Academic,Attendance,and Behavioral Outcomes of a Suspension Reduction Policy: Lessons for School Leaders and Policy Makers

Abstract

Background: Exclusionary discipline (e.g. suspension and expulsion) is associated with lower student achievement, drop-out, and involvement in the juvenile justice system. Recently, states and school districts have begun to restrict exclusionary discipline, but there remains much to be learned about the potential impact on students. Research Design: I use a comparative interrupted time series to estimate whether a state policy prohibiting out-of-school suspension as a consequence for truancy affected student achievement, attendance, truancy, or disciplinary referrals. Findings: After testing a variety of specifications checks, I find evidence of slight increases in attendance, particularly for disadvantaged students, with suggestive evidence of improvements in test scores and reductions in disciplinary referrals for some students. Conclusions: These improvements were quite modest relative to what we might expect from an intuitively appealing policy and were likely influenced by incomplete compliance, particularly in areas serving more students from traditionally disadvantaged backgrounds. Implications for policy design and school leadership are discussed.

Keywords

exclusionary discipline suspensions attendance truancy policy implementation

Introduction and Literature Review

There are many concerns in the education community about exclusionary discipline such as out-of-school suspensions (OSS) and expulsions, which remove students from school for disciplinary reasons. Suspensions and racial disparities in suspensions are particularly common in the Southern states; in 1 year, 55% of the nation’s suspensions and 50% of the nation’s Black student suspensions occurred in 13 Southern states (Smith & Harper, 2015). A large body of evidence links exclusionary discipline to negative student outcomes related to academic achievement (e.g., Anderson, Ritter, & Zamarro, 2019; Arcia, 2006; Beck & Muschkin, 2012; Cobb-Clark, Kassenboehmer, Le, McVicar, & Zhang, 2015; Skiba & Rausch, 2004), grade retention and dropout (Anderson, Ritter, et al., 2019; Balfanz, Byrnes, & Fox, 2014; Cobb-Clark et al., 2015; Fabelo et al., 2011; Marchbanks, Blake, Smith, Seibert, & Carmichael, 2014; Swanson, Erickson, & Ritter, 2017), and juvenile justice system involvement (Fabelo et al., 2011; Nicholson-Crotty, Birchmeier, & Valentine, 2009).

Many states and school districts have passed laws or changed policies aimed at reducing suspensions and implementing less punitive strategies. As of May 2015, 22 states and the District of Columbia had passed such laws, and as of the 2015-2016 school year, 23 of the 100 largest school districts had implemented similar reforms (Steinberg & Lacoe, 2017). Between 2016 and 2017, at least 31 states proposed legislation directly related to suspensions and expulsions, with 20 bills passed in 13 of these states (Education Commission of the States, 2018b).

A common reform is to limit suspensions for students in the early grades, often with exceptions (e.g., in Arkansas, Connecticut, Louisiana, Maryland, New Jersey, Oregon, and Tennessee), which may be important, given that stark racial disparities in suspensions begin as early as preschool (U.S. Department of Education, 2016). Other reforms include reducing suspension length as in Chicago and Philadelphia (Lacoe & Steinberg, 2018; Sartain, Allensworth, & Porter, 2015), or limiting suspensions for minor misbehaviors as in California and Philadelphia (Hashim, Strunk, & Dhaliwal, 2018; Public Counsel, 2014; Steinberg & Lacoe, 2018). Miami-Dade County Public Schools attempted to eliminate suspensions altogether (O’Connor, 2015).

Arkansas recently adopted legislation to remove OSS as a legal consequence for truancy (Arkansas § 6-18-507, 2013), becoming one of 17 states plus Washington, D.C., that have prohibited suspensions or expulsions for students solely based on attendance or truancy (Education Commission of the States, 2018a). Truancy is a legal term defined by states, and often, but not always, specifies a number of unexcused absences from school that constitutes truancy (Sutphen, Ford, & Flaherty, 2010). Seven states—including Arkansas—have no statewide definition, while others define truancy as 3 to 21 days unexcused absences (Conry & Richards, 2018). Therefore, comparing truancy rates across different contexts is very difficult.

Using OSS in response to truancy is counterintuitive and difficult to justify given that this consequence further excludes the student from school (Smink & Heilbrunn, 2005; U.S. Department of Education & U.S. Department of Justice, 2014). For example, the U.S. Department of Education and U.S. Department of Justice (2014) wrote that these practices “raise concerns because a school would likely have difficulty demonstrating that excluding a student from attending school in response to the student’s efforts to avoid school was necessary to meet an important educational goal” (p. 12).

Evidence on the Impacts of Student Discipline Policy Reforms

There is limited but growing evidence on the effectiveness of discipline policy reforms. Much of this work is focused in large urban centers such as Philadelphia (Lacoe & Steinberg, 2018; Steinberg & Lacoe, 2018), New York City (Baker-Smith, 2018; Eden, 2017), Chicago (Hinze-Pifer & Sartain, 2018; Sartain et al., 2015), and Los Angeles (Hashim et al., 2018); so little is known about the impact of suspension-reducing policies in Southern states and rural communities. Among the available studies, some work compared outcomes before and after policy changes (Eden, 2017; Loveless, 2017), or focused primarily on suspensions and disparities in suspensions as the key outcomes (Baker-Smith, 2018; Hashim et al., 2018). Others have used difference-in-differences (DD) designs to estimate the impact of suspensions on students’ outcomes (Lacoe & Steinberg, 2018; Sartain et al., 2015; Steinberg & Lacoe, 2018) or exploited policy-induced changes in suspensions to estimate the relationship between suspension reductions and other student outcomes (Hinze-Pifer & Sartain, 2018).

The findings of these studies are quite mixed. Some suggest that suspension bans reduce suspensions and racial gaps (Hashim et al., 2018), but others suggest that overall suspensions are reduced without declines in racial disproportionalities (Loveless, 2017; Steinberg & Lacoe, 2018), or that initial declines in suspensions do not persist (Lacoe & Steinberg, 2018). Identifying and supporting schools that need additional training or supports has been linked to greater reductions in suspensions (Hashim et al., 2018). Reform implementation likely matters, as relatively disadvantaged schools (Anderson, 2018; Steinberg & Lacoe, 2018) and schools that previously suspended at high rates (Anderson, 2018) may be less likely to comply. Next, I discuss some of the relevant studies in more detail.

Loveless (2017) examines California’s efforts to promote restorative practices and ban suspensions for willful defiance below fourth grade. Following the reforms, suspension rates decreased without a decrease in the racial gaps. Middle and high schools serving high proportions of poor or Black students continued to suspend Black students at higher rates. Also, some California educators reported declines in safety and learning (Loveless, 2017).

Beginning in the 2012-2013 school year, Chicago Public Schools began requiring principals to obtain approval for suspensions longer than 5 days and eliminated mandatory 10-day suspensions for serious offenses. Using a DD analysis, Sartain et al. (2015) find that in schools that were heavily using long suspensions prior to the policy, and thus, were most likely to be affected by this policy change, student attendance improved by almost 4 days. In more typical schools, the increase was about 2 days. This improvement in attendance appears not to have translated into student achievement gains, and moreover, teachers and students reported declines in school climate, particularly in schools that previously relied heavily on long suspensions.

Lacoe and Steinberg (2018) estimate the effect of a 2012-2013 reform in the School District of Philadelphia to limit suspensions for nonviolent student misbehavior and give principals more discretion over responses to more serious misconduct. The reform resulted in a temporary decline in suspensions for less serious offenses, but serious misconduct increased, student achievement declined, and truancy rates increased. In other work, Steinberg and Lacoe (2018) estimate the impact of another School District of Philadelphia policy reform prohibiting OSS for classroom disorder infractions (e.g., profane language or gestures and failure to follow classroom rules). Prior to the reform, students could receive 1 to 3 days of OSS, but after the new policy, the maximum punishment allowed was an in-school suspension or other discipline that kept students in school. For students who had previously been suspended, there were improvements in classroom disorder OSS and attendance but not academic achievement. For their nonsuspended peers, there were no changes in achievement or attendance for students in schools that fully complied and declines in achievement and attendance for students in schools that did not fully comply.

Hinze-Pifer and Sartain (2018) assess how declines in reliance on suspensions for severe infractions are associated with student achievement, attendance, and school climate. They use school fixed effects, student fixed effects, and a robust set of controls and find that reductions in OSS for severe infractions were associated with increases in test scores and attendance, and improvements in perceived school climate in schools serving predominately Black students.

Arkansas Context

This study focuses on Arkansas’s removal of OSS as a legal response to truancy and estimates the effect on student- and school-level outcomes. Here, I briefly describe the context surrounding this reform, but for more detail, see Supplemental Appendix A (available online) and Anderson (2018).

In March 2013, the Arkansas legislature passed a law banning OSS as a consequence for truancy (Arkansas Code § 6-18-507, 2013), but there was noncompliance even 3 years later. Using incident-level data provided by the state, Table 1 shows that, in 2012-2013, 14% of reported truancy cases resulted in OSS, and this dropped to 9% by 2015-2016. Based on internet searches, particularly of the Arkansas Department of Education (ADE) website and local news sources, it appears there was little official communication notifying schools of this change, except that an ADE Commissioner’s Memo was distributed in January 2017, after the study period (ADE, 2017).

Table 1.

Consequences for Truancy, All Arkansas Schools.

	Prepolicy					Policy Passed	Postpolicy
	2008-2009	2009-2010	2010-2011	2011-2012	4-Year Total	2012-2013	2013-2014	2014-2015	2015-2016	3-Year Total
Percentage of truancy cases resulting in
ISS	71.4	67.3	68.5	67.1	68.5	74.9	61.5	56.3	51.9	56.3
Other action	8.3	16.7	14.5	17.4	14.4	9.0	26.1	31.7	36.5	31.7
OSS	14.9	12.1	12.8	12.6	13.0	13.8	10.0	9.1	8.7	9.2
Corporal punishment	4.9	2.7	2.8	2.7	3.3	2.1	1.6	1.9	1.8	1.8
No action	0.3	1.0	1.3	0.1	0.7	0.1	0.7	0.9	1.0	0.9
ALE	0.1	0.2	0.1	0.0	0.1	0.1	0.1	0.1	0.1	0.1
Expulsion	0.1	0.1	0.0	0.0	0.0	0.0	0.1	0.0	0.0	0.0
Truancy cases	9,968	11,834	11,734	10,464	44,000	9,407	12,914	14,987	15,598	43,499
Number of schools	385	366	370	371		374	399	396	415

Note. ISS = in-school suspensions; OSS = out-of-school suspensions; ALE = alternative learning environment. Number of schools indicates the schools that reported at least one truancy incident. Prepolicy 4-year average represents the weighted average from 2008-2009 to 2011-2012, that is, the percentage of all truancy cases over those 4 years that resulted in each consequence type. Postpolicy 3-year average represents the weighted average from 2013-2014 to 2015-2016 or, in other words, the percentage of all truancy cases over those 3 years that resulted in each consequence type.

In prior work, I find that controlling for other observable school characteristics, schools with higher baseline truancy, higher baseline OSS rates, and greater proportions of students of color were less likely to comply with the policy suggesting equity concerns with respect to compliance (Anderson, 2018). Despite a lack of full compliance, there was a reduction in the use of OSS in response to truancy, and the impact of this reform remains an important question.

Purpose and Research Questions

The existing evidence on suspension reductions is primarily related to district-level interventions in urban areas, and there is still little known about the impact of state-level mandates at the local level, particularly in the South. Thus, this work fills a gap in the literature regarding whether broad-based student discipline reforms are effective. In this study, I ask

Research Question 1 (RQ 1): How did student-level outcomes such as math and English Language Arts (ELA) test scores, attendance, chronic absenteeism, truancy, and disciplinary infractions change in “policy-affected” schools (i.e., those using OSS as a consequence for truancy in 2012-2013)?

Research Question 2 (RQ 2): How did school-level reports of disciplinary outcomes change in “policy-affected” schools (i.e., those using OSS as a consequence for truancy in 2012-2013)?

Data and Descriptive Statistics

This study uses 9 years (2007-2008 through 2015-2016)¹ of de-identified student achievement, demographic, attendance, and discipline referral data, from all Arkansas K-12 public schools provided by the ADE. Demographic data include race, gender, grade level, special education status, limited English proficiency (LEP), and free and reduced-price lunch (FRL) eligibility. Achievement data include ELA and mathematics test scores in Grades 3 through 8,² standardized within grade, year, test subject, and testing group (with or without accommodations).

Student-level attendance data are reported quarterly. I limit the impact of outliers³ using Winsorization (Dixon, 1960; Locker, 2001), replacing the top 1% of the total days per quarter with the value at the 99th percentile.⁴ In the cases in which the total number of days was adjusted, I adjust the days absent such that the student-by-quarter percentage of days absent remains constant pre- and post-Winsorization. Then, these quarterly values are used to calculate a percentage of days absent for each student-year. The data do not distinguish between partial and full days of absences, and reporting practices likely differ by school. Thus, the use of school fixed effects in my modeling approach, described later, is key to account for unobserved school heterogeneity.

Discipline data are at the incident level and specify an infraction type (out of 17 types) and the resulting consequence (7 types). During the study period, the most common consequences were in-school suspension (ISS; 38.3%), “other” consequences, which do not fit into a state reporting category and include a variety of consequences⁵ (24.9%), OSS (22.2%), and corporal punishment (13.3%). No action (0.85%), referrals to an alternative learning environment (0.31%), and expulsions (0.10%) are particularly rare. The policy of interest focuses on truancy (6.5% of all infractions), and the use of OSS for truancy, which occurred in 11.4% of truancy cases.

The trends in truancy and disciplinary responses are in Table 1. In 2012-2013, the year in which Act 1329 was passed, 13.8% of truancy cases resulted in OSS. This figure declined to 8.7% by 2015-2016. Across the same period, there was a rise in “other” consequences. Given uncertainty about the “other” category, it is unclear whether this change will have a meaningful impact on students. For example, some “other” consequences could be referrals to a truancy prevention program or supportive services, whereas others may still resemble exclusionary discipline, but very limited qualitative evidence indicates these are primarily nonexclusionary consequences.⁶ During this time period, there was also a shift away from using ISS for truancy (as a share of total), although the raw number of truancy incidents resulting in ISS increased.

The trends in Table 1 represent all schools in the state, but similar patterns exist for the schools that used OSS as a response to truancy in 2012-2013 (see Supplemental Appendix Table B). In these schools, 18.3% of 2012-2013 truancy cases resulted in OSS, and this decreased to 10.7% by 2015-2016. At the same time, there was an increase in “other” consequences and a decline in ISS.

Analytic Methods

RQ 1: How Did Student-Level Outcomes Change in “Policy-Affected” Schools?

In Arkansas, approximately 99% of truancy cases are reported in Grades 6 to 12, so the analytic samples only include these grade levels. Models estimating policy-related changes in test scores focus on Grades 6 to 8, because after eighth grade, students are not tested in both subjects each year. I limit the sample to students in schools that reported nonzero levels of truancy in the baseline year (2012-2013) to further isolate a set of policy-relevant schools.

I use a comparative interrupted time series (CITS) analysis. This approach compares changes between “treatment” students in schools affected by the policy and “comparison” students in schools that were not. The results are estimated using a variety of definitions of treatment exposure, each based on the theory that schools that previously used OSS as a consequence for truancy would be more affected by the policy. Students in schools that were not using OSS in response to truancy would theoretically not be affected and serve as comparison students. A key benefit of this approach is that it isolates the impact of the ban on OSS for truancy separately from other policies and programs that were enacted at the same time.

CITS, an interrupted time series with a nonequivalent comparison group, has been used to estimate the impacts of school accountability policies (Dee & Jacob, 2011; Wong, Cook, & Steiner, 2011), school turnaround reforms (Strunk, Marsh, Hashim, & Bush-Mecenas, 2016; Strunk, Marsh, Hashim, Bush-Mecenas, & Weinstein, 2016), literacy interventions (Somers, Zhu, Jacob, & Bloom, 2013), and job programs (Bloom & Riccio, 2005). According to Somers et al. (2013), CITS accounts for treatment comparison differences in baseline mean and baseline trends, whereas DD assumes that the baseline trends in the treatment groups and comparison groups are parallel. CITS relies on the assumption that deviations from prior trends for comparison units serve as a valid counterfactual for what would have happened to the trends for treatment units in the absence of the policy. This may be a strong assumption, because schools that administered OSS for truancy in 2012-2013 may be very different from other schools and perhaps in unobservable ways. While it is possible to use propensity score matching methods, this still cannot ensure that I have accounted for unobservable characteristics, so I simply control for a robust set of observable characteristics, school fixed effects, and student fixed effects.

The following regression equation illustrates the CITS design:

\begin{array}{l} Y_{i t} = β_{0} + β_{1} Y E A R_{t} + β_{2} P O L I C Y_{t} + β_{3} Y R_S I N C E_P O L I C Y_{t} + β_{4} (T_{i} \times Y E A R_{t}) + \\ β_{5} (T_{i} \times P O L I C Y_{t}) + β_{6} (T_{i} \times Y R_S I N C E_P O L I C Y_{t}) + X_{i t} β + δ_{s} + θ_{i} + ε_{i t} \end{array}

(1)

The dependent variable, $Y_{i t}$ , is a student-by-year outcome such as math or ELA test scores, student absenteeism (percentage of school days absent),⁷ an indicator for chronic absenteeism (equal to 1 if the student missed at least 10% of school days in academic year, t, and 0 otherwise), truancy incidents (count and an indicator for having at least one citation in year t), and total disciplinary incidents (count and an indicator for at least one in year t).⁸

$Y E A R_{t}$ is a time-trend variable starting with 1 in the first year. $P O L I C Y_{t}$ is an indicator equal to 1 for observations after the policy and zero prepolicy. $Y R_S I N C E_P O L I C Y_{t}$ is a time-trend variable defined such that it equals 0 in all periods prior to and including the year of the policy change (through 2012-2013), one in 2013-2014, two in 2014-2015, and three in 2015-2016.

$X_{i t}$ is a vector of time-varying student-level characteristics, including FRL eligibility, special education status, and English Language Learner status.⁹ I control for time-invariant unobservable characteristics of students using student fixed effects, $θ_{i}$ . I include school fixed effects, $δ_{s}$ , to capture time-invariant unobservable characteristics of schools, which could include school climate, disciplinary and attendance policies and reporting practices, and other attributes. The idiosyncratic error term is indicated by $ε_{i t}$ . Standard errors are clustered at the district level.

I test the sensitivity of the results to four definitions of treatment exposure, $T_{i}$ , two binary and two continuous. In some cases, $T_{i}$ is a time-invariant binary indicator for whether student i attended a treatment school (e.g., a school that used OSS for truancy at least once in the baseline year, 2012-2013) during the year the policy was passed (2012-2013), or the year closest to the policy for which student i is observed. Another version of $T_{i}$ is a binary indicator of whether the student ever attended a treatment school, following Strunk, Marsh, Hashim, and Bush-Mecenas (2016).

In other specifications, I use continuous measures of treatment exposure, following the of No Child Left Behind studies, leveraging prior state accountability laws as measures of treatment exposure (Dee & Jacob, 2011; Grissom, Nicholson-Crotty, & Harrington, 2014). The magnitude of the policy-related change should be influenced by the degree to which a school was “subject” to the policy. Schools with few cases of truancy resulting in OSS may experience little change relative to schools that use OSS frequently as a consequence for truancy. Therefore, I estimate models where treatment is defined as the school’s percentage of truancy cases in 2012-2013 resulting in OSS, using either this rate for the school that student i attended closest to the policy year or the highest rate of any school the student ever attended. This latter variable, in other words, is created by assigning—across all the schools that student i attended during the study period—the highest value of school share of truancy that resulted in OSS during 2012-2013. To simplify the text in the tables, I refer to this treatment measure as “maximum treatment exposure.”

Using interactions with the other variables, $T_{i}$ allows the policy-related change to be reflected in a level shift (i.e., $β_{5}$ ) and a shift in trend (i.e., $β_{6}$ ). In the models using binary indicators of $T_{i}$ , the total estimated change after 3 years is $({\hat{β}}_{5} + 3 \times {\hat{β}}_{6})$ . The term $β_{4}$ indicates whether there was a difference between the treatment and comparison groups’ baseline trends. In the models using continuous measures of $T_{i}$ , the sum $({\hat{β}}_{5} + 3 \times {\hat{β}}_{6})$ is the change in a school that used OSS for 100% of truancy cases in the baseline year, 2012-2013, relative to the change in a school that never used OSS for truancy in 2012-2013. Given noncompliance, these measures are considered intent-to-treat estimates, as opposed to treatment-on-the-treated.

RQ 2: How Did School-Level Disciplinary Outcomes Change in “Policy-Affected” Schools?

Next, I estimate policy-related changes in three school-level disciplinary outcomes. I estimate whether the policy may have induced schools to use “other” consequences for truancy. In addition, I test for strategic miscoding of truancy as something else, perhaps as an “other” infraction. Therefore, I test for policy-related changes in the share of truancy cases resulting in “other,” as well as truancy reports per 100 students and “other” infractions per 100 students.

I rely on a CITS analysis similar to the student-level analyses. Here, all data are collapsed to a school-by-year level. I define treatment in two ways: (1) a binary indicator for whether the school reported using OSS for truancy at least once in 2012-2013 and (2) the share of 2012-2013 truancy cases that resulted in OSS. I exclude schools that reported no truancy in 2012-2013.

The following regression illustrates the CITS design following Dee and Jacob (2011):

\begin{array}{l} Y_{s t} = β_{0} + β_{1} Y E A R_{t} + β_{2} P O L I C Y_{t} + β_{3} Y R_S I N C E_P O L I C Y_{t} + β_{4} (T_{s} \times Y E A R_{t}) + \\ β_{5} (T_{s} \times P O L I C Y_{t}) + β_{6} (T_{s} \times Y R_S I N C E_P O L I C Y_{t}) + X_{s t} β + δ_{s} + ε_{s t} \end{array}

(2)

The variables $Y E A R_{t}$ , $P O L I C Y_{t}$ , and $Y R_S I N C E_P O L I C Y_{t}$ are the same as in Equation (1). $X_{s t}$ is a vector of school-level characteristics in year t, including the log of student enrollment, school type (indicators for middle school and high school, with elementary as the reference group), and student demographic characteristics, including percent FRL-eligible, percent Black, percent Hispanic, percent other non-White race (Asian, Native Hawaiian/Pacific Islander, American Indian/Alaska Native, and two or more races), and percent receiving special education services.¹⁰ I also include seven controls for the frequency of each consequence type (count per 100 students) to account for school disciplinary practices. To control for time-invariant unobservable characteristics of schools, I include school fixed effects, $δ_{s}$ . The idiosyncratic error term is indicated by $ε_{s t}$ . Standard errors are clustered at the school level.

Results

RQ 1: How Did Student-Level Outcomes Change in “Policy-Affected” Schools?

Table 2 shows the overall results from Equation (1). Each panel uses a different measure of treatment exposure. Panel A uses a binary measure, assigning students to treatment schools (those that ever used OSS for truancy in 2012-2013) or comparison schools (those that did not) based on the school the student attended in the year closest to the policy year. Panel B uses a binary measure assigning students to treatment if the student ever attended a treatment school. In Panels A and B, the total “effect” after 3 years is the sum of Post × Treat + 3(YSP × Treat). Panel C uses a continuous measure of treatment based on the share of 2012-2013 truancy that resulted in OSS for the school the student attended closest to the policy year. In Panel D, treatment is a continuous measure based on the “maximum treatment exposure.”¹¹ The total “effect” in Panels C and D represents the total change in a school that used OSS in 100% of 2012-2013 truancy cases, relative to a school that used OSS in 0% of 2012-2013 truancy cases.

Table 2.

Estimated Policy-Related Change in Student Outcomes.

Outcome Variable	Math Z Score	ELA Z Score	Percentage of Days Absent	Chronically Absent	Truancy (≥1)	Truancy (Count)	Discipline Referral (≥1)	Discipline Referrals (Count)
Panel A: Using binary treatment measure based on school student was in during year closest to policy year
Trend	0.014	0.018**	0.006***	0.024***	0.002**	0.002	−0.015***	−0.069***
	(0.016)	(0.009)	(0.001)	(0.003)	(0.001)	(0.002)	(0.003)	(0.018)
Post	−0.028	a	a	a	0.002	0.004	0.015	0.063
	(0.020)	(0.016)	(0.002)	(0.006)	(0.003)	(0.005)	(0.013)	(0.047)
YSP	0.041*	−0.014	0.003***	0.016***	0.005**	0.009**	0.029***	0.100***
	(0.021)	(0.016)	(0.001)	(0.005)	(0.003)	(0.004)	(0.007)	(0.030)
Trend × Treat	0.009	0.004	0.002*	0.009*	a	−0.002	−0.003	−0.031
	(0.017)	(0.010)	(0.001)	(0.005)	(0.002)	(0.003)	(0.004)	(0.030)
Post × Treat	0.025	0.019	−0.001	−0.012	0.004	0.002	−0.005	0.048
	(0.029)	(0.020)	(0.002)	(0.012)	(0.005)	(0.010)	(0.015)	(0.097)
YSP × Treat	0.005	0.015	−0.001	−0.005	0.001	0.004	0.002	0.027
	(0.029)	(0.027)	(0.002)	(0.010)	(0.003)	(0.006)	(0.009)	(0.043)
Observations	396,524	401,410	1,466,383	1,466,383	1,487,734	1,487,734	1,487,734	1,487,734
Adjusted R²	0.813	0.801	0.557	0.420	0.148	0.173	0.350	0.455
Total 3-year “effect”	0.040	0.063	−0.004	−0.027	0.006	0.016	0.000	0.128
Total 3-year “effect”	(0.080)	(0.075)	(0.006)	(0.033)	(0.011)	(0.020)	(0.025)	(0.174)
Panel B: Using binary treatment measure based on whether student was ever in a treatment school
Trend	0.005	0.010	0.005***	0.023***	0.002***	0.002	−0.014***	−0.068**
	(0.021)	(0.012)	(0.001)	(0.003)	(0.001)	(0.002)	(0.003)	(0.028)
Post	−0.054**	−0.005	−0.002	−0.005	0.002	0.005	0.031*	0.134**
	(0.027)	(0.020)	(0.002)	(0.008)	(0.004)	(0.006)	(0.017)	(0.064)
YSP	0.028	−0.008	0.004***	0.020***	0.004	0.008	0.021***	0.078**
	(0.025)	(0.020)	(0.001)	(0.005)	(0.003)	(0.006)	(0.008)	(0.036)
Trend × Treat	0.020	0.015	0.002**	0.010*	−0.001	−0.001	−0.005	−0.029
	(0.022)	(0.013)	(0.001)	(0.005)	(0.001)	(0.003)	(0.004)	(0.035)
Post × Treat	0.041	0.016	0.001	−0.003	0.003	0.001	−0.025	−0.057
	(0.033)	(0.023)	(0.003)	(0.012)	(0.005)	(0.009)	(0.019)	(0.100)
YSP × Treat	0.029	0.005	−0.002	−0.010	0.002	0.005	0.012	0.055
	(0.033)	(0.026)	(0.002)	(0.009)	(0.004)	(0.007)	(0.010)	(0.046)
Observations	396,524	401,410	1,466,383	1,466,383	1,487,734	1,487,734	1,487,734	1,487,734
Adjusted R²	0.813	0.801	0.557	0.420	0.148	0.173	0.350	0.455
Total 3-year “effect”	0.127	0.030	−0.005	−0.034	0.008	0.015	0.012	0.108
Total 3-year “effect”	(0.085)	(0.072)	(0.006)	(0.028)	(0.011)	(0.023)	(0.024)	(0.180)
Panel C: Using continuous treatment measure based on school student was in during year closest to policy year
Trend	0.022*	0.024***	0.006***	0.028***	0.002*	0.001	−0.017***	−0.087***
	(0.012)	(0.008)	(0.001)	(0.004)	(0.001)	(0.002)	(0.003)	(0.020)
Post	−0.031	0.0020	−0.001	−0.009	0.006*	0.009	0.020*	0.114*
	(0.020)	(0.013)	(0.002)	(0.009)	(0.003)	(0.006)	(0.011)	(0.058)
YSP	0.040**	−0.017	0.004***	0.017***	0.005*	0.010**	0.030***	0.108***
	(0.019)	(0.013)	(0.001)	(0.006)	(0.003)	(0.005)	(0.006)	(0.025)
Trend × Treat	−0.008	−0.012	0.003***	0.009	a	a	−0.001	−0.008
	(0.016)	(0.011)	(0.001)	(0.006)	(0.002)	(0.003)	(0.008)	(0.059)
Post × Treat	0.069*	0.034	0.003	0.010	−0.010**	−0.018**	−0.036**	−0.109
	(0.037)	(0.027)	(0.003)	(0.014)	(0.004)	(0.008)	(0.015)	(0.100)
YSP × Treat	0.012	0.038	−0.007***	−0.026***	0.004	0.008	0.000	0.053
	(0.046)	(0.042)	(0.002)	(0.009)	(0.007)	(0.012)	(0.019)	(0.109)
Observations	396,524	401,410	1,466,383	1,466,383	1,487,734	1,487,734	1,487,734	1,487,734
Adjusted R²	0.813	0.801	0.557	0.420	0.148	0.173	0.350	0.455
Total 3-year “effect”	0.106	0.149	−0.018***	−0.067**	0.002	0.005	−0.034	0.049
	(0.118)	(0.123)	(0.007)	(0.033)	(0.017)	(0.031)	(0.060)	(0.367)
Panel D: Using continuous treatment measure based on maximum treatment exposure
Trend	0.013	0.019**	0.006***	0.027***	0.002**	0.002	−0.016***	−0.071***
	(0.014)	(0.009)	(0.001)	(0.004)	(0.001)	(0.002)	(0.003)	(0.019)
Post	−0.031	0.0008	−0.002	−0.010	0.004	0.004	0.020*	0.069
	(0.022)	(0.015)	(0.002)	(0.009)	(0.003)	(0.005)	(0.012)	(0.047)
YSP	0.044**	−0.013	0.004***	0.018***	0.005	0.009*	0.029***	0.095***
	(0.020)	(0.014)	(0.001)	(0.006)	(0.003)	(0.005)	(0.006)	(0.025)
Trend × Treat	0.018	0.007	0.003***	0.009*	−0.002	−0.001	−0.004	−0.063
	(0.023)	(0.019)	(0.001)	(0.005)	(0.002)	(0.004)	(0.006)	(0.072)
Post × Treat	0.048	0.025	0.002	0.011	0.001	0.003	−0.024	0.078
	(0.035)	(0.025)	(0.003)	(0.012)	(0.010)	(0.019)	(0.017)	(0.233)
YSP × Treat	−0.002	0.019	−0.005**	−0.021**	0.004	0.009	0.004	0.081
	(0.047)	(0.045)	(0.002)	(0.009)	(0.006)	(0.012)	(0.015)	(0.086)
Observations	396,524	401,410	1,466,383	1,466,383	1,487,734	1,487,734	1,487,734	1,487,734
Adjusted R²	0.042	0.081	−0.013	−0.051	0.013	0.031	−0.012	0.322
Total 3-year “effect”	0.042	0.081	−0.013**	−0.051*	0.013	0.031	−0.012	0.322
Total 3-year “effect”	(0.127)	(0.131)	(0.006)	(0.030)	(0.022)	(0.041)	(0.049)	(0.430)

Note. ELA = English Language Arts; Treat = treatment; YSP = year since policy. All models include student fixed effects, school fixed effects, and indicators for free and reduced-price lunch, special education, and limited English proficiency. Standard errors clustered at the district level. Panel A assigns students to treatment or comparison schools based on the type of school that a student attended in the year closest to the policy year. Panel B assigns students to a treatment school if the student ever attended a treatment school. Because Panels A and B use binary measures of treatment, the total “effect” after 3 years is the sum of Post × Treat + 3(YSP × Treat) and can be interpreted as the total “effect” of being in a treatment school after 3 years. Panel C uses a continuous measure of treatment based on the share of 2012-2013 truancy that resulted in OSS for the school the student attended in the year closest to the policy. Panel D uses a continuous measure equal to the highest share of 2012-2013 truancy that resulted in OSS among all the schools that the student attended during the panel. The total “effect” in Panels C and D can be interpreted as the total change in a school that used OSS in 100% of 2012-2013 truancy cases, relative to a school that used OSS in 0% of 2012-2013 truancy cases. Test score models include Grades 6 to 8, and all others include Grades 6 to 12. An “a” indicates an absolute value <0.001.

p < .1. **p < .05. ***p < .01.

In Panels A and B, there were no policy-related changes, but in Panels C and D, there is evidence of a decline in absenteeism. For each 10 percentage point increase in prior reliance on OSS for truancy (the continuous treatment variables), the percentage of days absent per year declined by about 0.13 to 0.18 percentage points, or about one quarter to one third of a day based on a 180-day calendar. Recall that the absences include suspensions. This means that at least part of this improvement in attendance is due to the decline in OSS days, not necessarily a substantive shift in other types of absences. Indeed, back of the envelope calculations based on the number of truancy incidents, the typical number of days suspended for truancy (about 1.7, when reported), and the number of students, it is possible that all the attendance gains are due to the policy-induced decline in OSS days. Regardless, the improvement does indicate that students were in school more days, on average, as a result of the policy. In addition, the likelihood of being chronically absent declined slightly for treatment students. There were no estimated changes in test scores, truancy infractions, or disciplinary infractions.

The findings in Table 2 may mask important heterogeneity, so I estimate separate models for students that may be more or less affected by the policy. In Arkansas, Black students are about 4.3 times as likely as White students to receive OSS, and FRL-eligible students are about 2.5 times as likely as non–FRL-eligible students to receive OSS (Anderson & Ritter, 2017). Therefore, I estimate separate models for Black, non-Black, FRL-eligible, and non–FRL-eligible students.¹² In addition, I estimate models for students who were never truant and students who were truant at least once during the study period, as the direct effects of the policy may differ for these groups, and these are particularly relevant student groups for the design of discipline policy reforms.

Tables 3 to 6 show the subgroup results, which are all either null or beneficial changes. The improvements were primarily in absenteeism (Table 4), with no estimated changes in truancy (Table 5), and limited changes in test scores (Table 3) and discipline referrals (Table 6). Relatively disadvantaged groups (e.g., Black, FRL-eligible, and ever-truant students) were more likely to experience improvements; however, other groups (those never truant), also experienced declines in absenteeism (Table 4). Only Black students experienced policy-related declines in disciplinary referrals (Table 6). The most consistently estimated benefits were improvements in absenteeism, and the other results should be interpreted as more suggestive.

Table 3.

Estimated Policy-Related Change in Student Test Scores, by Student Subgroup (Grades 6-8).

Group	Dependent Variable = Math Test Scores						Dependent Variable = ELA Test Scores
Group	Black	Non-Black	FRL-eligible	Non–FRL-eligible	Ever Truant	Never Truant	Black	Non-Black	FRL-eligible	Non–FRL-eligible	Ever Truant	Never Truant
Panel A: Using binary treatment measure based on school student was in during year closest to policy year
Total 3-year “effect”	0.044	−0.002	0.080	−0.009	−0.008	0.049	0.157*	0.035	0.082	0.041	0.103	0.064
Total 3-year “effect”	(0.102)	(0.082)	(0.086)	(0.086)	(0.087)	(0.082)	(0.086)	(0.077)	(0.087)	(0.072)	(0.098)	(0.076)
Observations	90,925	305,588	243,448	153,071	50,466	346,052	91,705	309,694	245,259	156,146	50,678	350,728
Adjusted R²	0.745	0.808	0.773	0.813	0.761	0.813	0.869	0.878	0.873	0.865	0.867	0.883
Panel B: Using binary treatment measure based on whether student was ever in a treatment school
Total 3-year “effect”	0.120	0.092	0.140*	0.122	0.162	0.124	0.104	0.011	0.041	0.022	0.136	0.026
Total 3-year “effect”	(0.100)	(0.092)	(0.083)	(0.107)	(0.104)	(0.089)	(0.086)	(0.075)	(0.082)	(0.078)	(0.099)	(0.074)
Observations	90,925	305,588	243,448	153,071	50,466	346,052	91,705	309,694	245,259	156,146	50,678	350,728
Adjusted R2	0.745	0.809	0.773	0.813	0.761	0.814	0.869	0.878	0.873	0.865	0.867	0.883
Panel C: Using continuous treatment measure based on school student was in during year closest to policy year
Total 3-year “effect”	0.138*	-0.022	0.160	0.015	0.239**	0.095	0.235***	0.105	0.199	0.095	0.359**	0.129
Total 3-year “effect”	(0.082)	(0.110)	(0.127)	(0.114)	(0.093)	(0.124)	(0.077)	(0.144)	(0.130)	(0.125)	(0.148)	(0.124)
Observations	90,925	305,588	243,448	153,071	50,466	346,052	91,705	309,694	245,259	156,146	50,678	350,728
Adjusted R²	0.745	0.808	0.773	0.813	0.761	0.813	0.869	0.878	0.873	0.865	0.867	0.883
Panel D: Using continuous treatment measure based on the maximum treatment exposure
Total 3-year “effect”	0.098	−0.072	0.081	−0.025	0.136	0.030	0.178*	0.036	0.109	0.070	0.207	0.064
Total 3-year “effect”	(0.100)	(0.105)	(0.140)	(0.123)	(0.103)	(0.134)	(0.097)	(0.151)	(0.146)	(0.122)	(0.139)	(0.134)
Observations	90,925	305,588	243,448	153,071	50,466	346,052	91,705	309,694	245,259	156,146	50,678	350,728
Adjusted. R²	0.745	0.808	0.773	0.813	0.761	0.813	0.869	0.878	0.873	0.865	0.867	0.883

Note. ELA = English Language Arts; FRL = free and reduced-price lunch. All models include student fixed effects, school fixed effects, and indicators for special education, and limited English proficiency. Students are treated as Black or FRL-eligible if the data indicated they were Black or FRL-eligible in at least half of the years they were observed. All models except for the FRL versus non-FRL models also control for FRL-eligible status. Standard errors clustered at the district level. Panel A assigns students to treatment or comparison schools based on the type of school the student attended in the year closest to the policy year. Panel B assigns students to a treatment school if the student ever attended a treatment school. Panel C uses a continuous measure of treatment based on the share of 2012-2013 truancy that resulted in OSS for the school the student attended in the year closest to the policy. Panel D uses a continuous measure equal to the highest share of 2012-2013 truancy that resulted in OSS among all the schools that the student attended during the panel. Because Panels C and D use continuous treatment measures, the total “effect” can be interpreted as the total change in a school that used OSS for 100% of truancy in 2012-2013, relative to a school that used OSS for 0% of 2012-2013 truancy.

p < .1. **p < .05. ***p < .01.

Table 4.

Estimated Policy-Related Change in Student Absenteeism, by Student Subgroup (Grades 6-12).

Group	Dependent Variable = Percentage of Days Absent						Dependent Variable = Chronically Absent (Missed ≥ 10% of Days)
Group	Black	Non-Black	FRL-eligible	Non–FRL-eligible	Ever Truant	Never Truant	Black	Non-Black	FRL-eligible	Non–FRL-eligible	Ever Truant	Never Truant
Panel A: Using binary treatment measure based on school student was in during year closest to policy year
Total 3-year “effect”	−0.015	−0.002	−0.004	−0.004	0.001	−0.006	−0.054	−0.025	−0.022	−0.038	−0.015	−0.036
Total 3-year “effect”	(0.011)	(0.006)	(0.007)	(0.007)	(0.011)	(0.006)	(0.046)	(0.039)	(0.033)	(0.044)	(0.052)	(0.032)
Observations	318,258	1,148,117	839,317	627,066	198,576	1,267,806	318,258	1,148,117	839,317	627,066	198,576	1,267,806
Adjusted R²	0.591	0.542	0.546	0.543	0.508	0.567	0.457	0.406	0.418	0.378	0.392	0.423
Panel B: Using binary treatment measure based on whether student was ever in a treatment school
Total 3-year “effect”	−0.013	−0.004	−0.005	−0.006	−0.002	−0.007	−0.047	−0.034	−0.032	−0.041	−0.030	−0.041
Total 3-year “effect”	(0.011)	(0.006)	(0.007)	(0.006)	(0.010)	(0.006)	(0.046)	(0.032)	(0.031)	(0.033)	(0.050)	(0.027)
Observations	318,258	1,148,117	839,317	627,066	198,576	1,267,806	318,258	1,148,117	839,317	627,066	198,576	1,267,806
Adjusted R²	0.591	0.542	0.546	0.543	0.508	0.567	0.457	0.406	0.418	0.378	0.392	0.423
Panel C: Using continuous treatment measure based on school student was in during year closest to policy year
Total 3-year “effect”	−0.035***	−0.009	−0.025***	−0.006	−0.039***	−0.016**	−0.136***	−0.037	−0.112***	0.001	−0.198***	−0.055*
Total 3-year “effect”	(0.008)	(0.006)	(0.007)	(0.007)	(0.013)	(0.007)	(0.033)	(0.033)	(0.033)	(0.036)	(0.059)	(0.033)
Observations	318,258	1,148,117	839,317	627,066	198,576	1,267,806	318,258	1,148,117	839,317	627,066	198,576	1,267,806
Adjusted R²	0.592	0.542	0.546	0.543	0.509	0.567	0.458	0.406	0.418	0.378	0.392	0.423
Panel D: Using continuous treatment measure based on the maximum treatment exposure
Total 3-year “effect”	−0.031***	−0.006	−0.019**	−0.004	−0.023**	−0.012*	−0.121***	−0.031	−0.091***	0.000	−0.138***	−0.045
Total 3-year “effect”	(0.010)	(0.005)	(0.008)	(0.005)	(0.009)	(0.006)	(0.046)	(0.026)	(0.034)	(0.027)	(0.046)	(0.030)
Observations	318,258	1,148,117	839,317	627,066	198,576	1,267,806	318,258	1,148,117	839,317	627,066	198,576	1,267,806
Adjusted R²	0.592	0.542	0.546	0.543	0.509	0.567	0.458	0.406	0.418	0.378	0.392	0.423

Note. ELA = English Language Arts; FRL = free and reduced-price lunch. All models include student fixed effects, school fixed effects, and indicators for special education, and limited English proficiency. Students are treated as Black or FRL-eligible if the data indicated they were Black or FRL-eligible in at least half of the years they were observed. All models except for the FRL versus non-FRL models also control for FRL status. Standard errors clustered at the district level. Panel A assigns students to treatment or comparison schools based on the type of school the student attended in the year closest to the policy year. Panel B assigns students to a treatment school if the student ever attended a treatment school. Panel C uses a continuous measure of treatment based on the share of 2012-2013 truancy that resulted in OSS for the school the student attended in the year closest to the policy. Panel D uses a continuous measure equal to the highest share of 2012-2013 truancy that resulted in OSS among all the schools that the student attended during the panel. Because Panels C and D use continuous treatment measures, the total “effect” can be interpreted as the total change in a school that used OSS for 100% of truancy in 2012-2013, relative to a school that used OSS for 0% of 2012-2013 truancy.

p < .1. **p < .05. ***p < .01.

Table 5.

Estimated Policy-Related Change in Student Truancy, by Student Subgroup (Grades 6-12).

Group	Dependent Variable = Truant (At Least Once)				Dependent Variable = Truancy (Count)
Group	Black	Non-Black	FRL-eligible	Non–FRL-eligible	Black	Non-Black	FRL-eligible	Non–FRL-eligible
Panel A: Using binary treatment measure based on school student was in during year closest to policy year
Total 3-year “effect”	−0.009	0.002	0.006	0.006	−0.003	0.004	0.021	0.006
Total 3-year “effect”	(0.032)	(0.009)	(0.016)	(0.006)	(0.057)	(0.016)	(0.029)	(0.009)
Observations	324,577	1,163,149	851,581	636,153	324,577	1,163,149	851,581	636,153
Adjusted R²	0.169	0.135	0.147	0.133	0.188	0.164	0.174	0.147
Panel B: Using binary treatment measure based on whether student was ever in a treatment school
Total 3-year “effect”	0.006	0.003	0.010	0.004	0.020	0.002	0.021	0.002
Total 3-year “effect”	(0.032)	(0.009)	(0.016)	(0.006)	(0.061)	(0.019)	(0.035)	(0.009)
Observations	324,577	1,163,149	851,581	636,153	324,577	1,163,149	851,581	636,153
Adjusted R²	0.169	0.135	0.147	0.133	0.188	0.164	0.174	0.147
Panel C: Using continuous treatment measure based on school student was in during year closest to policy year
Total 3-year “effect”	−0.031	−0.003	−0.006	0.006	−0.056	−0.008	−0.006	0.007
Total 3-year “effect”	(0.026)	(0.010)	(0.022)	(0.009)	(0.055)	(0.016)	(0.041)	(0.011)
Observations	324,577	1,163,149	851,581	636,153	324,577	1,163,149	851,581	636,153
Adjusted R²	0.169	0.135	0.147	0.133	0.188	0.164	0.174	0.147
Panel D: Using continuous treatment measure based on the maximum treatment exposure
Total 3-year “effect”	0.007	−0.002	0.009	0.011	0.024	−0.003	0.027	0.016
Total 3-year “effect”	(0.050)	(0.010)	(0.029)	(0.011)	(0.094)	(0.017)	(0.053)	(0.016)
Observations	324,577	1,163,149	851,581	636,153	324,577	1,163,149	851,581	636,153
Adjusted R²	0.169	0.135	0.147	0.133	0.188	0.164	0.174	0.147

Note. ELA = English Language Arts; FRL = free and reduced-price lunch. All models include student fixed effects, school fixed effects, and indicators for special education, and limited English proficiency. Students are treated as Black or FRL-eligible if the data indicated they were Black or FRL-eligible in at least half of the years they were observed. All models except for the FRL versus non-FRL models also control for FRL status. Standard errors clustered at the district level. Panel A assigns students to treatment or comparison schools based on the type of school the student attended in the year closest to the policy year. Panel B assigns students to a treatment school if the student ever attended a treatment school. Panel C uses a continuous measure of treatment based on the share of 2012-2013 truancy that resulted in OSS for the school the student attended in the year closest to the policy. Panel D uses a continuous measure equal to the highest share of 2012-2013 truancy that resulted in OSS among all the schools that the student attended during the panel. Because Panels C and D use continuous treatment measures, the total “effect” can be interpreted as the total change in a school that used OSS for 100% of truancy in 2012-2013, relative to a school that used OSS for 0% of 2012-2013 truancy. An “a” indicates an absolute value <0.001. None of the estimates were significant at the 90% confidence level.

Table 6.

Estimated Policy-Related Change in Student Discipline Referrals, by Student Subgroup (Grades 6-12).

Group	Dependent Variable = Disciplined (At Least Once)						Dependent Variable = Discipline Referrals (Count)
Group	Black	Non-Black	FRL-eligible	Non–FRL-eligible	Ever Truant	Never Truant	Black	Non-Black	FRL-eligible	Non–FRL-eligible	Ever Truant	Never Truant
Panel A: Using binary treatment measure based on school student was in during year closest to policy year
Total 3-year “effect”	−0.073	−0.001	−0.002	0.003	−0.030	−0.003	−0.191	0.005	0.161	0.064	0.087	0.027
Total 3-year “effect”	(0.066)	(0.021)	(0.034)	(0.018)	(0.047)	(0.022)	(0.610)	(0.083)	(0.258)	(0.066)	(0.364)	(0.086)
Observations	324,577	1,163,149	851,581	636,153	201,996	1,285,737	324,577	1,163,149	851,581	636,153	201,996	1,285,737
Adjusted R²	0.352	0.308	0.338	0.309	0.130	0.322	0.452	0.429	0.450	0.406	0.432	0.428
Panel B: Using binary treatment measure based on whether student was ever in a treatment school
Total 3-year “effect”	−0.046	0.008	0.012	0.008	−0.008	0.009	−0.039	−0.020	0.121	0.053	−0.278	0.076
Total 3-year “effect”	(0.065)	(0.021)	(0.033)	(0.019)	(0.055)	(0.021)	(0.594)	(0.125)	(0.296)	(0.062)	(0.710)	(0.076)
Observations	324,577	1,163,149	851,581	636,153	201,996	1,285,737	324,577	1,163,149	851,581	636,153	201,996	1,285,737
Adjusted R²	0.352	0.308	0.338	0.309	0.130	0.322	0.452	0.429	0.450	0.406	0.432	0.428
Panel C: Using continuous treatment measure based on school student was in during year closest to policy year
Total 3-year “effect”	−0.169**	−0.011	−0.057	−0.015	0.021	−0.038	−0.924*	0.005	−0.069	0.050	0.903	−0.062
Total 3-year “effect”	(0.067)	(0.044)	(0.071)	(0.036)	(0.131)	(0.050)	(0.530)	(0.148)	(0.457)	(0.145)	(0.965)	(0.187)
Observations	324,577	1,163,149	851,581	636,153	201,996	1,285,737	324,577	1,163,149	851,581	636,153	201,996	1,285,737
Adjusted R²	0.353	0.308	0.338	0.309	0.130	0.322	0.453	0.429	0.450	0.406	0.432	0.429
Panel D: Using continuous treatment measure based on the maximum treatment exposure
Total 3-year “effect”	−0.120	−0.007	−0.031	−0.001	−0.009	−0.017	0.001	0.014	0.300	0.141	0.959	0.086
Total 3-year “effect”	(0.083)	(0.030)	(0.058)	(0.031)	(0.071)	(0.043)	(1.023)	(0.102)	(0.543)	(0.161)	(0.721)	(0.200)
Observations	324,577	1,163,149	851,581	636,153	201,996	1,285,737	324,577	1,163,149	851,581	636,153	201,996	1,285,737
Adjusted R²	0.352	0.308	0.338	0.309	0.130	0.322	0.452	0.429	0.450	0.406	0.432	0.429

Note. ELA = English Language Arts; FRL = free and reduced-price lunch. All models include student fixed effects, school fixed effects, and indicators for special education, and limited English proficiency. Students are treated as Black or FRL-eligible if the data indicated they were Black or FRL-eligible in at least half of the years they were observed. All models except for the FRL versus non-FRL models also control for FRL status. Standard errors clustered at the district level. Panel A assigns students to treatment or comparison schools based on the type of school the student attended in the year closest to the policy year. Panel B assigns students to a treatment school if the student ever attended a treatment school. Panel C uses a continuous measure of treatment based on the share of 2012-2013 truancy that resulted in OSS for the school the student attended in the year closest to the policy. Panel D uses a continuous measure equal to the highest share of 2012-2013 truancy that resulted in OSS among all the schools that the student attended during the panel. Because Panels C and D use continuous treatment measures, the total “effect” can be interpreted as the total change in a school that used OSS for 100% of truancy in 2012-2013, relative to a school that used OSS for 0% of 2012-2013 truancy.

p < .1. **p < .05.

While the results so far represent the overall effects, the effects in compliant schools may be most relevant for what we might expect from this type of policy, if implemented completely. Thus, I estimate separate models for the schools that did not report using OSS for truancy in the first postpolicy year, 2013-2014. The results, in Supplemental Appendix Table C, are very consistent with Table 2: decreases in absenteeism, with impacts on student achievement, truancy referrals, and overall disciplinary referrals that were statistically indistinguishable from zero.

The results presented previously indicate policy-related declines in absenteeism and improvements in test scores, particularly for Black students, FRL-eligible students, and students who were truant during the study period. Never-truant students had higher attendance and Black students had lower disciplinary referrals, postpolicy. When focusing just on compliant schools, the overall estimated changes were similar (only slight improvements in attendance measures).

To test whether these results may be affected by other confounding factors, I conduct two placebo checks, using just prepolicy data, that estimate the impacts of fake policies, 1 and 2 years prior to the true policy (e.g., St. Clair, Hallberg, & Cook, 2016). Any estimated “effects” of these fake policies raise doubt that the main models provide causal estimates. Two separate tests are conducted. The test using a fake policy 1 year back has the advantage of four prepolicy years in the test score models (five in other models), which is the minimum recommended for CITS (Somers et al., 2013). The downside is there is only one outcome year remaining. The placebo check using a fake policy 2 years back has the benefit of allowing two outcome years but is limited to 3 years prepolicy in the test score models (four for other outcomes).

In Supplemental Appendix Table D, I report Post × Treat from the 1-year-back model and Post × Treat + 2(Treat × YSP) from the 2-years-back model as the total “effects.” These are not directly comparable with the main 3-year effects. I focus on absenteeism and chronic absenteeism, as these were the only outcomes that were estimated to have policy-related changes for the overall population in Table 2. None of the 16 estimates for these absenteeism outcomes are significant. This does not prove that the estimated policy-related changes in Table 2 are causal but at least does not provide evidence against causal inference. Of the 64 estimates in Supplemental Appendix Table D, only four estimated effects are statistically significant at the 90% confidence level, less than the six (≈10% of 64) we would expect due to mere chance.

Similar placebo checks were conducted for each subgroup. I focus in Supplemental Appendix Tables E to G on the significant subgroup effects in Tables 3 to 6, but the full results are available on request. The results in Supplemental Appendix Table E create doubt about the causality of the increase in math test scores for FRL-eligible students and the increase in ELA scores for students who were ever truant (from Table 3). For the impact on ELA scores for students who were ever truant, the placebo effects estimated were of the opposite sign as the main effects, suggesting the possibility that the estimated effects are driven by reversion to the mean. The findings that the policy increased the math and ELA test scores for Black students did not fail the placebo check.

Supplemental Appendix Table F shows the absenteeism results of the placebo checks, focusing on the groups with estimated gains in Table 4. In general, the placebo checks pass, with the exception of an estimated increase in chronic absenteeism for Black students, suggesting possible reversion to the mean rather than casual effects.

I do not show placebo results for the impact on truancy, as I find no estimated effects on truancy in Table 5. Turning to disciplinary outcomes, the placebo checks for the estimated decrease in discipline referrals for Black students, as seen in Table 6, are shown in Supplemental Appendix Table G. These placebo checks passed in all cases.

Finally, I conducted placebo checks for compliant schools. Supplemental Appendix Table C indicated that both measures of student absenteeism went down in compliant schools. In all cases, the placebo checks for these attendance improvements, shown in Supplemental Appendix Table H, passed, providing more confidence in these results.

In summary, the most consistent student-level results, which are robust to the placebo checks, are that absenteeism improved overall, in compliant schools, and particularly for truant students and students from traditionally underserved backgrounds. In addition, there is some evidence that test scores improved and disciplinary referrals decreased for Black students.

RQ 2: How Did School-Level Disciplinary Outcomes Change in “Policy-Affected” Schools?

The results of the school-level CITS analysis are in Table 7. Panel A uses the treatment measure indicating whether a school used OSS as a consequence for truancy at least once ( $T_{s}$ = 1) or not at all ( $T_{s}$ = 0) in 2012-2013. Panel B uses the alternative definition of treatment, the school’s percentage of 2012-2013 truancy cases that resulted in OSS. I report the coefficients on $(T_{s} \times P O L I C Y_{t})$ and $(T_{s} \times Y R_S I N C E_P O L I C Y_{t})$ as well as the total effect after 3 years. In Panel B, the total “effect” by 2015-2016 represents the “effect” for schools with 100% OSS for truancy, compared with a school with 0% OSS for truancy, in 2012-2013. Panel A (but not Panel B) provides suggestive evidence, significant at the 90% confidence level, of a reduction in truancy by 2.2 incidents per 100 students. Fewer truancy reports could indicate a reduction in truancy behavior or a change in reporting behavior, but this is not testable with the available data.

Table 7.

Estimated Policy-Related Change in the Use of “Other” Consequences for Truancy.

	Truancy per 100 Students	“Other” Infractions per 100 Students	Percentage of Truancy Resulting in “Other”
Panel A: T_s = used OSS for truancy at least once in 2012-2013
T_s × POLICY_t	0.019	1.980	0.066*
	(0.762)	(2.989)	(0.037)
T_s × YR_SINCE_POLICY	−0.746	2.706*	0.016
	(0.483)	(1.463)	(0.019)
Total “effect” by 2015-2016	−2.220*	10.100**	0.115***
	(1.184)	(4.678)	(0.041)
Number of schools	374	374	374
Observations	3,205	3,205	2,631
Adjusted R²	0.183	0.589	0.249
Panel B: T_s = percentage of truancy cases resulting in OSS in 2012-2013
T_s × POLICY_t	−0.579	−3.779	0.066
	(0.846)	(3.332)	(0.059)
T_s × YR_SINCE_POLICY	0.064	1.077	0.028
	(0.484)	(1.805)	(0.032)
Total “effect” by 2015-2016	−0.386	−0.547	0.150**
	(1.106)	(4.926)	(0.067)
Number of schools	374	374	374
Observations	3,205	3,205	2,631
Adjusted R²	0.181	0.590	0.245

Note. All models include school fixed effects and school-level characteristics including log of enrollment, truancy frequency (incidents per 100 students), percent special education, percent FRL-eligible, percent Black, percent Hispanic, and percent other non-White, indicators for middle and high schools (with elementary schools as the omitted group), and seven controls for the frequency of each consequence type (count per 100 students). Exception: The models predicting the frequency of truancy and other infractions (per 100 students) do not include the frequency of truancy as a control variable. Standard errors are clustered at the school level. Dependent variables are on a 0 to 1 scale. Total “effect” by 2015-2016 in Panel B represents the “effect” for schools with 100% OSS for truancy, compared with a school with 0% OSS for truancy, in 2012-2013.

p < .1. **p < .05. ***p < .01.

Panel A also shows an increase in “other” infractions of 10.1 incidents per 100 students. Comparing this with the estimated truancy reduction, it does not appear that schools are simply recoding truancy as “other.” Also, this may not be a result of the policy, as a similar result is not indicated in Panel B, and the rise in “other” infractions was occurring before the policy change.

Finally, Table 7 indicates the policy-related change in the use of “other” consequences for truancy. Table 1 and Supplemental Appendix Table B available online showed that schools were shifting away from OSS and ISS toward “other” consequences, but the CITS analysis estimates the size of the policy-related change by using the comparison schools as the counterfactual for what theoretically would have happened in the treatment schools in the absence of the policy. Both Panels A and B suggest a policy-related increase in the use of “other” consequences for truancy.

Placebo check

I conduct placebo checks for the school-level models, estimating the same model as in Equation (2), but adjusting the $P O L I C Y_{t}$ and $Y R_S I N C E_P O L I C Y_{t}$ variables to represent fake policies 1 and 2 years prior to the true policy and dropping the years that follow the true policy. The results are in Supplemental Appendix Table I. The placebo checks “passed” for 11 out of 12 models in Table 7. The one test that failed suggested an effect of the fake policy 1 year back on the share of truancy resulting in “other” consequences. The direction of the estimated effect in the placebo check (negative) suggests the increase in Table 7 may just be reversion to the mean.

In summary, the school-level changes that were robust to the placebo checks are a slight decline in truancy rates and a slight increase in “other” infraction rates in treatment schools relative to comparison schools. However, it is unclear whether these are simply change in reporting practices or actual changes in student behavior.

Additional robustness checks

The assumption—required for causal inference—that deviations from trend within the comparison schools serve as a valid counterfactual is a strong assumption and would be invalidated if unobservable factors changed around the time of the policy in different ways in the treatment and comparison schools. For example, if treatment or comparison schools changed practices in ways that affect these outcomes (or both types of schools were making changes in different ways), this would prohibit a causal interpretation. While it is impossible to directly test changes in unobservable factors, I can test whether observable factors appear to be affected by the policy, which might raise concerns that unobservable factors have changed as well or that the estimation approach is picking up spurious effects, rather than causal ones. I estimate regressions as in Equation (2) but predict school-by-year measures, including the percentage of students who are FRL-eligible, percent in special education, percent Black, percent Hispanic, and school enrollment size. The explanatory variables are the same as in Equation (2), except that, for each model, the dependent variable (or a derivation there of) is not included as an explanatory variable.¹³ In general, these results (in Supplemental Appendix Table J) indicate that the policy did not affect these characteristics, so I do not find evidence to reject the identifying assumption.

In summary, across a variety of model specifications and robustness checks, the most consistent findings are that Arkansas’s policy banning OSS as a consequence for truancy may have improved attendance overall (particularly for disadvantaged students), increased test scores for Black students, and decreased the number of disciplinary referrals for Black students. There were no student-level impacts on truancy.

Discussion and Conclusions

The state of Arkansas pursued a policy prohibiting the use of OSS for truancy, theoretically with the goal of improving educational outcomes for students by encouraging reasonable consequences and reengaging students in the school environment. I hypothesized that this policy could affect eight student-level outcomes related to achievement, absenteeism, truancy, and disciplinary referrals, as well as school-level discipline practices such as reports of truancy, reports of “other” infractions, and the use of “other” consequences for truancy.

I tested a variety of specifications and placebo checks. The policy is related to slight improvements in attendance—an important measure of student engagement (Liu & Loeb, 2017; Taylor & Parsons, 2011)—overall, and particularly for disadvantaged students (ever-truant, Black, and FRL-eligible students). The concentration of these impacts in compliant schools is consistent with an interpretation of these estimates as policy effects. However, these estimated policy-related changes are small—similar to what we might expect simply due to declines in OSS as a result of the policy—and were only estimated in certain specifications. Black students also experienced policy-related declines in discipline referrals and improvements in test scores. Notably, the benefits are concentrated among students who are generally overrepresented in disciplinary referrals and exclusionary discipline in Arkansas (Anderson & Ritter, 2017; Ritter & Anderson, 2018) and the nation (U.S. Department of Education & U.S. Department of Justice, 2014).

School-level analyses do not provide strong evidence that schools are reporting truancy incidents as “other” infractions to comply with the policy, although treatment schools increased their reporting of “other” infractions more than comparisons schools. This could be due to increased misbehavior, increased reporting, or a combination of the two.

While this policy may have improved outcomes for some relatively disadvantaged groups of students, truancy was apparently not affected. Moreover, the improvements in attendance for ever-truant students are not significantly greater than the improvements in attendance for never-truant students, so the policy may not have directly affected the types of students theoretically targeted by this policy. In fact, in other work, Anderson, Egalite, and Mills (2019) find that the policy was not related to differential changes in attendance for truant students, relative to nontruant students, in the first-year postpolicy.¹⁴

A few limitations exist for a causal interpretation of these results. The comparison schools may not be a clean counterfactual, as treatment and comparison schools do differ in observable ways (Anderson, 2018). Furthermore, there was variation in compliance across schools, so I am not able to say what the impact of the policy might have been if compliance was complete. In addition, administrative data are dependent on reporting practices that may differ across schools and across districts. The use of school fixed effects allows me to control for unobservable characteristics of schools that are constant over time, but bias could remain if there are within-school changes in reporting practices over time that confound my estimates.

Lessons for School Leaders and Policy Makers

What conclusions can be drawn for school leaders and policy makers seeking to improve student engagement, reduce absenteeism, and reduce suspensions? In this case, the effects of a ban on suspensions are small and are likely influenced by low levels of compliance, perhaps due in part to a lack of communication between policy makers and implementers at various levels.

Communication is critical for local implementation of state or federal policies. To be effective, policies should be unambiguous (Firestone, 1989; Sabatier & Mazmanian, 1979; Weatherly & Lipsky, 1977), and the policy’s “deep underlying principles,” should be communicated (Spillane, Resier, & Reimer, 2002, p. 416). In this case, although the law was unambiguously worded, a lack of communication about the rationale for reform may have affected compliance.

In addition, local capacity and will are important for implementation, particularly when there are multiple layers of government or institutions (Hill & Hupe, 2003; McLaughlin, 1987). McLaughlin (1987) has suggested that effective implementation requires a careful balance between pressure and support. Balance is likely important with discipline reforms, as pressure to comply, without supports, may create unintended consequences related to misreporting disciplinary outcomes, but in this case, it also appears that there was not enough pressure either.

The state’s hands-off approach may be due in part to deference to local control, which has been cited as a reason to continue allowing corporal punishment in the state’s public schools (Caputo, 2017; Froelich, 2016). It may also be logistically difficult to coordinate among many small districts in relatively rural states.¹⁵ Lack of policy knowledge, resources, and accountability are key barriers to policy impact in rural schools (Belansky et al., 2009), and legislation is often passed without fully considering the impact on rural schools (Chance, 1993).

Unfortunately, we cannot know what the effect of this policy would have been if implemented more fully, but focusing on altering disciplinary responses to truancy may not be as effective as preventing truancy in the first place. Evidence generally suggests that educators should focus on preventative and social-based supports rather than on punitive responses (Smink & Heilbrunn, 2005). In a review of 16 studies on truancy interventions, Sutphen et al. (2010) conclude, for example, that incentive programs show some promise (e.g., Brooks, 1975, Ford & Sutphen, 1996; Licht, Gard, & Guardino, 1991), as do comprehensive school reorganization (McPartland, Balfanz, Jordan, & Legters, 1998), and parent contact (McCluskey, Bynum, & Patchin, 2004). Some punitive responses, such as loss of public assistance, may actually lead to declines in attendance over time (Jones, Harris, & Finnegan, 2002). Many of the included studies were limited by methodological challenges, and very few were experimental (Brooks, 1975; Jones et al., 2002). More recently, Flannery, Frank, and Kato (2012) found that when used repeatedly in response to truancy, OSS can actually reinforce the truant behavior.

Along the lines of preventative and supportive alternatives, one possible solution to absenteeism and misbehavior is School-Wide Positive Behavior Interventions and Supports, a framework of tiered supports for students at different levels of need. Experimental studies at the high school level are lacking, but when implemented with fidelity, the School-Wide Positive Behavior Interventions and Supports framework has been linked to improvement in disciplinary incidents (Flannery, Fenning, Kato, & McIntosh, 2014; Freeman et al., 2015) and attendance (Freeman et al., 2015) in high schools.

There are at least 33 districts with 107 schools in Arkansas incorporating Positive Behavioral Interventions and Supports, through training and technical support from the Center for Community Engagement at Arkansas State University (2018). Furthermore, Arkansas recently included attendance as an indicator of student engagement in its Every Student Succeeds Act plan, placing even more scrutiny on attendance. At the time of writing, organizations such as Attendance Works are working to track and improve attendance in 40 Arkansas school districts (Arkansas Campaign for Grade Level Reading, 2018).

To ensure the success of reforms, it is critical to identify schools in need of additional support. A state like Arkansas, with many small, rural districts may face a particular challenge with respect to communicating and providing these supports (Sugai & Horner, 2006), so context should be considered when designing and implementing programs. Furthermore, care should be taken to avoid a “train-and-hope” approach (Stokes & Baer, 1977). Effective classroom management and positive climate take time, practice, and critical feedback from supervisors and mentors (Oliver & Reschly, 2007). Moreover, literature suggests that training and implementation of interventions requires collaboration and support from various stakeholders; should be aligned to existing routines, philosophies, and goals; and should consider the ramifications for staff in the school building (Forman, Olin, Hoagwood, Crowe, & Saka, 2009; Sugai & Horner, 2006).

It is not enough simply to reduce suspensions—the alternative approach taken matters. Both the U.S. Department of Education (2014) and the Council of State Governments (Morgan, Salomon, Plotkin, & Cohen, 2014) have supported teacher professional development on social emotional learning, conflict resolution, and building positive relationships, and there is experimental evidence that PD related to nonpunitive classroom behavior management can reduce behavioral incidents and suspensions (Flynn, Lissy, Alicea, Tazartes, & McKay, 2016).

School and district leaders have a role to play in supporting teachers. Many new teachers feel inadequately prepared to establish positive and productive learning environments (Baker, 2005), which is worrisome given that economically disadvantaged students are disproportionately exposed to less experienced teachers (e.g., Goldhaber, Lavery, & Theobald, 2015; Sass, Hannaway, Zu, Figlio, & Feng, 2012). School leaders should encourage teachers to use rules that are positively stated, simple, and consistent with a schoolwide behavior plan (Oliver & Reschly, 2007). There are also simple ways that school leaders can use data to build awareness around student discipline, because teachers may underestimate the extent to which exclusionary discipline is used in their schools (Barnhart et al., 2008).

As policies and programs are developed or expanded, we must evaluate the impact on students. Qualitative and mixed methods research could help illuminate some of the questions about the impact of this particular policy, as there is much left unknown about how schools are actually responding. Importantly, the state recently expanded the reporting categories for both infractions and consequences, allowing additional insights into student discipline going forward.

In conclusion, this study provides evidence on the student- and school-level outcomes of a state law prohibiting OSS as a consequence for truancy. This law, theoretically enacted with the goal of reengaging students and improving student outcomes, appears to have slightly benefited students, particularly in terms of attendance, and particularly for students from relatively disadvantaged backgrounds. Nonetheless, evidence on compliance with this policy indicates that certain types of schools may need additional supports to ensure local compliance (Anderson, 2018). Looking forward, it will be interesting to see how schools in Arkansas react to a recent policy change banning OSS and expulsion in kindergarten through fifth grade except in cases of “physical risk” or “serious disruption that cannot be addressed through other means” (Arkansas Act 1059, 2017). Given the findings here, it appears that more support may be required to ensure that the policy is implemented as intended.

Supplemental Material

EAQ_861138_Online_Appendix_updated – Supplemental material for Academic, Attendance, and Behavioral Outcomes of a Suspension Reduction Policy: Lessons for School Leaders and Policy Makers

Supplemental material, EAQ_861138_Online_Appendix_updated for Academic, Attendance, and Behavioral Outcomes of a Suspension Reduction Policy: Lessons for School Leaders and Policy Makers by Kaitlin P. Anderson in Educational Administration Quarterly

Footnotes

Declaration of Conflicting Interests

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

Funding

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

ORCID iD

Kaitlin P. Anderson

Supplemental Material

Supplemental material for this article is available online.

Notes

Author Biography

Kaitlin P. Anderson, Ph.D. is a post-doctoral research associate in the Education Policy Innovation Collaborative at Michigan State University. Her research interests include educational equity and access, particularly related to student discipline, teacher quality, and school choice.

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