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School-Based Violence Prevention Programs
Systematic Review of Secondary Prevention Trials
Julie A. Mytton, MBBS, MRCGP, MSc;
Carolyn DiGuiseppi, MD, MPH;
David A. Gough, PhD;
Rod S. Taylor, MSc, PhD;
Stuart Logan, MSc, MRCP
Arch Pediatr Adolesc Med. 2002;156:752-762.
ABSTRACT
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Objective To quantify the effectiveness of school-based violence prevention programs
for children identified as at risk for aggressive behavior.
Design Systematic review and meta-analysis of randomized controlled trials.
Electronic databases and bibliographies were systematically searched and authors
and organizations were contacted to identify randomized controlled trials.
Standardized, weighted mean effect sizes were assessed by meta-analysis.
Setting Elementary, middle, and high schools.
Participants Children at risk for aggressive behavior.
Main Outcome Measures Violent injuries, observed or reported aggressive or violent behaviors,
and school or agency responses to aggressive behaviors.
Results Of the 44 trials identified, none reported data on violent injuries.
For the 28 trials that assessed aggressive behaviors, the pooled difference
between study groups was -0.36 (95% confidence interval, -0.54
to -0.19) in favor of a reduction in aggression with intervention. For
the 9 trials that reported data on school or agency responses to aggression,
the pooled difference was -0.59 (95% confidence interval, -1.18
to 0.01). Subgroup analyses suggested greater effectiveness in older students
and when administered to mixed-sex groups rather than to boys alone.
Conclusions School-based violence prevention programs may produce reductions in
aggressive and violent behaviors in children who already exhibit such behavior.
These results, however, need to be confirmed in large, high-quality trials.
INTRODUCTION
IN 1998 in the United States, 43 of every 1000 children were victims
of nonfatal violent crime while at school or on their way to and from school.1 More than 250 000 serious violent crimes (1%
of all schoolchildren), including rape, sexual assault, and aggravated assault,
were committed against students at school or while going to or from school.
Teachers are also victims of school violence, with 31 per 1000 teachers reporting
violent crime victimization in 1998. Youth violence in the school has become
an increasing concern in the United States and other nations.2-3
Many schools have implemented prevention programs that attempt to address
this problem. According to a US Surgeon General's report, "Hundreds of youth
violence prevention programs are being used in schools and communities throughout
the country, yet little is known about the actual effects of many of them."2, 4 Although previous reviews have attempted
to identify model programs and best practices,2, 4
informed decision making by policymakers and school professionals about violence
prevention programs requires ready access to information about the effectiveness
of such programs based on systematic and comprehensive review and synthesis
of all available literature. The most reliable evidence for effectiveness
comes from randomized controlled trials.5 We
therefore conducted a systematic review and meta-analysis of such trials to
explore and quantify the effect of school-based violence prevention programs
on aggressive and violent behaviors in children at high risk for violent behavior.
METHODS
INCLUSION CRITERIA
Studies were included if (1) participants were randomly assigned to
intervention and control groups; (2) outcome data were collected concurrently
in the 2 groups; (3) the study population was composed of children in grades
kindergarten (K) through 12 (or their international equivalent) identified
by author-defined criteria as exhibiting or at risk for aggressive behavior;
(4) the experimental intervention was designed, either wholly or largely,
to reduce aggression and violence; (5) the intervention was primarily school
based, although it could contain additional components; and (6) outcome measures
included aggressive behavior, school and agency responses to acts of aggression,
or violent injuries. We defined outcome measures as follows. Aggressive behavior
was defined as scores on standardized tests that assess aggressive behavior
(eg, Achenbach Child Behavior Checklist, Miller School Behavior Checklist)
or actual counts of aggressive behaviors, such as fights or bullying (eg,
via classroom observation and videotapes). School or agency actions were defined
as any school or agency actions, such as detention, suspension, or court contact,
recorded in official records that were taken in response to aggressive behaviors
(eg, fighting and bullying). When school or agency records did not differentiate
between responses to aggressive behaviors and responses to nonaggressive misbehaviors,
such as truancy, all types of misbehaviors were included. The last outcome
measure was violent injuries (eg, emergency department attendances).
For studies with multiple outcome measures, 1 aggressive behavior and
1 school or agency action outcome were chosen on the basis of a predefined
hierarchy of factors (in order, data availability, measure specificity, quality
assurance of measure, outcome assessor, data completeness and validation of
the measure) and random choice if none of these applied (details available
from the authors). We did not assess outcomes indirectly related to violence,
such as school achievement, knowledge about or attitudes toward violence,
mental health outcomes, and measures of aggressive responses to artificial
stimuli or experimental tasks. We excluded cluster randomized trials with
only 2 randomized schools or classes in which confounding factors cannot be
effectively eliminated by randomization.
SEARCH STRATEGY
To identify relevant trials, electronic databases were searched using
content terms such as aggress*, violen*, and fight*, with terms such as school*, educat*, and student*. The results were combined
with the Cochrane Collaboration's optimally sensitive search strategy to identify
controlled trials, adapted as required for each database (full search strategy
available from the authors). We searched the Cochrane Controlled Trials Register
(1998, issue 1), MEDLINE (1994–June 1998), EMBASE (1980–January
1998), PsycLIT (1887–March 1998), ERIC (Educational Resource Information
Centre) (1970–September 1997), CINAHL (Cumulative Index to Nursing and
Allied Health Literature) (1982–April 1998), Dissertation Abstracts
(1861–March 1998), IBSS (International Bibliography of Social Sciences)
(1952-1998), and NCJRS (National Criminal Justice Reference Service) (1970–May
1999) and the bibliographies of published reviews6-8
and relevant trials. Aggression and Violent Behavior
(Issue 1, 1996–Issue 3, 1998) were hand searched. We contacted relevant
international organizations and experts and attempted to contact the authors
of relevant studies to identify unpublished and internal reports. No language
or date restrictions were applied.
STUDY SELECTION
Titles, abstracts, and keywords of identified records were screened
to exclude ineligible trials (if specified in sufficient detail). Full texts
of remaining reports were reviewed and additional ineligible trials excluded.
Authors were contacted for clarification where necessary.
DATA EXTRACTION
From eligible reports, 2 of us (J.A.M. and C.D.) independently extracted
detailed data on study participants, interventions, outcomes, follow-up, results,
methods of group assignment and allocation concealment, blinding of outcomes
assessment, and loss to follow-up. A third author (D.A.G.) also independently
extracted data on participants, interventions, and outcomes. Differences were
resolved by discussion. We attempted to contact all authors of eligible trials
to confirm study details, obtain missing data, and identify relevant unpublished
outcomes.
ANALYSIS
We compared results of any intervention to no intervention (ie, control
or placebo group) immediately after intervention and at the 12-month follow-up
in the subsample for which these data were collected. We also assessed the
effect of different types of interventions, grouping them according to the
predominant training focus: (1) skills of nonresponse, either managed (eg,
conflict resolution) or not (eg, anger control); or (2) relationship skills
and other interventions of social context (eg, family or social relationships,
peer mediation).
Study-specific differences between intervention and control groups for
each of these comparisons were pooled using meta-analysis9
(RevMan 4.1; The Nordic Cochrane Centre, Copenhagen, Denmark) to produce an
overall estimate of effect. Pooled results are expressed as standardized mean
differences (with 95% confidence intervals [CIs]). In trials with multiple
intervention or control groups, weighted, pooled means and SDs were used in
the meta-analysis to avoid statistical problems with nonindependence of data
that would result from including multiple intervention groups as separate
trials. Studies comparing different intervention groups or different intensities
of the same intervention, with no placebo or control group, were excluded
from the meta-analysis but are described in Table 1.10-13
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Summary of Secondary Prevention Trials*
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Trial heterogeneity was explored with a  2 test using
a significance level of .05.9 If there was
statistical evidence of heterogeneity, a random-effects model was used. We
used formal statistical testing (using Stata statistical software, version
6; Stata Corp, College Station, Tex) and funnel plot analysis (in which study
size is plotted against intervention effect)14
to examine effects of study size and bias. In funnel plots, results from small
studies tend to scatter widely at the bottom, with the spread narrowing among
larger studies, so that the plot should represent a symmetrical inverted funnel.
Asymmetry or gaps in the funnel plot may indicate that some studies or study
data exist that may not have been published or located.14
It may also indicate poor methodologic quality of smaller studies (which tend
to show larger effect sizes [ESs]) or true heterogeneity in the results.14-15 Exploration of heterogeneity by meta-regression,
using covariates indicative of study quality such as allocation concealment,
use of blinding, and type of intervention, was planned but could not be conducted
because of inadequate reporting of such data.
When SDs were not published and could not be obtained, they were imputed
by standard statistical methods16 or derived
from trials reporting the outcome in a similar population, where possible.
Sensitivity analyses were performed on the effect of imputing SDs.
Six trials11, 17-21
used cluster randomization at the level of the class or school. Of these,
3 trials11, 19-20
did not report data suitable for inclusion. One trial18
analyzed results by cluster. We analyzed the results of the other 2 trials17, 21 using a published intraclass correlation
coefficient of 0.02 to take into account the cluster randomization.22-23 As sensitivity analyses, we used
more extreme values for the intraclass correlation coefficient (ie, 0.0001
and 0.1); there was no effect on results to one decimal place (data not shown).
Subgroup analyses specified a priori included assessing differences
in intervention effects by whether the program was administered to primary
or secondary school students and boys-only intervention groups vs mixed (or
girls-only) groups. "Primary schools" included elementary schools (grades
K through 5 or K through 6) or students of equivalent ages if grade was unspecified
or study was international. "Secondary schools" included middle, junior high,
and high schools (grades 6 through 12 or 7 through 12) or students of equivalent
ages.
RESULTS
We identified 9286 unduplicated electronic records, from which 274 potentially
relevant reports were identified and the full texts examined. Thirty-five
eligible trials12-13,18-21,24-52
were found. An additional 3 trials10-11,17
were identified from authors, 233, 53
from bibliographies, and 454-57
from expert contacts, giving 44 randomized controlled trials of secondary
violence prevention programs. Five authors provided additional data.26, 37, 42, 52-53
We received responses from 66% of all trial authors contacted. No trials reported
data on violent injuries. Trial details are shown in Table 1.
MAIN ANALYSES
Thirty-eight trials compared the intervention to a no intervention or
placebo (ie, alternative classroom activity) control group and measured aggressive
behavior. Twenty-three had complete data, 5 reported group means alone but
the SD could be imputed, and 10 reported only partial or no data, giving 28
trials for analysis. Of these, 5 adjusted posttest results for pretest scores.
Combining these 28 trials (Figure 1),
aggressive behavior was reduced in intervention compared with control groups
after intervention (ES, -0.36; 95% CI, -0.54 to -0.19).
A test for heterogeneity was significant (P<.001),
indicating variation in results across trials. Results were similar for 6
trials that collected data to 12 months after intervention (ES, -0.35;
95% CI, -0.79 to 0.09, with significant heterogeneity; P<.001), suggesting that effects were maintained.
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Figure 1. Comparison of any violence prevention
intervention vs no intervention by type of school. The outcome was the difference
in aggression scale score or observed aggression by type of school (after
intervention). SMD indicates standardized mean difference; CI, confidence
interval; and CPPRG, Conduct Problems Prevention Research Group.
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Results were similar for different types of training. Training in skills
of nonresponse produced beneficial effects on aggressive behavior immediately
after intervention (ES, -0.38; 95% CI, -0.65 to -0.11, with
significant heterogeneity; P = .001) and at 12 months
(ES, -0.56; 95% CI, -1.08 to -0.05, without heterogeneity; P = .38). Interventions to improve relationship skills
or social context also reduced aggressive behavior after intervention (ES, -0.65;
95% CI, -1.05 to -0.25, without heterogeneity; P = .24). One trial measured this outcome at 12 months (ES, -0.50;
95% CI, -0.97 to -0.04).
Among 15 trials that measured effects on school or agency actions, 6
published no data and the authors either could not provide data or could not
be contacted. The pooled ES among 9 included trials was -0.59 (95% CI, -1.18
to 0.01), indicating a reduction in school or agency actions with intervention
(Figure 2). There was significant
heterogeneity (P<.001). In 2 trials, there was
no apparent effect at 12 months (ES, 0.05; 95% CI, -0.45 to 0.55).
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Figure 2. Comparison of any violence prevention
intervention vs no intervention by type of school. The outcome was the difference
in school or agency response to acts of aggression and other acts by type
of school (after intervention). SMD indicates standardized mean difference;
CI, confidence interval; and CPPRG, Conduct Problems Prevention Research Group.
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Training in skills of nonresponse produced less conclusive beneficial
effects on school or agency actions (ES, -0.32; 95% CI, -0.90
to 0.26, with heterogeneity; P = .003). Training
to improve relationship skills or social context produced more favorable effects
(ES, -0.69; 95% CI, -1.26 to -0.13), although only 2 trials
were included.
SUBGROUP ANALYSES
Primary vs Secondary School
The immediate postintervention effect on aggressive behavior was similar
for trials in primary schools (ES, -0.33; 95% CI, -0.54 to -0.12)
and secondary schools (ES, -0.43; 95% CI, -0.75 to -0.11).
Significant heterogeneity persisted within each subgroup (Figure 1).
There was no evidence of benefit from interventions in primary schools
on school or agency actions (ES, 0.11; 95% CI, -0.48 to 0.70, without
heterogeneity; P = .05). The remaining 7 studies,
in secondary schools, showed a stronger positive effect of the intervention
(ES, -0.82; 95% CI, -1.56 to -0.09, with significant heterogeneity; P<.001).
Sex
Most students identified as aggressive or violent were boys. Twelve
trials10, 25-26,29, 35-39,43-44,52
studied boys alone, 1 trial13 studied girls
alone, and the remaining 31 studied mixed groups in which most students were
boys. Violence prevention programs delivered to boys alone had a modest effect
on aggressive behavior (ES, -0.18; 95% CI, -0.47 to 0.1, without
heterogeneity; P = .18), which may have been due
to chance. The ES was greater for interventions delivered to mixed groups
or girls alone (ES, -0.44; 95% CI, -0.66 to -0.23), although
results were heterogeneous (P<.001). Two trials
evaluating the effect of interventions on school or agency actions among male
students alone reported no evidence of a benefit (ES, 0.22; 95% CI, -0.20
to 0.63, without heterogeneity; P = .25). Among 7
studies17-18,24, 28, 32, 45, 51
of mixed-sex groups, there was a substantial reduction in school or agency
actions after intervention (ES, -0.85; 95% CI, -1.59 to -0.10,
with significant heterogeneity; P<.001).
Effect of Imputing Data
The SD was imputed for 5 trials with incomplete reporting.27, 30, 39, 41, 46
Omitting these data, the ES is -0.24 (95% CI, -0.40 to –0.08),
a more modest effect than that found in the main analysis. The 5 studies with
imputed data showed a strong effect (ES, -1.19; 95% CI, -1.62
to –0.76).
Evaluating Data for Heterogeneity and Publication Bias
The Begg test (P = .07) and Eggar test (bias
coefficient P<.001) suggested a relationship between
study size and reported effects on aggressive behavior (ie, larger studies
reported smaller effects). This is illustrated in the funnel plot (Figure 3). The plot also demonstrates asymmetry,
with fewer trials showing a positive standardized mean difference, suggesting
that small studies showing harm or no benefit were not included.
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Figure 3. Funnel plot of measures of aggressive
behavior for any school-based violence prevention program vs no program. The
standardized mean difference demonstrates the treatment effect from each trial;
the precision of the treatment effect is the reciprocal of the standard error.
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COMMENT
School-based violence prevention programs for high-risk children modestly
reduced both aggressive behaviors and school or agency actions. Training in
nonresponse skills and in relationship skills both showed beneficial effects.
Although the ESs appear small, the overall benefits may be substantial when
implemented on a schoolwide or districtwide basis.
Effects on aggressive behavior were similar in primary and secondary
schools, whereas effects on school or agency actions were greater in secondary
schools, although this difference may have been due to chance or to the way
such actions are implemented at different ages. Although most programs focused
solely or largely on boys, program effects appeared to be greater among mixed
groups. Whether programs are more effective when delivered to mixed-sex groups
or schools or whether such programs have greater effects on girls than on
boys cannot be determined from these data.
Both subgroup analyses were prespecified, but, given the relatively
small number of studies in each subcategory and the possibility of confounding
by other trial characteristics, they should be interpreted with caution.
Tests for heterogeneity highlighted wide variation in the magnitude
of results across trials. Funnel plot asymmetry is often used as an indication
of publication bias, but it can also be explained by true heterogeneity among
studies, resulting from differences in type or intensity of intervention,
underlying risk, and study quality.58 We found
that differences in age group, sex, and training focus contributed to, but
did not fully explain, the substantial heterogeneity. Trials in this review
varied substantially in their quality, execution, and reporting. Most sample
sizes were small, and many studies provided limited methodologic information
(Table 1). Data on indicators
of methods, such as allocation concealment, use of blinding, and type of intervention,
were so poorly reported that exploration of heterogeneity by meta-regression
was not possible. Therefore, we cannot make firm conclusions about the impact
of these factors on the apparent heterogeneity.
All the trials selected students at high risk for violent or aggressive
behavior. However, selection processes varied considerably. Because of inadequate
information on these processes for most trials and difficulty in establishing
population rates for the service actions on which selection was based, we
could not explore whether program effectiveness differed according to how
the study determined "high-risk" status.
Meta-analyses were performed on posttest results. Although randomized,
most trials were relatively small. Therefore, differences in the pretest scores
and other baseline characteristics (eg, age) may have occurred by chance.
Unfortunately, the difference between the posttest and pretest means was not
available for most studies. Posttest scores adjusted for pretest differences
were used where available, otherwise unadjusted posttest scores were used.
The 5 studies27, 30, 39, 41, 46
in which the SD was imputed showed a greater beneficial effect from intervention
than did those reporting full data. This may have been due to quality differences.
Methodologically weaker studies, which may be less likely to report complete
data, tend to show larger ESs.5 Exclusion of
trials with imputed values reduced the ES but did not change its direction.
Excluding such trials could introduce bias, however. Of 3 trials that reported
group means but were excluded from the meta-analysis because SDs could not
be imputed, 234-35 reported that
the intervention had beneficial effects in reducing the outcomes measured,
whereas 143 reported no effect. Their exclusion
may have biased our results toward the null.
Publication bias is an important threat to validity in systematic reviews.
Authors may choose not to submit results that are negative or not significant,
and journals may not publish such studies.58-59
Publication bias may also operate within individual studies when investigators
selectively report outcomes with "significant" results.59
We attempted to contact each author to establish whether any unpublished data
were available and whether they knew of any further studies, published or
unpublished. In addition, we contacted experts and organizations for unpublished
studies. Despite such efforts, many trials did not provide data for relevant
outcomes known to have been measured, which may have affected these results.
The funnel plot suggests that negative studies may exist that were not retrieved
and included.
CONCLUSIONS
Violence within our society has been a public concern in recent years.
Substantial resources have been allocated to preventing violent injuries and
crime. Schoolchildren have been intensively targeted. We identified 44 randomized
controlled trials that evaluated school-based programs, of which 28 (64%)
provided outcome data. Many trials were small and reported insufficient information
to assess quality. Nevertheless, pooled results suggest that these interventions
may reduce aggressive and violent behavior and school or agency actions in
response to such behavior. However, analysis also suggests the possibility
of bias toward studies with positive results and genuine differences among
trials, which may mean that the true effect is smaller than that indicated.
Larger, better controlled trials, with improved reporting of methods, use
of adequate methods for allocation, blinding of outcome assessment, and more
complete reporting of results, appear warranted to determine whether the apparent
benefit is real. In addition, unexpected results emerged regarding differential
effects by sex, which warrant further research.
| What This Study Adds
Each year, 1 in 25 US schoolchildren are victims of violent crime while
at school or on the way to and from school. The aggregate effects of the hundreds
of school-based youth violence prevention programs currently being implemented
have not been adequately evaluated.
School-based violence prevention programs for high-risk children modestly
reduced both aggressive behaviors and school or agency actions in response
to aggressive behavior. Effects on aggressive behavior were similar regardless
of whether the programs focused on training in skills of nonresponse (eg,
conflict resolution or anger control) or on training in social skills or social
context changes. The benefits of violence prevention programs were similar
in programs introduced in both primary and secondary schools, but appeared
to be greater among mixed-sex groups. Additional large, well-controlled trials
are needed to determine whether the apparent benefits are real.
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AUTHOR INFORMATION
Accepted for publication February 27, 2002.
This study was funded by the Systematic Reviews Training Unit, Institute
of Child Health (Dr Mytton), and Camden and Islington Health Authority, London,
England (partial funding to Dr DiGuiseppi).
We thank Ian Roberts, MBBCh, MRCP, PhD, Public Health Intervention Research
Unit, London School of Hygiene and Tropical Medicine, London, for his advice
throughout this project, and Frances Bunn, BSc, MSc, coordinator of the Cochrane
Injuries Group, London.
Corresponding author: Julie A. Mytton, MBBS, MRCGP, MSc (e-mail: jmytton{at}doctors.org.uk).
From the Department of Paediatric Epidemiology and Biostatistics (Drs
Mytton and DiGuiseppi) and Systematic Reviews Training Unit (Dr Logan), Institute
of Child Health, Social Science Research Unit (Dr Gough), and National Institute
for Clinical Excellence (Dr Taylor), London, England. Dr Mytton is now with
the Department of Public Health, Oldham Primary Care Trust, Oldham, England.
Dr DiGuiseppi is now with the Department of Preventive Medicine and Biometrics,
University of Colorado Health Sciences Center, Denver. Dr Taylor is now with
the Department of Public Health and Epidemiology, University of Birmingham,
Edgbaston, England.
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