Types of studies

All types of randomised controlled trials (RCTs) will be considered for inclusion.

Types of participants

Children, adolescents and adults of all ages with a clinical diagnosis of Crohn's disease, ulcerative colitis (with or without a total colectomy), or any other form of IBD (e.g. indeterminate colitis or IBD unclassified) will be considered for inclusion. Participants will be included regardless of whether disease status is active or in remission.

Types of interventions

Any pharmacological and non‐pharmacological interventions designed to help alleviate fatigue in individuals with IBD will be included. To be eligible for inclusion, an intervention must have a focus on fatigue explicitly stated in its aims, content, or as a primary or secondary outcome measure.

The following comparisons will be considered:

1. Pharmacological versus non‐pharmacological;

2. Pharmacological versus pharmacological (different drugs or same drugs with different doses and time intervals);

3. Pharmacological versus usual or standard care;

4. Non‐pharmacological versus usual or standard care;

5. Non‐pharmacological versus non‐pharmacological (different non‐pharmacological interventions or same non‐pharmacological intervention with different formats); or

6. Any of the above versus placebo.

Interventions may be delivered in any form, for example but not limited to, face to face, telephone, the internet, or technology in the case of non‐pharmacological interventions. Interventions may be delivered individually or be group focused and occur in different settings such as a clinic or home environment.

Types of outcome measures

Electronic searches

We will search MEDLINE, CINAHL, EMBASE and PsycINFO from inception to date. We will also search the Cochrane IBD Group Specialized Register and the Cochrane Central Register of Controlled trials (CENTRAL) for applicable RCTs. The search strategies will be modified for each database. Search limits will include humans and English only. The search strategies will use the relevant database filters or the recommended Cochrane search string for the identification of RCTs (Lefebvre 2011). The search strategies for each database are reported in Appendix 1, Appendix 2, Appendix 3, Appendix 4, Appendix 5 and Appendix 6. One author (DF) will liaise with the Cochrane IBD Group Trials Search Coordinator for the identification of potentially eligible studies.

Searching other resources

To identify other relevant published, unpublished and ongoing trials we will:

1. Examine the reference lists of included studies and review articles for additional citations;

2. Search ongoing trials and research registers including the Current Controlled Trials register (www.controlled‐trials.com), ClinicalTrials.gov (www.clinicaltrials.gov) and the WHO International Clinical Trials Registry Platform (ICTRP) (www.who.int/ictrp/en/), using the search terms ’fatigue’ and 'inflammatory bowel disease’ or ‘ulcerative colitis’ or ‘Crohn’s disease’;

3. Contact trial authors, known specialists in the field and pharmaceutical companies to identify further published and unpublished trials and ask if they are willing to disclose their unpublished data; and

4. Search published abstracts from conference proceedings, including the European Crohn’s and Colitis Organisation Congress, Digestive Disease Week and Advances in Inflammatory Bowel Diseases.

Selection of studies

Initially, two review authors (DF, MA) will independently screen titles and abstracts identified by the search and exclude those studies that are obviously not relevant to the review. The remaining titles and abstracts will be independently examined for eligibility by two review authors (DF, ES) based on the predetermined inclusion criteria described above. Full text papers will be retrieved for all studies appearing to meet the inclusion criteria and will be read independently by two review authors (DF, ES). We will only include trials with a heterogeneous sample of disorders,if relevant data from participants with IBD can be extracted. We will contact study authors where information is unclear or missing in order to reach a decision about inclusion. Disagreement about the selection of a study will be resolved by consensus. In the event a consensus cannot reached, arbitration will be sought from a third author (CN).

Data extraction and management

For each included study, two review authors will independently extract and document the relevant data using standardised data extraction forms. The lead author (DF) will extract data for all included trials. Second independent extraction of data from included trials will be shared between three review authors (WCD or LPJJ or MA). If necessary, study authors will be contacted to provide additional (unpublished) relevant information. We will resolve any disagreements by consensus including discussion with two additional authors (ES and CN). We will gather data on the following and document in both data extraction forms and Review Manager 5:

Study

• Study aim

Participant characteristics

• Number of participants

• Setting of study

• Country of origin

• Demographic characteristics such as age and gender

• Disease characteristics such as disease type, disease status and treatment type

• Inclusion and exclusion criteria for participation in the study

Intervention characteristics

For each arm:·

• Assignment to groups·

• The aim, type, mode and content of the intervention·

• Time points of delivery ·

• Duration of the intervention, number and duration of sessions/dose

• Providers of the intervention

• Comparison intervention/s

• Setting of the intervention

• Participant adherence

Outcomes

• Time, frequency and duration at which outcomes are measured

• Instruments used for key primary and secondary outcomes

• Adverse events

Others

• Funding

• Declaration of interest

• Sample size and evidence of power calculation statistical analysis.

• Follow up – withdrawal/dropout

Assessment of risk of bias in included studies

For each study, the authors who extracted the data from the included studies will also independently assess methodological quality using the Cochrane risk of bias tool (Higgins 2011a). We will assess trials for random sequence generation, allocation concealment, blinding (participants, personnel and outcome assessors), incomplete outcome data, outcome misclassification, selective outcome reporting and other potential sources of bias. We will then make a judgment on each of these criteria relating to the risk of bias, of ’low risk of bias’, ’high risk of bias’ or ’unclear risk of bias’.

We will use the GRADE criteria (risk of bias, inconsistency, imprecision, indirectness and publication bias) to assess the overall quality of evidence for the prespecified primary and secondary outcomes (Schünemann 2011a; Schünemann 2011b). All decisions to downgrade or upgrade the quality of the evidence will be explained using footnotes.

If agreement cannot be achieved by the two review authors (DF and WCD or LPJJ or MA) through discussion, another two other review authors (ES and CN) will provide consensus assessment.

Using the GRADEpro software, we will create a ‘Summary of findings’ table for the following outcomes:

• Fatigue;

• Quality of life; and

• Adverse events.

Measures of treatment effect

We will use the Cochrane Collaboration’s Review Manager Software, RevMan 5, for all analyses. Outcomes will be recorded both at the end of the intervention period and at the end of the follow‐up for the purpose of comparison between the intervention and control groups. We will calculate the mean difference (MD) and the corresponding 95% confidence interval (CI) for continuous outcomes. We will calculate the risk ratio (RR) and 95% CI for dichotomous outcomes (e.g. fatigue or no fatigue). We will calculate the number needed to treat for an additional beneficial outcome (NNTB) where appropriate.

Unit of analysis issues

The level at which randomisation occurs will be accounted for in the data analysis. We expect that participants will be individually randomised to one of two groups, where the unit of analysis will be the individual.

Where groups of individuals are randomised together to the same intervention (i.e. cluster‐randomised trials), the group will be the unit of analysis. Group level interventions are often analysed and reported at an individual rather than a group level, or without adjusting for group effect. Authors will be contacted for further information if these group data are not reported.

Where individuals undergo more than one intervention during the period of the study (i.e. in a cross‐over trial), an assessment of the suitability of this method for the condition and intervention in question and the likelihood of serious carry‐over will be addressed. If neither carry‐over nor period effects are an issue, we will follow the methods of analysis for cross‐over trials as recommended in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b).

We will follow the recommendations outlined in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions for studies where events may reoccur, studies where there are multiple treatment attempts, and studies where there are multiple intervention groups or repeated observations on participants (Higgins 2011b).

Dealing with missing data

Where data are missing, we will contact the trial authors and request the missing data. If this information is unattainable, an available case analysis will be undertaken by analysing only the available data (i.e. ignoring the missing data). If change scores are not available and the mean change can be calculated, standard deviations will be imputed from baseline data using methods recommended in Chapter 16 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011b). If the number of patients randomised to each group and the number of drop outs are known, a worst case intention‐to‐treat (ITT) analysis, whereby all drop outs are assumed to be treatment failures, will be calculated.

Assessment of heterogeneity

The studies will be assessed for clinical homogeneity with regards to participants, interventions, and outcomes. A meta‐analysis would not be appropriate for studies judged to be clinically heterogeneous. We plan to assess heterogeneity as follows.

1. We will review the results of the Chi² test to determine if the heterogeneity is statistically significant. A P value of 0.10 will be considered statistically significant.

2. If the Chi² test indicates statistically significant heterogeneity, we will quantify the heterogeneity across studies by reporting the I² results. An I² value of 25% represents low heterogeneity, 50% represents moderate heterogeneity and 75% represents high heterogeneity.

3. If there is significant heterogeneity, the forest plot will be visually inspected and a sensitivity analysis performed, excluding any obvious outliers, to assess if this explains the heterogeneity. For example, if the original pooled analysis had an I² value of 68% and after the outlier study (or studies) was excluded the I² value changed to 22%. If the sensitivity analysis appears to explain the heterogeneity, the outlier study (or studies) will be examined to determine if it differs from the other studies in the pooled analysis, in a way that could explain the heterogeneity. For example, the outlier study may include participants with both active and quiescent disease, while the other studies in the pooled analysis enrolled patients with quiescent disease only.

4. Finally if heterogeneity is suspected, the possibility of utilising a random‐effects model of meta‐analysis will be considered as recommended in Chapter 9 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011).

Assessment of reporting biases

All studies will be assessed for reporting bias. If reporting bias is suspected, we will attempt to contact trial authors and request missing outcome data. For example, results for pre‐specified outcomes that were not reported in the paper. Alternatively, if this information is unattainable and there are an appropriate number of studies in the pooled analysis (i.e. > 10 studies), we will explore potential publication bias by testing for funnel plot asymmetry (Sterne 2011).

Data synthesis

Where appropriate, the data from included studies will be combined in a meta‐analysis. Data will be pooled when patients, interventions and outcomes are sufficiently similar, which will be determined by consensus. We will pool statistically homogeneous studies (I² < 50%) using a fixed‐effect model. We will pool statistically heterogeneous (I² ≥ 50%) studies using a random‐effects model. Data will not be pooled if there is a high degree of statistical heterogeneity (I² > 75%). For continuous outcomes, we will calculate the pooled mean difference (MD) and corresponding 95% confidence interval (CI). Where different scales are used to measure the same underlying construct, we will calculate the standardised mean difference (SMD) and corresponding 95% CI. Continuous data will be combined only where (i) means and standard deviations are available or calculable and (ii) there is no clear evidence of a skewed distribution (Deeks 2011). For dichotomous outcomes, we will calculate the pooled RR and corresponding 95% CI. According to Cohen 1977, we will classify effect sizes into small (< 0.2), medium (0.2 to 0.8) and large (> 0.8).

Subgroup analysis and investigation of heterogeneity

If sufficient power and data are available, subgroup analysis will be performed for the following subsets: disease type (Crohn’s disease, ulcerative colitis); disease activity (active disease, inactive disease), sex (male, female); age groups (child, adolescents, adults, elderly), co‐morbidities, and intervention type (pharmacological non‐pharmacological). All review authors will be involved in interpreting the analyses. We will restrict subgroup analyses to looking at effects of subgroups on the primary outcome.

Sensitivity analysis

Sensitivity analysis will be performed, where appropriate, to explore the effects of risk of bias. Studies identified as high risk of bias will be excluded from the pooled analysis to see if the effect estimate changes in a substantive way. If no substantive difference exists, the studies with a high risk of bias will be included in the main analysis. For allocation concealment, we intend to re‐analyse the data including only those trials with adequate concealment of allocation. Finally for blinding of outcome assessment, trials with double blinding of outcome assessment will be included in a re‐analysis, due to the subjective nature of fatigue. Sensitivity analysis will be conducted for the primary outcome only. We will also compare the results of any 'available case' analysis with a worst case ITT analysis to see if the effect estimate changes.