for preventing postpartum depression (Protocol) - Wiley Online Library

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Interventions (other than psychosocial, psychological and pharmacological) for preventing postpartum depression (Protocol) Dennis CL, Brown HK, Morrell J

Dennis CL, Brown HK, Morrell J. Interventions (other than psychosocial, psychological and pharmacological) for preventing postpartum depression. Cochrane Database of Systematic Reviews 2016, Issue 5. Art. No.: CD012201. DOI: 10.1002/14651858.CD012201.

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Interventions (other than psychosocial, psychological and pharmacological) for preventing postpartum depression (Protocol) Copyright © 2016 The Cochrane Collaboration. Published by John Wiley & Sons, Ltd.

TABLE OF CONTENTS HEADER . . . . . . . . . . ABSTRACT . . . . . . . . . BACKGROUND . . . . . . . OBJECTIVES . . . . . . . . METHODS . . . . . . . . . ACKNOWLEDGEMENTS . . . REFERENCES . . . . . . . . APPENDICES . . . . . . . . CONTRIBUTIONS OF AUTHORS DECLARATIONS OF INTEREST .

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[Intervention Protocol]

Interventions (other than psychosocial, psychological and pharmacological) for preventing postpartum depression Cindy-Lee Dennis1 , Hilary K. Brown2 , Jane Morrell3 1 University of Toronto and St. Michael’s Hospital, Toronto, Canada. 2 Psychiatry, Women’s College Hospital, Toronto, Canada. 3 School of Nursing, Midwifery and Physiotherapy, Faculty of Medicine and Health Sciences, University of Nottingham, Nottingham, UK

Contact address: Cindy-Lee Dennis, University of Toronto and St. Michael’s Hospital, 155 College Street, Toronto, ON, M5T 1P8, Canada. [email protected]. Editorial group: Cochrane Pregnancy and Childbirth Group. Publication status and date: New, published in Issue 5, 2016. Citation: Dennis CL, Brown HK, Morrell J. Interventions (other than psychosocial, psychological and pharmacological) for preventing postpartum depression. Cochrane Database of Systematic Reviews 2016, Issue 5. Art. No.: CD012201. DOI: 10.1002/14651858.CD012201. Copyright © 2016 The Cochrane Collaboration. Published by John Wiley & Sons, Ltd.

ABSTRACT This is the protocol for a review and there is no abstract. The objectives are as follows: The primary objective of this review was to assess the effects, on mothers, infants and their families, of interventions other than pharmacological, psychosocial, or psychological interventions compared with usual antepartum or postpartum care in the prevention of postpartum depression.

BACKGROUND

Description of the condition Depression is a major cause of disability among women and men of all ages worldwide (WHO 2010). Among women, lifetime rates of depression vary between 10% and 25% (Kessler 2005; Weissman 1996). By 2020, the World Health Organization (WHO) projects that depression will carry the greatest disease burden of all health conditions in women, contributing to 5.7% of the total disease burden measured in disability-adjusted life years (WHO 2010). The public health significance of depression is therefore undeniable. Depression impedes both social and physical functioning, is a major contributing factor in suicide, and results in increased healthcare costs, morbidity, and mortality from medical illness. Among women between 15 and 44 years of age in the United

States, depression is the leading cause of non-obstetric hospitalizations (O’Hara 2009). Postpartum depression is broadly defined as depression that occurs within the first 12 months after childbirth. It includes depression that is a continuation of that experienced during pregnancy as well as new-onset depression. Postpartum depression is not recognized by the Diagnostic and Statistical Manual of Mental Disorders (DSM) as diagnostically distinct from depression at other times (APA 2013). However, the DSM-5 does allow for the addition of a “peripartum-onset specifier” among women whose depression developed during pregnancy or within four weeks of childbirth (APA 2013). A meta-analysis of 59 studies found an overall prevalence of postpartum depression of 13% within the first 12 weeks following childbirth (n = 12,810; 95% confidence interval 12.3% to 13.4%) (O’Hara 1996). A more recent systematic review found the period prevalence of all depression to be


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19.2% in the first 12 weeks after childbirth, with a period prevalence for major depression of 7.1% (Gaynes 2005). This review also showed that depression was common during pregnancy, with a period prevalence of 18.4% for depression that continued across the nine months of pregnancy and a period prevalence of 12.7% for having an episode of major depression during this time. Antenatal depression is a strong risk factor for postpartum depression. For many women, postpartum depression often develops within the first 12 weeks postpartum and common symptoms include anxiety, emotional lability, dysphoria, confusion, guilt, and insomnia. Depressive symptoms continue past the first year postpartum for approximately 8% of mothers (Dennis 2012). In a small number of cases, postpartum depression may lead to suicide, which is one of the top causes of maternal deaths in the UK (Lewis 2007; Lindahl 2005).

Description of the intervention The causes of postpartum depression is very diverse and multifactorial. Following consistent evidence of the importance of stressful life events, marital conflict, and lack of social support as potential risk factors for postpartum depression (Robertson 2004), psychological and psychosocial interventions (e.g. peer support, nondirective counselling, nurse/midwifery home visits) have been developed to prevent postpartum depression (Dennis 2013). These interventions are thought to directly influence the development of postpartum depression by decreasing feelings of loneliness, improving health practices, promoting individual motivation, and providing valuable information on access to health services and positive health behaviours (NCCMH 2010). A Cochrane systematic review of psychosocial and psychological interventions for the prevention of postpartum depression has been completed (Dennis 2013). However, access to psychotherapy may be limited, particularly in rural or remote areas (Villegas 2011). Interventions other than psychosocial or psychological are also available for the prevention of depression. These “alternative” prevention options, including light therapy and herbal supplements, are often used partly because of a common belief that “natural is better” (Ravindran 2009). Research on the use of alternative therapies to treat depression suggests that there is some reason to support the use of these therapies. In a review of commonly-used complementary and alternative medicine treatments for major depressive disorders, the American Psychiatric Association noted that randomized controlled trials of these approaches showed promising results, but that more rigorous and larger studies were needed (Freeman 2010). According to the review, there is some evidence to support St. John’s wort as a monotherapy for mild to moderate depression but not more severe depression; drug interactions are an important safety concern. Light therapy also has some evidence as a monotherapy. Omega3 fatty acids and exercise have limited evidence as monotherapies, but may be useful as augmentation strategies. Findings for

acupuncture are conflicting, and more research is needed given the small number of studies. Finally, the review found that there is no evidence to support the use of folate as a monotherapy, but it may be useful as an adjunctive treatment (Freeman 2010). A survey of primary care patients found approximately 11% of individuals with depression and anxiety reported using complementary or alternative medicine therapy (Roy-Byrne 2005). This rate is similar to the proportion of people with depression who use pharmacological options (Mojtabai 2008). The popularity of these complementary and alternative medicine approaches makes an evaluation of their use for preventing postpartum depression warranted.

How the intervention might work There are several alternative options available for preventing depression. These include physical therapies (e.g. physical exercise, yoga, acupuncture, sleep deprivation, bright light therapy), nutraceuticals (e.g. omega-3 fatty acids), and herbal remedies (e.g. St. John’s Wort) (Ravindran 2009). One prevention option is physical exercise over eight to 20 weeks (average of 12 weeks), usually three to five times a week for 30 to 60 minutes per session (Lewis 2012; Ravindran 2009). Similarly, yoga integrates physical postures, breath control, and meditation. It is usually practiced for four to eight weeks, typically four times a week for 45 to 60 minutes per session (Ravindran 2009). Exercise and yoga are thought to improve general well-being and modulate serotonin systems (Ravindran 2009). Acupuncture uses needles to pierce the skin surface at specific points in the body. It is usually delivered for four to eight weeks and the number of needles (two to 16) and sessions varies widely (Ravindran 2009). Sleep deprivation involves keeping patients awake for short periods of time (three to four hours) or total sleep deprivation (40 hours). Usually, one to six cycles are used over four weeks (Ravindran 2009). The mechanism by which sleep deprivation might improve mood is through its effect on the hypothalamic-pituitary adrenal axis and on circadian rhythms (Ravindran 2009). Another option is light therapy, which is exposure to bright light; the standard is a 30-minute per day “dose” of 10,000 lux (intensity) with a fluorescent light box. This is usually administered in the early morning at home (Crowley 2012; Sohn 2005). Light therapy is thought to correct disturbed circadian rhythms and modulate serotonin and catecholamine systems (Crowley 2012; Sohn 2005). Nutraceuticals are nonprescription natural health products. These are usually in a concentrated forms of naturally occurring substances (e.g. vitamins and minerals such as omega-3 fatty acids, tryptophan, S-adenosyl-L-methionine (SAM-e), inositol, folic acid, amino acids, dehydroepiandrosterone (DHEA), alpha-lactalbumin, and acetyl-L-carnitine) (Ravindran 2009). Nutraceuticals are used alone or in combination (Freeman 2011). Omega-3 fatty acids have been studied in different formulations and doses, which include estyl esters of eicosaepentanoic acid (EPA) or docosahex-


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aenoic acid (DHA), or a combination (Freeman 2011); however, their exact mechanism of action is not yet fully understood. Nutraceuticals are outside of the scope of the current review as a current Cochrane review examines the effects of these substances on the prevention of postpartum depression (Millar 2013). Herbal remedies are a sub-category of natural health products that are derived from plants and plant extracts including leaves, flowers, bark, roots, and berries, and sold as a non-prescription product (Ravindran 2009). This category includes St. John’s wort, Crocus sativus, Rhodiola rosea, Lavandula angustifolia, and Gingko biloba among others.

international experts have clearly identified maternal depression as a major childhood adversity; effective interventions to address this condition are one of the most critical public health preventive strategies that can be implemented to reduce the long-term adverse developmental outcomes among children (England 2009). This review will assist in the development of effective postpartum depression interventions with the aim of reducing the number of women who develop postpartum depression and thus aid in preventing poor child developmental outcomes.

OBJECTIVES Why it is important to do this review Postpartum depression has significant implications for both mother and infant. Women with postpartum depression experience feelings of inadequacy, difficulty coping, problems with relationships, and suicidal ideation (Burke 2003; Lindahl 2005), and are at increased risk for experiencing future depressive episodes within five years (Cooper 1995). They are also at increased risk for suicidality and, in rare cases, suicide attempts and deaths (Lindahl 2005). Postpartum depression occurs during a period when the infant is completely dependent on parental care and is extremely sensitive to the quality of the interaction. Mood disorders can interfere with good parenting interactions and may cause significant stress for children (England 2009; Goodman 1999); thus, cause for concern for infant development is warranted. There is a substantial body of research showing that maternal depression and poor maternal-infant interactions can negatively affect the developing child ( Weissman 2006). Observational studies show that, on average, children of depressed mothers, compared with those of non-depressed mothers, receive lower scores on measures of motor and intellectual development, are more fussy, react more negatively to stress, have more difficult temperaments and less secure attachments to their mothers, have delayed development of self-regulatory strategies, and show poorer academic performance, lower selfesteem, fewer social competencies, and more behavioural problems (England 2009; Goodman 1999). A recent meta-analysis, which included 193 studies, reported that maternal depression (not restricted to the postpartum period), was associated with higher levels of externalising behaviour, internalizing behaviour, and general psychopathology and to lower levels of positive affect in the child (Goodman 2011). Of particular relevance is the finding that these effects were stronger among children who were exposed to maternal depression at an earlier age. There are several hypothesized mechanisms by which maternal-interactions could transmit risk from depressed mother to the child. These include maternal modelling of depressed affect, cognitions, and behaviours; inconsistent discipline practices and reduced positive reinforcement for the child; the development of an insecure child attachment; and poor marital or family functioning. Not surprisingly,

The primary objective of this review was to assess the effects, on mothers, infants and their families, of interventions other than pharmacological, psychosocial, or psychological interventions compared with usual antepartum or postpartum care in the prevention of postpartum depression.

METHODS

Criteria for considering studies for this review

Types of studies All published and unpublished randomized controlled trials (including those using a cluster-randomized design) examining interventions other than pharmacological, psychosocial, or psychological interventions in which the primary or secondary aim was to prevent postpartum depression. If studies are published in abstract form only, we will contact the trial authors for study details. We will exclude quasi-randomized trials (e.g. those randomized by delivery date, or odd versus even medical record numbers) and cross-over studies. Types of participants Participants included will be pregnant women and new (less than six weeks postpartum) mothers, including those at no known risk and those identified as at-risk for developing postpartum depression. We will exclude trials where more than 20% of participants are depressed at trial entry. Types of interventions Interventions include any form of standard or usual care compared to a variety of interventions including physical therapies (including physical exercise, yoga, acupuncture, sleep deprivation, bright light therapy) and herbal remedies (e.g. St. John’s Wort). These


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could be delivered via home or clinic visits or via telephone postnatally by a professional (e.g. nurse, midwife, childbirth educator, physician, psychiatrist, psychologist) or lay person (e.g. a specially trained woman from the community, research assistant, student). Interventions which involved instruction (e.g. exercise or yoga) could be delivered individually or in group sessions. We will not include trials in which the focus was nutraceuticals (e.g. omega-3 fatty acids), as a current Cochrane review examines the effects of these substances on the prevention of postpartum depression (Millar 2013). Types of outcome measures

Primary outcomes

1. Postpartum depression (as variously defined and measured by trialists).

Secondary outcomes

Maternal 1. Maternal mortality and serious morbidity including selfharm, suicide attempts. 2. Maternal-infant attachment. 3. Anxiety. 4. Maternal stress. 5. Parental stress (e.g. measured using a tool such as the parenting stress index, Abidin 1995). 6. Maternal perceived social support. 7. Maternal dissatisfaction with care provided.

Infant 1. Infant health parameters including no immunization or having accidental injury or non accidental injury. 2. Infant developmental assessments (variously defined). 3. Child abuse and/or neglect.

Family outcomes 1. Marital/partner discord. Other 1. Adverse events or outcomes.

Search methods for identification of studies The following methods section of this protocol is based on a standard template used by the Cochrane Pregnancy and Childbirth Group.

Electronic searches We will search the Cochrane Pregnancy and Childbirth Group’s Trials Register by contacting their Information Specialist. The Register is a database containing over 21,000 reports of controlled trials in the field of pregnancy and childbirth. For full search methods used to populate the Pregnancy and Childbirth Group’s Trials Register including the detailed search strategies for CENTRAL, MEDLINE, Embase and CINAHL; the list of handsearched journals and conference proceedings, and the list of journals reviewed via the current awareness service, please follow this link to the editorial information about the Cochrane Pregnancy and Childbirth Group in the Cochrane Library and select the ‘Specialized Register ’ section from the options on the left side of the screen. Briefly, the Cochrane Pregnancy and Childbirth Group’s Trials Register is maintained by their Information Specialist and contains trials identified from: 1. monthly searches of the Cochrane Central Register of Controlled Trials (CENTRAL); 2. weekly searches of MEDLINE (Ovid); 3. weekly searches of Embase (Ovid); 4. monthly searches of CINAHL (EBSCO); 5. handsearches of 30 journals and the proceedings of major conferences; 6. weekly current awareness alerts for a further 44 journals plus monthly BioMed Central email alerts. Search results are screened by two people and the full text of all relevant trial reports identified through the searching activities described above is reviewed. Based on the intervention described, each trial report is assigned a number that corresponds to a specific Pregnancy and Childbirth Group review topic (or topics), and is then added to the Register. The Information Specialist searches the Register for each review using this topic number rather than keywords. This results in a more specific search set that will be fully accounted for in the relevant review sections (Included, Excluded, Awaiting Classification or Ongoing). In addition, we will search ClinicalTrials.gov and the WHO International Clinical Trials Registry Platform (ICTRP) for unpublished, planned and ongoing trial reports using the terms in Appendix 1.

Searching other resources We will examine secondary references and contact experts in the field. We will determine whether included articles were cited by other authors after their publication in order to identify additional eligible studies. We will not apply any language or date restrictions.

Data collection and analysis


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The following methods section of this protocol is based on a standard template used by the Cochrane Pregnancy and Childbirth Group. Selection of studies Two review authors will independently assess for inclusion all the potential studies identified as a result of the search strategy. We will resolve any disagreement through discussion or, if required, we will consult a third person. We will create a study flow diagram to may out the number of records identified, included, and excluded. Data extraction and management We will design a form to extract data. For eligible studies, two review authors will independently extract the data using the agreed form. We will resolve discrepancies through discussion or, if required, we will consult a third person. We will enter data into Review Manager software (RevMan 2014) and check for accuracy. When information regarding any of the above is unclear, we will attempt to contact the authors of the original reports to provide further details. Assessment of risk of bias in included studies Two review authors (CLD, HB) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreements by discussion or by involving the third review author (JM).

(1) Sequence generation (checking for possible selection bias)

We will describe for each included study the method used to generate the allocation sequence in sufficient detail to allow an assessment of whether it should produce comparable groups. We will assess the method as: • low risk of bias (any truly random process, e.g. random number table; computer random number generator); • high risk of bias (any non-random process, e.g. odd or even date of birth; hospital or clinic record number); • unclear risk of bias. (2) Allocation concealment (checking for possible selection bias)

We will describe for each included study the method used to conceal the allocation sequence and determine whether intervention allocation could have been foreseen in advance of, or during recruitment, or changed after assignment. We will assess the methods as:

• low risk of bias (e.g. telephone or central randomization; consecutively numbered sealed opaque envelopes); • high risk of bias (open random allocation; unsealed or nonopaque envelopes, alternation; date of birth); • unclear risk of bias.

(3) Blinding (checking for possible performance bias)

We will describe for each included study the methods used, if any, to blind study participants and personnel from knowledge of which intervention a participant received. Since women and care providers cannot be easily blinded as to whether an exercise intervention was given (for example), we will consider blinding adequate if outcomes were recorded by outcome assessors who had no knowledge of the woman’s group assignment or if the women self-reported outcome data by mailed questionnaire. We will consider studies at low risk of bias if they were blinded, or if we judge that the lack of blinding could not have affected the results. We will assess blinding separately for participants and staff and for outcome assessors. We will assess the methods as: • low, high or unclear risk of bias for participants and personnel; • low, high or unclear risk of bias for outcome assessors.

(4) Incomplete outcome data (checking for possible attrition bias through withdrawals, dropouts, protocol deviations)

We will describe for each included study, and for each outcome or class of outcomes, the completeness of data including attrition and exclusions from the analysis. We will state whether attrition and exclusions were reported, the numbers included in the analysis at each stage (compared with the total randomized participants), reasons for attrition or exclusion where reported, and whether missing data were balanced across groups or were related to outcomes. Where sufficient information was reported, or could be supplied by the trial authors, we plan to include missing data in the analyses. We will not exclude any trial or outcome from the analysis based on rate of incomplete data. We will perform a sensitivity analysis for those trials where 80% of data on a given outcome were available for those who were originally randomized versus those with < 80%. We will assess methods as: • low risk of bias; • high risk of bias; • unclear risk of bias.

(5) Selective reporting bias

We will describe for each included study how we investigated the possibility of selective outcome reporting bias and what we found. We will assess the methods as:


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• low risk of bias (where it is clear that all of the study’s prespecified outcomes and all expected outcomes of interest to the review have been reported); • high risk of bias (where not all the study’s pre-specified outcomes have been reported; one or more reported primary outcomes were not pre-specified; outcomes of interest were reported incompletely and so could not be used; study failed to include results of a key outcome that would have been expected to have been reported); • unclear risk of bias.

(6) Other sources of bias

We will describe for each included study any important concerns we have about other possible sources of bias. We will assess whether each study was free of other problems that could put it at risk of bias: • low risk of other sources of bias; • high risk of other sources of bias; • unclear risk of other sources of bias. For cluster-randomized trials, we will describe the following (as per the Cochrane Handbook for Systematic Reviews of Interventions 16.3.2 Higgins 2011). 1. Recruitment bias - whether the individuals participating in the trial were blinded to the type of cluster they were in before agreeing to participate. 2. Baseline imbalances - whether there were differences in baseline characteristics between the randomized groups. 3. Loss of clusters - whether any complete clusters were lost to follow-up and the reasons. 4. Incorrect analysis - whether the proper statistical analysis was carried out for a cluster-randomized design. 5. Differences in intervention effects - whether the cluster randomization method could have resulted in different intervention effects than an individually-randomized trial.

(7) Overall risk of bias

We will make explicit judgements about whether studies were at high risk of bias, according to the criteria given in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). With reference to (1) to (6) above, we will assess the likely magnitude and direction of the bias and whether we consider it to be likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses - see Sensitivity analysis.

Assessing the quality of the evidence using GRADE We will assess the quality of the evidence using the GRADE approach as outlined in the GRADE Handbook in order to assess the

quality of the body of evidence relating to the following outcomes for the main comparison (intervention versus standard care). 1. Postpartum depression 2. Maternal mortality and serious morbidity including selfharm, suicide attempts 3. Maternal-infant attachment 4. Anxiety 5. Maternal stress 6. Parental stress 7. Maternal perceived social support We will use the GRADEpro Guideline Development Tool to import data from Review Manager 5.3 (RevMan 2014) in order to create ’Summary of findings’ tables. A summary of the intervention effect and a measure of quality for each of the above outcomes will be produced using the GRADE approach. The GRADE approach uses five considerations (study limitations, consistency of effect, imprecision, indirectness and publication bias) to assess the quality of the body of evidence for each outcome. The evidence can be downgraded from ’high quality’ by one level for serious (or by two levels for very serious) limitations, depending on assessments for risk of bias, indirectness of evidence, serious inconsistency, imprecision of effect estimates or potential publication bias. Measures of treatment effect

Dichotomous data

For dichotomous data, we will present results as summary risk ratio with 95% confidence intervals.

Continuous data

For continuous data, we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardized mean difference to combine trials that measure the same outcome, but use different methods. Unit of analysis issues

Cluster-randomized trials

We will include cluster-randomized trials in the analyses along with individually-randomized trials. We will adjust their sample sizes using the methods described in the Handbook [Section 16.3.4 or 16.3.6] using an estimate of the intracluster correlation co-efficient (ICC) derived from the trial (if possible), from a similar trial or from a study of a similar population. If we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC. If we identify both cluster-randomized trials and individually-randomized trials, we plan to synthesise the relevant information. We will consider it


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reasonable to combine the results from both if there is little heterogeneity between the study designs and the interaction between the effect of intervention and the choice of randomization unit is considered to be unlikely. We will also acknowledge heterogeneity in the randomization unit and perform a sensitivity analysis to investigate the effects of the randomization unit.

Cross-over trials

We will not include cross-over trials.

Other unit of analysis issues

For trials with more than two treatment groups, where possible we will combine arms and carry out pair-wise comparisons.

Dealing with missing data For included studies, we will note levels of attrition. We will explore the impact of including studies with high levels of missing data in the overall assessment of treatment effect by using sensitivity analysis. For all outcomes, we will carry out analyses, as far as possible, on an intention-to-treat basis, i.e. we will attempt to include all participants randomized to each group in the analyses, and all participants will be analyzed in the group to which they were allocated, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial will be the number randomized minus any participants whose outcomes are known to be missing.

Assessment of heterogeneity We will assess statistical heterogeneity in each meta-analysis using the T2 , I2 and Chi2 statistics. We will regard heterogeneity as substantial if a T2 is greater than zero or if there is a low P value (less than 0.10) in the Chi2 test for heterogeneity. We will interpret the I2 value as per the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011), as follows: 1. 0% to 40%: might not be important; 2. 30% to 60%: may represent moderate heterogeneity; 3. 50% to 90%: may represent substantial heterogeneity; 4. 75% to 100%: considerable heterogeneity.

Assessment of reporting biases If there are 10 or more studies in the meta-analysis we will investigate reporting biases (such as publication bias) using funnel plots. We will assess funnel plot asymmetry visually. If asymmetry is suggested by a visual assessment, we will perform exploratory analyses to investigate it.

Data synthesis We will carry out statistical analysis using the Review Manager software (RevMan 2014). We will use fixed-effect meta-analysis for combining data where it is reasonable to assume that studies are estimating the same underlying treatment effect: i.e. where trials are examining the same intervention, and the trials’ populations and methods are judged sufficiently similar. If there is clinical heterogeneity sufficient to expect that the underlying treatment effects differ between trials, or if substantial statistical heterogeneity is detected, we will use random-effects meta-analysis to produce an overall summary, if an average treatment effect across trials is considered clinically meaningful. The random-effects summary will be treated as the average of the range of possible treatment effects and we will discuss the clinical implications of treatment effects differing between trials. If the average treatment effect is not clinically meaningful, we will not combine trials. If we use random-effects analyses, the results will be presented as the average treatment effect with 95% confidence intervals, and the estimates of Tau² and I².

Subgroup analysis and investigation of heterogeneity If we identify substantial heterogeneity, we will investigate it using subgroup analyses and sensitivity analyses. We will consider whether an overall summary is meaningful, and if it is, use random-effects analysis to produce it. We plan to do the following subgroup analyses: 1. the effects of sample selection criteria (e.g. interventions targeting women with specific risk factors versus the general population); 2. the effects of intervention mode (e.g. individual versus group); 3. the effects of intervention provider (e.g. professional versus lay); 4. the effects of intervention setting (e.g. home-based versus non home-based). 5. the effects of intervention onset (e.g. antenatal-only versus antenatal and postnatal versus postnatal-only interventions). Where data are available, the following postpartum depression outcomes will be used in subgroup analysis: 1. depressive symptomatology (as defined by trialist, presented as dichotomous outcome); 2. mean depression scores (as defined by trialist, presented as continuous measure); 3. diagnosis of depression (as defined by trialist). All outcomes will be assessed at two time points: immediately post-treatment and within the first year postpartum. For randomeffects and fixed-effect meta-analyses, we will assess differences between subgroups by inspection of the subgroups’ confidence intervals; non-overlapping confidence intervals suggest a statistically significant difference in treatment effect between the subgroups.


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ACKNOWLEDGEMENTS

Sensitivity analysis We plan to carry out sensitivity analyses, for the primary outcome, in instances in which there was a high risk of bias due to any of the following: 1. inadequate allocation concealment; 2. unblinded outcome assessment or outcome assessment uncertain; 3. incomplete outcome data (more than 20% missing data) for any of the included trials. We will also perform a sensitivity analysis to investigate the effects of the randomization unit. These sensitivity analyses will be undertaken where there were an adequate number of studies.

As part of the pre-publication editorial process, this protocol has been commented on by four peers (an editor and three referees who are external to the editorial team), a member of the Pregnancy and Childbirth Group’s international panel of consumers and the Group’s Statistical Adviser. This project was supported by the National Institute for Health Research, via Cochrane Infrastructure funding to Cochrane Pregnancy and Childbirth. The views and opinions expressed therein are those of the authors and do not necessarily reflect those of the Systematic Reviews Programme, NIHR, NHS or the Department of Health.

REFERENCES

Additional references Abidin 1995 Abidin RR. Parenting Stress Index Professional Manual. 3rd Edition. Florida: Psychological Assessment Resources Inc, 1995.

Freeman 2010 Freeman MP, Fava M, Lake J, Trivedi MH, Wisner KL, Mischoulon D. Complementary and alternative medicine in major depressive disorder: The American Psychiatric Association Task Force report. Journal of Clinical Psychiatry 2010;71(6):669–81.

APA 2013 American Psychiatric Association. Diagnostic and Statistical Manual of Mental Disorders. 5th Edition. Washington, DC: American Psychiatric Association, 2013.

Freeman 2011 Freeman MP, Rapaport MH. Omega-3 fatty acids and depression: from cellular mechanisms to clinical care. Journal of Clinical Psychiatry 2011;72:258–9.

Burke 2003 Burke L. The impact of maternal depression on familial relationships. International Review of Psychiatry 2003;15(3): 243–55.

Gaynes 2005 Gaynes BN, Gavin N, Meltzer-Brody S, Lohr K, Swinson T, Gartlehner G, et al. Perinatal depression: prevalence, screening accuracy, and screening outcomes. http:// www.ahrq.gov/downloads/pub/evidence/pdf/peridepr/ peridep.pd (accessed 2011) 2005.

Cooper 1995 Cooper P, Murray L. The course and recurrence of postnatal depression. British Journal of Psychiatry 1995;166:191–5. Crowley 2012 Crowley SK, Youngstedt SD. Efficacy of light therapy for perinatal depression: a review. Journal of Physiological Anthropology 2012;31:15. Dennis 2012 Dennis CL, Heaman M, Vigod S. Epidemiology of postpartum depression among Canadian women: regional and national results from a cross-sectional survey. Canadian Journal of Psychiatry 2012;57(9):537–46. Dennis 2013 Dennis CL, Dowswell T. Psychosocial and psychological interventions for preventing postpartum depression. Cochrane Database of Systematic Reviews 2013, Issue 2. [DOI: 10.1002/14651858.CD001134.pub3] England 2009 England MJ, Sim LJ. Depression in Parents, Parenting, and Children: Opportunities to Improve Identification, Treatment, and Prevention. Washington, DC: The National Academies Press, 2009.

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APPENDICES

Appendix 1. Search terms for ICTRP and ClinicalTrials.gov preventing AND postpartum depression prevention AND postpartum depression preventing AND postnatal depression prevention AND postnatal depression

CONTRIBUTIONS OF AUTHORS Dr Dennis wrote the text of the review protocol with the assistance of Dr Brown and Dr Morrell.

DECLARATIONS OF INTEREST Cindy-Lee Dennis: is a principal investigator on two trials that may be considered for inclusion in this review. Data for these trials will be extracted by the two other review authors who were not involved in the trials. Hilary K Brown: none known. Jane Morrell: none known.


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