Abstract
This meta-analytic review quantified the effects of universal interventions, those implemented with all children, on improving mental well-being in young children aged 0-6 years old. Potential factors that moderated the effects of interventions were explored. A systematic search of PubMed, CINAHL (EBSCO), PsycINFO (ProQuest), and grey literature identified 21,942 records. After screening, 134 articles reporting 133 studies and 141 interventions among 32,512 participants met eligibility criteria. Meta-analyses were conducted, using random-effects models and cluster-robust variance estimation to account for within-study dependence and to compute pooled Hedges’ g. Mean effects at post-intervention were small to medium on overall mental well-being (g = 0.35) across cognitive (g = 0.23), social (g = 0.37), emotional (g = 0.40), and behavioral (g = 0.35) domains. Sensitivity analyses (e.g., excluding high-risk and low-reliability studies) produced similar results. Follow-up effects adjusted for baseline were 0.22, and the maintenance of effects from post-intervention to follow-up was only 0.04. Exploratory moderator analyses revealed three significant moderators including study design, control group, and intervention target. Child-focused interventions yielded the largest effects, exceeding those targeting family and child, the occupational role (e.g., teachers), or family member only. Though these results support some promises of universal interventions for enhancing early mental well-being, interpretation warrants caution. Between-study heterogeneity was substantial, some studies exhibited high risk of bias, and publication bias was present. Future research should prioritize rigorous designs with follow-up assessments and booster strategies to support maintenance and include implementation-relevant outcomes (e.g., fidelity), while adhering to transparent reporting.
Keywords: mental well-being, cognitive, social, emotional, behavioral, young children, meta-analysis
A recent meta-analysis of ten international epidemiological studies (2006-2020) revealed a 20% pooled prevalence of mental health disorders among more than 18,000 children aged one- to six-years old (Vasileva et al., 2021). Common diagnoses included oppositional defiant disorder, attention-deficit hyperactivity disorder (ADHD), and anxiety, with an estimated 6.4% of children experiencing a co-morbidity (Vasileva et al., 2021). Notably, the authors reported fewer cases of depression and conduct disorders, suggesting these conditions may be underdiagnosed in young children but identified later in development. According to the United Nations Children's Fund (2024), an estimated 13% (11.2 million) of children and adolescents aged 0-19 in the European Union had a mental health condition. Prevalence rises from about 2% in children under 5 to 10% among those aged 5-9, with higher rates in boys than girls (under 5: 3% vs 1%; ages 5-9: 12% vs 8%; (United Nations Children’s Fund, 2024).
Recognizing the early emergence of mental health challenges, the Task Force of the World Association for Infant Mental Health (Lyons-Ruth et al., 2017) emphasized the global need for education and treatment availability for infants, toddlers, and their caregivers (Lyons-Ruth et al., 2017). Despite efforts to differentiate between normal development and psychopathology, systemic barriers hinder the adoption of Diagnostic Classification of Mental Health and Developmental Disorders of Infancy and Early Childhood (DC:0-5) criteria, including complex billing requirements, additional diagnostic criteria, and limited clinical expertise (Williams et al., 2023). Some states in the United States have successfully integrated DC:0-5 into policy and practice. For example, Washington State mandates DC:0-5 use for Medicaid-covered assessments, Nevada incorporates DC:0-5 into electronic health records, and Massachusetts employs a "train-the-trainer" model to enhance frontline professionals’ capacity for early symptom recognition (Cohen & Andujar, 2023).
Early identification of developmental concerns is essential, but equally critical are evidence-based universal preventative strategies that foster socioemotional growth in all children under six before the onset of pathology. Universal interventions are designed to benefit all children, fostering optimal development across diverse populations (Greenberg & Abenavoli, 2017). Unlike selective interventions focusing solely on children at high risk, universal interventions have the potential for broader and more sustainable impact over time (Greenberg & Abenavoli, 2017). To guide prevention efforts in early childhood, it is important to articulate mechanisms of change grounded in established theoretical frameworks. Although empirical evidence on mechanisms among young children remains limited, research in older children and adolescents may provide some insights into how interventions may impact mental well-being. Across developmental and behavioral theories, including Social Learning Theory, Attachment Theory, and Ecological and Transactional Models, interventions are theorized to operate through several potential mechanisms: increasing knowledge and awareness of emotions and behaviors, strengthening supportive relationships with parents and peers, and enhancing self-regulation and management skills (Bosqui & Marshoud, 2018).
Although substantial research has been dedicated to developing and evaluating universal interventions to enhance young children’s mental well-being, overall effectiveness of these interventions remains unclear. To determine the most effective approaches, comprehensive synthesis of existing evidence is essential. Despite a growing number of systematic reviews, results remain inconsistent. For example, a review of 19 studies found no evidence of body-oriented interventions (e.g., play, dance, physical activity) improving emotional competence, but found moderate evidence for improving social skills and decreasing externalizing behaviors (Dias Rodrigues et al., 2022). Similarly, another review of 19 studies found no effect of interventions targeting social and emotional learning on enhancing emotional competence in young children (Blewitt et al., 2021). In contrast, a systematic review of positive psychology interventions (focusing on positive emotions and character traits), though limited to only three studies, reported positive effects on young children’s overall well-being (Benoit & Gabola, 2021). These conflicting results underscore the urgent need for more rigorous, large-scale meta-analysis, to clarify effectiveness of interventions and inform best practices for promoting mental well-being in early childhood.
Only a limited number of meta-analytic reviews have comprehensively and quantitatively synthesized the effects of universal interventions on enhancing mental well-being in young children before primary schools. Luo et al. (2022) analyzed 39 studies and found that classroom-based social-emotional interventions had medium mean effects on social (Hedges’ g = 0.42), emotional competence (g = 0.33), and challenging behavior (g = −0.31). They identified two significant moderators, family engagement and interventionist, showing that interventions involving families and delivered by non-classroom teachers (e.g., researchers) produced greater effects (Luo et al., 2022). Similarly, Blewitt et all (2018) synthesized 63 studies and reported that universal curriculum-based interventions resulted in medium effects on emotional competence (Cohen’s d = 0.54), and small effects on social competence (d = 0.30), self-regulation (d = 0.28), and behavioral and emotional difficulties (d = 0.19). A few moderators were identified, including child age, interventionists, assessment method, and study quality. Barnes et al. (2018) identified a small effect of school-based social problem-solving interventions on preschoolers’ social competence (d = 0.05) and externalizing behaviors (d = −0.27) among 26 studies. Moderators were not examined due to the limited sample size.
Beyond school-based interventions, several meta-analyses have focused on home-based or parent-targeted interventions. For example, a Cochrane review of seven randomized control trials (RCTs) revealed small mean effects (d = 0.30) of home-based interventions on preschoolers’ cognitive development (Miller et al., 2011). The review did not meta-analyze socioemotional outcomes or examine moderators because only three studies assessed these outcomes and did not provide sufficient effect size data. Another Cochrane review focused on group-based parenting programs and found overall large effects (d = −0.81) on emotional and behavioral problems among children aged 0-3 years old with 22 RCTs and two quasi-experimental trials (Barlow et al., 2016). Yet, the effects diminished to −0.67 after excluding the two quasi-experimental trials. The effects of interventions did not vary significantly by intervention duration (≤ 7 weeks vs ≥ 8 weeks) or prevention type (primary vs secondary/tertiary; (Barlow et al., 2016). Lastly, Jeong et al. (2021) synthesized 102 parent-targeted interventions and found small effects on cognitive (d = 0.32) and socioemotional development (d = 0.19), and behavior problems (d = −0.13) among children aged 0-3 years, with no moderating effects of child age or study quality.
These prior meta-analyses have some notable limitations. Many focused exclusively on school-based (Barnes et al., 2018; Blewitt et al., 2018; Luo et al., 2022), parent-targeted (Barlow et al., 2016; Jeong et al., 2021), or home-based interventions (Miller et al., 2011); or on specific domains such as socioemotional learning (Murano et al., 2020) or nutritional (Prado et al., 2019), overlooking comprehensive, multi-setting approaches. Limiting the scope to school-based interventions may introduce bias, as merely attending preschool programs has shown to improve young children’s social skills and cognitive outcomes (Camilli et al., 2010), making it difficult to isolate the effects of specific interventions. Several reviews excluded grey literature (Blewitt et al., 2018; Jeong et al., 2021; Luo et al., 2022), potentially omitting valuable findings. Some meta-analyses are restricted to specific regions (Fukkink et al., 2017; Kumar et al., 2022; Rao et al., 2017) or highly controlled studies (e.g., RCTs only, those with a control group or matched quasi-experimental design; (Miller et al., 2011; Murano et al., 2020). Whereas these approaches can enhance internal validity, they may limit the generalizability of results and potentially overlook significant evidence from diverse cultural and socioeconomic contexts. Notably, no consistent approach has been applied to describe intervention strategies, hampering comparisons across studies and reviews. These gaps underscore the critical need for a comprehensive and globally inclusive synthesis of universal intervention targeting young children's mental well-being.
Purpose of the Present Review
The primary purpose of this systematic review and meta-analysis was to quantify and comprehensively evaluate the immediate effects from baseline to post-intervention of universal interventions on mental well-being among young children aged 0-6 years. Based on World Health Organization’s (2020) guidelines on child health and development and Pollard and Lee’s (2003) child well-being indicators, we classified child mental well-being into cognitive (Best & Miller, 2010; Diamond, 2013), social (Djamnezhad et al., 2021; Kochenderfer-Ladd & Ladd, 2019), emotional (Choi, 2018; Gross, 2014), and behavioral (Chen, 2024; Korucu et al., 2022) domains (Table 1). These mental well-being domains were used as organizing categories for synthesis; many constructs were inherently multidimensional (Nigg, 2017), and domain assignment was based on how outcomes were operationalized and measured in the primary studies. The secondary purpose was to assess whether the effects of interventions were sustained during follow-up on preschoolers’ mental well-being. Additionally, we aimed to explore the potential key moderators, including study characteristics (i.e., continent, study design, control group, child mean age, percent female child, percent ethnic/racial minority child) and intervention characteristics (i.e., setting, theory, target, interventionists, intervention, duration in weeks, and dose in hours), to better understand the conditions under which interventions yielded the greatest impact. These potential moderators were selected according to prior literature indicating that study and intervention characteristics (e.g., study design, age, sex, ethnicity/race, setting, target population, interventionists, intervention duration, treatment dose) might influence the effects of interventions (Blewitt et al., 2018; Jeong et al., 2021; Luo et al., 2022).
Table 1.
Child mental wellbeing domains, definitions, indicators, and measures
| Domain | Definition | Sample Indicators | Example Measures |
|---|---|---|---|
| Cognitive | Internal mental processes or information processing supporting age-appropriate thinking, learning, memory, attention, and problem solving | Executive function, reasoning, attention, inhibitory control (cognitive), cognitive flexibility, working memory, theory of mind, emotion understanding, problem solving | Early Executive Function Rating Scales Ages and Stages Questionnaire (problem solving subscale) Wally Social Problem Solving Test Symptoms and Normal Behavior (attention subscale) Kusche Emotional Inventory Picture Memory Task, Desire-Emotion Task, True-Belief Task, Flanker Task, Sun-Moon Stroop Task, Sound Stroop Task, Challenging Situations Task, Emotional Matching Task, Flanker Task |
| Social | Interpersonal functioning reflected in the ability to initiate, form, and sustain relationships with peers and adults |
Positive: cooperation, empathy, sharing, social communication, peer acceptance, prosocial behaviors, positive relations at home/school, social competence, attachment Negative: antisocial behaviors, peer problems, social withdrawal |
Bayley-III Socio-Emotional and Adaptive Behavior Scales (play, social interactions subscales) Preschool and Kindergarten Behavior Scales-2 (PKBS-2, social skills subscales) Social Competence and Behavior Evaluation scale (social competence) Social Skills Scale for preschool children Student-Teacher Relationship Scale Direct observation of interactions and social behaviors |
| Emotional | Processes involved in the experience, expression, and regulation of one’s own emotions |
Positive: positive affect, emotion regulation, emotion expression, emotional self-confidence Negative: stress, anxiety, depressive symptoms, negative affect, emotional distress |
Child Health and Illness Profile Physiological stress markers (hair/salivary cortisol) Preschool Pediatric Symptom Checklist (emotional symptoms) Emotional Regulation Checklist Child Behavior Checklist (internalizing subscale) Minnesota Preschool Affect Checklist (positive, negative affect subscales) Preschool Anxiety Scale Emotional State Talk (video recording) |
| Behavioral | Observable actions and behaviors reflecting regulation in response to situational demands and social norms |
Positive: behavioral self-regulation, observable inhibitory control, adaptability, compliance Negative: impulsivity, aggression, hyperactivity, inattention, disruptive behavior, conduct problems |
Child Behavior Checklist Preschool Self-Regulation Assessment Child Self-Regulation and Behavior Questionnaire PKBS-2 (externalizing problems) Strengths and Difficulties Questionnaire (conduct problem, hyperactivity/inattention subscales) Checklist for Screening Behavioral Problems in Preschool Children Behavior Assessment System for Children (externalizing problems) Observable regulation of behaviors (Head-Toes-Knees-Shoulders, go/no-go task, Peg Tapping Task, Statue Task, Hand Game task) |
Notes. Several indicators (e.g., inhibitory control, self-regulation) span cognitive, emotional, and behavioral processes (Nigg, 2017). Indicators were categorized based on whether measures primarily assessed internal mental processes, observable behavior, or interpersonal functioning.
Although theory is central to intervention design and to articulating mechanisms of change (Petersen & Govender, 2010), no prior meta-analysis has evaluated whether the use of a theoretical framework moderates the effects of interventions on mental well-being in young children. In addition, because practices of implementation and reporting vary globally, cross-context heterogeneity may shape observed effects; accordingly, we examined country as a potential moderator. To enhance comparability and reproducibility, we classified interventions using the Behaviour Change Intervention Ontology (BCIO), a standardized taxonomy for specifying intervention content and components (Michie et al., 2021).
Method
Transparency and Openness
To ensure transparency and rigor, this meta-analytic review followed the seven key steps in the evidence synthesis process (Johnson, 2021). The reporting adheres to the Preferred Reporting Items for Systematic reviews and Meta-Analyses (PRISMA) guideline (Page et al., 2021). All meta-analysis data are available at (osf.io/bhxug). Data were analyzed using R (version 4.5.1). The protocol was registered in the international prospective register of systematic reviews (PROSPERO, CRD42024523362).
Data Sources and Search Strategy
A comprehensive literature search was conducted by a Master’s-prepared health sciences librarian on May 8, 2023, with an updated search performed on August 18, 2025. The search encompassed three databases: PubMed, CINAHL (EBSCO), and PsycINFO (ProQuest), focusing on interventions to promote mental well-being among young children aged 0-6 years old. Initially, the search (including MeSH and CINAHL subject headings) yielded over 60,000 results, prompting the authors to limit the search to title and abstract only. The final search, with robust and comprehensive keyword development, was confined to title and abstract only in each database. To target the young child population, relevant keywords were added to exclude adolescents/teenagers, adults, and geriatric or elderly populations. Associated keywords were added to exclude postpartum or prenatal population and animal studies. There were no date limits or language restrictions applied. The exact search strategies for each database are provided in Supplemental Table 1S. Grey literature, including ClinicalTrials.gov and MedRxiv, was searched. The reference lists of review articles were manually scrutinized to identify pertinent articles. All search results were imported into Covidence software (www.covidence.org) for managing the screening process. Covidence is recommended as a suitable and easy-to-use tool to support screening in systematic reviews within healthcare research (Harrison et al., 2020). This software automatically removed identified duplicates and facilitated transparent, independent screening by multiple reviewers in accordance with PRISMA guidelines.
Eligibility Criteria
The inclusion criteria were (a) participants being young children aged 0-6 years old before attending primary schools; (b) targeting outcomes on mental well-being including cognitive (capacity to engage in age-appropriate thinking, learning, and problem-solving), social (ability to form and sustain positive relationships with peers and adults), emotional (capacity to recognize, communicate, and regulate emotions), and behavioral (ability to control actions, follow rules, and behave adaptively) domains (Table 1); (c) all primary experimental studies, regardless of design (e.g., RCTs, quasi-experimental studies, or single-group pre-post studies), to obtain a broader and more comprehensive understanding of the evidence; (d) testing a non-pharmacological or non-surgical intervention; and (e) universal interventions designed for the general population regardless of risk level. Articles reporting a commentary, editorial, author response, erratum, expert report, review, book review, case and case series study, protocol, or abstract were excluded. Additionally, we excluded studies focused on children with diagnosed physical, psychiatric/mental health, or behavioral disorders such as autism, ADHD, Fragile X Syndrome, Down syndrome, Prader-Willi syndrome, nephrotic syndrome, hemophilia, brain tumor, overweight or obesity, palliative care, physical disability (e.g., visually impaired, language problem), and learning disability. Studies that evaluated preschool program models (e.g., Montessori learning, half-day vs full-day schedules, district-wide preschool programs, dual language program) were excluded, as the focus of this review was not on preschool program structure. We also excluded interventions targeting mental or emotional responses to medical procedures, such as stress, anxiety, or fear.
Study Screening
Articles were screened by six independent reviewers following first title and abstract screening and then full-text screening. For citations lacking full-text access, copies were requested through the university library and from corresponding authors. A reminder was sent one week later, and absence of a reply within two weeks was considered as a nonresponse. Review articles were tagged during screening for backward citation searching. Eligible articles were selected according to the developed inclusion and exclusion criteria. The team met monthly to discuss screening conflicts until reaching consensus.
Data Extraction
A data extraction scheme was developed according to previous published reviews (Ling et al., 2022; Ling et al., 2021). Specifically, we extracted data on sample characteristics (e.g., country, sample size, age, sex, ethnicity/race, parents’ demographics), study characteristics (e.g., study design, control group, funding, attrition rate), intervention, outcomes and measures, and main results. Data from each eligible article were extracted by one researcher and then independently verified by a second researcher. JL and SC then triple checked the completed summary table and any discrepancies were resolved through discussions.
We followed the BCIO to extract information on the content and delivery of interventions (Michie et al., 2021). Specifically, we extracted data on intervention setting (early years facility, household residence, social center or community hall facility), theoretical framework (yes, no), target population (child, family-child, family member, occupational role), interventionists (science and engineering professional, teaching professional, health professional, parent), and intervention strategies (advise how to change emotions behavior change techniques [BCT]; advise specific behavior BCT; awareness of other people's thoughts, feelings and actions BCT; guide how to perform behavior BCT; manage mental processes BCT; prompt thinking related to successful performance BCT).
Table 2 presents the BCTs used by interventions designed to improve young children’s mental well-being. Putative mechanisms were coded using BCIO-aligned constructs informed by the Mechanism of Action Ontology, which organizes mechanisms as hierarchically structured classes rather than a fixed set of categories (Schenk et al., 2024). Mechanisms of action were independently identified and coded by the study team using BCIO-aligned constructs. A coding crosswalk was developed to map BCTs to independently coded putative mechanisms of action, allowing for many-to-many relationships between intervention components and mechanisms in accordance with Schenk et al. (2024). Putative mechanisms of action were then mapped to the closest corresponding mechanisms in the Theory and Techniques Tool (TaTT), which includes 26 empirically derived mechanisms of action linked to BCTs. Where necessary, conceptually similar constructs were aligned to the nearest TaTT mechanism. Mechanisms and BCTs were presented separately, as they are conceptually distinct but may be related in multiple ways (Zhang et al., 2025).
Table 2.
Behaviour change techniques (BCTs) used by interventions designed to improve young children’s mental well-being
| Example Intervention Description |
BCT (BCIO Code) |
BCT Definition |
BCIO-aligned Putative Mechanism of Action |
TaTT aligned Mechanism of Action |
Mechanism Definition |
|---|---|---|---|---|---|
| Child emotional skill training (Lafay et al., 2023); Emotion Knowledge intervention using Emotional Knowledge & Affective Knowledge Task/Emotional State Talk (Ornaghi et al., 2017); Tuning into Kids (TIK) parent emotion coaching program (Qiu & Shum, 2022) | Advise how to change emotions (BCIO:007147) | A BCT that suggests a method to alter emotions. | Emotional awareness | Emotion | Ability to identify and label internal emotional states |
| Emotion regulation skills | Emotion; Behavioral regulation | Ability to modulate emotional responses using adaptive strategies | |||
| Cognitive reappraisal | Emotion; Memory, Attention, and Decision Processes | Modification of emotional responses through reinterpretation of stimuli | |||
| Structured playful activities using problem-solving games (Dereli, 2009); Parent-guided emotional and behavioral expression (Koopowitz et al., 2024); Incredible Years Teacher Classroom Management (Seabra-Santos et al., 2018) | Advise specific behavior (BCIO:007168) | A BCT that advises the person to perform a behavior in a particular way. | Behavioral capability | Skills | Acquisition of skills required to perform a behavior |
| Self-efficacy | Beliefs about capabilities | Belief in one’s capability to perform a behavior | |||
| Action planning | Behavior regulation, goals | Development of specific plans linking situations to behaviors | |||
| Pretend play and group play therapy (Bergman Deitcher et al., 2021); Buddy Up intervention (Hanish et al., 2022); Caregiver nurturing care interventions (Xu et al., 2023) | Awareness of other people's thoughts, feelings and actions (BCIO:007072) | A BCT that increases awareness of what other people think, do, or feel. | Theory of mind | Social influences, social cognition | Understanding that others have distinct mental states |
| Perspective taking | Social influences, social cognition | Ability to consider another person’s viewpoint | |||
| Social cognition | Social influences, social cognition | Processing and interpretation of social cues | |||
| Teacher professional development programs (Dinler et al., 2025); Preschool Life Skills program (Hanley et al., 2014); Incredible Years Teacher Classroom Management (Vale & Gaspar, 2024) | Guide how to perform behavior (BCIO:007050) | A BCT that provides guidance regarding how to perform the behavior. | Procedural knowledge | Knowledge | Knowledge of how to execute a behavior step-by-step |
| Skill acquisition | Skills | Development of competence through guided practice | |||
| Instructional clarity | Understanding context and resources | Reduction of ambiguity in behavior execution to support fidelity | |||
| Mindfulness-based activities (Jansen et al., 2025); Mindfulness/Philosophy for Children (Malboeuf-Hurtubise et al., 2020); Executive Function Training (Romero-López et al., 2025) | Manage mental processes (BCIO:007185) | A BCT that advises how to manage mental processes to facilitate the behavior. | Executive functioning | Memory, attention and decision processes | Cognitive processes supporting planning, inhibition, and flexibility |
| Cognitive control | Memory, Attention, and Decision Processes | Ability to regulate attention and inhibit impulsive responses | |||
| Attentional regulation | Memory, Attention, and Decision Processes | Ability to direct and sustain attention over time | |||
| Dialogic storybook reading and discussion (Linnavalli et al., 2024); Reflective play prompts (Tucker et al., 2017); Move for Thought (Vazou & Mavilidi, 2021) | Prompt thinking related to successful performance (BCIO:007239) | A BCT that prompts thinking relating to successful performance of the behavior. | Metacognition | Memory, Attention, and Decision Processes | Awareness and regulation of one’s own thinking processes |
| Self-monitoring | Behavioral regulation | Ongoing tracking of one’s behavior and performance | |||
| Reflective processing | Memory, Attention, and Decision Processes; Behavioral regulation | Evaluation of past behavior to inform future actions |
Notes. TaTT: Theory and Techniques Tool; BCIO: Behaviour Change Intervention Ontology.
For articles published in languages other than English, we used both DeepL and Google Translate to perform double translation for articles in Arabic, Dutch, French, German, Greek, Hungarian, Japanese, Portuguese, Russian, and Spanish. Articles in Persian were translated into English using ChatGPT 5. Although human translation is considered the gold standard, it is time-consuming and costly, particularly when screening and extracting data from large numbers of studies (Hendrickson et al., 2013; Turner et al., 2014). We used machine translation tools (DeepL, Google Translate, and ChatGPT) rather than human translators, because this approach preserves translation quality and is more efficient in time and cost (Chen & Lin, 2025; Turner et al., 2014), and is appropriate for the purposes of systematic review screening and data extraction (Balk et al., 2013; Kong et al., 2025). All extracted outcome data were cross-checked against the original source documents to ensure accuracy. Following translation into English, the same data extraction process was applied.
Assessment of Risk of Bias
Studies using an RCT design were evaluated using the revised Cochrane risk-of-bias tool for randomized trials (RoB 2; (Sterne et al., 2019). The RoB 2 tool includes five domains of bias, and each domain was rated as having a low (1), moderate (2), or high risk (3). For the randomization process, studies were rated as moderate risk if allocation concealment was not applied or if baseline characteristics were imbalanced, and as high risk if randomization methods were not reported and baseline characteristics were imbalanced. For deviations from intended interventions, studies were rated as moderate risk if intervention fidelity was not reported and as high risk if fidelity was low or poorly implemented. For missing outcome data, studies were rated as moderate risk if attrition exceeded 5% and significant differences between missing and non-missing participants were observed without appropriate statistical handling, and as high risk if attrition was not reported or exceeded 5% without comparison between missing and non-missing participants. For outcome measurements, studies were rated as moderate risk if data collectors were not blinded or outcomes relied on proxy reports, and as high risk if self-developed measures lacked psychometric evaluation or if outcome measures differed across groups. For selective reporting, studies were rated as moderate risk if the trial was not registered and as high risk if measured outcomes were not fully reported or if analytic methods were not described. The overall risk of bias was evaluated as low (all domains have a low risk), moderate (at least one domain has a moderate risk and no domain has a high risk), and high (at least one domain has a high risk).
Studies that applied a quasi-experimental design were assessed using the Risk Of Bias In Non-Randomized Studies - of Interventions (ROBINS-I; (Sterne et al., 2016). The ROBINS-I contains seven domains on confounding, selection of participants into the study, classification of interventions, deviations from intended intervention, missing data, outcome measurement, and selective reporting. The response choices for each domain are low (1), moderate (2), and high risk (3) of bias. For bias due to confounding, studies were rated as low risk when confounders were measured and approximately adjusted for, as moderate risk when some confounders were measured but not adequately examined or controlled for, and as high risk when potential confounders were not measured or adjusted for. For bias in the selection of participants into the study, studies were rated as moderate risk when participants were excluded after enrollment based on post-baseline factors, and as high risk when participant inclusion was determined by researcher or teacher selection rather than predefined eligibility criteria. For bias in the classification of interventions, studies were rated as low risk when the intervention and its components were clearly defined. The remaining domains (deviations from intended interventions, missing data, outcome measurement, and selective reporting) were evaluated using criteria consistent with the RoB 2 framework. Overall judgments were also rated as low (all domains had a low risk), moderate (at least one domain has a moderate risk), and high (at least one domain has a high risk).
To ensure uniform evaluation, JL and SC convened and developed rating schemes for this review, adhering to published detailed guidelines. Subsequently, the risk of bias for each study was assessed by one evaluator, with the second evaluator randomly and independently examining 20% of the studies. All studies were scrutinized in the event of identifying any inconsistencies. Disagreements were resolved through discussion between evaluators until consensus was achieved.
We applied the Grading of Recommendations Assessment, Development, and Evaluation (GRADE) system to assess the quality of evidence, that is our confidence in the pooled effect estimates (Guyatt et al., 2011). For each outcome, we assessed five domains: 1) risk of bias (proportion of studies at high risk, proportion of RCTs), 2) imprecision (total sample size, width of the 95% CI), 3) inconsistency (between-study heterogeneity and relevant subgroup analyses), 4) indirectness of the evidence, 5) publication bias (undetected vs strongly suspected [−1]; (Balshem et al., 2011). For domains 1-4, ratings were no concern (+1), serious concern (−1), or very serious concern (−2; (Puhan et al., 2014). We also considered factors that could increase quality of evidence: large effect (+1, or +2), dose response (+1), and no plausible confounding (+1). Overall quality of evidence for each outcome was categorized as high (4), moderate (3), low (2), or very low (1; (Puhan et al., 2014).
Statistical Synthesis and Analyses
The characteristics of included studies and interventions were synthesized with means, standard deviations, ranges, frequencies, and percentages. All meta-analyses were conducted in R (version 4.5.1). The data used in the analyses are provided in Supplemental Tables 2S–3S. All analyses were two-sided with a significance level of α = .05. Influential outliers were identified with studentized deleted residuals (∣z∣>1.96), Bonferroni-adjusted p-values<.05, DFFITS (standardized change in the fitted value when a study is deleted), Cook’s distance (overall influence of a study on all fitted values), leave-one-out τ2 (after removing each study), leave-one-out QE (residual heterogeneity test statistic with each study removed), hat values (leverage, extremity of each study), and weights (the inverse-variance contribution of each study to the fit; (Viechtbauer & Cheung, 2010). Influential outliers were excluded from further analyses. Effect sizes Hedges’ g (small [g = 0.20], medium [g = 0.50], and large [g = 0.80]) were calculated using multiple approaches based on the available data: (a) baseline and post-intervention means and standard deviations from one group or both groups, assuming a fixed within-group correlation of .59 (Balk et al., 2012); (b) change score means and standard deviations from one or both groups; (c) post-intervention means and standard deviations from both groups; (d) reported effect size (e.g., Cohen’s d, odds ratio); and (e) statistical test results and/or p-values for the effects of the intervention. Positive effect sizes indicate that the intervention group had better mental well-being compared to the control group at post-intervention or showed greater improvements from baseline to post-intervention. A 95% prediction interval was calculated from the random-effect models to estimate the range in which the true effect of a future similar study is expected to fall (IntHout et al., 2016). Sustainability of intervention effects was evaluated in two ways: (a) follow-up effects adjusted for baseline values, which accounted for baseline differences and provided more accurate estimates of effects at follow-up, and (b) maintenance of effects from post-intervention to follow-up. When the published data were insufficient, the corresponding author was contacted twice within two weeks to request additional data for calculating effect sizes.
We conducted random-effects models with restricted maximum likelihood (REML) estimation using the metafor package (Viechtbauer, 2010). We then applied cluster‐robust variance estimation (CR2) using the clubSandwich package to account for the potential dependencies among multiple outcomes within individual studies (Moeyaert et al., 2017; Pustejovsky & Tipton, 2018). Cochran’s Q test (test for null hypothesis of no between-study variability), Higgins & Thompson’s I2 (proportion of variability in estimates due to heterogeneity), and tau-squared (τ2, between-study variance of the true effects) were applied to assess the study’s heterogeneity (Stogiannis et al., 2024); with I2 of 25%, 50%, and 75% being low, moderate, and high levels of heterogeneity, respectively.
The Begg and Mazumdar rank correlation test, Egger’s regression asymmetry test (robust standard errors [SEs]), and contour-enhanced funnel plot (plotting effect size against SEs with regions corresponding to different levels of statistical significance) were employed to identify potential publication bias (Lin et al., 2018; Peters et al., 2008). Potential publication bias existed when results from either test were significant, and funnel plot was asymmetric. When there was evidence of potential publication bias, we applied the PublicationBias package to produce a significance funnel plot, which compared the pooled effect from all studies to the pooled effect of non-affirmative studies (Mathur & VanderWeele, 2020). This visualization indicated whether effects that were non-significant were systematically smaller. We then estimated publication-bias-adjusted pooled effects across a range of assumed selection ratios (η, the ratio of the publication probability of affirmative vs non-affirmative results; (Mathur & VanderWeele, 2020).
Moderation analyses were conducted on an exploratory basis. Potential moderators included both categorical (e.g., study design, intervention setting, intervention) and continuous variables (e.g., child mean age, proportion of ethnic/racial minority participants, intervention duration in weeks, intervention dose in hours). Ethnic/racial minority status was defined within the context of each study’s country, based on the classifications and reporting used in the original articles. Consistent with methodological guidance, categorical moderator analyses were conducted only for moderators with at least five studies per subgroup, and continuous moderator analyses were limited to moderators with at least 10 studies (Borenstein et al., 2021; Higgins et al., 2024). Single-moderator models were applied to reduce the risk of overfitting and unstable estimates given the limited number of studies (Borenstein et al., 2021). For categorical moderators, we conducted omnibus Wald tests with CR2 cluster-robust variance estimators. For continuous moderators, we performed random‐effects meta‐regression models, with inference based on CR2 small-sample-adjusted tests.
We conducted sensitivity analyses to examine whether our results were robust to the quality of study and reliability of measurement. Risk of bias was coded on a three-level ordinal scale (low = 1, moderate = 2, high = 3). Reliability of measurement was classified into two groups: 1) adequate/reported: utilized reliable and valid instruments or reliability met thresholds (e.g., Cronbach’s alpha or interrater reliability ≥ .70); and 2) low/unreported: no reliability coefficients were reported, or values were below the thresholds. Analytically, we refit the random-effects model after excluding high risk-of-bias studies or those with low/unreported reliability and compared pooled effects among risk-of-bias levels or reliability groups.
Results
Search Results
Figure 1 shows the PRISMA flow diagram. The literature search identified 21,942 studies (PubMed: 8,058; PsycINFO: 7,233; CINAHL: 6,651), and additional searches from other sources produced 853 references (Citation searching: 14; Grey literature: 839). After removing 4,562 duplicates, authors screened titles and abstracts of 18,233 studies. The first screening resulted in 517 (2.8%) articles sought for full-text retrieval and eligibility assessment. Following full-text screening, 383 (74.1%) articles were excluded due to ineligible participants or study design, abstract only, not original research, did not report the effects of the intervention, or no relevant outcomes. Finally, 134 (25.9%) eligible articles reporting on 133 studies were included in this review. Due to insufficient data for calculating effect sizes and unsuccessful attempts to contact corresponding authors, one (0.7%) study was excluded from the meta-analysis.
Figure 1.
Study flow diagram
Study Characteristics
Among the 133 included studies (Supplemental Table 4S and Table 3), 43 (32.3%) were conducted in the United States, 11 (8.3%) in Spain, 10 (7.5%) in Turkey, 9 (6.8%) in Germany, 8 (6.0%) in China, 7 (5.3%) in Italy, and 6 (4.5%) in Canada; many countries were represented by one study each. Regarding the study design, 35 (26.3%) were RCTs, 33 (24.8%) used cluster RCTs, and 65 (48.9%) employed quasi-experimental designs, including 21 (32.3%) one-group, 40 (61.5%) two-group, 3 (4.6%) three-group, and 1 (1.5%) 3x2 factorial design. Among the 112 studies with a control group, 80 (71.4%) utilized usual care, 16 (14.3%) employed attention control, 15 (13.4%) used waitlist control, and 1 (0.9%) study included both usual care and attention control. The total number of participants across all studies was 32,512, with an average of 244 (SD = 393.35) and a median of 106 participants per study, ranging from 9 to 2,625 with a mode of 43. Reported attrition rates ranged from 0% to 47.3%, and 63 studies (47.4%) did not report attrition.
Table 3.
Characteristics of studies and interventions
| Study characteristics | M (n) | SD (%) |
|---|---|---|
| Number of studies | 133 | |
| Language (non-English) | 13 | 9.8% |
| Study setting (country) | ||
| Argentina | 1 | 0.7% |
| Australia | 3 | 2.3% |
| Brazil | 3 | 2.3% |
| Canada | 6 | 4.5% |
| Chili | 1 | 0.7% |
| China | 8 | 6.0% |
| Croatia | 1 | 0.7% |
| Ethiopia | 1 | 0.7% |
| Finland | 2 | 1.5% |
| France | 2 | 1.5% |
| Germany | 9 | 6.8% |
| Greece | 4 | 3.0% |
| Iran | 2 | 1.5% |
| Ireland | 1 | 0.7% |
| Israel | 1 | 0.7% |
| Italy | 7 | 5.3% |
| Jamaica | 1 | 0.7% |
| Japan | 2 | 1.5% |
| Mozambique | 1 | 0.7% |
| Norway | 1 | 0.7% |
| Peru | 1 | 0.7% |
| Portugal | 4 | 3.0% |
| Romania | 3 | 2.3% |
| South Africa | 1 | 0.7% |
| Serbia | 1 | 0.7% |
| Spain | 11 | 8.3% |
| Switzerland | 1 | 0.7% |
| Turkey | 10 | 7.5% |
| United Kingdom | 1 | 0.7% |
| United States | 43 | 32.3% |
| Study design | ||
| 2-group RCT | 32 | 24.0% |
| 3-group RCT | 3 | 2.3% |
| 2-group cluster RCT | 32 | 24.0% |
| 3-group cluster RCT | 1 | 0.8% |
| 1-group quasi-experimental | 21 | 15.8% |
| 2-group quasi-experimental | 40 | 30.1% |
| 3-group quasi-experimental | 3 | 2.3% |
| 3x2 factorial | 1 | 0.7% |
| Control group | ||
| No control | 21 | 15.8% |
| Attention | 16 | 12.0% |
| Usual care | 80 | 60.2% |
| Usually care and attention | 1 | .8% |
| Waitlist | 15 | 11.3% |
| Child age (years, range: 1-6.10) | 4.42 | 1.01 |
| Child sex (%female, range: 0.08-1.0) | 0.49 | 0.09 |
| Child ethnicity/race (%minority, range: 0-1.0) | 0.51 | 0.34 |
| Intervention characteristics | ||
| Number of interventions | 141 | |
| Intervention duration (weeks, range: 1-156) | 22.63 | 24.15 |
| Intervention dose (hours, range: 0.25-390) | 24.37 | 46.74 |
| Intervention setting | ||
| Early years facility | 127 | 90.1% |
| Household residence | 5 | 3.5% |
| Social center or community hall facility | 9 | 6.4% |
| Theoretical framework (yes) | 45 | 31.9% |
| Target population | ||
| Child | 109 | 77.3% |
| Family member | 7 | 5.0% |
| Family-child | 9 | 6.4% |
| Occupational role | 16 | 11.3% |
| Interventionists | ||
| Health professional | 8 | 5.7% |
| Parent | 3 | 2.1% |
| Science and engineering professional | 45 | 31.9% |
| Teaching professional | 85 | 60.3% |
| Intervention strategies | ||
| Advise how to change emotions BCI | 16 | 11.3% |
| Advise specific behavior BCI | 8 | 5.7% |
| Awareness of other people's thoughts, feelings and actions BCI | 28 | 19.9% |
| Guide how to perform behavior BCI | 35 | 24.8% |
| Manage mental processes BCI | 10 | 7.1% |
| Prompt thinking related to successful performance BCI | 44 | 31.2% |
Notes. m: mean; n: frequency; SD: standard deviation.
Intervention Characteristics
The 133 studies collectively reported 141 interventions (Tabel 3). Among the 141 interventions, 127 (90.1%) were conducted in an early year facility, 5 (3.5%) at a household residence, and 9 (6.4%) at a social center or community hall facility. Only 45 interventions (31.9%) were grounded in a theoretical framework. There was a diverse range of theoretical frameworks. Social learning-based and cognitive-behavioral theories, such as Social Learning Theory and Social Cognitive Theory (Bayrak & Akman, 2018; Chiou et al., 2013; Dereli, 2009; Ștefan et al., 2023; Xu et al., 2023), were most frequently reported. Several studies also referenced social-cognitive frameworks, such as Theory of Mind and Mentalization Theory (Gavazzi & Ornaghi, 2011; Linnavalli et al., 2024; Paik et al., 2022); emotional and self-regulation theories, including Emotional Competence Theory and Achievement Goal Theory (Aadland et al., 2024; San Pío et al., 2023; Sansone & Iatesta, 2022); and relational and ecological models, such as Attachment Theory and Ecological Systems Theory (Dinler & Cevher-Kalburan, 2025; Tucker et al., 2017). Regarding target population, 109 interventions (90.1%) focused on children only, 9 (6.4%) targeted both children and their family members, 16 (11.3%) focused on occupational role such as teachers, and 7 (5.0%) targeted family members only. As for interventionists, 85 (60.3%) were teaching professionals, 45 (31.9%) were science and engineering professionals (e.g., researchers), 8 (5.7%) were health professionals (e.g., psychologist, clinician, consultant, specialist, licensed counselor), and 3 (2.1%) were parents.
The behavior change techniques implemented across the 141 interventions were categorized using the BCIO framework as: (a) advise how to change emotions BCI (n = 16, 11.3%); (b) advise specific behavior BCI (n = 8, 5.7%); (c) awareness of other people's thoughts, feelings and actions BCI (n = 28, 19.9%); (d) guide how to perform behavior BCI (n = 35, 24.8%); (e) manage mental processes BCI (n = 10, 7.1%); and (f) prompt thinking related to successful performance BCI (n = 44, 31.2%). The average duration of interventions was 22.63 weeks (SD = 24.15), with a median duration of 13 weeks, and a range of 1 to 156 weeks. The average intervention dose was 24.37 hours (SD = 46.74; median = 13), ranging from 0.25 to 390 hours.
Effects at Post-Intervention
Before removing any influential outliers, the overall effects of interventions on children’s mental well-being were g = 0.42 (k = 631, n = 140; 95% CI [0.33, 0.51]; p < .001). The heterogeneity was large with τ2 = 0.38 (Q = 10855.54, p < .001) and I2 = 96.3%. Fifteen influential outliers were identified (z = 3.00-9.04; DFFITS = 0.12-0.55; Cooks’ds = 0.01-0.26; τ2del = 0.31-0.37; QE = 9125.56-10821.28; hat = 0.001-0.002; weights = 0.05-0.18). After removing these outliers, the effects decreased to g = 0.35 (k = 616, n = 137; 95% CI [0.29, 0.41]; p < .001), with a large heterogeneity I2 = 92.2% (τ2 = 0.17; Q = 5393.66, p < .001).
Table 4 demonstrates the effects of interventions on mental well-being by domains. All heterogeneity was large. The overall effects of interventions were g = 0.35 (95% CI [0.23, 0.48], 0.36 (95% CI [0.26, 0.46]), 0.38 (95% CI [0.28, 0.48]), and 0.31 (95% CI [0.22, 0.40]) on cognitive, social, emotional, and behavioral domains, respectively. These effects did not significantly differ from each other (F = 0.51, p = .677). After excluding one-group quasi-experimental designs, effect estimates decreased slightly (g = 0.27-0.34), and heterogeneity remained high. We therefore retained all studies for subsequent analyses. Based on the GRADE assessment, the overall quality of evidence for effects at post-intervention was moderate. The 95% prediction intervals were wide, ranging from −0.49 to 1.22 across models, indicating substantial between-study heterogeneity and suggesting that true effects in future studies may vary from negative to large positive values.
Table 4.
Effects at post-intervention on mental well-being by domains
| Outcome | k | n | Hedges’ g | 95% CI |
#
95% Predictive
interval |
Heterogeneity |
Quality
of Evidence |
|||
|---|---|---|---|---|---|---|---|---|---|---|
| I 2 | τ2 | Q | p-value | |||||||
| All studies | ||||||||||
| Mental well-being | 616 | 137 | 0.35 | 0.29, 0.41 | −0.46, 1.16 | 92.2% | 0.17 | 5393.66 | <.001 | 3 |
| Cognitive | 102 | 51 | 0.35 | 0.23, 0.48 | −0.45, 1.16 | 90.4% | 0.17 | 600.90 | <.001 | 3 |
| Social | 188 | 82 | 0.36 | 0.26, 0.46 | −0.43, 1.15 | 89.8% | 0.16 | 1143.26 | <.001 | 3 |
| Emotional | 154 | 82 | 0.38 | 0.28, 0.48 | −0.46, 1.22 | 93.8% | 0.18 | 1937.69 | <.001 | 3 |
| Behavioral | 172 | 85 | 0.31 | 0.22, 0.40 | −0.49, 1.11 | 92.9% | 0.16 | 1555.06 | <.001 | 3 |
| Studies without one-group quasi-experimental designs | ||||||||||
| Mental well-being | 534 | 117 | 0.31 | 0.24, 0.36 | −0.47, 1.07 | 91.0% | 0.15 | 4101.54 | <.001 | |
| Cognitive | 96 | 46 | 0.33 | 0.20, 0.45 | −0.46, 1.11 | 90.4% | 0.16 | 545.98 | <.001 | |
| Social | 159 | 69 | 0.28 | 0.20, 0.37 | −0.41, 0.98 | 86.5% | 0.13 | 842.65 | <.001 | |
| Emotional | 130 | 72 | 0.34 | 0.23, 0.45 | −0.51, 1.19 | 94.0% | 0.19 | 1593.28 | <.001 | |
| Behavioral | 149 | 74 | 0.27 | 0.17, 0.36 | −0.49, 1.02 | 90.6% | 0.15 | 955.72 | <.001 | |
Notes. k: number of estimates; n: number of clusters/studies/interventions; df: degree of freedom; CI: confidence interval. Positive effect sizes indicate the intervention group experienced greater improvements in mental well-being outcomes compared to the control group or showed an increase in mental well-being outcomes from baseline to post-intervention; #95% prediction intervals were derived from the random-effects model, as robust variance estimation does not directly provide prediction intervals.
Moderation Analysis
As shown in Tables 5 and 6, study design (F = 5.67, p = .003), control group (F = 5.03, p = .008), and intervention target (F = 5.83, p = .013) were identified as significant moderators. Relative to one-group quasi-experimental designs (g = 0.66), effects were lower for two-group quasi-experimental designs (g = −0.30), RCTs (g = −0.28), and cluster RCTs (g = −0.42). Similarly, studies with attention control (g = 0.41) or no control group (g = 0.25) yielded larger effects than those using usual care (g = −0.13) or waitlist (g = −0.11). By intervention target, interventions targeting child only (g = 0.38) had the largest effects, followed by those targeting family and child (g = −0.09), the occupational role (e.g., teachers; g = −0.11), and family member only (g=−0.26).
Table 5.
Potential categorical moderators for effects at post-intervention
| Categorical Moderator | k | n |
Hedges’
g △ |
df | 95%CI | p-value | F | p-value |
|---|---|---|---|---|---|---|---|---|
| Country | 1.37 | .286 | ||||||
| Canada (ref) | 27 | 7 | 0.12 | 4.64 | −0.17, 0.40 | .340 | ||
| China – ref | 21 | 8 | 0.26 | 8.51 | −0.07, 0.60 | .109 | ||
| Germany – ref | 39 | 9 | 0.12 | 9.23 | −0.18, 0.41 | .389 | ||
| Italy – ref | 26 | 8 | 0.26 | 9.93 | −0.25, 0.78 | .281 | ||
| Spain – ref | 74 | 13 | 0.32 | 7.25 | −0.08, 0.72 | .099 | ||
| Turkey – ref | 27 | 9 | 0.51 | 9.17 | 0.10, 0.91 | .019 | ||
| United States – ref | 217 | 44 | 0.17 | 5.6 | −0.12, 0.47 | .197 | ||
| Study design | 5.67 | .003 | ||||||
| 1-group quasi-experimental (ref) | 82 | 20 | 0.66 | 10.11 | 0.46, 0.86 | <.001 | ||
| 2-group quasi-experimental – ref | 149 | 38 | −0.30 | 21.35 | −0.53, −0.07 | .012 | ||
| 2-group RCT – ref | 148 | 32 | −0.28 | 21.83 | −0.53, −0.03 | .028 | ||
| 2-group cluster RCT – ref | 134 | 31 | −0.42 | 20.52 | −0.63, −0.21 | <.001 | ||
| Control group | 5.03 | .008 | ||||||
| Attention (ref) | 72 | 19 | 0.41 | 11.13 | 0.19, 0.63 | .002 | ||
| No control – ref | 82 | 20 | 0.25 | 21.24 | −0.02, 0.53 | .070 | ||
| Usual care – ref | 388 | 85 | −0.13 | 15.48 | −0.35, 0.10 | .244 | ||
| Waitlist – ref | 74 | 16 | −0.11 | 20.03 | −0.37, 0.14 | .371 | ||
| Intervention setting | 0.27 | .776 | ||||||
| Early years facility (ref) | 575 | 123 | 0.35 | 78.74 | 0.28, 0.41 | <.001 | ||
| Household residence – ref | 9 | 5 | −0.08 | 2.68 | −0.43, 0.27 | .514 | ||
| Social center or community hall facility – ref | 32 | 9 | 0.05 | 5.63 | −0.45, 0.56 | .797 | ||
| Theory | 0.07 | .792 | ||||||
| No (ref) | 435 | 93 | 0.36 | 56.64 | 0.28, 0.44 | <.001 | ||
| Yes – ref | 181 | 44 | −0.02 | 55.04 | −0.15, 0.12 | .792 | ||
| Intervention target | 5.83 | .013 | ||||||
| Child (ref) | 464 | 105 | 0.38 | 65.51 | 0.30, 0.46 | <.001 | ||
| Family member – ref | 32 | 7 | −0.26 | 5.05 | −0.40, −0.11 | .006 | ||
| Family-child – ref | 34 | 9 | −0.09 | 5.26 | −0.30, 0.11 | .310 | ||
| Occupational role – ref | 86 | 16 | −0.11 | 13.31 | −0.27, 0.06 | .189 | ||
| Intervener | 0.81 | .467 | ||||||
| Health professional (ref) | 47 | 7 | 0.25 | 4.30 | −0.08, 0.58 | .103 | ||
| Science and engineering professional – ref | 191 | 45 | 0.16 | 6.87 | −0.16, 0.48 | .284 | ||
| Teaching professional – ref | 374 | 82 | 0.09 | 5.40 | −0.24, 0.41 | .535 | ||
| Intervention | 0.32 | .897 | ||||||
| Advise how to change emotions BCI (ref) | 81 | 17 | 0.36 | 10.94 | 0.18, 0.53 | .001 | ||
| Advise specific behavior BCI – ref | 33 | 8 | −0.11 | 7.58 | −0.57, 0.36 | .615 | ||
| Awareness of other people's thoughts/feelings/actions BCI – ref | 113 | 26 | 0.07 | 23.41 | −0.15, 0.29 | .499 | ||
| Guide how to perform behavior BCI – ref | 139 | 33 | −0.02 | 23.33 | −0.24, 0.19 | .818 | ||
| Manage mental processes BCI – ref | 56 | 10 | 0.02 | 11.88 | −0.32, 0.37 | .877 | ||
| Prompt thinking related to successful performance BCI – ref | 194 | 43 | −0.04 | 21.28 | −0.24, 0.17 | .723 |
Notes. k: number of estimates; n: number of clusters/studies/interventions; df: degree of freedom; CI: confidence interval. Positive effect sizes in the reference groups indicate the intervention group experienced greater improvements in mental well-being outcomes compared to the control group or showed an increase in mental well-being outcomes from baseline to post-intervention. Effect sizes for other groups were calculated as the reference-group effect size + the estimated difference (△).
Table 6.
Potential continuous moderators for effects at post-intervention
| Moderator | k | n | Coefficient | 95%CI | p-value |
|---|---|---|---|---|---|
| Child mean age | 440 | 102 | 0.03 | −0.05, 0.12 | .460 |
| Percent female child | 574 | 125 | −0.66 | −1.89, 0.57 | .267 |
| Percent ethnic/racial minority child | 265 | 53 | −0.14 | −0.49, 0.21 | .426 |
| Intervention duration in weeks | 585 | 129 | −0.0002 | −0.004, 0.003 | .925 |
| Intervention dose in hours | 485 | 101 | −0.001 | −0.006, 0.005 | .643 |
Notes. k: number of estimates; n: number of clusters/studies/interventions.
Sustainability of Intervention Effects
Sixteen studies (12.0%) reporting 17 interventions examined the sustainability of effects with an average follow-up duration of 11.83 months (SD = 13.06, median = 6.5, mode = 12, range: 1-48). We evaluated whether the effects of interventions were sustained in two ways: 1) follow-up effects adjusted for baseline values, and 2) maintenance of effects from post-intervention to follow-up.
Among the 15 interventions with a follow-up effect, two influential outliers were identified (z = 5.50, 5.97; QE = 286.06, 297.03). Before removing any outliers, the pooled effect was g = 0.25 (k = 72, n = 15; 95% CI [0.03, 0.48]; 95% prediction interval [−0.55, 1.06]; p = .030) on mental well-being. Between-study heterogeneity was τ2 = 0.16 (Q = 333.64, p < .001) and I2 = 79.9%. After removing the two influential outliers, the effects decreased to g = 0.22 (k = 70, n = 14; 95% CI [0.03, 0.41]; 95% prediction interval [−0.41, 0.86]; p = .026), with a moderate heterogeneity I2 = 71.7% (τ2 = 0.10; Q = 249.40, p < .001). The follow-up effects did not vary by outcome domain (F = 0.41, p = .759) or follow-up duration (B = 0.05, p = .103).
Among the 16 interventions examining the maintenance of effects, four influential outliers (z = −2.73, 2.97, −3.25, −5.77, QE = 157.89, 152.06, 158.19, 138.23) were noted. Before removing the outliers, the pooled effects on mental well-being were g = 0.02 (k = 81, n = 16; 95% CI [−0.05, 0.08]; 95% prediction interval [−0.26, 0.30]; p = .531), and between-study heterogeneity was moderate (τ2 = 0.02; Q = 172.26, p < .001; I2 = 40.1%). After removing the four outliers, the pooled effects increased to g = 0.04 (k = 77, n = 15; 95% CI [−0.01, 0.08]; 95% prediction interval [−0.10, 0.17]; p = .114) and heterogeneity was small (τ2 = 0.004; Q = 90.80, p = .118; I2 = 11.6%). Effects were not maintained differently by outcome domain (F = 2.28, p = .321) or follow-up duration (B = −0.001, p = .680). The overall quality of evidence for the sustainability of intervention effects was very low.
Sensitivity Analysis by Risk of Bias and Reliability of Measurement
After excluding high-risk studies, the pooled effects decreased slightly from g = 0.35 to 0.31 (k = 193, n = 39; 95% CI [0.20, 0.43]; p < .001), with heterogeneity remaining high (I2 = 93.1%; τ2 = 0.16; Q = 2132.63, p < .001). Excluding low-risk studies, the pooled effects were unchanged (k = 614, n = 136; g = 0.35; 95% CI [0.28, 0.41]); p < .001). Nevertheless, effect sizes varied significantly by the level of risk of bias (F = 69.50, p = .003), with the largest effects observed among low-risk studies (g = 1.24; 95% CI [0.51, 1.97]; df = 1; p = .030), followed by high-risk (g = 0.37) and moderate-risk (g = 0.31) studies.
The effects of interventions were not significantly associated with the reliability of measurement (F = 0.46, p = .528). After excluding studies with low or unreported reliability, the pooled effects remained stable (k = 608, n = 134; g = 0.35; 95% CI [0.28, 0.41]; p < .001), and heterogeneity was still high (I2 = 92.2%; τ2 = 0.17; Q = 5347.66, p < .001).
Publication Bias
Effects at Post-Intervention
Publication bias was evident for the post-intervention effects (Tau = 0.16, p < .001; intercept = 0.35, 95% CI [0.29-0.41], p < .001; Figure 2 contour-enhanced funnel plot). Visual inspection of the significance funnel (Figure 3) showed that the pooled effects based on non-affirmative studies alone were near zero, indicating that the overall effects were largely driven by affirmative studies. According to the bias-sensitivity analysis results (Table 7), under no assumed selection (η = 1), the pooled effects were 0.35; assuming moderate selection favoring affirmative results (η = 5) attenuated the effects to 0.14 (≈ 60% reduction). The effects were still significant even under extreme selection (η = 1000).
Figure 2.
Contour-enhanced funnel plot (effect size vs. standard error) visualizing publication bias for effects at post-intervention
Figure 3.
Significance funnel plot visualizing publication bias for effects at post-intervention
Notes. Black dots: affirmative studies; grey dots: non-affirmative studies
Table 7.
Publication bias-corrected effects at post-intervention on selection ratios η (k=616, n=137)
| Assumed η | Hedges’ g | 95% CI | p-value |
|---|---|---|---|
| 1 (no publication bias) | 0.35 | 0.29, 0.41 | <.001 |
| 2 | 0.24 | 0.19, 0.30 | <.001 |
| 3 | 0.19 | 0.14, 0.24 | <.001 |
| 4 | 0.16 | 0.12, 0.21 | <.001 |
| 5 | 0.14 | 0.10, 0.18 | <.001 |
| 10 | 0.10 | 0.06, 0.13 | <.001 |
| 20 | 0.07 | 0.03, 0.11 | <.001 |
| 30 | 0.06 | 0.02, 0.09 | .001 |
| 40 | 0.06 | 0.02, 0.09 | .002 |
| 50 | 0.05 | 0.02, 0.09 | .003 |
| 100 | 0.05 | 0.01, 0.08 | .004 |
| 200 | 0.05 | 0.01, 0.08 | .005 |
| 300 | 0.04 | 0.01, 0.08 | .006 |
| 400 | 0.04 | 0.01, 0.08 | .007 |
| 500 | 0.04 | 0.01, 0.08 | .007 |
| 600 | 0.04 | 0.01, 0.08 | .011 |
| 700 | 0.04 | 0.01, 0.08 | .013 |
| 800 | 0.04 | 0.01, 0.08 | .014 |
| 900 | 0.04 | 0.01, 0.08 | .015 |
| 1000 | 0.04 | 0.01, 0.08 | .015 |
Notes. η: the ratio of the publication probability of affirmative vs. non-affirmative results.
Sustainability of Intervention Effects
No evidence of publication bias was noted for the maintenance of effects (Tau = −0.07, p = .388; intercept = 0.04, 95% CI [−0.01, 0.08], p = .114), but there was some potential publication bias for the follow-up effects (Tau = −0.07, p = .368; intercept = 0.22, 95% CI [0.03, 0.41], p = .026; Figure 4a contour-enhanced funnel plot). Figure 4b (significance funnel plot) shows that the pooled effect based only on non-affirmative studies was notably smaller than the overall pooled effect, indicating some publication bias favoring affirmative results. Table 8 presents the sensitivity analysis results with selection ratios ranging from 1 to 10. The threshold selection ratio was η = 2, implying that even modest preferential publication of affirmative findings would render the pooled effect statistically indistinguishable from zero.
Figure 4a.
Contour-enhanced funnel plot (effect size vs. standard error) visualizing publication bias for effects at follow-up
Figure 4b. Significance funnel plot visualizing publication bias for effects at follow-up
Notes. Grey dots: non-affirmative studies; black dots: affirmative studies
Table 8.
Publication bias-corrected effects at follow-up on selection ratios η (k=70, n=14)
| Assumed η | Hedges’ g | 95% CI | p-value |
|---|---|---|---|
| 1 (no publication bias) | 0.22 | 0.03, 0.41 | .026 |
| 2 | 0.15 | −0.02, 0.31 | .070 |
| 3 | 0.11 | −0.04, 0.27 | .109 |
| 4 | 0.10 | −0.05, 0.24 | .143 |
| 5 | 0.09 | −0.05, 0.23 | .172 |
| 6 | 0.08 | −0.06, 0.22 | .197 |
| 7 | 0.08 | −0.06, 0.21 | .219 |
| 8 | 0.07 | −0.06, 0.21 | .237 |
| 9 | 0.07 | −0.07, 0.20 | .253 |
| 10 | 0.07 | −0.07, 0.20 | .266 |
Notes. η: the ratio of the publication probability of affirmative vs. non-affirmative results.
Risk of Bias
The risk of bias evaluation for the included 68 RCTs is summarized in Supplemental Table 5S. Of these, 53 (77.9%) studies had a high risk of bias, 14 (20.6%) had a moderate risk of bias, and only one (1.5%) had a low risk of bias. Five (7.4%) studies demonstrated issues such as lack of concealment or unbalanced baselines, resulting in a moderate risk of bias for the randomization domain. Thirty-two (47.1%) studies were rated as high risk for intervention due to the absence of intent-to-treat (ITT) analysis. Intervention fidelity information was missing for 17 (25.0%) studies, leading to a moderate risk of bias rating. Forty-two (61.8%) studies failed to report attrition/missing data or comparisons between missing and non-missing data when the attrition rate exceeded 5%, resulting in a high risk of bias for the missing data domain. For the measurement domain, 48 (70.6%) studies were considered to have a moderate risk due to unblinded assessors and proxy-reported data. Regarding the domain of bias in the selection of reported results, nine (13.2%) studies were rated as high risk due to a lack of reported data analysis, and 46 (67.6%) were assessed as having a moderate risk because they were not pre-registered.
Supplemental Table 6S demonstrates the assessment of risk of bias for the 65 included non-RCTs. Among these, 23 (35.4%) studies were rated as having a moderate risk of bias, and 42 (64.6%) had a high risk. Fourteen (21.5%) studies were rated as having moderate risk and fifteen (23.1%) as high risk of bias in the confounding domain. For participant selection, three studies were rated as high risk due to purposeful selection by center directors or teachers. All studies clearly defined their interventions, yielding a low risk of bias. Forty-four (67.7%) studies lacked information on intervention fidelity, resulting in a moderate risk of bias. Two studies were rated as high risk as one has a wide variation in intervention duration (10-47 weeks; (Fitzgerald et al., 2018) and the other intervention was not implemented consistently (Schick & Cierpka, 2006). Regarding the missing data domain, 35 (53.8%) studies were rated as high risk because they either provided no information on missing data or failed to address missing rates exceeding 5%. Subjective measures were employed in 34 (52.3%) studies, resulting in a moderate risk of bias. Additionally, 56 (86.2%) studies were not registered, and 8 (12.3%) studies failed to report data analysis methods.
Discussion
This systematic review and meta-analysis, comprising 133 studies reporting 141 interventions, comprehensively evaluated the effectiveness of universal interventions on young children’s mental well-being across cognitive, social, emotional, and behavioral domains. The findings revealed that universal interventions have achieved only small to medium effect sizes with moderate certainty of evidence. Additionally, the effects of interventions varied significantly by study design, control group, and intervention target. These findings suggest that contextual and design characteristics may influence the effectiveness of interventions and highlight the potential value of tailoring interventions to specific populations and implementation settings.
The overall effects of interventions designed to promote young children’s mental well-being are small to medium (g = 0.31-0.38), aligning well with the most recent research. For instance, a previous meta-analysis of 33 studies identified small effects of classroom-based socioemotional interventions on emotional competence (g = 0.33), social competence (g = 0.42), and challenging behaviors (g = −0.31; (Luo et al., 2022). A large meta-analysis of 63 studies reported medium effects of universal, socioemotional learning programs on emotional competence (d = 0.54) and small effects on social competence (d = 0.30), behavioral self-regulation (d = 0.28), and behavioral and emotional challenges (d = −0.19; (Blewitt et al., 2018). Another global review of 102 studies reported small to medium effects of parent-targeted interventions on cognitive (d = 0.32), socioemotional development (d = 0.19), and behavior problems (d = −0.13) among children aged 0-3 years (Jeong et al., 2021). Given these small-to-medium effects, further work is needed to identify key mechanisms of change and optimal delivery strategies to increase impact.
Although a small follow-up effect (g = 0.22) remained after adjustment for baseline, assuming modest publication bias (η = 2) rendered it non-significant, and maintenance from post-intervention to follow-up was negligible (g = 0.04). To our knowledge, no prior review has synthesized the sustained effects among young children. By contrast, evidence in school-age youth (5-18 years) indicates some sustainability of effects on mental health. For example, one review of 138 studies with 12-month follow-ups found that effects of psychological interventions on mental health were maintained at follow-ups (g = 0.31; (Pilling et al., 2020). Similarly, another review of 57 trials observed short-term (≤ 12 months) follow-up effects on reducing depressive and anxiety symptoms, and long-term (> 12 months) follow-up effects on decreasing internalizing problems (Dray et al., 2017). One plausible explanation is developmental capacity: older children and adolescents may be more capable of acquiring and retaining mental health literacy to support sustained effects over time (Freţian et al., 2021). Nevertheless, early intervention remains essential given the lifelong consequences of early childhood mental health concerns (Mercy & Saul, 2009). Notably, only 12% of studies in our review included any follow-up (mean duration = 12 months) and certainty of evidence was very low. Therefore, future trials should focus on examining whether the effects of interventions can be sustained beyond early childhood and evaluating cost-effectiveness relative to interventions targeting school-age youth.
Our review found that child-focused interventions consistently outperformed those targeting family member, family-child, or occupational role alone. The results align with growing research calling for improved mental health literacy among children and youth and for empowering them as active agents of change (Choi, 2023; Pavarini et al., 2023). Because children spend the majority of their day in school, schools are a natural platform for universal prevention (Hoover & Bostic, 2021). Despite strong recognition of the urgent need for school-based mental health programs, barriers such as limited funding, stigma, competing academic demands, and resource constraints, hinder their broader dissemination and sustainability (Carlock et al., 2023). These barriers underscore the need for policymakers and educators to secure dedicated funding and resources, integrate mental health literacy and skill training into routine curricula, and build implementation capacity to support sustainable, school-based, child-focused mental health programs.
The additional benefits of parental involvement remain inconclusive due to inconsistent results in the literature. Though some studies report that engaging parents enhances young children’s emotional competence and social skills as well as reduces emotional and behavioral difficulties (Barlow et al., 2016; Luo et al., 2022), our review found that child-only programs overperformed those that involved parents. In contrast, a recent umbrella review of 152 reviews among children aged 4-9 years old found that behavior-based interventions targeting both parents and children were more effective in reducing children’s externalizing behaviors than parent-only interventions, and more effective in reducing anxiety than child-only interventions (Hudson et al., 2023). Nonetheless, the review did not identify conclusive evidence of additional benefits from simultaneously targeting both children and parents for other outcomes, such as social skills. Importantly, Hudson et al.’s umbrella review primarily examined treatment interventions for young children with existing behavioral or mental health conditions, including ADHD, autism spectrum disorder, anxiety, depression, selective mutism, behavioral problems, and trauma. In such contexts, parental involvement may be particularly critical because parents play a central role in supporting treatment implementation and reinforcing behavioral strategies at home (Dekkers et al., 2021; Lawrence et al., 2021). In contrast, studies included in this review evaluated universal interventions, in which parental engagement may be more variable and less intensive. Differences in the intensity and nature of parental involvement across intervention contexts may therefore influence the effectiveness of parent-inclusive interventions.
Additionally, Luo et al. (2022) reported in a meta-analysis of 39 studies that interventions incorporating parental components were associated with larger improvements in preschoolers’ social competence (g = 0.69 vs 0.25) and greater reductions in challenging behaviors (g = −0.52 vs −0.18) compared with interventions without a family component. Differences in methods may partly explain the discrepancy between these findings and those of the present review. For example, Luo et al. (2022) did not adjust for clustering effects within studies and selected a single effect size for each outcome based on measures with stronger psychometric properties or teacher ratings. These analytic decisions may have influenced the magnitude of the estimated effects. In contrast, the current review applied more conservative analytic procedures, which may yield more cautious estimates of the effects of interventions. Given these discrepancies, more rigorous studies are needed to better specify and assess parental engagement and determine whether actively involving parents adds benefits to child-focused interventions.
Our findings reveal that one-group quasi-experimental studies, despite their lower internal validity and limited generalizability, were associated with larger effects than more rigorous designs (e.g., two-group quasi-experiment and RCTs). The results may reflect methodological biases inherent in less rigorous study designs. The result is consistent with a prior meta-analysis showing that effects of interventions diminished from −0.81 to −0.67 after excluding quasi-experimental studies from analyses (Barlow et al., 2016). In our review, removing all one-group quasi-experimental studies did not substantially change the pooled effects. These studies had larger SEs and therefore received lower inverse-variance weights under the random-effects model. Even though quasi-experimental designs have clear limitations, their flexibility and adaptability may be more suitable for addressing mental health problems in rapidly changing populations. We also observed that studies conducted in Turkey tended to show larger effects than those from other countries (e.g., Spain, Italy, China, the United States, Canada, and Germany), although the difference was not statistically significant. Attention to country-specific and cultural factors may help design more contextually responsive interventions for young children’s mental well-being (Bernard et al., 2021).
Consistent with a prior review of health behavior interventions (Prestwich et al., 2014), the presence of a reported theoretical framework did not significantly moderate the effects of interventions. The null finding may reflect reporting rather than true absence of theory: although 32% of studies did not specify a guiding framework, many interventions were likely theory-informed but not explicitly documented, leading to misclassification in the moderator analysis. Additionally, heterogeneity in how theory was operationalized (e.g., partial vs full alignment of components with mechanisms) could attenuate observable effects. These results underscore the need to report theory more transparently (e.g., specifying constructs, hypothesized mechanisms, and theory-component mapping) and fidelity measures that capture adherence to theory-based elements. We recommend using a consistent Theory Coding Scheme to describe the theoretical framework guiding intervention development, to ensure comprehensive and transparent reporting (Michie & Prestwich, 2010).
Drawing on the theoretical frameworks reported in the included studies, many interventions are designed to improve children’s mental well-being by targeting proximal skills such as self-regulation, social cognition, and emotion understanding. These approaches are grounded in social learning, cognitive-behavioral, and emotional competence theories (Bandura, 1991; Denham, 2023; Kendall, 2011). Changes in these proximal mechanisms may be modest or insufficiently reinforced across contexts, which may limit longer-term impacts. Ecological and transactional theories suggest that without concurrent changes in family, school, or broader environmental contexts, early gains may fade over time (Sameroff & Fiese, 2000). The finding that child-focused interventions showed more consistent effects than those involving parents may indicate that mechanisms operating directly at the child level, such as skill acquisition or in-the-moment behavioral regulation, are more immediately influential than indirect pathways through parents, which may be constrained by contextual factors (Burney et al., 2024). Notably, although many studies referenced theories, few empirically tested proposed mediators, underscoring an important gap and the need for future research to directly examine mechanisms of change.
Another important finding is the inadequate attention given to the fidelity monitoring and reporting of intervention implementation. Only slightly more than half of the studies (54.1%) reported their approaches for monitoring fidelity, despite its significant role in evaluating the effectiveness of interventions (Sanetti et al., 2021). The low rates of reported fidelity monitoring may contribute to the observed pattern in which professionally delivered interventions showed somewhat greater effects than parent-led interventions. Moreover, the small to medium effects at post-intervention and negligible maintenance effects likely reflect insufficient monitoring of how interventions were delivered in many studies. Self-monitoring, where interventionists observe and assess their own delivery using recorded sessions, has been suggested as a promising strategy for improving fidelity (Scheibel et al., 2022). In addition, developing intervention-specific checklists and scoring systems while identifying key fidelity components (delivery, receipt, enactment) can strengthen intervention implementation (Baker et al., 2024; Ginsburg et al., 2021). Future trials should embed prospective implementation fidelity plans (standardized checklists, dose tracking, observation/audit-feedback) to reduce implementation drift and improve effects.
The results also highlight insufficient emphasis on transparent reporting and trial preregistration, contributing to moderate to high risk of bias. Consistent with prior literature showing that 56% of trials reported a CONSORT flow diagram yet many omitted the attrition data (Hopewell et al., 2011), this review found that about 47% did not report an attrition rate. Information on loss to follow up is essential for interpreting the effective sample size and evaluating the validity of final results. Although ITT analysis is recommended for RCTs to handle protocol deviations and missing data (Gupta, 2011), 47% RCTs in our review did not report using ITT, though some may have applied it without explicitly stating so. Additionally, clinical trial registration was reported in only 23% of included manuscripts in this review, despite recommendations that registration be mandated for transparency and as best practice in clinical research (Aslam et al., 2013). Low registration rates may also contribute to the publication bias observed in this review. Although trial registration has dramatically increased, global variation persists (Viergever & Li, 2015), indicating the need for consistent international guidelines. Collectively, these reporting gaps argue for mandated adherence to reporting guidelines (e.g., CONSORT, PRISMA) to ensure transparency and reproducibility.
Strengths and Limitations
The strengths of this systematic review and meta-analysis include its comprehensive scope, encompassing a large number of studies and interventions across multiple geographic regions and various cultural contexts and languages, providing a robust and diverse body of evidence. The application of advanced statistical techniques, such as random-effects meta-analysis with cluster-robust variance estimation, omnibus Wald tests, and meta-regression, enabled an objective and nuanced evaluation of the effects of interventions, enhancing the reliability and interpretability of the findings. The application of the BCIO framework to classify content and delivery of interventions enhanced transparency and comparability. In addition, GRADE system was utilized to rate certainty of evidence, further strengthening confidence in the findings.
This review has several limitations. First, the substantial heterogeneity and high levels of risk of bias among included studies and interventions complicate interpretation of the results and necessitate cautious conclusions, particularly the results from exploratory moderation analyses. Removing high-risk studies produced little change in the pooled effects, and the larger effect observed in the only low-risk study is not trustworthy due to the extremely small low-risk sample. Second, potential publication biases were identified for post-intervention and follow-up effects, potentially leading to an overestimation of the effects of interventions. Whereas the effect estimate at post-intervention is sensitive to publication bias, the evidence is not fully explained by plausible levels of selection; the bias-robust effect is likely smaller than the conventional meta-analytic estimate. Third, the use of varying tools or methods to measure outcomes across studies may have affected the comparability and synthesis of results, although results were relatively robust according to the reliability of measurement. There is potential overlap across mental health domains, as many measures capture multiple aspects of child functioning. Domain classification was therefore guided by outcome operationalization within each study, which may have introduced some imprecision in categorization. Additionally, inconsistent results reported in literature, coupled with unsuccessful attempts to contact corresponding authors, may have introduced biases into the effect size calculations. Grey literature searching was restricted to ClinicalTrials.gov and MedRxiv, limiting the comprehensiveness of the literature captured. The meta-analysis did not account for certain potential confounders, such as baseline differences in participant characteristics or contextual policy and environmental factors, which may have influenced the results.
Conclusions
This comprehensive meta-analytic review with 133 studies found overall small to medium effects of universal interventions at post-intervention on enhancing mental well-being across cognitive, social, emotional, and behavioral domains among children aged 0-6 years old. The overall certainty of evidence was moderate. Sustained effects at follow-up were negligible, and child-focused interventions tended to yield larger immediate effects. Given the high study heterogeneity, risk of bias, and potential publication bias, interpreting the results of the review warrants caution. Future research with longer follow-up may focus on evaluating sustainability of intervention effects and identifying the additional benefits of actively engaging parents or other family members, while ensuring study implementation fidelity and reporting transparency across diverse settings.
Supplementary Material
Public Significance Statement.
This review finds that programs designed for all children can improve young children’s mental well-being, though the benefits are typically small to moderate across cognitive, social, emotional, and behavioral domains. Over an average follow-up period of approximately 12 months, most early gains diminish, with only small benefits remaining at follow-up. Programs that work directly with children appear most effective, and adding active parental involvement does not result in larger effects.
Acknowledgement:
We would like to acknowledge Jessica Sender, MS, a health sciences librarian at Michigan State University, for her valuable contribution to the systematic literature search. We also acknowledge the contributions of PhD students Esra’a Sawalmeh and Orawee Changrueang at Michigan State University College of Nursing in literature screening, data extraction, and data entry. Special thanks to Paige Ellis, an undergraduate student at Michigan State University College of Nursing, for her assistance with data entry.
Funding:
Research reported in this publication was supported in part by the National Center For Complementary and Integrative Health of the National Institutes of Health under Award Number UH3AT012521 (PI: Jiying Ling). The content is solely the responsibility of the authors and does not necessarily represent the official views of the National Institutes of Health.
Footnotes
Transparency and Openness. Generative artificial intelligence was not used in this research.
Data Availability Statement.
The data used in the meta-analysis are available at the following link: https://osf.io/bhxug/overview?view_only=ab1f3d54711d4a6f94b91d6b55df3003
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Associated Data
This section collects any data citations, data availability statements, or supplementary materials included in this article.
Supplementary Materials
Data Availability Statement
The data used in the meta-analysis are available at the following link: https://osf.io/bhxug/overview?view_only=ab1f3d54711d4a6f94b91d6b55df3003