Omega‐3 fatty acid supplementation for depression in children and adolescents

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

Main Objective:

This review aims to determine the impact of omega‐3 PUFA supplementation versus a comparator (e.g. placebo, wait‐list control) on clinician‐diagnosed depression or self‐reported depression symptoms in children and adolescents aged 6 to 19 years.

Secondary objectives are:

1. Estimate the size of the effect of omega‐3 PUFAs on depression;

2. Estimate the effect of each type of omega‐3 PUFA (EPA or DHA), compared with placebo, on depression;

3. Determine if the effect is modified by dosage, format (capsule or liquid), sex or age.

Background

Mental health problems, including depression, often start in childhood or adolescence. In 2020, the WHO reported that almost 20% of children and adolescents experience mental health disorders globally with the most common being anxiety and depression (WHO 2020). Depression usually emerges after puberty but starts to increase in prevalence around 10 years of age, especially in girls (Maughan 2013). Treatment options for childhood and adolescent Major Depressive Disorder (MDD) and depressive symptoms include pharmacological, psychological, and combined approaches. Poor response to current treatment and high remission rates indicate a need for new treatments (Brent 2008; Goodyer 2007; Locher 2017; Weisz 2017). An emerging potential treatment is omega‐3 polyunsaturated fatty acids (PUFA) which are naturally found in fatty fish, marine sources, as well as some nuts and seeds. Recent evidence from systematic reviews of omega‐3 PUFA has demonstrated efficacy in treating MDD in adults (Liao 2019; Hallahan 2016; Mocking 2016; Luo 2020; Zhang 2019), though uncertainties about the quality of the available evidence remain (Appleton 2015). These beneficial effects of omega‐3 PUFA are likely dependent on dosage and type (Hallahan 2016; Mocking 2016; Luo 2020; Liao 2019; Zhang 2019). The current review will examine the efficacy of omega‐3 PUFA treatment for depression in children and adolescents.

Description of the condition

MDD and dysthymia are two common types of unipolar depressive disorders that occur in childhood and adolescence. MDD is a common mental health disorder, characterised by a persistent sad mood, irritability, or loss of interest in activities for at least two weeks (APA 2019). Persistent depressive disorder, also called dysthymia, is similar to MDD and characterised by less profound though longstanding sadness, with continued symptoms for at least one year (APA 2019). Children and adolescents with unipolar depression may also display loss of energy, change in appetite or sleeping patterns, restlessness, feelings of worthlessness, guilt, hopelessness, indecisiveness, or thoughts of self‐harm or suicide (APA 2019). The diagnostic criteria of childhood depression do not differ from adult depression, except that children and adolescents may experience irritability rather than sadness. Diagnosis is achieved following clinical assessment. Individuals who exhibit symptoms of depression that do not reach the cut‐off for a formal diagnosis, termed 'subthreshold' depression are also subject to an increased risk of major depressive disorder and a decreased quality of life (Bertha 2013). Depression is a broad term used to describe these disorders.

Despite its high prevalence and socioeconomic impact, the pathophysiology of depression is not well understood (Deacon 2017). Depression often has biological, psychological, and social underpinnings (Maughan 2013). Risk factors for depression include familial, genetic, psychosocial, and neural/neuroendocrine risks (APA 2019). During childhood and adolescence, depression has far‐reaching negative implications on physical, emotional, and social development (WHO 2020). The impacts of MDD and its associated consequences may decrease the overall quality of life and health outcomes of affected youth, including increased illness severity, increased risk of comorbidity, hospitalization, obesity, and premature cardiovascular death (Korczak 2009; Luppino 2010; Osby 2001). MDD affects approximately 1 to 2% of children, and prevalence increases to 5 to 8% with adolescent age (Maughan 2013). In adolescents, depression is a major cause of disability and can increase the risk of death by suicide which is the second leading cause of death for people aged 15 to 19 years (WHO 2020). 

Description of the intervention

Omega‐3 PUFA are an emerging treatment for depression and other neuropsychiatric disorders. There are three types of naturally occurring lipids, classified by the number of carbon‐carbon double bonds present in their fatty acid side chains: saturated, monounsaturated, and PUFA. PUFA are further classified into two groups, based on the position of the first carbon‐carbon double bond site: n‐3 or omega‐3 and n‐6 or omega‐6 (Deacon 2017). A growing body of evidence indicates that omega‐3 PUFA are effective in improving depression and depressive symptoms (Liao 2019; Hallahan 2016; Mocking 2016; Luo 2020; Liao 2019; Zhang 2019) though uncertainties remain (Appleton 2015).

Omega‐3 PUFA are considered essential as they cannot be synthesized in the body, and are naturally found in plant and animal food sources. There are three main omega‐3 fatty acids: (1) alpha‐linolenic acid (ALA); (2) eicosapentaenoic acid (EPA); and (3) docosahexaenoic acid (DHA). ALA is found in plant sources such as canola, hemp, walnuts and flaxseed (Logan 2004). Within the body, ALA is converted to eicosapentaenoic acid (EPA) and docosahexaenoic acid (DHA) (Parker 2006). The conversion of ALA to EPA and DHA is inefficient in humans, with studies suggesting that only 1% to 15% of ALA is metabolized (a process which takes place primarily in the liver) (Harris 2010; Sontrop 2006). Dietary sources of EPA and DHA include oily fish such as tuna, salmon, mackerel, or sardines. Dietary supplements may contain combinations of EPA and DHA however, the most effective dietary supplement preparations for depression in adults have at least 60% EPA relative to DHA (Liao 2019). Fish oils, which contain both EPA and DHA, have been associated with reduced depression risk in observational research.  Consuming EPA and DHA directly from foods or dietary supplements is considered the most effective way to increase levels of these fatty acids in the body with six months being the minimum duration of supplementation for omega‐3 PUFA to equilibrate into the brain (Browning 2012).

Omega‐3 PUFA supplementation is currently recommended by the International Society for Nutritional Psychiatry Research (ISNPR) as a preventative treatment for depression in high‐risk adult populations (Guu 2019). The Canadian Network for Mood and Anxiety Treatments (CANMAT) (Ravindran 2016) also recommends omega‐3 PUFA as a second‐line monotherapy for adults with mild to moderate MDD, or adjunctive to antidepressants for adults with moderate to severe MDD. Currently, no guidelines exist for children or adolescents. 

How the intervention might work

Omega‐3 PUFA likely act on multiple processes within the body and are necessary for brain function and development. The role of omega‐3 PUFA in the treatment of paediatric depression has been suggested to have the same pathway of action as in adults. The benefits of omega‐3 PUFA intake on depressive illness have been hypothesised to occur as a result of their effect on neurotransmission, maintenance of membrane fluidity, and anti‐inflammatory action (Burhani 2017; Khanna 2019). Omega‐3 PUFA are also crucially important for brain development. Omega‐3 PUFA metabolism is needed for myelination and synaptic pruning, which are core processes during normal pubertal brain development (McNamara 2019). Omega‐3 PUFA may also counteract changes in the hippocampus seen in individuals with depression (Godos 2019; Kang 2013). 

Omega‐3 PUFA are essential components of intracellular and neuronal cell membranes, affecting cell membrane integrity and fluidity and resulting in improved neurotransmission. Membrane organization and the associated assembly of signalling proteins  have been associated with the induction of depression‐ and anxiety‐related behaviours (Muller 2015). DHA, in particular, plays a vital role in maintaining cell membrane integrity and fluidity (Parker 2006). An increase in membrane fluidity facilitates transmission by increasing the flexibility of the membrane. Through their effect on the efficiency of membrane functioning, omega‐3 PUFA plays a role in a variety of biological mechanisms, such as enzyme and receptor activity, ion channel functioning, and the production and activity of neurotransmitters. Changes in membrane fluidity also affect the structure and functioning of proteins embedded in the membrane. This influences the activity of membrane‐bound enzymes (Bowen 2002), the number and affinity of receptors and the function of ion channels all of which alter proper neurotransmission. Additionally, the production and activity of neurotransmitters, gene expression, as well as neuroplasticity are also affected through the omega‐3 PUFA impact on neurotrophins (proteins that support neuronal growth, development, survival, and function) such as brain‐derived neurotrophic factor (BDNF)(Deacon 2017). Omega‐3 PUFA are also directly involved in various neurotransmitter pathways. Omega‐3 PUFA‐deficient diets have been associated with reduced receptor density and disruptions to neurotransmitter activity in serotonergic, dopaminergic, and adrenergic systems, compared to controls. Disruptions to normal cell signalling, inflammatory processes, and neurotransmitter system activities have been implicated in MDD (Parker 2006). 

High levels of inflammation have been associated with the progression and severity of depression (Deacon 2017; Suarez 2003; Kuhlman 2020). Omega‐3 PUFA also act as anti‐inflammatory agents (Kalkman 2021). Reduced inflammation is associated with better clinical outcomes among MDD patients (Osimo 2019). Chronic stress also activates the immune system invoking a neuroinflammatory response that releases inflammatory mediators (Joffre 2019). Inflammatory mediators, like cytokines, influence the activity of the hypothalamic‐pituitary‐adrenal (HPA) axis — an important aspect of the stress‐response system. Some examples of inflammatory mediators are pro‐inflammatory cytokines including interleukin‐1beta (IL‐1β), interleukin‐2, interleukin‐6, interferon‐γ, and tumour necrosis factor‐α (TNF‐α) which are indicative of the up‐regulation of inflammatory reactions  (Anisman 2002; Deacon 2017). Documented effects of high levels of cytokines also include decreased neurotransmitter precursor availability, altered neurotransmitter metabolism and neurotransmitter transporters (Logan 2004) which may further contribute to depression. The consumption of omega‐3 PUFA has been linked to the reduced production of cytokines ‐ TNF‐α, interleukin 1B, interleukin‐6, C‐reactive protein and serum amyloid A; increased serotonergic and dopaminergic activity; and decreased concentrations of noradrenaline (Deacon 2017). Increased release of anti‐inflammatory mediators, such as eicosanoids, prostaglandins, and leukotrienes, have been attributable to higher levels of omega‐3 PUFA in cell membranes (Gutiérrez 2019). 

Why it is important to do this review

This review aims to determine the role of omega‐3 PUFA as a nutrition intervention in depression treatment plans for children and adolescents. Clinicians cannot advise young people and their and families without understanding the evidence base. Thus, a clear synthesis and quantification of the current evidence for the use of omega‐3 PUFA in children and adolescents is required. Providing high‐quality evidence for effective alternative therapies for depression is of importance as omega‐3 PUFA emerge as an alternative or adjunctive therapy. Several systematic reviews conducted in adults suggest a positive antidepressant effect of omega‐3 PUFA supplementation (Liao 2019; Hallahan 2016; Mocking 2016; Luo 2020; Appleton 2015), particularly when used as adjunctive therapy (Liao 2019). However, limited evidence regarding the efficacy of omega‐3 PUFA supplementation for the treatment of depression in children and adolescents currently exists (Lopresti 2015). The current review expands on a previously published review (Zhang 2019) on omega‐3 PUFA for the treatment of depressive disorders in children and adolescents with a more comprehensive search strategy and will include studies which have been recently added to the literature. To date, there are no dietetic practice guidelines for children and adolescents that make recommendations regarding omega‐3 PUFA supplementation for the treatment of depression. This review aims to provide up‐to‐date evidence on its efficacy in depression in children and adolescents.

Objectives

Main Objective:

This review aims to determine the impact of omega‐3 PUFA supplementation versus a comparator (e.g. placebo, wait‐list control) on clinician‐diagnosed depression or self‐reported depression symptoms in children and adolescents aged 6 to 19 years.

Secondary objectives are:

1. Estimate the size of the effect of omega‐3 PUFAs on depression;

2. Estimate the effect of each type of omega‐3 PUFA (EPA or DHA), compared with placebo, on depression;

3. Determine if the effect is modified by dosage, format (capsule or liquid), sex or age.

Methods

Criteria for considering studies for this review

Types of studies

We will include all published and unpublished protocols and trials that meet the inclusion criteria, whether or not they include the primary or secondary outcomes of interest. The RCTs should report the dosage and duration of EPA or DHA supplementation. We will include all RCTs regardless of their quality.  Cross‐over and cluster RCTs will be included.

Types of participants

Participant Characteristics  

Studies with participants of either sex, between 6 and 19 years of age, and from all geographical locations will be eligible for inclusion. We selected the lower age bound of 6 years so as not to exclude studies that might include children at this age. We also decided to set the lower bound at 6 because it would be very unlikely to find RCT studies among younger children.

Diagnosis

We will include studies that recruited participants with depression (regardless of their other symptoms).

1. Diagnosed depression (MDD or dysthymia) using validated diagnostic criteria, e.g. DSM IV‐TR (APA 2000), International Classification of Diseases 10 (ICD10) (WHO 2016), or by other standardised criteria such as the Research Diagnostic Criteria (Spitzer 1978); or

2. Self‐report of depressive symptoms by standardised questionnaire validated in children and adolescents with depressive symptoms. These participants may not have a diagnosis of MDD or dysthymia, but must display symptoms of sadness, loss of energy, change in appetite or sleeping patterns, anxiety, restlessness, feelings of worthlessness, guilt, hopelessness, indecisiveness, or thoughts of self‐harm or suicide prior to randomization (APA 2019). Participants may have comorbidities (physical or physiological) but depression must be the primary diagnosis.

We will not include the studies if diagnoses are unclear or the investigators used an unstandardized questionnaire or assessment method. We will include RCTs that use a combination of both clinician‐diagnosed depression and self‐reported depressive symptoms. In studies where only a subgroup of the participants met the diagnosis criteria, we will include the data from that subgroup if the study defined and distinguished the subgroup prior to randomization. 

Comorbidity

 There is a high incidence of comorbidity in people with depression. We will include children and adolescents with other psychiatric diseases, provided they have a primary diagnosis of MDD/dysthymia or their self‐reported depressive symptoms suggest clinically significant depressive symptoms. 

Adjunctive Therapy

We will also include RCTs with adjunctive therapy for depression. There is a high frequency of using adjunctive therapies for depressive disorders. Adjunctive therapy must be present in both the intervention and control groups.

Setting

We will include studies from any setting (inpatient/outpatient or community settings). 

Types of interventions

We will consider RCTs with placebo control or comparative treatment control that assess the effect of omega‐3 PUFA supplementation. We will include RCTs of omega‐3 PUFA supplementation as sole or adjunctive therapy, regardless of the type of omega‐3 PUFA (EPA, DHA, or a combination), as long as the trial administered a standardised dose (capsule or liquid form). We will include any dosage of omega‐3 PUFA or duration of supplementation, as long as these are clearly specified in the study. We will exclude studies from the analysis if they do not provide details of the type or dose of omega‐3 PUFA. 

Comparator 

All studies must have a comparator. Possible comparators include placebo, wait‐list controls, no treatment/supplementation, or standard care. Comparators will be presented separately in the main analyses. Placebo will be the preferred comparator where necessary in any subgroup analyses.

Types of outcome measures

Depression is our primary outcome. The outcome measure will be a resolution of clinically‐diagnosed depression or a decrease in self‐reported depression symptoms. We will include all studies that measure depressive symptoms as primary or secondary outcomes. Where available, data for all outcomes will be recorded at baseline, the end of the treatment/supplementation period, and at post‐treatment/supplementation follow‐up.

Primary outcomes

The primary outcome is depression which is clinically diagnosed or depressive symptoms which are self‐reported.

1. Clinically diagnosed depressive disorder will be a dichotomous measure: the absence or presence of depression assessed using ICD/DSM diagnostic criteria, either through a diagnostic interview or expert opinion (Appendix 1).

2. Self‐reported depressive symptoms will be a continuous measure (score) reported by any continuous validated measure. We will assess a change in depressive symptoms as the difference when comparing the scores before the intervention to those reported after the intervention. There is a wide range of validated rating scales for this age group but the most common examples are the Beck Depression Inventory (BDI) (Beck 2005) and the Children's Depression Inventory (CDI) (Kovacs 2014), but we will also include studies using other scales. Published RCTs of treatments for adolescent MDD are known to be heterogeneous and sometimes lack detail when reporting their primary outcomes (Monsour 2020).

Secondary outcomes

Secondary outcomes we will consider include:

1. Adverse events: we will record the number of participants who experienced ‘any adverse event’ or ‘any serious adverse event’. Examples of possible adverse events include unpleasant taste, bad breath, bad‐smelling sweat, headache or gastrointestinal symptoms such as heartburn, nausea, and diarrhoea (NIH 2018).

2. Attrition: we will report the number of individuals who drop out of the trials for any reason.

3. Compliance with the intervention: we will measure this by pill counts, blood tests, or both.

Reporting one or more of the secondary outcomes listed here in the trial is not an inclusion criterion for the review. Where a trial (published or unpublished) does not appear to report one of these secondary outcomes, we will access the trial protocol and contact the trial authors to ascertain whether they measured the secondary outcomes but did not report them. If relevant trials measured these secondary outcomes but did not report the data at all, or not in a usable format, we will include them in the review as part of the narrative. 

Search methods for identification of studies

We will identify studies to include by searching databases, clinical trial registries, additional grey literature sources, and possibly by contacting authors of published trials or trial protocols, if necessary.

Electronic searches

Indexed Literature Searches 

We will carry out systematic searches across all languages and years in the following electronic databases:

• Cochrane Central Register of Controlled Trials (CENTRAL, current issue);

• Ovid MEDLINE (1946 to present, including Epub ahead of print, in‐process, and other unindexed citations);

• Ovid Embase (1947 to present);

• EBSCO Child Development and Adolescent Studies  (1927 ‐ Present);

• Ovid PsycINFO (1806 to present); and

• EBSCO CINAHL (Cumulative Index to Nursing and Allied Health Literature) Plus with Full Text (1981 to present).

An academic health sciences librarian (GBR) will develop the search strategies, and a second librarian will review these, using peer review of electronic search strategies (PRESS) guidelines (McGowan 2016). We will use published, validated search strategies to identify randomized trials when possible, such as the Cochrane Highly Sensitive Search Strategies for identifying randomized trials in Ovid MEDLINE (Lefebvre 2021). We will translate the search strategies into each database using that platform’s command language, including text words, controlled vocabulary, and subject headings. The Ovid MEDLINE search strategy is in Appendix 2. 

Grey Literature Searches

To supplement the database searches, we will also conduct a grey literature search. We will identify relevant authorities, organisations, and stakeholders using the DuckDuckGo search engine as it does not display personalised search results, thus reducing the risk of bias. We will also use the Canadian Agency for Drugs and Technologies in Health (CADTH) Grey Matters Checklist and the Cochrane Handbook guidelines to identify supplemental search locations (CADTH 2015; Lefebvre 2021). We will then conduct searches of relevant conference websites, clinical trial repositories, association websites, and institutional repositories to locate any additional or ongoing clinical trials. 

Searching other resources

We will search the reference sections of included studies and previously published systematic reviews, and hand‐search relevant journals to locate additional trials. We will also contact individual authors who are known experts in the field of paediatric depression and nutritional psychology. 

Data collection and analysis

We will carry out the review according to the recommendations of Chapter 5 of the Cochrane Handbook for Systematic Reviews of Interventions (Li  2021). We will download search results into Covidence to facilitate the screening and selection of studies. We will use RevMan Web 2020 for all analyses. We will record the number of search results at each stage of the search and selection process, and report this in the 'Results' section.

Selection of studies

Review authors (SS, CZ) will independently screen titles and abstracts to identify potentially eligible studies. They will code each article as 'retrieve' (eligible or potentially eligible/unclear) or 'do not retrieve'. If there are any disagreements, a third author will arbitrate (SC). We will retrieve all full‐text study reports/publications, and two review authors (SS, CZ) will independently screen these to identify studies for inclusion. They will identify and record reasons for exclusion of the ineligible studies. We will resolve any disagreement through discussion with a third person (SC). We will identify and exclude duplicates and collate multiple reports of the same study so that each study rather than each report is the unit of interest in the review. We will record the selection process in sufficient detail to complete a PRISMA flow diagram and 'Characteristics of excluded studies' table (Liberati 2009).

Data extraction and management

We will extract data in duplicate, using a data collection form designed in advance by all the review authors. We will use Microsoft Office Excel to design the data collection sheet. The review authors will extract data from three studies to pilot‐test the form, and make modifications as necessary to reconcile differences and ensure consistency. We will extract the following study characteristics.

1. Background: time period when the study took place, study country or countries, funding source(s), whether it is a published or unpublished study, and conflicts of interest

2. Setting: laboratory/community centre/clinic

3. Methods: study design, depression diagnosis (clinician or self), description of study arms, unit of allocation, sample size per intervention arm (for individually or cluster‐randomized trials respectively), start and end date, the total duration of supplementation, post‐supplementation follow‐up duration, and details of any 'lead‐in' periods.

4. Participants: total number randomized/allocated, age, sex, the baseline severity of the condition, diagnostic criteria, inclusion criteria, and exclusion criteria, withdrawals.

5. Intervention group details: number randomized/allocated to a group, description of the intervention (including dose and type), duration of supplementation and post‐supplementation follow‐up duration, delivery of the intervention, providers and their training, concomitant therapies, and comorbidity

6. Comparison group details: number randomized/allocated to a group, description of the intervention, duration of supplementation and post‐supplementation follow‐up duration, delivery of the intervention, providers and their training, concomitant therapies, and comorbidity

7. Outcomes: measurement tool, validation of the tool, the total number in intervention, comparison and follow‐up groups. Where available, we will extract data on all primary and secondary outcomes (clinically diagnosed depression, self‐reported depressive symptoms, adverse events, attrition and compliance). When depression is reported using a self‐assessment tool the mean depression score at baseline, at the treatment/supplementation end and at post‐treatment/supplementation follow‐up will be extracted. When depression is clinician assessed, we will extract the clinician assessment at baseline at the treatment/supplementation end and post‐treatment/supplementation follow‐up will be extracted. 

Two review authors (SS, CZ) will independently extract outcome data from the included studies. We will resolve disagreements by consensus or by involving a third person (SC). One review author (CZ) will transfer data into the RevMan Web 2020 file. We will double‐check that data are entered correctly by comparing the data presented in the systematic review with the data collection form. A second review author (SS) will verify data entry for accuracy.

Assessment of risk of bias in included studies

Two review authors (SS, CZ) will independently assess the risk of bias for each study, using the Cochrane 'Risk of Bias 2' tool (RoB2) (Sterne 2019), outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021b) and in Appendix 2. We will resolve any disagreements by discussion or by involving another author (SC). We will assess the risk of bias of specific results of a trial according to the following domains:

1. bias arising from the randomization process (random sequence generation, allocation concealment, blinding of participants and personnel);

2. bias due to deviations from intended interventions;

3. bias due to missing outcome data;

4. bias in the measurement of the outcome; and

5. bias in the selection of the reported result

We will use the RoB2 Excel tool to assess individually‐randomized, parallel‐group trials. For cluster‐randomized trials and crossover trials, the appropriate RoB2 Excel tool will be used.

We will use the signalling questions in the 'RoB2' tool and rate each domain as 'low’ risk of bias, 'some concerns' or 'high’ risk of bias. We will summarise the 'Risk of bias' judgements across different studies for each of the domains listed for each outcome. A judgement of ‘high’ risk of bias within any domain will have similar implications for the overall result, irrespective of which domain is being assessed. Therefore, if the answers to the signalling questions yield a judgement of ‘high’ risk of bias, we will consider whether any identified problems are of sufficient concern to warrant this judgement for that result overall. Where we judge there to be ‘some concerns’ in multiple domains, we will consider an overall judgement of ‘High’ risk of bias for that result or group of results

When considering the effects of treatment/supplementation, we will take account of the risk of bias for each outcome. We will assess risk of bias for our two primary outcomes (clinically diagnosed depression (dichotomous) and depressive symptomology (continuous), as well as adverse events. If the trials report that they performed an 'intention‐to‐treat (ITT) analysis, took losses to follow‐up into account, or performed the last observation carried forward (LOCF) analysis, we will consider the impact of attrition bias on results of the review to be low. The overall RoB2 judgement for each outcome will be considered as part of the GRADE assessment presented in our Summary of Findings

Measures of treatment effect

Continuous data

Random effects models will be constructed to determine the pooled estimate of omega‐3 PUFA on depression. We will use the mean difference (MD) where studies have reported continuous outcomes on the same scale, and the standardised mean difference (SMD) where studies have reported the same continuous outcome but measured it on different scales. 

Dichotomous data

We will use the risk ratio (RR) with 95% confidence intervals for dichotomous outcomes. 

Unit of analysis issues

Appropriate methods for the analysis of non‐standard designs, such as cluster‐randomized trials and cross‐over trials, are outlined below.

Cross‐over RCT

In the case of the inclusion of a cross‐over RCT, we will treat the control and intervention periods as separate entities and extract data from the first period (before cross‐over) as the control data.

Cluster‐RCT

If we include a cluster‐RCT, we will calculate a cluster mean and use that summary measure with the cluster as the unit of analysis. 

Multiple Treatment Arms

In the case of multi‐arm RCTs, in order to avoid a unit‐of‐analysis error, we will keep arms separate and split the control group.  All intervention groups of a multi‐intervention study will be stated in the table of ‘Characteristics of included studies'.

Timing of outcome assessment

Where the study reports outcomes at multiple time points, we will extract the time point of the treatment/supplementation end and, if available, at follow‐up. The impact of supplementation duration and follow‐up duration will be explored through a meta‐regression.

Dealing with missing data

We will contact trial authors to obtain missing outcome data (e.g. when a study is identified as abstract only) since such missingness potentially contributes to selective outcome reporting. We will also contact trial authors for missing statistics (standard deviations/errors). However, when no further missing statistical data is provided, missing statistics will be calculated based on methods outlined in The Cochrane Handbook (Higgins 2021a). We will not impute missing outcome data as we think the missing data could introduce serious bias. Missing data due to attrition will be considered in the RoB2 assessment of studies and its impact considered in the Discussion. 

Assessment of heterogeneity

We will inspect forest plots visually to consider the direction and magnitude of effects and the degree of overlap between confidence intervals. We will use the I² statistic to quantify inconsistency and measure statistical heterogeneity among the trials but acknowledge that there is substantial uncertainty in the value of I² when there is only a small number of studies. We will also consider the p‐value from the Chi² test. If we identify substantial heterogeneity, we will report it and explore possible causes using subgroup analysis. Rough thresholds for interpretation of the I² statistic outlined in the Cochrane Handbook are: 0% to 40%: might not be important; 30% to 60%: may represent moderate heterogeneity; 50% to 90%: may represent substantial heterogeneity and 75% to 100%: considerable heterogeneity (Deeks 2021). The contribution of each study to the statistical heterogeneity will also be explored visually using the graphical display of study heterogeneity (GOSH) plots. Leave‐one‐out sensitivity analysis will be performed by iteratively removing one study at a time and recalculating the pooled effect size.

Assessment of reporting biases

We will attempt to minimise reporting bias by searching for and including published and unpublished trials. We will source unpublished trials from grey literature searches, conference abstracts and trial registries. If we are able to pool more than 10 trials, we will create and examine a funnel plot to explore possible publication biases for the primary outcomes. Publication bias will also be explored with Egger’s test.

Data synthesis

We will undertake meta‐analyses only where this is meaningful, i.e. if the treatment/supplementation, participants, and underlying clinical questions are similar enough for pooling to make sense. We will upload the outcome data for each study into the data tables in RevMan Web 2020 to calculate the pooled effect size.

We will express uncertainty by reporting 95% confidence intervals (CIs) for all effect estimates. When means and standard deviations are not reported, we will use other available data (e.g. confidence intervals, t‐values, p‐values) and appropriate methods described in the Cochrane Handbook for Systematic Reviews of Interventions to calculate the means and standard deviations (Higgins 2021b). Where data are not sufficient to calculate standard deviations, we will describe them in a table. We will also consider the possibility and implications of skewed data when analysing continuous outcomes, as they can mislead results due to small sample size (Piovesana 2018). We will report the overall pooled estimate and subgroup pooled estimate.

All eligible trials will be included in the primary analysis regardless of the risk of bias. It is unlikely that all the included studies will be functionally equivalent, due to the studies having different methods and being produced by researchers working independently. Accordingly, we will use a random‐effects model as we expect substantial heterogeneity among studies. The participants, outcome measures, settings, and other characteristics are likely to be different, so it will not be appropriate to assume that the studies are estimating a common effect.

Subgroup analysis and investigation of heterogeneity

We will investigate whether various study characteristics can explain the clinical diversity or heterogeneity if the number of studies included meets the threshold of k=10 for subgroup analysis and meta‐regression. We will use subgroup analysis and meta‐regression analyses by comparing effect sizes with selected study characteristics.

We plan to carry out subgroup analysis on the following [categorical] variables:

1. Type omega‐3 PUFA. To explore whether effects due to the composition of the supplement may alter treatment outcomes and recommendations. We will compare the following subgroups: studies where only DHA was used; studies where only EPA was used; and studies where a combination was used.

2. Adjunctive therapy: We will compare the following subgroups: studies involving individuals receiving adjunctive therapies; studies involving individuals not receiving adjunctive therapies; and studies involving a mix of individuals receiving and not receiving adjunctive therapies.

Meta‐regression will be carried out for the following [continuous] variables :

1. Age (in years). This analysis explores effects due to participant age that may alter treatment/supplementation outcomes and recommendations;

2. Duration of omega‐3 PUFA supplementation (in weeks). We will examine any dose‐response effects due to supplementation duration, where possible. In the case where the dosage range is reported, we will take the mean or the midpoint if the mean is not reported.

3. Dose levels of omega‐3 (PUFAs (in mg). We will examine any dose‐response effects where possible. In cases where multiple doses are reported in a single trial we will keep them separate and split the control group.

4. Duration of follow‐up (in weeks). We will examine any long term effects effects post‐supplementation, where possible. In the case where a follow‐up range is reported, we will take the mean or the midpoint if the mean is not reported.

5. Percentage of female participants.

Subgroup analysis and meta‐regression analysis will be conducted in R version 4.0.2 using the ‘met’, ‘metafor’ and ‘dmetar’ packages.

Sensitivity analysis

We plan to carry out the following sensitivity analyses, to test whether key methodological factors or decisions have affected the main result: 

• We will exclude studies with high drop‐out rates (more than 20%) and compare this against the overall analysis, to determine the extent to which attrition bias affects the main result.

• Study quality: we will exclude studies at a high risk of bias and compare this against the main result, to determine the impact of study quality on the outcome's overall effect estimate.

Summary of findings and assessment of the certainty of the evidence

The 'Summary of Findings' table will include Depressive symptomology (continuous), Clinically diagnosed depression (dichotomous), and Adverse Events. We will use the five GRADE considerations (study limitations based on RoB2 judgements, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of a body of evidence as it relates to the studies which contribute data to the meta‐analyses for the prespecified outcomes. We will use methods and recommendations described in Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2021), and develop the table using GRADEpro software (GRADEpro GDT). We will justify all decisions to downgrade the quality of studies using footnotes and we will make comments to aid the reader's understanding of the review where necessary.

Two review authors (CZ, SS) will make independent judgements about evidence quality, with disagreements resolved by discussion or involving a third author (SC). We will justify all judgements, document them and incorporate them into the reporting of results for each outcome.

Appendices

Appendix 1. DSM‐ ICD Criteria

When clinical diagnoses are provided, the following DSM‐5 and ICD‐11 diagnoses are eligible. Comparable diagnoses are acceptable for DSM‐IV and ICD‐10.

DSM5 Codes and Diagnoses

296.36  F33.42  Major depressive disorder, recurrent episode, in full remission

296.35  F33.41  Major depressive disorder, recurrent episode, in partial remission

296.31  F33.0     Major depressive disorder, recurrent episode, mild

296.32  F33.1     Major depressive disorder, recurrent episode, moderate

296.33  F33.2     Major depressive disorder, recurrent episode, severe

296.30  F33.9     Major depressive disorder, recurrent episode, unspecified

296.34  F33.3     Major depressive disorder, recurrent episode, with psychotic features

296.26  F32.5     Major depressive disorder, single episode, in full remission

296.25  F32.4     Major depressive disorder, single episode, in partial remission

296.21  F32.0     Major depressive disorder, single episode, mild

296.22  F32.1     Major depressive disorder, single episode, moderate

296.23  F32.2     Major depressive disorder, single episode, severe

296.20  F32.9     Major depressive disorder, single episode, unspecified

296.24  F32.3     Major depressive disorder, single episode, with psychotic features

300.4    F34.1     Persistent depressive disorder (dysthymia)

311       F32.9     Unspecified depressive disorder

ICD‐11 Codes and Diagnoses

6A70 Single episode depressive disorder 

6A70.0 Single episode depressive disorder, mild 

6A70.1 Single episode depressive disorder, moderate, without psychotic symptoms 

6A70.2 Single episode depressive disorder, moderate, with psychotic symptoms 

6A70.3 Single episode depressive disorder, severe, without psychotic symptoms 

6A70.4 Single episode depressive disorder, severe, with psychotic symptoms 

6A70.5 Single episode depressive disorder, unspecified severity 

6A70.6 Single episode depressive disorder, currently in partial remission 

6A70.7 Single episode depressive disorder, currently in full remission 

6A70.Y Other specified single episode depressive disorder 

6A70.Z Single episode depressive disorder, unspecified 

6A71 Recurrent depressive disorder 

6A72 Dysthymic disorder

6A73 Mixed depressive and anxiety disorder 

6A7Y Other specified depressive disorders 

6A7Z Depressive disorders

SD82 Depression disorder

Appendix 2. Risk of Bias Assessment Tool 

Risk of bias arising from the randomization process

Low risk

• A random component was used in the sequence generation process (e.g. computer‐generated random numbers, reference to a random number table, coin‐tossing, shuffling cards or envelopes, throwing dice or drawing lots). An allocation sequence that is generated using minimisation will generally be considered random

• All of the following:

1. The allocation sequence was adequately concealed: The trial used any form of remote or centrally administered method to allocate interventions to participants (e.g. independent central pharmacy, telephone or Internet‐based randomization service providers) and envelopes or drug containers were used appropriately

2. Any baseline differences observed between intervention groups appear to be compatible with chance or there is no information about baseline imbalances

3. The allocation sequence was random or there is no information about whether the allocation sequence was random

High risk

• No random element was used in generating the allocation sequence or the sequence is predictable (e.g. methods based on dates, patient record numbers, allocation decisions made by clinicians or participants, allocation based on the availability of the intervention, any other systematic or haphazard method)

• Any of the following:

1.  The allocation sequence was not adequately concealed (there is reason to suspect that the enrolling investigator or the participant had knowledge of the forthcoming allocation)

2. There is no information about concealment of the allocation sequence and baseline differences between intervention groups suggest a problem with the randomization process (e.g. substantial differences between intervention group sizes, compared with the intended allocation ratio, a substantial excess in statistically significant differences in baseline characteristics between intervention groups, beyond that expected by chance; or imbalance in one or more key prognostic factors, or baseline measures of outcome variables, that is very unlikely to be due to chance and for which the between‐group difference is big enough to result in bias in the intervention effect estimate)

Unclear risk

• Insufficient information about the sequence generation process to permit judgement

• The only information about randomization methods is a statement that the study is randomized

• There is no useful baseline information available

Risk of bias due to deviations from the intended interventions (effect of assignment to intervention)

Low risk

• Any of the following:

1. Participants, carers and people delivering the interventions were unaware of intervention groups during the trial (through the use of a placebo or sham intervention)

2. Participants, carers or people delivering the interventions were aware of intervention groups during the trial and no deviations from intended intervention arose because of the trial context 

• An appropriate analysis was used to estimate the effect of assignment to intervention

High risk

• All of the following:

1. Participants, carers or people delivering the interventions were aware of intervention groups during the trial

2. There is evidence or strong reason to believe, that the trial context led to failure to implement the protocol interventions or to implementation of interventions not allowed by the protocol

3. These deviations were likely to have affected the outcome

4. These deviations were unbalanced between the intervention groups

5. An appropriate analysis was not used to estimate the effect of assignment to intervention

6. The potential impact (on the estimated effect of the intervention) of the failure to analyze participants in the group to which they were randomized was substantial

Unclear risk

• Insufficient information about the deviations from the intended interventions to permit judgement

Risk of bias due to deviations from the intended interventions (effect of adhering to intervention)

Low risk

• An appropriate analysis was used to estimate the effect of assignment to intervention

• All of the following:

1.  Participants, carers and people delivering the interventions were unaware of intervention groups during the trial or participants, carers or people delivering the interventions were aware of intervention groups and the important non‐protocol interventions were balanced across intervention groups

2.  Failures in implementing the intervention could not have affected the outcome

3. Study participants adhered to the assigned intervention regimen

High risk

• Participants experienced side effects or toxicities that they knew to be specific to one of the interventions

• Participants experienced side effects or toxicities that carers or people delivering the interventions knew to be specific to one of the interventions​​​​​​

• Any of the following:

1. Participants, carers and people delivering the interventions were unaware of intervention groups during the trial and failures in implementing the intervention could have affected the outcome or study participants did not adhere to the assigned intervention regimen 

2. Participants, carers or people delivering the interventions were aware of intervention groups and the important non‐protocol interventions were balanced across intervention groups. Failures in implementing the intervention could have affected the outcome or study participants did not adhere to the assigned intervention regimen

3. Participants, carers or people delivering the interventions were aware of intervention groups and the important non‐protocol interventions were not balanced across intervention groups

• An appropriate analysis was not used to estimate the effect of adhering to intervention

Unclear risk

• Insufficient information about deviations from the intended interventions to permit judgement

Risk of bias due to missing outcome data

Low risk

• Analysis methods that correct for bias or sensitivity analyses showing that results are little changed under a range of plausible assumptions about the relationship between missingness in the outcome and its true value.

• Outcome data were available for all, or nearly all, randomized participants

• All missing outcome data occurred for documented reasons that are unrelated to the outcome 

• There is evidence that the result was not biased by missing outcome data

• Missingness in the outcome could not depend on its true value

• The analysis accounted for participant characteristics that are likely to explain the relationship between missingness in the outcome and its true value

High risk

• Outcome data were not available for all, or nearly all, randomized participants

• There is no evidence that the result was not biased by missing outcome data

• Missingness in the outcome could depend on its true value

• Missingness in the outcome likely depended on its true value.

• If loss to follow up, or withdrawal from the study, could be related to participants’ health status

• Differences between intervention groups in the proportions of missing outcome data. If there is a difference between the effects of the experimental and comparator interventions on the outcome, and the missingness in the outcome is influenced by its true value, then the proportions of missing outcome data are likely to differ between intervention groups. Such a difference suggests a risk of bias due to missing outcome data because the trial result will be sensitive to missingness in the outcome being related to its true value. For time‐to‐event‐data, the analogue is that rates of censoring (loss to follow‐up) differ between the intervention groups.

• Reported reasons for missing outcome data provide evidence that missingness in the outcome depends on its true value;

• Reported reasons for missing outcome data differ between the intervention groups;

• The circumstances of the trial make it likely that missingness in the outcome depends on its true value (i.e. continuing symptoms make drop out more likely)

• In time‐to‐event analyses, participants’ follow‐up is censored when they stop or change their assigned intervention, for example, because of toxicity

Unclear risk

• Insufficient information about missing outcome data to permit judgement

Risk of bias in the measurement of the outcome

Low risk

• Both of the following

1. The method of measuring the outcome was not inappropriate and the measurement or ascertainment of the outcome did not differ between intervention groups

2. The outcome assessors were unaware of the intervention received by study participants  or the assessment of the outcome could not have been influenced by knowledge of the intervention received

High risk

• Outcome assessors were blinded to intervention status. For participant‐reported outcomes, the outcome assessor is the study participant.

• Any of the following:

1. The method of measuring the outcome was inappropriate

2. The measurement or ascertainment of the outcome could have differed between intervention groups

3.  It is likely that the assessment of the outcome was influenced by knowledge of the intervention received

Unclear risk

• Insufficient information about the measurement of the outcome process to permit judgement

Risk of bias in the selection of the reported result

Low risk

• The researchers’ pre‐specified intentions are available in sufficient detail

• Changes to analysis plans were made before unblinded outcome data were available, or were clearly unrelated to the results

• There is clear evidence that all eligible reported results for the outcome measurement correspond to all intended analyses. There is only one possible way in which the outcome measurement can be analysed (hence there is no opportunity to select from multiple analyses)

• Analyses are inconsistent across different reports on the same trial, but the trialists have provided the reason for the inconsistency and it is not related to the nature of the results

• All of the following:

1. The data were analysed in accordance with a pre‐specified plan that was finalised before unblinded outcome data were available for analysis

2. The result being assessed is unlikely to have been selected, on the basis of the results, from multiple eligible outcome measurements (e.g. scales, definitions, time points) within the outcome domain

3. Reported outcome data are unlikely to have been selected, on the basis of the results, from multiple eligible analyses of the data

High risk

• There is clear evidence that measurement was analysed in multiple eligible ways, but data for only one or a subset of analyses is fully reported (without justification), and the fully reported result is likely to have been selected on the basis of the results

• Selection on the basis of the results arises from a desire for findings to be newsworthy, sufficiently noteworthy to merit publication or to confirm a prior hypothesis

• One of the following:

1. The result being assessed is likely to have been selected, on the basis of the results, from multiple eligible outcome measurements (e.g. scales, definitions, time points) within the outcome domain

2. The result being assessed is likely to have been selected, on the basis of the results, from multiple eligible analyses of the data

Unclear risk

• Any analysis intentions are not available, or the analysis intentions are not reported in sufficient detail to enable an assessment, and there is more than one way in which the outcome measurement could have been analysed

• Insufficient information about the selection of the reported result process to permit judgement

Appendix 3. OVID Medline Search Strategy

Ovid MEDLINE: Epub Ahead of Print, In‐Process & Other Non‐Indexed Citations, Ovid MEDLINE® Daily and Ovid MEDLINE® <1946‐Present>

#	Searches	Results
1	Depression/	124910
2	Depressive Disorder/	73649
3	Depressive Disorder, Major/	31328
4	Dysthymic Disorder/	1146
5	mental disorders/	165708
6	Mood Disorders/	14656
7	depress*.tw,kf.	483463
8	dysthymi*.tw,kf.	3204
9	melanchol*.tw,kf.	3100
10	MDD.tw,kf.	14199
11	(mood* or mental health).tw,kf.	239188
12	internaliz*.tw,kf.	61121
13	(affective disorder* or affective symptom*).tw,kf.	19182
14	1 or 2 or 3 or 4 or 5 or 6 or 7 or 8 or 9 or 10 or 11 or 12 or 13	863028
15	pediatrics/	55035
16	young adult/	898681
17	Adolescent/	2071950
18	Child/	1722702
19	Child, Preschool/	935182
20	(minors or boy or boys or boyhood or girl or girls or girlhood or kid or kids or kiddie or child* or schoolchild* or adolescen* or juvenil* or youth* or teen* or underage* or under age* or pubescen* or puberty or pe?diatric* or p?ediatric* or school*).tw,kf.	2168107
21	(young* adj2 (adult* or person* or individual* or people* or population* or man or men or wom?n)).tw,kf.	232842
22	(youngster* or preschool* or pre‐school* or kindergarten* or freshm?n* or junior* or sophmore* or senior* or highschool* or college* or universit* or student* or undergrad*).tw,kf.	795961
23	(grade* adj2 (one or first or two or second or three or third or four* or five or fifth or six* or seven* or eight* or nine* or ninth or ten* or eleven* or twelfth or twelve or "1" or "2" or "3" or "4" or "5" or "6" or "7" or "8" or "9" or "10" or "11" or "12")).tw,kf.	133780
24	15 or 16 or 17 or 18 or 19 or 20 or 21 or 22 or 23	4928408
25	Fatty Acids, Omega‐3/	13799
26	fish oils/	7828
27	cod liver oil/	539
28	docosahexaenoic acids/	9048
29	eicosapentaenoic acid/	6345
30	dietary fats, unsaturated/	5316
31	alpha‐Linolenic Acid/	2995
32	Dietary Supplements/	60364
33	(omega3* or omega 3*).tw,kf.	17420
34	fatty acid*.tw,kf.	228329
35	((n3 or n‐3 or w3 or w‐3) adj3 polyunsaturat*).tw,kf.	5726
36	(PUFA or n‐3PUFA* or n3PUFA*).tw,kf.	12706
37	((n3 or n‐3 or w3 or w‐3) adj3 oil*).tw,kf.	888
38	(fish* adj2 oil*).tw,kf.	11550
39	(cod adj2 oil*).tw,kf.	978
40	icosapentanoic*.tw,kf.	1
41	icosapentaenoic*.tw,kf.	35
42	timnodonic*.tw,kf.	21
43	(1553‐41‐9 or aan7qov9ea).tw,kf.	0
44	(diet* adj2 (fat* or oil*)).tw,kf.	57945
45	(unsaturate* adj2 (fat* or oil*)).tw,kf.	13637
46	(alphalinolen* or alpha‐linolen*).tw,kf.	5491
47	(linolenate* or linolenic*).tw,kf.	11720
48	Epanova.tw,kf.	17
49	((diet* or food*) adj2 supplement*).tw,kf.	48078
50	Marine oil*.tw,kf.	634
51	marine lipid*.tw,kf.	144
52	Coromega.tw,kf.	2
53	Efamed.tw,kf.	0
54	MaxEPA.tw,kf.	172
55	Lovaza.tw,kf.	53
56	Omtryg.tw,kf.	2
57	(Vascepa or icosapent ethyl).tw,kf.	188
58	DHA.tw,kf.	15195
59	Docosahex*.tw,kf.	15220
60	(Eicosapent* or ethyl‐eicosapent* or ethyleicosapent*).tw,kf.	11287
61	EPA.tw,kf.	19285
62	25 or 26 or 27 or 28 or 29 or 30 or 31 or 32 or 33 or 34 or 35 or 36 or 37 or 38 or 39 or 40 or 41 or 42 or 43 or 44 or 45 or 46 or 47 or 48 or 49 or 50 or 51 or 52 or 53 or 54 or 55 or 56 or 57 or 58 or 59 or 60 or 61	376475
63	randomized controlled trial.pt.	524301
64	controlled clinical trial.pt.	94088
65	randomi#ed.ab.	611602
66	placebo.ab.	215700
67	drug therapy.fs.	2285762
68	randomly.ab.	352323
69	trial.ab.	541881
70	groups.ab.	2161841
71	clinical trials as topic/	194948
72	(randomi#ed or randomi#ation or randomi#ing).ti,ab,kf.	676172
73	(RCT or cRCT or "at random" or (random* adj3 (administ* or allocat* or assign* or class* or cluster or crossover or cross‐over or control* or determine* or divide* or division or distribut* or expose* or fashion or number* or place* or pragmatic or quasi or recruit* or split or subsitut* or treat*))).ti,ab,kf.	596752
74	placebo.ab,ti,kf.	221794
75	trial.ti.	235413
76	(control* adj3 group*).ab.	563711
77	(control* and (trial or study or group*) and (waitlist* or wait* list* or ((treatment or care) adj2 usual))).ti,ab,kf,hw.	27154
78	((single or double or triple or treble) adj2 (blind* or mask* or dummy)).ti,ab,kf.	179374
79	double‐blind method/ or random allocation/ or single‐blind method/	286013
80	63 or 64 or 65 or 66 or 67 or 68 or 69 or 70 or 71 or 72 or 73 or 74 or 75 or 76 or 77 or 78 or 79	5275166
81	exp animals/ not humans.sh.	4795064
82	80 not 81	4576359
83	14 and 24 and 62 and 82	596

Contributions of authors

SC: Conceived, designed and wrote the review protocol. 
CZ: Wrote the review protocol.
SS: Wrote the review protocol.
GB‐R: Designed the search strategy, translated it to the different database languages, coordinated the peer review of the search strategy, and coordinated the search methods section. Wrote the review protocol.
PS: Provided clinical expertise and senior supervision for the review protocol.
DK: Provided clinical expertise and senior supervision for the review protocol.

Sources of support

Internal sources

• Hospital for Sick Children, Canada

  Susan C Campisi is supported in part by the SickKids RestraComp Post Doctoral Award and by the Canadian Institutes of Health Research (CIHR) grant number 409491.

External sources

• Centre for Addiction and Mental Health (CAMH), Canada

  Funding CZ

Declarations of interest

SC: None to declare
CZ: None to declare
SS: None to declare
GB‐R: None to declare
PS: None to declare
DK: None to declare

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