The effectiveness of information and communication technology-based psychological interventions for paediatric chronic pain: protocol for a systematic review, meta-analysis and intervention content analysis

The primary outcomes of interest are those that measure change in pain characteristics including intensity, severity or frequency and pain interference including physical and social interference (e.g. related school absenteeism) from pre to post treatment. Pain intensity, severity and frequency are generally measured using self-reported verbal or numerical rating scales or visual analogue scales. Pain interference is commonly measured using psychometric tools with established validity and reliability, e.g. Functional Disability Inventory (FDI) [49] or the Pediatric Quality of Life Inventory (PedsQL) [50]. In cases where the chronic pain condition refers to chronic headache pain or migraine, psychometric tools such as the PedMIDAS [51] may be used. As per Eccleston et al. (2014) and McGuire et al. (2014), we will also report the responder rate (the percentage of subjects in the treatment group with at least 50 % reduction in the primary efficacy measure) [30, 52].

Secondary outcomes of interest include emotional functioning (self-reported measures of psychological distress such as depression and/or anxiety), quality of life (self-report questionnaires assessing the impact of chronic pain on quality of life) and global ratings of improvement (self-reported measure of change in subjective sense of wellbeing). Data relating to treatment acceptability and satisfaction, retention and attrition will also be extracted as a secondary outcome. Adverse events will also be reported. These variables may be measured using psychometric tools with established validity and reliability such as the Paediatric Quality of Life Inventory (PedsQL) [50], the Children’s Depression Inventory (CDI) [53]. Finally, we will include variables which are measured as a discrete outcome or as a subscale within a composite measure.

The titles and abstracts of publications obtained by the search strategy will be independently screened by two authors (AT, BMG). Those that fail to meet the outlined inclusion criteria will be removed. All remaining publications will be retrieved for further scrutiny. Two review authors (AT, BMG) will independently assess the full text of studies which initially meet the review criteria. Disagreements between review authors will be discussed until resolved; in the event a resolution cannot be reached, a third review author will arbitrate (JE). A record will be kept of all articles excluded at this stage and the reason for their exclusion. We will produce a PRISMA flow diagram to illustrate the search and systematic review process as recommended in Chapter 6 of the Cochrane Handbook [54].

A data extraction form will be created prior to data extraction. Data will be extracted independently by one reviewer (AT) and verified by another (BMG) using a customised form, which will be piloted prior to use. Disagreements in data extraction will be resolved through discussion with the primary data extractor, as required. In the event that resolution cannot be reached, a third review author will arbitrate (JE). The finalised data will be entered into RevMan 5.3 [56]. Multiple publications of the same study will be identified, linked and used for all relevant reported data. In such cases, the original publication will be given priority. Where the necessary outcome data are unavailable, we will contact study authors. If the data remains unavailable, the study will not be included in any assessment. The authors will not be blind to the study author, institution or journal.

We will extract data relevant to the following categories: (i) Study population and design, (ii) Intervention and (iii) Outcome. Characteristics of included studies’ table(s) will be created and may include the following information:

The use of theory in the included interventions will be coded according to the Theoretical Domains Framework (TDF) [57]. This is an integrative framework which was developed and validated by Cane, O’Connor and Michie (2012). The TDF summarises the range of psychological theory potentially driving behaviour change, into a total of 14 distinct domains. In line with the approach taken by Little et al. (2015), descriptions of intervention and control conditions will be assessed to determine if and to what extent TDF domains are targeted within [58]. This process will be carried out independently by two coders (AT, EM) using a data extraction form similar to the form used by Little et al. (2015). Inter-rater reliability will be calculated and discrepancies will be discussed until resolved.

The behaviour change technique taxonomy (v1) of 93 hierarchical clustered techniques [59] will be used to code intervention content. Mode of delivery and usability factors will be coded using a novel coding scheme adapted by Webb et al. (2010) and van Genugten (2016) [60, 61]. Two qualified coders (AT, EM) will independently code the behaviour change techniques described in the intervention and control conditions. Kappa and percentage disagreement will be calculated. Disagreements between reviewers will be discussed until resolved or with third party arbitration (BMG) if required.

For each included study the review authors (AT, BMG) will independently carry out a domain-specific assessment of risk of bias using the recommended Cochrane Collaboration’s tool for risk of bias assessment [54]. This will involve the classification of risk of bias in included studies as ‘low’, ‘unclear’ or ‘high’ risk of bias. If the authors (AT, BMG) disagree the final rating will be made by consensus with the third author (JE). The domains assessed will include:

Where necessary, we will contact the study authors to request missing data and/or data clarification. The quality of the data included in the review and the presence of any serious flaws will be reported.

If appropriate, we will use the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach to summarise the quality of evidence for each outcome at post-treatment and follow-up [54, 62, 63]. We will use GRADEprofiler (GRADEpro) to import data from Rev Man 5.3 to create Summary of Findings table(s) [54, 64, 65]. This will report outcome-specific information concerning the overall quality of evidence (risk of bias, inconsistency, imprecision and indirectness). Only the most important outcomes will be included in each ‘Summary of findings’ table. As per Fisher et al. (2015), the most important outcomes will be deemed those with the largest number of participants in each arm [38].

Sensitivity analysis based on methodological rigour and risk of bias will be carried out to determine the robustness of results. Studies deemed to be of high or unclear risk of bias across different domains will be systematically excluded then included, in order to assess differences in the overall effect estimates. If no significant differences exist, the studies will be included in the main analysis.

In order to synthesise data across studies, we will compute and report mean differences where identical scales are used to measure the same clinical outcome. Where different scales are used to measure the same clinical outcome, we will compute standardised mean differences (SMDs) (otherwise weighted mean differences). For dichotomous data, we will report odds ratios (ORs), 95 % confidence intervals (CIs) and number needed to treat to benefit (NNTB). For continuous data we will most likely report standardised mean differences and 95 % confidence intervals. There are a small number of studies in this area. We expect data to be sparse, event rates may be low or study size may be small therefore we will use Mantel-Haenszel methods in analyses of dichotomous data. We anticipate effect sizes will be similar but not identical across studies therefore a random-effects model will be used in analyses. Pain-related interference and pain intensity outcomes tend to be reported using primarily continuous data and studies which include headache conditions are likely to report pain symptoms using primarily dichotomous data. Chronic pain conditions will be categorised according to pain condition. In line with Fisher et al. (2015), data from studies reporting mixed pain conditions will be entered into all appropriate analyses. When studies use more than one measure for a given outcome, we will extract the most reliable or widely accepted. As per Eccleston et al. (2014) and Fisher et al. (2015), the timeframe allowed for collection of follow-up data will range from 3 to 12 months’ post treatment. If more than one-time point is available at follow-up, the latest data collection point will be extracted.

We will report rates of missing outcome data per arm and refer to the Cochrane risk of bias tool for missing outcome data in any evaluation of imputation methods. Finally, we address the potential impact of missing data on the findings of the review in the ‘Discussion’ section [54].

We anticipate unit of analysis issues such as repeated observations of the same outcome and studies including multiple intervention arms. For studies reporting repeated measurements of the same outcome, we will extract data at the following time points: baseline, post-treatment (not longer than 3 months post-randomisation) and follow-up (not longer than 12 months post-randomisation). For studies including more than two intervention groups, we will adhere to the recommended method suggested by the Cochrane Collaboration in section 16.5 for combining multiple groups from one study [54]. If cluster-randomised controlled trials are included, we will check for unit of analysis errors. Where possible, we will recalculate results using the appropriate unit of analysis (Higgins 2011). As per the Eccleston et al., (2012) protocol, all psychological intervention conditions will be labelled ‘treatment’ and all comparator conditions will be labelled ‘control’ conditions.

We will assess heterogeneity by calculating χ² and I² values for all outcome variables. Statistical heterogeneity will be considered substantial if I² values are above 50 %. We will also assess the impact of heterogeneity through sensitivity analyses and assume the appropriate random-effects or fixed-effect model in meta-analyses accordingly [54].

According to section 10.1 of the Cochrane Handbook, reporting biases arise when dissemination of findings is influenced by the nature and direction of results [54]. For this reason, we will, where possible, retrieve and compare the protocol for the included studies with the final reports.

The potential for small study effects such as publication bias will be assessed visually by inspection of funnel plots of estimated effects by standard error and using statistical tests which are in line with recent recommendations [66, 67]. Funnel plots will be assessed if ten or more studies are identified. The possible reasons for asymmetry will be investigated.

We will pool data using the Cochrane Collaboration’s Review Manager Software, RevMan 5.3 (RevMan 2014). A quantitative synthesis will be carried out only if the included studies are sufficiently homogenous in terms of quality, study design, participants, interventions, outcomes and type of analyses to provide a meaningful summary of effects. A narrative synthesis will be carried out if there is insufficient data to justify a formal meta-analysis. For continuous data, we will calculate and report standardised mean differences (SMDs) and 95 % confidence intervals (CIs). For dichotomous data, we will calculate and report odds ratios (ORs), 95 % confidence intervals (CIs) and number needed to treat to benefit (NNTB). In the event that data is sparse, we will use Mantel-Haenszel methods in analyses of dichotomous outcomes. Given the likely differences in interventions, comparators and participants we expect sufficient clinical heterogeneity that included studies will estimate different but related intervention effects. As some heterogeneity is inevitable we anticipate a random-effects model will be used in analyses.

In line with Little et al. (2015), a Pearson correlation (two-tailed) will be used to explore the relationship between the total number and frequency of different TDF domains coded and the effect size of the intervention for both the ICT-based interventions and the control conditions. For example, the number of different domains coded in the control group will be subtracted from the number of different domains coded in the intervention group. Sensitivity analysis will be used to investigate whether subtracting domains that appear in the control group impacts on the findings [58]. If there are no significant differences, data synthesis will be descriptive e.g. the proportion of studies that target specific domains will be identified.

If sufficient data are available, several subgroup analyses will be performed. The following factors will be examined in subgroup analyses to determine their effect on the response to a psychological intervention for paediatric chronic pain:

Of these subgroup analyses, modes of delivery and the extent of personalised contact with the therapist may be the most important because it remains unknown which ICT-based intervention types are most effective for paediatric chronic pain management and also how effective personalised contact with therapist (e.g. an e-coach) is in comparison with pure (e.g. no contact with therapist) self-led programmes.