Peer support interventions for parents and carers of children with complex needs

Demands of caregiving

Parents caring for children with complex needs experience anxiety about their child's diagnosis and prognosis, and may also experience short-term emotional distress, loneliness, uncertainty and symptoms of depression (Barlow 2006). Physical caregiving activities, supporting the provision of therapy, and advocating for the child can prove extremely time-consuming (McGuire 2004). Parents may have difficulty gaining access to the services and resources they need (Banach 2010).

Behavioural problems may cause stress for families regardless of the underlying condition. For example, in families where children have a developmental delay, behavioural problems resulting from the delay were a greater contributor to increased parenting stress than was the developmental delay itself (Baker 2002). Parents may feel a lack of confidence in dealing with behavioural issues and suffer from a paucity of support services (Twoy 2007).

Changes to family life

A recent review found that chronic diseases in children interfere with daily life in the family, increasing the parents' burden of care (Barlow 2006). Balancing the healthcare needs of the affected child against other family needs, and the reduced time for other necessary or enjoyable activities, is a source of family stress (Banach 2010). In addition to stresses directly relating to the child's condition, families of children with complex needs must adapt to new roles, adjust their lives to cope with the needs of the child, and accommodate increased strain on family resources. As well as managing the needs of the affected child and any other children in the family, parents must cope with their own chronic stress and periodic family crises (Bourke-Taylor 2010; Dellve 2006).

Social stigma and isolation

Families in which a child has a chronic illness are at increased risk of isolation from formal and informal social support mechanisms (Tak 2002).

Challenging behaviours may make social outings difficult, a problem exacerbated by a lack of understanding in the community of the underlying condition (Twoy 2007), meaning parents may choose isolation over the frustrations of taking their child out in public (Tak 2002). Physical frailty of the child may similarly restrict parents' ability to maintain social networks.

Parents often feel a need to assist family and friends in handling their feelings about their child's condition, and to educate others about the condition (Dellve 2006). Parents can feel stigmatised (either through the direct actions and comments of others, or indirectly through their own attributions and anxieties about what others might be thinking). As a result, they may restrict social activities or may socialise only with other families whose children have a similar diagnosis. In some cases families may be excluded from social gatherings by others (Gray 2002).

Benefits of social support

Social support (defined as a combination of emotional concern, instrumental (tangible) aid, information, and appraisal) may mediate the stress experienced by families of children with serious physical, emotional, or behavioural challenges by contributing to coping resources (Lazarus 1987; Dunkel-Schetter 1987). It reduces stress in, for example, parents of children with severe learning difficulties (Quine 1991). Social integration and support protect against the potentially harmful effects of stressful family circumstances, but also have beneficial effects on well-being whether or not a person is currently under stress (Armstrong 2005).

Types of studies

Studies will not be limited to randomised controlled trials as, perhaps due to the self-directed nature of participation in peer support interventions, our preliminary searches of the literature have found that few if any randomised controlled trials have been performed in this area.

We will include:

1. randomised controlled trials (RCTs) and cluster RCTs,

2. quasi-RCTs,

3. controlled before and after (CBA) studies, and

4. interrupted times series (ITS) studies.

To be included in this review, CBA and ITS studies must meet the Cochrane Effective Practice and Organisation of Care Review Group (EPOC) criteria (Ryan 2011). These specify, for CBA designs: at least two intervention sites and two control sites, comparable timing of measurements for control and intervention groups, and comparable key characteristics for control and intervention groups; and for ITS designs: a clearly specified intervention time-point and at least three data collection points before and after that intervention.

We will include studies with a broad range of control groups, including no-treatment, wait list, and usual care controls.

We will enhance this review by incorporating evidence from qualitative research which we may identify whilst searching for evidence of effectiveness (Noyes 2011b). We will include qualitative data associated with the studies of effectiveness described above, but will not conduct a separate search for qualitative studies and will therefore not include either qualitative-only studies, or conduct an exhaustive review of mixed-methods studies.

Types of participants

Parents and carers of children with complex needs, where complex needs include chronic or severe acute illness, disability, or delayed/atypical development in the physical, psychological, developmental, or intellectual domains.

Children will be defined as individuals aged 18 years or younger.

Types of interventions

The target intervention will be the provision of peer support through networks or groups. This will include peer-led and facilitator-led interventions where the focus is on peer-to-peer interactions and support. We will include one-to-one and group interventions, and both face-to-face interventions and those which are technology-assisted (i.e. conducted over the telephone or Internet).

We will include the following comparisons in the review:

• Any peer support intervention delivered to parents or carers of children with complex needs versus control (no-treatment, wait list, or usual care); and

• One peer support intervention versus another.

We will exclude studies if the effects of the peer intervention are not able to be separated from those of other intervention components. For example, studies will be excluded where the primary focus is other than developing and supporting peer networks (e.g. where professionals deliver an educative component or formal therapy), and improved peer networks are an incidental outcome.

Studies where the client or focus of the intervention is the child will only be included if direct outcomes for parents and carers are measured. For example, an intervention where the child is the primary client (such as play groups and early intervention programs) and parent peer support is an incidental putative outcome will be excluded from the review, unless this support and other parental outcomes are directly measured.

Types of outcome measures

Electronic searches

We will search:

• Cochrane Central Register of Controlled Trials (CENTRAL, The Cochrane Library, latest issue)

• MEDLINE (OvidSP) (1966 to present)

• EMBASE (OvidSP) (1974 to present)

• Journals@OVID

• PsycINFO (OvidSP) (1887 to present)

• BiblioMap (EPPI-Centre, Health Promotion research database)

We will also search the Science Citation Index and the Social Sciences Citation Index.

We present the MEDLINE (OvidSP) strategy in Appendix 1. Strategies will be tailored to other databases and reported in the review.

There will be no date restrictions. We will seek translation of potentially-relevant studies in languages other than English.

Searching other resources

We will handsearch the reference lists of relevant retrieved articles to locate studies that are not identified by the database search.

We will search www.clinicaltrials.gov and the World Health Organisation clinical trials registry (www.who.int/ictrp) for relevant studies.

We will search Scopus conference proceedings. We will also consult databases at http://www.evidence.nhs.uk/ (Evidence in Health and Social Care), the New York Academy of Medicine Grey Literature report, and the OpenGrey system for information on grey literature in Europe for other avenues leading to unpublished studies.

We will consult advocacy and support groups, and contact colleagues and key investigators identified through other searches, for advice on identifying other unpublished data. We will also make use of existing professional connections with disability support and early childhood agencies in order to identify results which might otherwise be missed.

We will check trial registries (e.g. the International Clinical Trials Registry Platform Search Portal (www.who.int/trialsearch), and mRCT (www.controlled-trials.com/mcrt)) for trials commenced in recent years, for which data may exist which have not yet been published.

Selection of studies

Search strategies will be reviewed by the Cochrane Consumers and Communication Review Group before being executed. Bibliographic details for all search results will be consolidated and duplicate records removed using reference management software such as EndNote.

Abstracts will be reviewed and rated for inclusion independently by two authors based on the Criteria for considering studies for this review. Differences in rating will be resolved by a third author. We will record details of abstracts and decisions about inclusion, exclusion, or need to request further information from authors in an electronic database. Studies will not be excluded on the basis of outcomes; if an included study fails to report on an outcome of interest this will be reported in the review.

We will retrieve in full text all studies assessed as possibly relevant by one or more authors, based on assessment of title and abstract. Full text studies will be assessed against the Criteria for considering studies for this review, and any excluded at this stage will be listed in the Characteristics of Excluded Studies table, together with a reason for exclusion. We will use an adapted PRISMA (Preferred Reporting Items for Systematic Reviews and Meta-Analyses) flow-chart to describe the study selection process (Liberati 2009).

Data extraction and management

We will use the data extraction template provided by the Cochrane Consumers and Communication Review Group (Ryan 2011) for quantitative data relating to intervention effectiveness, revising where needed (for example, any ITS studies will need to be assessed using the Review Group's amended risk of bias tool (Ryan 2011), and the presence of any qualitative component addressing review outcomes will be noted) and piloting any revised version.

Data to be extracted will include the following items: details of the study (aim, design, recruitment method, statistical method); characteristics of the participants; characteristics of the intervention(s) including control/usual care; outcome measures; and results.

We will extract qualitative data identified during study search and selection using a template similar to that used by Noyes and Popay (2007, cited in Noyes 2011a). This template will be modified to enable the extraction of data relating to the process outcomes described above (Types of outcome measures). We will take the inclusive approach outlined in Noyes 2011a where all text or tables labelled as results in study reports will be included if they relate to our specified outcomes, not only direct quotations from respondents.

Data will be extracted by one author and will be cross-checked and confirmed by another; where necessary, consensus will be reached through discussion and consultation with a third author.

All extracted data will be entered into RevMan software (RevMan 2012) by one review author, and will be checked for accuracy against the data extraction sheets by a second review author working independently.

Assessment of risk of bias in included studies

We will assess and report on the risk of bias of included studies using the tool provided in the Cochrane Handbook (Higgins 2011b) and the guidelines of the Cochrane Consumers and Communication Review Group (Ryan 2011), assessing the following domains: random sequence generation; allocation sequence concealment; blinding (participants, personnel); blinding (outcome assessment); completeness of outcome data (attrition), selective outcome reporting; other sources of bias. This latter category will cover risks specific to non-randomised studies, such as selection bias (Higgins 2011a) and sources of bias associated with cluster-randomised trials (Higgins 2011c). We will judge each item as being at high, low, or unclear risk of bias as set out in the data extraction template adapted by the Cochrane Consumers and Communication Review Group (Ryan 2011, adapted from Higgins 2011a), and describe the relevant supporting information provided by the study authors for each item. Risk of bias will be addressed at study level and at outcome level.

RCTs will be deemed to be at the highest risk of bias if they are scored as being at high risk of bias on the sequence generation, allocation concealment, or incomplete outcome data domains. RCTs will be rated as at unclear risk of bias if they are rated as unclear on at least one of these three domains; while low risk of bias studies will be defined as those receiving a low risk of bias rating on all three of the sequence generation, allocation concealment and incomplete outcome data domains of the tool.

If quasi-RCTs are included in this review we will assess and report them as being at high risk of bias on the random sequence generation item of the 'Risk of bias' tool.

If cluster RCTs are included in this review we will also assess and report the risk of bias associated with an additional domain: selective recruitment of participants (described in Ryan 2011).

If CBA studies are included in this review, we will assess their risk of bias systematically using the adaptations developed by the EPOC Group, outlined in Ryan 2011. CBA studies will be assessed against the same criteria as RCTs, but will be reported as being at high risk of bias on both the random sequence generation and allocation concealment items. We will exclude these studies from the review if intervention and control groups are not reasonably comparable at baseline.

If ITS studies are included in the review, we will assess their risk of bias systematically using the adaptations developed by the EPOC Group, outlined in Ryan 2011. Specifically, we will assess and report the following individual items for ITS studies: intervention independence of other changes; pre-specification of the shape of the intervention effect; likelihood of intervention affecting data collection; blinding (participants, personnel); blinding (outcome assessment); completeness of outcome data; selective outcome reporting; and other sources of bias.

In all cases, two authors will independently assess the risk of bias of included studies, with any disagreements resolved by discussion and consensus. We will contact study authors for additional information about the included studies, or for clarification of the study methods as required.

Measures of treatment effect

Where both intervention and control baseline data are available, we will report pre- and post-intervention means.

We will present dichotomous outcomes as risk ratios (relative risk) and 95% confidence intervals (CI), based on the number of events and numbers of people in the control and intervention groups. We will also calculate risk difference, along with the number needed to treat to achieve the desired outcome. As advised in the Cochrane Handbook (Higgins 2011a, section 9.2.2.2) any results reported as odds ratios will be converted to risk ratios before interpretation.

For continuous outcomes, we will use final values scores in preference to change-from-baseline scores. If only change scores are reported in a study, and if it is not possible to extract the final score, mean and standard deviation, or other data necessary to calculate a standardised mean difference (SMD), we will report change scores in a separate table.

We will assume that included studies will use a variety of measures to assess the same outcome. We will therefore calculate the SMD and 95% CI using the mean, standard deviation and number of people assessed in control and intervention groups using the inverse variance method in Review Manager 5 software (Higgins 2011a, section 9.4.3.2; RevMan 2012).

If reporting CBA studies, we will report dichotomous and continuous outcomes as described above.

If reporting ITS studies, we will use the change in the level of outcome (extrapolating pre-intervention regression line to the first point post-intervention) or change in trend (post-intervention regression slope minus pre-intervention regression slope) as determined by the included study (Ramsay 2003).

Trichotomous outcomes may be relevant to this review (for example, classification of distress as mild/moderate/severe). The review is also very likely to encounter ordinal outcome data in the form of various scales. We will check such scales for established cut-points for conversion to dichotomous data; we will treat larger ordinal scales as continuous data.

Count measures may be relevant to this review (for example, numbers of social connections established). However, they are likely to be counts of common events and hence will be treated in the same way as continuous data; i.e. treatment effect will be measured via mean difference.

Unit of analysis issues

If the assessment of bias of individual RCT studies outlined above identifies sufficient studies for a meta-analysis to be appropriate (Higgins 2011a, section 9.1.4), the analysis will take into account the level at which randomisation occurred (e.g. individual, cluster, cross-over) in included studies.

If cluster-randomised trials are included, we will check that the original analysis was conducted appropriately for clusters as units of randomisation (rather than, incorrectly, for individuals). If an inappropriate analysis was performed, we will attempt to extract: (1) the number or mean size of clusters randomised to each intervention group; (2) outcome data for the total number of individuals, ignoring cluster design, and (3) an estimate of the intracluster correlation coefficient (ICC). This estimate will be sourced using the Health Services Research Unit 2012 online database and Ukoumunne 1999.

Once an appropriate ICC is obtained, we will follow the procedure for obtaining an effective sample size outlined in Higgins 2011a (section 16.3.4).

If it is not possible to obtain sufficient information to reanalyse the data, we will report effect estimates and annotate 'unit-of-analysis error'.

Dealing with missing data

In the first instance, we will attempt to contact authors of studies with missing data to request the missing data. If missing data cannot be obtained, we will seek the advice of a biostatistician and impute the missing data, with appropriate adjustments to the standard error to account for the added uncertainty in the results. If there are significant missing data, we will also consider how sensitive our results are to changes in the assumptions made to impute the data, and address the implications of any sensitivity in the Discussion section.

Assessment of heterogeneity

Where studies are considered similar enough, based on consideration of populations and intervention settings to allow pooling of data using meta-analysis, we will assess the degree of heterogeneity by visual inspection of forest plots and by examining the Chi² test for heterogeneity. Heterogeneity will be quantified using the I² statistic. An I² value of 50% or more will be considered to represent substantial levels of heterogeneity, but this value will be interpreted in light of the size and direction of effects and the strength of the evidence for heterogeneity, based on the P value from the Chi² test (Higgins 2011a).

Where we detect substantial clinical, methodological, or statistical heterogeneity across included studies we will not report pooled results from meta-analysis but will instead use a narrative approach to data synthesis. In this event we will attempt to explore possible clinical or methodological reasons for variation by grouping studies that are similar in terms of the variables listed under Subgroup analysis.

Assessment of reporting biases

The existence of reporting bias will be assessed by testing for asymmetry of the funnel plot of intervention effect estimates against standard error of the intervention effect estimates. We will only proceed with these tests if there are least 10 studies included in the meta-analysis (Higgins 2011a; Sterne 2011).

Data synthesis

The decision to meta-analyse or not will be based on an assessment on whether participants, settings, intervention, comparison, and outcomes are sufficiently similar to ensure a clinically-meaningful result. We will use a random-effects model, as we expect our included studies to be clinically heterogeneous.

We will meta-analyse RCT (including cluster RCT and quasi-RCT) studies. Meta-analyses will be stratified into low versus high or unclear risk of bias according to the methods described at Assessment of risk of bias in included studies.

If our 'Risk of bias' assessment indicates that many studies located are at generally high risk of bias, or if the risk is unclear for all, we will present an estimated intervention effect with a tabulated discussion of risk of bias.

If included RCTs are not suitable for meta-analysis (because they are insufficiently similar to ensure clinically-meaningful conclusions), we will follow the recommendation of Higgins 2011a (section 13.6.2.4) and display their individual results in a forest plot while suppressing a pooled estimate.

We will present data from CBA and ITS studies descriptively (for example as median effect sizes) and graphically where possible.

We will present tables of the results for studies included in the review but not suitable for meta-analysis, which will be grouped according to outcome, and will summarise study type, intervention sub-type (if relevant), participant characteristics, and the findings of the study. We will use the summary of the risk of bias of an outcome across studies to judge the robustness of this evidence (Cash-Gibson 2012). Tables of results will be used to form a narrative assessment of the evidence, clustering studies by intervention type and setting. For each study, we will report the same elements of information in the same order (Higgins 2011a, section 11.7.2).

We will conduct statistical analyses using the latest version of RevMan software (RevMan 2012).

Subgroup analysis and investigation of heterogeneity

As discussed in the Background, subgroups of the population may differ in their capacity to benefit from the intervention, and intervention mode and setting may also influence outcomes for different subgroups.

If our assessment of heterogeneity suggests that substantial heterogeneity is present in meta-analysed data, we will conduct subgroup analyses to investigate the variables (described in detail in the Background) which may influence the effectiveness of the intervention, such as:

• existing social connectedness of participants (where this is measured using scales with established thresholds for high versus low connectedness);

• delivery mode:

  • paired versus group;

  • peer-led versus facilitator-led;

• setting (e.g. face-to-face versus technology-assisted);

• duration and size. Preliminary investigation suggests that peer support group duration, frequency of meeting, and size vary considerably where details are specified (which is not universal) (Bywater 1984; Campbell 2004; Castelein 2008; Doull 2005). Cut-points for duration, frequency, and size comparisons will be determined following retrieval of studies. Typical ranges identified in the preliminary searches are:

• • Duration of program: 10 weeks to 8 months;

  • Duration of session: 60 to 90 minutes;

  • Number of sessions: 8 to unbounded;

  • Size of groups: 4 to 16 people;

• How recently the child's condition was diagnosed (e.g. parent referred to peer support intervention as part of diagnosis/initial medical intervention versus later referral);

• homogeneous (that is, condition-specific) versus heterogeneous conditions affecting children.

Sensitivity analysis

While some sensitivity analyses can be pre-specified in this protocol, many issues which could be suitable for sensitivity analysis will only become apparent during the review process when the individual peculiarities of the studies under investigation are identified (Higgins 2011a). Questions which may be relevant to this review are:

• For dichotomous outcomes, should odds ratios, risk ratios, or risk differences be used?

• For continuous outcomes, should results be analysed as a standardised mean difference across all scales or as individual mean differences across all scales? (Higgins 2011a)

• Where ordinal outcome measures have been converted to dichotomous or trichotomous outcomes, and where there is no consensus on cut-points for making such conversions, do different cut-points affect the results of the analysis?

• If missing data were imputed, do changes in the assumptions made for the imputation affect the results of the analysis?