School finance centralization and revenue levels: evidence from a school finance reform

ABSTRACT

This paper studies whether the centralization of public school finance affects school revenue levels. The theoretical framework indicates that centralization has price and income effects on the pivotal voter’s demand for school revenue, but the overall effect is ambiguous. A public school finance reform in Michigan (U.S. state), which centralized its school finance system by restricting local discretion on school revenue, provides a good policy variation for a quasi-experimental design. Using district-level panel data on school finance in Michigan and neighboring states over the fiscal-year period of 1990–2004, I find that the reform has a negative effect on revenue levels. The sixth year after the reform and onwards, the reform reduces per-pupil revenue by $1,300 on average. The reform reduces revenue levels in both low- and high-revenue districts, but the higher-revenue districts tend to sustain more pronounced reductions.

KEYWORDS:

• School finance centralization
• school revenue levels
• school finance equalization

1. Introduction

In the United States, public education for children has been traditionally financed through local property taxes; as a result, school revenue strongly correlates with local property wealth. The Tiebout model implies that the provision of school services can be efficient under the local financing system, in which residents “vote with their feet”; meanwhile, substantial school revenue inequalities can arise. Since the 1970s, many lawsuits and legislative actions have occurred across the country in an effort to reduce revenue inequalities, bringing significant changes to the existing school finance system in some states.

Most state-level public school finance reforms have merely changed grant formulas so as to favor low-income school districts, leaving relatively intact districts’ discretion on revenue levels. On the other hand, in Michigan (U.S. state), public school finance reform sharply reduced local property taxes and introduced a foundation aid system, so that school districts have become highly dependent on state funding. Thus, the reform is considered one of school finance centralization with limited local supplementation (Loeb, 2001). In the public finance literature, the concept of fiscal centralization/decentralization usually relates to the degree of either taxing or spending power among subnational governments. In this paper, the term “school finance centralization” means that the taxing power of district governments has been conferred on the state government, thus possibly equalizing school revenue among districts through state grants.

The Michigan school finance reform may achieve revenue equality through centralization, but there may be consequences for school revenue levels. Fischel (1989, 1996) argues that centralization is unpopular in high-income districts, so that they may not be financially supportive of such a system which redistributes resources from high-income districts to low-income districts. It can be re-expressed that centralization increases high-income districts’ tax price (defined as the amount of local tax for one additional dollar of school spending). Silva and Sonstelie (1995) incorporate this argument through their analysis of the price and income effects of centralization on spending levels. In their model, there exists the voter who is pivotal in determining the spending level, and the price and income effects depend on the pivotal voter’s tax price and income. With the assumption about who the pivotal voter is and a tax price schedule, they suggest that the income effect is negative and the price effect is positive.

The potential effects of centralization on school revenue or spending have drawn the attention of several researchers. Manwaring and Sheffrin (1997) estimate the effects of state-level school finance reforms on the desired level of school spending across the United States, by entering interaction terms between a reform dummy and several control variables in their regression model. Their results suggest that desired school spending levels fell in California, where a reform centralized school finance, but increased in other states where reforms did not centralize school finance to the same extent. Downes and Shah (2006) also enter interaction terms between school reform dummies and other control variables and find that while court-ordered reforms reduce the spending level, legislative reforms increase it. Their results may imply that constraints on local discretion on school revenue have a negative effect on the mean spending level, as court-ordered reforms usually impose tighter constraints on local discretion. Hoxby (2001) focuses on tax price and its effect on mean school spending; she finds that, at the district level across the country, a higher tax price leads to lower per-pupil school spending, which in turn implies that less local discretion would result in lower spending.

In addition, there exists a voluminous body of empirical literature on the effects of state-level school finance reforms on school spending across the United States. Those studies generally find that school finance reforms reduce school spending inequalities among districts (e.g., Card & Payne, 2002; Murray et al., 1998) and increase mean per-pupil spending (e.g., Jackson et al., 2016; Lafortune et al., 2018; Sims, 2011a, 2011b). However, many of the school finance reforms did not entail the significant centralization of school finance, and so the estimated effects provide no clear implication with respect to centralization; most reforms modified grant formulas to equalize school revenue without substantially conferring school revenue discretion from local governments to the state government. Based on the calculated tax prices in Hoxby (2001), it seems that of the 34 school finance reforms that occurred during the 1970–1990 period, only two (i.e., those of California and New Mexico) might be classified as centralization.

This present paper estimates the effect of the Michigan school finance reform on the level of school revenue, considering the reform as school finance centralization. The paper employs the difference-in-differences event study method that dynamically compares the districts of Michigan to those in neighboring states (Illinois and Indiana); here, the neighboring states comprise the control group. School districts are grouped together in terms of pre-reform level of school revenue, and the heterogeneous effects of the reform are examined across revenue groups. I find that the reform has a negative effect on revenue levels. The sixth year after the reform and onwards, the reform reduces per-pupil revenue by $1,300 on average. The reform reduces revenue levels in both low- and high-revenue groups, but the higher-revenue groups tend to sustain more pronounced reductions.

This paper is distinguished from existing school finance reforms studies, on two bases. First, those studies scarcely investigate the effects of school finance centralization on revenue levels. Although multiple national-level studies examine the effects of reforms on spending levels (e.g., Card & Payne, 2002; Downes & Shah, 2006; Lafortune et al., 2018; Manwaring & Sheffrin, 1997), the reforms differ considerably from state to state, and they frequently bring little centralization to existing school finance systems. Therefore, it is difficult to directly link their results to the consequences of centralization, even though some of the studies attempt to draw out the implications of centralization.

Second, the effects of the Michigan school finance reform on revenue levels have not been thoroughly investigated. Although multiple papers examine the Michigan school finance reform, they tend to focus on revenue/spending equalization among districts, resource allocation among spending types, and educational attainment (Chakrabarti & Roy, 2015, 2017; Hyman, 2017; Papke, 2005; Roy, 2011; Zimmer & Jones, 2005). Chaudhary (2009) estimates the effects of the Michigan school finance reform on the log of per-pupil spending, but the effect on spending level is not the focus of her study. Furthermore, my paper improves upon her empirical model by accounting for the dynamic response of the outcome variable.¹

The remainder of this paper is organized as follows. Section II describes the Michigan school finance system in the pre- and post-reform periods. Section III briefly presents the theoretical framework by which to examine the effects of centralization on revenue levels. Sections IV and V explain the data set and empirical strategy used herein. Section VI presents the estimation results, and Section VII concludes.

2. School finance in Michigan

Before its reform in fiscal year (FY) 1995, Michigan had a power equalization system, under which the state government subsidized those districts whose property tax base was below the state’s minimum tax base.² This system intended to equalize school revenue by guaranteeing that lower-income districts would have the same revenue-raising power as higher-income districts. In FY 1994 (before the reform), 61% of districts received a positive power equalization grant (excluding a flat grant) from the state government (Courant & Loeb, 1997).³ Based on the paper’s calculation, approximately 60% of school revenue was funded by themselves in districts below the 20th percentile of school revenue per pupil, while the number is about 80% in districts above the 80th percentile of school revenue per pupil. These values were higher than values that neighboring states had (as seen in Figure 1), implying that the Michigan’s power equalization program had less actively intervened in school finance so had played a smaller role in reducing resource inequalities than neighboring state’s equalization programs had.

Figure 1. Trends in the percent of school revenue from local sources by revenue group.Notes: Each point is the state-group mean of the district-level percentage of local-source revenue.

Therefore, Substantial inequalities in school spending and widespread calls for a larger role of state government in public education were important factors that led to Michigan’s 1994 reform. The reform was also largely motivated by a heavy property tax burden. Before the reform, Michigan’s residents had a property tax burden approximately 33% higher than the national average, but a sales tax burden approximately 32% lower than the national average (Office of Revenue and Tax Analysis, 2002). There had been public discontent with the property tax burden as well as heavy reliance on local property taxes to finance school. As regards this issue, Governor John Engler pledged a property tax cut in 1990 Gubernatorial election; however, the 1993 proposal for a property tax cut (and a state income tax increase) was rejected in a referendum. In July 1993, legislature passed a bill (Public Act 145 of 1993) to eliminate local property taxes as a source of school revenue. It was in Oct. 1993 that Governor Engler clarified his plan to improve school funding equity in a message to a joint session of the Michigan Legislature, and the new foundation aid program was enacted in Dec. 1993. In a circumstance that a new funding plan was required, proposals were put to a referendum in March 1994 which resulted in approval of the school finance reform by a 69%/31% vote.⁴

The reform eliminated a school operating tax (which is a district property tax) on owner-occupied housing; additionally, the school operating tax rate on nonhomestead properties (e.g., rental homes) was required to drop to 18 mills if the tax rate was above 18 mills. Furthermore, a cap was introduced on the increase in property taxable values, so that each year the growth rate in taxable property values could not exceed either 5% or the inflation rate. As a result, each district government had increasingly less discretion on how much additional local revenue it could raise over time, with the end result being that governments became more reliant on state grants over time. To compensate for the resulting revenue loss, the reform increased the state general sales tax from 4% to 6% and newly introduced statewide property taxes of six mills.⁵ These additional state-level taxes were earmarked to school revenue.

Under the new school finance system, some high-income school districts qualified for levying a hold-harmless tax on properties, to ensure that post-reform school revenue would not be lower than pre-reform levels. In practice, however, the hold-harmless tax was rarely imposed. Thus, we can say that a district’s own revenue for school operations was effectively capped by the 18-mill school operating tax on nonhomestead properties. Even after the reform, however, districts retained full discretion on property taxes for school capital spending.

The reform package also introduced the foundation aid program, which grants to each district a minimum per-pupil school revenue level (called a foundation allowance). In FY 1994, the foundation allowance level initially depended on each district’s per-pupil revenue, and so higher-revenue districts initially received larger foundation allowances. The program gradually reduced over time the initial gap in foundation allowance by increasing smaller foundation allowances more quickly than larger foundation allowances. The gradual equalization of foundation allowances is reported in the literature (e.g., Chakrabarti & Roy, 2015; Roy, 2011).

In short, the Michigan school finance reform imposed constraints on each district’s own revenue, increased state-level taxes, and equally distributed state-raised funding to each district. In line with Loeb (2001), the reform can be considered school finance centralization with limited local supplementation. This centralization can be characterized by two things – namely, 1) the transfer of local discretion on school revenue to the state government and 2) revenue equalization among districts. The transfer of discretion gives the state government more money for grants to districts, and this entails the state’s larger revenue equalization program (such as a foundation aid program). Revenue equalization may not be the same as centralization, as equalization programs could be implemented with little transfer of local discretion to the state government.⁶ However, it is hard to imagine the transfer of discretion in the absence of some equalization programs.

Table 1 presents school revenue from federal, state, and district governments in the pre- and post-reform years. Column (3) shows that per-pupil revenue from the state government increased by approximately $3,200 in the first year of the reform. The increase in state-source revenue seems to derive mostly from an increase in formula grants (e.g., foundation grants and flat grants). We also see that the increase in state-source revenue was offset by a drop in each district’s own revenue; this drop can be mainly attributed to a drop in property tax revenue.

Table 1. Sources of school revenue in Michigan.

	Mean of variables (US dollar per pupil)
	Pre-reform year (FY 1994) (1)	Post-reform year (FY 1995) (2)	Differences: (2)-(1) (3)
Federal sources	329.8 [275.3]	356.6 [284.4]	26.7 (17.3)
State sources:	2,302.5 [1,377.8]	5,549.6 [1,143.1]	3,247.2 (78.1)
Formula grants	1,475.7 [1,255.1]	5,174.4 [1,017.4]	3,698.7 (70.5)
Other state sources	826.8 [494.8]	375.3 [471.3]	−451.5 (29.8)
Local sources:	5,398.2 [2,871.4]	2,298.4 [1,620.7]	−3,099.8 (143.9)
Property taxes	4,752.6 [2,616.9]	1,586.1 [1,459.3]	− 3,166.5 (130.7)
Other local sources	645.6 [776.7]	712.3 [510.6]	66.7 (40.6)
Sum	8,030.5 [2,409.4]	8,204.6 [1,730.3]	174.1 (129.4)

Values are adjusted to 2004 prices by using the CPI. Standard deviations are in brackets, and standard errors are in parentheses.

Figure 1 shows trends in the mean percentages of revenue from district governments. The bottom (top) revenue group is defined as districts with per-pupil revenue below the 20th (above the 80th) percentile of the per-pupil revenue within each state in FY 1994. We can see that the percentage of each district’s own revenue dropped dramatically because of the reform – by approximately 40 percentage points in both the bottom- and top-revenue groups in Michigan. This indicates that districts in Michigan became heavily dependent on state grants as they switched from the power equalization program to the foundation aid program. On the other hand, during our study period, there seem to be no dramatic changes in neighboring states’ trends. This is because there were no major changes made to the school finance systems in those neighboring states during that time.

Figure 2 presents trends in the mean of total per-pupil revenue of the bottom- and top-revenue groups. Compared to neighboring states’ trends, it seems that per-pupil revenue grew more quickly in Michigan for a pre-reform period than a post-reform period. This paper seeks to analyze trends in Michigan’s school revenue, compared to counterfactual trends where the reform did not occur. Thus, an important issue in terms of empirical identification will be how to capture the different preexisting trends among states; this is addressed below, in Section V.

Figure 2. Trends in total per-pupil school revenue by revenue group.Notes: Neighboring states include Illinois and Indiana. Each point is the state-group mean of district-level total per-pupil revenue.

3. Theoretical framework

This section briefly describes the theoretical framework by which to examine the effects of centralization on school revenue levels, by analyzing fully decentralized and centralized systems. This framework relies on the work of Silva and Sonstelie (1995). Although the Michigan school finance system has been neither fully decentralized nor fully centralized, this framework can capture an important political – economic mechanism that underlies the effects of Michigan school finance reform. From this framework, we would see that the effect of centralization on the level of school revenue is ambiguous.

The effects of centralization on revenue levels are explained in terms of price and income effects. It is assumed that the voter with a median income is pivotal in determining state-level school revenue under the centralized school finance system, whereas the voter with a mean income is pivotal in determining the mean revenue level under the decentralized school finance system (Fernandez & Rogerson, 1999; Silva & Sonstelie, 1995).⁷ Because the median income is generally lower than the mean income, we can say that the income effect of centralization is negative. The price effect of centralization depends on how the tax price of pivotal voters changes as school finance is centralized. In theory, the direction of the price effect is ambiguous. Silva and Sonstelie (1995) suggest that the pivotal voters’ tax price would drop as a state switches from a decentralized to a centralized system, assuming that the tax structure of the centralized system is sufficiently progressive; in this case, the price effect is positive.

Figure 3 shows the relationship between voter demand for per-pupil school revenue and voter income. The voter has a demand for per-pupil school revenue, given by $\mathit{D}\left(\mathit{P},\mathit{I}\right)$; here, $\mathit{P}$ is the voter tax price and $\mathit{I}$ is the voter income $\left(\frac{\mathrm{\partial D}\left(\mathit{P},\mathit{I}\right)}{\mathrm{\partial P}}⟨0\mathit{and}\frac{\mathrm{\partial D}\left(\mathit{P},\mathit{I}\right)}{\mathrm{\partial I}}⟩0\right)$. For simplicity, I assume that under the decentralized system, the tax price is constant across districts; additionally, I assume that under the centralized system, the tax price is an increasing function of income $\left(\frac{\mathit{dP}\left(\mathit{I}\right)}{\mathit{dI}}>0\right)$.⁸ Then, as seen in the figure, $D_d$ is increasing more quickly with respect to income than is $D_c$, where $D_d$ and $D_c$ are demand functions for per-pupil school revenue under decentralized and centralized systems, respectively.

Figure 3. Demand for school revenue under the decentralized and centralized systems.

Under the aforementioned assumption of pivotal voters under decentralized and centralized systems, the mean per-pupil revenue is $D_d^{\ast }$ under the decentralized system and $D_c^{\ast }$ under the centralized system in equilibrium, where $I_m$ is mean income and $I_{\mathit{md}}$ is median income. $I_0$ is the level of income above which voter’s tax price is higher under the centralized system than the decentralized system. Movement along demand curve $D_d$ from point A to point C represents the income effect of centralization, and movement from point C to point B represents the price effect; the income effect is negative, and the price effect is positive. We can see that $D_c^{\ast }<D_d^{\ast }$, indicating that centralization reduces the mean per-pupil revenue.

However, we could not assure that $I_0$ lies between $I_{\mathit{md}}$ and $I_m$ as in Figure 3. What we can only say about is that centralization might decrease the median income voter’s tax price if the centralized system is sufficiently progressive so that $I_0$ is higher than $I_{\mathit{md}}$. In the case that $I_0$ is higher than $I_m$, centralization could increase mean per-pupil revenue in equilibrium ($D_c^{\ast }>D_d^{\ast }$). Therefore, in theory, the effect of centralization on the level of school revenue is ambiguous.

4. Data

My empirical analysis is based on panel data for the period from FY 1990–2004 in Michigan and neighboring states (Illinois and Indiana).⁹ This data set is drawn from multiple sources. Data on district-level school finance are obtained from the Public Elementary – Secondary Education Finance Data of the U.S. Census Bureau for the FY 1992–2004 period. Because the Public Elementary – Secondary Education Finance Data does not provide data before 1992, I add school finance data for the FY 1990–1991 period from the Common Core of Data (CCD).¹⁰ Both the Public Elementary – Secondary Education Finance Data and CCD data sets are based on common school finance data that are submitted by each state education agency, and so there is little concern regarding consistency of panel data between the two sources. The FY 1990 is the earliest year for which annual school finance data is available.

I also add county-level personal income and population by age to my panel data set.¹¹ These variables are reported in terms of calendar years and are six months forward in terms of school fiscal years. Thus, I lag these variables by one year in the regression model. Descriptions of the variables used are presented in Table 2.

Table 2. Descriptive statistics.

	Mean [S.D]
Variable	All districts	Districts in Michigan	Districts in Illinois	Districts in Indiana
School revenue per pupil ($)	6,936.4	7,143.0	6,789.0	7,007.3
	[2,494.8]	[2,392.8]	[2,738.3]	[1,770.7]
School capital spending	751.6	834.6	743.5	625.8
per pupil ($)	[1,410.9]	[1,633.5]	[1,450.8]	[626.7]
Indicator for Michigan school	0.206	0.664	0.000	0.000
finance reform	[0.405]	[0.472]	[0.000]	[0.000]
Indicator for minor reforms in	0.298	0.000	0.332	0.733
neighboring states	[0.457]	[0.000]	[0.471]	[0.442]
Federal grants per pupil ($)	300.3	323.5	293.0	280.6
	[330.2]	[323.6]	[355.7]	[250.1]
Log number of students	7.136	7.350	6.821	7.697
	[1.174]	[1.238]	[1.131]	[0.836]
Number of schools	5.507	6.496	4.569	6.549
	[17.012]	[12.999]	[20.833]	[8.098]
Personal income	23,531.3	22,377.6	24,675.5	22,165.6
at the county level ($)	[6,865.1]	[6,401.7]	[7,363.1]	[5,354.1]
Log population aged btw 5 and 19	10.177	10.135	10.433	9.478
at the county level	[1.720]	[1.458]	[1.956]	[1.074]
Percent of white students	89.224	90.148	86.922	94.501
	[18.250]	[15.520]	[20.963]	[11.557]
Percent of black students	5.489	4.726	6.818	2.857
	[14.999]	[13.547]	[17.110]	[9.066]
Percent of Asian students	1.392	0.953	1.941	0.527
	[3.419]	[1.601]	[4.475]	[1.024]
Percent of Indian students	0.597	1.666	0.105	0.146
	[2.959]	[5.126]	[0.345]	[0.327]
District government debt ($)	3,394.7	5,512.1	2,794.2	1,376.2
	[4,681.4]	[6,334.0]	[3,544.5]	[1,986.5]
Number of districts	1,685	526	871	288
Obs.	25,178	7,819	13,039	4,320

The unit of observation is school districts in Michigan, Illinois, and Indiana. The study period is FY 1990–2004. Data for district government debt is missing in FY 1991.

5. Empirical strategy

Using districts in Illinois and Indiana as the control group, I estimate the effects of the reform by employing a DD event study framework. I choose these neighboring states as the control group for two reasons. First, over the study period, there were few major changes in the school finance systems of these states. Although Illinois and Indiana each sustained over the study period minor school finance reforms or a change in formulas by which to calculate state foundation grants to districts, these reforms were on a much smaller scale than the Michigan school finance reform.¹² These reforms are grouped together and controlled in the regression model. Second, Illinois and Indiana are geographically close to Michigan, and so socioeconomic factors among them might not be very different.¹³ Ohio borders Michigan, but I do not use Ohio in the control group, since it successively had large-scale, court-ordered school finance reforms in 1997, 2000, and 2002 (Jackson et al., 2016; Lafortune et al., 2016).

The DD event study regression is as follows:

(1) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{k}=0}^{6+}{\beta }_k\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(1)

where $Y_{\mathit{dgst}}$ is an outcome variable (i.e., per-pupil revenue in district $\mathit{d}$, group $\mathit{g}$, state $\mathit{s}$, and fiscal year $\mathit{t}$). $\mathit{Refor}{m}_{\mathit{s},\mathit{t}}$ is an independent variable of interest, and it is a dummy for indicating the effective year of the Michigan school finance reform; it is one for districts in Michigan in FY 1995 and zero otherwise. $\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}$ is a $\mathit{k}$-year lagged variable for $\mathit{Refor}{m}_{\mathit{s},\mathit{t}}$. By including the set of $\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}$ for $\mathit{k}=1,\dots ,\mathit{\hspace{0.17em}}6+$ in the regression model, the dynamic effects of the reform can be estimated. $\mathit{District}\text{0}\mathit{effects}$ is district-fixed effects, and $\mathit{Year}\text{-}\mathit{effect}{s}_t$ is year effects.

I divide the districts into five revenue groups based on per-pupil revenue in FY 1994 (one year before the reform); group 1 comprises districts with per-pupil revenue below the 20th percentile of per-pupil revenue within each state, group 2 comprises districts with per-pupil revenue between the 20th and 40th percentile of per-pupil revenue within each state, and so on. Revenue groups are time-invariant. In an equation (1)(1) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{k}=0}^{6+}{\beta }_k\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(1) , $D_g$ is a dummy for revenue groups with $\mathit{g}\in \left\{1,2,3,4,5\right\}$. For example, $D_{\mathit{g}=5}$ is one if a district belongs to group 5, and zero otherwise.

As a key strategy for controlling different preexisting trends between Michigan and neighboring states, equation (1)(1) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{k}=0}^{6+}{\beta }_k\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(1) includes state-group-specific linear time trends ${\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)$ which is state time trend dummies interacting with revenue group dummies in the regression model. This might capture unobserved confounders that evolve differently over time among states and among revenue groups.

$X_{\mathit{dgst}}$ is a set of control variables, including federal grants per pupil, log number of students, dummies for the number of schools, county-level personal income, county-level population aged between 5 and 19. Obviously, the amount of federal grants is a determinant of school revenue. The number of students and schools are district characteristics. Personal income and population aged 5 and 19 are to control for socioeconomic characteristics.

One might be curious about how the effects of the reform on revenue levels differs among districts. To investigate this issue, this study also estimates the following regression model.

(2) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{g}=1}^5\sum _{\mathit{k}=0}^{6+}{\beta }_{\mathit{gk}}\left(\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}\ast D_g\right)+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{Postreform}\text{-}\mathit{group}{ }_{\mathit{gt}}+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(2)

In the above equation, I have $\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}$ interact with $D_g$, which makes the regression model analogous to the triple differences framework.¹⁴ In so doing, the coefficients on $\left(\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}\ast D_g\right)$ produce the effects of the reform by revenue group over time.

My DD event study method outlined in equations (1)(1) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{k}=0}^{6+}{\beta }_k\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(1) and (2(2) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{g}=1}^5\sum _{\mathit{k}=0}^{6+}{\beta }_{\mathit{gk}}\left(\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}\ast D_g\right)+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{Postreform}\text{-}\mathit{group}{ }_{\mathit{gt}}+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(2) ) is different from the standard DD method (which uses a single treatment dummy), in that the former estimates the dynamic response of outcome variables. My method is better suited to this research than is the standard DD method, because 1) centralization might have long-run effects through the political process of adjusting revenue levels, 2) the reform was intended to gradually equalize school revenue over time, rather than suddenly cut grants to high-income districts and increase grants to low-income districts all at once, and 3) districts might become increasingly more dependent on state grants over time, as the reform capped the growth rate in taxable property values. When the magnitude of the treatment effect changes over time, state-specific time trends are likely to capture the dynamic effects of treatment that are not captured by the single treatment dummy in the standard DD model, in which DD estimators are be biased (Wolfers, 2006). A simple remedy for this problem is using the DD event study method and then estimating the dynamic effects of treatment.

To deal with potential serial correlation, standard errors are clustered at the district level.

6. Results

Table 3 reports the estimated effects of the reform on revenue per pupil, employing the event-study model in equation (1)(1) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{k}=0}^{6+}{\beta }_k\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(1) . The specifications are with and without controlling for state-group time trends and pre-reform dummies. In column (1) without controlling for state-group time trends, most estimates are significant, but their signs and sizes seem inconsistent over time. In column (2), I control for state-group time trends to capture potentially different preexisting trends between Michigan and control states, which should identify the causal effect of the reform if preexisting trends are stable over time. The results show that the reform has a negative effect on revenue levels in column (2). The estimated effect has a downward trend from the effective year of the reform to the fifth year after the reform. In the sixth year after the reform and onwards, I find that the reform reduces per-pupil revenue by $1,300.

Table 3. Effect of the reform on revenue levels.

Years from the reform	(1)	(2)	(3)	(4)
−2 years			310.8***	74.4
			(60.4)	(49.2)
−1 year			349.5***	24.2
			(75.3)	(75.8)
Effective year	214.3***	−157.8**	349.6***	−109.0
	(47.3)	(61.8)	(64.7)	(90.5)
1 year	184.1***	−299.5***	319.4***	−242.4**
	(61.7)	(60.5)	(82.5)	(97.3)
2 years	−130.0**	−730.8***	5.7	−665.3***
	(63.4)	(103.6)	(77.1)	(133.8)
3 years	44.3	−666.8***	179.8**	−592.9***
	(66.7)	(105.7)	(83.6)	(138.0)
4 years	−518.2***	−1,287.6***	−377.2***	−1,203.8***
	(70.1)	(128.9)	(87.1)	(162.6)
5 years	−708.1***	−1,477.6***	−521.4***	−1,388.1***
	(75.7)	(147.4)	(96.9)	(186.0)
6 years+	−179.9**	−1,300.3***	−23.6	−1,185.5***
	(73.2)	(223.9)	(78.9)	(236.1)
State-group time trends	No	Yes	No	Yes
Obs.	25,178	25,178	25,178	25,178
R-squared	0.746	0.749	0.747	0.749

Each column is a separate regression. All regressions control for minor reforms in neighboring states (dummies), federal grants per pupil, log number of students, the number of schools (dummies), log population aged between 5 and 19 at the county level, personal income at the county level, district-fixed effects, and year effects. Standard errors are clustered at the district level and are in parentheses.

*p < 0.1, **p < 0.05, ***p < 0.01.

By including pre-reform dummies in my regression model in columns (3) and (4), I check whether different preexisting trends among states are still a problem. If different preexisting trends are properly controlled in my model, the coefficients on pre-reform dummies would be close to zero. In column (3) without controlling for state-group time trends, the coefficients on pre-reform dummies are large and significant. In presence of these large and significant estimates, post-reform estimates seem unreliable. Controlling for state-group time trends in column (4), however, I am able to substantially suppress pre-reform estimated effects, which is a good sign of the identification of a causal effect.

The results for the effect of the reform are robust to the different study period and additional controls by using the same event-study model, as reported in Table 4. In columns (1) and (2), I restrict the sample into the period of FY 1990–2000. A variable for racial composition of students is added in columns (3) and (4) to see if the results would be different when conditioning on household sorting. In columns (5) and (6), I control for per-pupil district government debt, estimating the reform effect conditioning on the endogenous changes in the school deficits and construction projects.¹⁵ We can see that estimates are not sensitive to these specifications. I also re-estimated Table 3 by using the number of enrolled students as district-level weights – the results are presented in Table A1 in the Appendix; the results are similar with Table 3.

Table 4. Effect of the reform on revenue levels; a different study period and additional controls.

Years from the reform	Sample: Fiscal year ≤ 2000		Control: Racial composition of students		Control: District government debt per pupil
	(1)	(2)	(3)	(4)	(5)	(6)
−2 years		36.7		78.5		29.2
		(46.8)		(49.0)		(60.8)
−1 year		−25.1		26.9		−15.8
		(87.7)		(75.7)		(79.4)
Effective year	−210.4***	−211.3*	−161.0***	−108.4	−148.7**	−146.4
	(67.0)	(125.4)	(61.5)	(90.5)	(61.1)	(90.8)
1 year	−434.9***	−436.9***	−305.8***	−244.3**	−270.4***	−268.5***
	(78.8)	(153.5)	(60.3)	(97.5)	(59.5)	(98.7)
2 years	−763.2***	−766.0***	−734.2***	−663.7***	−802.7***	−801.0***
	(132.0)	(220.8)	(102.5)	(132.3)	(104.6)	(130.0)
3 years	−809.3***	−813.2***	−674.1***	−594.6***	−753.1***	−751.6***
	(144.9)	(246.7)	(105.0)	(137.8)	(107.2)	(133.9)
4 years+ or 4 years	−1,489.2***	−1,497.8***	−1,296.4***	−1,206.1***	−1,470.3***	−1,470.2***
	(176.1)	(297.8)	(127.8)	(161.7)	(132.3)	(156.6)
5 years			−1,489.1***	−1,392.4***	−1,556.8***	−1,561.7***
			(145.9)	(185.1)	(154.1)	(175.4)
6 years+			−1,315.1***	−1,191.2***	−1,421.8***	−1,424.5***
			(221.8)	(235.6)	(240.0)	(221.1)
Obs.	18,528	18,528	25,178	25,178	23,494	23,494
R-squared	0.726	0.726	0.750	0.750	0.760	0.760

Each column is a separate regression. All regressions control for minor reforms in neighboring states (dummies), federal grants per pupil, log number of students, the number of schools (dummies), log population aged between 5 and 19 at the county level, personal income at the county level, district-fixed effects, year effects, and state-group time trends. Control variables for racial composition are percent of white students, percent of black students, percent of Asian students, and percent of Indian students at the district level. Data for district government debt is missing in 1991. Standard errors are clustered at the district level and are in parentheses.

*p < 0.1, **p < 0.05, ***p < 0.01.

When employing the standard DD method (which uses a single treatment dummy) instead of the DD event study method, state time trends might incorrectly capture post-reform downward trends in revenue. As a result, the standard DD estimator might have captured the remaining trend, as the treatment group’s trend is incorrectly adjusted upward by confounded state time trends, thus biasing the DD estimator toward a positive value. Using districts in Illinois as the control group, Chaudhary (2009) employs the standard DD method with state time trends and concludes that Michigan’s reform increases log per-pupil expenditure; however, her results may not be free from confounded state time trends.

To check whether the use of the standard DD estimator significantly changes my results, I re-estimate the findings in Table 3 while using a single reform dummy instead of reform dummies for 0–6 years+. From this, I have very different results in Table 5. In column (2) with controlling for state-group time trends, the coefficient on a single reform dummy is small and not significant. Including both pre-reform dummies and state-group time trend dummies in column (4), the results show that the coefficient on a single reform dummy becomes greater than zero and significant. We can also see that the coefficients on pre-reform dummies are far greater than zero and significant, indicating that preexisting trends might not be properly controlled in regression. It seems consistent with speculation that state time trends might incorrectly capture post-reform downward trends in revenue so that the standard DD estimator would be biased toward a positive value.

Table 5. Single-dummy effect of the reform on revenue levels by using the standard DD model.

Years from the reform	(1)	(2)	(3)	(4)
−2 year			315.9***	320.4***
			(60.6)	(69.0)
−1 years			420.4***	429.2***
			(78.0)	(89.0)
Reform	9.8	−49.6	169.8**	203.3**
single dummy	(49.4)	(64.1)	(68.6)	(102.6)
State-group time trends	No	Yes	No	Yes
Obs.	25,178	25,178	25,178	25,178
R-squared	0.740	0.744	0.741	0.745

Each column is a separate regression. All regressions control for minor reforms in neighboring states (dummies), federal grants per pupil, log number of students, the number of schools (dummies), log population aged between 5 and 19 at the county level, personal income at the county level, district-fixed effects, and year effects. Standard errors are clustered at the district level and are in parentheses.

* p < 0.1, ** p < 0.05, *** p < 0.01.

This paper also estimates the effect of the reform on revenue levels by revenue group, employing the event-study model in equation (2)(2) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{g}=1}^5\sum _{\mathit{k}=0}^{6+}{\beta }_{\mathit{gk}}\left(\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}\ast D_g\right)+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{Postreform}\text{-}\mathit{group}{ }_{\mathit{gt}}+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(2) . The results are reported in Table 6 (also in Figure 4) in which each column is not a separate regression. Both pre-reform dummies and state-group time trend dummies are included in the regression model. Group 1 is the bottom revenue group, and group 5 is the top revenue group, as aforementioned. I find that the reform reduces the revenue level of all revenue groups. Especially, the higher-revenue groups sustain more pronounced reductions in revenue. The results suggest that, the sixth year after the reform and onwards, the reform reduces per-pupil revenue of group 1 by $399, that of group 3 by $1,389, and that of group 5 by $1,609. It seems that the reform equalizes revenue levels across districts as per-pupil revenue drops by a larger amount in the higher-revenue groups.

Figure 4. Effect of reforms on revenue levels with pre-reform dummies by revenue group.

Table 6. Effect of the reform on revenue levels by revenue group.

Year from the reform	Group 1 (1)	Group 2 (2)	Group 3 (3)	Group 4 (4)	Group 5 (5)
−2 years	142.2***	21.3	24.0	247.6***	−59.5
	(52.4)	(66.8)	(54.6)	(83.5)	(152.7)
−1 year	−4.6	−130.9	−88.3	71.8	269.3
	(68.3)	(80.1)	(69.7)	(98.7)	(261.3)
Effective year	−10.8	−232.5**	−138.7	−48.1	−127.1
	(93.8)	(110.9)	(98.4)	(138.9)	(284.3)
1 year	106.2	−267.4**	−253.8**	−203.1	−627.8**
	(108.3)	(128.5)	(108.7)	(159.2)	(276.0)
2 years	−115.8	−669.6***	−719.7***	−631.0***	−1,239.3***
	(129.3)	(144.4)	(141.4)	(201.0)	(412.6)
3 years	−19.0	−614.1***	−587.5***	−535.6***	−1,262.1***
	(127.3)	(162.0)	(134.1)	(203.1)	(441.1)
4 years	−561.0***	−1,239.4***	−1,227.0***	−1,151.3***	−1,899.9***
	(149.5)	(184.0)	(155.3)	(222.9)	(507.8)
5 years	−596.9***	−1,422.1***	−1,470.1***	−1,480.1***	−2,041.6***
	(174.5)	(210.9)	(179.9)	(244.1)	(568.5)
6 years+	−399.2**	−1,292.8***	−1,389.3***	−1,298.5***	−1,608.7**
	(203.0)	(240.1)	(199.9)	(277.4)	(789.8)
Obs.: 25178; R-squared: 0.750

Each column is not a separate regression. A regression controls for minor reforms in neighboring states (dummies), federal grants per pupil, log number of students, the number of schools (dummies), log population aged between 5 and 19 at the county level, personal income at the county level, state-specific time trends, district-fixed effects, and year effects. Standard errors are clustered at the district level and are in parentheses.

*p < 0.1, **p < 0.05, ***p < 0.01.

There might have been an incentive for districts to increase revenue before the reform to receive larger state aids after the reform. However, according to the results, consistent pre-reform upward trends are not found across revenue groups. Districts might not be able to adjust school revenue in the middle of FY 1994 (one year before the reform) when the new foundation aid program was formed.

As aforementioned, the reform cut the school operating tax but did not change district’s property taxes for school capital spending. Thus, we could expect that the reform would not have a direct effect on school capital spending in Michigan. As a falsification test for the reform effect on revenue, therefore, this paper estimates the effect of the reform on school capital spending per pupil by employing the event-study model in equation (1)(1) $Y_{\mathit{dgst}}=\mathit{\alpha }+\sum _{\mathit{k}=0}^{6+}{\beta }_k\mathit{Refor}{m}_{\mathit{s},\mathit{t}-\mathit{k}}+X_{\mathit{dgst}}^{\prime }\mathit{\gamma }+\sum _{\mathit{g}=1}^5{\delta }_{\mathit{gs}}\left(\mathit{T}\ast D_g\right)+\mathit{District}\text{-}\mathit{effect}{s}_d+\mathit{Year}\text{-}\mathit{effect}{s}_t+{\epsilon }_{\mathit{dgst}}$(1) . If my estimates for revenue are driven by a common secular trend which affecting both school revenue and capital spending, my estimates for capital spending would be large and significant. Table 7 reports the estimated effect of the reform on school capital spending per pupil. In column (2) with state-group time trends, although the estimated effect is negative and significant in the effective year, other estimated post-reform effects are relatively small and not significant. In column (4) with pre-reform dummies and state-group time trends, most estimated effects are not significant except for the estimated effect one year before the reform.

Table 7. Effect of the reform on school capital spending per pupil.

Years from the reform	(1)	(2)	(3)	(4)
−2 years			99.2**	113.8
			(46.2)	(81.3)
−1 year			169.8***	220.5*
			(55.6)	(120.5)
Effective year	−189.8***	−267.5***	−134.4**	−70.9
	(52.2)	(72.9)	(57.3)	(156.7)
1 year	−10.1	−115.1	45.3	117.8
	(59.7)	(96.4)	(60.7)	(188.3)
2 years	172.1**	36.8	227.7***	306.1
	(81.6)	(124.5)	(81.8)	(226.4)
3 years	267.7***	103.8	323.1***	409.4
	(84.7)	(144.6)	(84.0)	(262.8)
4 years	137.7	20.2	196.0**	377.0
	(85.6)	(162.1)	(85.5)	(303.2)
5 years	−12.7	−76.9	70.2	338.1
	(106.5)	(203.7)	(105.9)	(370.8)
6 years+	13.1	−139.9	79.4	365.2
	(84.2)	(210.4)	(85.0)	(418.3)
State-group time trends	No	Yes	No	Yes
Obs.	25,178	25,178	25,178	25,178
R-squared	0.076	0.077	0.076	0.077

Each column is a separate regression. All regressions control for minor reforms in neighboring states (dummies), federal grants per pupil, log number of students, the number of schools (dummies), log population aged between 5 and 19 at the county level, personal income at the county level, district-fixed effects, and year effects. Standard errors are clustered at the district level and are in parentheses.

* p < 0.1, ** p < 0.05, *** p < 0.01.

7. Conclusions

This study examines the effects of school finance centralization on school revenue levels, using the Michigan school finance reform as a policy variation. I find that the reform substantially reduces revenue levels over time; the sixth year after the reform and onwards, per-pupil revenue drops by $1,300 on average. I also find that the reform reduces revenue levels in both low- and high-revenue districts, but the higher-revenue districts tend to sustain more pronounced reductions; per-pupil revenue becomes more equal across districts through leveling down.

The leveling down effect seems analogous to the conventional framework of the underprovision of public goods as people are reluctant to finance public goods that benefit herself as well as others. The Michigan’s reform intended to equalize school revenue among districts but resulted in a drop in revenue levels overall even in bottom revenue districts, as it broke the tax-benefit linkage so made public education finance collectively less supported. California’s reform (Proposition 13 passed in 1978 and related changes in a state aid program) could be another example of it; to improve the equality and adequacy of school finance, it restricted district’s control of property taxes and equalized per-pupil revenue across districts by state aids.¹⁶ It was observed that California’s reform might have unintentionally leveled down school expenditures across districts (Manwaring & Sheffrin, 1997; Sontelie et al., 2000).

In conclusion, my results show a potential tradeoff between revenue levels and equality, having policy implications for school finance reforms in Michigan as well as other states. Careful consideration would be needed on suitable compromises between revenue levels and equality, allowing local discretion on school revenue levels to some extent.

8.

Data availability statement

Table

Variable	Data sources
− School revenue − School capital spending − Federal grants − District government debt − Number of pupils − Number of schools	Local Education Agency Finance Survey Data, Common Core of Data, National Center for Education Statistics; FY 1990 Longitudinal School District Fiscal-Nonfiscal Detail File, Common Core of Data, National Center for Education Statistics; FY 1991 Public Elementary-Secondary Education Finance data, U.S. Census Bureau; FY 1992–2004
− Racial composition of students	Public School Universe Data, Common Core of Data, National Center for Education Statistics; FY 1990–2004
−Per-capita personal income	U.S. Bureau of Economic Analysis; 1989–2003
− Population aged btw 5 and 19	Population estimates, U.S. Census Bureau; FY 1989–2003

Disclosure statement

No potential conflict of interest was reported by the author(s).

Additional information

Notes on contributors

Jinsub Choi

Jinsub Choi is an associate research fellow at Korea Institute of Local Finance. He has a PhD in Economics from Georgia State University. He works on public economics and local finance.

Notes

¹ The dynamic response may have occurred because 1) centralization could have long-run effects, 2) the reform’s equalization plan was phased in over time, and 3) the district’s taxing power might be gradually limited over time, given that the growth rate in taxable property values had been capped.

² The local property tax base is called the state equalized value, which in Michigan was approximately one-half of the market value.

³ For districts that had tax bases exceeding the minimum tax base, their flat grants were reduced by the amount in excess of the minimum tax base times property tax rates; however, no district could receive a negative power equalization grant (including a flat grant).

⁴ The new program became effective in FY 1995.

⁵ The reform also increased an excise tax on cigarettes by $0.5 per pack and newly introduced a 16% tobacco tax. The reform reduced the state income tax by 0.2%.

⁶ For example, the state government can change the existing grant formula so as equalize school revenue, without transferring local discretion.

⁷ Assuming that the demand for school revenue is a linear function of income and that families sort into communities according to income under the decentralized school finance system, the mean school revenue of the system should be equal to the demand of the mean-income voter.

⁸ The voters’ tax price exists and is identified, since local property taxes and state-level taxes are earmarked as school revenue. Under the centralized system, the voters’ tax price increases with income, due to the equalization plan.

⁹ The dataset constructed for this study is available on reasonable request.

¹⁰ School finance data from 1990 come from the Local Education Agency Finance Survey of the CCD, and the data from 1991 come from the Longitudinal Fiscal – Nonfiscal Detail File of the CCD.

¹¹ Personal income is obtained from the Bureau of Economic Analysis, and population by age comes from Census population estimates.

¹² Through the enactment of PA 90–548, Illinois increased the foundation level from US$3,108 to US$4,225 in FY 1999. In 1993, Indiana rewrote its foundation grant formula so as to make school revenue more equal among districts. These legislative changes might increase foundation grants to low-revenue districts, but noticeable changes cannot be seen in Figure 1.

¹³ The comparison of state-level socioeconomic statistics can be seen in Table A2. It seems that pre-reform trends in those statistics were not very different between Michigan and neighboring states.

¹⁴ In the equation, $\mathit{Postreform}\text{-}\mathit{grou}{p}_{\mathit{gt}}$ indicates a post-reform period interacting with revenue group dummies, which is essential for the triple differences framework.

¹⁵ Unfortunately, Data for district government debt is missing in 1991.

¹⁶ After the reform, district’s control of property taxes was restricted by a cap on tax rates as well as an increase in the assessed value of a property. State became able to effectively decide district-level school revenue.

Appendix

Table A1. Effect of the reform on revenue levels: regressions weighted by the number of students.

Years from the reform	(1)	(2)	(3)	(4)
−2 years			330.3***	79.8
			(74.5)	(79.7)
−1 year			431.6***	66.9
			(85.3)	(105.2)
Effective year	419.8***	−8.4	582.8***	70.4
	(56.1)	(94.3)	(53.2)	(96.6)
1 year	356.1***	−196.0*	517.7***	−104.3
	(58.4)	(109.4)	(54.0)	(107.4)
2 years	13.5	−664.4***	173.2***	−559.8***
	(54.7)	(113.1)	(59.9)	(136.6)
3 years	320.6***	−473.7***	481.7***	−355.7**
	(66.3)	(140.7)	(63.7)	(145.8)
4 years	−203.2***	−1,106.2***	−27.8	−969.0***
	(71.3)	(165.0)	(65.5)	(170.6)
5 years	−298.8***	−1,241.5***	−52.1	−1,087.5***
	(102.1)	(201.9)	(90.0)	(200.9)
6 years+	45.7	−1,283.5***	245.1***	−1,092.9***
	(97.4)	(237.6)	(86.8)	(229.3)
State-group time trends	No	Yes	No	Yes
Obs.	25,178	25,178	25,178	25,178
R-squared	0.861	0.863	0.862	0.863

The regressions are weighted by the number of enrolled students in each district; instead, the number of enrolled students is not included as controls. The rest of specifications in this Table are identical to the ones in Table 3. Standard errors are clustered at the district level and are in parentheses.

* p < 0.1, **p < 0.05, ***p < 0.01.

Table A2. Comparison of trends in state-level socioeconomic variables among states.

	Michigan (1)	Illinois (2)	Indiana (3)
GDP per capita in 1994 ($)	26,238.7	29,476.6	24,946.8
% change in GDP per capita 1990–1994	26.5	20.9	25.0
Unemployment rate in 1994 (%)	6.0	5.7	4.8
Change in unemployment rate 1990–1994	−1.7	−0.4	−0.5
Population in 1994 (thousand)	9,584.5	11,805.0	5,745.6
% change in population 1990–1994	2.9	3.1	3.4
Population aged btw 5 and 19 in 1994 (thousand)	2,088.7	2,508.1	1,250.1
% change in population aged btw 5 and 19 1990–1994	2.1	3.3	2.0
% of students who are white in FY 1994 (state-level mean)	91.1	88.7	95.2
Change in % of students who are white FY1990-FY1994	−0.9	−1.5	−0.5
% of students who are black in FY 1994 (state-level mean)	4.2	6.1	2.7
Change in % of students who are black FY1990-FY1994	0.2	0.6	0.2