Psychosocial, psychological, and pharmacological interventions for treating antenatal anxiety

Abstract

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

The primary objective of this review is to assess the effects, on women and their families, of psychosocial, psychological, and pharmacological interventions compared with usual antepartum care in the treatment of antenatal anxiety.

Secondary objectives are to examine:

1. the effectiveness of specific types of psychosocial interventions (e.g. diverse supportive interactions including support groups);

2. the effectiveness of specific types of psychological interventions (e.g. CBT and interpersonal psychotherapy);

3. the effectiveness of specific types of pharmacological interventions (e.g. benzodiazepines);

4. the effectiveness of non‐pharmacological (e.g. psychosocial and psychological) versus pharmacological interventions;

5. the effects of intervention mode (e.g. group‐based versus individual interventions);

6. the effects of intervention duration (e.g. multiple‐contact versus single‐contact interventions); and

7. the effects of intervention delivery (e.g. face‐to‐face versus technology‐based interventions).

Background

Description of the condition

Mental illness is a leading cause of disability worldwide and an important public health issue (Baxter 2014). Anxiety disorders, including generalized anxiety disorder, panic disorder, social phobia, and obsessive‐compulsive disorder, are the most common mental health issues, with lifetime prevalence reported to be as high as 30% (Kessler 2005). Anxiety often affects women during their childbearing years (Halbreich 2003 ; McLean 2011). In a recent meta‐analysis, Dennis et al. showed that the prevalence of self‐reported anxiety symptoms across the three trimesters of pregnancy was 22.9% (95% confidence interval (CI) 20.5 to 25.2); the prevalence of a clinical diagnosis was 15.2% (95% CI 9.0 to 21.4) for any anxiety disorder and 4.1% (95% CI 1.9 to 6.2) for a generalized anxiety disorder specifically (Dennis 2017). Antenatal anxiety is also a leading risk factor for postpartum anxiety and depression (Leigh 2008). Despite this condition affecting so many women across the perinatal period, antenatal anxiety has received minimal attention from clinicians and researchers.

Description of the intervention

Anxiety disorders can be effectively treated with both pharmacological and psychological therapies (Bandelow 2017); psychosocial intervention may also be beneficial for mild symptomatology. While benzodiazepines are traditionally the most commonly used medication for anxiety disorders, they are not currently recommended for routine use because of known side‐effects (Bandelow 2014). Pharmacological therapies for the treatment of anxiety now include medications also used to treat depression, including selective serotonin reuptake inhibitors (SSRIs) and serotonin‐norepinephrine reuptake inhibitors (SNRIs). SSRIs and SNRIs have been shown to be effective in the treatment of generalized anxiety disorder and social phobia, and do not carry the same sedative and overdose risks as benzodiazepines (Baldwin 2014). However, when deciding on treatment options, women must weigh the risks and benefits of pharmacological treatment during pregnancy (Walton 2014). Women are often reluctant to take antidepressants and other psychotropic medications due to concerns about foetal and neonatal complications (Grigoriadis 2013; Grigoriadis 2014). It is therefore also important to consider non‐pharmacological interventions for use in antenatal women. Thus, this Cochrane Review focuses on psychosocial (e.g. non‐directive counselling), psychological (e.g. interpersonal psychotherapy, cognitive behavioural therapy (CBT)), and pharmacological interventions for antenatal anxiety.

Psychosocial interventions are based on the observation that the onset of anxiety is frequently associated with social factors (Biaggi 2016). They are often unstructured in nature (Kazdin 2016), and are marked by a 'confiding relationship' that includes enhanced support and therapeutic listening. The goal of these interventions is to provide an opportunity for feelings to be expressed (Kazdin 2016), and examples include peer support groups and other support interactions. Additionally, a range of psychological interventions are available and include several approaches that typically use manuals to guide structured therapy. Cognitive behavioural therapy (CBT) is a common treatment option based on the idea that the manner in which an individual perceives an event partially determines how they will respond both behaviourally and emotionally (Hollon 1998). According to cognitive theory, dysfunctional beliefs and processing of information are at the centre of many psychiatric disorders; CBT therefore helps individuals to identify and correct false beliefs and systematic distortions in the way that they process information (Hollon 1998). Interpersonal therapy (IPT) was developed as a time‐limited, weekly outpatient treatment given by a trained mental health professional (Klerman 1993). The focus of treatment is on the association between symptoms and interpersonal problems; however, this method makes no assumption about aetiology or the cause of the condition. IPT is characterized by three phases:

1. diagnosis evaluation, psychiatric/social history, and linkage between the current situation within one of the interpersonal problem areas to set the framework for treatment;

2. pursuit of strategies (defined in the IPT manual) that target the interpersonal problem area; and

3. encouragement to recognize and consolidate therapeutic gains and develop ways of identifying and countering depressive symptoms (Klerman 1993).

Psychodynamic therapy, also called insight‐oriented therapy, focuses on unconscious processes as they are shown through the ways a person currently behaves (Egger 2015). The goal of treatment is to improve an individual's self‐awareness and understanding of the influence of unresolved conflicts and symptoms from past dysfunctional relationships on present behaviour. Several approaches to brief psychodynamic psychotherapy have evolved from psychoanalytic theory and have been applied to a wide range of psychiatric disorders including anxiety (Leischsenring 2013).

How the intervention might work

Risk factors for antenatal anxiety include young maternal age, single marital status, low education and income, stressful life events, and low social support (Buist 2011; Grant 2008; Lim 2005), highlighting the importance of social factors (Biaggi 2016). Psychosocial and psychological interventions target these social factors. There is also evidence for a biological basis; antenatal anxiety is often comorbid with depression (Ross 2003), and is strongly predicted by previous history of generalized anxiety disorder or depression (Bowen 2008; Buist 2011). These factors indicate a potential for chronicity and thus a role for pharmacological treatment (Bowen 2008 ; Buist 2011). As such, this review examines the effectiveness of psychosocial, psychological, and pharmacological interventions in the treatment of antenatal anxiety where treatment is defined as any intervention initiated among pregnant women who have been identified with anxiety symptomatology.

Why it is important to do this review

If left untreated, antenatal anxiety has significant negative implications for both the mother and the developing fetus. Antenatal anxiety is associated with increased risk for pregnancy complications, labour pain and distress, early requests for pain relief, and operative delivery as well as increased somatic problems, negative expectations about motherhood, difficulty adjusting to the maternal role, anxiety in the postnatal period, postnatal depressive symptoms, and increased frequency of consultation with physicians (Andersson 2004; Chen 2010; Dayan 2002; Field 2009). Antenatal anxiety is also associated with preterm birth, low birthweight, and low Apgar scores as well as poor infant temperament, lower intelligence, language problems, behaviour problems, and poor maternal‐child interactions (Austin 2005; Browers 2001). While infant and child difficulties among the offspring of women with antenatal anxiety may reflect shared genetic risk for psychiatric problems, evidence suggests that high maternal levels of cortisol released during times of significant anxiety influence glucocorticoid receptors in the foetal brain (Dunkel Schetter 2015 ; O'Connor 2002). The research highlights the need for early identification and treatment of antenatal anxiety in order to prevent adverse maternal, infant and child outcomes.

Objectives

The primary objective of this review is to assess the effects, on women and their families, of psychosocial, psychological, and pharmacological interventions compared with usual antepartum care in the treatment of antenatal anxiety.

Secondary objectives are to examine:

1. the effectiveness of specific types of psychosocial interventions (e.g. diverse supportive interactions including support groups);

2. the effectiveness of specific types of psychological interventions (e.g. CBT and interpersonal psychotherapy);

3. the effectiveness of specific types of pharmacological interventions (e.g. benzodiazepines);

4. the effectiveness of non‐pharmacological (e.g. psychosocial and psychological) versus pharmacological interventions;

5. the effects of intervention mode (e.g. group‐based versus individual interventions);

6. the effects of intervention duration (e.g. multiple‐contact versus single‐contact interventions); and

7. the effects of intervention delivery (e.g. face‐to‐face versus technology‐based interventions).

Methods

Criteria for considering studies for this review

Types of studies

All published, unpublished, and ongoing randomized controlled trials and cluster‐randomized controlled trials of psychosocial interventions, psychological interventions, or pharmacological interventions in which the primary or secondary aim is to treat antenatal anxiety.

We will exclude quasi‐randomized trials (e.g. those randomized by even versus odd medical record numbers) and cross‐over trials from the analysis.

Types of participants

Participant characteristics

Pregnant women of all ages identified with antenatal anxiety (variously defined by trialists).

Diagnosis

We will include women with various levels of anxiety symptomatology that developed between conception and delivery who were identified either via self‐report measure (e.g. State‐Trait Anxiety Inventory (STAI) (Spielberger 1983)) or a diagnostic interview (e.g. Structured Clinical Interview for DSM‐IV (SCID) (Spitzer 1992)). The threshold scores for the respective scales will be those defined by the trialists.

Comorbidities

Studies including women with a co‐morbid psychiatric or other medical condition (e.g. depression) will be eligible for inclusion if the comorbidity is not the study's focus.

Setting

We will include studies in which participants were recruited from diverse settings, including home, primary care, and hospital clinics.

Types of interventions

Experimental interventions

We will include non‐pharmacological interventions (e.g. psychoeducational strategies, non‐directive counselling, various supportive interactions, tangible assistance, CBT, and interpersonal psychotherapy) and pharmacological interventions (e.g. benzodiazepines, selective serotonin reuptake inhibitors, and serotonin‐norepinephrine reuptake inhibitors). Psychosocial and psychological interventions may be delivered via telephone or Internet, home or clinic visits, or individual or group sessions antenatally by a professional (e.g. psychologist, nurse, midwife, childbirth educator, or physician) or lay person (e.g. a specially trained individual from the community or a student). Both review authors (CLD and HKB) will classify non‐pharmacological interventions as either psychosocial or psychological; a third person will resolve any discrepancies where necessary.

Comparator interventions

Standard or usual care will include any appropriate healthcare received during the trial, including psychological or pharmacological placebo, waiting list (i.e. delayed entry into the intervention group), attention placebo (i.e. a treatment that mimics the amount of time and attention received in the intervention group), or simple educational strategies. We will exclude trials that evaluate one non‐pharmacological treatment against another non‐pharmacological treatment. We will include comparisons between non‐pharmacological and pharmacological interventions.

Types of outcome measures

We will examine a number of maternal, infant, and family outcomes.

Primary outcomes

The primary outcome will be maternal anxiety, as variously defined and measured by trialists, including above a self‐reported cut‐off or clinical diagnosis (dichotomous) and anxiety severity (continuous). Common measures include the STAI (Spielberger 1983). Our primary time point will be assessment of antepartum anxiety immediately post‐treatment, i.e. after treatment completion in the case of psychosocial or psychological interventions or the first follow‐up assessment in the case of pharmacological interventions.

Secondary outcomes

Maternal outcomes

1. Depression (as variously defined by the trialists including using the Edinburgh Postnatal Depression Scale (Cox 1987));

2. stress (as variously defined by the trialists, including using the Perceived Stress Scale (Cohen 1983));

3. parenting stress (as variously defined by the trialists, including using the Parenting Stress Index (Abidin 1990));

4. dissatisfaction with intervention.

Infant outcomes

1. Preterm birth (less than 37 weeks' gestation);

2. breastfeeding duration (variously defined);

3. infant developmental assessments (variously defined).

Family outcomes

1. Marital discord (as variously defined by the trialists including using the Dyadic Adjustment Scale (Spanier 1987)).

Timing of outcome assessment

For all comparisons, outcomes will be categorized as assessments carried out immediately post‐treatment.

Hierarchy of outcome measures

If studies include more than one measure of the same outcome, we will include in the data analyses the most commonly used measure, focusing on assessor‐blinded outcomes. For example, for diverse measures of maternal anxiety (e.g. the STAI and Hospital Anxiety and Depression Scale‐Anxiety (HADS‐A)), we will use the internationally recognized STAI.

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 Cochrane Pregnancy and Childbirth’s Trials Register by contacting their Information Specialist.

The register is a database containing over 23,000 reports of controlled trials in the field of pregnancy and childbirth. For full search methods used to populate Cochrane Pregnancy and Childbirth’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 Cochrane Pregnancy and Childbirth 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’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.

Two people screen search results and the full text of all relevant trial reports identified through the searching activities described above is assessed. Based on the intervention described, each trial report is assigned a number that corresponds to a specific Pregnancy and Childbirth 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 studies).

We will also search ClinicalTrials.gov and the World Health Organization (WHO) International Clinical Trials Registry Platform (ICTRP) for unpublished, planned, and ongoing trial reports using the terms given in Appendix 1.

Searching other resources

We will contact experts in the field to identify other unpublished or published trials. We will also scan secondary references, search reference lists of retrieved studies, and determine whether retrieved studies were cited by other authors after their publication to identify additional eligible studies.

We will not apply any language or date restrictions.

Data collection and analysis

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

Selection of studies

Both review authors (CLD and HKB) will independently assess for inclusion all the potential studies we identify as a result of the search strategy. After assessing titles and abstracts, we will retrieve the full‐text articles of potentially eligible studies. We will then include and exclude studies according to the methods described above. We will resolve any disagreement through discussion or, if required, we will consult a third person. We will collate multiple reports that pertain to the same study so that each study rather than each report will be the unit of interest in our review. We will record the study selection process using a PRISMA flow diagram and 'Characteristics of included studies' table.

Data extraction and management

We will design a form to extract data, which will include information on trial methods (method of allocation generation, method of allocation concealment, loss of participants to follow‐up, blinding, use of intention‐to‐treat analysis), inclusion and exclusion criteria for participants, details of the intervention and control groups, outcome data (number of events and total number of participants or mean and standard deviations for intervention and control groups, as relevant), trial funding, trial dates, and trialists' declarations of interest. For eligible studies, both review authors (CLD and HKB) will 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 5 (RevMan 5) software (RevMan 2014), and will check for data entry accuracy. When information regarding any of the above is unclear, we will attempt to contact authors of the original reports to provide further details.

Assessment of risk of bias in included studies

Both review authors (CLD and HKB) will independently assess the risk of bias for each included study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011). We will resolve any disagreement by discussion or by involving a third assessor.

(1) Random 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 allocation to interventions prior to assignment and will assess 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 non‐opaque envelopes, alternation; date of birth);

• unclear risk of bias.   

(3.1) Blinding of participants and personnel (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. We will consider that studies are at low risk of bias if they were blinded, or if we judge that the lack of blinding would be unlikely to affect results. We will assess blinding separately for different outcomes or classes of outcomes.

We will assess the methods as:

• low, high, or unclear risk of bias for participants;

• low, high, or unclear risk of bias for personnel.

(3.2) Blinding of outcome assessment (checking for possible detection bias)

We will describe for each included study the methods used, if any, to blind outcome assessors from knowledge of which intervention a participant received. We will assess blinding separately for different outcomes or classes of outcomes.

We will assess methods used to blind outcome assessment as:

• low, high, or unclear risk of bias.

(4) Incomplete outcome data (checking for possible attrition bias due to the amount, nature and handling of incomplete outcome data)

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 and 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 is reported, or can be supplied by the trial authors, we will re‐include missing data in the analyses which we undertake.

We will assess methods as:

• low risk of bias (e.g. no missing outcome data or < 20%; missing outcome data balanced across groups);

• high risk of bias (e.g. numbers or reasons for missing data imbalanced across groups; ‘as treated’ analysis done with substantial departure of intervention received from that assigned at randomization);

• unclear risk of bias.

(5) Selective reporting (checking for 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:

• low risk of bias (where it is clear that all of the study’s pre‐specified 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 are reported incompletely and so cannot be used; study fails to include results of a key outcome that would have been expected to have been reported);

• unclear risk of bias.

(6) Other bias (checking for bias due to problems not covered by (1) to (5) above)

We will describe for each included study any important concerns we have about other possible sources of bias such as extreme baseline imbalances. We will assess whether each study was free of other problems that could put it at risk of bias:

• low risk of other bias;

• high risk of other bias;

• unclear whether there is risk of other bias.

(7) Overall risk of bias

We will make explicit judgements about whether studies are 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 is likely to impact on the findings. We will explore the impact of the level of bias through undertaking sensitivity analyses ‐ seeSensitivity analysis.

Assessment of the quality of evidence using the GRADE approach

We will assess the overall quality of the evidence for the review's primary outcome using the GRADE approach as outlined in the GRADE handbook for the main comparisons:

• psychosocial interventions versus usual care;

• psychological interventions versus usual care;

• pharmacological interventions versus usual care.

We will use GRADE profiler, GRADEpro 2013, to import data from RevMan 5, RevMan 2014, in order to create 'Summary of findings’ tables. We will produce a summary of the intervention effect and a measure of quality for each of the above outcomes 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 (e.g. anxiety symptomatology based on an established cut‐off or diagnosis of anxiety), we will present results as summary risk ratio with 95% CIs. 

Continuous data

For continuous data (e.g. mean anxiety symptomatology scores), we will use the mean difference if outcomes are measured in the same way between trials. We will use the standardised 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 Section 16.3.4 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) 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 synthesize the relevant information. We will consider it 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 exclude cross‐over designs from our review.

Other unit of analysis issues

We will combine treatment arms if there is more than one group that meets the criteria for psychosocial, psychological, or pharmacological interventions. We also will combine control arms if there is more than one group that meets the criteria for 'standard care'.

Dealing with missing data

We will contact study authors for missing data. It is important to note that if data remain missing after attempts to obtain them, for some measures of variation where there is an approximate or direct algebraic relationship with the standard deviation, it may be possible to obtain the required statistic even if it is not published in the paper, as explained in the Cochrane Handbook for Systematic Reviews of Intervention Sections 7.7.3.2 to 7.7.3.7 (Higgins 2011). We will closely examine our missing data and determine if imputations are possible.

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. We will compare trials in which 80% of data on a given outcome were available for those originally randomized to those with less than 80%. 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 analysed 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 statistic, and Chi² test. We will regard heterogeneity as substantial if the I² statistic value is greater than 30% and either T² is greater than zero, or there is a low P value (< 0.10) in the Chi² test for 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, and at any suggestion of asymmetry, we will perform exploratory analyses to investigate it.

Data synthesis

We will carry out statistical analysis using RevMan 5 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. We will treat the random‐effects summary as the average 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. We will not use random‐effects models if fewer than five studies are included. If we use random‐effects analyses, we will present the results as the average treatment effect with 95% CIs, and the estimates of  T² and I² statistic.

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 carry out the following subgroup analyses:

1. the effectiveness of specific types of psychosocial interventions (e.g. diverse supportive interactions including support groups);

2. the effectiveness of specific types of psychological interventions (e.g. CBT and interpersonal psychotherapy);

3. the effectiveness of specific types of pharmacological interventions (e.g. antidepressant medication);

4. the effects of intervention mode (e.g. group‐based versus individual interventions);

5. the effects of intervention duration (e.g. multiple‐contact versus single‐contact interventions); and

6. the effects of intervention delivery (e.g. face‐to‐face versus technology).

Where data are available, we will use the following anxiety outcomes in subgroup analyses:

• anxiety symptomatology (as defined by trialist, presented as dichotomous outcome);

• mean anxiety scores (as defined by trialist, presented as continuous measure);

• diagnosis of anxiety (as defined by trialist, presented as dichotomous outcome).

All outcomes will be assessed at one time point: immediately post‐treatment. For fixed‐effect inverse variance meta‐analyses, we will assess differences between subgroups by interaction tests. For random‐effects and fixed‐effect meta‐analyses using methods other than inverse variance, we will assess differences between subgroups by inspection of the subgroups’ CIs; non‐overlapping CIs indicate a statistically significant difference in treatment effect between the subgroups. When comparing treatment effects between subgroups we will implement interaction tests.

Sensitivity analysis

We will undertake sensitivity analyses to explore the effect of trial quality. We will do this based on risk of selection bias and attrition bias. Studies of poor quality will be excluded in the analysis (i.e. those with high risk of bias). This analysis will allow us to assess for any important differences to the overall result. These sensitivity analyses will be undertaken where there are an adequate number of studies (i.e. two or more studies remaining after exclusion of high‐risk studies, for a given analysis). Finally, if we include cluster randomized controlled trials and we use ICCs from other sources, we will report this and conduct sensitivity analyses to investigate the effect of variation in the ICC.

Appendices

Appendix 1. Search terms for the WHO ICTRP and ClinicalTrials.gov

antenatal AND anxiet*

prenatal AND anxiet*

antepartum AND anxiet*

Contributions of authors

Drs Dennis and Brown wrote the text of the review protocol. Dr Dennis is the guarantor for this review.

Sources of support

Internal sources

• No sources of support supplied

External sources

• Canadian Institutes of Health Research, Canada Research Chair, Canada.

Declarations of interest

Cindy‐Lee Dennis: none known.

Hilary Brown: none known.

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