Discussion

In this chapter, we place the findings summarised in the Chapter 9 in context, with reference to the existing literature, and we discuss the limitations of the study. The implications for practice and research are discussed and conclusions presented.

Comparison with other studies

Depression and anxiety

In placing the findings reported here in context, it may be informative to compare the effect sizes from the present analysis with those observed in psychotherapeutic meta-analyses for the treatment of childhood depression and anxiety. The most robust evidence observed in our primary analyses was in universal secondary settings, in which there was weak evidence of a small benefit for CBT-based interventions (anxiety: SMD –0.15, 95% CrI –0.34 to 0.04; depression: SMD –0.04, 95% CrI –0.16 to 0.07). This can be contrasted with the evidence for group CBT relative to treatment as usual, observed by Zhou et al.273,274 from a NMA of psychotherapies for treatment of anxiety274 (SMD –0.84, 95% CI –1.47 to –0.21) and depression273 (SMD –0.32, 95% CI –0.60 to –0.08).

Our results are largely consistent with the findings from large-scale RCTs of school-based prevention of anxiety and depression. Twelve RCTs included in our NMA had sample sizes of > 1000 at baseline.118,119,125,126,141,142,151,159,196,204,206,207 All were passive-controlled RCTs (in two studies the control was a waiting list, in two it was no intervention and in eight it was the usual curriculum). Eight of the 12 RCTs concluded that there was no evidence of an effect of the intervention on self-reported symptoms of anxiety and/or depression, of which five were at low risk of bias for both random sequence generation and allocation concealment (Table 21). We also compared our findings with those of 20 systematic reviews of RCTs published since 2005. A summary of the review characteristics is provided in Appendix 9. Reviews were identified via a combination of non-systematic scoping searches in MEDLINE, PsycInfo, EMBASE and Google Scholar. Nineteen concluded that there were beneficial effects of anxiety and depression prevention programmes for CYP. Most noted that effect sizes were small; however, some were interpreted as showing ‘significant reductions’,113 as ‘consequential’,275 of ‘practical relevance’276 or providing ‘strong support’111 for the effect of interventions. Only one review reported that ‘Results of the various programs . . . are not particularly positive . . . the effects (if there are any) are not sustained over time’.277 Two reviews were more cautious in their interpretation of the small positive effects, noting that when preventative interventions were compared with an attention control, they ‘showed a sobering lack of effect’.68,278 We consider possible reasons for the difference in our findings and those of some systematic reviews below.

Confirmation and developer bias

Confirmation bias may explain the differing interpretations between the present study and previously published reviews.279 There has been debate about whether systematic reviews should be carried out by those with no conflicts of interest or by subject experts, who are best placed to understand the nuances of study inclusion/exclusion and interpretation of findings.280 In an empirical study in which subject experts and methodologists were shown the same meta-analysis, Panagiotou and Ioannidis281 observed that subject experts were more likely than methodologists to over-interpret the pooled effect from a meta-analysis. Furthermore, subject experts who had also published a ‘statistically significant’ study showing a positive intervention effect were even more likely to over-interpret findings and to overlook the importance of the between-study heterogeneity on the overall interpretation.

There was some evidence to suggest that preventative RCTs involving the original intervention developer(s) observed stronger intervention effects, although the mechanism was not clear.282,283 For example, it is possible that implementation and fidelity to intervention are superior in developer-led trials. The impact of so-called ‘developer bias’ on systematic reviews is unknown; however, in the case of 14 of the 20 reviews we identified, the first or senior author was a researcher who subsequently developed/published a school-based RCT to prevent anxiety or depression. Owing to an increased emphasis on reducing research waste,284 it is increasingly common for intervention developers or triallists to first conduct a systematic review. Further research could consider the role of developer bias in systematic reviews.

Inclusion criteria and meta-analytic method

Differences in inclusion criteria should also be considered. We investigate whether or not there was a discrepancy between the studies included in the present review and the 20 reviews described above (see Appendix 9). Reviews for which there was a > 40% discrepancy were Horowitz and Garber285 (57%), Neil and Christensen111 (42%), Neil and Christensen112 (48%), Stice et al.113 (46%) and Teubert276 (58%). For example, of the 30 studies included in Horowitz and Garber,285 only 13 were included in the present review. The main inclusion differences related to the earlier reviews having broader inclusion criteria, for example severity of symptoms;113,276 inclusion of interventions for children of divorce or alcoholics;113,285 and interventions to address situational (state) anxiety, such as test and public speaking276 or stress reduction.111,112,276

The choice of meta-analytic method could be a further explanation for findings differing across reviews. Of the 14 reviews conducting a meta-analysis, 10 used a random-effects model, two used a fixed-effects model and two used an undefined model to estimate a pooled effect. Nine summarised intervention effects using Cohen’s d and nine using Hedges’ g. In the present review, we fitted both fixed- and random-effects models, but presented results from the random-effects models based on statistical evidence of heterogeneity. We summarised effects using Hedges’ g, which is observed to be less biased in the presence of small studies (i.e. < 20 participants). Durlak286 states that the Hedges’ g correction typically amounts to a 4% reduction in effect when the total sample size is 20 participants, and around 2% when the sample size is 50. In the present analysis, four studies had sample sizes of ≤ 20 participants, and 19 had sample sizes of ≤ 50. Therefore, the impact of the adjustments made by Hedges’ g is likely to be small.

There are several ways to estimate the SMD; here we used the (standardised) difference in mean change from baseline (also known as change score) and we standardised using the pooled baseline SD. A common alternative is to use the final values (also known as post-intervention score, or follow-up score). It is not clear which approach was taken in the previous meta-analyses. However, using final values may not be appropriate when randomisation is questionable or when there is baseline imbalance in factors that may interact with the outcome. For example, if participants randomised to the control arm have higher depression symptom scores at baseline than those in the active arm, one cannot confidently conclude that the final values reflect the effect of the intervention, rather than severity of initial illness. In such cases, using final values may overestimate the effect of an intervention. In addition, our analyses were conducted in a Bayesian framework, in contrast to all 20 previous reviews, which took a frequentist approach. In a Bayesian analysis, the uncertainty in all parameters is fully represented. In particular, it takes full account of uncertainty in the between-studies SD in a random-effects model. Frequentist methods typically assume that the between-studies SD is known with certainty; as a result, Bayesian CrIs tend to be wider than frequentist CIs for random-effects models.287

Standard pairwise meta-analysis and network meta-analysis

A further difference between the present review and those described previously is that we separated intervention and control groups into their distinct types. We a priori identified four distinct control conditions: attention control, waiting list, no intervention and usual curriculum. This was based on the psychotherapeutic literature, in which it was established that control group choice contributes to differences in effect size estimate.73,74 To explore the possible impact of this decision, we ran a simple analysis ‘lumping’ these control conditions to form a single comparator. To emulate previous analyses more closely, we also included psychoeducation and psychosupport conditions in the conflated ‘control’ condition. Primary and secondary settings were also combined, but we kept universal and targeted populations separate. We also ran a second analysis combining psychological interventions, to form a ‘psychological intervention versus control’-type analysis.

When control conditions were conflated, our results were consistent with previous reviews, that is intervention effects for CBT versus ‘control’ now indicated a beneficial effect of CBT in every network at post intervention (see Appendix 9). This suggests that previously observed beneficial effects may have been a consequence of differential control group effects being obscured by ‘lumping’. However, the impact of lumping control groups in meta-analyses of public mental health interventions should be explored further. Certainly, in the psychotherapeutic literature, the use of a waiting list has been called a ‘nocebo’73 and a technique ‘to prove your therapy is effective, even when it is not’.74 Future preventative and public health trials should also consider the importance of control groups at the feasibility or pilot stages of development.

Conduct disorder

The preliminary signs of conduct problems often emerge during early childhood. As a result, school-based interventions specifically aimed at the prevention of conduct disorder have been implemented in primary school settings. In recent years, however, interventions for preventing conduct disorders have largely focused on parenting skills, in community or home settings (e.g. Family Check-up, Nurse Family Partnership, Triple P).288 The 2013 NICE guidelines on recognition of, intervention for and management of conduct disorders among CYP289 included a review of classroom-based interventions for selective and indicated prevention of conduct disorders. Noting that only 53% of the eligible studies included sufficient data for inclusion in a meta-analysis, the NICE guidelines concluded that, for selective interventions, the mean teacher-rated antisocial behaviour in the intervention groups was SMD –0.43 (95% CI –0.96 to –0.09). However, it is unlikely that teachers could have been blinded to intervention allocation. Conversely, there was no evidence of an effect when rated by an external observer (SMD –0.43, 95% CI –0.96 to 0.09) or for parent-reported antisocial behaviour (SMD –0.13, 95% CI –0.39 to 0.13).

We found few reviews explicitly referring to the prevention of conduct disorder, and most were conducted in the 1990s.290–294 Instead, authors have focused on the prevention of collections of behaviours associated with conduct disorder, for example interventions that aim to prevent multiple risk behaviours such as substance misuse, aggression and stealing.295 For example, in an early review of the prevention of ODD and conduct disorder, Tremblay et al.293 state:

To our surprise, we found no preventative interventions that met our selection criteria . . . We thus broadened the scope and selected studies with outcome measures related to CD [conduct disorder]/ODD symptoms including court recorded or self-report delinquency, self-, parent- or teacher-rated measures of aggressive externalising behaviour and observer measures of aversive behaviour in the classroom. We generally refer to these outcomes using the term Disruptive Behaviour Disorders.

More recent reviews taking this broader approach for school settings, such as Park-Higgerson et al.,296 suggest that there is no evidence of an effect for interventions reducing aggression and violence, compared with the control (effect size –0.09, 95% CI –0.23 to 0.05).296 de Vries et al.297 examined prevention programmes for adolescents showing early signs of antisocial and disruptive behaviour problems. For interventions in a school setting, there was no evidence of an effect relative to usual curriculum [β –0.19 (SE 0.33)]. However, in a 2018 Cochrane review84 of interventions to prevent multiple risk behaviours, a positive effect of universal school-based interventions to prevent a composite outcome of ‘anti-social behaviour and offending’ was observed (OR 0.81, 95% CI 0.66 to 0.98).84 We note that studies contributing to such reviews may not even reference conduct or disruptive behaviour disorders in their aims or backgrounds. We return to the issue of defining conduct disorder subsequently, in the limitations section.

Strengths and limitations of the study

To the best of our knowledge, this is the first NMA of preventative mental health interventions and the first to review the comparative effectiveness of distinct psychological, educational and physical interventions in a single analysis for CYP.

Limitations relating to search strategy

There is growing interest in improving the efficiency of study identification in systematic reviews.54,298–302 However, there is no consensus on the number of databases to search or for defining appropriate ‘stopping rules’ or abbreviated search strategies.52,53 A limitation of the present study is, therefore, that we searched only four electronic health-related and psychology databases. The selection of databases was consistent with the Cochrane MECIR conduct standards for searching, and included reference list searching of published systematic reviews and scoping searches to inform the ‘stopping’ strategy. The electronic database searches retrieved all but two eligible studies previously included in published systematic reviews; neither of these contributed to the NMA.188,303 The scoping searches of two educational databases (ERIC and BEI) did not identify any further eligible studies. However, the possibility that potentially eligible studies have been missed cannot be ruled out emphatically.

Limitations relating to inclusion criteria

The inclusion and exclusion criteria were specified to minimise the potential for between-study heterogeneity and to address the assumption of consistency for the NMA. This condition was satisfied in 8 of the 10 networks, with inconsistency being noted in the two tertiary/university-level analyses. Nevertheless, we consider the implications of the narrow inclusion criteria below.

Definition of disorder

To be eligible for inclusion in the present review, the explicit aim of a study had to be the prevention of anxiety, depression or conduct disorder. These might be considered as ‘disorder-specific’ prevention interventions, although, in practice, some sought to prevent both anxiety and depression. The focus of the present review was the prevention of anxiety, depression and conduct disorder, and not specific diagnostic subtypes of disorders. Although we did not exclude studies focusing on specific disorders (e.g. social anxiety), our preferred outcome was a total symptom score. This approach is consistent with a population health perspective,304 the existing trial literature and previous systematic reviews. Only one study119 focused on the prevention of a specific anxiety disorder (social anxiety), and none addressed the prevention of subtypes of depression or conduct disorder.

To reduce the risk of selective outcome reporting, studies were not selected on the basis of reported outcomes. That is, studies were not selected on the basis of whether or not they reported anxiety, depression or conduct disorder outcomes. Selective outcome reporting can occur when studies measure multiple outcomes but select only those that are ‘statistically significant’ for publication. In turn, this can cause bias in a body of evidence and overestimate the effect of interventions. Prospective trial registration and protocols reduce the likelihood of selective reporting; however, this was not made a mandatory requirement in medicine until 2008. We are not aware of a current similar requirement within psychological science. As noted in Chapter 9, only 32 of the 142 studies included in this review had protocols or trial registrations readily available. We therefore chose a conservative approach of including studies based on the stated intent of the trial, as written in the publication.

The decision to restrict inclusion to disorder-specific prevention interventions is likely to have had the biggest impact for the review of conduct disorder. Fairchild et al.305 note that conduct disorder is a highly heterogeneous disorder and they state there are > 32,000 different symptom profiles that could lead to a diagnosis. Such clinical variation is likely to pose an even bigger problem for primary preventative studies with regard to defining a target population. Over the preceding 25 years (since the publication of the DSM-IV), clinical language has evolved and, in the present review, it was not easy to judge whether or not study authors were using the terms ‘problems’ and ‘disorders’ interchangeably. Again, in the absence of trial registrations and protocols, we chose a conservative approach and restricted to ‘disorders’. A related concern refers to our reliance on DSM-5 criteria and the decision to exclude neurodevelopmental and neurobiological conditions. In DSM-III, -IV and -IV Text Revision (spanning 1980–2012), conduct disorders were categorised together with ADHD under ‘Attention-deficit and disruptive behavior disorders’. In DSM-5,61 they were separated. Conduct disorders are now grouped under ‘Disruptive, Impulse-Control, and Conduct Disorders’ and ADHD is separately considered under the ‘Neurodevelopmental Disorders’ heading. It is not clear whether or not older studies considered ‘conduct disorder’ as a catch-all for ‘disruptive behaviour disorders’, which historically included ADHD. In a NMA of psychosocial interventions for the treatment of childhood disruptive behaviour disorders, Epstein et al.306 conclude that future studies must more clearly identify the target population for intervention. We echo their conclusion here, for preventative interventions.

Intervention focus

To minimise potential between-study heterogeneity and to address the assumption of consistency for the NMA, we included a narrowly defined set of interventions. Unless it was clear that the aim of the intervention was to prevent anxiety, depression or conduct disorder, we excluded interventions focused on mental health promotion. Similarly, we excluded studies addressing the related constructs of social and emotional well-being and positive mental health. Here we followed the NAM’s definition of mental health promotion as interventions that ‘aim to enhance an individual’s ability to achieve developmentally appropriate tasks and a positive sense of self-esteem, mastery, well-being and social inclusion, and strengthen their ability to cope with adversity’.27 Recent evidence has suggested that well-being is only weakly correlated (r = 0.2) with mental illness in children,64 raising doubts that interventions targeting one will necessarily affect the other.63 However, some interventions may aim to address both prevention and promotion, for example the Aussie Optimism Program.152 In such instances, we referred to trial registrations and protocols to inform our inclusion decision. However, given the absence of trial registrations or protocols, it was difficult to operationalise this distinction, and this is a limitation of the review.

In common with previously published systematic reviews that focused on disorder-specific prevention of anxiety, depression or conduct disorder,36–39,68 we did not include interventions that primarily addressed the prevention of substance use, bullying or stress, although these factors have been shown to be associated with later mental ill health. We also excluded classroom management and social and emotional learning interventions. Classroom management interventions use conditioning and reinforcement to encourage prosocial behaviours and reduce challenging behaviours in their classrooms (e.g. providing clear expectations and routines, stating clear rules and consequences, and consistently using praise and other rewards). Consequently, interventions such as the Good Behaviour Game were not included in our review. However, there is recent evidence that these interventions do affect general conduct outcomes for children and are cost-effective in a UK context.307 This could be considered a limitation of the findings for conduct disorder.

Mental health is multifaceted, with biological and environmental factors contributing to the development of a disorder. A further limitation of this review is that the interventions included are largely ‘downstream’. That is, they are focused on changing an individual’s cognitions, emotions or mood, without addressing the wider ‘upstream’ social determinants of mental health or the complex adaptive systems in which interventions are implemented.308 It is, therefore, important to situate our findings in the context that there are calls to reframe preventative mental health towards a broader dimensional approach309,310 and incorporate other perspectives, such as a developmental psychopathological perspective to prevention.311 In psychology and psychiatry, this has manifested in calls for a ‘paradigm shift’ away from the categorical approach to diagnosing mental disorders (e.g. ICD and DSM).312–314 In public health, the focus has shifted to whole-school, systemic interventions as a wider, structural approach to tackle the increasing prevalence of CYP with mental health problems. Whole-school interventions have shown promise for physical health outcomes83 and emotional well-being;315 however, there is limited evidence, to date, that they are effective in the prevention of CMDs.83,316 The present review is limited by the absence of these perspectives; future work should be considered to evaluate the comparative effectiveness of such interventions.

Defining population

We followed the NAM’s intervention spectrum for mental disorders, which defines three populations: universal, selective and indicated. By definition, participants in universal interventions are included irrespective of diagnostic status; consequently, studies included in the universal analyses will have included CYP with diagnosed mental health conditions at baseline. As noted in Chapter 1, a definitive boundary between indicated prevention and early intervention (i.e. treatment) is difficult to draw. Our eligibility criteria sought to minimise the inclusion of CYP with clinical conditions in the ‘targeted’ analyses, but, in the absence of clearly defined scale cut-off points or diagnostic tests for anxiety, depression or conduct disorder, we relied on author descriptions of participants. As a result, we cannot rule out the possibility that some of the participants in the ‘targeted’ analyses may also have had clinically diagnosable conditions. Here we reflect that the distinction between indicated prevention and early intervention is a qualitative one and is likely to rest with the intent of the triallist. If the intent of a study is to decrease the likelihood of the onset of a mental disorder or decrease detectable, but subclinical, symptoms, it can be considered prevention. If the aim of the study is to reduce existing, clinically meaningful or diagnosed symptoms, it can be considered treatment.

The inclusion criteria meant that there were few studies of eligible university-based interventions. In the original protocol, we stated that the upper age limit for eligible studies was 25 years, which was intended to allow for follow-up time points. As described in Table 1, this was difficult to operationalise, and was modified to be ≤ 19 years at baseline. In turn, this limited the eligible university population and is likely to have excluded interventions specifically aimed at older undergraduate and postgraduate students. The inclusion criterion that the intervention should be educational setting based was also restrictive. In tertiary education institutions, many interventions were delivered in health-care settings (e.g. primary care, psychology clinics) or remotely, without supervision (e.g. via mobile phone, internet). As a comparison, a 2019 review with broader inclusion criteria included 62 studies of preventing anxiety and depression in university students.317 This larger review concluded that the overall effect size was moderate (Hedges’ g 0.65, 95% CIs 0.57 to 0.73). In combination with the potential for inconsistency observed in the tertiary NMAs, the small number of included tertiary/university studies is a further limitation of the present review; therefore, we do not make inferences about the effect of interventions in that setting.

Limitations relating to outcomes

Although agreement between parent- and child-reported symptoms is typically low, multi-informant measures of mental disorder symptoms among CYP are often considered preferable to single report.318–320 Therefore, it may be considered a limitation that our primary outcomes were only symptoms self-reported by CYP. Parent-reported child symptoms were included as a secondary outcome; however, only 12% of the anxiety and depression studies included a parent report. All studies included for the prevention of conduct disorder included a parent and/or teacher report. Self-reported outcomes may be at higher risk of performance bias than observer-rated outcomes owing to lack of blinding to intervention allocation. In trials of school-based interventions, however, it is also questionable whether or not parents and teachers can be successfully blinded. Furthermore, the outcome of interest for decision-makers wanting to reduce the burden of common mental disorders is likely to be clinical diagnosis or service use, not symptoms. Clinical diagnosis was infrequently reported for the anxiety and depression studies, but was reported for the longer-term follow-ups in the conduct disorder studies.

Other limitations

The typology of interventions was based on previous literature, piloting and discussion among our team. However, the use of the constant comparative method was time-consuming and, inevitably, subjective. We sought greater objectivity by one reviewer initially drawing up a list of components, which was refined by a second reviewer through discussion. The list was further reviewed by two additional members of the team. Their suggested modifications were piloted and a final classification scheme constructed. This scheme was then applied and further refined during data extraction, until no further components were identified (saturation). Relying on published papers also generated problems for classifying components. To ensure a consistent approach across all studies, we did not assume the presence of a component unless it was explicitly stated in the paper or confirmed via correspondence with the authors. Inevitably, the taxonomy reflects the narrow set of interventions on which it is based, and it may not generalise to other preventative mental health interventions, as a result of the inclusion and exclusion criteria adopted here. Owing to the subjectivity of classification and lack of a consistent format for reporting of intervention details, there is potential for component misclassification.321 It is also of note that the classification scheme that we developed for anxiety and depression did not generalise to conduct disorder interventions. As a result, we do not claim this as a definitive taxonomy, but a contribution to the growing literature.

Few studies reported sufficient detail to judge how randomisation or allocation concealment had been conducted; consequently, the risk of bias for these domains are mostly judged to be unclear. Many studies also had short follow-up periods, and it was not always clear whether reported follow-up periods referred to post intervention or from baseline. Only 13% of studies of anxiety and depression prevention studies reported a follow-up of > 1 year, and 5% reported a follow-up of > 2 years. For conduct disorder, two studies reported longer-term follow-ups and both indicated strong evidence of an effect (although they were not cost-effective; see Chapter 8).

Implications for practice

In this review, we conclude that there is weak evidence to support the effectiveness of school-based anxiety, depression or conduct disorder prevention interventions, but that it is not robust evidence. The available economic evidence for a UK context suggests that school-based anxiety and depression prevention interventions are ‘highly unlikely’ to be cost-effective, compared with usual curriculum, especially when the usual curriculum already contains a personal, social and health education aspect.261,322 For conduct disorder, the US-based Fast Track cost-effectiveness evaluation suggests that it is unlikely that such a comprehensive, multisystemic approach would be implemented in practice.250,263,264

However, the policy environment in the UK has recently placed schools front and centre in the prevention, early detection and support of students with mental health needs. Therefore, schools and local authorities may need access to comprehensive and independent sources of information to ensure that they are not susceptible to exaggerated claims or ‘trends’ about what works for the mental health of CYP.323,324 Examples of freely accessible, evidence-based repositories and services include Evidence for Impact325 and the Early Intervention Foundation.326 However, bespoke evidence-based services could also be useful to support schools that have identified specific mental health needs, and could emulate those run by AskFuse327 for Public Health and the Avon and Wiltshire Mental Health Partnership NHS Trust’s BEST in Mental Health328 evidence service for treatment of mental disorders.

Local government, education authorities, schools and universities should be made aware that few studies have measured potential harms or side effects of the interventions. This may include explicit harms, social harms or equity harms.329 For example, in our study, we observed weak evidence that depression and anxiety prevention interventions may be more beneficial in higher-income settings than in low-income settings. The opportunity cost of implementing a potentially harmful intervention (one that has the potential to increase symptoms) should be considered by those commissioning interventions. Lorenc and Oliver329 describe this as ‘the potential benefits which may be forgone as a result of committing resources to ineffective or less effective interventions’.

Implications for research

The following implications for research are described in priority order.

Although overall evidence was weak, and risk of bias was judged to be unclear, the component NMA provided evidence that CBT interventions including a psychoeducation component may be effective for the prevention of anxiety and depression in universal secondary settings. There was also evidence that exercise and mindfulness/relaxation interventions were effective for symptoms of anxiety in universal secondary settings, although this was not robust. In the light of these findings, a future RCT in a secondary school setting might consider a multiarm design comparing CBT with mindfulness/relaxation with an attention control. It may also be of interest to explore the impact of including an active exercise component. However, before progression to a RCT, further work is undoubtedly necessary to optimise the content of such an intervention,330 including exploring the mechanisms of action for psychoeducation components for CYP. Such work should be conducted in consultation with CYP. What is clear is that any future RCTs of preventative mental health interventions must be well designed and include an economic evaluation.

Further research on the importance of control conditions for all public health interventions should also be a priority. Until then, we echo Merry and Hetrick’s331 conclusions and suggest that RCTs of interventions to prevent CMDs should use an active control (attention control or alternative intervention) and that waiting list controls should be discouraged.

It has been suggested that intervention effects can emerge over a longer time period in public health.332,333 However, the majority of studies included in this report reported a post-intervention time point only, and we are not able to confirm or refute this observation. For anxiety and depression, only 18 trials from the 137 included had outcomes available at > 12 months post intervention and only seven trials reported time points at > 24 months. Follow-up periods were longer for the conduct disorder studies, and the positive study-level findings from the 20-year follow-up of Fast Track247 suggest that school-based RCTs should plan for longer follow-up periods. The possibility of using data linkage could be considered as an adjunct or substitute for primary data collection where resources are a concern.

Future preventative intervention studies should also include measurements of potential harms and/or side effects. However, it is not clear from our review what harms or side effects should be measured, and further research on core outcome sets should consider this issue.334 Consideration of prevention of common mental health disorders from a systems perspective335 may also help to identify such unintended consequences.

Finally, the reporting of basic methodological aspects of the included studies was inadequate and scientific journals should ensure that the Consolidated Standards of Reporting Trials (CONSORT) guidance,336 and its extension to Social and Psychological interventions,337 is fully adhered to. To improve reporting of intervention components, authors should be encouraged to complete TIDieR reporting guideline for complex interventions and comparator conditions. The work reported in this monograph contributes to the growing literature around components of mental health interventions. However, the field lacks consensus and future work should focus on agreeing a taxonomy for preventative mental health interventions and control conditions.

Conclusions

With regard to the comparative effectiveness of school-based anxiety, depression and conduct disorder prevention interventions, there is a lack of robust evidence that any one type of intervention can be preferred across all populations and settings. However, in making this statement, we reiterate that the present review specifically addressed prevention of clinically referenced disorders. These conclusions, therefore, relate to a narrowly defined set of largely ‘downstream’ interventions, which focus on changing an individual’s cognitions, emotions or behaviours, without addressing wider ‘upstream’ social determinants of mental health (e.g. SES) or the complex, adaptive systems in which interventions are implemented.288