Screening for depression in children and adolescents: a protocol for a systematic review update

From the 2014 Ontario Child Health Study, the 6-month prevalence of possible major depressive episodes (MDE) was 1.1% for children (4- to 11-year-old) and 5.2% or 7.5% for adolescents (12- to 17-years-old) based on parent or adolescent report, respectively [8]. In pooled estimates from the Canadian Community Health Survey, a series of cross-sectional surveys from 2000 to 2014, 5.5% of 12- to 19-year-olds reported experiencing MDE-like episodes in the past year, with little change in prevalence from 2000 to 2014 [9]. Rates were higher among females and among those aged 15 to 19 years (10.1% for females; 4.1% for males) compared to those aged 12 to 14 years (4.1% for females; 0.6% for males) [9], with similar findings supported by other literature [10‐12].

The burden of depression is high among children and adolescents. Unipolar depressive disorders (i.e., major depressive episode, dysthymia) are a leading cause of years lost to disability among both the 10- to 14-year-old and 15- to 19-year-old age groups [13, 14]. Poor long-term social outcomes are also a consequence of depression in adolescence. Those with depression are at an increased risk of leaving secondary school, unemployment, early pregnancy, and parenthood [15]. As well, they have a lower likelihood of entering post-secondary education [15]. Depression with onset in childhood and adolescence can continue into adulthood, posing a burden on individuals, families, and communities [15‐18]. A recent systematic review found that adolescents who suffer from depression have around 2.5 (2.78 [95% CI 1.97, 3.93]) times the odds of developing depression in adulthood compared with adolescents without depression [16]. Additionally, those who suffer from depression in adolescence are at an increased risk for suicidal ideation, attempts, and completion in adulthood [19‐21].

There are several risk factors associated with depression in children and adolescents. As shown above, females are at a higher risk, particularly in adolescence, with the difference between sexes becoming smaller later in adulthood [12, 22]. A family history of depression and exposure to adverse events such as illness or death of a family member, physical or sexual abuse, are also strong risk factors [23, 24]. Parental behaviors associated with an increased risk include aversive behaviors toward the child or adolescent (e.g., criticism, punishment, and conflict), lack of autonomy given to the child or adolescent, lack of warmth, inconsistent parental discipline, and parental over-involvement [25]. Other influential factors include aspects related to the school environment such as bullying, low connectedness with peers and teachers [26, 27], poor academic achievement [28], learning disabilities (e.g., attention deficit hyperactivity disorder, dyslexia) [29‐31], and community environment factors such as safety, ethnicity, and prevalence of discrimination [32]. Additional risk factors include substance abuse (e.g., alcohol, tobacco, cannabis, other illicit drugs), poor sleep, screen time, unhealthy diet, and weight problems [33‐35].

A screening program for depression must identify symptomatic disease that would not otherwise be reported (e.g., by spontaneous patient self-report, parent/caregiver report, or clinical inquiry). If effective, screening for depression would be expected to lead to interventions that improve future health outcomes in those who otherwise would not have been identified [36]. However, as noted by Cosgrove et al. [37], without evidence on the benefits and harms of screening, there are several assumptions that are questionable in the case of depression screening. First, unlike other disorders, depression does not have a detectable asymptomatic early stage. It manifests as one or more discrete episodes and many patients remit after an initial episode. Screening tools rely on identifying symptoms of depression itself and therefore can only be effective at early detection if the use of the tool prompts consideration of whether or not symptoms of depression are present. Second, there is currently little evidence that adding screening questionnaires to primary care reduces depressive symptoms. Third, optimal treatment for screen-detected depression is not clear. Most people identified as depressed via screening will have mild symptoms that may resolve without intervention. Many are treated with antidepressant medications. However, the majority of antidepressant medications have not been shown to be as effective in adolescents as in adults, may increase risk for suicidality, and may be even less likely to be effective for the mild cases likely overrepresented in patients identified through screening questionnaires [38, 39]. Psychological therapies are a reasonable option to medications with some positive effects [40, 41].

In considering the potential benefits and harms of screening, the proper design of trials is paramount [42, 43]. Experts have criticized previous systematic reviews on depression screening that have not explicitly defined the characteristics of screening trials to isolate the effect of screening from, for example, diagnostic suspicion by patients or clinicians [44, 45]. For example, a screening trial should separate the effect of screening from the effect of providing additional treatment resources not otherwise available. Since screening programs should only identify previously unrecognized cases, a screening trial should also exclude patients already diagnosed or under care for depression [42]. Accordingly, we have specified criteria that would need to be met to reduce selection and confounding bias in the inclusion of evidence. These are detailed in the “Methods” section.

In 2005, the Canadian Task Force on Preventive Health Care (“Task Force”) published recommendations on screening for depression in the adult population as well as children and adolescents. The Task Force guideline concluded that there was insufficient evidence to recommend either for or against depression screening in children and adolescents [46]. In 2016, the U.S. Preventive Services Task Force (USPSTF) updated their 2009 guideline and systematic review and recommended routinely screening for depression in adolescents (age 12 to 18 years) in primary care settings “with adequate systems in place to ensure accurate diagnosis, effective treatment, and appropriate follow-up,” but not in children (aged ≤ 11 years) due to insufficient evidence [47, 48]. The USPSTF recommendation for screening relied on indirect and linked evidence that screening instruments for depression can accurately identify MDD in adolescents and that treatment of MDD detected through screening in adolescents is associated with moderate benefit. However, this was not based on screening trials, as no trials were identified that directly assessed the effects of screening compared with no screening [48]. The recommendation was based on eight “fair- “or “good-quality” placebo-controlled intervention trials examining the effectiveness of antidepressants, psychotherapy, and collaborative care interventions (e.g., the Massachusetts Child Psychiatry Access Project, an inter-professional collaboration among primary care providers and mental health specialists) for children and adolescents with MDD. They found that one trial had shown effectiveness with fluoxetine as well as combined fluoxetine and cognitive behavioral therapy. Furthermore, one of the two escitalopram trials and the one collaborative care trial had demonstrated benefits. The USPSTF considered the evidence on screening test accuracy and treatment of MDD adequate and the harms of pharmacotherapy treatment to be minimal if patients were closely monitored. Similar to the USPSTF, the Guidelines for Adolescent Depression in Primary Care (GLAD-PC) Steering Group updated their 2007 systematic literature review and guideline [49] and found no evidence comparing screening to no screening or usual care in primary care settings [50]. They relied upon indirect evidence surrounding the validity and feasibility of screening tools and the feasibility and effectiveness of treatment for individuals with depression. GLAD-PC recommended annual screening for depression in adolescents (ages 12 and older) based on psychometric data on depression screening tools as well as research on screening issues (e.g., whether screening is occurring and whether screening impacts follow-up procedures or treatment to the specifics of screening). They considered that early identification and treatment of adolescent depression is important because of the high prevalence of depression and its persistence, its potential occurrence during a crucial brain development period, and the potential consequences with transition into adulthood. Among those with depression risk factors ages 10 to 21 years, GLAD-PC recommended not only annual screening but also more frequent targeted screening (i.e., systematically monitoring individuals over time for the development of a depressive disorder) during other health care visits. Their justification for this recommendation was that these individuals are likely to experience future depressive episodes and those who are not diagnosed with depression but report high scores on the screening tools may be at risk for depression within 6 months [50].

There are inconsistencies among the current screening guidelines reviewed above, notably their reliance on indirect evidence and the failure to include RCTs where the potential impacts of screening and treatment are clearly separated. A recent review by Roseman and colleagues [51] was selected by the Task Force working group as an appropriate review to update but with modifications, such as also addressing patients that may have an elevated risk of depression, including other outcomes of relevance to decision making, other study design filters, and expanding the search approach. This review update will provide a current assessment of the evidence for the Task Force guideline recommendations.

This protocol was developed by the ERSC and reviewed by their clinical experts and patient representative, the Depression working group members and their external clinical experts, the PHAC, Task Force members, and stakeholder organizations.

The protocol was prepared following the Preferred Reporting Items for Systematic Reviews and Meta-Analyses Protocols (PRISMA-P checklist) [53] (Additional file 2). The project is registered with the International Prospective Registry of Systematic Reviews (PROSPERO) database (CRD42020150373). The final review will be reported using the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA) checklist and the A Measurement Tool to Assess Systematic Reviews (AMSTAR 2) tool will be used for additional quality control [54, 55]. We will document any amendments to this study protocol in PROSPERO and present them in the final manuscript.

Studies for the review will be selected for inclusion according to the eligibility criteria presented in Table 1. Randomized controlled trials (RCTs) examining depression screening tools among patients who are up to 17 years of age will be eligible. If no or only a single RCT is available, controlled studies without random assignment will be sought. Studies that include other ages (e.g., 6 to 20 years of age), but present results separately for those up to 17 will be included and those that do not present results separately for the relevant ages will be excluded. Children will be defined as 6 to 11 years of age and adolescents will be defined as 12 to 17 years of age. For KQ1a, the target population will include patients who are selected for screening because they have characteristics that suggest elevated risk of depression. In all cases, we will include studies where caregivers respond to screening tool questions on behalf of children.

The depression screening tool can be a single question, a small set of questions, or a screening questionnaire (validated or not) with a pre-defined cut-off score to identify patients who may have depression but who have not reported their symptoms to healthcare providers or who have otherwise not been identified as possibly depressed by healthcare providers. The eligible comparator will be no depression screening. Both the screening and no screening arms will offer the same interventions for patients identified with depression symptoms. We will consider “no screening” to reflect normal clinical care that requires ongoing active observation and conversation with patients around symptoms suggestive of depression but no use of a formalized screening instrument. Depression screening should involve administering a depression symptom questionnaire to all patients and using a pre-identified cut-off threshold to classify patients as having positive or negative screening results. Accordingly, the use of a screening tool without the consideration of a pre-defined cut-off threshold would not be considered screening. Those with positive screening results can then be evaluated to determine if they have depression and, if appropriate, be offered treatment.

Studies in primary care or non-mental health clinic settings (e.g., medical specialist clinics, schools, or recreational/community settings) and online settings where screening is administered by a health practitioner will be eligible. Since this is a review update from Roseman et al. [51], we will continue to limit to RCTs and include reports from January 2017 onwards. If non-randomized controlled studies are sought, we will search from January 2015 onwards and replace the RCT study filter with a non-randomized controlled study design filter. The search date will be based on the latest search from the 2016 USPSTF review (February 2015), which did not find any non-randomized controlled studies assessing the effects of screening [48]. Their search would be difficult to replicate as it used one search for multiple key questions that were not relevant for this project. However, the USPSTF had similar eligibility criteria to ours for their key question on the effectiveness of screening and we will consider their list of excluded studies to ensure all studies of interest are captured. Reports will be restricted to those written in English and French. Previous literature suggests including other languages when reviewing topics such as complementary and alternative medicines interventions [56]. We will use the following inclusion criteria from a recent depression screening systematic review to determine eligible RCTs and controlled studies without random assignment, where possible [43, 57]: (1) the patient population is clearly defined and randomized prior to administering the screening test (only applies to RCTs); (2) patients known to have a diagnosis of depression, or who are being treated for depression are excluded (screening is intended to identify undetected cases, and those who are known to have depression should not be screened in clinical practice); and (3) similar resources for depression management and treatment must be available both to patients in the screening arm of the trial and to patients in the non-screening arm of the trial who are identified as depressed via other methods (e.g., unaided clinician diagnosis, patient report).

Members of the Depression working group developed the list of preliminary outcomes of interest, presented in Table 1. Through consensus, those outcomes were rated by the six working group members according to GRADE methodology as critical (rated 7 to 9 out of 9), important (rated 4 to 6 out of 9), or of limited importance (rated 1 to 3 out of 9) for making guideline recommendations [58]; only critical and important outcomes will be included. These outcomes will also be rated, according to GRADE methodology, by relevant groups of patients who are unaware of the working group ratings through the Task Force patient engagement activities conducted by the Knowledge Translation Program at St. Michael’s Hospital in Toronto, Ontario. The list of outcomes will be finalized before final study selection and data extraction, and the PROSPERO record will be updated, as required. For more details on the outcome rating process, please see https://​canadiantaskforc​e.​ca/​methods/​ for the working group outcome rating and https://​canadiantaskforc​e.​ca/​methods/​patient-preferences-protocol/​ for rating through patient engagement.

Outcomes will not be used in the selection of studies. Based on ratings to date by the six working group members, outcomes of interest deemed of critical importance for guideline development and decision-making are the symptoms of depression or diagnosis of MDD (average rating of 8.7), suicidality (average rating of 7.5), health-related quality of life (average rating of 6.8), social function (average rating of 6.5), and impacts on lifestyle behavior such as substance use (average rating of 6.5). Outcomes rated as important are school performance (average rating of 6.2), harms of treatment (average rating of 6.2), lost time at work or school (average rating of 5.5), false-positive result, overdiagnosis, or overtreatment (average rating 5.5), and labeling (average rating of 4.7). No outcomes were rated as limited importance. The outcomes are listed in Table 1.

The search strategies were developed and tested through an iterative process by an experienced medical information specialist in consultation with the review team. Using the OVID platform, we will search Ovid MEDLINE®, including Epub Ahead of Print and In-Process & Other Non-Indexed Citations, Embase Classic+Embase, and PsycINFO. We will also search the Cumulative Index to Nursing and Allied Health Literature (CINAHL) (Ebsco) and CENTRAL (Wiley). The searches will utilize a combination of controlled vocabulary (e.g., “Depressive Disorder,” “Mass Screening,” “Adolescent”) and keywords (e.g., MDD, screen, pediatric). We will apply an amended version of the 2008 Cochrane Highly Sensitive Search Strategy, sensitivity- and precision-maximizing version, to identify randomized controlled trials, and an additional filter to identify non-randomized controlled studies. Vocabulary and syntax will be adjusted across the databases. There will be no language restrictions, but results will be limited to the period of 2017 to the present for RCTs and 2015 for non-randomized controlled studies. Animal-only and opinion pieces will be removed from the results.

The draft search strategy for the MEDLINE database was peer-reviewed by another experienced librarian using the Peer Review of Electronic Search Strategies (PRESS) checklist [59], modified where necessary, and then translated to other databases. The draft strategies are available in Additional file 3.

We will search grey literature sources to identify studies not formally published in journals and any ongoing trials using the Canadian Agency for Drugs and Technologies in Health (CADTH) Grey Matters checklist [60]. The CADTH checklist includes public health websites, health technology assessment agencies, clinical practice guideline organizations, clinical trials registries, search engines, and additional databases. We will also search the websites of the following organizations: American Academy of Child and Adolescent Psychiatry, American Academy of Family Physicians, American Academy of Pediatrics, American College of Physicians, American Nurses Association, American Psychological Association, Anxiety and Depression Association of America, Canadian Academy of Child and Adolescent Psychiatry, Canadian Mental Health Association, Canadian Nurses Association, Canadian Paediatric Society, Canadian Psychiatric Association, Centre for Addiction and Mental Health, Child Mind Institute, and the College of Family Physicians of Canada. Searches for grey literature will be restricted to English and French language documents and limited to a 5-day maximum search period by one person. The reference list of included studies and secondary evidence reports (e.g., evidence-based clinical practice guidelines, systematic reviews, and meta-analyses) will also be reviewed. Using Robinson et al. (2014) as guidance [61], a review would need to meet the following criteria to be considered systematic: (1) At least one database was searched; (2) authors report selection criteria; (3) risk of bias (or intended analogous) of included studies is reported; and (4) authors report a list and synthesis of included studies.

Citations from bibliographic databases, grey literature, and supplemental source searching will be collated in Reference Manager [62]. Those citations will be de-duplicated and uploaded to an online systematic review management software package, DistillerSR [63]. A pilot test will be conducted by two reviewers for title and abstract (random sample of 50 citations) and full-text levels (random sample of 25 articles) to test the screening questions and to ensure consistent application of the selection criteria among reviewers. Adjustments to the forms will be made as needed.

Title and abstract screening will be performed by two reviewers using the liberal accelerated method [64]. This approach involves one reviewer screening citations and a second reviewer verifying the citations excluded by the first reviewer. References will be screened in random order, and screening will be done concurrently among reviewers to reduce the likelihood that a citation has been already considered by another reviewer. Conflict resolution will not be conducted at this stage.

At the full-text screening stage, two reviewers will independently and in duplicate review the full text of potentially relevant articles to determine eligibility. Conflicts will be resolved by consensus or by consulting with a senior team member. Reviewers will agree on the reasons for exclusion at the full-text stage.

Where study eligibility is unclear, authors will be contacted for additional information twice by email over three weeks. Where input is needed for potentially eligible studies, we will consult with working group members and clinical experts who are blinded to study identification information and outcome data. Articles that are not available electronically will be ordered via interlibrary loan, allowing 30 days for receipt. Potentially relevant studies available only in abstract form will be excluded and the citation will be annotated in the list of excluded studies. To reduce potential bias, we will consult with working group members and clinical experts on any potentially missing studies once all outstanding queries related to synthesizing the evidence are addressed. Draft screening forms are available in Additional file 4.

Before commencing data extraction, we will pilot the data extraction form in DistillerSR on a random sample of full-text articles (three to six articles, depending on the number of included studies) and modify the form as needed. Two reviewers will independently extract data, compare data sets, discuss, and resolve any conflicts through discussion. If consensus cannot be reached, we will consult with a senior team member. Study authors will be contacted by email twice over 3 weeks for further information as required. We will extract all formats of continuous outcome data whether reported as post-intervention or change from baseline. Draft items for data extraction are provided in Additional file 5, and clinical experts and the working group will be consulted on extraction variables.

Concurrently with data extraction, we will follow Task Force methods and will appraise the risk of bias (ROB) using the Cochrane ROB tool for RCTs [65] and the Newcastle-Ottawa Scale (NOS) for non-randomized controlled studies [66]. Two reviewers will independently assess the ROB of all included studies, compare assessments, and resolve any assessments and their supports for judgments where disagreement has occurred. This will be done by consensus or by consulting with a senior team member when required. The Cochrane ROB tool consists of the following seven domains: (1) random sequence generation, (2) allocation concealment, (3) blinding of participants and personnel, (4) blinding of outcome assessment, (5) incomplete outcome data, (6) selective reporting, and (7) other sources of bias. As recommended by the Cochrane Handbook [67], certain domains are outcome-specific (e.g., blinding of outcome assessors) and will be assessed at the outcome level. The overall ROB will require the consideration of the relative importance of the seven domains accompanied by the known empirical evidence of bias, likely direction of bias, and likely magnitude of bias [65]. For outcome and analysis reporting bias, we will use the methods outlined in the Agency for Healthcare Research and Quality guidance [68]. For assessing cluster randomized trials, we plan to assess recruitment bias (when trial recruitment follows after clusters have been randomized and the knowledge of intervention and control clusters could affect the types of participants recruited) in the “other risks of bias” domain of the Cochrane ROB tool [69]. We will classify the overall ROB as low if all domains were assessed at low ROB, high if at least one domain was assessed at high ROB, or unclear if at least one domain was assessed at unclear ROB and no domain was at high risk.

The NOS for cohort studies consists of the following three domains: (1) selection of study groups, (2) comparability of study groups, and (3) outcome assessment. Each item within the selection (4 items) and outcome (3 items) domains can be awarded a maximum of one point, and two points for the single item in the comparability domain. A study can be awarded a maximum of nine points for the least risk of bias [66]. We will classify good quality studies as scoring at least 3 stars in the selection domain, at least 1 star in comparability, and at least 2 stars in the outcome domain. A fair quality study will require 2 stars in selection, at least 1 star in comparability, and at least 2 stars in the outcome domain. A poor-quality study will score 0 or 1 star(s) in selection, or 0 stars in comparability, or 0 or 1 star(s) in the outcome domain.

The individual study ROB and NOS assessments will inform the study limitations domain assessment across studies for each outcome using GRADE assessments, described in the following sections [70].

We will describe and present in summary tables the study characteristics, participant characteristics, intervention and comparator details, outcome results, and Cochrane ROB or NOS evaluations. We will convert data (e.g., recovery of intervention group standard deviations from standard errors or 95% confidence intervals) to facilitate consistent presentation and synthesis of the results across studies. We will calculate the appropriate statistics based on the type of outcome data. Relative and absolute effects with 95% confidence intervals will be calculated to facilitate the presentation of outcome data according to the GRADE guidance for developing evidence profile tables and summary of findings. Risk ratios and risk differences will be used to report effects for binary data. When presenting continuous data, GRADE guidance will be used [71]. Where needed, we will use a conservative value for a correlation coefficient of 0.25 to impute standard deviations for means used in change from baseline calculations, as performed in other reviews [72]. Studies with a cluster design (e.g., allocation by clinical setting) with data analyzed at the individual level (e.g., patients) will provide incorrect estimates of precision if correlation within clusters is not taken into account [73]. Where authors of cluster randomized trials have not adjusted for unit-of-analysis errors, we will attempt to correct these by using intra-class correlation coefficients (ICC) when available and by estimating ICCs when not [67, 74]. Where possible, the number needed to screen will be calculated.