THREE ESSAYS IN THE ECONOMICS OF EDUCATION

By

Kevin Kho

A DISSERTATION

Michigan State University

in partial fulﬁllment of the requirements

Submitted to

for the degree of

Economics – Doctor of Philosophy

2018

ABSTRACT

THREE ESSAYS IN THE ECONOMICS OF EDUCATION

By

Kevin Kho

Chapter 1: School Cellphone Bans and Student Substance Abuse: Evidence From California
Public High Schools

Following high proﬁle school shootings and the September 11th terrorist attacks, public concern
over school emergency preparedness prompted the California State Legislature in 2003 to overturn
a statewide ban against student possession of cellphones on campuses. After the repeal of the
prohibition, which had been established in 1988 to curb drug dealing, school districts were allowed
individually to either continue banning phones or modify their device policies; most opted over
time to accommodate usage during certain hours of the day. Using ﬁxed eﬀects regression analysis
clustered at the district level, I exploit variation in the timing of district policies to estimate the
impact on substance abuse from lifting school cellphone bans. Results provide evidence that
allowing students to use cellphones at school increases opportunities to obtain and abuse controlled
substances; this eﬀect is particularly pronounced in the incidence of marijuana smoking among 9th
graders, who exhibit a 1.3 percentage point higher chance of reporting past-month marijuana use
in the year a ban is lifted. Factors involved may include the capability that the technology provides
to negotiate high risk interactions in private and to seek out and contact a relatively small number
of drug suppliers; as is thus to be expected, no impact is found on the consumption of cigarettes,
which can be obtained legally by a large proportion of high schoolers.

Chapter 2: Impact of Internet Access on Student Learning in Peruvian Schools (with Leah
Lakdawala and Eduardo Nakasone)

We investigate the impacts of school-based internet access on pupil achievement in Peru, using
a large panel of 5,903 public primary schools that gained internet connections during 2007-2014.

We employ an event study approach and a trend break analysis that exploit variation in the timing of
internet roll-out up to 5 years after installation. We ﬁnd that internet access has a moderate, positive
short-run impact on school-average standardized math scores, but importantly that this eﬀect grows
over time. We provide evidence that schools require time to adapt to internet access by hiring
teachers with computer training and that this process is not immediate. These dynamics highlight
the need for complementary investments to fully exploit new technological inputs and underscores
the importance of using an extended evaluation window to allow the eﬀects of school-based internet
on learning to materialize.

Chapter 3: Discretionary School Discipline Policies and Demographic Disparities

In 2014, California passed the law AB 420, becoming the ﬁrst state to limit the use of school
suspensions and expulsions as punishment for “willful deﬁance” — a subjectively determined
oﬀense thought by state lawmakers to lead to racial disparities in discipline.
In this paper, I
overview the state’s recent (from 2012-2017) progress in reducing exclusionary discipline and note
eﬀects on disproportionality, here characterized as the diﬀerence between a given group’s proportion
of discipline and its proportion of enrollment. Using identiﬁcation by treatment intensity, based on
schools’ pre AB 420 proportion of discipline attributable to willful deﬁance, I also attempt to gauge
the eﬀectiveness of reducing punishment of deﬁance in mitigating disproportionality. School level
administrative data from elementary schools (spanning kindergarten through 5th grade) indicate
that exclusionary discipline has considerably declined throughout the period. On the other hand,
it does not appear that AB 420, along with lower willful deﬁance related discipline, has reduced
disproportionality.

ACKNOWLEDGEMENTS

I am grateful for the generous feedback and comments provided by Jeﬀ Biddle, Scott Imberman,
Leah Lakdawala, Eduardo Nakasone, and several other faculty and graduate students who made
time to attend my job market paper workshop sessions and departmental applied seminar.

I am also thankful to Jorge Mesinas at the Peruvian Ministry of Education for access to the data
from the Evaluacion Censal de Estudiantes, as well as to many others who provided feedback to
my coauthors and I during seminars at the Michigan Development Day, Michigan State University,
and University of Wisconsin-Madison.

The opinions expressed are those of the author. All errors are my own.

iv

TABLE OF CONTENTS

LIST OF TABLES .
LIST OF FIGURES .

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ix

CHAPTER 1 SCHOOL CELLPHONE BANS AND STUDENT SUBSTANCE ABUSE:

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Sample

Introduction .

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1.4 Analysis and Results

1.1
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1.2 Literature Review .
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1.3 Policy Setting and Data .

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EVIDENCE FROM CALIFORNIA PUBLIC HIGH SCHOOLS . . . . . . .
1
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1.3.1 Repeal of Statewide Campus Cellphone Ban . . . . . . . . . . . . . . . . .
9
1.3.2 California Healthy Kids Survey . . . . . . . . . . . . . . . . . . . . . . . .
1.3.3 District Cellphone Regulations . . . . . . . . . . . . . . . . . . . . . . . . 10
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1.3.4
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1.4.1 Drug Use Before and After District Policy Revision . . . . . . . . . . . . . 17
1.4.1.1 Multiple Outcomes . . . . . . . . . . . . . . . . . . . . . . . . . 19
1.4.2 Endogenous Policy Timing and Event Studies . . . . . . . . . . . . . . . . 20
1.4.3
Impacts As Shifts and Trend Breaks . . . . . . . . . . . . . . . . . . . . . 30
1.4.4 Academic Performance . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32
1.5 Mechanisms .
. 33
1.6 Robustness to Concurrent Changes in Controls . . . . . . . . . . . . . . . . . . . . 36
1.7 Policy Implications and Heterogeneous Eﬀects . . . . . . . . . . . . . . . . . . . . 37
Proportion of School Eligible for Free and Reduced Price Lunches (FRPL) . 37
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1.7.1
1.7.2 Gender
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1.8 Summary .

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CHAPTER 2

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Introduction .

2.1
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2.2 Setting and data .

IMPACT OF INTERNET ACCESS ON STUDENT LEARNING IN PERUVIAN
SCHOOLS (WITH LEAH LAKDAWALA AND EDUARDO NAKASONE)
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43
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. 48
2.2.1 Education and ICT Access in Peru . . . . . . . . . . . . . . . . . . . . . . 48
2.2.2 Data .
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2.2.2.1 Censo Escolar (CE) and School-based Internet Access . . . . . . 50
Evaluación Censal de Estudiantes (ECE)
2.2.2.2
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2.2.2.3
Estimation Sample . . . . . . . . . . . . . . . . . . . . . . . . . 54
2.3 Empirical strategies and results . . . . . . . . . . . . . . . . . . . . . . . . . . . . 55
2.3.1 Event study speciﬁcation . . . . . . . . . . . . . . . . . . . . . . . . . . . 55
2.3.2 Trend break speciﬁcation . . . . . . . . . . . . . . . . . . . . . . . . . . . 60
. 61
2.4.1 Changes in sample composition . . . . . . . . . . . . . . . . . . . . . . . 62
2.4.1.1 Unbalanced panel and attrition . . . . . . . . . . . . . . . . . . . 63

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2.4 Robustness checks .

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2.4.1.2

Student composition and endogenous sorting . . . . . . . . . .

2.4.2 Concurrent changes in school resources
2.4.3 Diﬀerential pre-trends

. 66
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2.5 Explaining dynamics and identifying potential mechanisms . . . . . . . . . . . . . 73
. 73
. 74
. 75
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Increased individualized attention . . . . . . . . . . . . . . . . . . . . .
Substitution between internet access and teacher qualiﬁcations . . . . . .

2.5.1 Why do the eﬀects of internet access take time to emerge?
2.5.2
2.5.3

2.6 Conclusions . .

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Introduction .

CHAPTER 3 DISCRETIONARY SCHOOL DISCIPLINE POLICIES AND DEMOGRAPHIC

DISPARITIES .
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3.1
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3.2 Disparities and Bias: Review of Theories and Evidence . . . . . . . . . . . . . . . 83
3.3 AB 420 and Willful Deﬁance in California Public Schools
. . . . . . . . . . . . . 85
3.4 Recent CA Suspensions and Disproportionality . . . . . . . . . . . . . . . . . . . 88
. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 90
3.5 Role of Willful Deﬁance
3.5.1 Treatment Intensity: Initial Use of Willful Deﬁance . . . . . . . . . . . . . 90
3.5.2 Robustness
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Separate Quantiles by Initial Use of Willful Deﬁance . . . . . . . . . . . . 95
3.5.3
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CHAPTER 1 APPENDIX . . . . . . . . . . . . . . . . . . . . . . . 101
CHAPTER 2 APPENDIX . . . . . . . . . . . . . . . . . . . . . . . 115
CHAPTER 3 APPENDIX . . . . . . . . . . . . . . . . . . . . . . . 130
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APPENDICES .
APPENDIX A
APPENDIX B
APPENDIX C
BIBLIOGRAPHY .

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3.6 Summary .
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LIST OF TABLES

Table 1.1:

Introduction of District Policies

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Table 1.2: Student Summary Statistics: Pre and Post District Policy Revision . . . . . . . . 13

Table 1.3: School Summary Statistics: Pre and Post District Policy Revision . . . . . . . . 14

Table 1.4: Year 2002 School Summary Statistics . . . . . . . . . . . . . . . . . . . . . . . 15

Table 1.5: Year 2002 Student Summary Statistics

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Table 1.6: Drug Use Pre vs. Post District Policy Revision . . . . . . . . . . . . . . . . . . 18

Table 1.7: Trend Break Speciﬁcation . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 32

Table 1.8: Heterogeneity: Time of Day When Cellphone Use is Allowed . . . . . . . . . . 35

Table 1.9: Heterogenety: Race .

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Table 1.10: Heterogeneity: School is Above/Below Median Proportion FRPL Eligible . . . . 40

Table 1.11: Heterogeneity: Gender .

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Table 2.1:

Internet Access & Test Scores: Trend Break Results

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Table 2.2: Eﬀect of Internet Access on Grade 2 Transfers, Re-entry, Test Taking, and

Student Composition .

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Table 2.3: Eﬀect of Internet Access on School Resources

. . . . . . . . . . . . . . . . . . 70

Table 2.4: Allowing for State, State-Sector, and School-speciﬁc Pre-trends

. . . . . . . . . 72

Table 3.1: Eﬀects of “Willful Deﬁance” on Disproportionality in Suspensions . . . . . . . . 92

Table 3.2: Proportion of Deﬁance Suspensions Regressed on School Demographics

. . . . 94

Table A.1: Trend Break Speciﬁcation on Pooled Sample (9th & 11th Graders) . . . . . . . . 101

Table A.2: Controlling for School Speciﬁc Time Trends . . . . . . . . . . . . . . . . . . . . 113

Table A.3: Controlling for District Speciﬁc Time Trends . . . . . . . . . . . . . . . . . . . 114

vii

Table B.1: Predictors of Internet Access

. . . . . . . . . . . . . . . . . . . . . . . . . . . 117

Table B.2: Summary Statistics (2007 or Earliest Available Year) of Public Primary Schools

in ECE, by Year of Internet Access . . . . . . . . . . . . . . . . . . . . . . . . . 118

Table B.3: Eﬀect of Internet Access on Standardized Test Scores

. . . . . . . . . . . . . . 119

Table B.4: Summary Statistics for Alternate Estimation Samples

. . . . . . . . . . . . . . 123

Table B.5: Understanding the Role of School-level Compositional Changes: Trend Break

Results

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Table B.6: Attrition (Number of Observations)

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Table B.7: Eﬀects of Computers in Non-internet Schools . . . . . . . . . . . . . . . . . .

. 126

Table B.8: Eﬀects of Concurrent Computer Investments: Back of the Envelope Calculations

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Table B.9: Internet Access and Computer Teachers: Trend Break Results

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Table B.10: Heterogeneity in the Impact of Internet Access across Schools by Student to

Teacher Ratios and Teacher Qualiﬁcations: Trend Break Results . . . . . . . . . 129

Table C.1: Disproportionality in Suspensions Over Time by Initial Use of “Willful Deﬁance”

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viii

LIST OF FIGURES

Figure 1.1: District policy revisions by year . . . . . . . . . . . . . . . . . . . . . . . . .

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Figure 1.2: Current policies (2017)

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8

Figure 1.3: Composite: Any substance in past 30 days . . . . . . . . . . . . . . . . . . .

. 23

Figure 1.4: Used cocaine/crack in past 30 days . . . . . . . . . . . . . . . . . . . . . . .

. 24

Figure 1.5: Used marijuana in past 30 days . . . . . . . . . . . . . . . . . . . . . . . . . . 25

Figure 1.6: Used inhalants in past 30 days . . . . . . . . . . . . . . . . . . . . . . . . . . . 26

Figure 1.7: Used meth in past 30 days . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 27

Figure 1.8: Used alcohol in past 30 days . . . . . . . . . . . . . . . . . . . . . . . . . . . . 28

Figure 1.9: Used cigarettes in past 30 days

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Figure 2.1:

Internet Connectivity in Primary Public Schools, 2006-2014 . . . . . . . . . . . 52

Figure 2.2: Standardized Average Math Scores over Time, by Year of Initial Internet

Access .

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Figure 2.3:

Impact of Internet Access on Test Scores . . . . . . . . . . . . . . . . . . . . . 59

Figure 2.4: Eﬀect of Internet Access in the Sample of Schools Observed in at least Two

Periods before and Two Periods after Internet Access: Event Study Results . . . 64

Figure 2.5: Eﬀect of Internet Access in the Sample of Schools Observed in All Periods:

Event Study Results .

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Figure 2.6:

Internet Access and Presence of a Computer Teacher

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. 74

Figure 2.7: Heterogeneity in the Impact of Internet Access on Test Scores: Event Study

Results .

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Figure 3.1: Suspensions Over Time Among Schools With Large Initial Proportion of

Deﬁance Suspensions . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 87

Figure 3.2: Average Suspensions and Expulsions Over Time . . . . . . . . . . . . . . . . . 89

ix

Figure 3.3: Disproportionality in Suspensions Over Time

. . . . . . . . . . . . . . . . . . 91

Figure 3.4: Proportion of Discipline Related to Deﬁance by Initial Proportion of Discipline

Related to Deﬁance .

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. . . . . . . . . . . . . . . . . . . . . . . . . . . . . . 96

Figure 3.5: Disproportionality in School Discipline by Initial Use of “Willful Deﬁance” . . 97

Figure A.1: Event Study Regressions Using Pooled Sample of 9th and 11th Graders

Together .

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Figure A.2: 9th Grade Girls vs. Boys: Alcohol

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Figure A.3: Districts not revising policy until 2006: Composite: g9 Any drugs

. . . . . . . 104

Figure A.4: Districts not revising policy until 2006: g9 Cocaine/crack . . . . . . . . . . .

. 105

Figure A.5: Districts not revising policy until 2006: g9 Marijuana . . . . . . . . . . . . . . 106

Figure A.6: Districts not revising policy until 2006: g9 Inhalants . . . . . . . . . . . . . . . 107

Figure A.7: Districts not revising policy until 2006: g9 Meth . . . . . . . . . . . . . . . . . 108

Figure A.8: Districts not revising policy until 2006: g9 Alcohol

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. 109

Figure A.9: Districts not revising policy until 2006: g9 Cigarettes . . . . . . . . . . . . . . 110

Figure A.10:Grade 9 Robustness: Gender and Proportion Black . . . . . . . . . . . . . . . . 111

Figure A.11:Mostly C’s or worse this past year . . . . . . . . . . . . . . . . . . . . . . . .

. 112

Figure B.1: Performance of Grade 2 Students in Public Schools on the ECE (2007-2014) . . 115

Figure B.2: Translated Excerpt of Flow Chart for Prioritization under Plan Huascarán . . . 116

Figure B.3: Translated Excerpt of Prioritization Directive for Plan Huascarán . . . . . . . . 120

Figure B.4: Translated School Data Sheet for Plan Huascarán . . . . . . . . . . . . . . . . 121

Figure B.5: Schools and Students in ECE, 2007-2014 . . . . . . . . . . . . . . . . . . . . . 122

x

CHAPTER 1

SCHOOL CELLPHONE BANS AND STUDENT SUBSTANCE ABUSE: EVIDENCE

FROM CALIFORNIA PUBLIC HIGH SCHOOLS

1.1 Introduction

In the United States today, educators and policymakers increasingly allow secondary school
students to carry and use cellphones on campuses. In easily the most visible instance of this trend, the
New York City Department of Education—the nation’s largest school district by enrollment—lifted
a decade-long campus cellphone ban in March 2015. The change, not without controversy, followed
longstanding complaints by parents and civil rights advocates that the policy hampered emergency
preparedness, reduced ﬂexibility in scheduling after school activities, and unduly burdened low
income students, for whom the fees charged by daytime phone storage services caused appreciable
hardship (Harris and Schweber, 2015).1 With mobile devices’ increased ubiquity and role in
household communication, issues of safety and convenience have elsewhere also weighed heavily
in the determination of reasonable device policies.

Furthermore, the emergence of more sophisticated models featuring ever broader capabilities
has fueled interest in using student devices to address unmet needs in learning. Hence, a growing
number of teachers in Los Angeles Uniﬁed, the second largest school district by enrollment, sidestep
oﬃcial regulation by conducting class exercises that incorporate cellphones (Gerson, 2015). At
a specially designated pilot school within LAUSD, software such as Google Classroom and the
Remind app enhances student-teacher communication and promotes accountability by tracking
course progress (Gerson, 2015). Thus, outright bans have also waned in popularity due to the
technology’s role as a platform for new and evidently promising pedagogical tools.

On one hand, greater preparedness for emergencies and access to modern education resources
1Truck and van based services, generally operated by individual owners, charged roughly a
dollar per day or twenty dollars per month to securely store students’ cellphones during the school
day (Harris and Schweber, 2015).

1

oﬀer compelling reasons to embrace mobile phones. However, it is also the case that many
current cellphone bans came into existence in order to mitigate serious problems—in particular,
drug dealing among students, which continues to challenge communities nationwide.
In 2016,
9.8% of 10th graders and 14.3% of 12th graders across the country reported having used an illicit
drug other than marijuana in the past year, including cocaine, methamphetamines, and inhalants
(National Institute on Drug Abuse, 2016). While these ﬁgures in fact reﬂect a modest decline
over previous years, use of marijuana remains ever prevalent; 38.3% of 12th graders in states
with medical marijuana provisions reported use in the past year, compared to 33.3% even in states
without such laws (National Institute on Drug Abuse, 2016). Furthermore, only 31.1% of 12th
graders associate regularly smoking marijuana with harm, a proportion that has fallen substantially
over time (National Institute on Drug Abuse, 2016). If cellphone use facilitates risky behaviors,
then device policies may bear meaningful inﬂuence on human capital development through other
channels than instructional resources and test performance.

In fact, cellphone communication very likely defeats several barriers to obtaining drugs. While
it may not be uncommon that high schoolers, possibly handicapped by limited maturity and faced
with questionable information from peers, develop some interest in health compromising behaviors,
including drug and alcohol use, far fewer might be expected to actually have access to controlled
substances. As such, eﬀort is required to discover and trade with a relatively limited number of
suppliers—tasks complicated by risk and social stigma. These obstacles are directly addressed by
the ability to communicate and establish relationships before physically meeting and without the
supervision of adults. This last concern also highlights the importance of the school environment;
a high density of peers and the absence of watchful household members logistically oﬀers unique
opportunities to youth, who may otherwise exert less control over their movements and activities
than adults.

This paper studies the eﬀect of lifting school cellphone bans on alcohol and drug abuse among
high school students in the state of California. As a result of the 2003 repeal of California’s
statewide school cellphone ban, district governance boards were allowed individually to either

2

continue banning phones or to modify their device policies. Over time, most opted to accommodate
usage during certain hours of the day. Using ﬁxed eﬀects regression analysis clustered at the district
level, I exploit variation in the timing of district policies to estimate the impact on substance abuse
from permitting cellphone use on school grounds. Results provide evidence that allowing students
to use cellphones at school increases opportunities to obtain and abuse controlled substances; this
eﬀect is particularly pronounced in the incidence of marijuana smoking among 9th graders, who
exhibit a 1.3 percentage point higher chance of reporting past-month marijuana use in the year a
ban is lifted. Factors involved may include the capability that the technology provides to negotiate
high risk interactions in private and to seek out and contact a relatively small number of drug
suppliers; as is thus to be expected, no impact is found on the consumption of cigarettes, which can
be obtained legally by a large proportion of high schoolers.

Student substance abuse outcomes are obtained from the California Healthy Kids Survey
(CHKS), a project funded by the California Department of Education (CDE) and executed by the
company WestEd. As a requirement for receiving Title IV funding under the No Child Left Behind
Act,2 the survey was administered to students in nearly every school of every California district at
least biennially during 2003-2010, continuing afterwards to be required of school districts receiving
state funds for certain drug prevention programs.3 Administration of the CHKS is carefully planned
to result in data representative of enrollment at the district level. Since there is no oﬃcial, central
database of school district governance codes, information on current and historical cellphone
policies was obtained from individual district websites and oﬃces during March through May of
2017.
In cases where on-line records were unavailable or insuﬃcient, oﬀ-line documents were
requested from administrative oﬃces by phone and email correspondence.

2Large districts may submit a sampling scheme that does not include all schools, and which

must be approved as being representative of the district (WestEd, n.d.)

3The CHKS includes various core and supplementary modules which broadly ask students about
health habits, lifestyle, risk behaviors, relationships (e.g. with peers, teachers, and community
members), and beliefs and attitudes. The survey forms one part of the California School Climate,
Health, and Learning Survey (CAL-SCHLS) system, which aims to provide educators with timely
insights on school climate.

3

The rest of this paper is structured as follows: Section 1.2 overviews related literature, Section
1.3 describes the policy setting, data sources, and sample studied, Section 1.4 reports empirical
analyses and results, Section 1.5 discusses mechanisms, Section 1.6 explores possible confounding
inﬂuences on outcomes by non-policy factors, Section 1.7 examines heterogeneous eﬀects that may
bear policy implications, and Section 1.8 concludes.

1.2 Literature Review

Thus far, studies in economics and education concerning high schoolers’ use of cellphones
and other mobile technologies have exclusively or almost exclusively targeted outcomes directly
related to learning (Beland and Murphy, 2016; Fryer, 2016; Hull and Duch, 2016). From a survey
of policies and interventions involving various technologies, eﬃcacy in this regard appears to
depend on the degree to which usage is planned and supervised to ensure educational applications.
In particular, evidence has associated few if any gains in learning to technology use that is not
deliberately managed by educators for learning purposes.4 Evaluating a more structured context,
however, Hull and Duch (2016) conclude that a North Carolina school district’s one-to-one laptop
program eﬀectively improved the math skills of fourth through eighth grade students over the course
of four to ﬁve years following initial assignment.5

On the other hand, experimental and quasi-experimental literature that explores broader behavioral

and health outcomes has focused on college students, with most current work underlining negative
consequences of technology dependence and misuse (Jenaro et al., 2007; Lepp et al., 2013, 2014,
2015; Li et al., 2015; Thomée et al., 2011). 6

4For instance, Fryer (2016) reports that providing cellphones to students in the Oklahoma City
Public Schools produced no measurable changes in state test scores, attendance, student eﬀort,
or behavioral incidences (which refers to the total number of suspensions, irrespective of type of
infraction). In fact, Beland and Murphy (2016) ﬁnd banning the devices to be a highly eﬀectively
means of raising the standardized test scores of the lowest achieving quintile of students, equating
the resulting gains to the average eﬀect of extending the school year by ﬁve days.

5Improvements appear to rise over time and peak at 0.16 standard deviations after ﬁve years.

Reading scores appear also to have improved to a lesser extent.

6Speciﬁcally, frequent usage has been associated with heightened anxiety and decreased life
satisfaction (Lepp et al., 2014; Jenaro et al., 2007), boredom and lower receptiveness to challenges

4

As an eﬀort to bridge the above bodies of research, this paper utilizes a quasi-experiment to
identify the role of campus cellphone policies in controlling the health compromising behaviors
of high school students. Whereas prior studies concerning high schoolers’ health habits and use
of technology has been largely descriptive, I aim to shed light on possible causal relationships
between use of phones and health outcomes. In doing so, I also contribute the ﬁrst quantitative
analysis on the eﬃcacy of a historically widespread education policy in the U.S., school cellphone
bans, speciﬁcally with regard to one of its major original aims.

Pertinently, a large number of surveys and descriptive analyses may be taken to implicate
cellphone use in enabling or exacerbating health compromising behaviors—including substance
abuse—by high school aged adolescents. According to Sánchez-Martínez and Otero (2009),
intensive phone use among youth between the ages of 13 to 20 correlates positively with drug abuse
(i.e. amphetamines, hallucinogens, cocaine, ecstasy, or heroin), as well as cellphone dependence,
school failure, and mental health issues.7 Leena et al. (2005) link problematic alcohol consumption
to cellphone use among 14 to 16 year old Finns.8 Yang et al. (2010) also highlight apparent links
between teen drinking and excessive cellphone use, further positing that cellphones “could provide
private and instant communication that is convenient to get illicit drugs.”

Furthermore, qualitative studies delving into classroom use of mobile devices as teaching tools
(Lepp et al., 2015), diminished ﬁtness (Lepp et al., 2013), and poor sleep habits (Li et al., 2015;
Thomée et al., 2011). Apart from experimental and quasi-experimental literature, Tao et al. (2017)
note from a survey 2,376 college students in Anhui, China that an association between excessive
mobile phone use and alcohol consumption persists after accounting for depressive symptoms,
while Augner and Hacker (2012) ﬁnd evidence of problematic usage among Austrian nursing
students as characterized by psychological dependence and interruption of sleep.

7Findings are based on the authors’ survey of 1,328 Spanish adolescents on mobile phone use

and other lifestyle factors and behaviors.

8Studies also suggest heterogeneity across gender and socioeconomic factors in purposes and
manner of cellphone use. For example, Sánchez-Martínez and Otero (2009) reports that girls are
signiﬁcantly more likely than boys to take cellphones to school. Additionally, Koivusilta et al.
(2007) observe in a nationally representative survey of 12 to 18 year old Finns that problematic
use of mobile phones occurs more commonly among children of parents with low socioeconomic
status or education. Moreover, while excessive use of any form of information and communication
technology (e.g. household computers) correlates with poor health outcomes, this is most apparent
with girls’ use of mobile phones.

5

have uncovered, along with opportunities, substantial challenges that highlight the extent to which
cellphones impair the ability to supervise and control student behavior. While, for instance, Engel
and Green (2011) note that a system for anonymous audience response beneﬁted shy students
who might otherwise not have answered questions posed by the teacher, they observe also that the
ability to “backchannel,” or have private conversations, necessitates a greater degree of trust due to
heightened potential for disruptive behavior.9 At a high school in its third year of a “Bring Your Own
Device” policy (promoting the use of students’ personal devices in instructional activities), Ross
(2013) report that teachers who did not attempt to integrate cellphones viewed student distraction
as a prohibitive barrier to exploiting the technology, and that the most common oﬀ-task behavior
among students of teachers who permitted the devices was text messaging.10

Finally, from nationally representative survey data on 800 12-17 year olds, Wolfe et al. (2016)
ﬁnds that school restrictions on student cellphone use signiﬁcantly impact the incidence of “sext”
messaging: teens attending schools that completely ban the devices have 48% lower odds of ever
having received a sexually explicit text message. Notably, the extent of parental supervision appears
unrelated to the likelihood of sexting, suggesting that the school environment, more so than the
home and outside environments, presents opportunities for inappropriate device usage.

1.3 Policy Setting and Data

Data for this study was obtained from the California Department of Education, the company

WestEd, and individual school district websites and oﬃces. School-level enrollment and sociodemographic
information is available from the CDE public data website.

9The authors study a pilot program that integrated cellphones into planned activities in a high
school pre-calculus course with 18 students, whom they observe during class and from whom they
collect feedback.

10For similar reasons, Thomas et al. (2014) ﬁnd that slightly over half of 1,121 teachers in
Kentucky and Tennessee (mostly in high schools) did not support the use of mobile phones in the
classroom. Teachers cited concerns such as access to inappropriate information on the internet and
diﬃculty regulating communication with parents during instructional time.

6

Figure 1.1: District policy revisions by year

1.3.1 Repeal of Statewide Campus Cellphone Ban

Eﬀective January 1, 2003, the California State Legislature repealed a prohibition against student
possession of cellphones on school campuses (Education Code 48901.5). The ban, which had
previously been in eﬀect since 1988, was established due to the widely held belief by police and
school oﬃcials that students were using the devices primarily for the coordination of drug dealing
(Willon, 2002).

In conjunction with the spread of cellphone ownership, several high-proﬁle incidents, such
as the Columbine and Santana school shootings (Willon, 2002) and the September 11th terrorist
attacks (Matthews, 2002a), led to increasing pressure from parents on school oﬃcials to allow
cellphone communication with their children at school sites. Opting for a more ﬂexible regulatory
solution to accommodate varying concerns and circumstances in diﬀerent communities, the new
law allowed each school district’s board of education to determine its own rules governing student
cellphone use and possession. Figure 1.1 charts the timing of district cellphone policy revision

7

Figure 1.2: Current policies (2017)

This change in legislation was pushed largely by a handful of grassroots eﬀorts (e.g.

among districts for which the date of the ﬁrst revision after 2003 could be obtained.11 Figure 1.2
illustrates that nearly all districts have since passed some manner of local policy on cellphone use.
the
principal of an LAUSD high school announcing in 2001 that his school would no longer enforce the
state law (Matthews, 2002b)). In fact, Senator Liz Figueroa (D-Fremont), who sponsored the new
bill, was initially approached to do so by a class of students at Logan High School in Union City
(Matthews, 2002b). The legislation was also advocated by the La Canada school board (Matthews,
2002b).

By default, most districts almost certainly depended on the language of the 1988 CA Ed Code
in their governance board policies until further revision at the district level. While it is not possible
to conﬁrm with certainty that some districts did not enter into a period free of device rules, district
codes tend to contain or cite the language of relevant state codes. Additionally, Los Angeles
11Shapeﬁles detailing CA school district boundaries were obtained from U.S. Census Bureau

(2017).

8

Uniﬁed, Irvine Uniﬁed, and Corona-Norco Uniﬁed, continued to enforce bans until local level
revisions (Helfand and Hayasaki, 2003). The data furthermore suggests that the new state law
aﬀected little to no immediate change at the local level by itself—support for this is provided later
in Section 1.4. Hence, later district-level policies that both restrict students from using cellphones
at certain times (e.g. instruction time) while permitting use at others (e.g. before the ﬁrst bell, after
the last bell, during lunch, nutrition break, passing periods, etc) in fact produced a less restrictive
environment by recognizing permissible usage times.

While degree of enforcement of the prior state law may certainly have varied, some facts suggest
that it was generally taken seriously. Firstly, the state reform was largely driven by local level actors
who would have had little incentive to oﬃcially challenge a toothless policy. Additionally, 77%
of LAUSD high school principals predicted in a district survey that diﬃculties would arise from
passing a district policy with relaxed restrictions (Helfand and Hayasaki, 2003), indicating a non-
negligible degree of existing control that would be hamstrung by weaker rules.

1.3.2 California Healthy Kids Survey

The California Healthy Kids Survey (CHKS) is a youth risk behavior monitoring system funded by
the California Department of Education (CDE) and managed by the company WestEd. The purpose
of the survey is to provide both state and local level education oﬃcials with insights for creating
safer and more eﬀective learning environments, as well as mitigating youth problems beyond
the classroom (e.g. drunk driving, unsafe sex, violence, and drug abuse). As such, the survey
encompasses a large number of core and supplemental modules designed to collect information on
a broad range of activities, health habits, relationships (e.g. teachers, other students, community
members, etc), attributes of home life, and beliefs and attitudes. While certain elements feature
consistently in the core modules during each iteration (i.e. substance abuse), other content has
evolved over time to monitor current issues (e.g. cyber harassment, gang involvement).

Between 2003 and 2010, the CDE required all districts to administer the survey at least every
two years in order to receive federal funds provided under Title IV of the No Child Left Behind

9

Act (Austin, 2013). As of 2013, the survey remained mandatory for districts receiving funds from
the Tobacco Use Prevention Education (TUPE) program or the Safe and Supportive Schools grant
(Austin, 2013). This requirement entails collecting data from all schools within each district, or else
collecting data from all schools selected in an approved sampling plan (WestEd, n.d.). Resulting
data is meant to be representative at the district level—WestEd provides local administrators
district-level reports, with analyses disaggregated by grade level.12

1.3.3 District Cellphone Regulations

Current and historical district-level cellphone policies were retrieved mostly from district governance
board websites. Key information consists of the date of a district’s ﬁrst code revision pertaining
to student cellphone use following the state law change, as well as the particular time and/or
location based restrictions and allowances for cellphone use. Where the nature of a district’s policy
changed again afterwards, the analysis to follow is based on the conditions laid out in the ﬁrst
policy. While board policies show only current rules along with dates when the document was
edited, it was possible in many cases to use revision dates to search on-line archives of board
meetings for speciﬁc changes made in the past. Naturally, this could only be done with districts
having a current cellphone policy to trace backwards (including policies delegating regulation to
individual school sites), and only if boards archived suﬃciently old information. When on-line
information was insuﬃcient, attempts were made to obtain policy records from district oﬃces and
board archivists. In general, it is not common to retain or furthermore to digitize long-obsolete
policies, and asking district oﬃce staﬀ to recall details from unavailable historical documents proved
largely ineﬀective; due to ubiquitously high turnover, there were few instances of staﬀ members
being able to recall rules from more than a few years in the past. Understandably, few staﬀ were
willing to retrieve non-digitized documents. Apart from being unlikely to report any older policies
due to the above mentioned turnover, districts with no recent policy to trace back were also omitted
12In the case of suﬃcient data, such as districts that survey all students in all schools, school

level reports can also be generated (WestEd, n.d.).

10

due to the likelihood of recalling only the latest rule—possibly reﬂecting some change stemming
from dissatisfaction with a prior rule, and potentially thereby introducing bias.

Of the roughly over 400 public uniﬁed and high school districts active over the period 2002-
2013, policy information was obtained for 295 districts. However, due to the above described
limitations, complete historical information was unavailable for many of these districts. Thus, key
historical policy dates and stipulations were only obtained for 170 public uniﬁed and high school
districts that operated during the period (and are of course necessarily still active, since information
cannot be retrieved from defunct districts).

1.3.4 Sample

The CHKS high school surveys from the 2001-2002 to 2012-2013 school years targeted 9th and 11th
graders, with approximately 15% more 9th graders in the data.13 According to WestEd’s CHKS
website: “It is important that schools collect grade-level data (rather than use a general high-
school sample) because most health-risk behaviors increase or change with age. Understanding
developmental diﬀerences is critical to implementing better programs that target each age group”
(WestEd, n.d.). On the particular grade selection, the company cites the following rationale: “Grade
9 (age 14) is typically the ﬁrst year of senior high school, and is a time when prevalence of AOD
[alcohol or drug] use can increase to substantial levels,” while “grade 11 was selected because
research shows that virtually all students initiating AOD use in secondary school will have done so
by the end of grade 11” (WestEd, n.d.).

The sample consists of repeated cross sections of student level observations with information
for outcomes and controls, including past month use of cocaine/crack, marijuana, inhalants, meth,
alcohol, and cigarettes, and various individual and school-level sociodemographic variables (e.g.
age, gender, race, proportion of school eligible to receive free and reduced price lunches). Analysis
13While the data contain some 10th and 12th grade respondents as well, they are very few in
number and not representative, as their inclusion is an incidental artifact of class based sampling.
According to a WestEd employee, the presence of 10th and 12th grade students in classes with 9th
and 11th grade students is not indicative of remedial/advanced status, and may be due to mixed
grade activities.

11

Table 1.1: Introduction of District Policies

(1)

Students Schools Districts
175216
87930
105806
15372
52942
46768
110460
24579
7794
933
20542

11

648742

(2)

178
134
86
22
38
43
91
22
10
2
26
1
654

(3)

42
21
21
6
9
16
23
13
3
2
10
1
168

2003
2004
2005
2006
2007
2008
2009
2010
2011
2012
2013
2014
Total

Sample students and schools are in districts
for which I could obtain policy dates, and
which had information for all outcomes and
controls.

is ultimately performed on 346,195 ninth graders and 302,547 eleventh graders from 654 schools
across 168 districts.

Table 1.1 breaks down school districts, schools, and students by year in which the district
board of education ﬁrst revised its governance code concerning cellphones. While some bunching
is evident immediately after the state repeal, considerable variation occurs in timing of the ﬁrst
district policy.

Tables 1.2 and 1.3 show within-sample comparisons of student and school characteristics before
and after the ﬁrst local level code revision. Drug use generally appears higher in the post period,
and the analyses that follow will investigate these changes.

School and student summary statistics from the 2001-2002 school year are presented in Table 1.4
and Table 1.5. From Table 1.4, sample schools have generally smaller enrollment, a larger average
proportion of Hispanic students, and a smaller average proportion of white students. Diﬀerences in
school level characteristics are statistically signiﬁcant at the 5 percent level in enrollment, proportion

12

Cocaine/crack

Marijuana

Inhalants

Meth

Alcohol

Cigarettes

Age 14 or younger

Age 15 or older

Girl

Asian

Black/AA

White

Other

(1)

0.018
(0.133)
0.068
(0.252)
0.026
(0.159)
0.017
(0.131)
0.124
(0.330)
0.049
(0.217)
0.728
(0.445)
0.272
(0.445)
0.521
(0.500)
0.235
(0.424)
0.099
(0.298)
0.579
(0.494)
0.087
(0.282)

(3)

(2)-(1)
0.012∗∗∗
(0.001)
0.047∗∗∗
(0.001)
0.017∗∗∗
(0.001)
0.009∗∗∗
(0.001)
0.056∗∗∗
(0.002)
0.024∗∗∗
(0.001)
-0.065∗∗∗
(0.002)
0.065∗∗∗
(0.002)
-0.006∗∗∗
(0.002)
-0.023∗∗∗
(0.002)
-0.008∗∗∗
(0.001)
-0.097∗∗∗
(0.002)
0.128∗∗∗
(0.002)

0.030
(0.169)
0.115
(0.319)
0.043
(0.202)
0.026
(0.160)
0.180
(0.384)
0.073
(0.260)
0.663
(0.473)
0.337
(0.473)
0.515
(0.500)
0.212
(0.409)
0.091
(0.287)
0.482
(0.500)
0.215
(0.411)

(4)

0.023
(0.150)
0.127
(0.333)
0.024
(0.152)
0.020
(0.139)
0.222
(0.416)
0.096
(0.295)
0.004
(0.060)
0.996
(0.060)
0.519
(0.500)
0.236
(0.424)
0.089
(0.285)
0.594
(0.491)
0.081
(0.273)

63263

(6)

(5)-(4)
0.010∗∗∗
(0.001)
0.050∗∗∗
(0.002)
0.013∗∗∗
(0.001)
0.007∗∗∗
(0.001)
0.060∗∗∗
(0.002)
0.018∗∗∗
(0.001)
-0.000
(0.000)
0.000
(0.000)
-0.003
(0.002)
-0.019∗∗∗
(0.002)
-0.005∗∗∗
(0.001)
-0.093∗∗∗
(0.002)
0.117∗∗∗
(0.002)

0.033
(0.179)
0.177
(0.382)
0.037
(0.189)
0.027
(0.163)
0.283
(0.450)
0.114
(0.318)
0.003
(0.058)
0.997
(0.058)
0.516
(0.500)
0.216
(0.412)
0.084
(0.278)
0.501
(0.500)
0.198
(0.399)

Table 1.2: Student Summary Statistics: Pre and Post District Policy Revision

9th grade

(2)

11th grade

(5)

Pre-period Post-period

Pre-period Post-period

Obs
Sample students are in districts for which I could obtain policy dates, and who had information for all
outcomes and controls. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

269061

346195

77134

239284

302457

13

Table 1.3: School Summary Statistics: Pre and Post District Policy Revision

Total enrollment

Grade 9 enrollment

Grade 11 enrollment

Proportion Hispanic

Proportion Black

Proportion White

Proportion FRPL eligible

Proportion ELL

(1)
Pre
1897
(971)
548
(314)
444
(235)
0.404
(0.248)
0.079
(0.108)
0.358
(0.253)
0.367
(0.234)
0.159
(0.125)

(2)
Post
1920
(957)
535
(293)
460
(235)
0.443
(0.261)
0.083
(0.118)
0.315
(0.245)
0.442
(0.265)
0.151
(0.119)

Schools

420

592

Sample schools are in districts for which I could
obtain policy dates, and which had information for
all outcomes and controls.

Hispanic, and proportion White, but not in proportion Black, percent FRPL eligible, and percent
English Language Learners (ELL).

Student summary statistics compare sample 9th and 11th graders to non-sample 9th and 11th
graders. For both 9th and 11th graders, diﬀerences are statistically signiﬁcant at the 5 percent
level for all drug use outcomes, the age 14 dummy indicators, and all race dummies except those
indicating Black/ African American (with sampled students being more likely to report being
Asian). While sampled schools do not appear very diﬀerent from other schools in proportion
of FRPL eligible and ELL students, observable drug use behaviors appear lower among sampled
students than in the population at large.

14

Table 1.4: Year 2002 School Summary Statistics

Total enrollment

Grade 9 enrollment

Grade 11 enrollment

Proportion Hispanic

Proportion Black

Proportion White

Proportion FRPL elig.

Proportion ELL

(1)

(2)

Sample Non-Sample
2401
(920)
159
713
(339)
159
551
(215)
159
0.374
(0.259)

1898
(952)
468
549
(317)
468
442
(221)
468
0.327
(0.246)

159
0.086
(0.130)

159
0.373
(0.241)

159
0.325
(0.233)

159
0.172
(0.135)

159

468
0.070
(0.105)

468
0.458
(0.271)

468
0.290
(0.230)

468
0.150
(0.131)

444

(3)
(1)-(2)
503∗∗∗
(87)
627
164∗∗∗
(30)
627
110∗∗∗
(20)
627
0.047∗∗
(0.023)

627

627
0.016
(0.010)
-0.085∗∗∗
(0.024)
627
0.035∗
(0.021)
627
0.022∗
(0.012)

603

Sample schools are in districts for which I could obtain policy dates,
and which had information for all outcomes and controls. ∗ p < 0.10,
∗∗ p < 0.05, ∗∗∗ p < 0.01.

15

Table 1.5: Year 2002 Student Summary Statistics

Cocaine/crack

Marijuana

Inhalants

Meth

Alcohol

Cigarettes

Age 14 or younger

Age 15 or older

Girl

Asian

Black/AA

White

Other

(1)

9th grade

(2)

Sample Non-Sample
0.010
(0.099)
13900
0.038
(0.191)
13900
0.013
(0.112)
13900
0.010
(0.101)
13900
0.069
(0.254)
13900
0.031
(0.172)
13900
0.773
(0.419)
13900
0.227
(0.419)
13900
0.532
(0.499)
13900
0.263
(0.441)
13900
0.080
(0.271)
13900
0.610
(0.488)
13900
0.046
(0.211)
13900

0.014
(0.119)
70659
0.085
(0.279)
66923
0.021
(0.143)
69603
0.015
(0.123)
70647
0.131
(0.337)
57481
0.057
(0.231)
67705
0.748
(0.434)
72518
0.252
(0.434)
72518
0.535
(0.499)
72222
0.165
(0.371)
42534
0.081
(0.273)
42534
0.697
(0.460)
42534
0.057
(0.232)
42534

(3)

(1)-(2)
-0.004∗∗∗
(0.001)
84559
-0.047∗∗∗
(0.002)
80823
-0.008∗∗∗
(0.001)
83503
-0.005∗∗∗
(0.001)
84547
-0.061∗∗∗
(0.003)
71381
-0.026∗∗∗
(0.002)
81605
0.025∗∗∗
(0.004)
86418
-0.025∗∗∗
(0.004)
86418
-0.003
(0.005)
86122
0.098∗∗∗
(0.004)
56434
-0.001
(0.003)
56434
-0.087∗∗∗
(0.005)
56434
-0.010∗∗∗
(0.002)
56434

(4)

11th grade

(5)

Sample Non-Sample
0.013
(0.113)
11516
0.078
(0.269)
11516
0.012
(0.110)
11516
0.014
(0.117)
11516
0.143
(0.350)
11516
0.075
(0.263)
11516
0.001
(0.037)
11516
0.999
(0.037)
11516
0.530
(0.499)
11516
0.260
(0.439)
11516
0.077
(0.267)
11516
0.622
(0.485)
11516
0.041
(0.198)
11516

0.016
(0.127)
59162
0.139
(0.346)
54553
0.016
(0.124)
58905
0.018
(0.133)
59241
0.244
(0.430)
44700
0.107
(0.309)
55760
0.003
(0.051)
60673
0.997
(0.051)
60673
0.540
(0.498)
60361
0.155
(0.362)
37959
0.074
(0.262)
37959
0.720
(0.449)
37959
0.051
(0.221)
37959

(6)

(4)-(5)
-0.004∗∗∗
(0.001)
70678
-0.061∗∗∗
(0.003)
66069
-0.004∗∗∗
(0.001)
70421
-0.004∗∗∗
(0.001)
70757
-0.101∗∗∗
(0.004)
56216
-0.032∗∗∗
(0.003)
67276
-0.001∗∗
(0.000)
72189
0.001∗∗
(0.000)
72189
-0.009∗
(0.005)
71877
0.105∗∗∗
(0.004)
49475
0.003
(0.003)
49475
-0.098∗∗∗
(0.005)
49475
-0.010∗∗∗
(0.002)
49475

Sample students are in districts for which I could obtain policy dates, and who had information for all
outcomes and controls. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

16

1.4 Analysis and Results

1.4.1 Drug Use Before and After District Policy Revision

This study exploits district level variation in the timing of policy changes in order to estimate the
eﬀect of relaxing campus cellphone rules on student substance abuse—separately from coinciding
statewide factors that might confound analysis in a case study setting. First, I examine staggered
comparisons of drug outcomes before versus after the ﬁrst revision of applicable district code
following the state repeal. By using multiple instances of local level policy changes in diﬀerent
calendar years, I am able to separately attribute part of the observed changes in drug outcomes to
each district’s post-policy period (policy eﬀects) versus the corresponding calendar years (possibly
reﬂecting statewide trends).14 To this end, I estimate the following model:

Yisr = φ1Post district revisionsr + γXisr + αs + θr + εisr

(1.1)

In the above equation, Yisr is an indicator for past 30 day use of a given drug (the main outcomes
are cocaine/crack, marijuana, inhalants, methamphetamines, alcohol, and cigarettes) by student i
in school s during academic calendar year r. “Post district revision” indicates the years after the
district to which school s belongs revised its cellphone policy. Xisr is a set of individual and
school-level controls,15 and αs and θr are school and year ﬁxed eﬀects, respectively.

Table 1.6 presents the results of estimating Equation 1.1 on the samples of 9th and 11th graders,
with the outcomes of past month use of cocaine, marijuana, inhalants, methamphetamine, alcohol,
and cigarettes, as well as the composite drug use indicator. For 9th graders, the period following
district code revision is positively and statistically signiﬁcantly correlated at conventional levels
with all drug use measures except for cigarettes. Among the non-cigarette speciﬁcations (1-6), the
14This analysis will use the same time frame, from ﬁve years before district revision to eight

years after, as the disaggregated event study speciﬁcation to follow (below in Subsection 1.4.2).

15Controls include age, sex, race, and school-level enrollment, racial demographics, proportion
of student body eligible for Free and Reduced Price Meals, proportion of student body that are
English Language Learners.

17

Table 1.6: Drug Use Pre vs. Post District Policy Revision

(2)

(3)

(1)

Any drugs Coc./crack Marijuana
0.0123∗∗∗
0.014∗∗∗
(0.003)
(0.004)

0.004∗∗∗
(0.001)

(4)

(5)
Inhalants Meth
0.002∗
0.004∗∗
(0.001)
(0.002)

(6)

(7)

Alcohol Cigarettes
0.010∗∗
(0.004)

0.003
(0.002)

0.151
346195
0.033∗∗∗
(0.004)

0.260
302547

Yes
Yes
Yes

0.018
346195
0.004∗∗∗
(0.001)

0.023
302547

Yes
Yes
Yes

0.068
346195
0.026∗∗∗
(0.004)

0.127
302547

Yes
Yes
Yes

0.026
346195

0.002
(0.002)

0.024
302547

Yes
Yes
Yes

0.017
346195
0.002∗
(0.001)

0.020
302547

Yes
Yes
Yes

0.124
346195
0.024∗∗∗
(0.004)

0.222
302547

Yes
Yes
Yes

0.049
346195

0.002
(0.003)

0.096
302547

Yes
Yes
Yes

Grade 9
Post

Pre-period
mean
Obs
Grade 11
Post

Pre-period
mean
Obs
School FE
Year FE
Controls

Outcomes are indicators for any use of the substance in past 30 days. Controls include age, gender, race,
school level enrollment, demographic composition, FRPL, and proportion English learners. Standard
errors in parentheses, clustered at the district level. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

coeﬃcient on Post is signiﬁcant at least at the ﬁve percent level in all except methamphetamine, in
which it is nonetheless signiﬁcant at the ten percent level. Hence, 9th graders are 1.4 percentage
points more likely in the post period to report having used any substance in the past 30 days. At
a glance, this appears to be driven by marijuana and alcohol. For 9th graders, the likelihood of
reporting past month marijuana and alcohol use rises in the post period by 1.2 and 1 percentage
points, respectively. These are relatively larger changes than those exhibited in cocaine/crack,
inhalant, and methamphetamine use (which increase in the post period by 0.2 - 0.4 percentage
points), and they are important in magnitude considering that only 6.8% and 12.4% of 9th graders
in the pre period report past month use of marijuana and alcohol, respectively.

For 11th graders, the period following district code revision is positively and statistically
signiﬁcantly correlated at conventional levels with all drug use measures except for inhalants and
cigarettes. Among the non-inhalant and non-cigarette speciﬁcations, the coeﬃcient on Post is

18

signiﬁcant at the one percent level for all except methamphetamine, in which it is again signiﬁcant
at the ten percent level. Once again, the eﬀect on the composite measure (“Any drugs”) seems
to be largely driven by marijuana and alcohol. Among 11th graders, the likelihood of reporting
past month marijuana and alcohol use rises in the post period by 2.6 and 2.4 percentage points,
respectively. These are again relatively important changes if compared to pre period reported use
(12.7% and 22.2% of 11th grader reported marijuana and alcohol use in the period before the ﬁrst
relevant district code revision).

While marijuana and alcohol are by far more prevalent among both grade levels in the data than
cocaine/crack, inhalants, and methamphetamine, the incidence of cigarette smoking is also fairly
close to that of marijuana use. Moreover, the much larger incidence of cigarette smoking among
11th compared to 9th graders (9.6% vs. 4.9% in the pre period) parallels the diﬀerential use of
marijuana and alcohol between the grades—contrast this with the other substances, for which there
is a much less evident or even reversed diﬀerence. Though it may thus seem that cigarettes are
in some manner equally popular or socially acceptable as marijuana and alcohol, the lack of any
apparent impact on cigarette smoking should be expected under the scenario in which cellphones
facilitate student drug use by lowering the eﬀort and risk of discovery associated with obtaining
controlled substances. In contrast with alcohol, which cannot legally be possessed by any person of
high school age, and marijuana, which is a controlled substance even for adults at any age, cigarettes
can be legally be bought and possessed by a large fraction of high schoolers. In that regard, private
communication by cellphone likely does not contribute much or at all to the ease of ﬁnding and
communicating with a potential supplier of cigarettes.

1.4.1.1 Multiple Outcomes

When testing multiple independent outcomes, inference is often adjusted by the Sidak or Bonferroni
procedure to account for the higher likelihood of statistically signiﬁcant results arising by chance.
However, in the case of correlated outcomes, both of these result in highly conservative inference
(Conneely and Boehnke, 2007) (e.g. consider the hypothetical case in which multiple outcomes

19

are perfectly correlated—eﬀectively a single test requiring no adjustment). The drug use outcomes
in the sample analyzed here are indeed highly correlated. For example, the correlation between
past month use of cocaine and past month use of methamphetamines is 0.79. Following Aker et al.
(2012), I employ the Bonferroni correction for multiple tests, adapted to account for inter-variable
correlation.16 As the 9th and 11th grade analyses involve separate, non-overlapping samples, I
consider the set of (individual) drug use measures for each grade to be a “family” of tests. Like
Aker et al. (2012) and Gibson et al. (2011), I base testing on the ten percent signiﬁcance level.
For 9th graders, based on an average inter-outcome correlation of 0.47, the Bonferroni adjusted
critical value is 0.040. All previous impacts remain signiﬁcant at this level except for that on use
of inhalants (which joins use of cigarettes in exhibiting no signiﬁcant impact). For 11th graders,
based on an inter-outcome correlation of 0.42, the Bonferroni adjusted critical value is 0.037. All
impacts remain signiﬁcant at this level except for that on use of methamphetamine (the change in
use of inhalants was not statistically signiﬁcant to begin with).

1.4.2 Endogenous Policy Timing and Event Studies

In order to check for possibly endogenous timing of local policy changes (which may manifest as
trends in drug outcomes that begin prior to policy changes), I also disaggregate the comparison
periods into a year-by-year event study centered on the event of ﬁrst revising district student
cellphone rules after the state repeal.

8

t=−5

Yisr =

βt1 {Esr = t} + γXisr + αs + θr + εisr,

t (cid:44) −1

(1.2)

Event time, here represented by Esr, refers to time as counted relative to the ﬁrst year a student
cellphone policy is introduced. Hence, event time during the year of policy introduction is equal to
zero, while event time during the year prior is equal to negative one, and event time during the year
after is equal to positive one. Formally, Esr = r− Rs, where Rs is the year that school s’s district ﬁrst
changed its governance code concerning student cellphone rules in response to the new state law.

16The procedure is described in more detail by Sankoh et al. (1997).

20

The event window inspected spans from ﬁve periods prior to the event to eight periods following
(the results of the main analysis that follow are robust to using other, shorter event windows, e.g.
t = −2 to t = 2, not shown). I aim to estimate the βt’s (using t = −1 as the reference period)
while accounting for Xisr, the set of observable individual characteristics and time-varying school
characteristics as controls. As before, αs and θr are school and year ﬁxed eﬀects, respectively.

District board policies may be changed both during the summer and also throughout the school
year, which typically spans from late August or early September to May or June. CHKS survey
administration has no set date, but must not start until at least 30 days into the school year, and
must be completed before the end of June. I code school years in which the relevant policy change
was made before April as being in event time zero (t = 0), and school years in which the change
was made in April or later as being in event time one. Thus, some school years that count as t = 0
may only have had the new policy in place for two or three months before survey administration.
Not many policy changes fell around the chosen cutoﬀ, and the main results that follow are robust
to using earlier cutoﬀs.

Figures 1.3 through 1.9 show the results of estimating Equation 1.2 on the samples of 9th and
11th graders (represented in each ﬁgure’s upper and lower panels, respectively), using the outcomes
of past month cocaine, marijuana, inhalant, methamphetamine, alcohol, and cigarette use, as well as
the composite drug use indicator. Additionally, pooled results for both grades together are provided
in Figure A.1 in the Appendix. For 9th graders, although many coeﬃcients on the event times from
t = −5 to t = −3 are negative, only one pre period in the composite and alcohol speciﬁcations is
signiﬁcantly so at the ﬁve percent level relative to the reference period t = −1. Visually, it appears
that a pre trend in the composite measure is driven by the alcohol speciﬁcation (Figures 1.3 & 1.8),
as none of the other graphs exhibit a similar pattern. This is addressed in Section 1.4.3. Otherwise,
the pre periods for 9th graders in general do not diﬀer signiﬁcantly in relation to t = −1. On the
other hand, all periods from t = 0 onwards are positively and signiﬁcantly correlated with marijuana
use (Figure 1.5). The ﬁrst year in which a district revises its own cellphone rules is correlated with
a 1.3 percentage point increase in the likelihood of smoking marijuana, an eﬀect which seems to

21

rise before leveling oﬀ at around 2 percentage points from t = 4 onwards.

While eﬀects are initially less clear with respect to consumption of alcohol, the periods from
t = 2 onwards are positively associated with alcohol use (although the coeﬃcients on t = 6 and
t = 7 are not statistically signiﬁcant) (Figure 1.8). Eﬀects over this period lie between 1.3 to
2.4 percentage points greater likelihood of past month alcohol consumption compared to t = −1.
As may be expected from the previous analysis, the graphs representing the use of cocaine/crack,
inhalants, and methamphetamine speciﬁcations are visually indicative of an increase in 9th grade
drug use brought on at t = 0, although the individual period coeﬃcients tend to be very and mostly
insigniﬁcant (Figures 1.4, 1.6, 1.7). Nothing suggests any particular signiﬁcance of the policy event
for incidence of cigarette smoking among 9th graders.

Results from the analysis of 11th graders diﬀer most noticeably from the 9th grade analysis in
that a visually apparent upward trend in marijuana use during periods t = −5 to t = −1 seems to
precede the policy event (Figure 1.5). A subtler trend possibly also precedes alcohol consumption
(Figure 1.8). As might be expected from the analysis in Section 1.4.1, coeﬃcients on the post
periods in the marijuana and alcohol speciﬁcations are roughly 2-3 times as large as for 9th graders.
For instance, t = 2, the second year after the policy event is associated with a 3.2 percentage point
increase in the likelihood of 11th graders’ past month marijuana use compared to t = −1, while
the eﬀect among 9th graders is 1.4 percentage points. The same time period correlates with a 3
percentage point increase in 11th grade alcohol consumption and only a 1.3 percentage increase
in 9th grade alcohol consumption (Figure 1.8). Otherwise, the analyses concerning cocaine and
methamphetamines produces results fairly close to those from the 9th grade analysis, while the
graph of the inhalants speciﬁcation, like in the Section 1.4.1 model, does not suggest any particular
impact of the policy event.
In particular, the 11th grade methamphetamine graph (Figure 1.7),
appears to more clearly suggest an upward shift in consumption attributable to the policy event.
Once again, the cigarettes speciﬁcation (Figure 1.9) seems to concur with the previous analysis in
revealing no appreciable impact of the policy event on the incidence of cigarette smoking among
11th graders.

22

Figure 1.3: Composite: Any substance in past 30 days

9th graders

11th graders

23

−.013−.016−.018−.0020.011.0068.016.018.026.029.028.023.032−.04−.020.02.04.06Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599−.03−.031−.019−.00320.022.035.037.05.065.067.077.078.091−.050.05.1.15Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 302547Schools: 633Figure 1.4: Used cocaine/crack in past 30 days

9th graders

11th graders

24

−.00044−.00071.0017.00150.0046.0063.0049.000073.0036.0077.008.0046.0025−.010.01.02Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599.0014−.0029.0019−.0020.0021.0076.00088.0038.001.0086.0068.0074.003−.010.01.02Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 302547Schools: 633Figure 1.5: Used marijuana in past 30 days

9th graders

11th graders

25

−.0052−.0043−.005.00250.013.0087.014.017.023.017.023.016.02−.020.02.04Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599−.031−.02−.02−.00380.018.027.032.041.047.054.063.064.073−.050.05.1Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 302547Schools: 633Figure 1.6: Used inhalants in past 30 days

9th graders

11th graders

26

−.0016.0011−.0015.00140.0049.0036.006.0011.0066.0038.0076.000014.0049−.01−.0050.005.01.015Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599.0016−.0038.0018−.00130−.00044.0035.0011.0029.0013.0026.0011.0053.0033−.01−.0050.005.01.015Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 302547Schools: 633Figure 1.7: Used meth in past 30 days

9th graders

11th graders

27

−.0014−.002−.0013.000410.0018.0045.0037−.00048.0019.0036.0065.0023.0037−.01−.0050.005.01Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599−.00043−.0041.00063.000610.00097.0042.0034.0032.0024.0048.0052.0055.0056−.01−.0050.005.01.015Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 302547Schools: 633Figure 1.8: Used alcohol in past 30 days

9th graders

11th graders

28

−.012−.016−.015−.000690.0075.0015.013.013.017.017.014.014.024−.04−.020.02.04Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599−.021−.024−.013−.00330.013.027.03.037.047.047.056.059.067−.050.05.1Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 302547Schools: 633Figure 1.9: Used cigarettes in past 30 days

9th graders

11th graders

29

.0017−.0014.0013−.00120.0019.0017.0021−.0021.0042−.0064−.0051−.0074−.0026−.02−.010.01.02Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599−.00092−.0025−.0026−.00890−.0033.0029−.0032−.0042−.0065−.0088−.0094−.0075−.0092−.03−.02−.010.01Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 302547Schools: 633While it is not possible to determine whether in practice each and every school district by
default continued enforcing the campus cellphone ban after the state law change (as opposed to
allowing unregulated cellphone use by students), the data suggest this was generally the case. The
top panels of Figures A.3 through A.9 show the transition from 2002 (a year prior to the state
repeal) through 2005 for 9th graders in school districts that did not enact policy changes pertaining
to campus cellphones until at least 2006. Drug behaviors do not appear to change as students enter
an “interim” period between the state repeal and a response in local policy.17 The bottom panels
of these ﬁgures reproduce the event study graphs for this subset of districts, showing the change
in drug use when going from the “interim” period into a most likely less restrictive environment
with respect to campus cellphone use.18 Positive and signiﬁcant impacts of the change in cellphone
policy emerge within a year for cocaine, marijuana, methamphetamines, and inhalants, though
coeﬃcients diﬀer somewhat with the smaller and more select sample (e.g. the eﬀect on marijuana
peaks at 4.8 percentage points in t = 6 instead of 2.3).

1.4.3

Impacts As Shifts and Trend Breaks

In order to account for possible pre trends in the outcome measures leading up to district code
revision (as well as possible changes in trends resulting from code revision), I also estimate the
following model:

Yisr = φ1Post district revisionsr + φ2Esr + φ3Post district revision × Esr

+γXisr + αs + θr + εisr

(1.3)

In the above equation, φ1 captures the eﬀect of the district policy change in terms of a level
shift in the outcome measure, while φ2 accounts for any linear trend in substance use prior to
17This is robust to using the subset of students in districts not enacting a policy until 2004, as

well as 2005, and also for 11th graders, not shown.

18Note that over the study period 2002-2013, districts that adopted policies in 2006 and onwards

could not have a period t = 8 in the event window.

30

code revision. The parameter φ3 captures any linear departure from that outcome trend in the post
period, which this framework will attribute to the district policy event.

Table 1.7 presents the results of estimating Equation 1.3 on the 9th and 11th grade samples
for all substance outcomes. Results using the pooled sample are also shown in Appendix Table
A.1. As mentioned in the previous section, preexisting trends in alcohol consumption among 9th
graders, as well as marijuana and alcohol consumption among 11th graders, appear to lead up to
the district policy event. Additionally, the eﬀect on marijuana use among 9th graders appears more
positive over time, while any impact on cigarette smoking among 11th graders (Figure 1.9 bottom)
appears almost to become negative over time.

Among 9th graders, estimating the model with linear pre and post trends leaves the coeﬃcient
on “Post” signiﬁcant only in the marijuana speciﬁcation, suggests a modest pre trend (“Evt Time”)
in alcohol, and reveals no other trends or level shifts. Results support the existence of signiﬁcant
upward trends in marijuana and alcohol consumption among 11th graders preceding the policy event
(“Evt Time” in columns 3 & 6). After accounting for trends, a signiﬁcant upward shift in 11th grade
cocaine/crack, marijuana, and alcohol consumption is associated with the period following district
governance code revision. All eﬀects except for the level shift in 11th grade cocaine use remain
signiﬁcant after performing the multiple testing correction discussed above. Based on inspection
of the prior event studies, estimation of linear trends is likely only appropriate in the speciﬁcations
involving alcohol and marijuana among 11th graders, and perhaps only for alcohol among 9th
graders. On one hand, it appears that the popularity of alcohol and marijuana may have risen in
tandem with gradual environmental changes endogenous to district code revision. However, use of
both substances additionally exhibits a level shift upon the policy change. Additionally, analyses
of the other drug outcomes qualitatively suggest upward level shifts without mirroring the pattern
in preceding trends.

In Appendix Tables A.2 and A.3, I further control for school-speciﬁc and district-speciﬁc time
trends, respectively. With the additional sets of covariates, the estimated level shift in 9th grade
marijuana use is no longer statistically signiﬁcant, though still positive. The estimated level shift

31

Table 1.7: Trend Break Speciﬁcation

(2)

(3)

(1)

Any drugs Coc./crack Marijuana
0.009∗∗∗
(0.003)

0.006
(0.005)

0.003
(0.002)

-0.001
(0.002)
0.004∗∗
(0.002)

346195
0.016∗∗∗
(0.005)

-0.000
(0.002)
0.009∗∗∗
(0.002)

302547

Yes
Yes
Yes

-0.000
(0.001)

0.000
(0.001)

346195
0.005∗
(0.002)

0.001
(0.001)

-0.000
(0.001)

302547

Yes
Yes
Yes

-0.000
(0.001)

0.002
(0.001)

346195
0.011∗∗∗
(0.004)

-0.001
(0.002)
0.008∗∗∗
(0.002)

302547

Yes
Yes
Yes

(4)

(5)
Inhalants Meth

0.003
(0.002)

-0.001
(0.001)

0.000
(0.001)

0.001
(0.002)

-0.000
(0.001)

0.001
(0.001)

346195

346195

0.002
(0.002)

0.000
(0.001)

-0.000
(0.001)

302547

Yes
Yes
Yes

0.002
(0.002)

0.000
(0.001)

0.000
(0.001)

302547

Yes
Yes
Yes

(6)

(7)

Alcohol Cigarettes

0.002
(0.005)

-0.002
(0.002)
0.004∗∗
(0.002)

346195
0.012∗∗
(0.005)

-0.000
(0.002)
0.006∗∗∗
(0.002)

302547

Yes
Yes
Yes

0.003
(0.003)

-0.001
(0.001)

-0.000
(0.001)

346195

0.002
(0.004)

-0.002
(0.001)

0.000
(0.001)

302547

Yes
Yes
Yes

Grade 9
Post

Post x
Evt Time

Evt Time

Obs
Grade 11
Post

Post x
Evt Time

Evt Time

Obs
School FE
Year FE
Controls

Outcomes are indicators for any use of the substance in past 30 days. Controls include age, gender, race,
school level enrollment, demographic composition, FRPL, and proportion English learners. Standard
errors in parentheses, clustered at the district level. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

in 11th grade marijuana use remains positive and statistically signiﬁcant when allowing for either
school-speciﬁc and district-speciﬁc trends.

1.4.4 Academic Performance

The vast majority of relevant literature pertaining speciﬁcally to mobile phone use in the learning
environment (e.g. Beland and Murphy (2016)) has shown cellphones to have a negative or
ambiguous impact on student academic performance. Due to the great interest in this particular

32

category of outcomes, I examine the impact of campus cellphones on self reported academic
performance, reﬂected as having received mostly scores of C or worse over the course of the school
year (a C in many settings indicates minimum proﬁciency required to proceed into a more advanced
course in a sequence). No statistically signiﬁcant eﬀects are found for either 9th or 11th graders
from estimating Equation 1.1 using this outcome. Figure A.11 in the Appendix presents the results
from estimating Equation 1.2 with this outcome.

1.5 Mechanisms

If we assume that prospective buyers, in order to purchase drugs, must establish contact and
negotiate with a relatively small number sellers, then removing the need to meet in person might
increase trades by reducing the cost of building the requisite relationships. Firstly, cellphones may
enable sellers to interact with more buyers at once than would otherwise be possible, as well as
grant interested buyers more convenient access to sellers, who may otherwise be out of their way.
Based on accounts of law enforcement involved in drug purchasing operations, drug users beneﬁt
from convenience, expedience, and—to an extent—safety from detection, while among sellers
“cellphones and word of mouth to sell the product tends to be common practice” (Smith, 2014).

Particularly, both the real and subjective risk involved in trading illicit drugs may be reduced
by the ability to communicate by text message before physically meeting. In addition to the need
for buyers and sellers to establish mutual trust, both parties might be wary of drawing unnecessary
attention during lengthy negotiations in public.

That the analyses in this study generally reveal no eﬀects of a new district cellphone policy on
student cigarette smoking may thus be considered consistent with both the risk and eﬀort aspects
of the cost reduction scenario described above. Since cigarettes may be legally possessed and
purchased by a large fraction of the student body (anyone over the age of eighteen), baseline
access to potential suppliers may very likely be great enough that cellphones oﬀer little in the way
of additional convenience. Moreover, the subjective risk or social stigma associated with using
cigarettes might be lower than that associated with strictly illegal items. If being discovered while

33

purchasing cigarettes incurs a relatively low cost, then a reduction in the risk of discovery might be
less likely to pivotally inﬂuence the decision to smoke.

With regard to campus cellphone use in particular, the school environment entails a high density
of peers and replaces the relatively personal supervision of parents and other household members
with that of staﬀ who are tasked with oversight of relatively larger populations.19 Furthermore,
heterogeneous impacts on drug outcomes based on amount of time during the school day when
phone use is permitted provides supporting evidence that changes in drug consumption are in fact
linked to ease of campus cellphone communication.20 For this purpose, policies are categorized
as follows: 1. those permitting use before ﬁrst bell and after last bell (thus oﬃcially allowing for
device possession on campus), and 2.
those further permitting use during the school day, such
as during lunch period, nutrition break, passing periods, or in class for instructional purposes (in
addition to before and after school).

Table 1.8 presents the coeﬃcients on “Post” from estimating Equation 1.3 using separate samples
based on time of day when students may use their phones.
If it is the case that unsupervised,
private communication between students facilitates drug trades, then the samples of students in
districts allowing the use of phones during lunch, nutrition breaks, and passing periods, should see
larger/more signiﬁcant impacts on substance abuse than students in districts only permitting use
before and after the school day (e.g. 9th grade use of cocaine/crack, marijuana, and alcohol).

Among 9th graders, this appears to be somewhat true; in particular, students subject to more
lenient policies seem to drive the focal marijuana result. However, this pattern does not hold among
11th graders. Overall, few diﬀerences are large or statistically signiﬁcant between students under
19A nationally representative U.S. study conducted by Wolfe et al. (2016) ﬁnds that school
cellphone restrictions eﬀectively limit the incidence of sexually explicit text messaging between
adolescents, while parental eﬀorts speciﬁcally targeting inappropriate phone use prove largely
irrelevant. The authors posit that certain risk behaviors are generally not attempted outside of
school due to relatively more intense household supervision of adolescents’ activities.

20In line with the intent of the state law change, which was to allow for policies appropriate for
diﬀerent local circumstances and environments, district policies regulating cellphone use vary not
only in time of day permitted, but also in fairly speciﬁc stipulations (e.g. prohibition against the
wearing of headphones).

34

Table 1.8: Heterogeneity: Time of Day When Cellphone Use is Allowed

(2)

(3)

Any drugs Coc./crack Marijuana

(4)

(5)
Inhalants Meth

(6)

(7)

Alcohol Cigarettes

(1)

-0.006
(0.009)
117293

0.008
(0.006)
228902

0.09

0.020∗∗
(0.009)
104090

0.010
(0.007)
198457

0.507
Yes
Yes
Yes

Grade 9

Before/aft.
hours ONLY

School day
ALSO

Grade 11

Before/aft
hours ONLY

School day
ALSO

School FE
Year FE
Controls

-0.001
(0.005)
117293
0.010∗∗
(0.004)
228902

0.001
(0.002)
117293

0.004
(0.003)
117293

0.001
(0.003)
117293

-0.005
(0.009)
117293

0.004
(0.003)
228902

0.003
(0.006)
228902
P-values for test that coeﬃcients equal across policy type
0.324

0.002
(0.002)
228902

0.002
(0.003)
228902

0.314

0.762

0.622

0.117

0.004
(0.003)
104090

0.008
(0.007)
104090

0.008∗∗
(0.003)
104090

0.003
(0.003)
104090

0.019∗∗
(0.009)
104090

0.004
(0.003)
198457

-0.001
(0.003)
198457

0.007
(0.005)
198457

0.001
(0.002)
198457

0.005
(0.007)
198457
P-values for test that coeﬃcients equal across policy type
0.477
Yes
Yes
Yes

0.144
Yes
Yes
Yes

0.429
Yes
Yes
Yes

0.019
Yes
Yes
Yes

0.27
Yes
Yes
Yes

0.002
(0.004)
117293

0.003
(0.003)
228902

0.818

0.006
(0.006)
104090

-0.001
(0.005)
198457

0.145
Yes
Yes
Yes

Outcomes are indicators for any use of the substance in past 30 days. Each cell shows the coeﬃcient on
“Post” from estimating the trend break regression speciﬁed in Equation 1.3, using only the sample speciﬁed
in the row title. Controls include age, gender, race, school level enrollment, demographic composition,
FRPL, and proportion English learners. Standard errors in parentheses, clustered at the district level. ∗
p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

35

the diﬀerent policy categories, and it is diﬃcult to tell whether and how additional permitted usage
time between/during classes aﬀects student behavior.

1.6 Robustness to Concurrent Changes in Controls

While control variables representing various aspects of demographic variation are accounted
for in all estimations presented, changes in the composition of either students sampled or the
actual population enrolled in the public school system may take place concurrently with broader,
unobserved changes that could be correlated with both student drug use and the school policy
environment. Hence, if policies were altered to accommodate a changing body of students, this
might introduce a positive or negative bias into the estimation of the impacts of the policy change,
depending on whether or not these changes tend to result systematically in a student body that is
more or less inclined to use drugs.

From estimating Equation 1.1 using each control as an outcome to be regressed on the others,
nearly all controls apart from the enrollment variables, proportion of student body that is Hispanic,
and age are statistically signiﬁcantly related to the post period. However, in period-by-period
event studies using the controls as outcomes, these changes over time occur as gradual trends with
no apparent connection to the policy event of interest (not shown). Estimating the trend break
speciﬁcation (Equation 1.3) conﬁrms this to be the case, except with respect to a level decrease in
girl respondents and a level decrease in school wide proportion of Black students, for which the event
study graphs are presented for the 9th grade sample in Figure A.10. Note that the heterogeneity
analysis that follows (Section 1.7) does not appear to provide support for a scenario under which
either of these dynamics contributes to the main patterns from the prior sections: with respect to
11th graders’ consumption of alcohol, the estimated impact is signiﬁcantly larger for girls, while
the sample of Black students reveals generally large and signiﬁcant impacts of the policy event on
drug use. Of course, both of these variables are also included in all estimated speciﬁcations.

36

1.7 Policy Implications and Heterogeneous Eﬀects

One key argument motivating the New York City DoE’s removal of its campus cellphone
ban centered on perceived inequity along demographic lines in enforcement, with schools having
proportionally larger minority enrollment also employing stricter treatment of students. Hence,
heterogeneity in impacts by demography may contribute relevant insight and additional context for
qualifying these concerns. Previous literature has also possibly provided reason to believe that the
role of cellphone use in fomenting problem behaviors may occur heterogeneously by socioeconomic
factors, aspects of which are in many environments correlated with race.21

Table 1.9 presents the coeﬃcients on “Post” from estimating Equation 1.3 on separate samples
by self-identiﬁed race category (i.e. Black or African American, White, Asian, and Other).
Joint testing of the eﬀect of district policy revision across the samples suggests a degree of
sociodemographic heterogeneity in the role of cellphones in health risk behaviors.

Among 9th graders, a large and signiﬁcant “Post” coeﬃcient in the marijuana speciﬁcation can
be found among the samples of students identifying as Black or one of the race options categorized
under Other (e.g. American Indian/Alaska Native, Hawaiian/Paciﬁc Islander, etc). Among students
identifying as White, the marijuana speciﬁcation also exhibits a signiﬁcant eﬀect (though not as
large), while yet a smaller but still signiﬁcant eﬀect also emerges with respect to use of inhalants.
The “Post” coeﬃcient is not signiﬁcant in any of the speciﬁcations within the sample of Asian
students, except in the inhalants speciﬁcation, where it is slightly negative. Among 11th graders,
the sample of White students appears to drive the estimated policy eﬀects in the marijuana and
alcohol speciﬁcations.

1.7.1 Proportion of School Eligible for Free and Reduced Price Lunches (FRPL)

Table 1.10 presents the coeﬃcients on “Post” from estimating Equation 1.3 on separate samples of
students based on being surveyed in a school where the proportion eligible for free and reduced price
21Koivusilta et al. (2007) report that children with low socioeconomic status both exhibit high

frequency phone use and are more likely to use their devices for playing games.

37

Table 1.9: Heterogenety: Race

(2)

(3)

Any drugs Coc./crack Marijuana

(4)

(5)
Inhalants Meth

(6)

(7)

Alcohol Cigarettes

(1)

0.026∗∗
(0.013)
32060

0.004
(0.006)
174279

-0.006
(0.007)
75257
0.026∗∗
(0.013)
64599

0.03

0.001
(0.015)
25840
0.024∗∗∗
(0.007)
157537

-0.001
(0.007)
66619

0.000
(0.015)
52551

0.028
Yes
Yes
Yes

Grade 9

Black

White

Asian

Other

Grade 11

Black

White

Asian

Other

School FE
Year FE
Controls

0.006
(0.008)
32060

0.002
(0.002)
174279

0.020∗
(0.012)
32060
0.008∗∗
(0.004)
174279

-0.001
(0.007)
32060

0.002
(0.002)
174279

0.018
(0.012)
32060

0.002
(0.006)
174279

0.002
(0.008)
32060
0.005∗
(0.003)
174279
-0.005∗
(0.003)
75257

-0.007
(0.006)
75257

-0.004
(0.002)
75257

-0.002
(0.003)
75257
0.026∗
(0.014)
64599

-0.003
(0.002)
75257
0.014∗
(0.008)
64599
P-values for test that coeﬃcients equal across race
0.102
0.14

0.010
(0.009)
64599

0.008
(0.006)
64599

0.014
(0.011)
64599

0.012

0.151

0.082

0.012
(0.008)
25840

0.003
(0.003)
157537

-0.000
(0.003)
66619

-0.009
(0.013)
25840
0.017∗∗∗
(0.005)
157537

0.003
(0.006)
66619

0.004
(0.007)
25840

0.002
(0.003)
157537

-0.003
(0.002)
66619

0.000
(0.014)
25840
0.020∗∗∗
(0.007)
157537

-0.004
(0.007)
66619

0.006
(0.008)
25840

0.001
(0.002)
157537

-0.002
(0.002)
66619
0.014∗
(0.008)
52551

0.004
(0.012)
52551

0.012
(0.009)
52551

0.012
(0.008)
52551
P-values for test that coeﬃcients equal across race
0.266
Yes
Yes
Yes

0.151
Yes
Yes
Yes

0.153
Yes
Yes
Yes

0.277
Yes
Yes
Yes

0.047
Yes
Yes
Yes

-0.003
(0.014)
52551

0.001
(0.008)
32060

0.004
(0.003)
174279

-0.004
(0.003)
75257
0.017∗
(0.010)
64599

0.07

-0.003
(0.008)
25840

0.004
(0.005)
157537

-0.005
(0.006)
66619

0.006
(0.011)
52551

0.606
Yes
Yes
Yes

Outcomes are indicators for any use of the substance in past 30 days. Each cell shows the coeﬃcient
on “Post” from estimating the trend break regression speciﬁed in Equation 1.3, using only the sample
speciﬁed in the row title. Controls include age, gender, school level enrollment, demographic composition,
FRPL, and proportion English learners. Standard errors in parentheses, clustered at the district level. ∗
p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

38

lunches lies either above or below the median for that year.22 While it may be perhaps unintuitive
that 9th graders in schools with relatively lower meal program eligibility, and which may thus
be better oﬀ ﬁnancially, exhibit a greater increase in post period likelihood of drug use, none of
these diﬀerences are statistically signiﬁcant in either grade. It is furthermore possible that poverty
exercises conﬂicting inﬂuences on drug use: while schools with higher average socioeconomic
status may have more resources to expend on safety, their students may also be better able to aﬀord
illegal substances.23

1.7.2 Gender

With respect to gender diﬀerences in cellphone use, girls have been found not only to take
their phones to school with them more frequently, but also to use them more frequently during
inappropriate times (Sánchez-Martínez and Otero, 2009), and are more likely to develop psychological
dependence and related health issues (Augner and Hacker, 2012; Roser et al., 2016). On the other
hand, frequent phone use among Finnish teenagers has been found to correlate more strongly with
excessive alcohol consumption and smoking for boys than for girls (Leena et al., 2005). In Taiwan,
Yang et al. (2010) note conversely that high frequency cellphone use among girls under 15 is
particularly associated with illicit drug use.24

Table 1.11 presents the coeﬃcients on “Post” from estimating Equation 1.3 on separate samples
of 9th and 11th grade boys and girls. Each cell in the table shows the shift associated with the
period post district code revision in the outcome speciﬁed in the column header, for the sample
speciﬁed by the row title. While, among 9th graders, boys appear to be more likely than girls to
22Quartiles are calculated at the school level: within each year, the median proportion FRPL
eligible is determined among schools, which may thus alternate between being above and below
the median form year to year.

23Patrick et al. (2012) in fact ﬁnd teen alcohol and marijuana consumption to be linked with

higher childhood socioeconomic status.

24Yang et al. (2010) also ﬁnd, interestingly, that cellphone use among boys correlates with
chewing betel nuts—an association that does not occur among girls. Used in a manner similar to
caﬀeine, the nuts are often chewed as a part of socializing with colleagues. While not illegal, they
cause oral cancer (Sui and Lacey, 2015).

39

Table 1.10: Heterogeneity: School is Above/Below Median Proportion FRPL Eligible

(1)

(2)

(3)

Any drugs Coc./crack Marijuana

(4)

(5)
Inhalants Meth

(6)

(7)

Alcohol Cigarettes

-0.003
(0.009)
106996

0.006
(0.006)
239199

0.002
(0.004)
106996

0.003
(0.002)
239199

0.363

0.763

0.009
(0.009)
92827
0.020∗∗∗
(0.007)
209720

0.339
Yes
Yes
Yes

0.004
(0.004)
92827

0.004
(0.003)
209720

0.947
Yes
Yes
Yes

-0.001
(0.003)
106996

-0.000
(0.007)
106996
0.010∗∗∗
(0.004)
239199

-0.002
(0.004)
106996
0.005∗
(0.003)
239199

0.002
(0.002)
239199
P-values for test that Above = Below
0.378

0.147

0.184

0.004
(0.007)
92827
0.012∗∗
(0.005)
209720

0.002
(0.003)
92827

-0.000
(0.003)
92827

0.003
(0.004)
209720

0.003
(0.003)
209720
P-values for test that Above = Below
0.544
Yes
Yes
Yes

0.956
Yes
Yes
Yes

0.273
Yes
Yes
Yes

-0.004
(0.008)
106996

0.004
(0.006)
239199

-0.003
(0.005)
106996
0.006∗∗
(0.003)
239199

0.394

0.121

0.006
(0.009)
92827
0.017∗∗
(0.007)
209720

0.34
Yes
Yes
Yes

-0.003
(0.006)
92827

0.004
(0.004)
209720

0.369
Yes
Yes
Yes

Grade 9

Above

Below

Grade 11

Above

Below

School FE
Year FE
Controls

Outcomes are indicators for any use of the substance in past 30 days. Each cell shows the coeﬃcient
on “Post” from estimating the trend break regression speciﬁed in Equation 1.3, using only the sample
speciﬁed in the row title. Controls include age, gender, race, school level enrollment, demographic
composition, and proportion English learners. Standard errors in parentheses, clustered at the district
level. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

40

Table 1.11: Heterogeneity: Gender

(1)

Any drugs Coc./crack Marijuana

(2)

(3)

Grade 9

Girls

Boys

Grade 11

Girls

Boys

School FE
Year FE
Controls

0.002
(0.006)
178732
0.010∗
(0.006)
167463

0.002
(0.002)
178732
0.005∗
(0.003)
167463

0.217

0.204

0.020∗∗∗
(0.007)
156252

0.011
(0.007)
146295

0.256
Yes
Yes
Yes

0.004
(0.003)
156252

0.005
(0.003)
146295

0.64
Yes
Yes
Yes

(4)

(5)
Inhalants Meth

0.004
(0.003)
178732

-0.000
(0.002)
178732

0.010∗∗
(0.004)
178732
0.008∗∗
(0.004)
167463

0.002
(0.002)
167463

0.003
(0.002)
167463
P-values for test that Girls = Boys
0.367

0.717

0.776

0.013∗∗
(0.005)
156252

0.002
(0.002)
156252

0.002
(0.001)
156252

0.009
(0.006)
146295

0.003
(0.004)
146295

0.002
(0.003)
146295
P-values for test that Girls = Boys
0.911
Yes
Yes
Yes

0.845
Yes
Yes
Yes

0.676
Yes
Yes
Yes

(6)

(7)

Alcohol Cigarettes

-0.003
(0.006)
178732

0.008
(0.005)
167463

0.002
(0.003)
178732

0.005
(0.003)
167463

0.063

0.467

0.015∗∗
(0.006)
156252

0.008
(0.006)
146295

0.329
Yes
Yes
Yes

0.001
(0.004)
156252

0.003
(0.005)
146295

0.812
Yes
Yes
Yes

Outcomes are indicators for any use of the substance in past 30 days. Each cell shows the coeﬃcient
on “Post” from estimating the trend break regression speciﬁed in Equation 1.3, using only the sample
speciﬁed in the row title. Controls include age, race, school level enrollment, demographic composition,
FRPL, and proportion English learners. Standard errors in parentheses, clustered at the district level. ∗
p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

report having used drugs, this is less evident for 11th graders, and none of the gender diﬀerences
in either grade are statistically signiﬁcant at conventional levels except for that with respect to 9th
grade use of alcohol. At a glance, it may be reasonable to suspect that 9th grade boys may be
driving the eﬀects seen for 9th graders in alcohol consumption, a pattern which would align with
the ﬁndings of Leena et al. (2005). Figure A.2 compares the results from estimating the event study
model with this outcomes on the samples of 9th grade girls (top) and 9th grade boys (bottom).

41

1.8 Summary

This study ﬁnds supporting evidence that removing campus cellphone bans elevates the
likelihood of student substance abuse, lending credence to the concerns of law enforcement and
policy makers that in many cases gave rise to such rules. Although existing research in economics
and education has assessed the beneﬁts and challenges of applying mobile technology to improving
academic outcomes,25 few studies have applied similar methodology to exploring the devices’ role
in broader areas of high school students’ lives, which may inﬂuence human capital development
and later life outcomes.

In particular, cellphone rule changes in California districts appear to have had a clear and
pronounced eﬀect on 9th grade marijuana use, supporting the CHKS’s focus on freshmen; the
transitional ﬁrst year of high school indeed appears to be a formative period with regard to health
compromising behaviors. Eﬀect magnitudes are important relative to the incidence of substance
abuse before bans were lifted. Furthermore, allowing campus mobile phone use only clearly appears
to exacerbate abuse of illegal or highly stigmatized substances, which is to be expected if cellphone
communication reduces the transaction costs incurred in obtaining drugs.

Ultimately, recent trends towards more relaxed device policies may be justiﬁed by convenience,
educational beneﬁt, and safety in certain critical situations. However, it is likely also the case that
without adequate preparation, including establishing trust and understanding between students and
educators, these changes may compromise the safety of the school environment in other respects.
While each of the above considerations will naturally bear more relevance in some settings than in
others, this study suggests that eﬀective policy will generally demand a broad view of consequences
over a narrow focus on select metrics.

25For further reading on this subject, see Dietz and Henrich (2014), Ellis et al. (2010), Hawi and

Samaha (2016), Junco (2012), Patterson and Patterson (2016), and Sana et al. (2013).

42

CHAPTER 2

IMPACT OF INTERNET ACCESS ON STUDENT LEARNING IN PERUVIAN

SCHOOLS (WITH LEAH LAKDAWALA AND EDUARDO NAKASONE)

2.1 Introduction

In recent decades, developing countries have achieved large increases in school enrollment,
particularly at the primary level. However, most remain far behind developed countries in terms
of school quality as measured by student achievement (Glewwe and Kremer 2006). Traditional
policies — such as hiring additional teachers or providing textbooks — do not appear to have
improved student achievement in developing countries (Kremer et al., 2013). In turn, there has been
an increasing interest in new approaches, such as Information and Communication Technologies
(ICTs), to improve school performance. Their potential to boost modern-day digital competencies,
promote interactive student-centered teaching models, and provide up-to-date learning materials
even in remote areas (World Bank, 2018) has encouraged considerable investments in ICTs in
schools developing countries (World Bank, 2018; Escueta et al., 2017; One Laptop per Child, 2016;
UNESCO, 2012; Trucano, 2016; International Telecommunication Union, 2014).

Among ICTs, the internet in particular may have an important role as a pedagogical tool in
developing countries. Internet access can provide students in understaﬀed schools with otherwise
unavailable sources of information (Levin and Arafeh, 2002). Additionally, internet can expand
teachers’ access to references and teaching aids as well as their ability to share information among
peers (Jackson and Makarin, 2016; Purcell et al., 2013). However, as with any new technology,
beneﬁts materialize only after a period of learning and adaptation, suggesting the importance of
understanding the dynamic eﬀects of ICT interventions over time.

Despite the potential of internet to improve learning, few studies have rigorously evaluated its
impacts on student performance in developing countries. While previous research in developed
countries has led to ambivalent conclusions on the eﬀectiveness of internet access as a learning

43

input (Belo et al., 2014; Faber et al., 2015; Gibson and Oberg, 2004; Goolsbee and Guryan, 2006;
Machin et al., 2007; OECD, 2015; Vigdor et al., 2014), school-based connectivity can be potentially
more important in developing countries due to lower levels of teacher skills, larger class sizes, and
limited access to other conventional inputs.1 Additionally, since the broader literature on ICTs
(Escueta et al. 2017 and Bulman and Fairlie 2016) typically examines bundles of interventions such
as computer access, learning software, and internet expansion2, it is not yet clearly understood how
internet on its own aﬀects learning.3

Moreover, most prior studies of internet access — and of ICTs more generally — have been
based on short-term observation of small samples, and are thus only prepared to detect large and
immediate treatment eﬀects. Importantly, such studies may overlook potential longer term impacts
that may follow from an initial learning period, during which teachers, students, and administrators
adapt to new technology. Hence, detecting gains in learning that may arise over such a learning
period requires a longer evaluation window.

We examine the impact of internet access on student performance in the universe of public
primary schools in Peru that initially acquired internet between 2007 and 2014, emphasizing its
dynamic eﬀects in schools over time. During our sample period, about 933,000 students gained
access to internet. We link administrative data on school-based access to internet with school-
1In a recent paper, Malamud et al. (2018) investigate the impact of a home-based internet
on students’ school performance in Peru. The authors ﬁnd no statistically signiﬁcant eﬀect on
standardized test scores 9 months after the implementation of the program. The authors posit that
the lack of impact might in part be due to relatively little time spent at home using computers.
Additionally, children might use internet as a tool for entertainment rather than learning. Both of
these problems might be reduced when internet is provided at school rather than home.

2Some notable exceptions analyze the individual impact of computer access (Beuermann et al.,
2015; Cristia et al., 2017; Barrera-Osorio and Linden, 2009; Mo et al., 2013; Toyama, 2015; de
Melo et al., 2013; Sharma, 2014; Meza-Cordero, 2017; Bai et al., 2016) or learning software (Bando
et al., 2016; Banerjee et al., 2007; Carrillo et al., 2010; He et al., 2008; Linden, 2008; Muralidharan
et al., 2016) in developing countries. However, there is little evidence on the impact of internet
access.

3Previous work (e.g., Cristia et al., 2014; Bet et al., 2014; Sprietsma, 2007) has assessed the
impact of programs that have provided school-based internet as part of larger schemes of ICT
expansion. However, disentangling eﬀect of internet from other technologies is not the aim of these
papers.

44

average math scores from a large-scale national test that covers nearly the universe of second
graders in public schools in Peru. We construct a panel dataset of 5,903 schools that gained internet
during our study period. To fully exploit the longitudinal structure of our data and identify dynamic
eﬀects, we employ an event study framework in addition to a trend break analysis — approaches
which also allow us to detect and control for pre-existing trends in student performance. Since we
observe a large panel of schools over eight years, we are also able to assess how other determinants
of school performance change over time, tracing out the dynamics of student, teacher, and school-
level inputs. This allows us to discuss potential channels through which internet aﬀects school
performance, as well as to thoroughly explore the possibility that other confounding factors drive
our results.

Using within-school variation in the timing of internet installation, we ﬁnd that internet access
leads to initial modest math score improvements of 0.042 to 0.076 standard deviations in the ﬁrst
18 months after installation. Importantly, this advantage also grows signiﬁcantly over time (at a
rate of about 0.047 standard deviations per year on top of an initial level improvement), reaching
0.29 standard deviations ﬁve periods after installation.

We posit that this growth in our estimated impacts over time reﬂects an adaption period, during
which schools must learn to integrate new technologies. Namely, we observe that schools respond to
internet access by hiring teachers with formal training in digital skills, and that this process follows
only gradually. In particular, schools are 2.1 percentage points more likely to have a computer-
trained teacher in the ﬁrst year after installing internet and 9.6 percentage points more likely by the
ﬁfth year after installation (a doubling of the pre-internet likelihood of having computer-trained
teachers). Hence, the fact that the gradual growth over time in test scores shadows growth in the
staﬃng of computer-trained teachers may suggest that complementary investment in staﬀ computer
proﬁciency is needed to fully exploit internet-enabled classroom capabilities.4

Furthermore, our data oﬀers suggestive evidence for two potential channels through which
4Similarly, evaluations of laptop provision in the U.S. (Hull and Duch 2016) and computer
assisted learning in China (Mo et al. 2015) estimate that the eﬀects of ICT interventions grow over
time.

45

internet access improves test scores. First, gains in test scores are predominantly driven by schools
with high student-to-teacher ratios, suggesting that internet-related activities may supplement the
limited individualized attention that teachers can provide in large classes. Second, gains in test
scores are largest for schools with relatively low teacher qualiﬁcations — as measured by the per
student count of teachers holding a pedagogical or university degree — which is consistent with
internet resources compensating for or addressing deﬁcits in teacher training.5

Additionally, our main ﬁndings are robust to a number of alternative explanations. Concerning
potential endogeneity in the timing of internet access, we ﬁnd that, conditional on year and school
ﬁxed eﬀects and a set of time-varying school characteristics (e.g., school size, infrastructure, and
resources), schools receiving access to internet do not exhibit positive pre trends in performance or
have diﬀerent pre internet scores compared with those that do not. Second, we also ﬁnd that our
results are not explained by concurrent changes in other inputs (e.g., infrastructure, textbooks, or
computers) or by regional (and even school-speciﬁc) trends. Third, while our main speciﬁcations
are based on an unbalanced sample of schools, our results are qualitatively similar across diﬀerent
sample speciﬁcations (including a balanced panel of schools). Lastly, analyzing student composition
within schools shows that our ﬁndings cannot be driven by endogenous sorting of students.

We contribute novel insights and perspective to a nascent body of research in developing
countries on the educational beneﬁts of school-based internet access, as well as to a wider literature
concerning ICTs as schooling inputs. Primarily, the size and time span of our data present
opportunities to complement and contextualize existing knowledge from randomized control trials
(RCTs), which largely comprise the current work relating ICTs and academic performance. Whereas
RCTs are mostly constrained to observe short term eﬀects (rarely beyond one academic year), we
use our extended study period to analyze the eﬀects of internet access up to 5 years after it is
introduced to schools. Our results indicate that this longer evaluation window is highly relevant to
understanding the impact of internet access, due to the dynamic eﬀects of internet on learning over
5These ﬁndings complement evidence from the developed country context, where providing
teachers with online access to “oﬀ the shelf” lesson plans improves students’ math achievement
and that beneﬁts were larger for weaker teachers (Jackson and Makarin 2016).

46

time.

Additionally, the large scale of our sample — about 6,000 public schools — provides power
to detect the short-run impacts of internet, which appear to be modest in size. Namely, we
discover average math score gains of 0.042-0.076 standard deviations in the ﬁrst year of internet
access, statistically signiﬁcant at the 5% level. While several evaluations of programs distributing
computers in developing countries report similarly sized short-run eﬀects (ranging from 0.052-
0.088 standard deviations 5-22 months after initial access; Bet et al. 2014, Barrera-Osorio and
Linden 2009, Cristia et al. 2017, Beuermann et al. 2015, Mo et al. 2013), none of these studies are
able to statistically distinguish eﬀects from zero, perhaps in part because they analyze far smaller
samples of schools (ranging from 13 to 318 schools). Since we investigate a massive national policy
(which aﬀected a wide array of public primary schools serving roughly 900,000 children), we can
assess conditions relevant for internet provision programs. We ﬁnd that the eﬀects of internet
access are the largest in schools with low levels of existing resources, particularly those that are
understaﬀed and with less qualiﬁed teachers.

Finally, we are able to explicitly identify the gains that internet access confers over hardware
resources alone. Anecdotally, the usefulness of school computers without internet access has been
limited by lack of access to information (National Public Radio 2012) and the inability to obtain
routine maintenance and software updates — particularly in remote, diﬃcult-to-reach locations
(One Laptop per Child 2011). Indeed, our data suggest that computers alone (in schools without
internet access) have only modest impacts on student learning. To the best of our knowledge,
the scale, longitudinal length, and setting of this study, along with the comprehensiveness of the
available data uniquely address important gaps in the existing literature. More broadly, our work
contributes to understanding the role of internet access in economic development. In consideration
of prior research connecting faster internet to higher employment, incomes, and wealth in African
countries (Hjort and Poulsen 2017), increased human capital production may factor importantly in
this progress.

The paper proceeds as follows. In Section 2.2 we describe the educational setting in Peru and

47

Plan Huascarán, the source of variation in internet installation for many pubic schools during our
sample period. We also provide details about the two administrative datasets we merge for our
analysis, the Censo Escolar and the Evaluación Censal de Estudiantes. Section 2.3 ﬁrst describes
our event study and trend break strategies and then presents the main estimates of the impact
of internet access on test scores.
In Section 2.4 we investigate the robustness of our results to
a number of plausible confounding factors: changes in other school resources, potential regional
shocks correlated with internet access and student performance, diﬀerential pre-trends in test scores,
and changes in sample composition (both in terms of schools and students). In Section 2.5 we show
that the dynamic patterns in test score impacts may be explained by an adaptation period, during
which schools hire computer-trained teachers. We also shed light on two potential mechanisms
through which internet access generates gains in learning by examining heterogeneity in the eﬀects.
Section 2.6 concludes.

2.2 Setting and data

2.2.1 Education and ICT Access in Peru

Education in Peru is compulsory and free through the public school system beginning at age 3 and
continuing until the end of secondary school. In the past few decades, Peru has greatly increased
access to primary school (grades 1-6, approximately age 6-11), raising the net enrollment rate from
85.6% in 1980 to 97.9% in 2015 (The World Bank 2016). At the same time, however, the education
budget has seen little growth and greater enrollment over time has eroded per-student resources
(Saavedra and Suarez 2002). The World Bank (2012) ﬁnds that, within Latin America, only the
Dominican Republic has a lower education expenditure-to-GDP ratio than Peru.

This dearth of resources has limited the quality of education, as evidenced by Peru’s performance
in the OECD’s Program for International Student Assessment (PISA) — an international standardized
test among 15 year olds — in 2012 and 2015. In 2012, Peru ranked last out of 65 participating
countries in all three evaluated subjects, with results revealing that most Peruvian students have
serious deﬁciencies in math (75% deﬁcient), science (69%), and reading (60%). In 2015, Peru

48

jumped to the 64th place (out of 70 countries in the evaluation), nonetheless demonstrating that
substantial progress remains to be made. Widespread under-preparedness is evident as early as
primary school. In 2007, the Ministry of Education began administering yearly standardized tests,
the National Student Assessment or Evaluacion Censal de Estudiantes (henceforth ECE, described
below), to all second graders registered in classes with ﬁve or more students. The inaugural results
of the ECE in 2007 showed that only 7% of students acquired skills mandated by the national
curriculum in math (Appendix Figure B.1). Despite improvement since then in test scores and in
the proportion of students meeting expected skill levels, the quality of schooling has continued to
prove inadequate for many children; even by 2014, fewer than a quarter of second graders achieved
proﬁciency in math.

In the early 2000s, the Peruvian government launched Plan Huascarán, which produced much
of the variation in school internet access observed during our sample period. This project aimed
to “incorporate information and communication technologies to increase the coverage, quality,
decentralization, democratization, and equity of the Peruvian education system.” Project planners
ambitiously aimed to install hardware and internet in 32,000 schools and to train 180,000 teachers
by 2020. Plan Huascarán targeted primary, secondary, and integrated schools (i.e., those that
teach both primary and secondary classes) under public management, particularly in rural (or peri
urban) and high poverty areas. Oﬃcially, selection into the program was rationed, with each Local
Educational Management Unit (UGEL) allowed to submit a set number of its schools, adhering
to a set proportion of primary, secondary, and integrated schools (see Appendix Figure B.2 for
an excerpt of the oﬃcial Ministry of Education ﬂow chart that outlined the speciﬁc prioritization
protocol under Plan Huascarán).6 The largest allocated proportion (50%) was set aside for primary
schools. As prerequisites for program selection, schools needed to have electricity and a computer
lab (also called an “innovation classroom”) with anti-theft measures (i.e., perimeter fencing).
Within each UGEL and level (e.g., primary), prioritization among qualiﬁed schools was oﬃcially
based on the size of the student population with larger schools receiving higher priority. Lists
6An excerpt from the translated Ministry of Education directive regarding the prioritization

protocol for Plan Huascarán is provided in Appendix Figure B.3.

49

of eligible schools were aggregated to the regional level and then submitted to Plan Huascarán
headquarters, accompanied by data sheets on the characteristics of each school listed, a sketch and
description of each school’s computer facilities, and the discussion minutes from each UGEL.7
Oﬃcially, no school was integrated into the project without all required information.

As a consequence of initiatives such as Plan Huascarán and the One Laptop per Child program
(OLPC, undertaken by the Peruvian government in 2008)8, the ratio of students to computers in
primary schools fell dramatically from 240 to 6 between 2000 and 2014 .

In parallel, the government has steadily increased access to internet in schools (as described
in Section 2.2.2.1). In 2013, the Ministry of Education announced plans to triple the number of
schools with internet access in the country.

2.2.2 Data

Our analysis uses data from two sources administered by the Ministry of Education: the Censo
Escolar (CE), an annual census of schools, and the Evaluación Censal de Estudiantes (ECE), an
annual standardized test of second graders’ skills.

2.2.2.1 Censo Escolar (CE) and School-based Internet Access

Each year, all school principals are required to submit two forms with their updated information to
the Ministry of Education. Between April and July, principals complete a form on enrollment (by
grade and age), teachers (by qualiﬁcation), available supplies and materials (e.g., books, computers,
and laboratories), and infrastructure (e.g., access to utilities, building characteristics, and internet
connectivity). Between December and February, another form is completed on year-end pupil

7A translated version of the school data sheet is provided in Appendix Figure B.4.
8Peru has been the single largest buyer of OLPC laptops and to date has distributed close to one
million laptops, mainly targeting school children in poor areas of the country. For a discussion of
the OLPC program in Peru, see Trucano (2012). In general, impact evaluations of OLPC in Peru
suggest that the provision of laptops did not improve student performance (Beuermann et al. 2015;
Cristia et al. 2017).

50

outcomes (e.g. number of pupils transferring to other schools).9 We refer to the CE for data
on school characteristics such as internet access, enrollment, teachers, educational materials and
resources, and physical infrastructure. Between 2007 and 2014, around 29,500 public primary
schools reported administrative information in the CE annually.

We use information from the CE to determine the timing of initial internet connection among
schools in our sample. Administrators report in the ﬁrst semester of every year whether their school
currently has access to internet. Though some schools report gaps in internet access the data do not
allow us to distinguish between temporary outages and longer-term disruptions to connectivity.10
Based on this information, we determine the ﬁrst year in which a school reports gaining access
to internet and interpret this as the time of connection. In our estimation framework, this implies
a conservative estimate of the impact of internet access because we treat schools that might have
permanently lost their connections as still being connected. Another beneﬁt of using initial internet
connection rather than current access is that we avoid bias due to endogenous changes in access.
We estimate that 7,089 schools — and the 933,000 students in these schools — at some point gained
internet connectivity between 2007 and 2014.11 This implies that the rate of internet connection in
schools increased from 5% to 30% and that the share of students with internet connection in their
schools jumped from 23% to 66% (Figure 2.1).

Most of the observed expansion in internet connectivity during this period was due to Plan
Huascarán. In Appendix Table B.1 we verify that the oﬃcial qualiﬁcation and prioritization rules
(set by the Ministry of Education) predict actual installation in practice. Schools received priority
primary based on quotas by province (Local Education Management Units, UGELs), high poverty
status, location in a rural versus urban area, public versus non-public management, the presence
of required infrastructure (including electricity, a computer lab, and anti-theft measures such as

9The school year in Peru runs from March to December.
10Out of the 30,338 public primary schools with at least one year of data in the CE between 2006
and 2014, 13.2% report not having access after having access in a previous year; about 20% of
those schools regain internet access at a later point.

11Note we do not observe test scores at least twice during our sample period for all 7,089 schools,

so some are not included in our estimation sample. See Section 2.2.2.3 for more details.

51

Figure 2.1: Internet Connectivity in Primary Public Schools, 2006-2014

NOTE: The stock of schools that gained internet connections is based on the ﬁrst year in which
they report internet access in the Peruvian Censo Escolar.

perimeter fencing), and enrollment. Column 1 includes these characteristics and year eﬀects
to control for aggregate trends in internet connectivity. To approximate the status of “adequate
infrastructure, in good condition,” we include indicators of whether the school has a library and
administrative oﬃces. To capture high poverty status, we include district-level ﬁxed eﬀects. We
also include UGEL ﬁxed eﬀects to account for the UGEL-speciﬁc quotas. As expected, most
prioritization characteristics positively predict internet access, though location in urban areas is not
statistically signiﬁcant. In column 2, we add school ﬁxed eﬀects to match our main speciﬁcation
(described in Section 2.3), thus dropping terms for prioritization characteristics that are time-
invariant within schools (e.g., UGEL, district, and location). Even with school ﬁxed eﬀects,
facilities such as the existence of a computer room, administrative oﬃces, and a library positively
predict internet access. This pattern is consistent across columns 3 and 4, which add perimeter
fencing (available only for 2010 and later) and information from school data sheets (number of
computers used for instruction, number of computers used for administrative purposes, and number
of teachers), respectively. Since these factors predict internet access and are also likely to inﬂuence
student performance directly, we control for all of these measures (except perimeter fencing due to
data limitations) in our main speciﬁcations.

52

.2.3.4.5.6.7% of students.05.1.15.2.25.3% of schools200620072008200920102011201220132014YearProportion of schools with internet accessProportion of Primary students with internet access2.2.2.2 Evaluación Censal de Estudiantes (ECE)

The Ministry of Education also mandates the Evaluación Censal de Estudiantes (ECE), a yearly
standardized assessment of second graders’ skills, which is administered in late November or early
December (before the end of the school year). In order to ensure uniform testing environments —
and to prevent content leaks or inﬂuence from school personnel — the Ministry hires independent
staﬀ to administer the test in all schools simultaneously. Furthermore, the ECE was designed for
comparability of results over time: experts deﬁned the current and future skill categories prior to
the test’s ﬁrst administration. Hence, since its inauguration in 2007, the ECE has assessed the same
skill sets with consistent relative focus. To account for diﬀerences in diﬃculty across cohorts, we
standardize ECE scores across the universe of tested schools within each year.

The ECE allows us to gauge the academic performance of the vast majority of second graders
in Peru, targeting all public and private schools that meet two criteria: 1) having at least ﬁve second
graders enrolled during the test year, and 2) using Spanish as the primary language of instruction.
The rationale for the ﬁrst criterion is entirely budgetary, as smaller schools are often in remote
areas and would take considerable resources to reach. As it stands, the ECE already requires about
40,000 ﬁeld workers each year. Schools teaching in indigenous languages are covered under a
separate testing schedule.

In total, 16,000 – 19,000 primary public schools participated per year (55% to 65% of all
primary schools; see Figure B.5a). About 27% – 39% of schools were exempt under the minimum
enrollment or language criteria. The remaining schools (between 4% and 10%) were not tested due
to logistical problems. The coverage of the test was nonetheless very broad: because the smallest
schools were excluded by deﬁnition and because schools in native language tend to have modest
enrollments, between 83% and 90% of all second graders in the country were tested in the ECE in
a given year (Appendix Figure B.5b).

53

2.2.2.3 Estimation Sample

Our empirical strategies exploit the timing of internet connection within schools. Therefore, we
restrict our sample to only those schools that help identify the eﬀects of internet access conditional
on school ﬁxed eﬀects — i.e., those who had internet installed during the study period (2007-2014)
— and exclude all schools without changes in internet access during this period — i.e., those
that already had internet before 2007 and those that did not gain access by 2014. This leaves us
with 7,089 schools, roughly a quarter of all public primary schools in Peru. We then merge this
information with annual school-level average math scores from the ECE. All in all, there are 5,903
schools that were tested in the ECE, that gained internet in our period of analysis, and that are
observed at least twice during our window of analysis.

Appendix Table B.2 presents summary statistics from 2007 (or each school’s earliest available
year in our sample) for the 25,624 schools that appear in both the CE and the ECE in our sample
period. We divide the sample into schools that already had access to internet before 2007 (“early
adopters”), those that became connected between 2007 and 2014 (our estimation sample), and those
that had not gained access by 2014 (“non-adopters”).

We highlight two key observations from Appendix Table B.2. First, only 1,359 (5.3%) of
schools were internet-equipped by 2007. While 17,738 (69.2%) remained unconnected by 2014,
6,527 (25.5%) of schools gained access during our study period. The sharp expansion in internet
connectivity during this period allows us to form insights from a large number of schools despite
our sample restrictions.12 Second, schools that gained internet from 2007-2014 generally fall
“between” the early adopters and non-adopters in various measures of school quality. Namely,
early adopters appear to be schools with higher performance, larger enrollment, and endowed
with better infrastructure and educational inputs (e.g., piped water, libraries, administrative oﬃces,
12Within the group of schools that gained connection between 2007-2014, there is considerable
variation in the timing of access for our analysis: 4,915 schools are observed for at least one period
prior to internet connection, 5,424 are observed 1-2 years after internet connection, and 3,316 are
observed 3-5 years after internet connection. This allows us to implement the event study approach
described in Section 2.3.1.

54

teachers, classrooms, computers, and textbooks). Conversely, non-adopters systematically appear
worse in these areas. Consequently, our estimation sample focuses neither on the best nor on the
worst performing schools.

In Figures 2.2b-2.2i below, we plot each treatment “cohort’s” (by year of initial internet
connection) average math performance over time.13 Additionally, Figures 2.2a and 2.2j represent
the performance of schools that gained access prior to 2007 (the start of our sample period) and
that had not gained access to internet by the end of our analysis period, respectively. Generally,
schools that connected later or remained unconnected exhibit lower average test scores, indicating
that variation in internet access across schools is not random.

However, within a cohort of schools becoming connected in a given year (2007-2014), there
do not appear to be trends in scores prior to internet access. This suggests that within cohorts
of treated schools, the timing of access is unrelated to test score trends on average. Furthermore,
Figure 2.2 suggests that performance gains among treated schools are modest initially and only
become sizable in the medium term. In contrast, the relative math performance of schools that
never connected to the internet appears to have stagnated over the period of analysis. Furthermore,
it appears that schools with internet connectivity prior to 2007 continued to experience increases in
average test scores during our period of analysis.14 This pattern motivates the strategies employed
in our main analysis (Section 2.3) to identify the dynamic eﬀects of internet.

2.3 Empirical strategies and results

2.3.1 Event study speciﬁcation

In order to analyze dynamic impacts of internet access over time, we estimate the following event
study speciﬁcation:

13Recall that within each year, school level averages are normalized across all schools giving the

ECE, including those not in our main estimation sample.

14Unfortunately, we cannot determine the timing of internet connectivity prior to 2007. While
we can identify schools that had internet installed by 2007, we do not have information about the
speciﬁc year in which they gained connectivity.

55

Figure 2.2: Standardized Average Math Scores over Time, by Year of Initial Internet Access

Access before 2007

Initial Year: 2007

Initial Year: 2008

Initial Year: 2009

Initial Year: 2010

Initial Year: 2011

Initial Year: 2012

Initial Year: 2013

Initial Year: 2014

Without Connection by 2014

Figure 2.2a plots the standardized test scores for all public schools that had an internet connection prior to 2007. Figures 2.2b-2.2i
plot the standardized test scores over time separately for groups of schools based on the year of initial internet connection. The
sample includes all public schools that initially gained internet access between 2007 and 2014 and with at least two observations
within the same period. Figure 2.2j plots the standardized test scores for all public schools that did not have an internet connection
by 2014.

56

−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.7120062008201020122014−.37−.19−.01.17.35.53.71200620082010201220145

t=−3

Yir =

βt1 {Eir = t} + γXir + αi + θr + εir,

t (cid:44) −1

(2.1)

Our primary outcomes of interest are averages of standardized math scores for second grade
students in school i in year r (Yir) (normalized across the universe of Peruvian schools within each
year). αi and θr are school and year ﬁxed eﬀects that capture school-speciﬁc ﬁxed determinants of
and aggregate changes in student performance over time, respectively.15 Xir is a set of time-varying
characteristics that includes total school enrollment, number of second grade students scheduled
to take the test, facilities (piped water, library, administrative oﬃces), and resources per student
(classrooms, computers and teachers).

Let Ii denote the year in which school i gains internet connection (the ﬁrst year in the dataset in
which i reports internet access in the CE). Eir represents time relative to internet access for each
school; speciﬁcally, Eir = r − Ii. The coeﬃcients on the set of event study dummy variables βt
capture the path of test scores relative to the year before a school receives internet access (i.e.,
relative to t = −1). It is worth highlighting one important feature in the timing of the two datasets
we use. The CE reports internet access in the beginning of the school year, while the ECE is a
year-end test. Any school that installs internet after the CE (April-July) does not report internet
access until the following calendar year. If internet installation occurs before the ECE exams (end
of November - December), students are (at least partially) exposed to internet access in the year
prior to reporting initial access in the CE. Therefore in merging internet information from the CE
to test scores from the ECE, we match test scores from the ECE to the internet status in the CE
of the following calendar year. This means that some schools acquire internet access in t = 0
(if installation occurred before submitting the CE information) while others acquire it in t = 1 (if
installation occurred after submitting the CE information). Unfortunately, school-level information
15A regression that includes school ﬁxed eﬀects, event study time dummies, and a full set of
calendar year ﬁxed eﬀects results in perfect multicollinearity. We therefore pool two year eﬀects
(which should be close to zero, given that school-level scores are normalized within each year to
a mean of zero and standard deviation of one). Results are robust to our pooling choice, and are
similar when pooling two pre-internet event study indicators (e.g., t=-3 and t=-2) or dropping year
eﬀects altogether.

57

is not available for either the month of installation or completion of the CE so we are unable to tell
how many schools receive internet in t = 0 and t = 1. Thus, in interpreting estimates of βt it is
important to keep in mind that t = 0 is a partially treated year for some schools and a pre-treatment
year for others, while t = 1 is a partially treated year for some schools and a (fully) treated year for
others.

By exploiting variation in the timing of internet access within schools (as well as additionally
controlling for aggregate year eﬀects and a set of time-varying characteristics), we aim to identify
the eﬀects of internet access separately from potential confounders that are ﬁxed at the school
level. We consider this a reﬁnement over Hopkins (2014), who also examines the relationship
between internet access and test performance in Peru — but compares internet-connected schools
to non-connected schools (including those that never become connected). We use the event study
framework to examine both pre-treatment trends and dynamic eﬀects in up to ﬁve periods following
internet access in a non-parametric fashion. Standard errors are clustered at the school level to
allow for arbitrary serial correlation in εit.

Figure 2.3 displays the results of estimating Equation 2.1 on our main sample. The full set
of coeﬃcients for the event study dummy variables are reported in Appendix Table B.3. We ﬁnd
that, prior to internet access (t < 0), schools’ relative math performance compared with their peers
was roughly constant from year to year (Figure 2.3). Importantly, there is no apparent trend in
math scores prior to internet access, indicating that the timing of internet access within schools is
unrelated to pre-trends in student performance. In particular, we rule out the case in which internet
installation is budgeted endogenously as a reward for steadily improving test performance. While
relative math performance rises in all years following initial connectivity, immediate gains are
small in magnitude (0.042 standard deviations in the ﬁrst partial year of access). The improvement
does not surpass 0.1 standard deviations until 2 years after installation. By year 5, scores are 0.29
standard deviations higher compared with other schools than before internet installation.

On the surface, this ﬁnding stands in contrast to other studies in developing countries that ﬁnd
limited or no impacts of ICTs on test scores. However, our short run estimates are in fact similar in

58

Figure 2.3: Impact of Internet Access on Test Scores

The above ﬁgures plot the coeﬃcients and 95% conﬁdence intervals from estimating equation 2.1. Full regression
results are reported Table B.3. Scores are standardized to have mean zero and standard deviation of 1 across the
universe of schools reporting scores within each calendar year. Coeﬃcients capture the increase in test scores
relative to the year prior to a school receiving internet access (t = −1). Note that due to the timing of the Censo
Escolar relative to the ECE exam, some schools receive internet access in t = 0 while some receive it in t = 1.
For more details, see Section 2.3.1. Control variables include total school enrollment, number of second grade
students scheduled to take the ECE, facilities (computer room, library, administrative oﬃces), and resources
per student (classrooms, computers, and teachers). The sample includes all public schools with at least two
observations within the sample period (2007-2014). Standard errors are clustered by school.

magnitude to those from several studies of hardware-only ICTs —which range from 0.052 to 0.088
standard deviations, 5 to 22 months post-intervention (Bet et al. 2014, Barrera-Osorio and Linden
2009, Cristia et al. 2017, Beuermann et al. 2015 Mo et al. 2013) — though these other studies
are unable to statistically distinguish estimates from zero (based on smaller samples of schools
that range from 13 to 318).16 Results from Figure 2.3 suggest that though classroom internet is
beneﬁcial to learning, improvement in the initial years post-intervention is small. The majority
of the studies in this literature focus on impacts within the ﬁrst 18 months post intervention, an
early stage in which impacts may not be statistically detectable in smaller samples. The fact that
our estimates grow over time, at least through the medium-term, is also consistent with the only
16Other studies (Angrist and Lavy 2002, Meza-Cordero 2017, Sharma 2014) ﬁnd negative —

though not always statistically signiﬁcant — eﬀects of hardware introduction on test scores.

59

other two longer-term studies of ICTs in education — which have also supported the need for an
adaptation period to fully utilize new technologies (Hull and Duch 2016; Mo et al. 2015).

In the medium-run (3-5 years), the increase in math scores is sizable, though somewhat smaller
than those typically found in evaluations of computer assisted learning and related interventions
(0.18 to 0.59 standard deviations) (e.g., see Bando et al. 2016, Banerjee et al. 2007, Carrillo
et al. 2010, He et al. 2008, Linden 2008, Muralidharan et al. 2016). Our smaller albeit statistically
signiﬁcant estimates may owe partly to the fact that introduction of internet into Peruvian schools was
unaccompanied by any particular pedagogical software service, pre-speciﬁed uses, or complementary
interventions.17 Unlike in many of the interventions associated with relatively larger impacts,
teachers and students here would have needed to ﬁnd eﬀective uses of the internet on their own.

2.3.2 Trend break speciﬁcation

Though the shape of Figure 2.3 suggests a steadily increasing eﬀect of internet access on math
test scores over time, it does not explicitly test for a break in the trajectory of scores at the time of
internet installation. To do so, we estimate a linear trend break speciﬁcation as follows:

Yir = φ1Post-internet Accessir + φ2Event Timeir

+φ3Post-internet Accessir × Event Timeir + γXir + αi + θr + εir

(2.2)

Here, Post-internet Access is a dummy variable that is equal to one in all periods after internet
installation (t ≥ 0). Event Time is a linear term for time relative to the year prior to access, t = −1.
The control set is otherwise identical to that described in Section 2.3.1. In this speciﬁcation, φ1
captures the level shift in test scores in response to internet access; φ3 represents the change in
the linear time trend in math scores after schools gain internet access; and φ2 accounts for any
17Though many public schools gain access to the internet through Plan Huascarán, which
also aims to increase computers in schools, our main speciﬁcations control for the number of
computers per student so that the estimated eﬀects of internet access account for diﬀerential access
to computers. We discuss the relationship between the eﬀects of internet access and computer
availability in more detail in Section 2.4.

60

pre-existing linear trend. Based on the results in Section 2.3.1, it is unlikely that there are any
existing pre-trends. However, one beneﬁt of this speciﬁcation is that even in the presence of any
linear pre-trends in test scores, φ3 measures the impact of internet access on the growth in test
scores apart from any such trends.

Results from estimating equation 2.2 are displayed in Table 2.1. The speciﬁcation in column 1
controls only for year ﬁxed eﬀects. Though the estimate of the trend break in scores starting in the
year of internet installation is positive and signiﬁcant, we also observe a (statistically insigniﬁcant)
pre-trend. This suggests that cross-sectional variation across schools may not account for selection
into internet access following test score growth. In column 2, we add school ﬁxed eﬀects to account
for time-invariant school-level unobservables. Basing identiﬁcation on only the within-school
variation in internet connectivity reveals a positive trend break at the time of installation, with
no pre-trend. This speciﬁcation also shows a larger level improvement in scores upon installation
(0.029), but we are unable to statistically distinguish this eﬀect from zero. Finally, we present
our preferred speciﬁcation in column 3, which includes additional controls for time-varying school
resources. Based on this speciﬁcation, estimates of both the level shift and trend break are positive
and statistically signiﬁcant, while the estimate of the pre-trend is close to zero and fairly precise.

Using our preferred speciﬁcation to linearly approximate the dynamic eﬀects of internet access,
we ﬁnd a level improvement of 0.036 standard deviations upon installation and an additional 0.047
standard deviation gain in each later year. We take care to note a particular limitation of our analysis
that stems from evaluating only the short and medium run eﬀects of internet installation: from
Figure 2.3, it is unclear when exactly the positive eﬀects of internet on math scores level oﬀ (as
opposed to continuing to rise at the rate estimated in Table 2.1). It may therefore not be appropriate
to extrapolate these results over much longer term time spans.

2.4 Robustness checks

In this setting, identiﬁcation of the impact of school-based internet access on student performance
may be confounded if the timing of internet access is non-random within schools. However,

61

Table 2.1: Internet Access & Test Scores: Trend Break Results

Dependent Variable: School Average Standardized Math Score

Only Year
Fixed Eﬀects

(1)
0.017
(0.021)
0.046***
(0.011)
0.014
(0.010)
31,368
5,903
Yes
No
No

Adding School
Fixed Eﬀects

(2)
0.029
(0.020)
0.043***
(0.011)
-0.008
(0.010)
31,368
5,903
Yes
Yes
No

Post-internet Access

Post-internet Access

× Event Time

Event Time

Observations
Number of Schools
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying Controls

Adding Time-
varying Controls

(Baseline)

(3)

0.036*
(0.020)
0.047***
(0.011)
-0.001
(0.010)
31,368
5,903
Yes
Yes
Yes

The sample includes all public schools that gained internet access between 2007 and 2014 and are observed at least
twice. Standard errors are clustered by school. Math scores are standardized to have mean zero and standard deviation
of 1 across the universe of schools reporting scores within each calendar year. Post-internet access is a dummy variable
for whether a school has gained internet access (i.e. t >= 0). Note that due to the timing of the Censo Escolar relative
to the ECE exam, some schools receive internet access in t = 0 while some receive it in t = 1. For more details, see
Section 2.3.1. Event time is years relative to internet access. Control variables include enrollment, number of second
grade students scheduled to take the ECE, facilities (computer room, library, administrative oﬃces), and resources
per student (classrooms, computers, and teachers).
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

conditional on school ﬁxed eﬀects, our analysis in Section 2.3 oﬀers no signs that the timing of
internet access relates to prior test performance. In this section, we address several other potential
challenges to identiﬁcation, namely endogenous changes in sample composition in terms of both
schools and students (including non-random attrition), concurrent changes in school resources, and
diﬀerential regional shocks and school-level pre-trends.

2.4.1 Changes in sample composition

Due to utilizing an unbalanced panel (schools are included when they participate in the ECE)
observed over a limited window of time (2007-2014), it is possible that our estimated treatment
eﬀects to some extent reﬂect changes in sample composition. Namely, identiﬁcation of pre-trends
and treatment eﬀects might rely on largely diﬀerent samples of schools. In Section 2.4.1.1, we ﬁnd

62

that our estimates are not contaminated by this issue or by school-level attrition. Additionally, we
consider also that the composition of students within schools may change in response to internet
access. For instance, internet access may attract a diﬀerent pool of students to a school (either from
other schools or from non-school activities). Section 2.4.1.2 presents evidence that this manner of
endogenous student sorting does not occur in our sample.

2.4.1.1 Unbalanced panel and attrition

Because some schools in our main sample are observed only prior to internet installation while
others are observed only after (ﬁxed eﬀects estimation only precludes including schools without at
least two years of data), it is possible that the pre-internet coeﬃcients and trends are identiﬁed from
a diﬀerent set of schools than those identifying the post-internet treatment eﬀects. Unfortunately,
the likelihood of observing a school’s pre-internet years versus post-internet years is furthermore
naturally inﬂuenced by the date of internet installation (in the extreme case, we of course do not
observe the pre-period of any school that installed internet in 2007). If these schools in actuality
experienced non-zero pre-trends, our estimates will not take these into account. On the other hand,
schools that installed internet in 2014 are not observed post-internet and can only be used to identify
pre-internet coeﬃcients/trends. Even though these schools may show no pre-trends, it is possible
that they also go on to experience zero (unobserved) eﬀects of internet access.

Figure 2.4 and column 2 of Appendix Table B.5 suggest that our main ﬁndings are not driven
by these school-level sample composition issues. Speciﬁcally, we restrict the sample to schools
that appear at least twice prior to and twice following internet installation, i.e. schools for which
we observe both pre-trends and treatment eﬀects.18 In this sample, which we refer to as the “2 Pre,
2 Post” sample, we ﬁnd no statistically signiﬁcant trends in performance prior to internet access,
and the estimated eﬀects are similar in magnitude and show similar dynamics as those using the
18This limits our sample to schools that gained access to the internet during a span of four (rather
than the full eight) calendar years. Our restricted sample includes only 3,670 schools versus the
5,903 in the main sample, but is highly comparable along many observable dimensions — including
student achievement (see Appendix Table B.4).

63

full sample.

Figure 2.4: Eﬀect of Internet Access in the Sample of Schools Observed in at least Two Periods
before and Two Periods after Internet Access: Event Study Results

The sample includes all public schools that gained internet access between 2007 and 2014 and are observed at
least twice prior to and twice after internet access. Coeﬃcients capture the increase in test scores relative to
the year prior to a school receiving internet access (t = −1). Note that due to the timing of the Censo Escolar
relative to the ECE exam, some schools receive internet access in t = 0 while some receive it in t = 1. For more
details, see Section 2.3.1. Control variables include enrollment, number of second grade students scheduled to
take the ECE, facilities (computer room, library, administrative oﬃces), and resources per student (classrooms,
computers and teachers). Standard errors are clustered by school.

Attrition from the panel may pose another compositional issue. Overall attrition in our sample
is 18.2%. Attrition can happen for several reasons. First, as mentioned in Section 2.2.2.1, only
schools with at least 5 second grade students and in which the language of instruction is Spanish are
required to administer the ECE exam. Therefore, observations will be missing when schools fall
below the threshold of 5 students (or which switch to an instructional language other than Spanish).
Some schools might have experienced permanent reductions in their second grade enrollment (and
drop from the sample at some point) and some others might “bounce” around the ECE enrollment
threshold (for example, a school might have ﬁve second graders during a year and only four during
the next year). Appendix Table B.6 shows that about half of overall attrition is likely due to a

64

school dropping below the enrollment threshold.19 The remaining attrition is either due to missing
ECE scores for another reason or missing CE (covariate) information. Only a very small portion
of attrition is due to school closures.

To illustrate that attrition does not aﬀect our results, we estimate equation 2.1 on the restricted
sample of schools that are observed for the entire sample period, i.e., the fully balanced sample.
The results are displayed in Figure 2.5 and Appendix Table B.5. It is clear that using the restricted
sample makes the estimates much less precise overall and that the short-run estimates are somewhat
smaller than in the baseline results. However, the pattern of eﬀects is otherwise very similar. In
fact, the 2- and 3-year post installation eﬀects appear even larger in this sample (Figure 2.5).

There are several important caveats to using the fully balanced sample. First, we are only
able to identify eﬀects for an evaluation window that spans seven periods, t = −3 to t = 3. This
considerably limits our ability to study the dynamic path of eﬀects, compared with our main results.
Second, this limits the identifying variation to only schools gaining access in 2009 and 2010. Third,
the balanced panel restriction shrinks the sample of schools shrinks considerably, from 5,903 to
1,043. Schools in the balanced sample appear to be higher achieving and larger compared with
the full sample overall (see Appendix Table B.4). In Appendix Table B.5 we display the results
of estimating equation 2.2, ﬁrst reproducing the results for the full sample using the restricted
evaluation window (column 3) and then using the balanced sample (column 4). In the balanced
sample, the trend break is large but imprecisely estimated. In line with the event study results in
Figure 2.5, the immediate impact (level shift) in this sample is small (the point estimate is actually
negative) and not statistically signiﬁcant.20

19A third is due to a school having fewer than 5 second grade students and an additional sixth is
explained by having enrollment “near” the threshold (deﬁned as having 5-7 second grade students).
20The data are not well suited to other methods of accounting for non-random attrition. For
example, Lee bounds are not appropriate in this context because it is not clear whether the internet
access would aﬀect attrition monotonically . We do not consider inverse probability weighting
because around 25% of attrited observations are missing covariate information.

65

Figure 2.5: Eﬀect of Internet Access in the Sample of Schools Observed in All Periods: Event
Study Results

The sample includes includes all public schools that gained internet access between 2007 and 2014 and are
observed for the entire sample period. Coeﬃcients capture the increase in test scores relative to the year prior
to a school receiving internet access (t = −1). Note that due to the timing of the Censo Escolar relative to the
ECE exam, some schools receive internet access in t = 0 while some receive it in t = 1. For more details, see
Section 2.3.1. Control variables include enrollment, number of second grade students scheduled to take the ECE,
facilities (computer room, library, administrative oﬃces), and resources per student (classrooms, computers, and
teachers). Standard errors are clustered by school.

2.4.1.2 Student composition and endogenous sorting

Another related issue is that the composition of students within schools may change in response
to internet access. A priori, it is hard to tell the direction of the bias that this would entail. If we
consider that gaining internet access might signal an increase in the quality of education in a school,
two things can happen. It might be that parents who would not have sent their kids to school (at
all) decide to enroll their children in a school connected to internet. If internet connectivity attracts
students that would have otherwise performed poorly in school, then our estimates of treatment
eﬀects are likely conservative. Alternatively, motivated parents seeking learning opportunities for
their children may decide to transfer students from schools without internet to schools that gained
connectivity. If these new students are better achievers on average, then our ﬁndings of positive

66

treatment eﬀects may owe to upward bias from changes in student composition.

Overall, it does not appear plausible that an inﬂux of high-achieving transfers or re-entrants
explains the performance gains in our main results. To rule out this possibility, we ﬁrst analyze the
response of grade 2 transfers and re-entry to internet access in columns 1-2 of Table 2.2. Transfers
are students enrolled in the current year who were enrolled in a diﬀerent school in the previous
year. Re-entrants are students that are currently enrolled but who were not enrolled in any school
during the previous year (i.e., dropouts who come back to school). It appears that schools gain
about 0.293 second grade transfers in the year that internet is introduced and that transfers increase
by about 0.167 students in every subsequent year (column 1). However, these increases are small
relative to total grade 2 enrollment (enrollment in grade 2 was 31.5, on average, prior to internet).
For example, the results in column 1 predict that 5 years after internet, there will be in total about
1.1 additional transfer students. Given that 31.5 students on average take the ECE each year, it is
unlikely that one additional student can substantially contribute to the observed increase in average
test scores.21 There are no apparent eﬀects of internet access on grade 2 re-entry, though there are
very few re-entrants to begin with (column 2).

Nevertheless, even if total enrollment remains relatively unchanged in response to internet
connectivity, the makeup of the students that take the test could still change. For example, if
internet availability induces attendance, then a diﬀerent set of students will be present to take
the test after a school gains internet access. We investigate this possibility in columns 3 and 4
of Table 2.2. Column 3 examines the eﬀect of internet on the number of students scheduled to
take the ECE, conditional on the total number of grade 2 students enrolled. It appears that, after
internet is introduced to a school, the number of test takers actually declines by 0.334 students.
Not only is this eﬀect likely too small (and, for this scenario, in the “wrong” direction) to drive the
estimated eﬀects of internet access, but this also represents a one-time decrease in the number of
test takers — which is unlikely to explain gradual performance gains that occur over time. These
21Additionally, the number of grade 2 transfer students is unrelated to test scores (point estimate
= 0.0003, p-value = .619) in a regression including school and year ﬁxed eﬀects and the controls
listed in Section 2.3.1.

67

results are consistent with Cristia et al. (2017) and He et al. (2008), who ﬁnd that neither hardware
nor CAI/CAL interventions have any signiﬁcant eﬀects on attendance.22 In column 4, we further
explore whether student background changes in response to internet access. The only information
on the background of students in the Censo Escolar is the proportion of native Spanish speakers
enrolled.23 To the extent that native language captures student background, it does not appear that
internet access attracts more advantaged students. Overall, the evidence in Table 2.2 does not seem
to indicate that endogenous student sorting drives our estimated impacts of internet access.

2.4.2 Concurrent changes in school resources

Timing of internet access may also possibly correlate with changes in other school resources. For
example, it might be that internet provision is bundled with other inputs in a multifaceted approach
to improve quality of schooling.24 If this is the case, the improvement of students’ performance
that we observe might be due to increases in these other resources.
In general we do not ﬁnd
that the timing of internet access is correlated with increases in other observable inputs such as
teachers, classrooms, or textbooks (Table 2.3). Though teachers per student rises slightly after
internet access, this eﬀect is small both in absolute terms and relative to the pre-internet mean
(column 1). Therefore we ﬁnd it unlikely that such a small shift in teachers per student explains our
main ﬁndings. Classrooms per students actually fall very slightly after internet access (a one-time
shift, column 2). In column 3, we report small and statistically insigniﬁcant changes in the number
of textbooks per student in schools that gain access to internet.

22Relatedly, Cristia et al. (2014) ﬁnd no eﬀects of computer and internet access on enrollment,

grade repetition, or dropout in secondary public schools in Peru.

23The proportion of Spanish-speaking students is positively related to higher test scores, even

after conditioning on school and year ﬁxed eﬀects and the controls listed in Section 2.3.1.

24It could also be the case that internet access at schools is highly correlated with alternative
sources of internet. For example, it might be that students who gain internet access at school
already have internet connections at home or go to cyber-cafes. However, we ﬁnd that only 23%
(32%) of students with access to internet at school also use it at cyber-cafes (at home) according to
the 2014 Peruvian National Household Survey (ENAHO). Additionally, our results are unchanged
if we include a control for whether the town nearest the school has a cyber cafe; results available
upon request.

68

Table 2.2: Eﬀect of Internet Access on Grade 2 Transfers, Re-entry, Test Taking, and Student
Composition

Grade 2 Grade 2
Transfers Re-entry

Scheduled to

Take Test

(1)

(2)

Grade 2
Students

(3)

Proportion of
Native Spanish

Speakers
in Grade 2

(4)

Post-internet Access

0.293**
(0.120)
Post-internet Access X Event Time 0.167***
(0.061)

Pre-internet mean
of dep. variable
Observations
Number of Schools
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying controls

0.028
(0.031)
0.005
(0.017)

0.372
31,368
5,903
Yes
Yes
Yes

-0.334*
(0.179)
-0.133
(0.104)

30.89
31,368
5,903
Yes
Yes
Yes

-0.002
(0.005)
0.000
(0.002)

0.850
31,357
5,903
Yes
Yes
Yes

2.866
31,368
5,903
Yes
Yes
Yes

Transfers are students enrolled in the current year who were enrolled in a diﬀerent school in the previous year. Re-entrants
are students that are currently enrolled but who were not enrolled in the previous year. The sample includes all public
schools that gained internet access between 2007 and 2014 and are observed at least twice. Standard errors are clustered
by school. Math scores are standardized to have mean zero and standard deviation of 1 across the universe of schools
reporting scores within each calendar year. Post-internet access is a dummy variable for whether a school has gained
internet access (i.e. t >= 0). Note that due to the timing of the Censo Escolar relative to the ECE exam, some schools
receive internet access in t = 0 while some receive it in t = 1. For more details, see Section 2.3.1. Event time is years
relative to internet access. Control variables include enrollment, number of second grade students scheduled to take the
ECE, facilities (computer room, library, administrative oﬃces), and resources per student (classrooms, computers, and
teachers). Columns 1-3 controls for both second grade enrollment and enrollment in other grades separately, not including
transfers or re-entrants when speciﬁed as an outcome variable. Column 4 also controls for the number of second grade
students scheduled to take the test.
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

However, in column 4, we note a positive and non-negligible level increase in computing
resources at the time of internet installation (on the other hand, the estimate of the trend break
is near zero and statistically insigniﬁcant). To better understand the potential for increases in
computers to confound our estimates of the impact of internet access, we perform some back-of-the
envelope calculations. Note that, by deﬁnition, internet connection is complementary to computer
access (i.e., generally students cannot use the internet without computers). However, students might
nevertheless beneﬁt from computers without access to internet (e.g., using preloaded software and
Joint increases in computer and internet
resources installed from ﬂash drives / DVDs, etc.).

69

Table 2.3: Eﬀect of Internet Access on School Resources

Post-internet Access

Post-internet Access X Event Time

Pre-internet mean
of dep. variable
Observations
Number of Schools
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying controls

Teachers
per Student

(1)

Classrooms
per Student

(2)

0.003***
(0.001)
0.002***
(0.001)

0.0552
31,368
5,903
Yes
Yes
Yes

-0.005*
(0.003)
-0.001
(0.001)

0.0721
31,368
5,903
Yes
Yes
Yes

Textbooks Computers
per Student
per Student

(3)

(4)

-0.132
(0.088)
-0.063
(0.046)

3.932
23,636
5,857
Yes
Yes
Yes

0.045***
(0.006)
-0.001
(0.003)

0.0676
31,368
5,903
Yes
Yes
Yes

In column 3, the dependent variable is the number of 2nd grade textbooks per 2nd grade student. In column 4, the
dependent variable is the number of instructional computers per student. The sample includes all public schools that
gained internet access between 2007 and 2014 and are observed at least twice. Standard errors are clustered by school.
Math scores are standardized to have mean zero and standard deviation of 1 across the universe of schools reporting
scores within each calendar year. Post-internet access is a dummy variable for whether a school has gained internet access
(i.e. t >= 0). Note that due to the timing of the Censo Escolar relative to the ECE exam, some schools receive internet
access in t = 0 while some receive it in t = 1. For more details, see Section 2.3.1. Event time is years relative to internet
access. Control variables include enrollment, number of second grade students scheduled to take the ECE, facilities
(computer room, library, administrative oﬃces), and resources per student (classrooms, computers, and teachers).
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

availability might thus possibly imply that our estimates capture (at least partially) the utility of
computers themselves apart from internet access.

By our calculations (displayed in Appendix Table B.8), we ﬁnd that the increase in computers
alone explains very little of the observed rise in test scores (at most, 6%). For these calculations
we use two pieces of information: (i) the impact of internet access on computer resources and
(ii) the impact of computer resources alone (i.e., without connections to the internet) on student
test scores. Our estimate of (i) comes from column 4 of Table 2.3 above. The pre-internet yearly
increase in computers is 0.034 (not shown in the table), suggesting that the approximate rise in
computers t years after internet access follows the formula 0.045 + 0.034 × t. To approximate (ii),
we use the sample of schools that do not gain access to the internet during our sample period and
regress math scores on computers per student (including school and year ﬁxed eﬀects as well as

70

all of the same controls listed in Section 2.3.1). These results are displayed in Appendix Table
B.7. In each successive column, we add in lags of computers per student to allow for dynamic
eﬀects of computing resources on student performance. Using both (i) and (ii), we can calculate the
approximate gain in math scores that is due to increases in computing resources (without internet
access) that occur around the introduction of internet.

Appendix Table B.8 displays these calculations. For t = 0, this calculation is relatively
straightforward: we see a rise in computers per student of 0.045, from which we would expect
a gain of 0.045 ∗ 0.031 = 0.001 standard deviations (relative to t = −1) based on the largest
estimate of contemporaneous computing resources’ impact on test scores (0.031, from column 1 of
Appendix Table B.7). From our event study speciﬁcation, our overall estimated eﬀect of internet
access at t = 0 is 0.042 standard deviations. Therefore, we estimate that the increase in computers
per student at t = 0 explains only about 3.3% of the rise in test scores that we observe in response to
internet access. The calculations for other post-internet periods are more complex when the eﬀect
of computers is allowed to be dynamic. However, our most “generous” estimates indicate that, at
most, acquisition of more computers explains about 6% of the estimated gains in math following
internet access.25

2.4.3 Diﬀerential pre-trends

Another possibility is that access to internet is correlated with pre-existing trends at the regional
level. For example, states with faster growing economies might be better able to ﬁnance internet
expansions, increase public spending on education, or otherwise improve student learning. Hence,
in Table 2.4 we re-estimate equation 2.2 including state-speciﬁc trends to allow for diﬀerential
25To get the “most generous” estimates, we take the largest individual estimated eﬀect of
computers for each lag across all speciﬁcations in Appendix Table B.7, regardless of signiﬁcance
level. Reassuringly, results with and without controlling for computers are virtually identical (post-
internet event study coeﬃcients are slightly - but not statistically signiﬁcantly - smaller when we
do not control for computers); results available upon request. These conﬁrm the conclusion of
our calculations in Appendix Table B.8; namely, that concurrent (one-oﬀ) increases in computing
resources at the time of internet installation do not aﬀect our estimated impacts of internet access.

71

pretreatment trajectories in academic performance driven by such state-level factors. Our results
are robust to the inclusion of state-speciﬁc pre-trends (column 2), as well as to allowing pre-trends
to diﬀer by state-sector (i.e. urban/rural) (column 3).

Table 2.4: Allowing for State, State-Sector, and School-speciﬁc Pre-trends

Dependent Variable:

School Average Standardized Math Score

Baseline

(1)

0.036*
(0.020)
0.047***
(0.011)
31,368
5,903
Yes
Yes
Yes

Post-internet Access

Post-internet Access

X Event Time

Observations
Number of Schools
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying controls

State-speciﬁc State-Sector School-speciﬁc
Pre-trends

Pre-trends

Pre-trends

(4)

(2)

(3)

0.039**
(0.020)
0.045***
(0.010)
31,368
5,903
Yes
Yes
Yes

0.038*
(0.020)
0.041***
(0.010)
31,368
5,903
Yes
Yes
Yes

0.024
(0.029)
0.031
(0.038)
22,321
3,670
Yes
Yes
Yes

In columns 1-3, the sample includes all public schools that gained internet access between 2007 and 2014
and are observed at least twice. Standard errors are clustered by school. In column 3, the sample is further
restricted to schools that are observed at least twice prior to and after gaining internet access. Math scores
are standardized to have mean zero and standard deviation of 1 across the universe of schools reporting scores
within each calendar year. Post-internet access is a dummy variable for whether a school has gained internet
t >= 0). Note that due to the timing of the Censo Escolar relative to the ECE exam, some
access (i.e.
schools receive internet access in t = 0 while some receive it in t = 1. For more details, see Section 2.3.1.
Event time is years relative to internet access. Control variables include enrollment, number of second grade
students scheduled to take the ECE, facilities (computer room, library, administrative oﬃces), and resources
per student (classrooms, computers, and teachers) as well as the additional ﬁxed eﬀects and/or time trends
indicated in each column heading (columns 2-4). Standard errors are clustered by school.
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

To also examine whether school-speciﬁc trends may confound our identiﬁcation, column 3
of Table 2.4 augments our equation 2.2 speciﬁcation with linear trends that are speciﬁc to each
school. Note that the inclusion of school-speciﬁc pre-trends limits our sample to those schools
within which we can identify both pre- and post-internet trends: namely, our “2 Pre & 2 Post”
sample. Accounting for diﬀerential pre-trends produces positive, albeit smaller and statistically
insigniﬁcant, estimates of the trend breaks and level increases from our main analysis. It is worth
emphasizing that the estimation of school-speciﬁc linear trends — which add an additional 3,670

72

covariates to the model — likely absorbs much of any potential exogenous variation in test scores
and internet access. As expected, precision drops considerably in this speciﬁcation. Thus, while
we are unable to reject the null hypothesis of zero eﬀects when including the additional trends, we
are also unable to reject that these estimates are equal to our baseline estimates.

2.5 Explaining dynamics and identifying potential mechanisms

In this section, we present some suggestive evidence to aid interpretation of our main results.
First, we show that the dynamic pattern of eﬀects of internet access in the years following installation
may be explained by the need for complementary investments in resources: namely, teachers with
formal training in digital skills. We then explore two potential mechanisms by which internet
access improves student learning: supplementing individualized teacher attention and mitigating
low teacher quality.

2.5.1 Why do the eﬀects of internet access take time to emerge?

One explanation for why we observe delayed impacts of internet access may be that schools
require teachers with digital and internet skills in order to incorporate the new technology into
the classroom. To investigate this possibility, we study whether schools respond to internet access
by hiring teachers with expertise in “computer and information technology.” This includes both
teachers trained to teach computer skills, as well as teachers who themselves underwent advanced
education relating to computers; hereafter, these are referred to as “computer teachers.” We estimate
equation 2.1 using an indicator for the presence of a computer teacher as the outcome.26

Figure 2.6 shows that internet access is accompanied by a slow but steady increase in the
likelihood a school has a computer teacher; by year 5, this results in a doubling of the pre-internet
likelihood. When taken together the ﬁndings for computer teachers and test scores are consistent
with the idea that schools may need time to make complementary investments to fully exploit new
26We use a dummy for the presence of a computer teacher rather than the number of computer
teachers because less than 3% of schools have more than one computer teacher in any given year.

73

classroom technologies, such as teachers with computer training.

Figure 2.6: Internet Access and Presence of a Computer Teacher

Coeﬃcients capture the increase in the likelihood of having a computer teacher on staﬀ relative to
the year prior to a school receiving internet access (t = −1). Note that due to the timing of the Censo
Escolar relative to the ECE exam, some schools receive internet access in t = 0 while some receive
it in t = 1. For more details, see Section 2.3.1. Control variables include enrollment, number of
second grade students scheduled to take the ECE, facilities (computer room, library, administrative
oﬃces), and resources per student (classrooms, computers, and teachers). The sample includes all
schools with at least two observations within the sample period (2007-2014). Standard errors are
clustered by school.

2.5.2

Increased individualized attention

Previous work suggests that ICTs may enable providing students with more individualized attention
than they would otherwise receive from teachers. To explore whether increased individualized
attention might explain our results, we follow Barrow et al. (2009) and examine heterogeneity
along the lines of class size. In theory, teachers divide their time in classrooms between group and
individualized instruction. If ICTs reduce the time teachers spend in group activities, they might
be able to increase the time they allocate to individualized instruction. Teachers might be more
constrained in providing individualized instruction when they have more students, so gains from

74

ICTs should be larger in large classes relative to small classes. Therefore, we expect the eﬀects of
internet access to matter more for schools with high versus low student to teacher ratios (STR).

Indeed, we ﬁnd that the positive eﬀects of internet access are concentrated among schools with
high STRs when schools are split by the pre-internet median STR. We deﬁne “high STR” and “low
STR” groups as follows. First, we calculate the total number of teachers per second grade student.
We do not use the number of teachers exclusively dedicated to second grade, as many smaller
schools have teachers that cater to multiple grades. Then, we calculate each school’s pre-internet
average STR (time-invariant). Finally, we divide the schools into high and low STR groups based
on having a pre-internet average STR above or below the median.27 In Figure 2.7a, the high and
low STR trends in test scores prior to internet access are nearly identical, but diverge once internet
is introduced. In low STR schools, the eﬀects are much smaller though the estimates are not very
precise in either subsample. Appendix Table B.10 (Columns 1-2) conﬁrms that the trend break in
test scores is larger and only statistically signiﬁcant in high STR schools, though the point estimate
of the immediate eﬀect of internet access is larger in low STR schools.28 Thus, these results are
qualitatively consistent with increased individualized attention as a causal pathway through which
internet access improves student performance.29

2.5.3 Substitution between internet access and teacher qualiﬁcations

Another possibility is that ICTs generate gains in student learning because they compensate for
the lack or low quality of other inputs. Relatedly, some have found that the success of ICT
27The average 2nd grade student-teacher ratios in the high and low STR groups are 8.28 and

2.77, respectively.

28The diﬀerence in the estimated trend break across the two samples is is marginally statistically
signiﬁcant; p-value = 0.139. The diﬀerence in level shifts is not statistically signiﬁcant; p-value =
0.866.

29Another way to investigate the mechanism of individualized instruction would be to look for
heterogeneity by student attendance (see Barrow et al. 2009). However, we do not have data
on attendance or any other student characteristics (e.g., prior achievement as in Bai et al. 2016,
Barrow et al. 2009, Linden 2008, He et al. 2008, Mo et al. 2015, and Muralidharan et al. 2016 or
age and gender as in Linden 2008) that would allow investigating heterogeneity along individual
dimensions.

75

Figure 2.7: Heterogeneity in the Impact of Internet Access on Test Scores: Event Study Results

Heterogeneity by Student to Teacher Ratios

Heterogeneity by Teacher Qualiﬁcations

Figure (a): The sample is split based on each school’s pre-internet average ratio of second graders to total teachers (STR) —
high (low) STR schools fall above (below) the median pre-internet STR. Figure (b): The sample is split based on each school’s
pre-internet average number of teachers with a pedagogical or higher education degree per student over the sample period relative
to the median of all schools’ sample averages. Coeﬃcients capture the increase in test scores relative to the year prior to a school
receiving internet access (t = −1). Note that due to the timing of the Censo Escolar relative to the ECE exam, some schools receive
internet access in t = 0 while some receive it in t = 1. For more details, see Section 2.3.1. Control variables include enrollment,
number of second grade students scheduled to take the ECE, facilities (computer room, library, administrative oﬃces), and resources
per student (classrooms, computers, and teachers). The sample includes all schools with at least two observations within the sample
period (2007-2014). Standard errors are clustered by school.

76

interventions may depend on whether they displace traditional instruction or constitute additional
learning activities outside of traditional classroom hours (as part of an after school tutoring program,
for example, as in Linden 2008). In cases where ICTs substitute for traditional instruction, impacts
may depend on the quality of instruction that the new technology is displacing. Such is hypothesized
in Bulman and Fairlie (2016, p. 20), “[...] Interestingly, evidence of positive eﬀects appears to be
the strongest in developing countries. This could be due to the fact that the instruction that is being
substituted for is not as of high quality in these countries.”

To shed some light on whether internet access may substitute for low teacher quality in the
context of our study, we examine heterogeneity in results by the level of qualiﬁcation that a
school’s teachers have obtained. In Figure 2.7b, we see that schools with low teacher qualiﬁcations
experience relatively larger gains in test scores over time, though all schools see a moderate rise in
scores immediately following access. The trend break among low teacher qualiﬁcation schools is
large (0.063 standard deviations per year after internet access) and statistically diﬀerent from the
trend break among high qualiﬁcation schools (columns 3 and 4 in Appendix Table B.10). Here,
we measure teacher qualiﬁcation as the per student number of teachers with a pedagogical or
university degree. We estimate the average ratio of qualiﬁed teachers-to-students by school using
the pre-internet period, and split the sample in two groups based on the sample median across
schools. Those with ratios above (below) the sample median are classiﬁed as schools with “high”
(“low”) teacher qualiﬁcations.30

These results align with ﬁndings from other contexts, such as Jackson and Makarin (2016),
who determine that the beneﬁts — in terms of math achievement — of providing teachers with
online access to “oﬀ the shelf” lesson plans were larger among students with weaker teachers.
Importantly, if technological tools can substitute for teacher quality, ICT interventions such as
school-based internet may help poor schools narrow or close achievement gaps vis-à-vis wealthier
30Though STR and teacher quality measures are related, schools with high and low teacher
qualiﬁcation are distinct from schools with high and low STR; about a quarter of high qualiﬁcation
schools are high STR schools and around 18% of low qualiﬁcation schools are low STR schools.
The analysis in Figure 2.7b and Appendix Table B.10 also control for the overall STR.

77

schools.

2.6 Conclusions

We ﬁnd evidence that the introduction of internet to Peruvian primary schools produces
economically meaningful improvements in student performance (as measured by standardized
test scores for grade 2). Gains increase over time, growing from 0.042 standard deviations in
the year of installation to 0.29 standard deviations 5 years after installation.
Importantly, there
are no apparent pre-existing trends in math test scores prior to internet access, suggesting little
role for reverse causality. Using a trend break speciﬁcation, we conﬁrm that there is a level shift
and (linear) trend break in test scores that occurs at the time of internet access. In the medium
term, the yearly gain in test scores is about 0.047 standard deviations. These results, which are
representative of about one quarter of all public primary schools in Peru, are robust to a number
of potential confounding factors, including changes in sample composition with respect to either
schools or students, changes in school resources, and endogenous timing of installation with respect
to prior trends in test performance. In our setting, the nationwide scale of roll-out, large sample of
schools, and extended time frame uniquely enable the analysis of this technology’s application at
the farthest-reaching level of policy.

On the one hand, previous research on ICTs has found that providing hardware with few or
no complementary learning tools has little immediate impact on student performance (Bet et al.
2014; Barrera-Osorio and Linden 2009; Cristia et al. 2017; etc.). Our short run results (based on
up to 1 year after internet installation) conﬁrm that any eﬀects are small in magnitude — and thus
perhaps impossible to detect in the small samples used by this literature’s many RCT studies. On
the other hand, medium run gains are sizable, pointing towards the necessity of a longer evaluation
window for understanding the eﬀectiveness of ICT interventions. Ultimately, our estimated eﬀects
of internet access for years 2-5 still fall below prior estimates of the impact of computer assisted
learning and instruction. Even so, while school-based internet does not fully confer the beneﬁts
of individualized pedagogical tools, it may provide access to learning resources that are otherwise

78

unavailable to many students in developing countries.

We provide supporting evidence that achievement gains are slow to emerge because schools
need time to adapt to new technologies. Speciﬁcally, after installing internet public schools require
time to augment their staﬀ with teachers experienced in computers and information technology.
We thus concur with several prior studies ﬁnding that student achievement begins to increase only
as teachers learn to integrate new technology into their curricula (Hull and Duch 2016, Mo et al.
2013, Sprietsma 2007).

Our data also yield evidence suggestive of two channels through which school-based internet
access facilitates human capital accumulation: allowance of greater individualized instruction and
substitution for low teacher qualiﬁcations. Gains in math scores are concentrated among schools that
have high student-teacher ratios and in which relatively few teachers hold pedagogical or university
degrees. Hence, school-based internet may generate important gains in learning particularly when
individualized instruction and teacher quality are constrained below the optimum.

However, interpretation of the results presented is subject to a number of limitations. Perhaps
most notably, school-level analysis may mask important individual-level dynamics. We are largely
unable to explore heterogeneity in the eﬀectiveness of school-based internet based on student
characteristics.
Indeed, previous work suggests that individual heterogeneity - especially with
regard to initial achievement - signiﬁcantly determines how technology aﬀects the learning process
(Bai et al. 2016; Barrow et al. 2009; Linden 2008; He et al. 2008; Muralidharan et al. 2016).
Future research on heterogeneous impacts of internet in education could bear broad implications
for inequality within and across learning environments.

79

CHAPTER 3

DISCRETIONARY SCHOOL DISCIPLINE POLICIES AND DEMOGRAPHIC

DISPARITIES

3.1 Introduction

Despite ostensibly race neutral disciplinary policies, large racial disparities in student suspensions
and expulsions persist throughout the U.S., causing Black students in particular to miss more days
of school than their peers. During the 2011-12 school year, Black students nationwide comprised
only 16% of enrollment, but 32% of students suspended and 42% of students expelled (Green,
2015). Furthermore, this magnitude of disproportionality in disciplinary outcomes manifests as
early as preschool: in the same year, Black students accounted for 18% of preschool enrollment
nationwide, but fully 42% of preschoolers suspended once and 48% of preschoolers suspended
multiple times (Smith and Harper, 2015). Recent research also indicates that punitive measures
(e.g.
suspensions, expulsions, and juvenile justice referrals), as opposed to restorative justice
practices and medicalized approaches, form a higher proportion of disciplinary measures faced by
Black and Hispanic students compared with peers (Ramey, 2015; “Trey” Marchbanks III et al.,
2016; Welch and Payne, 2018).1

Evidence suggests that exclusionary school discipline and the associated loss of instruction
time adversely impacts recipients’ academic performance, as well as later life labor outcomes and
contact with the criminal justice system (i.e. the oft referenced “school-to-prison pipeline”). From
a large scale study of thousands of middle and high schoolers, Morris and Perry (2016) estimate
that roughly a ﬁfth of the black-white academic achievement gap can be attributed to the gap in
1“Trey” Marchbanks III et al. (2016) analyzes statewide data from the Texas Education Research
Center, establishing a positive association between school minority composition and juvenile justice
referrals. Based on nationally representative data, Ramey (2015) and Welch and Payne (2018)
determine that schools with greater minority composition are more likely to employ punishment
and deterrence over milder or corrective methods.

80

suspensions.2 In particular, Aucejo and Romano (2016) ﬁnd that the penalty in math and reading
scores resulting from absences is larger in magnitude than the beneﬁt resulting from extra days
of instruction; this implies that extrapolating from studies of the eﬀects of extended school years
leads to an underestimate of the impact of the discipline gap on achievement.3 In terms of non-
cognitive outcomes, students who are suspended or expelled are “placed at risk of delinquency
and incarceration” due to removal from the structured school environment (Krezmien et al., 2014).
Perhaps unsurprisingly, dropouts who report feeling “pushed out” of school due to disciplinary
issues ultimately commit more property and drug crimes and record more frequent arrests than
peers who are similar in a broad array of home and community observables — including childhood
household income, family structure, having had a teenage mother, having attended schools with
gangs present, and urban location (Bjerk, 2012). Moreover, comparing pairs of siblings in the
NLSY79, Campbell (2015) observes lower incomes and fewer weeks worked in a year among
dropouts, even after accounting for sibling ﬁxed eﬀects.

Principally for these reasons, the Department of Education (DOE) and the Department of Justice
(DOJ) during the Obama administration together issued a guidance redeﬁning and expanding their
eﬀorts to enforce Title IV of the Civil Rights Act of 1964, which prohibits racial discrimination
Issued on January 8th, 2004, the guidance introduced the concept of disparate
in schools.
impact, stating that “a disproportionate and unjustiﬁed eﬀect on students of a particular race”
would constitute unlawful discrimination even if “the policy itself does not mention race —
and is administered in an evenhanded manner.”4 Schools and districts investigated for unlawful
discrimination can be compelled to engage in time consuming collection of evidential data, and
those found to have discriminated can be taken to court and ordered to invest in costly remedies,
2Morris and Perry (2016) observe a three-year panel of over 16,000 6th through 10th graders

across 17 schools in the Kentucky School Discipline Study.

3Aucejo and Romano (2016) ﬁnd that extending the school year by ten days raises math and
reading scores by 0.017 and 0.08 standard deviations, respectively. On the other hand, eliminating
ten days of absences raises math and reading scores by 0.055 and 0.029 standard deviations.

4For reference, see Dear Colleague Letter on the Nondiscriminatory Administration of School

Discipline (2014).

81

such as teacher training programs.

In response, California in 2014 passed the law AB 420, becoming the ﬁrst state to limit the use
of school suspensions and expulsions as punishment for “willful deﬁance.”5 Unlike other oﬀenses
listed in the state education code (e.g. having “stole or attempted to steal school property or
private property”), there is no concrete deﬁnition of what constitutes “disrupting school activities”
or “otherwise willfully defying the valid authority” of school personnel. As such, administrators
must determine at their own discretion whether or not a given student’s behavior constitutes a
suspendable/expellable oﬀense — a situation thought by state lawmakers to open the door to racial
bias and hence disparities in disciplinary outcomes.

While other work has extensively studied the relationships between school discipline, race,
and various academic and social outcomes, this paper examines a state legislated eﬀort aimed
at curbing disproportionality through reducing a certain application of discipline. As the afore
described policy is both recent and the ﬁrst of its kind, similar initiatives in the future may beneﬁt
from understanding the results and context of this speciﬁc situation. In particular, I aim to provide
the ﬁrst retrospective analysis of how disciplinary disproportionality has responded over the period.
In this paper, I provide an overview of the state’s recent progress in reducing exclusionary
discipline and disproportionality, here characterized as the diﬀerence between a given group’s
proportion of discipline and its proportion of enrollment, over the period 2012-2017.
I also
gauge the eﬀectiveness of reducing punishment of deﬁance in mitigating disproportionality, using
identiﬁcation by treatment intensity, characterized as a school’s pre AB 420 proportion of discipline
attributable to willful deﬁance.

Based on school level data on elementary school discipline and enrollment from the CA
Department of Education (CDE), exclusionary discipline has consistently and considerably declined
throughout the period. On the other hand, it is unclear that AB 420, along with lower willful
deﬁance discipline, have actually reduced disproportionality. Hence, there is so far no indication
that removing willful deﬁance from the toolbox of California educators has brought the state’s

5See California (2014).

82

schools closer to compliance with the DOE/DOJ guidance.

The rest of this paper is structured as follows: Section 3.2 reviews literature examining bias in
school discipline, Section 3.3 describes the recent legislative eﬀorts surrounding disparate impact
in California, including SB 607, proposed as a replacement for AB 420 after it expires July 2018,
Section 3.4 breaks down recent state trends in discipline and disproportionality, Section 3.5 explores
the impact of banning willful deﬁance on disproportionality, and Section 3.6 summarizes ﬁndings.

3.2 Disparities and Bias: Review of Theories and Evidence

Although not ﬁrmly establishing bias as a leading cause, recent large scale, quantitative studies
reveal that racial disparities in school discipline are not entirely explained by diﬀerences in actual
student conduct. On the one hand, students who engage in more frequent delinquency and drug use,
and who exhibit lower academic engagement and aspirations, are indeed more likely to encounter
exclusionary discipline (Mizel et al., 2016). However, Mizel et al. (2016) ﬁnd that after controlling
for self reported ﬁghting, theft, and vandalism, African Americans are still suspended and expelled
at rates higher than would be expected based on enrollment.6 Even when accounting for teachers’
own ratings of various disruptive student behaviors, Rocque (2010) still observed that teachers gave
out a disproportionate number of oﬃce referrals to African American students.7

Some literature suggests that congruence between student and staﬀ demographic background
may aﬀect both disciplinary and academic outcomes. Using statewide longitudinal data on
Texas middle and high school students, Blake et al. (2016) note that both Black and Hispanic
students experience signiﬁcantly elevated odds of discipline when moving to schools with more
racially dissimilar faculty.8 Broadly pointing to cultural diﬀerences as a source of classroom
misunderstandings, the authors posit that “teachers may unknowingly apply media-driven stereotypes
about Black culture to understand the ambiguous actions of Black students that are distinct from
6Mizel et al. (2016) collects survey data from a panel of 2,539 10th through 12th graders in 16

schools across 3 districts in Southern California.

7Rocque (2010) study a sample of over 28,000 students in 45 Virginia elementary schools, using

data from oﬃcial school records and teacher reports.

8This phenomenon varied by gender, and was particularly pronounced for Black males.

83

White, middle-class culture" (Blake et al., 2016). In terms of academic performance, Dee (2004)
estimates that being taught for one year by a teacher of the same race lead to math and reading
score improvements of 2 and 4 state percentiles,9 respectively, for both Black and White students.
Evidence of implicit bias also emerges in large sample studies of faculty and administrator
subjective perceptions of minority students. For instance, it has been documented that Black
teachers in the National Educational Longitudinal Study of 1988 are more likely to rate Black
students favorably in terms of behavioral characteristics and career prospects (Ehrenberg et al.,
1995). Conversely, White teachers in the ECLSK are more likely to give Black students poor
behavioral ratings (though Black kindergartners do not for their part appear to diﬀerentially prefer
teachers by race) (Downey and Pribesh, 2004).10 In a smaller study based on direct observation
of instructional time in a Louisiana school district, Casteel (1998) reports that White teachers both
called on Black students less frequently to answer questions, and also gave Black students less
praise for correct answers.11

In particular, from Figlio (2006), it is apparent that ad hoc discrimination in the modern era has
occurred on a large scale at least in some areas: throughout the period 1996-2000, school districts
in Florida selectively gave low achieving students longer suspensions — despite conduct policies
not explicitly diﬀerentiating between high and low performers — in order to prevent them from
inﬂuencing school performance in statewide high stakes assessments.

On the one hand, the above ﬁndings in general would suggest that minimizing faculty and
administrator discretion in disciplinary processes should lead to more equitable outcomes. On the
other hand, however, it is not clear that race gaps in discipline stem entirely from staﬀ bias. At least
across schools, Kinsler (2011) ﬁnds in administrative data from North Carolina that principal and

9Dee (2004) study test score data from the Tennessee STAR program.
10Similarly, Dee (2005) ﬁnd that teachers are more likely to deem students of other racial/ethnic
designations disruptive, regardless of whether they are White, Black, or Hispanic. Their study also
determines that this occurs across genders as well: both male and female students are face worse
assessments from teachers of the other sex.

11For an overview of smaller sample, mixed methods studies on classroom implicit bias, refer to

Irvine (1988).

84

teacher race does not explain away diﬀerences between Black and White students’ likelihood of
suspension or length of suspension. According to Kinsler (2013), the greater use of exclusionary
discipline by principals in predominantly minority schools is furthermore in fact “consistent with
achievement maximizing behavior on the part of principals”: as schools with proportionally more
minorities contain a higher concentration of individuals at risk of misbehavior, harsher punishments
are necessary to deter harmful disruptions. Note that in this case, since all students within a school
face the same schedule of punishments, large disparate impacts can arise throughout a district
absent any implicit bias by educational personnel. Importantly, one implication of this scenario
is that the use of concrete, highly speciﬁc rules for discipline within a given school should not by
itself aﬀect within-school gaps.

3.3 AB 420 and Willful Deﬁance in California Public Schools

In 2014, the California State Legislature passed AB 420, the second bill proposed since 2012
to curb the use of suspension and expulsion as punishment for “willful deﬁance.” The new law,
approved in September 2014 by Governor Jerry Brown, eliminated the option to expel students
for “disrupting school activities or otherwise willfully defying the valid authority of supervisors,
teachers, administrators, school oﬃcials, or other school personnel engaged in the performance of
their duties.” Brown had previously vetoed a similar bill, AB 2242, due to the fact that it would have
additionally banned willful deﬁance suspensions for all grades (Washburn, 2018). Unlike AB 2242,
AB 420 only banned willful deﬁance suspensions for students in Kindergarten through 3rd grade.
Sponsored mostly by democrats, AB 420 reﬂected a concern that the subjective judgments involved
in determining students to be “deﬁant” or “disruptive” opened the door for implicit bias, thereby
leading to diﬀerential punishment (Washburn, 2018). Henceforth until July 1, 2018, suspensions
and expulsions could only be issued to students found to have committed certain speciﬁcally deﬁned
acts, such as drug or weapon possession, theft, and assault.

With AB 420 set to expire prior to the 2018-19 school year, state lawmakers have recently
(as of this writing) considered implementing SB 607, the “Keep Kids in Schools Act,” to both

85

extend the current bill’s provisions on deﬁance related expulsion and also expand the ban against
deﬁance suspensions to all grades, this time for the next decade. As many educators view the
large decreases in exclusionary discipline associated with such recent eﬀorts to have increased the
diﬃculty of dealing with genuinely disruptive behavior, it is important to understand whether or
not this policy change has in fact reduced disproportionality. With proponents of SB 607 arguing
for school discipline to rely more on restorative justice (e.g. mediation)12 and Positive Behavioral
Intervention and Supports (PBIS),13 the California Teachers Association (CTA) has indicated that
its support of the bill will depend on increased funding for teacher training (Washburn, 2018).
Despite mixed evidence as to the academic beneﬁts of reducing punishment on its own, such an
expense by the state may still be justiﬁed by proven gains in equity (and hence assuring Title IV
compliance, a factor in federal education funding).

Although we might not expect to attribute a large share of suspensions to students in grades
K-3 traditionally, it appears that AB 420 did nonetheless correspond with a substantial decline in
deﬁance related suspensions. Figure 3.1 plots the average number of suspensions at schools whose
pre AB 420 proportion of suspensions attributable to deﬁance (averaged over the 2011-12 through
2013-14 school years) was above the median. Note that the solid black (thick) line plots average
total suspensions in each year only among schools having any suspensions in that year, and that
the solid red (thin) line does the same for average deﬁance related suspensions. While a gradual
decline in willful deﬁance suspensions appears to drive a decline in total suspensions throughout
the entire period, the proportion of schools issuing any willful deﬁance suspensions clearly exhibits
a sharp decline corresponding with the passage of AB 420.

It is possible that the passage of AB 420, particularly on the heels of the DOE/DOJ guidance
earlier in the year, discouraged citing students for willful deﬁance in general by a number of means.
12While varying by implementation, mediation generally entails convening a circle of peers of
the parties in conﬂict to determine steps necessary for resolution, with faculty acting in an advisory
capacity (Richmond, 2015). Resolution is intended to target root causes of speciﬁc behavior, rather
than the blunter aim of deterrence (Richmond, 2015).

13PBIS entails “implementing a multi-tiered approach to social, emotional and behavior support”

(for more details, see https://www.pbis.org/).

86

Figure 3.1: Suspensions Over Time Among Schools With Large Initial Proportion of Deﬁance
Suspensions

This graphic represents average suspensions over time among schools that gave out more than the
median pre-period average (2012-2014) proportion of willful deﬁance suspensions (as a proportion
of total suspensions).

Firstly, the bill’s passage may have caused administrators to anticipate that deﬁance suspensions
would soon be removed entirely from their toolkit, and they may thus have used this period to
adjust to other behavior management strategies for 4th and 5th graders as well. Additionally,
Babcock (2009) provides evidence that “state-level judicial-legal climate does appear to inﬂuence
administrators’ discipline policies.” Examining data from 132 middle and high schools across the
country, Babcock (2009) ﬁnds that student rights lawsuits brought by public interest law ﬁrms led
to subsequently less harsh punishments within states where the suits took place.

As AB 420 was brought about in the midst of both national and state-level coordinated shifts
towards less punitive approaches to discipline, the next section summarizes and breaks down trends
in exclusionary discipline in California from the 2011-12 through 2016-17 school years.

87

0.1.2.3.4.5.6.7.8.91 Proportion of schools with any instances0102030405060708090100Average Suspensions (schools with any) 201220132014201520162017YearSuspensionsDefiance SusupensionsProp. w/ suspensionsProp. w/ defiance suspensions3.4 Recent CA Suspensions and Disproportionality

As of this writing, administrative data on suspensions and expulsions in all California public
schools (approximately 10,500) are made available by the CA Department of Education for the
academic years from 2011-12 through 2016-17.
Information includes each school’s number of
suspensions and expulsions citing deﬁance and non-deﬁance reasons, broken down by racial/ethnic
designation. However, expulsions among elementary school students are exceedingly rare (as
shown below) and are therefore set aside in the analysis to follow.

As can be seen in panel (a) of Figure 3.2, school suspension fell signiﬁcantly in overall volume
over the period surrounding the passage of AB 420. While the proportion of schools issuing any
suspensions remained more or less constant (at around 80%), the average number of suspensions
among those schools dropped by roughly a third, from 21.7 in 2011-12 to only 13.9 in 2016-17.
In the case of suspensions speciﬁcally for willful deﬁance, a decrease in the proportion of schools
employing this method of discipline is evident (going from 57.8% in 2011-12 to 28% in 2016-17).
While we might expect this to be driven by administrators abandoning the practice who previously
had not relied heavily on it to begin with, Figure 3.1 suggests that the opposite is true: it is in fact
the schools which previously leaned most heavily on deﬁance suspensions (as a proportion of total
suspensions) that stopped. Hence, among schools that issued any deﬁance related suspensions, the
average number of these fell from 9.7 to 3.4.

In panel (b) of Figure 3.2, the proportion of schools issuing expulsions fall as well, albeit
following a notably diﬀerent pattern:
though the proportion declines slightly in the pre-period,
this trend is sharply broken upon the 2015-16 school year (one year after the passage of AB 420).
Similarly, the very slight pre-period downward trend in the average number of expulsions (among
schools issuing any) appears to reverse upon the 2015-16 school year. Among such schools,
expulsions overall actually rise from an average of 1.2 in 2011-12 to 1.4 in 2016-17. Ultimately,
the proportion of schools issuing expulsions falls from 3.5% initially to 1.8% in 2015-16, before
slightly climbing again to 2.5%.

It is unclear from the following analysis why these particular patterns emerge. While suspensions

88

Figure 3.2: Average Suspensions and Expulsions Over Time

Suspensions

Expulsions

In the above graphics, averages of suspensions/expulsions in each year are calculated based on
schools that gave out suspensions/expulsions in those years. For example, each year composing
the solid thin (red) line in panel (a) is based on schools giving out any suspensions speciﬁcally for
willful deﬁance in that year.

89

0.1.2.3.4.5.6.7.8.91 Proportion of schools with any instances0102030405060708090100Average Suspensions (schools with any) 201220132014201520162017YearSuspensionsDefiance SusupensionsProp. w/ suspensionsProp. w/ defiance suspensions0.05.1.15.2 Proportion of schools with any instances012Average Expulsions (schools with any) 201220132014201520162017YearExpulsionsProp. w/ expulsionshave recently become less popular among elementary schools, it may be the case that expulsions,
as the most severe punishment — undertaken as a last resort — have reached a functional ﬂoor: the
remaining instances might be generally necessitated by extreme situations, and therefore cannot be
reduced further. Here it is perhaps worth noting again that movements in the volume of exclusionary
discipline are not necessarily related to any particular student group’s relative proportion of citations.
In the graphs in either column of Figure 3.3, we may visualize disproportionality in suspensions
for each race category as the distance between its respective red (dashed) and black (solid) lines.
For example, the left panel of row (a) shows that Black students throughout the study period have
accounted for roughly 15-16% of suspensions, while comprising roughly 6-7% of enrollment.
Hence, overall, White students as a group are slightly overrepresented in suspensions, and Hispanic
students are underrepresented in suspensions. Like elsewhere in the country, Black students are
substantially overrepresented with respect to their enrollment in suspensions.

3.5 Role of Willful Deﬁance

3.5.1 Treatment Intensity: Initial Use of Willful Deﬁance

As noted previously, simply reducing the overall volume of exclusionary discipline does not
necessarily change disproportionality, and hence inequity as thought of by the DOE (and may
even be undesirable absent any gains in “fairness”). Thus, this paper also aims to shed light on
whether or not reducing deﬁance-related punishment alleviated racial disproportionality in school
suspension, as measured by the diﬀerence between a given group’s proportion of total suspensions
and its proportion of total enrollment.

To this end, I compare pre and post AB 420 disproportionality in exclusionary discipline across
elementary schools based on their pre-period (2012-2014) proportion of suspensions that cite the
oﬀense of willful deﬁance. With a one-time “treatment” and no control group, this approach may
be thought of as identifying eﬀects based on variation in treatment intensity. Explicitly, I assume
that elementary schools with a high pre-period proportion of discipline citing willful deﬁance are
ultimately more aﬀected by the law than those whose disciplinary citations mostly already involved

90

Figure 3.3: Disproportionality in Suspensions Over Time

All Instances

Willful Deﬁance

Black

White

Hispanic

91

.05.1.15.2201220132014201520162017Year.05.1.15.2201220132014201520162017Year.2.25.3.35201220132014201520162017Year.2.25.3.35201220132014201520162017Year.4.45.5.55201220132014201520162017Year.4.45.5.55201220132014201520162017YearTable 3.1: Eﬀects of “Willful Deﬁance” on Disproportionality in Suspensions

Diﬀerence between proportion of suspensions and proportion of enrollment
AB 420 X Initial deﬁance related proportion of discipline

(1)
Black White Hispanic

(3)

(2)

-0.035
(0.025)
.273
.261
12541
Yes
Yes
Yes

0.018
(0.014)
.159
.069
12100
Yes
Yes
Yes

0.023
(0.023)
.455
.509
12671
Yes
Yes
Yes

Initial prop. of suspensions
Initial prop. of enrollment
Observations
School FE
Year FE
Controls

Outcomes are the diﬀerences between each race category’s proportion of total suspensions and
its proportion of total enrollment. Controls include school level enrollment, proportion FRPL
eligible, and proportion English learners. Standard errors in parentheses, clustered at the district
level. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

concrete oﬀenses to begin with. Some evidence of this is shown further down in Figure 3.4. Without
suspensions by grade level, this analysis is agnostic as to whether changes in disproportionality
reﬂect schools being actually constrained by the law from issuing suspensions, versus responding
to politics or adjusting in preparation for further anticipated changes.

Yrit = β1(AB 420t × Initial W.D. prop. of discipl.i) + γXit + αi + φt + εit

(3.1)

In the above equation, Yrit represents the diﬀerence between group r’s proportion of total
suspensions and its proportion of enrollment in school i during year t. “Initial W.D. prop. of
discipline” is school i’s pre-period (2012-2014) average proportion of suspensions citing willful
deﬁance as the oﬀense being punished. Finally, Xit is a set of time-varying school level controls,14
and αi and φt are school and year ﬁxed eﬀects, respectively.

Table 3.1 shows the results of estimating Equation 3.1. As previously determined based on
Figure 3.3, overall disproportionality does not change notably from the pre period to the post period
14Control variables include overall enrollment, proportion eligible for free and reduced price

lunches (FRPL), and proportion English learners (ELL).

92

for any of the groups by race. Inspecting the coeﬃcients on the interaction term, it seems also that
the passage of AB 420 did not elicit diﬀerential responses in the overall disproportionality facing
any group based on schools’ initial proportion of discipline citing willful deﬁance.

Considering the law at face value, this is not necessarily surprising. Suppose that reducing the
volume of discipline entails pardoning a random selection of students from the pool of those who
would have been punished: although some groups would certainly see a larger number of students
pardoned, no group would mechanically achieve any gains in likelihood of discipline relative to the
others (their chances of discipline will fall by the same factor). The results of Table 3.1 may indicate
that administrators did not respond to AB 420 with particular focus on reducing the punishment
incurred by any one overrepresented group.

3.5.2 Robustness

As a check that the proportion of willful deﬁance citations is not inﬂuenced by other factors, besides
AB 420, that might also impact disciplinary disproportionality, I regress the contemporaneous
proportions of deﬁance-related suspensions on various school socio-demographic variables and on
their interactions with the AB 420 indicator. In Table 3.2, the fraction of discipline citing deﬁance
appears to be mostly unrelated to these other factors, at least as included on their own. However,
the fraction of English learner students as well as the interaction terms involving meal assistance,
English learners, and Black enrollment are statistically signiﬁcantly correlated with the proportion
of suspensions citing deﬁance. In other words, schools’ proportion of ELL students may be linked
with the use of willful deﬁance suspensions, and schools’ proportions of FRPL, ELL, and Black
students may be linked with their change in willful deﬁance suspensions following AB 420. As
noted previously, this paper’s analyses include these school characteristics as controls.

As a check for pre-trends, Figure 3.4 plots event studies of the school-level proportion of
suspensions citing deﬁance (with controls for school socio-economic characteristics), using separate
subsamples of schools by pre-period (2012-2014) proportion of suspensions citing deﬁance. On
the one hand, schools in the second quantile, which initially cited deﬁance more heavily, did indeed

93

Table 3.2: Proportion of Deﬁance Suspensions Regressed on School Demographics

AB 420 onwards

Proportion FRPL Eligible

Proportion English Learners

Total Enrollment

Proportion Black

Proportion White

Proportion Hispanic

AB 420 X Prop. FRPL

AB 420 X Prop. ELL

AB 420 X Tot. Enrol.

AB 420 X Prop. Black

AB 420 X Prop. White

AB 420 X Prop. Hisp.

Observations
School FE
Year FE
Controls

-0.105∗∗∗
(0.034)
0.067
(0.052)
-0.241∗∗∗
(0.078)
0.000
(0.000)
-0.196
(0.166)
-0.065
(0.143)
0.042
(0.100)
-0.153∗∗∗
(0.033)
0.177∗∗∗
(0.051)
-0.000
(0.000)
0.145∗∗∗
(0.053)
-0.008
(0.042)
0.056
(0.038)
12362
Yes
Yes
Yes

the
total

Outcomes
are
contemporaneous
proportions of
suspensions citing
willful deﬁance.
in
Standard errors
parentheses, clustered at the district level. ∗
p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

94

see a large decrease in their deﬁance-related proportion of disciplinary actions over the period (as
opposed to schools in the ﬁrst quantile, which did not). There furthermore appears to be a large
drop in these schools’ deﬁance-related proportion of suspensions coinciding with the passage of
AB 420. As we might suspect, however, considering the political climate surrounding the law and
the previous attempt to pass AB 2242, willful deﬁance citations look to have already been trending
downwards in the pre-period.
If steep downward trends in deﬁance-related discipline coincide
with additional eﬀorts to reduce racial disproportionality, then the estimates of the coeﬃcient on
the interaction term in Table 3.1 may be biased downward. As these estimates are nonetheless
not statistically signiﬁcant, this does not appear to be so (barring the case in which exogenously
reducing punishment for willful deﬁance otherwise leads to greater disproportionality).

3.5.3 Separate Quantiles by Initial Use of Willful Deﬁance

Figure 3.5 plots event study regressions of disciplinary disproportionality (with controls for school
socio-economic characteristics) on separate subsamples of schools, characterized by issuing an
above or below median pre-period average proportion of their total suspensions as punishment for
deﬁance (2nd quantile versus 1st quantile, respectively). Similar to the prior analysis reported in
Table 3.1, Figure 3.5 oﬀers little indication that disproportionality going from the pre to post AB
420 period changes any diﬀerently based on initial proportion of discipline citing willful deﬁance.
Table C.1 additionally presents the results of estimating Equation C.1 (see Appendix) on the
above described quantile subsamples.
In this speciﬁcation, the pre and post period years are
aggregated into a dummy indicator for the post period, while the year dummies are replaced with
a continuous time variable. Perhaps what is most interesting in the summary ﬁgures of Table C.1
is the fact that initial disproportionality (the diﬀerence between each group’s pre-period average
proportion of discipline versus enrollment) appears to be nearly similar between quantiles by
initial deﬁance proportion of discipline. That is to say, that schools initially issuing many of their
suspensions for deﬁance (on average 37.4% of all their suspensions) do not seem to have exhibited
greater racial disproportionality than schools issuing only 6.4% of their suspensions for deﬁance. If

95

Figure 3.4: Proportion of Discipline Related to Deﬁance by Initial Proportion of Discipline Related
to Deﬁance

Quantile 1

Prop. of suspensions initially for W.D.: .064

Quantile 2

Prop. of suspensions initially for W.D.: .374

Outcomes are the contemporaneous proportions of total suspensions citing willful deﬁance. Standard errors clustered at the district
level. Controls include school level enrollment, proportion FRPL eligible, and proportion English learners.
For each type of discipline, schools are divided into quantiles based on initial proportion of citations for willful deﬁance (averaged
over the period 2012-2014). Hence, the graph under “Quantile 2” illustrates the change in the proportion of deﬁance related
suspensions over time among schools which initially issued an above-median proportion of suspensions citing willful deﬁance.

96

.038.0210.031.019−.006−.3−.25−.2−.15−.1−.050.05.1Coefficient size201220132014201520162017Year.06.0350−.13−.2−.23−.3−.25−.2−.15−.1−.050.05.1Coefficient size201220132014201520162017YearFigure 3.5: Disproportionality in School Discipline by Initial Use of “Willful Deﬁance”

Quantile 1

Prop. of suspensions initially for W.D.: .064

Prop. of suspensions initially for W.D.: .374

Quantile 2

Black

White

Hispanic

Outcomes are the diﬀerences between each race category’s proportion of total suspensions and its proportion of total enrollment.
Standard errors clustered at the district level. Controls include school level enrollment, proportion FRPL eligible, and proportion
English learners.

97

−.0018−.00830−.0045−.0081−.0028−.04−.020.02.04.06Coefficient size201220132014201520162017Year−.0061−.00210−.0015.0037−.0085−.04−.020.02.04.06Coefficient size201220132014201520162017Year−.014−.0030.014.01.0032−.04−.020.02.04.06Coefficient size201220132014201520162017Year−.014−.00970.0051−.0061.0024−.04−.020.02.04.06Coefficient size201220132014201520162017Year.026.0110−.0041.00082−.0068−.04−.020.02.04.06Coefficient size201220132014201520162017Year.023.0130−.012.0019.0029−.04−.020.02.04.06Coefficient size201220132014201520162017Yearanything, Black students may be slightly less overrepresented in discipline among schools initially
leaning more on deﬁance citations. Consistent with the prior analysis, the afore described statistics
are unsurprising in the case that punishment of deﬁance is not any more disproportionate than
punishment of more concretely speciﬁed behavior.

3.6 Summary

In recent years, California educators have signiﬁcantly reduced their use of exclusionary
discipline for managing problem behavior among students. School suspensions have fallen
markedly over the period 2012-2017, in terms of both the fractions of schools issuing any
suspensions and the volume of occurrences recorded within these schools.

Counter to a popular narrative among many proponents of AB 420, trends in disciplinary
proportionality in the years around the passage of the law do not particularly support the notion that
punishment of willful deﬁance subjects students to greater implicit bias. Though deﬁance related
discipline naturally fell more sharply in the schools initially issuing the largest proportion of their
citations for deﬁance, the demographic distribution of discipline in these schools did not change
distinctly compared with other schools.

One caveat concerns the downward trend in deﬁance related discipline surrounding the passage
of AB 420; the decrease in punishment of deﬁance may correspond with other factors inﬂuencing
disproportionality. However, if those factors promote more evenly distributed discipline (as seems
likely when considering the recent political climate), then the absence of any evident link between
willful deﬁance and racial disparities is consistent with there truly being no “equalizing” eﬀect of
requiring administrators to concretely specify oﬀending acts.

With debate underway on whether or not to replace AB 420 — set to expire in July 2018 —
the above results oﬀer no evidence of gains in disciplinary equity (as currently conceptualized
within federal oversight) to justify any losses in achievement from limiting educators’ tools for
behavior management.
Indeed, many are quick to oppose eﬀorts targeting disparate impact in
general, on the grounds that prioritizing such metrics hamstrings teachers faced with genuinely

98

disruptive behavior (Green, 2015). According to the 2015 Education Next poll, only 23% of teachers
nationwide support “federal policies that prevent schools from expelling or suspending black and
Hispanic students at higher rates than other students,” with 59% opposed (Green, 2015). There
is certainly evidence to support their concerns: Figlio (2007) ﬁnds that adding a single disruptive
child to a class of 30 students reduces peers’ math scores by roughly 4 national percentiles, while
also increasing their likelihood of being suspended for ﬁve or more days by 3 percentage points.
Kinsler (2013) additionally notes that “losing classroom time as a result of suspension has a small
negative impact on performance, whereas exposure to disruptive behavior signiﬁcantly reduces
achievement.” Depending on the educational beneﬁt of removing troubled students from the
learning environment, future top-down eﬀorts may beneﬁt from more explicitly aiming to correct
the distribution of punishment, rather than regulating its volume.

99

APPENDICES

100

APPENDIX A

CHAPTER 1 APPENDIX

Table A.1: Trend Break Speciﬁcation on Pooled Sample (9th & 11th Graders)

(1)

(2)

(3)

Any drugs Coc./crack Marijuana
Grade 9 & 11 combined
0.009∗∗∗
0.009∗∗
Post
(0.003)
(0.004)

0.004∗
(0.002)

Post x
Evt Time

Evt Time

Obs
School FE
Year FE
Controls

-0.001
(0.002)
0.007∗∗∗
(0.002)

648742

Yes
Yes
Yes

0.000
(0.001)

-0.000
(0.001)

648742

Yes
Yes
Yes

-0.001
(0.001)
0.005∗∗∗
(0.001)

648742

Yes
Yes
Yes

(4)

(5)
Inhalants Meth

(6)

(7)

Alcohol Cigarettes

0.002
(0.002)

-0.000
(0.001)

0.000
(0.001)

648742

Yes
Yes
Yes

0.001
(0.001)

-0.000
(0.000)

0.001
(0.000)

648742

Yes
Yes
Yes

0.006
(0.004)

-0.001
(0.001)
0.006∗∗∗
(0.002)

648742

Yes
Yes
Yes

0.002
(0.003)

-0.001
(0.001)

0.000
(0.001)

648742

Yes
Yes
Yes

Outcomes are indicators for any use of the substance in past 30 days. Controls include age, gender, race,
school level enrollment, demographic composition, FRPL, and proportion English learners. Standard
errors in parentheses, clustered at the district level. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

101

Figure A.1: Event Study Regressions Using Pooled Sample of 9th and 11th Graders Together

Any drugs

Cocaine/crack

Marijuana

Inhalants

Meth

Alcohol

Cigarettes

102

−.022−.025−.02−.00240.016.019.026.033.045.047.052.049.061−.050.05.1Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 648742Schools: 654−.00012−.0023.0019−.0000940.0035.0067.0032.0016.0024.0081.0075.006.0029−.010.01.02Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 648742Schools: 654−.018−.013−.013−.000630.015.016.022.028.034.034.043.038.046−.04−.020.02.04.06Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 648742Schools: 654−.00045−.0013.00016.000650.0027.0035.004.0017.0043.0031.0049.0026.0044−.01−.0050.005.01Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 648742Schools: 654−.0016−.0033−.00024.000620.0015.0043.0038.0011.0022.0042.0061.004.0049−.01−.0050.005.01Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 648742Schools: 654−.018−.022−.014−.00190.01.012.021.024.031.031.035.035.046−.04−.020.02.04.06Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 648742Schools: 654.00022−.0018−.00078−.00390.0001.0019−.00017−.0034−.00058−.0074−.0063−.0074−.005−.02−.010.01Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 648742Schools: 654Figure A.2: 9th Grade Girls vs. Boys: Alcohol

Girls

Boys

103

−.017−.024−.019−.00140.0031−.0038.0089.0092.011.013.0064.0099.016−.04−.020.02.04Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 178732Schools: 577−.006−.0069−.01.000330.012.0069.018.017.022.022.022.018.031−.020.02.04.06Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 167463Schools: 588Figure A.3: Districts not revising policy until 2006: Composite: g9 Any drugs

Compared to 2002

Centered on district revision

104

0−.002.0089−.00096−.03−.02−.010.01.02Coefficient size2002200320042005Time to district policyObs: 41958Schools: 215−.021−.019−.025−.00730.0089.0088.027.033.038.064.058.011−.050.05.1Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7Time to district policyObs: 149485Schools: 229Figure A.4: Districts not revising policy until 2006: g9 Cocaine/crack

Compared to 2002

Centered on district revision

105

0−.0034.0026.0038−.01−.0050.005.01Coefficient size2002200320042005Time to district policyObs: 41958Schools: 215.0034.0033.0064.00150.0075.013.0056.00089.0025.021.0063.00041−.02−.010.01.02.03Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7Time to district policyObs: 149485Schools: 229Figure A.5: Districts not revising policy until 2006: g9 Marijuana

Compared to 2002

Centered on district revision

106

0−.0072−.0018−.0046−.02−.010.01Coefficient size2002200320042005Time to district policyObs: 41958Schools: 215−.0054−.002−.0039.0010.014.014.021.027.032.034.048.0043−.020.02.04.06.08Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7Time to district policyObs: 149485Schools: 229Figure A.6: Districts not revising policy until 2006: g9 Inhalants

Compared to 2002

Centered on district revision

107

0−.0034.0009.0041−.01−.0050.005.01.015Coefficient size2002200320042005Time to district policyObs: 41958Schools: 215−.0049−.0013−.0024−.00110.0067.0099.0098.007.0085.0081.012−.0039−.02−.010.01.02.03Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7Time to district policyObs: 149485Schools: 229Figure A.7: Districts not revising policy until 2006: g9 Meth

Compared to 2002

Centered on district revision

108

0−.003.0019.0029−.01−.0050.005.01Coefficient size2002200320042005Time to district policyObs: 41958Schools: 215−.0011−.0024−.00015−.00160.0024.011.004.0013−.000036.0059.0011−.0014−.02−.010.01.02Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7Time to district policyObs: 149485Schools: 229Figure A.8: Districts not revising policy until 2006: g9 Alcohol

Compared to 2002

Centered on district revision

109

0.0026.013.0079−.02−.010.01.02.03Coefficient size2002200320042005Time to district policyObs: 41958Schools: 215−.023−.023−.026−.00590.0072.0027.026.025.03.048.046.02−.050.05.1Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7Time to district policyObs: 149485Schools: 229Figure A.9: Districts not revising policy until 2006: g9 Cigarettes

Compared to 2002

Centered on district revision

110

0−.0058.0031.011−.010.01.02.03Coefficient size2002200320042005Time to district policyObs: 41958Schools: 215−.0078−.009−.0059−.00960.0002.0076.0085.0075.013.0039.0064.0031−.02−.010.01.02.03Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7Time to district policyObs: 149485Schools: 229Figure A.10: Grade 9 Robustness: Gender and Proportion Black

Girl

Proportion Black

111

−.012−.0084−.0089−.00940−.016−.0079−.014−.0079−.022−.014−.012−.0035−.002−.04−.020.02Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599.0024.00069.00042−3.3e−060−.0038−.0042−.008−.0076−.011−.0074−.012−.012−.014−.03−.02−.010.01Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 346195Schools: 599Figure A.11: Mostly C’s or worse this past year

9th graders

11th graders

112

−.0088.0026−.0099.00960.015−.0038.012−.0026.006.0011−.0039.0046−.0064−.04−.020.02.04Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 323570Schools: 590.011.024.012.0150.017.0036.0062.00047−.011−.0061−.012−.0089−.019−.04−.020.02.04Coefficient sizet=−5t=−4t=−3t=−2t=−1t=0t=1t=2t=3t=4t=5t=6t=7t=8Time to district policyObs: 286816Schools: 624Table A.2: Controlling for School Speciﬁc Time Trends

(1)

Any drugs Coc./crack Marijuana

(2)

(3)

(4)

(5)
Inhalants Meth

(6)

(7)

Alcohol Cigarettes

-0.001
(0.006)

0.000
(0.004)

0.001
(0.003)

-0.002
(0.002)

346195

346195

0.009
(0.006)

-0.001
(0.005)

302547

Yes
Yes
Yes

-0.000
(0.003)

-0.001
(0.002)

302547

Yes
Yes
Yes

0.004
(0.004)

0.002
(0.003)

346195
0.008∗∗
(0.004)

0.002
(0.004)

302547

Yes
Yes
Yes

0.004
(0.003)

-0.000
(0.002)

0.002
(0.002)

-0.002
(0.001)

0.001
(0.006)

0.000
(0.003)

0.003
(0.003)

-0.002
(0.003)

346195

346195

346195

346195

0.001
(0.003)

-0.000
(0.002)

302547

Yes
Yes
Yes

0.001
(0.002)

-0.001
(0.001)

302547

Yes
Yes
Yes

0.008
(0.006)

-0.002
(0.004)

302547

Yes
Yes
Yes

0.004
(0.004)

-0.004
(0.003)

302547

Yes
Yes
Yes

Grade 9
Post

Post x
Evt Time

Obs
Grade 11
Post

Post x
Evt Time

Obs
School FE
Year FE
Controls

Outcomes are indicators for any use of the substance in past 30 days. Controls include age, gender,
race, school level enrollment, demographic composition, FRPL, proportion English learners, and school-
speciﬁc linear time trends. Standard errors in parentheses, clustered at the district level. ∗ p < 0.10, ∗∗
p < 0.05, ∗∗∗ p < 0.01.

113

Table A.3: Controlling for District Speciﬁc Time Trends

(1)

Any drugs Coc./crack Marijuana

(2)

(3)

(4)

(5)
Inhalants Meth

(6)

(7)

Alcohol Cigarettes

-0.001
(0.006)

0.000
(0.004)

346195
0.009∗
(0.005)

-0.001
(0.004)

302547

Yes
Yes
Yes

0.001
(0.003)

-0.002
(0.001)

346195

0.000
(0.003)

-0.001
(0.002)

302547

Yes
Yes
Yes

0.004
(0.004)

0.002
(0.003)

346195
0.008∗
(0.004)

0.001
(0.004)

302547

Yes
Yes
Yes

0.004
(0.002)

-0.000
(0.002)

0.002
(0.002)

-0.002
(0.001)

0.001
(0.006)

0.000
(0.003)

0.004
(0.003)

-0.002
(0.003)

346195

346195

346195

346195

0.001
(0.002)

-0.000
(0.002)

302547

Yes
Yes
Yes

0.001
(0.002)

-0.000
(0.001)

302547

Yes
Yes
Yes

0.007
(0.006)

-0.001
(0.004)

302547

Yes
Yes
Yes

0.004
(0.004)

-0.004
(0.003)

302547

Yes
Yes
Yes

Grade 9
Post

Post x
Evt Time

Obs
Grade 11
Post

Post x
Evt Time

Obs
School FE
Year FE
Controls

Outcomes are indicators for any use of the substance in past 30 days. Controls include age, gender, race,
school level enrollment, demographic composition, FRPL, proportion English learners, and district-
speciﬁc linear time trends. Standard errors in parentheses, clustered at the district level. ∗ p < 0.10, ∗∗
p < 0.05, ∗∗∗ p < 0.01.

114

APPENDIX B

CHAPTER 2 APPENDIX

Figure B.1: Performance of Grade 2 Students in Public Schools on the ECE (2007-2014)

Average Test Scores in Math

Percentage of Students with Low, Medium,
Performance in Public Schools

and Satisfactory

Source: Authors’ calculations based on the Evaluación Censal de Estudiantes, 2007-2014

115

500520540560Average School Score20072008200920102011201220132014Year0102030405060708090100% of students20072008200920102011201220132014LowMediumSatisfactoryFigure B.2: Translated Excerpt of Flow Chart for Prioritization under Plan Huascarán

Authors’ translation. Original document in Spanish can be found here: http://www.minedu.
gob.pe/normatividad/directivas/Dir083VMGP2003.php. <Accessed October 4, 2017>

116

Table B.1: Predictors of Internet Access

Dependent Variable: School Has Gained Internet Access
Including
Adding

Adding

Characteristics
Prioritized by
Plan Huascarán

(1)

a Control for
for Fencing

(2010 and Later)

Characteristics

in School
Data Sheets

Adding
School

FE

(2)

0.033***
(0.005)
0.014***
(0.005)
0.014***
(0.005)
0.028***
(0.007)

(3)

0.025***
(0.006)
0.019***
(0.007)
0.008
(0.006)
0.030***
(0.011)

0.014
(0.009)

(4)

0.034***
(0.005)
0.015***
(0.005)
0.013***
(0.005)
0.027***
(0.007)

-0.001***
(0.000)
0.000
(0.000)
-0.003***
(0.001)
31,368
5,903
No
Yes
Yes

0.092***
(0.006)
0.039***
(0.005)
0.014**
(0.006)
0.033***
(0.002)
0.008
(0.010)

School Has a Computer Room

School Has a Library

School Has Administrative

Oﬃce(s)

Total Enrollment

(in 100s of students)

School Is in an Urban Area

School Has a Full

Perimeter Fence
Number of Computers

for Instruction

Number of Computers
for Administration

Total Number of Teachers

Observations
Number of Schools
UGEL and District FE
Year Fixed Eﬀects
School Fixed Eﬀects

31,368
5,903
Yes
Yes
No

31,368
5,903
No
Yes
Yes

22,669
5,766
No
Yes
Yes

The sample includes all public schools that gained internet access between 2007 and 2014 and are observed at least twice. Standard
errors are clustered at the school level. Prioritized characteristics include enrollment and facilities (computer room, electricity,
library, administrative oﬃces), Local Educational Management Unit (UGEL) ﬁxed eﬀects (to capture UGEL-level quotas), district
ﬁxed eﬀects (to capture poverty status) and year ﬁxed eﬀects. Information on the existence of a perimeter fence is only available
for 2010 and later. Additional characteristics on school data sheets include number of computers used for instruction, number of
computers used for administrative purposes, and number of teachers.
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

117

Table B.2: Summary Statistics (2007 or Earliest Available Year) of Public Primary Schools in ECE,
by Year of Internet Access

School Average Standardized Math Score

School Is in an Urban Area

One Teacher per Grade

Total Enrollment (Grades 1-6)

Enrollment in 2nd Grade

School Is Connected to

Public Water Network

School Has Library

School Has Administrative Oﬃce(s)

Number of Teachers

Number of Classrooms

Computers in School

Second Grade Textbooks

Number of Schools

Internet

before 2007

0.230
(0.620)
0.940
(0.240)
0.940
(0.240)
553.7
(347.8)
89.73
(58.62)
0.870
(0.340)
0.700
(0.460)
0.800
(0.400)
6.140
(7.880)
20.53
(11.60)
17.92
(19.57)
345.8
(279.6)
1359

Internet
2007-2014

-0.040
(0.910)
0.490
(0.500)
0.540
(0.500)
199.6
(233.9)
34.62
(39.82)
0.570
(0.500)
0.370
(0.480)
0.470
(0.500)
5.570
(7.950)
8.180
(6.830)
3.200
(7.260)
131.2
(181.1)
6527

No Internet

by 2014
-0.270
(1.160)
0.110
(0.320)
0.130
(0.340)
62.62
(69.83)
12.23
(12.62)
0.320
(0.470)
0.250
(0.440)
0.270
(0.440)
5.270
(7.780)
3.360
(2.920)
0.490
(2.590)
44.30
(54.97)
17738

When 2007 data are not available, we present data from the earliest available year in the sample. Samples include all schools with
at least one evaluation in the ECE between 2007 and 2014. Note that the estimation sample includes all schools in column 2 with
at least two evaluations in the ECE and with data within our analysis window (described in Section 2.3.1). Average school test
scores have been standardized to mean zero and standard deviation one across all tested schools within each year. In the Peruvian
school system, schools might be unidocente(only one teacher in the school teaches all grades), multigrado (more than one teacher,
but each might teach more than one grade in the same classroom), or polidocente completo (there is one teacher per grade in the
school). Standard deviations in parentheses.

118

Table B.3: Eﬀect of Internet Access on Standardized Test Scores

School Average

Standardized Math Score

(1)

t = -3

t = -2

t = 0

t = 1

t = 2

t = 3

t = 4

t = 5

Joint Test of Signiﬁcance for All t < 0:
Joint Test of Signiﬁcance for All t ≥ 0:
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying controls
Observations
Number of Schools

0.001
(0.020)
-0.003
(0.017)
0.042**
(0.017)
0.076***
(0.018)
0.117***
(0.021)
0.166***
(0.024)
0.213***
(0.028)
0.294***
(0.034)
0.968
0.000
Yes
Yes

31,368
5,903

The sample includes all public schools that gained internet access between 2007 and
2014 and are observed at least twice. Standard errors are clustered by school. Math
scores are standardized to have mean zero and standard deviation of 1 across the universe
of schools reporting scores within each calendar year. Note that due to the timing of the
Censo Escolar relative to the ECE exam, some schools receive internet access in t = 0
while some receive it in t = 1. For more details, see Section 2.3.1. Control variables
include enrollment, number of second grade students scheduled to take the ECE, facilities
(computer room, library, administrative oﬃces), and resources per student (classrooms,
computers, and teachers).
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

119

Figure B.3: Translated Excerpt of Prioritization Directive for Plan Huascarán

Authors’ translation. Original and complete directive in Spanish can be found here: http://www.
minedu.gob.pe/normatividad/directivas/Dir083VMGP2003.php. <Accessed October 4,
2017>

120

Figure B.4: Translated School Data Sheet for Plan Huascarán

Authors’ translation. Original document in Spanish can be found here: http://www.minedu.
gob.pe/normatividad/directivas/Dir083VMGP2003.php. <Accessed October 4, 2017>

121

ANNEX N ° 2 DATA SHEET OF THE EDUCATIONAL INSTITUTION Name of Educational Institution    School Site Code    Address    Department    Province    District    Town Center    Phone    Principal's name    Direct intermediate organ    Geographical area (urban, rural)    Type of Management (State, Parish, Cooperative, Supervised, etc.)    Number of computers for school use (only Pentium I or more)    Number of computers for administrative use (only Pentium I or more)    Do you have electricity?    Number of hours of electricity    Number of students and teachers per level  Students Teachers Initial   Primary   High school   Number of students and teachers per shift  Sections  Morning   Late   Night   Number of sections per shift  Sections  Morning   Late   Night   Number of sections per level  Students Teachers Initial   Primary   High school   Is there home-based telephone in the locality?    Native language of students    Distance to the nearest Huascarán Program educational institution    Source: Authors’ translation of Annex No. 2 available in Spanish here: http://www.minedu.gob.pe/normatividad/directivas/Dir083VMGP2003.php  Figure B.5: Schools and Students in ECE, 2007-2014

Primary Schools tested in ECE

Primary Students tested in ECE

Source: Authors’ calculations based on the Peruvian Censo Escolar (CE) and
Evaluacion Censsal de Estudiantes (ECE), 2007-2014.
* Note: Some schools both have fewer than ﬁve second graders and teach
primarily in native languages. For simplicity, the graph includes these under
“Fewer than ﬁve students.”

122

036912151821242730Number of schools (thousands)20072008200920102011201220132014In ECESchool with less than 5 studentsNative Language SchoolNot tested in ECE0125250375500625Number of students (thousands)20072008200920102011201220132014In ECEIn school with less than 5 studentsIn native Language SchoolNot tested in ECETable B.4: Summary Statistics for Alternate Estimation Samples

School Average Standardized Math Score

Years of Internet Access

Number of Students Scheduled to Take the ECE

School Has a Library

School Has Administrative Oﬃce(s)

Ratio of Classrooms to Students

Ratio of Computers to Students

Ratio of Teachers to Students

Total School Enrollment

Observations
Number of schools

Baseline
Sample

(1)

0.069
(0.924)
1.119
(1.448)
35.689
(38.955)
0.446
(0.497)
0.480
(0.500)
0.076
(0.076)
0.192
(0.329)
0.057
(0.040)
209.530
(227.649)

31,368
5,903

2 Pre & 2 Post Balanced
Sample

Sample

(2)

(3)

0.076
(0.917)
0.851
(1.227)
33.475
(34.180)
0.433
(0.496)
0.458
(0.498)
0.075
(0.079)
0.189
(0.319)
0.056
(0.033)
195.701
(197.098)

22,321
3,670

0.110
(0.878)
0.857
(1.125)
38.410
(34.447)
0.460
(0.498)
0.540
(0.498)
0.068
(0.047)
0.148
(0.252)
0.053
(0.029)
224.555
(199.243)

7,322
1,046

The baseline sample includes all public schools that gained internet access between 2007 and 2014 and are observed
at least twice. The “2 Pre & 2 Post” sample includes schools observed at least twice prior to and twice after internet
access. The balanced sample includes schools that are observed throughout the entire sample period and restricted
event window t = −3 to t = 3. Math scores are standardized to have mean zero and standard deviation of 1 across the
universe of schools reporting scores within each calendar year.

123

Table B.5: Understanding the Role of School-level Compositional Changes: Trend
Break Results

Dependent Variable: School Average

Standardized Math Score

Full Event Window:

t = −3 to t = 5

Restricted Event Window:

t = −3 to t = 3

2 Pre & 2 Post Baseline
Sample

Sample

Balanced
Sample

(2)
0.031
(0.022)
0.043***
(0.013)
0.007
(0.011)
22,321
3,670
Yes
Yes
Yes

(3)

0.041**
(0.021)
0.044***
(0.012)
-0.002
(0.010)
28,392
5,836
Yes
Yes
Yes

(4)

-0.005
(0.053)
0.061
(0.042)
0.011
(0.027
7,322
1,046
Yes
Yes
Yes

Baseline
Sample

(1)

0.036*
(0.020)
0.047***
(0.011)
-0.001
(0.010)
31,368
5,903
Yes
Yes
Yes

Post-internet Access

Post-internet Access

X Event Time

Event Time

Observations
Number of Schools
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying controls

Column 1 reproduces the baseline results using all public schools that gained internet access between 2007
and 2014 and are observed at least twice. Column 2 presents the results using the restricted sample of
schools observed at least twice prior to and twice after internet access. Column 3 presents the results using
the baseline sample for the restricted event window t = −3 to t = 3. Column 4 presents the results using
the sample of schools that are observed throughout the entire sample period and restricted event window.
Standard errors are clustered by school. Math scores are standardized to have mean zero and standard
deviation of 1 across the universe of schools reporting scores within each calendar year. Post-internet
access is a dummy variable for whether a school has gained internet access (i.e. t >= 0). Note that due
to the timing of the Censo Escolar relative to the ECE exam, some schools receive internet access in
t = 0 while some receive it in t = 1. For more details, see Section 2.3.1. Event time is years relative to
internet access. Control variables include enrollment, number of second grade students scheduled to take
the ECE, facilities (computer room, library, administrative oﬃces), and resources per student (classrooms,
computers, and teachers).
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

124

Table B.6: Attrition (Number of Observations)

All Information Observed (Not Attrited)

Attrited

Missing ECE Scores

Second Grade Enrollment less than 5
Second Grade Enrollment between 5 and 7
Other

Missing Census (CE) Information

Missing Information on Infrastructure
Missing Information on Resources

School Permanently Closed

N

31,368

%

81.78

6,989

18.22

2,340
1,022
1,915

1,467
218
27

6.10
2.66
4.99

3.82
0.57
0.07

Based on each school’s initial year of internet connection and our event study window
(t = −3 to t = 5), we determine all the periods that should be included in our panel dataset.
Enrollment is measured from the CE (reported at the beginning of each year). Only schools
with ﬁve or more second graders by the end of each year are tested in the ECE. Schools
that have 5-7 students at the beginning of the year might not have been included in the ECE
if they fell below the 5-student threshold by the end of the year. CE information is used
to calculate infrastructure (and, importantly, internet access) and school resources (control
variables in our regressions).

125

Table B.7: Eﬀects of Computers in Non-internet Schools

School Average Standardized Math Score

(2)

(3)

(4)

(5)

(1)

0.031**
(0.015)

0.030*
(0.018)
0.022
(0.018)

0.026
(0.019)
0.015
(0.020)
0.031
(0.023)

0.019
(0.022)
0.011
(0.021)
0.037**
(0.019)
-0.021
(0.023)

(6)

0.024
(0.037)
0.006
(0.037)
0.001
(0.032)
-0.017
(0.042)
-0.051
(0.060)
-0.049
(0.056)
21,852
9,516
Yes
Yes
Yes

0.016
(0.027)
0.023
(0.026)
0.028
(0.021)
-0.034
(0.024)
-0.036
(0.036)

29,727
10,509
Yes
Yes
Yes

Ratio of Computers to Students

Ratio of Computers to Students

Ratio of Computers to Students

1 Period Lag

2 Period Lag

Ratio of Computers to Students

Ratio of Computers to Students

3 Period Lag

4 Period Lag

Ratio of Computers to Students

5 Period Lag

Observations
Number of Schools
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying controls

80,288
17,464
Yes
Yes
Yes

65,596
16,198
Yes
Yes
Yes

51,450
14,903
Yes
Yes
Yes

39,351
12,732
Yes
Yes
Yes

The sample includes all schools that report ECE scores during 2007-2014 and that had not gained internet
access by 2014. Math scores are standardized to have mean zero and standard deviation of 1 across the universe
of schools reporting scores within each calendar year.
“Ratio of computers to students” is the number of
instructional computers per student. Control variables in all columns include school facilities (piped water,
library, administrative oﬃces) and resources per student (classrooms and teachers). Standard errors are clustered
by school.
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

126

Table B.8: Eﬀects of Concurrent Computer Investments: Back of the Envelope Calculations

Tot. Predicted Rise Tot. Dynamic Eﬀect Est. Eﬀect % of Tot. Internet
Eﬀect Explained
by Computers

in Computers
(per Student)

of Internet
on Scores

of Computers

on Scores

Time Relative to
Internet Access

(1)
t = 0
t = 1
t = 2
t = 3
t = 4
t = 5

(2)
0.045
0.079
0.113
0.147
0.181
0.215

(3)
0.001
0.003
0.007
0.009
0.010
0.009

(4)
0.042
0.076
0.117
0.166
0.213
0.294

(5)

3.32%
4.58%
5.97%
5.61%
4.79%
3.16%

Column 2 gives the total predicted rise in computers in each period using the parameter estimates from the trend
break regression of computers per student on Post-internet access, event time, and the interaction between the two
(from Table 2.3). Column 3 calculates the total dynamic eﬀect of computer as of time t using (i) the largest parameter
values from regressing ECE scores on computers per students (and lags) using the sample of non-internet connected
schools (from Appendix Table B.7), without regard to signiﬁcance level and (ii) the total predicted rise in computers
from column (2). Column 4 displays estimated eﬀects of internet access on test scores from the baseline event study
speciﬁcation (Appendix Table B.3). Column 5 expresses the total eﬀect of computers as a percent of the total eﬀect
of internet access (column 3 divided by column 4).

127

Table B.9: Internet Access and Computer Teachers: Trend Break Results

Dependent Variable:
Presence of a Teacher

with Formal Computer Training

Post-internet Access

Post-internet Access X Event Time

Event Time

Observations
Number of Schools
R-squared
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying controls

0.027***
(0.007)
0.015***
(0.004)
0.000
(0.003)
31,368
5,903
0.035
Yes
Yes
Yes

The sample includes all public schools that gained internet access between 2007 and 2014
and are observed at least twice. Standard errors are clustered by school. Math scores are
standardized to have mean zero and standard deviation of 1 across the universe of schools
reporting scores within each calendar year. Post-internet access is a dummy variable for
whether a school has gained internet access (i.e. t >= 0). Note that due to the timing of the
Censo Escolar relative to the ECE exam, some schools receive internet access in t = 0 while
some receive it in t = 1. For more details, see Section 2.3.1. Event time is years relative
to internet access. Control variables include enrollment, number of second grade students
scheduled to take the ECE, facilities (computer room, library, administrative oﬃces), and
resources per student (classrooms, computers, and teachers).
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

128

Table B.10: Heterogeneity in the Impact of Internet Access across Schools by Student
to Teacher Ratios and Teacher Qualiﬁcations: Trend Break Results

Dependent Variable:

School Average Standardized Math Score

Qualiﬁcations Qualiﬁcations

High
STR
(1)

Low
STR
(2)

0.050
0.025
(0.031)
(0.027)
0.009
0.046***
(0.020)
(0.015)
0.004
0.012
(0.013)
(0.015)
p-value for test that
High STR = Low STR

0.552

0.139

High
Teacher

(3)

0.036
(0.029)
0.063***
(0.016)
-0.002
(0.014)

Low
Teacher

(4)

0.043
(0.030)
0.006
(0.018)
0.006
(0.014)

p-value for test that

High Qual. = Low Qual.

0.866

0.022

Post-internet Access

Post-internet Access

× Event Time

Event Time

...for Post-internet Access
...for Post-internet Access

× Event Time

Observations
Number of Schools
Year Fixed Eﬀects
School Fixed Eﬀects
Time-varying controls

14,307
2,458
Yes
Yes
Yes

12,834
2,457
Yes
Yes
Yes

13,926
2,458
Yes
Yes
Yes

13,215
2,457
Yes
Yes
Yes

High and Low STR schools are deﬁned based on each school’s pre-internet average ratio of grade 2 students to
total teachers in the school (STR) over the sample period relative to the median of all schools’ sample averages.
High and Low Teacher Quality schools are deﬁned based on each school’s pre-internet average number of
teachers with a pedagogical or higher education degree per student over the sample period relative to the
median of all schools’ sample averages. Note that degree information is not available for all schools. Samples
includes all public schools that gained internet access between 2007 and 2014 and are observed at least twice.
Standard errors are clustered by school. Math scores are standardized to have mean zero and standard deviation
of 1 across the universe of schools reporting scores within each calendar year. Post-internet access is a dummy
variable for whether a school has gained internet access (i.e. t >= 0). Note that due to the timing of the Censo
Escolar relative to the ECE exam, some schools receive internet access in t = 0 while some receive it in t = 1.
For more details, see Section 2.3.1. Event time is years relative to internet access. Control variables include
enrollment, number of second grade students scheduled to take the ECE, facilities (computer room, library,
administrative oﬃces), and resources per student (classrooms, computers, and teachers).
Signiﬁcance levels denoted by: *** p< 0.01, ** p< 0.05, * p< 0.1.

129

APPENDIX C

CHAPTER 3 APPENDIX

Yrit = β1AB 420t + φYeart + γXit + αi + εit

(C.1)

130

Table C.1: Disproportionality in Suspensions Over Time by Initial Use of “Willful Deﬁance”

(1)

1st Quantile

2nd Quantile

(2)

.374

Schools’ initial willful deﬁance
proportion of suspensions
Black: Diﬀerence between proportion of suspensions and proportion of enrollment
AB 420 onwards

.064

Initial Black proportion of suspensions
Initial Black proportion of enrollment
Observations
White: Diﬀerence between proportion of suspensions and proportion of enrollment
AB 420 onwards

Year

Year

-0.004
(0.010)
0.001
(0.003)
.165
.069
5657

0.012
(0.012)
0.001
(0.003)
.256
.245
5906

0.006
(0.011)
-0.007∗∗
(0.003)
.468
.526
5992
Yes
Yes

0.001
(0.008)
-0.000
(0.003)
.152
.068
6443

-0.000
(0.010)
0.003
(0.003)
.291
.273
6635

-0.008
(0.010)
-0.002
(0.003)
.442
.503
6679
Yes
Yes

Initial White proportion of suspensions
Initial White proportion of enrollment
Observations
Hispanic: Diﬀerence between proportion of suspensions and proportion of enrollment
AB 420 onwards

Year

Initial Hispanic proportion of suspensions
Initial Hispanic proportion of enrollment
Observations
School FE
Controls

Standard errors in parentheses, clustered at the district level. Controls include school level
enrollment, proportion FRPL eligible, and proportion English learners. Outcomes are the
diﬀerences between each race category’s proportion of total suspensions and its proportion of
total enrollment. ∗ p < 0.10, ∗∗ p < 0.05, ∗∗∗ p < 0.01.

131

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