Sage Journals: Discover world-class research

Abstract

Arizona shifted to using current-year enrollment, instead of prior-year enrollment, as the basis for determining state aid for school districts following the passage of Arizona Education Finance Amendment (AEFA) in 2017. This study examines the short-term effects of AEFA implementation on school inputs—namely, expenditures and district personnel, particularly teachers. We find that the average district does not seem to respond to AEFA. However, our heterogeneity analyses reveal that the highest-income districts significantly reduce more inputs than the lowest-income districts in response to AEFA. The differential impact between these two groups is most evident in instructional expenditures, administration expenditures, total full-time equivalent teachers, and particularly teachers with 1–5 years of experience.

Keywords

econometric analysis educational policy enrollment declines finance k–12 policy school expenditures state education aid

Introduction

State aid plays a significant role in financing education for the majority of U.S. states, including Arizona. According to the most recent data from the Digest of Education Statistics (DES), state education aid comprised an average 50.1% of local school districts’ total revenue in 2019, with Arizona’s share at 49.1%.¹ Since 1980, Arizona has based its education aid on district enrollment. Before 2017, state education aid to school districts was based on their prior-year enrollment—a popular form of “hold-harmless” provisions in state education aid (Center for Public Education, 2021). Under the Arizona Education Finance Amendment (AEFA) since 2017, the state has used a school district’s current-year enrollment to determine its state aid. Although Arizona’s state education aid has always been based on current-year numbers in years of enrollment growth, AEFA removed the hold-harmless feature for districts with enrollment declines since 2018 (after a grace year with state backfill in 2017).

Figure 1 shows that public school enrollment in Arizona started to decline sharply at the beginning of the Great Recession in 2008 until 2012, when enrollment leveled off. The negative slope between 2012 and 2020 is much flatter than that between 2008 and 2011. Although 2012 is the start of a relatively steadier period of total enrollment in Arizona, 96.8% of school districts in our sample experienced annual enrollment declines at least once during this period of 2012–2020. Also, during the pre-AEFA (2012–2017) and post-AEFA (2018–2020) periods, the shares of enrollment decline occurrences are unchanged at 54% and higher than those of enrollment growth. This suggests state aid cuts in more than half of the postperiod district years. However, no study has ever been conducted to estimate the effects of AEFA on school districts’ expenditures and personnel. This study seeks to fill this gap in the literature.

Figure 1.

Total state trend of enrollment in public schools during 2006–2020.

This study straddled two lines of inquiry. Studies in the first line of inquiry examined the effects of enrollment changes on school inputs. These studies were, however, published decades ago (Cavin et al., 1985; Edelman & Knudsen, 1990). The second line of inquiry examined the relationship between state aid and school expenditures. When state aid is largely determined by enrollment, school district expenditures may vary according to enrollment-induced fluctuations in state aid. Several studies have found that school districts with increased state aid spent more (Card & Payne, 2002; Lafortune et al., 2018; Nguyen-Hoang & Yinger, 2014; Roy, 2011).

This study makes three contributions to the literature on education finance and policy. First, this study is the first to examine the short-term effects of AEFA three years after its full implementation and thus supplements the scant literature on the effects of enrollment changes on school inputs. Second, this is the first study to examine not only the enrollment effects statewide on the average school district’s inputs but also the heterogeneity of the enrollment effects on different district groups. Third, to the best of our knowledge, our study is also the first to examine the enrollment effects on cuts to district personnel, particularly teachers, not only in terms of total numbers but also in terms of experience levels and educational credentials.

To make these three contributions, this study examines three research questions by using a difference-in-differences (DID) design. First, what are AEFA’s effects on school district expenditures, especially current expenditures, in both years of enrollment decline (decline years) and years of enrollment growth (growth years)? Second, do AEFA-induced effects on expenditures vary by income-based district types? Third, how does AEFA affect the dismissal of district personnel, particularly teachers, as a cost-saving measure? Of interest is how AEFA-induced effects are reflected in terms of teacher academic credentials and experience levels. Although we do not find evidence of AEFA’s impact on the average district, we find evidence of significant district group-specific variation in AEFA-induced cuts to instructional expenditures and teachers. For example, the highest-income districts cut instructional spending, total FTE teachers, and teachers with 1–5 years of experience significantly more than the lowest-income districts.

The remainder of this paper is organized as follows. The following section reviews the literature on how enrollment changes may affect education inputs—particularly in the context of state aid reforms—and provides background on the Arizona state aid policy and a framework for how enrollment changes affect state aid. Next, the paper presents the empirical strategies, data used in our analyses, and the results. Finally, the paper concludes with suggestions for future research.

Background

Related Literature

As indicated earlier, state aid—a major revenue source for K–12 education—has grown in importance over the past century. According to the data reported by DES, in FY1920, states contributed only 16.5% to school districts’ total revenue, whereas local sources accounted for 83.2%. State education aid rose significantly from 38% in 1972 to 49% in 1987, then fluctuated slightly in the 1990s before reaching 47% in 2004 (Murray et al., 2007). This average share of state aid to total revenue increased to over 50% in FY2018 and FY2019.

Given this important role of state aid, studies have estimated its effects on education expenditures. Many studies focus on increased state aid through school finance reform (SFR). For example, Steinberg et al. (2016) found that SFR in Pennsylvania did not increase school spending, especially among high-taxing districts; the authors argued that Pennsylvania school districts used state aid to provide property tax relief to their residents. However, studies of SFR in other states found that SFR-induced aid increases resulted in higher school spending and reduced interdistrict spending disparities, specifically in California (Fan & Liang, 2020), Massachusetts (Nguyen-Hoang & Yinger, 2014), and Michigan (Roy, 2011). Nationwide SFR studies have found evidence of the positive short-term effects of school expenditures (Lafortune et al., 2018).

In many states, state education aid changes with enrollment numbers, especially during growth years. In decline years, states may employ a hold-harmless provision under which state aid continues to be the same as that of the previous year despite the decline in enrollment. Scholars have argued that this hold-harmless provision competes with charter schools (Roza & Fullerton, 2013), violates the principle of horizontal equity (Fahy, 2011), and may produce racial disparities (Kelly, 2021). Gigliotti and Sorensen (2018) examined the effects of the hold-harmless provision in New York and found that this provision did not significantly affect instructional spending but did increase administrative spending.

In cases of state aid distribution without the hold-harmless provision, current-year, enrollment-based state aid per student to districts experiencing an enrollment decline is less than that of the previous year. Reduced aid puts fiscal pressure on these school districts because they can hardly reduce their input levels (and hence, their spending) quickly in the decline years. Therefore, state aid policies face the challenge of supporting school districts with enrollment declines while bolstering their motivation to adapt (Cavin et al., 1985).

Enrollment may have a direct effect on school spending in addition to its indirect state aid-induced effect. Enrollment has been a key variable in education cost studies (Duncombe & Yinger, 2011). Duncombe et al. (2015) showed that economies of size exist in education. In other words, when school district enrollment grows, expenditures per student can go down. Larger districts can save their fiscal resources by maintaining an administration system for a larger enrollment and taking advantage of mass procurement benefits (Duncombe et al., 2015).

Two studies examined how enrollment changes affected school spending directly (Cavin et al., 1985; Edelman & Knudsen, 1990). Cavin et al. (1985) showed a statistically significant negative relationship between enrollment changes and expenditures per student. Edelman and Knudsen (1990) argue that personnel layoffs necessary in decline years often affect less-experienced staff. Our third research question is to test whether AEFA induces school districts to cut less- vs. more-experienced teachers in decline years.

Financing K–12 Education in Arizona

Arizona’s current school funding system was developed based on a 1980 reform when the state aimed to equalize education funding among its school districts. Specifically, the amount of state aid a district receives for current use is the difference between an equalization base and its expected property tax effort. The equalization base consists of three components: base support level (BSL), transportation support level, and district additional assistance (mostly for capital spending purposes). The base support level is derived from the base level amount and a measure of enrollment referred to as the weighted student count (WSC). The base level amount is determined annually by the legislature and adjusted for inflation (Arizona Association of School Business Officials, 2017)—for example, $4,305.73 per pupil for FY2021. The WSC is derived by multiplying weighted student counts and enrollment determined by the average daily membership (ADM)—that is, the total enrollment of fractional (part-time) and full-time students, minus withdrawals of each day through the first 100 days of instruction. Weighted student counts vary depending on district size, distance to neighboring districts, grade ranges, English language learners (ELLs), and students with disabilities.²

The second equalization base component, transportation support level, is based on approved average daily route miles driven in the district and its unweighted transportation-eligible student count. District additional assistance—the final element in the equalization base—is intended primarily for capital spending purposes but can be used for operational purposes. This assistance amount is determined by multiplying a district’s unweighted K–8 and 9–12 student counts with their respective annual set amounts.

The expected local tax effort is the product of a qualifying tax rate (QTR) set annually by the state and a school district’s assessed value. The QTR was $4,253 per $100 of taxable property for unified school districts in FY2018. While the state uses QTR to determine state aid, a district’s actual property tax rate may be higher or lower than the QTR. In addition, school districts can raise additional revenue from property taxes for transportation purposes up to the maximum of the transportation revenue control limit, which is equal to 120% of the transportation support level.

Enrollment is an important factor in the calculation of the three elements in the equalization base. Before the passage of AEFA in FY2017, the equalization base relied on prior-year enrollment. If a district experiences enrollment growth in the current year, additional state aid is provided in subsequent apportionments for the base support level but not for the transportation support level or district additional assistance (Arizona Department of Education, 2004). However, none of the three elements in the equalization base was adjusted downward for school districts with enrollment declines (Hunter & Gifford, 2000). This hold-harmless feature was intended to serve school districts experiencing either enrollment decline or growth.

Since AEFA’s passage in 2017, the state has continued to use previous-year enrollment to calculate district additional assistance. Yet, these other two elements—namely base and transportation support level—have been derived from current-year enrollment. However, in 2017, the state made a one-time backfill reservation of $31 million to compensate for the state aid loss of school districts with enrollment declines (Arizona Department of Education, 2017). In other words, the prior-to-current-year enrollment shift can be considered to have started in 2018. For ease of reference, we refer to the period starting in 2018 as the postperiod.

In addition to state aid, school districts in Arizona need to raise revenue locally, mostly from property taxes. Therefore, districts could raise local revenue to offset state aid cuts. We also examined if this is the case for districts in the state.

How Might AEFA Affect a District’s State Aid?

We assume, for simplicity, that the state aid a district receives in year $t$ , $A_{t}$ , depends primarily on base level amount ( $B$ ). Also, given that $B$ is adjusted for inflation, $B_{t}$ is plausibly assumed to equal $B_{t - 1}$ in real terms. In other words, $A_{t} = B_{t} N_{t}$ , where $N_{t}$ is the district’s enrollment in year $t$ . We first examine how the use of prior-year enrollment may help school districts with more stable state aid. Table 1 shows that in two consecutive growth years ( $N_{t} \geq N_{t - 1} \geq N_{t - 2}$ ), the district is expected to receive higher total state aid in year $t$ than the aid they received the year before ( $Δ A_{t} > 0$ ) (Case 1a). State aid can, however, stay (almost) unchanged if enrollment declines in year $t - 1$ and then grows in similar size in year $t$ (that is, $N_{t} \approx N_{t - 2}$ as in Case 1b). State aid is also unchanged in Case 2a, in which enrollment grows in year $t - 1$ and then declines in year $t$ . State aid only declines when enrollment declines in two consecutive years (double-decline years) (Case 2b). When $N_{t} - N_{t - 1} = N_{t - 1} - N_{t - 2}$ , then the state aid decrease in year $t$ is the same, regardless of which enrollment, prior- or current-year, is used. This scenario suggests that districts with multiple double-decline, preperiod years already experience state aid reductions in this period, and their postperiod response to enrollment decline may thus be similar to their preperiod response.

Table 1

Effects of Enrollment Changes on Real Total State Aid

Cases	$A_{t}$	$A_{t - 1}$	$Δ A_{t} = A_{t} - A_{t - 1}$	Expected ∆ $A_{t}$
Cases	(1)	(2)	(3)	(4)
Before 2018 (preperiod)
1.
a. $N_{t - 1} \geq N_{t - 2}$	$B_{t} N_{t}$	$B_{t - 1} N_{t - 1}$	$B_{t} (N_{t} - N_{t - 1})$	$> 0$
b. $N_{t - 1} < N_{t - 2}$	$B_{t} N_{t}$	$B_{t - 1} N_{t - 2}$	$B_{t} (N_{t} - N_{t - 2})$	= 0 (if $N_{t} = N_{t - 2}$ )
2.
a. $N_{t - 1} \geq N_{t - 2}$	$B_{t} N_{t - 1}$	$B_{t - 1} N_{t - 1}$	$B_{t} (N_{t - 1} - N_{t - 1})$	$= 0$
b. $N_{t - 1} < N_{t - 2}$	$B_{t} N_{t - 1}$	$B_{t - 1} N_{t - 2}$	$B_{t} (N_{t - 1} - N_{t - 2})$	$< 0$
2018 (postperiod)
3. $N_{t} < N_{t - 1}$
a. $N_{t - 1} \geq N_{t - 2}$	$B_{t} N_{t}$	$B_{t - 1} N_{t - 1}$	$B_{t} (N_{t} - N_{t - 1})$	$< 0$
b. $N_{t - 1} < N_{t - 2}$	$B_{t} N_{t}$	$B_{t - 1} N_{t - 2}$	$B_{t} (N_{t} - N_{t - 2})$	$< 0$
After 2018 (postperiod)
4. $N_{t} \geq N_{t - 1}$	$B_{t} N_{t}$	$B_{t - 1} N_{t - 1}$	$B_{t} (N_{t} - N_{t - 1})$	$> 0$
5. $N_{t} < N_{t - 1}$	$B_{t} N_{t}$	$B_{t - 1} N_{t - 1}$	$B_{t} (N_{t} - N_{t - 1})$	$< 0$

Notes: $A_{t}$ and $B_{t}$ are inflation-adjusted state aid and base-level amount in year $t .$ $B_{t}$ is assumed to equal $B_{t - 1}$ . Scenario 1 also applies to 2018.

Switching to current-year enrollment, AEFA might affect state aid in both decline and growth postperiod years. Under AEFA, school districts lose the previously described aid-stabilizing effect of prior-year enrollment (PYE), especially in cases of alternating enrollment changes. The aid a district receives in a postperiod decline year is always lower than the aid it received the previous year, regardless of whether the previous year was a growth or decline year (Cases 3a, 3b, and 5). State aid, especially the base support level, in growth years, is always based on current-year enrollment and thus should, in theory, not be affected by AEFA. Therefore, districts’ postperiod response to enrollment growth is plausibly expected to be similar to their preperiod response. However, their postperiod response to enrollment growth may be more muted than their preperiod response. Districts may go ahead with expenditure increases in a preperiod growth year because their state aid will stay unchanged in the case of enrollment decline the following year (Case 2a). This is not true in the postperiod because state aid will be immediately reduced in a decline year. Districts, therefore, may not want to increase as much spending in a postperiod growth year as in a preperiod growth year just to make a sizeable cut in the immediately following year of enrollment decline.

Empirical Strategy

We used a DID design on a panel of 190 Arizona school districts in our sample period of 2012–2020 to answer the three research questions.³ Our DID estimation approach has three methodological challenges to a conventional DID design. First, while there tends to be a clear set of treatment and comparison units in a conventional DID design, AEFA—the treatment—applies to all school districts. All school districts in Arizona can therefore be considered treatment units. Second, a treatment in a conventional DID design usually occurs either once or multiple times but only in the postperiod. AEFA affects school districts through enrollment changes, and enrollment changes may occur both before and after AEFA was implemented. Third, while AEFA affects state aid in years of enrollment decline, state aid in growth years, especially the base support level, is based on current-year enrollment in both the pre- and postperiod. Therefore, one might consider decline years as treatment units and growth years as comparison units. However, as previously explained, growth years may not be entirely immune from the potential effects of AEFA. When districts lose the PYE-enabled aid-stabilizing buffer, they may increase inputs in postperiod growth years significantly less than in preperiod growth years. In other words, decline and growth years can plausibly be considered potential treatment units. Given these challenges, our empirical strategy is similar to an interrupted time-series design. The DID estimator captures the combined AEFA-induced effect on district inputs in both decline and growth years.

We employed various dependent variables for the research questions. In the following illustration, we show estimation equations for logged total school district current expenditures, $\ln (E)$ . Specifically, we set $\ln (E)$ for district $i$ in year $t$ be a function of logged enrollment $(\ln (N))$ , other characteristics of the student body ( $W$ ), and other variables that influence demand for school expenditures ( $O$ ). A major potential source of estimation bias comes from unobserved time-constant factors that are correlated with both $E$ and $N$ . One can remove this source of bias by using either fixed effects or first differencing methods (see Wooldridge, 2020, for detailed discussions). Given that the key variable of interest is annual changes in $N$ , we chose first differencing for ease of interpretation. More specifically,

\begin{array}{l} Δ \ln (E_{i t}) = γ Δ W_{i t} + θ Δ O_{i t} + \sum_{t = 2012}^{2020} δ_{t} Δ d_{t} \\ + \sum_{T = A, B} α_{T} Δ_{- T} \ln (N_{i t}) + \sum_{T = A, B} β_{T} Δ_{+ T} \ln (N_{i t}) + ε_{i t} \end{array}

(1)

where subscript $T$ indicates the postperiod ( $A$ , or $t \geq$ 2018) and preperiod ( $B$ , or $t <$ 2018), respectively; $ε$ is an error term. The dependent variable in equation (1), district $i$ ’s change in $\ln (E)$ , or $Δ \ln (E_{t})$ , is the approximate annual growth rate in its total current expenditures from year $t - 1$ to $t$ . Following the education cost-function literature (Duncombe & Yinger, 2011), $W$ in equation (1) represents a set of variables of student characteristics—namely, percentages of school-age (i.e., ages 5 to 17) children in poverty ( $P$ ), ELL students, and students with disabilities. In addition, $O$ includes variables proxying for factors that influence demand for school expenditures, namely median household income, median tax share, the percentages of owner-occupied housing units, senior residents, and population aged 25 years and over with a four-year college education. All fiscal variables are log-transformed. A district’s median tax share is derived as the ratio of its median housing value to total taxable property value. The series of $d$ represents dummy year variables for 2012–2020 and captures common annual factors influencing all school districts.

Equation (1) includes a set of four key variables. For example, $Δ_{+ T} \ln (N_{t})$ equals $Δ \ln (N_{t})$ , or $\ln (N_{t}) - \ln (N_{t - 1})$ , when $\ln (N_{t}) \geq \ln (N_{t - 1})$ in period $T$ , and equals 0 otherwise; $Δ_{- T} \ln (N_{t})$ equals $- Δ \ln (N_{t})$ when $\ln (N_{t}) < \ln (N_{t - 1})$ in period $T$ , and equals 0 otherwise (we omit subscript $i$ for parsimony).⁴ Given that $Δ_{- T} \ln (N_{t})$ is positive, its coefficient, $α$ , is expected to be negative and indicates an $α$ -percent decrease in $E$ when enrollment declines by one more percent.

Given these four variables ( $α_{A}$ , $α_{B}, β_{A}$ , and $β_{B}),$ we then compare the estimated post-pre (first) differences in $E$ in response to enrollment decline, $D_{D}$ , where $D_{D}$ equals $(α_{A} - α_{B})$ and is referred to as post-pre decline difference, and to enrollment growth, $D_{G}$ , where $D_{G}$ —or post-pre growth difference—equals $(β_{A} - β_{B})$ . A significant and negative $D_{D}$ indicates that districts cut $E$ significantly more in postperiod decline years than preperiod decline years, which we refer to as the decline-aggravating effect of AEFA. As discussed previously, districts’ postperiod response to enrollment growth may be more muted than their preperiod response. That is, suppose $β_{B}$ is significantly positive; $β_{A}$ may be positively smaller or could even turn negative. This scenario may result in a negative and significant $D_{G}$ , which we refer to as the growth-dampening effect of AEFA.⁵

Given the first differences ( $D_{D}$ and $D_{G}$ ),⁶ we take additional differences based on $D_{D}$ and $D_{G}$ . Specifically, to answer the first research question, we test equation (2) using Stata’s lincom command:

D = (- D_{D} - D_{G}),

(2)

where we switch the sign of $D_{D}$ back to positive for comparison purposes. This decline-growth (second) difference, $D$ , in equation (2)—a DID estimator for our study—can be interpreted in two ways. First, $D$ indicates the post-pre decline difference in $E$ while taking into consideration the post-pre growth differences. Alternatively, we can apply $D$ for a two-year period of unchanged state aid and alternating enrollment when, for example, enrollment declines by one percent one year and then grows by one percent the next (a decline-growth period). As the second interpretation of $D$ , a positive and significant $D$ indicates that districts’ $E$ is $D$ % lower after a decline-growth postperiod than after a decline-growth preperiod, suggesting that districts have a significantly negative combined response to AEFA.⁷ This second interpretation is helpful in growth-dampening cases.

Valid causal interpretations of $D_{D}$ , $D_{G}$ , and $D$ rely on a key assumption that in the absence of the AEFA, districts’ postperiod responses to enrollment decline and growth would have been the same as their preperiod responses; that is, in the counterfactual scenario, $α_{A} = α_{B}$ and $β_{A} = β_{B}$ , therefore, $D =$ 0. Given this assumption, AEFA would be the sole explanation for statistically significant $D_{D}$ , $D_{G}$ , and $D$ .⁸

The estimated elasticity coefficients of $α$ s and $β$ s from total current expenditures ( $E$ ) in equation (1) imply how total current expenditures per pupil ( $\bar{E}$ ) change with enrollment. For example, in cases of enrollment growth, $\bar{E}$ decreases when $E$ stays unchanged or increases at a smaller percentage rate than the percentage enrollment growth rate (that is, $β < 1$ ). Similarly, $\bar{E}$ increases in decline years when $E$ remains unchanged or declines at a smaller percentage rate than the percent decline in enrollment (that is, $α > - 1$ ).⁹ However, we also present a set of results with expenditures per pupil for reference. The postregression results using question (2) are the same for total as well as per-pupil expenditures.

Equation (2) is designed to find the combined AEFA-induced effect on the average school district in Arizona. However, we hypothesize that AEFA may induce differential effects depending on district types. For the second research question, we put districts into quartiles using each district’s average sample-period median household income ( $\bar{H}$ ). Quartile 1 districts have the lowest $\bar{H}$ and districts in the top quartile (quartile 4) have the highest $\bar{H}$ . We estimate equation (3):

\begin{array}{l} Δ \ln (E_{i t}) = γ Δ W_{i t} + θ Δ O_{i t} + \sum_{t = 2012}^{2020} δ_{t} Δ d_{t} + \sum_{T = A, B}^{n = 1, 2, 3, 4} α_{T}^{n} Δ_{- T}^{n} \ln (N_{i t}) \\ + \sum_{T = A, B}^{n = 1, 2, 3, 4} β_{T}^{n} Δ_{+ T}^{n} \ln (N_{i t}) + ε_{i t} \end{array}

(3)

where superscript $n$ indicates quartiles. $Δ_{- T}^{n}$ equals $- Δ \ln (N_{t})$ when $Δ \ln (N_{t}) < 0$ for group $n$ in period $T$ and 0 otherwise; similarly, $Δ_{+ T}^{n}$ equals $Δ \ln (N_{t})$ when $Δ \ln (N_{t}) \geq 0$ for group $n$ in period $T$ and 0 otherwise. Using equation (2), we examined if each group $n$ has a decline-growth difference in testing $D_{n} = (- D_{D n} - D_{G n})$ , where $D_{D n} = (α_{A}^{n} - α_{B}^{n})$ and $D_{G n} = (β_{A}^{n} - β_{B}^{n})$ .

Given that AEFA primarily affects state aid in decline years, we also conducted another series of postregression DID tests by comparing the post-pre decline differences of each group pair’s ( $p$ ) $E$ in response to enrollment declines ( $D_{D p}$ ). For example, a test for the pair of groups 4 and 1 ( $p = 41$ ) is $D_{D 41} = (D_{D 4} - D_{D 1})$ . A negative and significant $D_{D 41}$ suggests that AEFA has a larger decline-aggravating effect on group 4 districts than on group 1 districts. Finally, we take a series of third differences ( $D_{p}$ ’s) by comparing decline-growth differences across groups. For example, a positive and significant $D_{41}$ indicates that group 4’s combined (i.e., post-pre and decline-growth differences) reduction in $E$ is larger (in absolute value) than group 1’s combined reduction. For cross-group comparisons, we use the lowest-income districts as the comparison group for three other district quartiles.

In addition to total current expenditures, we also employed other dependent variables—namely three categorical components of the current expenditures, capital spending, local revenue, and state aid. For the third research question, we employed the total number of full-time-equivalent (FTE) teachers, teacher aides (including paraprofessionals and short-term substitute teachers), and administrative personnel. Also, additional dependent variables are the total numbers of teachers with different experience levels and academic credentials (BA and MA degrees).

Summary Statistics

Table 2 provides the summary statistics and data sources we used for our estimations. The key dependent variable, namely total current expenditures ( $E$ ), consists of expenditures on classroom instruction and classroom supply (or instruction, for short), administration (those related to business operations of the district and school administration), and support services including student support services (e.g., social work, health, speech pathology, and audiology) and other support services (e.g., media services, maintenance, transportation).¹⁰ The average school district in Arizona spends $41.3 million in $E$ with a sizeable standard deviation of $74.5 million; 54% of the total current expenditures is spent on instruction, followed by spending on support services (35.3%) and administration (10.4%). The mean total current expenditures per pupil ( $\bar{E}$ ) is $11,396. The mean $E$ in postperiod decline years is nearly 19% higher than in preperiod decline years ($49 million vs. $41 million); the percent post-pre decline difference in $\bar{E}$ is only 0.6% ($11,695 million v. $11,628 million). Table A1 (letter A before a table number indicates that the table is in the appendix) provides additional summary statistics of key variables by four $\bar{H}$ -based district quartiles.

Table 2

Summary Statistics (2012−2020)

Variables	Obs	Mean	Std. Dev.	Min	Max	Source
Dependent variables
Total current expenditures ( $E$ )^a	1,707	41.3	74.5	0.9	554.8	1
$E$ when $Δ N < 0$ and $t \geq$ 2018^b	306	48.7	84.8	1.0	545.6	1, 2
$E$ when $Δ N < 0$ and 18	511	41.0	79.5	0.9	540.1	1, 2
$E$ when $Δ N \geq 0$ and $t \geq$ 2018	263	34.8	62.6	0.9	378.4	1, 2
$E$ when $Δ N \geq 0$ and $t <$ 2018	627	40.7	69.2	0.9	554.8	1, 2
Total current expenditures per pupil ( $\bar{E}$ )	1,707	11,396	4,630	2,175	45,060	1, 2
$\bar{E}$ when $Δ N < 0$ and $t \geq$ 2018^b	306	11,695	4,809	5,872	45,060	1, 2
$\bar{E}$ when $Δ N < 0$ and $t <$ 2018	511	11,628	4,638	4,352	34,156	1, 2
$\bar{E}$ when $Δ N \geq 0$ and $t \geq$ 2018	263	11,474	4,600	5,731	28,286	1, 2
$\bar{E}$ when $Δ N \geq 0$ and $t <$ 2018	627	11,028	4,533	2,175	31,883	1, 2
Classroom instruction and supply expenditures	1,707	22.4	41.9	0.2	312.8	1
Administrative expenditures	1,706	4.3	7.0	0.04	49.9	1
Support services expenditures	1,705	14.6	26.3	0.1	202.5	1
Capital expenditures	1,685	1.4	2.7	0.00006	27.9	1
Local revenue	1,699	13.7	28.9	0.0002	184.6	1
State aid	1,710	18.3	34.4	0.0178	303.6	1
FTE teachers	1,706	256.0	476.8	1	3,345	1
FTE teacher aides	1,695	77.0	143.3	0.5	1,385	1
FTE administrative personnel	1,702	16.8	24.7	0.04	168	1
Enrollment statistics
Total enrollment	1,710	4,706	8,616	37	61,151	1, 2
$Δ N$ ∆N when $Δ N < 0$ and $t \geq$ 2018^b (53.9%)	307	−3.5	3.4	−19.6	−0.01	1, 2
$Δ N$ ∆N when $Δ N < 0$ and $t <$ 2018 (53.9%)	512	−4.2	4.5	−33.6	−0.02	1, 2
$Δ N$ ∆N when $Δ N \geq 0$ and $t \geq$ 2018 (46.1%)	263	4.0	4.1	0.01	23.0	1, 2
$Δ N$ ∆N when $Δ N \geq 0$ and $t <$ 2018 (46.1%)	438	4.0	4.4	0.01	31.3	1, 2
Other control variables
% of school-age children in poverty (% poor)	1,710	25.0	11.1	3.90	61.4	3
% of ELL students (% ELL)	1,710	7.5	9.2	0	58.5	4
% of students with disabilities (% special ed.)	1,710	14.8	4.9	0	42.7	4
Median household income (median income)	1,710	46,601	16,102	9,206	116,331	5
Tax share	1,701	0.0	0.0	0.00003	0.19	1, 5
% people over 25 with college or higher education (% college)	1,710	19.3	12.4	0	71.3	4
% owner-occupied housing units (% occupied)	1,710	67.7	16.8	0	100	4
% population over 65 (% old)	1,710	18.6	12.5	0	71.5	4

Notes: There are 190 school districts. Data sources are Arizona Department of Education (1), authors’ calculations (2), Small Area Income and Poverty Estimates (3), Common Core Data (4), and American Community Surveys (5). The Arizona Department of Education data on free and reduced-price lunch students, ELL students, and students with disabilities contain many missing observations. We, therefore, use data from source 3 as a proxy for the percentage of free and reduced-price lunch students. We also use data from source 4 for the percentage of ELL students and students with disabilities. The data from sources 1 and 4 on nonmissing observations of these two variables are similar. Additional summary statistics can be found in Table A1.

Fiscal-dependent variables are in millions of dollars. All financial variables (including median household income) are adjusted for inflation and in 2020 dollars using the Bureau of Economic Analysis government price indexes.

The annual enrollment change is $Δ N = (((N_{t} / N_{t - 1}) - 1) \times 100)$ ; $Δ N_{t < 2018}$ starts in 2013. The numbers in parentheses indicate the shares of observations to the total number of observations (950 and 570) for the post- and preperiods, respectively.

Enrollment is the key independent factor in our estimations. We used ADM as a measure of enrollment. In the previously discussed state aid formula, ADM captures the total enrollment of part-time and full-time students who attend schools within a school district’s boundary, minus any student withdrawals for each day through the first 100 days of instruction. The average enrollment of 4,706 does not reflect the substantial enrollment variation by income. The highest-income quartile’s average enrollment is four times larger than the average enrollment of the lowest-income quartile (9,158 vs. 2,275 in Table A1). Table 2 also shows that in both pre- and postperiods, the relative frequencies of enrollment decline and growth are consistently 53.9% and 46.1%, respectively. While the mean annual enrollment increase is 4% for both pre- and postperiods, the mean annual enrollment decrease in the postperiod is 3.5%, which is slightly less than 4.2% in the preperiod. Figure 2 shows the annual shares (relative frequencies) of school districts with enrollment decline. The share started at over 60.5% in 2013, dropped to 45.8% in 2015, and became stable at around 55% between 2016 and 2020. (Table A1 provides additional quartile-specific variations in mean annual enrollment decreases and increases.)

Figure 2.

Annual shares of school districts with enrollment decline (2013−2020).

Table 2 shows that the average district has 256 FTE teachers, 77 FTE teacher aides, and nearly 17 FTE administrative people. Table A2 shows that teachers with 15 or more years of experience constitute the largest group (nearly 30%), followed by teachers with 1–5 years of experience (29%) and those with 6–10 and 11–14 years of experience (25.3% and 15.8%, respectively).

Results

Table 3 documents the main results for types of expenditures, local revenue, and state aid in total (Panel A) and per pupil (Panel B) terms. Expenditure and revenue items (columns 1–6) are basically within a school district’s control, while state aid (column 7) is not. Column 1 shows that school districts seem to cut total current expenditures ( $E$ ) slightly more after AEFA than before AEFA. Specifically, for a one-percent decline in enrollment, school districts reduce their total expenditures by 0.35% ( $α_{B}$ ) and 0.46% ( $α_{A}$ ) in the pre- and postperiods, respectively. The first difference between $α_{A}$ and $α_{B}$ , $D_{D} = α_{A} - α_{B},$ is $-$ 0.11 and not statistically significant. Also, districts significantly increase $E$ by approximately 0.4% ( $β_{B}$ ) for a one-percent preperiod enrollment growth rate,¹¹ but the postperiod increase is only 0.16 ( $β_{A}$ ) and not statistically significant. The first difference between $β_{A}$ and $β_{A}$ , $D_{G} = β_{A} - β_{B},$ is $-$ 0.24, suggesting that AEFA seems to have a growth-dampening, though insignificant, effect in growth years. The second difference, $D$ , between ( $- D_{D}$ ) and $D_{G}$ is 0.36 (Panel C) but is not statistically significant, suggesting that AEFA has an insignificant combined effect on the average district in Arizona.

Table 3

Main Fiscal Results

Key Vars.	Total Current ( $E$ )	Instruction( $E_{I}$ )	Administration ( $E_{A}$ )	Support Services ( $E_{S}$ )	Capital	Local Revenue	State Aid
Key Vars.	(1)	(2)	(3)	(4)	(5)	(6)	(7)
Panel A: Total
$α_{A}$	−0.464***	−0.663***	−0.367**	0.176	0.0521	−0.0777	−0.786***
	(0.135)	(0.175)	(0.168)	(0.276)	(1.250)	(0.483)	(0.207)
$α_{B}$	−0.346***	−0.394**	−0.179	−0.440***	−0.830	−0.219	−0.497*
	(0.118)	(0.176)	(0.151)	(0.146)	(0.724)	(0.310)	(0.284)
$β_{A}$	0.159	0.233	−0.170	0.325	−0.776	−0.208	0.774***
	(0.177)	(0.266)	(0.264)	(0.307)	(1.167)	(0.307)	(0.252)
$β_{B}$	0.397**	0.648***	0.0235	0.218	1.207*	0.00526	0.638***
	(0.155)	(0.208)	(0.369)	(0.325)	(0.716)	(0.292)	(0.206)
Panel B: Per pupil
$α_{A}$	0.536***	0.337*	0.633***	1.176***	1.052	0.922*	0.214
	(0.135)	(0.175)	(0.168)	(0.276)	(1.250)	(0.483)	(0.207)
$α_{B}$	0.654***	0.606***	0.821***	0.560***	0.170	0.781**	0.503*
	(0.118)	(0.176)	(0.151)	(0.146)	(0.724)	(0.310)	(0.284)
$β_{A}$	−0.841***	−0.767***	−1.170***	−0.675**	−1.776	−1.208***	−0.226
	(0.177)	(0.266)	(0.264)	(0.307)	(1.167)	(0.307)	(0.252)
$β_{B}$	−0.603***	−0.352*	−0.977***	−0.782**	0.207	−0.995***	−0.362*
	(0.155)	(0.208)	(0.369)	(0.325)	(0.716)	(0.292)	(0.206)
Panel C: Postregression tests of $D$ in equation (2)
$D$	0.357	0.684	0.382	−0.723	1.101	0.0723	0.152
	[0.352]	[0.516]	[0.477]	[0.605]	[2.475]	[0.880]	[0.536]
# of obs.	1512	1512	1510	1509	1485	1502	1517

Notes: As in equation (1), all the dependent variables are logged and first differenced. The results are estimated with all other independent variables reported in Table 2. The full results with all other independent variables and without any other control variable are reported in Tables A3 and A4, respectively. $D = - D_{D} - D_{G} = - (α_{A} - α_{B}) - (β_{A} - β_{B}) .$ When a postregression test on a first difference (i.e., $D_{D} = (α_{A} - α_{B})$ or $D_{G} = (β_{A} - β_{B})$ ) is stastistically significant at the 5% level, the first coefficient of the difference is in bold. Robust standard errors clustered at the school district level are in parentheses. Standard errors for postregression tests are in brackets.

0.10; **0.05; ***0.01.

As predicted, the changes in $E$ are reflected in changes to total current expenditures per pupil, $\bar{E}$ (Panel B). Because the percent decreases in $E$ (0.35% and 0.46%) are less than a 1-percent decline in enrollment, $\bar{E}$ increases. Similarly, $\bar{E}$ decreases because $E$ does not significantly increase or increase at a lower rate relative to a 1-percent enrollment growth.

Of all three current expenditure components, instruction expenditures $(E_{I})$ follow the most closely the pattern of changes of both total and per pupil current expenditures. Interestingly, in postperiod decline years, school districts cut administrative spending $(E_{A})$ by 3.7% (significant at the 5% level) but did not significantly change spending on support services $(E_{S})$ . Of all expenditures, capital spending has no statistically significant coefficient for the postperiod. This finding makes sense because capital spending is usually harder to change in response to an annual enrollment change and because under AEFA, district additional assistance—a capital component of state aid—is still based on prior-year enrollment. In column 7, total state aid in the postperiod decreases and increases, as expected, with enrollment decline and growth, respectively. The sizes of these changes are slightly larger in absolute value than their respective preperiod changes. However, school districts do not seem to change their total local revenue in response to these changes in total state aid (Panel A, column 6). Finally, as common with the first difference tests of $D_{D}$ and $D_{G}$ for $E$ , none of these tests for columns 2 to 7 are statistically significant at the 5% level, and none of the $D$ tests in Panel C revealed statistically significant results, either. As noted, the results of the post-regression tests on $D$ are the same for total expenditure regressions as expenditure-per-pupil regressions.

The insignificance of tests on first and second differences in Table 3 could result from averaging out heterogeneous district responses. Table 4 documents the results of estimating AEFA-induced responses in total current spending and its three components by district groups categorized by the mean sample-period median household income ( $\bar{H}$ ). Columns 1–4 report the results of the four expenditures’ estimated coefficients, and columns 5–8 report their difference tests. We find that for a 1-percent postperiod enrollment decline, the highest-income quartile (i.e., quartile 4) seems to have the largest cut of 0.7% in $E$ (column 1). This finding is understandable given that this quartile has the lowest relative frequency of preperiod double-decline years (Table A6), suggesting that this quartile is likely to benefit the most from aid-stabilizing PYE in preperiod decline years and thus to have a strong response to AEFA. None of the first, second, or third differences in $E$ for any quartile or quartile comparison is statistically significant at the 5% level (column 5).

Table 4

Fiscal Results of Heterogeneity Analyses for Four $\bar{H}$ -based District Quartiles

Keyvars	Estimates				Tests	Postregression Tests
	$E$	$E_{I}$	$E_{A}$	$E_{S}$		$E$	$E_{I}$	$E_{A}$	$E_{S}$
	(1)	(2)	(3)	(4)		(5)	(6)	(7)	(8)
$α_{A}^{1}$	−0.478*	−0.693**	−0.243	0.486
	(0.267)	(0.280)	(0.198)	(0.514)	$D_{1}$	−0.041	−0.087	−0.392	−0.571
$α_{B}^{1}$	−0.314***	−0.455***	−0.316**	−0.215*		[0.453]	[0.611]	[0.547]	[1.034]
	(0.0869)	(0.139)	(0.150)	(0.111)
$β_{A}^{1}$	0.319	0.586	0.543	−0.267	$D_{2}$	1.015*	1.960**	0.520	−0.488
	(0.305)	(0.562)	(0.359)	(0.695)		[0.607]	[0.843]	[0.622]	[0.801]
$β_{B}^{1}$	0.113	0.261	0.224	−0.137
	(0.204)	(0.238)	(0.277)	(0.539)	$D_{3}$	0.066	0.140	0.272	−0.594
$α_{A}^{2}$	−0.323*	−0.533***	−0.164	0.103		[0.423]	[0.618]	[0.572]	[0.801]
	(0.164)	(0.186)	(0.275)	(0.283)
$α_{B}^{2}$	−0.0998	−0.0486	0.236	−0.493	$D_{4}$	0.908*	1.332**	2.196*	−0.673
	(0.240)	(0.408)	(0.328)	(0.328)		[0.488]	[0.636]	[1.318]	[1.077]
$β_{A}^{2}$	−0.226	−0.425	−0.255	0.366
	(0.285)	(0.263)	(0.482)	(0.660)	$D_{D 21}$	−0.059	−0.246	−0.472	−0.105
$β_{B}^{2}$	0.565*	1.051**	−0.134	0.474		[0.359]	[0.499]	[0.464]	[0.579]
	(0.304)	(0.488)	(0.378)	(0.341)
$α_{A}^{3}$	−0.548**	−0.600*	−0.837***	−0.0892	$D_{D 31}$	0.191	0.223	−0.416	−0.136
	(0.244)	(0.306)	(0.316)	(0.354)		[0.370]	[0.429]	[0.440]	[0.555]
$α_{B}^{3}$	−0.574***	−0.585***	−0.494**	−0.653***
	(0.141)	(0.173)	(0.191)	(0.199)	$D_{D 41}$	−0.302	−0.572	−1.322	−0.291
$β_{A}^{3}$	0.275	0.419	0.0275	0.209		[0.364]	[0.411]	[0.881]	[0.641]
	(0.310)	(0.438)	(0.368)	(0.336)
$β_{B}^{3}$	0.368**	0.545***	−0.0432	0.179	$D_{21}$	1.056*	2.047**	0.913	0.083
	(0.151)	(0.151)	(0.192)	(0.620)		[0.626]	[0.866]	[0.708]	[1.129]
$α_{A}^{4}$	−0.704***	−1.051***	−0.580	−0.0761
	(0.184)	(0.228)	(0.361)	(0.422)	$D_{31}$	0.107	0.227	0.665	−0.023
$α_{B}^{4}$	−0.237	−0.241	0.669	−0.486*		[0.549]	[0.745]	[0.726]	[1.223]
	(0.188)	(0.260)	(0.731)	(0.264)
$β_{A}^{4}$	0.325	0.490	−0.786*	0.796	$D_{41}$	0.949*	1.419**	2.588**	−0.102
	(0.215)	(0.382)	(0.463)	(0.485)		[0.553]	[0.704]	[1.241]	[1.337]
$β_{B}^{4}$	0.767**	1.013***	0.161	0.532
	(0.342)	(0.278)	(1.483)	(0.721)

Notes: There are 1,512 observations. The results are estimated with all control variables listed in Table 2. The results without any variables are similar to those reported in this table and thus not reported. Robust standard errors clustered at the school district level are in parentheses. Standard errors for postregression tests are in brackets. When a postregression test on a first difference (i.e., $D_{D} = (α_{A} - α_{B})$ or $D_{G} = (β_{A} - β_{B})$ is stastistically significant at the 5% level, the first coefficient of the difference is in bold in columns 1−4. Columns 5−8 are the results of other postregression second and third difference tests. $D_{1}$ equals $(- D_{D} - D_{G})$ for group 1. $D_{D 21}$ is a test to compare group 2’s $D_{D}$ and group 1’s $D_{D}$ , or $D_{D 21} = D_{D 2} - D_{D 1}$ . The triple difference test of $D_{21}$ equals $(D_{2} - D_{1})$ .

0.10; **0.05; ***0.01.

However, AEFA-induced effects on $E_{I}$ and $E_{A}$ are more significant, especially for second and third differences. As indicated earlier, the lowest-income quartile (quartile 1) serves as a comparison group. This group has the smallest and close-to-0 $D_{1}$ for $E_{I}$ . Column 6 shows that quartile 2 and 4 districts’ $D_{2}$ and $D_{4}$ are both positive and significant, indicating that their $E_{I}$ s are nearly 2% and 1.3% lower, respectively, after a decline-growth postperiod than after a similar preperiod. Also, the combined $E_{I}$ reductions of the two quartiles are larger by similar sizes ( $D_{21} =$ 2 and $D_{41} =$ 1.4) than those of the comparison quartile. Quartile 4’s combined reduction in $E_{A}$ is approximately 2.6% larger than quartile 1’s combined $E_{A}$ reduction.

Table 5 reports the results for the third research question on how AEFA may affect district personnel, especially teachers. Column 1 shows that districts are found to reduce 0.63% of their FTE teachers for a 1-percent decline in enrollment in both the pre- and postperiods. Also, teacher aides and administrative people are not significantly changed in decline and growth years in the pre-and postperiods (columns 2 and 3). Panel B shows that none of the DID estimators are statistically significant.

Table 5

Main Results on District Personnel

Key Vars.	FTE Teachers	FTE Teacher Aides	FTE Admin People
Key Vars.	(1)	(2)	(3)
Panel A: Estimates
$α_{A}$	−0.630***	−0.627*	−0.258
	(0.201)	(0.376)	(0.328)
$α_{B}$	−0.627***	−0.505**	0.126
	(0.140)	(0.247)	(0.363)
$β_{A}$	−0.0758	0.691*	0.0367
	(0.224)	(0.376)	(0.579)
$β_{B}$	0.288**	0.164	0.372
	(0.116)	(0.400)	(0.315)
Panel B: Postregression tests of $D$ in equation (2)
$D$	0.368	-0.406	0.719
	[0.481]	[0.793]	[1.000]
Obs.	1509	1509	1513

Notes: The results are estimated with all other independent variables in Table 2. All dependent variables are logged. When a postregression test on a first difference (i.e., $D_{D} = (α_{A} - α_{B})$ or $D_{G} = (β_{A} - β_{B})$ is statistically significant at the 5% level, the first coefficient of the difference is in bold. The results without control variables are similar and not reported.

0.10; **0.05; ***0.01.

In a heterogeneity analysis, column 1 of Table 6 shows that the numbers of FTE teachers for districts in quartiles 2 and 4 are 1.7% and 1.4% lower, respectively, after a decline-growth postperiod than after a similar preperiod. The highest-income quartile’s combined reduction in FTE teachers is nearly 2% larger in absolute value than the lowest-income quartile’s combined reduction. These findings are consistent with the results on instruction spending reported in column 6 of Table 4. Column 1 also shows that AEFA has a significantly larger decline-aggravating effect on FTE teachers in the highest-income districts than on those in the lowest-income districts ( $D_{D 41}$ = −1.4). While district groups do not show significant second and third differences in their response to teachers with BA degrees (column 2) and teachers with 6–10 years of experience (column 5), the remaining columns show the lowest- vs. highest-income quartiles’ AEFA-induced responses to teachers with MA degrees and with different experience levels. For example, we find that AEFA has a significantly larger decline-aggravating effect on teachers with 1–5 and 11–14 years of experience in the highest-income districts than on those in the lowest-income districts. The highest-income quartile’s combined reduction in teachers with 1–5 years of experience is nearly 6.5% larger in absolute value than the lowest-income quartile’s combined reduction.¹²

Table 6

Postregression Test Results of Heterogeneity Analyses on District Personnel for Four $\bar{H}$ -based District Quartiles

	Total FTE Teachers	BA FTE Teachers	MA FTE Teachers	FTE Teachers (1–5 years of experience)	FTE Teachers (6–10 years of experience)	FTE Teachers (11–14 years of experience)	FTE Teachers ( $\geq$ 15 years of experience)
	(1)	(2)	(3)	(4)	(5)	(6)	(7)
$D_{1}$	−0.578	−0.680	0.334	−1.430	1.254	0.626	1.059
	[0.708]	[1.698]	[1.017]	[2.979]	[1.888]	[2.073]	[1.930]
$D_{2}$	1.731***	0.637	1.280	4.448*	−0.202	−0.369	4.427**
	[0.467]	[1.449]	[0.883]	[2.326]	[1.947]	[1.380]	[1.868]
$D_{3}$	−0.135	0.010	0.995	−4.966***	0.420	−3.007	−2.371
	[0.325]	[1.492]	[0.754]	[1.721]	[2.218]	[3.041]	[1.734]
$D_{4}$	1.386***	1.661	1.638**	5.113***	3.860	2.034	5.183**
	[0.469]	[1.028]	[0.836]	[1.960]	[2.514]	[2.356]	[2.579]
$D_{D 21}$	−0.895*	−0.323	−1.087	−4.605*	3.018*	−1.954	−1.719
	[0.470]	[1.183]	[1.078]	[2.514]	[1.782]	[1.350]	[1.715]
$D_{D 31}$	0.133	−0.129	−0.216	−1.852	1.308	0.554	0.914
	[0.517]	[1.098]	[1.088]	[2.278]	[1.903]	[2.314]	[1.264]
$D_{D 41}$	−1.439***	−1.454	−1.374	−5.306**	−0.617	−6.016***	−4.125*
	[0.481]	[0.936]	[1.015]	[2.386]	[1.814]	[2.000]	[2.307]
$D_{21}$	2.309***	1.317	0.945	5.878*	−1.456	−0.995	3.368
	[0.655]	[2.052]	[1.286]	[3.267]	[2.371]	[2.139]	[2.485]
$D_{31}$	0.443	0.690	0.660	−3.536	−0.834	−3.634	−3.430
	[0.681]	[2.025]	[1.238]	[3.186]	[2.717]	[3.403]	[2.593]
$D_{41}$	1.965***	2.341	1.304	6.543**	2.606	1.407	4.124
	[0.648]	[1.799]	[1.187]	[3.085]	[2.703]	[2.712]	[2.908]

Notes: There are 1,509 observations. Table A7 provides the results on key variables used to compute postregression tests in this table. All dependent variables are logged with undefined values being replaced by 0s for columns 2–7. The shares of 0s for dependent variables in these columns are 1.4%, 1.1%, 6.6%, 6.1%, 8.3%, and 2.8%, respectively. The results without these logged undefined observations are similar to those reported in this table. In addition, the results without control variables are similar to those with control variables and thus not reported.

0.10; **0.05; ***0.01.

Conclusion

State aid has been a major funding source for most school districts across the United States, including those in Arizona. A measure of enrollment is a key factor in the formulas that states use to allocate education aid. Two key issues are related to determining student enrollment: count methods and, relatedly, which year of data to use in aid formulas. Regarding the former issue, Ely and Fermanich (2013) classify ten student count methods based on whether the count is done at a single time or multiple times and whether they use membership or attendance. Several scholars have examined the potential fiscal and academic consequences of different student count methods (Baker, 2014; Ely & Fermanich, 2013; Hahnel & Baumgardner, 2022; Knight & Olofson, 1918). Regarding the second issue of enrollment determination, states vary in whether they use student counts in prior or current years, or a combination of both (Barnard & Smith, 2021). Specifically, Table A9 in the appendix shows that 22 states (e.g., Kansas) fund schools based on prior-year student counts, and nine other states factor prior-year counts into the final enrollment for state aid. However, unlike the first issue of enrollment determination, no study has yet examined the potential consequences of using, or changing between, different enrollment years. This study, to the best of our knowledge, represents the first attempt to fill this literature gap by focusing on Arizona.

In Arizona, school districts experiencing annual enrollment growth have consistently received state aid based on their current-year enrollment measured by ADM. Prior to 2017, the state used prior-year enrollment (PYE) to calculate education aid for districts with annual enrollment decline. However, with the enactment of the Arizona Education Finance Amendment (AEFA) in 2017, the state has transitioned to using current-year enrollment for education aid allocation to enrollment-declining districts. This study offers significant contributions to the literature as it examines, for the first time, the short-term effects of AEFA three years after its full implementation. Specifically, it analyzes the potential impacts of AEFA not only on statewide average school district inputs but also on heterogeneous district types as well as on district personnel, including teachers with varying academic credentials and experience levels.

First, our theoretical analysis suggests that when the state aid formula switches from prior-year to current-year enrollment, this change may elicit school districts’ fiscal responses in both decline and growth years. Specifically, AEFA may have two primary effects on school districts—decline-aggravating and growth-dampening. The former refers to districts’ inclination to reduce inputs more in postperiod decline years than in preperiod decline years, whereas the latter pertains to their propensity to increase inputs less in postperiod growth years than in preperiod growth years. A combination of the two effects may result in lower inputs in the postperiod.

Using a DID design on a data panel of 190 Arizona school districts during 2012–2020, we find that the DID estimators for total current expenditures (and their expenditure components) and FTE teachers show expected signs but are not statistically significant. These results suggest that the AEFA has little effect on the average district of the entire sample during the three-year period of its implementation. Despite the lack of significant effects on the average district, we find strong evidence of heterogenous AEFA-induced effects on inputs. AEFA has significantly larger decline-aggravating and growth-dampening effects on the highest-income districts than on the lowest-income districts. These differential effects are most pronounced in instructional expenditures, administration expenditures, total FTE teachers, and particularly teachers with 1–5 years of experience. Specifically, during the three years of AEFA, the highest-income districts reduce instructional and administrative expenditures, as well as the number of teachers, especially less-experienced teachers, more than the lowest-income districts. A plausible explanation for the disparity in responses between the highest- and lowest-income districts is that the former districts are more likely to benefit from aid-stabilizing PYE in decline preperiod years, leading to a stronger response to AEFA.

Our empirical approach supports a causal interpretation of the AEFA effects, or lack thereof, on Arizona school districts. First, our findings largely align with theoretical predictions of how school districts would respond to AEFA. Second, the model controls for time-invariant and time-varying factors that may bias the estimated results. However, given that our DID design is not conventional, there may be potential bias in our estimates from contemporaneous time-varying omitted factors, especially those in the postperiod.

Our study provides valuable insights into the effects of AEFA on Arizona school districts’ inputs. While these insights cannot be generalized to other states, our study’s results might be intriguing for any of the 22 states using prior-year enrollment and contemplating a switch to current-year enrollment in their education aid formula. For example, Kansas’s House Bill 2040 in 2023 proposed to use current-year enrollment instead of the greater of the preceding or second preceding year’s enrollment. Finally, our study leaves some questions unanswered. For example, has the AEFA had any effect on student achievement, particularly when using student-level data?¹³ Also, our sample period ends just before the pandemic, which has been shown to have a negative effect on school enrollment (Chatterji & Li, 2021; Dee & Murphy, 2021; Scafidi et al., 2021). Several states—for example, North Carolina (Fofaria, 2020), Delaware (Office of the Governor, 2020), and especially Arizona (Hernandez & Brodie, 2020)—provided temporary relief funding to help districts with declining enrollment. How does the combination of temporary relief funding and AEFA affect school districts in these states? What will be the medium- and long-term effects of the current-year-enrollment aid policy once the temporary funding ends? These questions warrant future research.

Supplemental Material

sj-docx-1-ero-10.1177_23328584231210281 – Supplemental material for The Short-Term Effects of the Shift From Prior-Year to Current-Year Enrollment on School Inputs in Arizona

Supplemental material, sj-docx-1-ero-10.1177_23328584231210281 for The Short-Term Effects of the Shift From Prior-Year to Current-Year Enrollment on School Inputs in Arizona by Phuong Nguyen-Hoang and Angie Nga Le in AERA Open

Footnotes

Acknowledgements

We would like to thank David Frisvold for his insights on empirical strategies and Alex Sukalski for his help with collecting the data on teachers.

Correction (January 2024):

This article has been updated with corrections in some of the Greek characters and equations under the Notes section since its original publication.

Declaration of Conflicting Interests

The author(s) declared no potential conflicts of interest with respect to the research, authorship, and/or publication of this article.

Funding

The author(s) received no financial support for the research, authorship, and/or publication of this article.

ORCID iDs

Phuong Nguyen-Hoang

Angie Nga Le

Supplemental Material

Supplemental material for this article is available online.

Notes

Authors

PHUONG NGUYEN-HOANG is associate professor at School of Planning and Public Affairs, University of Iowa, 334 Jessup Hall, Iowa City, IA 52242; email: phuong-nguyen@uiowa.edu. His research revolves around evaluating public, fiscal, and education policies.

ANGIE NGA LE is a postdoctoral associate in the New Jersey State Policy Lab at Rutgers, the State University of New Jersey, 33 Livingston Avenue, New Brunswick, NJ 08901; email: angie.le@rutgers.edu. Her research focuses on the impact of government-funded programs on local governments’ behaviors and local public services. Le’s research includes topics such as intergovernmental grant policy, fiscal federalism, public school finance, and energy subsidy policy.

References

Arizona Association of School Business Officials. (2017). Arizona School finance summary manual.

Arizona Department of Education. (2004). Fiscal year 2004 appropriations report. https://www.azleg.gov/jlbc/04app/adeassis.pdf

Arizona Department of Education. (2017). Fiscal year 2017 appropriations report. https://www.azleg.gov/jlbc/17AR/ade.pdf

Baker

B. D.

(2014). Not making the grade: How financial penalties for school absences hurt districts serving low-income, chronically ill kids. ChangeLab Solutions. https://edsource.org/wp-content/uploads/2022/03/School-Financing_StatePolicymakers_FINAL_09302014.pdf

Barnard

Smith

A. G.

(2021). How should states count students to calculate school funding? Reason Foundation. https://reason.org/commentary/how-should-states-count-students-to-calculate-school-funding/

Card

Payne

A. A.

(2002). School finance reform, the distribution of school spending, and the distribution of student test scores. Journal of Public Economics, 83(1), 49–82. https://doi.org/10.1016/S0047-2727(00)00177-8

Cavin

E. S.

Murnane

R. J.

Brown

R. S.

(1985). School district responses to enrollment changes: The direction of change matters! Journal of Education Finance, 10(4), 426–440.

Center for Public Education. (2021). How states implement hold-harmless provisions in 2020 and 2021. https://www.nsba.org/-/media/NSBA/File/cpe-hold-harmless-research-brief-2021.pdf

Chatterji

(2021). Effects of COVID-19 on school enrollment. Economics of Education Review, 83, 102128. https://doi.org/10.1016/j.econedurev.2021.102128

10.

Dee

Murphy

(2021). Patterns in the pandemic decline of public school enrollment. Educational Researcher, 50(8), 566–569. Scopus. https://doi.org/10.3102/0013189X211034481

11.

Duncombe

W. D.

Nguyen-Hoang

Yinger

(2015). Measurement of cost differentials. In Ladd

H. F.

Goertz

M. E.

(Eds.), Handbook of research in education finance and policy (pp. 260–278). Routledge.

12.

Duncombe

W. D.

Yinger

(2011). Are education cost functions ready for prime time? An examination of their validity and reliability. Peabody Journal of Education, 86(1), 28–57. https://doi.org/10.1080/0161956X.2011.539954

13.

Edelman

M. A.

Knudsen

J. J.

(1990). An analysis of selected school aid compensation options for school districts with declining enrollment. Journal of Education Finance, 15(3), 319–332.

14.

Ely

T. L.

Fermanich

M. L.

(2013). Learning to count: School finance formula count methods and attendance-related student outcomes. Journal of Education Finance, 38(4), 343–369.

15.

Fahy

(2011). Education funding in Massachusetts: The effects of aid modifications on vertical and horizontal equity. Journal of Education Finance, 36(3), 217–243.

16.

Fan

Liang

(2020). The effects of California’s School Finance Reform: Empirical evidence from the local control funding formula (LCFF). Journal of Education Finance, 46(2), 140–157.

17.

Fofaria

(2020, September 2). Legislature passes COVID-19 relief, holds districts harmless for budget reductions due to declines in enrollment. https://www.ednc.org/nc-senate-passes-second-round-of-covid-19-relief-child-care-education-funding/

18.

Gigliotti

Sorensen

L. C.

(2018). Educational resources and student achievement: Evidence from the Save Harmless provision in New York State. Economics of Education Review, 66, 167–182. https://doi.org/10.1016/j.econedurev.2018.08.004

19.

Hahnel

Baumgardner

(2022). Student count options for school funding trade-offs and policy alternatives for California. Policy Analysis for California Education. https://files.eric.ed.gov/fulltext/ED619643.pdf

20.

Hernandez

Brodie

(2020, June 24). Gov. Ducey announces $270M plan to aid Arizona schools’ reopenings. https://kjzz.org/content/1595152/gov-ducey-announces-270m-plan-aid-arizona-schools-reopenings

21.

Hunter

Gifford

(2000). A taxpayer’s guide to public school finance. Goldwater Institute. https://eric.ed.gov/?id=ED457668

22.

Kelly

M. G.

(2021). How to reform without reforming: School district racial composition and Pennsylvania’s “fair” funding formula. Education and Urban Society, 54(9), 1143–1165. https://doi.org/10.1177/00131245211048426

23.

Knight

D. S.

Olofson

(1918). Funding school districts based on student attendance. Center for Education Research and Policy Studies. https://www.utep.edu/education/cerps/_Files/docs/briefs/CERPS_PolicyBrief5_Attendance.pdf

24.

Lafortune

Rothstein

Schanzenbach

D. W.

(2018). School finance reform and the distribution of student achievement. American Economic Journal: Applied Economics, 10(2), 1–26. https://doi.org/10.1257/app.20160567

25.

Murray

S. E.

Rueben

Rosenberg

(2007). State education spending: Current pressures and future trends. National Tax Journal, 60(2), 325–345. https://doi.org/10.17310/ntj.2007.2.08

26.

Nguyen-Hoang

Yinger

(2014). Education finance reform, local behavior, and student performance in Massachusetts. Journal of Education Finance, 39(4), 297–322. https://www.jstor.org/stable/24459265

27.

Office of the Governor. (2020, December 4). Governor Carney, Secretary Bunting announce one-time enrollment funding for schools. https://news.delaware.gov/2020/12/24/governor-carney-secretary-bunting-announce-one-time-enrollment-funding-for-schools/

28.

Roy

(2011). Impact of school finance reform on resource equalization and academic performance: Evidence from Michigan. Education Finance and Policy, 6(2), 137–167. https://doi.org/10.1162/EDFP_a_00030

29.

Roza

Fullerton

(2013). Funding phantom students: State policies insulate districts from making tough decisions. Education Next, 13(3), 8–17.

30.

Scafidi

Tutterow

Kavanagh

(2021). This time really is different: The effect of COVID-19 on independent K-12 school enrollments. Journal of School Choice, 15(3), 305–330. Scopus. https://doi.org/10.1080/15582159.2021.1944722

31.

Steinberg

M. P.

Quinn

Kreisman

Anglum

J. C.

(2016). Did Pennsylvania’s statewide school finance reform increase education spending or provide tax relief? National Tax Journal, 69(3), 545–582. https://doi.org/10.17310/ntj.2016.3.03

32.

Wooldridge

J. M.

(2020). Introductory econometrics: A modern approach (7th ed.). Cengage.

Supplementary Material

Please find the following supplemental material available below.

For Open Access articles published under a Creative Commons License, all supplemental material carries the same license as the article it is associated with.

For non-Open Access articles published, all supplemental material carries a non-exclusive license, and permission requests for re-use of supplemental material or any part of supplemental material shall be sent directly to the copyright owner as specified in the copyright notice associated with the article.

0.00 MB

0.12 MB