the results. The driving force behind the fall in reporting gap should be a decrease in the positive side of the reporting gap for it to have a meaningful interpretation. This is indeed true for both control groups, however, I also find the negative of the reporting gap decreasing after the introduction of the Lacey Act. One potential reason for this can be that the trade in the 4th quarter of a year is recorded at different points in time by the importer and exporter country. For instance, exports may appear in the cur- rent year, while imports may appear the following year due to transit times. This, could potentially affect the negative gap to increase if exporter country reporting improves post the Lacey Act. However, the significant relationship between the pos- itive of the reporting gap and the Lacey Act provides suggestive evidence in favor of there being a meaningful treatment effect. Finally, I present the non-parametric estimates of the preferred specification. The omitted year dummy is 2007, the year before the introduction of the Lacey Act. The fall in the reporting gap only starts post 2008, consistent with the introduction of the policy.
These findings have important implications for education policy. First, they are relevant to the concern that disproportionate spending on special education drains resources from regular education; in 2000, the cost of educating the 13.2% of students who received special education services was $77.3 billion and accounted for 21% of spending on elementary and secondary education services (U.S. Office of Special Education Programs 2007; Chambers et al. 2004). Of course, disproportionate spending may be warranted if it generates positive spillovers for regular students, in addition to benefiting disabled students. An approximate dollar value of the benefit to regular students can be calculated from estimates of test score gains to non-disabled students and the labor market value of test score gains. A conservative estimate from Kane and Staiger (2002) is that a one standard deviation increase in math test scores is worth around $90,000 at age 9. This estimate implies that the receipt of special education by 13.2% of students yields math test gains of 0.06 standard deviations for each regular student, and with 40.9 million regular students, the test score gains alone are worth $220 billion, far surpassing the $77.3 billion cost of educating special education students. Second, as these gains may largely result from segregating disabled students, these findings suggest that peer effects should figure into the cost-benefit calculus of policies that mainstream special education students.
Proponents of school choice argue that the structure of the public educational system – where education is mainly provided by government with substantial monopoly power and largely no competition – leaves educational consumers with limited choice among schools. They further suggest that this may result in a disconnect between school quality and parents’ preferences. There is a growing literature in economics that suggests that expanding school choice could improve educational outcomes by increasing disadvantaged children’s access to high quality schools, and by causing underperforming schools to become more effective or to shrink as families “vote with their feet” (Friedman 1955; Becker 1995; Hoxby 2003; Belfield and Levin 2003). 1 These ideas have gained strong currency in education policy circles, leading to policy innovations such as open enrollment systems, magnet and charter schools, private school vouchers, and expanded public school choice for students in poorly performing schools.
While the first two essays show beneficial effects o f a targeted public program, government interventions can have unintended (and potentially harm ful) consequences as well. During the conflict in Vietnam, married men with dependents could obtain a deferment from the draft. In 1965, following President Johnson’s Executive Order 11241 and a Selective Service System announcement, this policy changed substantially in a way that provided strong incentives for childless American couples to conceive a first-born child. Since the changes were both unexpected and widely publicized, this is an ideal opportunity to study the effects o f policy on fertility. Information about the fecundity o f the U.S. population in the 1960’s and anecdotal evidence (e.g., conception of the current Vice President’s first daughter) suggest that young couples were ready to react quickly. In my third essay, I extract time series data from the Vital Statistics for 1963-68 and employ a difference-in-differences methodology. My analysis suggests that the number o f first births increased by 15,532 in June and August 1966 in response to the policy changes. Such an increase represents over 7% of the total number o f first deliveries and about 28% o f the Selective Service System calls for inductees in those months.
In this paper, I estimate the incentive cost of UI benefits associated with benefits paid at different parts of the unemployment spell. I use administrative data from the UK and exploit the variation in UI benefit profiles created by the dependence of UI benefit levels on the age of claimants. I first estimate the elasticity of total duration of unemployment with respect to benefits paid over different parts of the unemployment spell. These elasticities measure the magnitude of the behavioural response to UI benefits paid at different points of a spell. Similar to the standard Bailey-Chetty formula, the incentive cost of benefits paid at time t of the unemployment spell is fully captured by the corresponding fiscal externality, that is, the effect of increasing those benefits on government budget. I calculate these incentive costs for benefits paid in each part of the spell based on the corresponding estimates of duration elasticities. To provide a more detailed account of how the incentive cost changes with duration of unemployment, and to ensure robustness of the findings, I exploit the flexibility of the policy variation and hypothetically divide the benefit profile into periods of various lengths (e.g., 8-weeks, 12-weeks, 3 months, etc.) and repeat the estimation for each configuration.
Chapter 2, which is joint work with Peter Ganong, proposes a permutation test for the Regression Kink (RK) design—an increasingly popular empirical method for causal inference. Analogous to the Regression Discontinuity design, which evaluates discontinuous changes in the level of an outcome variable with respect to the running variable at a point at which the level of a policy changes, the RK design evaluates discontinuous changes in the slope of an outcome variable with respect to the running variable at a kink point at which the slope of a policy with respect to the running variable changes. Using simulation studies based on data from existing RK designs, we document empirically that the statistical signifi cance of RK estimators based on conven- tional standard errors can be spurious. In the simulations, false positives arise as a consequence of nonlinearities in the underlying relationship between the outcome and the assignment variable. As a complement to standard RK infer- ence, we propose that researchers construct a distribution of placebo estimates in regions with and without a policy kink and use this distribution to gauge statistical signifi cance.
Since the left had side of Equation 2.25 is directly observable in the data, this pins down the value of τ. γ is the return to human capital parameter in this model, and is used to match the absolute share of spending observed in the data in the 2000s. In this exercise I assume a fixed γ through out. One concern might be that the return to human capital in China has been increasing. Table 2.4 summarizes the yearly mincer return from year 1992 to 2009. It has increased significantly since the privatization in 1990s and then it has remained relatively stable in 2000s. For children born under the One-child Policy, when they enter labour market, the return has stabilized, so perhaps a constant γ may not be that a bad idea. I use γ to target the absolute expenditure share on education. Figure 2.6 summarizes the data and the model target on education spending.
In my first set of results, I consider the interaction among liquidity, information efficiency and welfare. First, I show that a tension between liquidity and informa- tion efficiency might arise: policy measures intended to promote liquidity might be harmful for information efficiency and vice versa and changes in the market environ- ment (such as risk-bearing capacity, number of large traders, information precision) can shift liquidity and information efficiency in opposite directions. Second, I show that a shock to the economic environment that has a positive direct effect on liq- uidity (an increase in risk-bearing capacity) may have a negative overall effect on liquidity ( liquidity paradox ). This is possible because the shock has a positive ef- fect on information efficiency and there is a tension between the two. Similarly, a positive shock to information efficiency (an increase in the precision of the signals) might have a negative overall effect on information efficiency ( information aggrega- tion paradox ). Third, when there is more competition between large traders, welfare might be lower. Moreover, all traders, even small ones, can be worse off as a result of more competition. This is possible because competition has negative effects on information efficiency. For a similar reason, breaking up a centralized market into two separate exchanges might improve welfare.
Theoretical models have drawn similar conclusions to the conventional wisdom. The ‘Law of 1/n’ (Weingast, Shepsle and Johnsen, 1981) models spending as a func- tion of the number of districts in a country, and finds that over-spending is increasing in the number of districts. The ‘veto player’ model (Tsebelis, 2002) focuses on the ability of a coalition of n ≥ 1 ‘veto players’ to change a policy. The intersection of sets of desirable policies is defined as the ‘winset’ for this coalition. It is straight-forward to understand the logic that the winset is decreasing in n. One way to ‘grease the wheels’ is by increasing the payoffs to veto players, which requires higher taxes in equilibrium. Austen-Smith (2000) finds that electoral rules that encourage a greater number parties will head to higher spending and transfers. Therefore these alterna- tive frameworks draw the same conclusion as the conventional wisdom: increasing the number of parties makes agreement more difficult, and thus higher spending (e.g. political pork) results.