Does Investing in School Capital Infrastructure Improve Student Achievement?

Does Investing in School Capital Infrastructure Improve Student Achievement? Kai Hong Ph.D. Student Department of Economics Vanderbilt University VU Station B#351819 2301 Vanderbilt Place Nashville, TN37235 kai.hong@vanderbilt.edu 615-322-2871 Ron Zimmer Associate Professor Vanderbilt University 230 Appleton Place Nashville, TN 37203 ron.zimmer@vanderbilt.edu 615-322-0722 February, 2014 Abstract: While there is broad support of the merit of additional expenditures for education among the public, there is greater debate within the research community. Some of the debate is an outgrowth of the lack of causal knowledge of the impacts of expenditures on student outcomes. To help fill this void, we examine the causal impact of capital expenditures on school district proficiency rates in Michigan using bond referendum election outcomes as a threshold for regression discontinuity design. Our results provide some evidence that capital expenditures can have positive effects on student proficiency levels. Keywords: Economics of Education Highlights: Examine the impact of capital expenditures on student outcomes Use various regression discontinuity approaches using election outcomes Provides some evidence that capital expenditures can have positive effects on proficiency levels. 1

1 Introduction Capital expenditures represent a significant investment into education. The U.S. Department of Education reports that as much as $70 billion are spent in a year on public school construction and repairs (U.S. Department of Education, 2012, Table 205). Despite this substantial investment, little is known about the effectiveness of these capital expenditures on student outcomes. Only a handful of studies have examined the issue (Jones and Zimmer, 2001; Schneider, 2002; Cellini et al., 2010). Of these, only Cellini et al. (2010) uses a causal design with a focus on the relationship between California capital expenditures and housing prices. The challenge of estimating the causal effect of capital expenditures is that bonds are not approved at random, but by districts that may have unobserved characteristics that not only make it more likely to approve a bond, but also more likely the district will have stronger student outcomes. Whether capital expenditures have an impact on student outcomes is part of larger debate on the merits of investing additional resources in education. While providing additional resources for education is a popular sentiment, some argue that past investments into education have not led to significant returns. For instance, Eric Hanushek and Alfred Lindseth note that between 1960 and 2005, inflation adjusted spending per pupil in the U.S. increased from $2,606 to $9,910 per pupil but was not accompanied by substantial improvement in national test scores, graduation rates, or the U.S. s relative rankings among developed countries (Hanushek and Lindseth, 2009, pgs 45-46). Hanushek (1986, 1996, 2003) found, in a series of literature reviews, no consistent relationship between increased inputs and student performance on test scores. These findings could lead one to question whether the U.S. should continue to invest more resources in education. However, some researchers argue that much of the literature that Hanushek relied upon was not always rigorous (Ferguson and Ladd, 1996) and have not controlled for the 2

possibility of reverse causality i.e., policymakers often invest more in schools performing poorly in hopes of improving outcomes. 1 Advocates for additional educational resources often point to evaluations of the Tennessee STAR experiment which used a causal research design of randomly assigning students to larger or smaller classes and found an inverse relationship between class size and student outcomes (Kruger, 1999; Kruger and Whitmore, 2001). While the Tennessee STAR experiment does provide some causal evidence of one input, the broader literature has provided little causal estimation of the relationship between student outcomes and educational inputs, including capital expenditures. 2 In this paper, we examine the impact of school capital expenditures on school outcomes by using fuzzy regression discontinuity design. We build on the Cellini et al. (2010) econometric approach and employ a dynamic regression discontinuity design (RDD) to obtain an unbiased estimate of capital expenditures on student outcomes in Michigan. Theoretically, districts that marginally pass a bond are quite similar both in observed and unobserved ways to those that marginally fail a bond. A comparison between these two groups could give us a causal estimate. We take into account the possibility that districts that fail to pass a bond may try to pass it again by extending Cellini et al. (2010) s dynamic sharp RDD to various dynamic fuzzy RDDs. The fuzziness comes from the fact that districts which fail a bond can propose another one in the same year. Cellini et al. (2010) found that passing a bond referendum had a positive effect on housing values in subsequent years. They also explored the effect of passing the referendum on student 1 On the flip side, it is possible that districts that are willing to spend more have families and students engaged in the educational production process, and these unobservable characteristics are not captured in these same studies, leading to an upward bias in the estimated relationship. 2 Another study that provides some rigorous results is Guryan (2001), which uses a combination of rigorous approaches to examine changes in state laws that have led to increase in funding in some districts, but not others. 3

outcomes in subsequent years and found mixed results, but it was a small part of their analysis. Our study focuses exclusively on student achievement and we examine whether there are heterogeneous effects by the previous expenditure levels of districts, the racial mix of students and the initial student achievements. In addition, unlike the Cellini et al (2010) paper, which did not discuss the issue of multiple elections, we incorporate approaches to address the issue. The remainder of the paper is organized as follows. Section 2 introduces the background on bond issuance in Michigan. Section 3 describes the data from Michigan and the overall analytical strategy. Section 4 examines the validity of our research design. Section 5 presents the empirical models and results. Section 6 interprets the findings and links the capital expenditure and achievement. Section 7 describes and presents a set of sensitivity analyses. Section 8 explores heterogeneous effects. Finally, Section 9 discusses the conclusions and implications of our results. 2. Issuing Bonds in Michigan Prior to 1994, Michigan primarily relied upon local property taxes to fund public education (Courant et al., 1995). Michigan began to rely more heavily on state funding of operating expenditures in schools with new legislation in 1994. Despite this policy change, funding of capital remained a local responsibility through a bond referendum in which the district must receive 50 percent approval from the electorate to approve a bond (Zimmer and Jones, 2005; Zimmer et al., 2010). Because Michigan school districts rely upon on a local referendum to approval capital expenditures, we are able to use an RDD as an identification strategy to estimate the impact of capital on student outcomes. For these referenda, we provide some general trends in the number of elections held and passage rates per year in Table 1, which descriptively summarizes all elections across years, As 4

the table indicates, the number of proposed measures decreased substantially over the years, which may be the result of the decline in Michigan s economy since the early 2000s. Table 1: School Bond Measure Summary Statistics Avg. bond amount per Avg. vote share (%) Number of bond Percent of passed pupil ($) Year (1) (2) Mean Std. deviation Mean Std. deviation (3) (4) (5) (6) 1996 164 51% 49.4 11.9 7312 5423 1997 149 43% 48.3 11.2 7764 5670 1998 107 41% 48.5 10.7 9472 7965 1999 117 48% 49.8 11.7 8348 6388 2000 117 49% 49.8 12.9 7694 5835 2001 108 63% 53.3 12.6 7487 6093 2002 83 59% 52.3 14.8 7882 6440 2003 70 39% 46.7 14.7 9820 10590 2004 71 63% 53.9 15.3 9243 6661 2005 58 40% 48.9 11.8 9981 10131 2006 59 44% 48.0 11.5 7771 6827 2007 68 47% 48.2 13.4 8033 8179 2008 44 57% 51.6 12.6 7598 4791 2009 50 70% 54.7 12.2 6087 6375 Note: Sample includes bonds with non-missing values in both of passage and vote share. Average bond amount per pupil is measured in constant year 2000 dollars. We should also note that one of the features that makes Michigan appealing for our analysis is that Michigan school districts are generally city/town based and are small relative to southern and western states, which often have county based school districts. Because of the relatively small districts with many districts only having one elementary, middle, and high school it easier to link the passage of a bond referendum to student achievement outcomes. These attributes make Michigan a strong place to evaluate the impact of capital expenditures. 3. Data and Analytical Strategy 3.1 Data Description We use data from the state of Michigan and the Common Core Data (CCD) from the National Center for Education Statistics (NCES). These sources include information on bond election outcomes as well as district expenditures, demographics and math and reading proficiency. We 5

only examine school district elections and exclude any county-wide elections because our outcome measure of student performance is at the district level. Our measures of academic achievement are the 1996-2009 4 th and 7 th grade district-level reading proficiency rates. 3 Proficiency rates are the metric by which schools and districts are held accountable under No Child Left Behind, but they do have certain disadvantages. First, changes in proficiency rates do not necessarily capture changes in performance across all students as the change only captures the performance of those students who switch from nonproficient to proficient status or vice versa. Second, we prefer to use the proficiency rate at the actual school which experiences a change in capital expenditures rather than a district-wide measure. However, as noted previously, in Michigan, most districts contain only a few schools in many cases one elementary, one middle, and one high school. Therefore, there should be a strong link of an approved capital bond and capital expenditures of schools within the district. Collectively, this suggests that a district-wide proficiency rate serves as a strong proxy for student achievement in the district. We examine the impact capital expenditures on intermediate outcomes of total expenditures and capital expenditures. We examine these outcomes to verify that districts that have approved bonds do indeed have additional capital expenditures for which bonds are issued. We also examine the baseline demographic information between districts that marginally failed a bond referendum relative to district that marginally passed to determine if there is balance in observables, which would provide suggestive evidence that there in balance on unobservables. 3.2 Challenges of Multiple Election 3 We do not have a consistent measure of math proficiency over the entire time horizon, and therefore, we focus exclusively on reading proficiency. However, for some our validity checks of RDD, we use baseline math proficiency as a check. 6

From a research perspective, ideally, each district would be able to propose one bond measure of capital expenditures. We would then observe whether the district passed the bond or not and examine whether the district that narrowly approved a bond measure had differential achievement levels than those schools that narrowly rejected a bond measure. In reality, each district could propose multiple elections, including a bond proposal after an initial bond measure failed. In addition, a district could strategically break up a large bond proposal into multiple bond proposals within the same year or even the same day in hopes that at least some of the capital expenditures can be authorized. These possibilities complicate the analysis. More specifically, it raises the possibility that the districts that propose multiple bonds are different from districts that choose to do one bond proposal. To examine this concern, we first descriptively examine whether single bond measures are more or less likely to pass relative to multiple bond measures on the same day or across multiple days in Table 2. Table 2: Comparison between Bonds Number of bonds (1) 7 Percent of passed (2) Avg. vote share (%) (3) Avg. bond amount per pupil ($) (4) Summary Single election 712 61% 52.4 9660 Multiple election 553 36% 46.9 6144 Same-day election 452 41% 47.3 4819 Different-day election 101 16% 45.3 12071 Difference (t test) Single and multiple elections -- 24%*** 5.5*** 3516*** Single and same-day elections -- 20%*** 5.1*** 4840*** Single and different-day elections -- 45%*** 7.1*** -2411*** Same-day and different-day elections -- 25%*** 2.0-7251*** Note: Sample includes bonds with non-missing values in both of passage and vote share. Average bond amount per pupil is measured in constant year 2000 dollars. It should first be noted that single elections account for well over half of all elections. However, there are substantial amount of multiple elections and most of them are held on the same day. In addition, single elections are more likely to be passed than multiple elections and multiple elections on the same day are more likely to be passed than those on different days. On

average, multiple bond proposed on different days has the largest bond amount per pupil. The same day multiple bond has the smallest bond amount per pupil. In addition to being correlated with bond characteristics, bond proposal may be correlated with characteristics of school districts. Table 3 shows the school district descriptive statistics by bond proposal patterns. Overall, the table does not suggest that these districts are very different in observed characteristics, including the crucial measures of student achievement as measures by proficiency levels. Nevertheless, unobservable differences between these school districts could exist and in the next section we lay out various analytical strategies to deal with the multiple elections. Current expenditures per pupil Total expenditures per pupil Percent point, free lunch program participants Construction capital outlay per pupil Instruction equipment capital outlay per pupil Land and structure capital outlay per pupil Total students Percent point, white students Table 3: School Districts Descriptive Statistics Proposed single measure only (1) 7312 (1754) [3536] 8977 (3010) [3536] 0.51 (1.75) [3489] 684 (1737) [3536] 43 (61) [3536] 92 (454) [3536] 3663 (10204) [3538] 85.60 (21.04) [3536] 66.65 (15.70) [931] 8 Ever proposed multiple measures (2) 7002 (3901) [2520] 8635 (4977) [2520] 0.35 (0.54) [2468] 737 (1785) [2520] 40 (52) [2520] 104 (505) [2520] 2653 (2914) [2520] 91.16 (10.68) [2520] 67.55 (14.47) [685] Ever proposed same day measures (3) 7002 (4227) [2128] 8673 (5312) [2128] 0.34 (0.58) [2128] 760 (1781) [2128] 39 (50) [2128] 100 (422) [2128] 2909 (3089) [2128] 91.58 (10.03) [2128] 68.92 4 th grade math proficiency (13.39) [574] 7 th grade math proficiency 57.57 59.78 60.97

(16.41) (13.89) (13.13) [928] [684] [573] 4 th 69.82 71.40 72.16 grade reading (18.48) (17.72) (17.24) proficiency [3389] [2481] [2090] 7 th 60.77 63.39 64.18 grade reading (19.05) (17.92) (17.54) proficiency [3391] [2476] [2087] Note: Current expenditures per pupil, total expenditures per pupil, construction capital outlay per pupil, instruction equipment capital outlay per pupil and land and structure capital outlay per pupil are measured in constant year 2000 dollars. Standard deviations are in parentheses and numbers of observations are in brackets. 3.3 Treatment Effect and Regression Discontinuity Design Our model builds on the Cellini et al. (2010) model in which y jt denotes the outcome in school district j at time t, e.g., the average student achievement measured as the percent of students in the district who achieve proficiency on the state exam. It can be related with bond passage in two ways. First, it is a function of one previous bond passage and other relevant variables. y jt = b j,t τ θ τ + e jt, for all τ when there was bond elections. (1) where τ is the time gap between the election and the year when the outcome was measured. b j,t τ indicates whether the bond passed τ year ago, and e j,t captures other factors affecting outcome at time t. If e jt and b j,t τ are uncorrelated, θ τ is identified as the intent-to-treat (ITT) effect of the bond passed τ year ago. The ITT incorporates the effect of passing a bond on the subsequent bond issuance. In other words, the ITT analysis provides insights into the policy decision of gaining successful passage of an initial referendum, not necessarily the effect of capital expenditures. Alternatively, y jt can also be expressed as a function of all bond passage before t and other relevant variables. y jt = τ τ=0 b j,t τ θ τ + τ e j,t τ τ=0 (2) 9

where τ and b j,t τ are defined in the same as before, and e j,t τ captures all of the other factors affecting outcome τ year ago. If b j,t τ is uncorrelated with τ τ=0 e j,t τ, θ τ is identified as the treatment on the treated (TOT) effect. It captures the pure effect of bond b j,t τ, conditional on bond issuance history from τ = 0 to τ = τ. In other words, the TOT analysis provides an actual estimate of the impact of capital expenditures based off the passage of an individual referendum. As shown in Cellini et al. (2010), the relation between ITT and TOT is τ θ ITT τ = θ TOT τ + θ db TOT j,t τ+ρ τ ρ ρ=1 db j,t τ where ρ measures time between t and τ; b j,t τ+ρ is a bond voted for ρ years after b j,t τ, the effect of which we are examining. In terms of interpretation, θitt τ is the effect of the policy of passing a bond by referendum and θtot τ is the effect of issuing a bond when there is no bond allowed after it. Usually bond issuance is not exogenous; b is correlated with the error terms. To get rid of such endogeneity we implement the regression discontinuity design (RDD) with vote share as the forcing variable. Controlling for a function of vote share, we can assume that the unobserved factors remained in the error terms are uncorrelated with bond issuance at the 50% threshold. Therefore, we can estimate the following equation for ITT: y jtτ = b jt θ τ + f(v jt, ω τ ) + α τ + β t + γ jt + e jtτ, (3) where y jtτ is the outcome in district j at time t, which is τ years after bond election b jt. f(v jt, ω τ ) is a function of vote share v jt and its coefficient ω τ, α τ is the year-gap fixed effect, β t is the calendar-year fixed effect, γ jt is the bond fixed effect and e jtτ is the error term. This equation identifies the ITT treatment effect of a bond passed exactly with 50% vote share. 10

For TOT we estimate the following regression: τ y jt = (b j,t τ θ τ + m j,t τ α τ + f(v j,t τ, ω t τ )) + λ j + κ t + μ jt, (4) τ=0 where y jt is the outcome in district j at time t, which is τ years after bond election b j,t τ, m j,t τ indicates whether a bond was proposed, λ j is the district fixed effect, κ t is the calendar year fixed, and μ jt is the error term. Equation (4) identifies the TOT treatment effect of a bond passed exactly with 50% vote share. In some specifications below, we estimate the third type of treatment effect of a bond when the bond passage is positively correlated with the indicator of whether the vote share is greater or equal to 50% but such relation is not deterministic there are bonds passed with vote share less than 50%. We first show the regression for an aggregate case. b j, t = 1{v j,f v j,f }φ + m j, t β + f(v j,f, ω) + κ t + ε j, t, (5) y j,tτ = b j, t θ τ + m j, t β + f(v j,f, ω) + α τ + κ t + μ j,tτ, (6) where m j, t and b j, t indicate whether at least one bond was proposed and passed before time t, 1{v j,f v j,f } is the indicator of whether the vote share of the first election during 1996-2009, if any, exceeds the threshold, τ is the years relative to the first election. Other parameters are the same as Equation (3) and (4). Equation (5) and (6) identify the local average treatment effect (LATE) for compliers that would pass at least one bond in the following τ years after the first election if the first bond was passed and would fail all of the bond proposed in the following τ years after the first election if they failed the first one. In Equations (7) and (8) we introduce the non-aggregate case which is comparable to Equation (4). We will discuss those specifications in details later. 11

b j,t τ = 1{v j,t τ v j,t τ }φ τ + m j,t τ β τ + f(v j,t τ, ω t τ ) + η j + φ t + ε jt (7) τ y jt = (b j,t τ θ τ + m j,t τ α τ + f(v j,t τ, ω t τ )) + λ j + κ t + μ jt, (8) τ=0 where the parameters on the bond passing indicators β τ, f, δ τ, η j, φ t and ε jt are defined in the same way as the parameters on achievement. m j,t τ and b j,t τ indicate whether at least one bond was proposed and passed τ years ago. 1{v j,t τ v j,t τ } is the indicator of whether the vote share τ years ago exceeds the threshold. Equation (7) and (8) jointly identify the local average treatment effect (LATE) for compliers that would pass the bond when the vote share exceeded the threshold and would fail the bond when the vote share was less than the threshold. 3.4 Multiple Election and Estimation Specification As noted previously, the presence of multiple elections in one year makes our estimation complicated. Given the panel data structure, we need to identify one treatment in each year, especially when we estimate the TOT. Moreover, uniquely identifying single election in each year simplifies the interpretation of estimation results. Because one could imagine a number of ways of estimating the ITT and TOT effects, we present a number of specifications that either relies upon different samples or different instruments (indicators) for the specification. Later, we test the validity of the various approaches to help narrow our focus on certain specifications, but nevertheless, we conduct the analyses across the various specification to add robustness to our results. In Table 4, we outline five specifications for ITT and four specifications for TOT. All of them identify at most one election in one district in each year, but the estimated effects are interpreted differently. Because these specifications use different identification strategies and samples, it allows us to examine the breadth of the implications of the results i.e., allows us to generalize 12

the results to more districts for which the effect may not be identified in one RDD specification but identified in others. Elections for analysis Table 4: Summary of Specifications of Multiple Elections Number of bond (1) Percent of passed (2) Avg. vote share (%) (3) Avg. bond amount per pupil ($) (1) All elections 1265 0.50 50.0 8121 Treatment effect estimated ITT: (weighted) average treatment effect of all bonds that were passed with 50% vote share. (4) (2.1) The first election during 1996-2009, parallel same day (2.2) The first election during 1996-2009, highest vote share Treatment effect estimated (3.1) The first election in a year, parallel same day (3.2) The first election in a year, highest vote share Treatment effect estimated (4) The election with the highest vote share in a year Treatment effect estimated (5) The fuzzy election in a year (the fuzzy election is passed if at least one bond is passed. The vote share equals to the average vote share in that year) Treatment effect estimated 513 0.52 50.5 8713 430 0.55 51.6 9921 ITT: (weighted) average treatment effect of the first bond during 1996-2009 passed with 50% vote share. LATE: average treatment effect of at least one bond passed in the past years for compliers with 50% vote share of the first bond during 1996-2009. The indicator (instrumental variable) is whether the first bond during 1996-2009 was passed. 1163 0.51 50.4 8151 935 0.57 51.9 9510 ITT: (weighted) average treatment effect of the first bond in a year passed with 50% vote share. LATE: average treatment effect of at least one bond passed in a year for compliers with the vote share of the first election in the corresponding year is 50%. The indicator (instrument variable) is whether the first bond in the corresponding year was passed. 936 0.60 52.3 9371 ITT: average treatment effect of the bond passed with 50% vote share, which is the highest in that year. TOT: average treatment effect of the bond passed with 50% vote share, which is the highest in that year. 936 0.55 51.2 8896 ITT: average treatment effect of passing at least one bond in a year with the average vote share equal to 50%. LATE: average treatment effect of passing at least one bond in a year for compliers with the average vote share equal to 50%. The indicator 13

(instrumental variable) is whether the fuzzy election was passed with average vote share greater or equal to 50%. Note: Sample includes bonds with non-missing values in both of passage and vote share. Average bond amount per pupil is measured in constant year 2000 dollars. In the second and third specifications regarding the first election, we can have multiple first elections on the same day. For ITT we can use all of them as parallel first elections or choose the one with the highest vote share. For LATE we only choose the first election with the highest vote share to avoid the cases with too many parallel election histories. ITT is obtained by fitting data to Equation (3), TOT is obtained by Equation (4) for Specification 4 (which is the specification used by Cellini et al. (2010)), and LATE is obtained by Equations (5) and (6) for Specification 2.2, and Equations (7) and (8) for Specification 3.2 and 5. In these analyses, there are three types of compliers all of them would pass at least one bond if the corresponding vote share was not less than 50%. In Specification 2, the compliers are school districts that would not pass any bonds after failed the first one from 1996 to 2009. In Specification 3, the compliers are school districts that would not pass any bonds in a year if they failed the first one in that year. In Specification 5, the compliers are school districts that would not pass any bond in a year with the average vote share of all bonds in that year less than 50%. 4 4 Validity of the Regression Discontinuity Design Before implementing the various specifications to address the multiple election challenge, we first check the validity of the general RDD by testing whether, at the threshold, there is a discontinuity in bond frequency or background variables and bond characteristics for all bonds. We then examine the validity of the various specifications above as they have different identification strategies and samples. In this section we will present the validity check for the first specification in detail and briefly show the results for others. 4.1 Bond Frequency and Density Test 4 In contrast, in Specification 5 the non-compliers are school districts that would barely pass a bond with failed ones with low vote share which drove the average vote share lower than 50%. 14

RDD produces unbiased estimate of effects of bond authorization on subsequent student achievement, θ τ, if there is no manipulation of the bond proposal. We first examine whether there is any evidence of manipulation by displaying the distribution of all elections observed in our data. According to McCrary (2008), discontinuity in density around the threshold indicates the risk of endogenous sorting around the threshold which violates the RDD assumptions. In our study, manipulation could occur if districts were perfectly able to predict outcomes based on the features of the bond (e.g., amounts, length of the bond, the type of capital investment) or if they tried several time in hopes of getting the bond passed. If districts could perfectly predict outcomes based on the bond features, then savvy districts would fine tune the bond features to gain exactly 50 percent of the vote. One means of fine tuning bonds is by marginally changing the features of a bond in repeated elections until the bond passes. These savvy districts could be different in unobserved ways from districts that give up after one failed election. However, while school districts can get information about electorate s preference, including through the results of previous elections, it seems very unlikely that a school district can perfectly predict the vote share. Therefore, such manipulation is restricted by imperfect prediction of the vote share and the fact that districts are allowed to hold elections only so many days in a year. As a result, a district that narrowly passes a bond is still likely to be similar both in observable and unobservable ways to districts that narrowly fail to pass a bond. Nevertheless, we need to test the bond frequency around the threshold to provide assurance of no manipulation. First, we display the distribution of all elections by vote share in Figure 1. The figure shows an approximately normal distribution that peaks at the 50 percent threshold, which provides no evidence of endogenous sorting. 15

Figure 1: Distribution by Vote Share, All Elections (1996-2009) In itself, this is not enough assurance that there is no manipulation. Therefore, we also perform McCrary s density test as shown in Figure 2. The discontinuity estimate is 0.19 with standard error 0.13. Overall, we find no evidence of endogenous sorting for all of the elections. Figure 2: Density of Bond by Vote Share, All Elections (1996-2009) 0 1 2 3 4 0.2.4.6.8 1 16

4.2 Balance Check of Background Variables To further examine whether districts that pass or fail a bond are different, we conduct a balance check using pairwise comparisons. This balance check is analogous to randomized control trial (RCT) studies that examine whether the randomization created a true random sample of treatment and control groups (Abdulkadiroglu et al., 2009; Cullen et al., 2006; Engberg et al., forthcoming; Bifulco, 2012). In these cases, researchers examine whether there are statistically significant differences in observable characteristics. If these observable characteristics are not statistically different more than what would be expected by random chance, then researchers typically conclude that the samples of treatment and control schools are balanced both on observable and unobservable characteristics. In Table 5, we first examine all districts in which bonds passed and failed, not just those near the cutoff. We do not expect the complete population of districts that passed and failed bonds to be similar. In fact, differences in observable characteristics among this population would suggest that a naïve estimate in the differences in outcomes across these two populations would be biased. Columns (1) and (2) provide means over district-year observations from the year just before a bond passed (1) or failed (2). Column (3) compares the means of the two samples with a t-test. In general, the results in Columns (1), (2) and (3) suggest that districts that passed an election are more advantaged in most aspects. They have larger general, current, and capital (i.e., construction, instructional equipment, and land) expenditures per pupil. In addition, these districts are larger in size but generally do not differ from their counterparts in racial composition. Finally, their students perform better in all subjects. Table 5: Pre-Estimation Balance Check, Background Variables (All Elections, 1996-2009) Passed a measure (time t-1) (1) Failed a measure (time t-1) (2) Difference (t test) (3) Year before measure (t-1) (4) 17

Current expenditures per pupil Total expenditures per pupil Construction capital outlay per pupil Instruction equipment capital outlay per pupil Land and structure capital outlay per pupil Percent point, free lunch program participant Total students Percent point, white students 4 th grade math proficiency 7 th grade math proficiency 4 th grade reading proficiency 7 th grade reading proficiency 6922 (1139) [551] 8106 (1804) [551] 331 (1012) [551] 50 (64) [551] 92 (414) [551] 0.48 (2.00) [535] 3455 (5674) [551] 89.73 (15.00) [551] 68.80 (14.58) [200] 61.04 (15.13) [201] 67.59 (17.44) [529] 58.74 (17.22) 6676 (894) [558] 7452 (1286) [558] 142 (625) [558] 53 (60) [558] 25 (105) [558] 0.32 (0.40) [544] 2617 (3012) [558] 90.38 (12.90) [558] 65.62 (14.54) [273] 57.35 (13.88) [272] 62.29 (18.82) [553] 53.83 (18.21) 246*** (61) 654*** (94) 189*** (50) -3 (4) 68*** (18) 0.15* (0.09) 838*** (272) -0.66 (0.84) 3.18** (1.36) 3.69*** (1.34) 5.30*** (1.10) 4.91*** (1.08) -66 (110) [13439] -364** (151) [13439] -176** (69) [13439] -0 (5) [13439] 14 (27) [13439] 0.00 (0.17) [13164] -51* (30) [13443] 1.11 (0.78) [13439] -1.08 (1.14) [2275] -0.23 (1.19) [2272] 0.68 (0.60) [13251] 0.98 (0.63) [13243] [530] [552] Note: Current expenditures per pupil, total expenditures per pupil, construction capital outlay per pupil, instruction equipment capital outlay per pupil and land and structure capital outlay per pupil are measured in constant year 2000 dollars. Numbers in parentheses are standard deviations in Column 1 and 2, standard errors in Column 3, and clustered standard errors by school district in Column 4. Sample size for columns 1, 2 and 4 are highlighted at the bottom of each cell. In Column 4 we assume that bond does not have any effect on outcomes two years before the election, and set those observations as the reference group. Thus 2 τ 13. Focusing on the population most critical to the RDD approach, Column (4) presents coefficients from estimating Equation (3) for each variable as dependent variable. The results suggest balance among most of observable characteristics in districts in which bonds narrowly passed and districts in which bonds failed, with no dramatic jump in observable characteristics at the threshold. The districts which passed a bond had slightly less total students, expenditure and 18

construction capital outlay per student in the year before the measure. Later, we will compare Specification 1 with other specifications and show that we have even less concern of balance of observables for these specifications. We also conduct a falsification test in which we examine whether there was any difference in those background variables the year before an election relative to the outcomes two and three years after the election. While we do not display the results here to conserve space, in each case, as expected, we get similar results as Table 5; for most of them we found no significant jump at the threshold in the year before the election or any jump relative to two and three years after the election, providing support for the validity of our research design. 5 4.3 Balance Check of Bond Characteristics So far, we have examined the characteristics of the districts near the threshold for the overall population of bonds using Specification 1, but have not examined whether there are observable differences in characteristics of the actual proposed bonds near the threshold. One might expect districts with bonds that successfully passed may have different bond characteristics than bonds that failed to pass. We examine this issue by examining four correlated bond characteristics: year of referendum, bond amount per pupil, repayment time and estimated yearly millage rate. Bond amount per pupil measures the level of investment and repayment time is the length of the bond. Those two, with the taxable local property, determine the estimated yearly millage rate, which measures the tax burden. 5 The results are available upon request. To conduct the analysis, we create figures where the outcomes are plotted by the vote share on the x-axis. The 50% threshold is normalized to 0 and each unit bin represents 5% relative percentage of yes. There are 20 bins and half of them are on the left side of the threshold. The y-axis represents the average of corresponding outcomes conditional on year fixed effects. The coefficients of bins (β) are estimated in the following regression: 20 y i = α t + β j b j + ε, where α t is the year fixed effect, b j is the jth bin. y i is the outcome in i relative year to the election. j=1 19

Table 6 presents the balance check of bond characteristics for all bonds. 6 Again, for this population, differences would not be unexpected. It is clear that a bond with less amount per pupil, shorter repayment time and smaller millage rate is more likely to be passed. However, when we check by the regression discontinuity estimation of Equation (3) for the population of interest, such difference in bond characteristics vanish. There is no evidence of endogenous sorting of bond around the threshold. Table 6: Pre-Estimation Balance Check, Bond Characteristics (All elections, 1996-2009) Year of referendum Bond amount per pupil Repayment time Millage rate Passed a measure (time t) (1) 2001.2 (4.0) [634] 7487 (5927) [634] 24.33 (5.29) [261] 2.62 (1.75) [261] Failed a measure (time t) (2) 2000.7 (3.8) [639] 8758 (7681) [639] 25.80 (4.64) [224] 3.22 (2.27) [223] Difference (t test) (3) 0.5** (0.2) -1271*** (385) -1.48*** (0.46) -0.60*** (0.18) Year of measure (t) (4) 0.08 (0.31) [2959] -203 (700) [2959] -0.40 (0.94) [1210] -0.12 (0.56) [1209] Note: Sample includes bonds with non-missing values in both of passage and vote share. Average bond amount per pupil is measured in constant year 2000 dollars. Numbers in parentheses are standard deviations in Column 1 and 2, standard errors in Column 3, and clustered standard errors by school district in Column 4. Sample size for columns 1, 2 and 4 are highlighted at the bottom of each cell. In Column 4 we use the same estimation strategy as Table 5, Column (4), with a modification that θ 1 and ω 1 are also free. 4.4 Validity Check of Other Specifications Table 7 summarizes the validity check of specifications listed in Table 5 other than Specification 1, including the density test, balance check of background variables and bond characteristics. Specification 2.1 and 2.2 pass all of the tests. Specification 3.1 shows unbalanced 6 For repayment time and millage rate we have data only in 2000-2005. We also predict the missing repayment time and millage rate by OLS fitted value, using bond amount per pupil, median income and median house value of the school districts, and the percent of students who enrolled in the free lunch program as explanatory variables. Median income and median house value are only available in one year and we use them as constant approximations during 1996 and 2009. For the predicted repayment time and millage rate we get similar results; there is no significant discontinuity at the 50% threshold. 20

total and construction expenditures. Specification 3.2 only marginally fails the test for percent free lunch with a very small magnitude (0.21%). 7 Interestingly, Specification 4, which is the specification used by Cellini et al., and 5 have the problem of unbalanced density in our data. Because specifications 4 and 5 performed poorly on the balance check and because Specification 3.2 allows us to distinguish the effect of passing a bond within a given year (which specifications 2.1 and 2.2. cannot) we focus on Specification 3.2 when we present our results. However, throughout the remainder of our paper, we do present the results of the other specifications to add robustness to our results. Table 7: Summary of Validity Check 2.1 (1) 2.2 (2) Density Test 0.01 0.03 (0.14) (0.22) Balance of Background Variables, Year before Measure (t-1) -327-230 Current expenditures per pupil (364) (224) [6322] [5258] Total expenditures per pupil Construction capital outlay per pupil Instruction equipment capital outlay per pupil Land and structure capital outlay per pupil Percent point, free lunch program participants Total students Percent point, white students -676 (467) [6322] -241 (164) [6322] 12 (11) [6322] 7 (29) [6322] 0.10 (0.41) [6203] -92 (68) [6324] 0.31 (0.48) [6322] -397 (327) [5258] -172 (176) [5258] 6 (14) [5258] -12 (45) [5258] 0.59 (0.38) [5164] -45 (173) [5260] -0.14 (0.54) [5258] Specification 3.1 3.2 (3) (4) 0.16 0.19 (0.14) (0.15) -94 (125) [12299] -376** (169) [12299] -166** (74) [12299] 2 (5) [12299] 7 (29) [12299] 0.03 (0.17) [12050] -47 (29) [12303] 1.03 (0.81) [12299] -66 (70) [9816] -98 (140) [9816] -31 (103) [9816] -1 (7) [9816] 17 (38) [9816] 0.21* (0.11) [9625] -28 (48) [9820] 0.89 (0.93) [9816] 4 (5) 0.43*** (0.16) -21 (67) [9829] -57 (139) [9829] -15 (102) [9829] -2 (7) [9829] -1 (37) [9829] 0.17 (0.11) [9638] -35 (46) [9833] 0.89 (0.91) [9829] 5 (6) 0.42*** (0.15) -23 (69) [9829] 34 (147) [9829] 58 (106) [9829] 3 (7) [9829] 2 (37) [9829] 0.14 (0.12) [9638] -45 (48) [9833] 0.92 (0.98) [9829] 4 th grade math proficiency 0.66 2.30-1.27-0.12 0.59 0.07 7 The average total number of students is 3017, so 0.21% is approximately equivalent to 6 students. 21

(2.03) [1337] (3.63) [1105] -0.20-1.00 7 th grade math proficiency (1.86) (2.98) [1334] [1102] 0.16 0.17 4 th grade reading proficiency (1.27) (1.94) [6163] [5121] -0.55-0.21 7 th grade reading proficiency (1.16) (1.65) [6157] [5118] Balance of Bond Characteristics, Year of Measure (t) -0.37-0.21 Year of referendum (0.39) (0.43) [1133] [932] Bond amount per pupil Repayment time Millage rate 1179 (1142) [1133] 1.17 (3.31) [425] 0.52 (1.49) [425] 3578 (3942) [932] 5.20 (25.13) [350] 12.62 (24.71) [350] (1.33) [2052] -0.49 (1.44) [2049] 0.50 (0.62) [12113] 0.81 (0.65) [12107] 0.27 (0.33) [2708] 579 (803) [2708] -0.12 (1.05) [1091] 0.18 (0.61) (2.14) [1635] -0.90 (2.44) [1632] 0.01 (0.90) [9652] 0.44 (0.96) [9650] 0.48 (0.35) [2110] -126 (1326) [2110] -2.08 (3.32) [855] -0.29 (1.02) (2.12) [1638] -0.24 (2.46) [1635] 0.26 (0.90) [9665] 0.61 (1.00) [9663] 0.23 (0.35) [2114] -344 (1235) [2114] -1.24 (3.08) [857] -0.29 (0.99) (2.19) [1638] 0.44 (2.46) [1635] 0.48 (0.90) [9665] -0.03 (0.97) [9663] 0.06 (0.38) [2181] 953 (1223) [2181] -1.99 (3.58) [894] -0.00 (1.09) [894] [1090] [854] [857] Note: Sample includes bonds with non-missing values in both of passage and vote share. Current expenditures per pupil, total expenditures per pupil, construction capital outlay per pupil, instruction equipment capital outlay per pupil, land and structure capital outlay per pupil and average bond amount per pupil are measured in constant year 2000 dollars. Numbers in parentheses are clustered standard errors by school district. Sample size are highlighted at the bottom of each cell. For background variables we assume that bond does not have any effect on outcomes two years before the election, and set those observations as the reference group. Thus 2 τ 13. For bond characteristics θ 1 and ω 1 are also free. 5 Effect of Passing Bond on Achievement 5.1 ITT Estimation In terms of achievement, we first perform the ITT analysis, which provides insights into the effect of passing an initial bond. ITT is estimated by Equation (3) with observations 2 τ 13. 8 f(v jt ) is a cubic function of v jt. θ 2, θ 1, ω 2 and ω 1 are restricted to zero. By doing this we assume that passing bond does not have any effect in previous years. Standard errors are clustered by school district j. Table 8 and 9 present the estimated ITTs on 4 th and 7 th grade reading proficiency. 8 We also fit the model with all observations 13 τ 13 and get similar results. 22

Table 8: ITT on 4 th Grade Reading Proficiency Specification 1 2.1 2.2 3.1 3.2 4 5 Relative year τ (1) (2) (3) (4) (5) (6) (7) -0.72-0.89-1.28-0.86-1.62** -1.72* -1.45* 0 (0.54) (1.05) (1.47) (0.57) (0.80) (0.82) (0.80) -0.46-0.71-1.84-0.65-1.49-1.26-0.48 1 (0.62) (1.07) (1.59) (0.66) (0.97) (0.97) (1.00) 0.17 1.05 0.65 0.08-0.70-0.77-0.94 2 (0.68) (1.25) (1.76) (0.78) (1.09) (1.06) (1.08) -0.06 1.30 0.90 0.10-0.50-0.76-0.22 3 (0.66) (1.11) (1.71) (0.74) (1.12) (1.10) (1.16) -0.19 0.60-0.06-0.26-0.58-0.75-0.66 4 (0.62) (1.04) (1.69) (0.69) (1.10) (1.06) (1.12) 0.20 0.35 0.15 0.11 0.07-0.08-0.21 5 (0.61) (1.03) (1.66) (0.67) (1.09) (1.07) (1.11) 0.16 0.76 0.17 0.13-0.34-0.60 0.43 6 (0.67) (0.99) (1.69) (0.72) (1.19) (1.21) (1.24) 0.06-0.63-1.05-0.32-0.72-0.38-0.59 7 (0.67) (1.04) (1.71) (0.74) (1.20) (1.17) (1.28) -0.17 0.23 0.16-0.66-0.74-0.30-0.84 8 (0.72) (1.06) (1.73) (0.81) (1.23) (1.23) (1.32) -0.28-0.12-0.37-0.63-0.87-0.57-0.59 9 (0.74) (1.06) (1.79) (0.85) (1.31) (1.28) (1.37) -0.52-0.83-1.10-0.72-0.91-0.59-0.51 10 (0.78) (1.11) (1.84) (0.88) (1.34) (1.28) (1.37) -1.21-1.72-2.02-1.93* -2.24-1.62-1.83 11 (1.01) (1.27) (1.98) (1.15) (1.55) (1.52) (1.58) -1.37-0.84-0.62-0.81-0.70-1.37-2.44 12 (1.15) (1.42) (2.10) (1.27) (1.71) (1.74) (1.78) -1.18-0.40-0.27-0.71-0.65-0.48-2.12 13 (1.58) (1.68) (2.36) (1.67) (2.09) (2.18) (2.30) Note: Numbers in parentheses are clustered standard errors by school district. Sample sizes are 13251, 6163, 5121, 12113, 9652, 9665 and 9665 respectively. Table 9: ITT on 7 th Grade Reading Proficiency Specification Relative year τ 1 2.1 2.2 3.1 3.2 4 5 (1) (2) (3) (4) (5) (6) (7) 0 0.56 1.79 3.77** 0.59 0.81 0.79 0.45 (0.63) (1.28) (1.59) (0.67) (0.82) (0.81) (0.82) 1-0.05 1.19 1.40-0.26-0.87-0.71-0.82 (0.66) (1.18) (1.64) (0.69) (0.91) (0.91) (0.96) 2-0.66 0.28 1.14-1.16-1.65-0.75-0.52 (0.68) (1.18) (1.76) (0.72) (1.01) (0.98) (1.04) 3-0.14-0.14 0.84-0.40-1.03-0.51-0.34 (0.70) (1.17) (1.75) (0.75) (1.01) (0.98) (1.00) 4-0.01-0.04 0.25-0.21-1.12-0.42 0.15 (0.64) (1.11) (1.68) (0.70) (0.99) (0.97) (1.07) 5-0.66 0.28 0.98-0.56-1.16-1.14-0.94 (0.61) (1.08) (1.71) (0.68) (0.95) (0.95) (1.00) 6-0.33 0.22 0.70-0.62-1.37-0.85-0.85 23

(0.69) (1.08) (1.73) (0.77) (1.13) (1.15) (1.21) 7 0.55 1.19 1.58 1.01 0.71 0.37-0.35 (0.68) (1.17) (1.79) (0.78) (1.13) (1.10) (1.19) 8 0.05 0.77 1.52-0.02-0.38 0.06 0.28 (0.71) (1.14) (1.78) (0.80) (1.13) (1.12) (1.25) 9 0.01 0.66 1.44-0.19-0.22 0.30 0.11 (0.82) (1.19) (1.86) (0.94) (1.21) (1.18) (1.31) 10-0.37-0.61-0.11-0.63-1.36-0.65-0.66 (0.87) (1.31) (2.02) (1.02) (1.37) (1.30) (1.45) 11 0.10 0.09 0.75-0.83-1.68-0.31-0.27 (0.96) (1.23) (1.94) (1.10) (1.47) (1.39) (1.62) 12-0.58-0.72 0.47-1.09-1.66-1.41-0.30 (1.14) (1.37) (2.07) (1.25) (1.59) (1.45) (1.69) 13-0.66-0.92 0.87-1.50-1.11-0.43-0.11 (1.50) (1.69) (2.29) (1.66) (1.89) (1.95) (2.09) Note: Numbers in parentheses are clustered standard errors by school district. Sample sizes are 13243, 6157, 5118, 12107, 9650, 9663 and 9663 respectively. Overall, the analysis suggests little effect of passing a bond on subsequent reading proficiencies in any specifications. This indicates that the policy of investing in infrastructure via referendum in itself will not necessarily lead to improved student achievement. Part of why this might be true is that passing an initial bond may reduce the likelihood of passing a subsequent bond. To explore this possibility, we estimate the ITT effect of passing a bond on the possibility of passing subsequent bonds using the same estimation strategy as Specification 1, which is shown in Figure 3. As the figure suggests, a school district passing an initial bond is less likely to pass another bond in the short term. We next explore the effect of passing each individual bond rather than the initial bond by estimating the TOT and LATE effects, which gives us a greater sense of the actual effect of capital expenditures. 24

Figure 3: ITT Effect on Possibility of Passing Subsequent Bonds 5.2 TOT and LATE Estimation TOT is estimated via Equation (4) for Specification 4, using the conventional panel data estimation and is the specification used by Cellini et al. (2010). LATE is estimated via Equation (5) and (6) for Specification 2.2 and Equation (7) and (8) for Specification 3.2 and 5, as a two- step fixed effect model (Papke and Wooldridge, 2008). 1{v j,t τ v j,t τ } serves as the set of instruments for b j,t in the first stage. Standard errors are clustered by school districts for both estimation and obtained by bootstrap with 1000 repetitions for LATE. LATE estimation is consistent with fuzzy RDD; the relation between indicator 1{v j,t τ v j,t τ } and bond passage b j,t is not deterministic. To examine the validity of this approach, we first graph whether the probability of passing a bond is discontinuously changed with magnitude 25

less than 1 across the threshold of the vote share. Figure 4 shows the result for Specification 3.2, which again, is our preferred specification. 9 Figure 4: Graphic Checks of Probability of Passing an Election The probability of passing a bond jumps substantially at the threshold, but the magnitude is less than 1, which provides some support for the fuzzy RDD approach. In addition, we also conducted a falsification test to examine whether there was a discontinuity either one year earlier or two years later and found no such discontinuity, again providing support for the fuzzy RDD approach. The graphic checks for other specifications present similar results. Because we rely upon an instrument to consistently estimate the effects, we also examine whether we have evidence of a weak instrument across the different outcomes examined. 10 Overall, the analysis 9 Elections with vote share of 50.001% to 55% are in bin 1, elections with vote share of 45.001% to 50% are in bin - 1, etc. Each point represents the average of corresponding variable conditional on year fixed effects. The value of bin -1 is normalized to 0. 10 Bound et al. (1995) argue that an analysis may be better off using an OLS model as opposed to instrumental variable (IV) approach if there is a weak correlation between the instrument and the endogenous variable(s) because the relationship between the instrument and error term can be magnified (Wooldridge, 2010). For Specification 3.2, Figure 4 informally shows no evidence of weak instrumental variable. To formally test the possibility of a weak correlation 26