Study designs.

Studies included will be randomised controlled trials (RCTs), non-randomised controlled trials, and observational studies (before and after studies) that have evaluated an intervention to manage fatigue. Due to the multifactorial nature of fatigue and its wide impact upon the lives of people living with CKD, qualitative evaluations of relevant interventions will also be included. Qualitative studies which focus only on the experience of fatigue, without reference to the effects of an intervention, and which do not focus upon the perspective of people living with CKD, or where these perspectives cannot be isolated from other interest-holders (e.g., in mixed focus groups) will be excluded. Literature reviews, editorials, and commentaries will all be excluded, but their reference lists will be reviewed for potentially relevant publications. Relevant conference abstracts will be included where they provide sufficient data for synthesis. No restriction will be placed on year of publication or minimum follow-up period.

Participants.

Due to the wide-ranging impacts of fatigue across all CKD stages, we will include all adults and children who are diagnosed with:

1. (1) CKD stages G3A-G5 (eGFR < 60); OR
2. (2) On dialysis (HD or PD); OR
3. (3) Kidney transplant recipients; OR
4. (4) End-stage kidney disease (ESKD) OR
5. (5) Post-dialysis withdrawal OR
6. (6) Being conservatively managed (full active treatment without KRT)

Studies involving animals will be excluded.

Interventions.

Included interventions include both pharmacological and non-pharmacological interventions for fatigue management. Given the absence of a universally accepted definition of fatigue, we will adopt an inclusive approach to study selection. Eligible studies will include those that (i) explicitly define fatigue, (ii) employ a recognised fatigue-specific outcome measure, or (iii) report fatigue as a subscale within a broader construct (e.g., health-related quality of life). This approach is intended to capture interventions that, although not explicitly designed to target fatigue, may nonetheless exert secondary effects on it (e.g., exercise-based interventions). By doing so, we aim to enhance the comprehensiveness and relevance of the synthesis.

Comparators.

For RCTs and non-randomised controlled studies, comparators will include usual care and other interventions, as the latter may contribute to the relative effect estimates within a network meta-analysis. Control groups that receive usual care plus a sham intervention or a placebo (for pharmacological interventions) will also be included.

Outcomes.

The primary outcome of interest will be the effectiveness of pharmacological and non-pharmacological interventions for reducing fatigue. Fatigue will be using patient-reported outcomes which directly measure fatigue (e.g., the Chalder Fatigue Scale) or include a fatigue subscale as part of a measure assessing a broader construct. Fatigue has been selected as the primary outcome due to the focus of the review, but also because it is consistently identified as one of the most important outcomes for people living with CKD across a range of age groups, disease stages and conditions [23–28].

To address conceptual heterogeneity in fatigue measurement, outcome measures will be prioritised using a predefined hierarchy. Primary focus will be given to validated fatigue-specific outcome measures. Fatigue subscales derived from multidimensional symptom or quality-of-life instruments will be secondary. Where multidimensional outcomes are used, only fatigue-specific subscales will be extracted. Where conceptually justified, different fatigue domains will be analysed separately.

Furthermore, in view of the heterogeneity of fatigue syndrome across chronic kidney disease cohorts, the primary outcome will be reported separately for four groups: patients undergoing dialysis, non-dialysis patients (including those in pre-dialysis stages), kidney transplant recipients, and individuals with CKD receiving conservative management and for adults and children. The primary outcome will likewise be analysed separately according to categories of pharmacological and non-pharmacological interventions.

Where addressing fatigue is the primary focus of the intervention secondary outcomes include:

• Fatigue measured using outcomes which are not patient-reported;
• Health-related quality of life;
• Mental health (e.g., depression and anxiety);
• Sleep quality;
• Withdrawal from treatment;
• Physical function and mobility;
• Cognitive function;
• Life participation;
• All-cause mortality;
• Cardiovascular mortality

Adverse events / safety outcomes of interventions in people living with CKD will also be included, including (but not limited to) worsening of fatigue.

All secondary analyses will also be stratified by CKD stage, as per the primary outcome, and by age group (adult/child).

Recognising the multidimensional nature of fatigue, we will also examine the perspectives of individuals with CKD on how interventions affect their fatigue, as certain impacts may not be fully captured by conventional objective or patient-reported outcome measures.

Timepoints.

Outcomes will be extracted at all available time points to allow for immediate and long-term effects of interventions to be examined where possible.

Setting.

All relevant healthcare settings (hospitals, outpatient clinics, dialysis centres, community and home settings, and hospices).

Language.

Non-English trials or studies deemed relevant at the title and abstract screening stage will be included. Decisions about these reports will be made on a case-by-case basis at the full-text screening stage.

Quantitative studies.

We will use the NIH Study Quality Assessment Tools to assess the risk of bias for each study [32]. Each study will be classified using the following criteria: (a) “good” (the study is judged to be at the least risk of bias for all domains, and results are considered to be valid); (b) “fair” (the study is judged to be susceptible to some bias but deemed not sufficient to invalidate its results), and (c) “poor” (the study is judged to be at significant risk of bias in a way that substantially lowers confidence in the results). Each risk of bias judgement will be accompanied by a clear rationale, allowing transparency and future replication of the review process. This documentation will be made available in the supplementary materials to provide context for each decision.

To ensure the validity and reliability of our findings, two independent reviewers will assess the risk of bias for each included quantitative study. Any discrepancies between the two reviewers over the risk of bias will be resolved with the inclusion of a third reviewer. Calibration exercises will be conducted before the review to ensure consistency between reviewers in applying the risk of bias tools.

Qualitative studies.

We will use the Joanna Briggs Institute (JBI) Critical Appraisal Checklist for Qualitative Research to assess the methodological strengths and limitations of the qualitative studies included [33]. The JBI tool is comprised of ten items and is widely used and has evaluates most concepts relating to methodological rigour in qualitative research [34]. The items within the checklist will not be scored, and the checklist will not be used to exclude studies based on quality. Instead, we will provide a narrative summary of studies by item to facilitate an overall assessment of methodological rigour and quality. As for the quantitative studies, two independent reviewers will apply the JBI tool for each included qualitative study, with recourse to a third in the event of any disagreements.

Mixed methods studies will be subject to both the NIH and the JBI tool for their quantitative and qualitative components.

Quantitative studies.

Where appropriate, data from randomised controlled trials using comparable outcomes will be pooled in meta-analyses with a Frequentist framework. If there is a limited scope to undertake a meta-analysis, due to a small amount of existing trials with a range of different outcomes measured reported, we will create narrative synthesis of the findings using published guidance on synthesis without meta-analysis [35]. Data from non-randomised and observational studies will be pooled and synthesised separately in an exploratory analysis.

Data analyses will be conducted in Stata (StataCorp. 2023. Stata Statistical Software: Release 18. College Station, TX: StataCorp LLC.). Where the same measure is used to assess the same outcome, intervention effects will be summarised as mean differences. Where different measures are used to assess the same outcome, intervention effects will be summarised as standardised mean differences (SMD) (using Hedge’s adjusted g) for the primary outcome measure.

If studies are sufficiently homogeneous in design, comparators, and outcome measures, we will conduct pairwise and network meta-analyses to estimate the relative intervention effects and their corresponding 95% confidence intervals. We will first conduct pairwise meta-analyses using a generic inverse variance random-effects model to compare individual interventions against control.

If there are sufficient included trials to perform network meta-analysis, we will then conduct a random-effects network meta-analyses to identify the most efficacious pharmacological and non-pharmacological interventions for fatigue management. Interventions that combine multiple approaches will be classified as distinct interventions within the analysis. Multi-arm studies will be accounted for by reweighting all comparisons of each multi-arm study [36]. Results from the network-meta-analyses will be presented as summary relative effects (MD or SMD) for every pair of interventions. Ranking probabilities for all interventions of being at each possible rank for each outcome will be estimated. We will obtain an intervention hierarchy using surface under the cumulative ranking curve (SUCRA) and mean ranks [37]. Inconsistency models will be used to evaluate the assumption of global consistency across the network. The separating indirect from direct evidence (SIDE) approach will be used to assess local consistency [37].

The validity of indirect comparisons relies on the transitivity assumption. Although variations in study populations (CKD stage) and intervention characteristics are anticipated, the included treatments will share similar therapeutic objectives. Therefore, it is considered plausible that relative treatment effects remain comparable across studies.

Important clinical and methodological characteristics that may be effect modifiers (including but not limited to demographics, CKD stage, intervention intensity, and study design) will be examined across comparisons. Where substantial heterogeneity is identified, subgroup analyses or meta-regression will be conducted where feasible. If, after these explorations, unexplained heterogeneity remains that undermines the assumptions of consistency and transitivity, the NMA results will not be reported. Transitivity will be assessed by comparing the distribution of effect modifiers across treatment comparisons. In cases of disconnected networks, analyses will focus on the largest connected network or be conducted separately for each network. Results will be interpreted with appropriate caution.

Unit of analysis.

The unit of analysis will be the participant. If cluster randomised trials are identified, then analysis will be at the level of the individual while accounting for the clustering in the data (using the “design effect” in line with the Cochrane Handbook). To calculate the design effect, the following data will be used: Number of cluster per intervention group; total number of participants per intervention group; outcome data (e.g., number of people who complete) and an estimate of the intracluster correlation coefficient (ICC). If the ICC is not reported, then it will be estimated from similar trials.

Assessment of heterogeneity.

To evaluate the presence of clinical heterogeneity, descriptive statistics for study and study population characteristics will be compared across the included studies within each pairwise comparison.

For the pairwise meta-analyses, statistical heterogeneity will be quantified using the I² statistic. I² values will be interpreted alongside the estimates of the between-study variance (tau-squared). For network meta-analysis, the model will assume a common estimate for the between-study variance (tau-squared).

If heterogeneity is identified, potential causes will be explored (e.g., clinical and/or methodological diversity) through subgroup analyses or meta-regression for pre-specified variables. Potential sources of heterogeneity that will be considered include population characteristics (e.g.,CKD stage, renal replacement therapy status, co-morbidities), treatment characteristics, study design or risk of bias (allocation concealment, blinding, attrition), duration of follow-up, date of publication.

Analysis of subgroups.

If possible, two subgroup analyses will be performed, one to explore the efficacy of interventions in different CKD cohorts (e.g., HD, PD, renal transplantation, CKM, and post-dialysis withdrawal) and the other to explore the efficacy of interventions on different types of fatigue – for example are some interventions more effective at addressing physical fatigue rather than mental or cognitive fatigue.

Sensitivity analysis.

We will conduct sensitivity analyses to explore the impact of bias by excluding studies judged to be at high risk of bias. To evaluate the influence of measurement heterogeneity, a further sensitivity analyses will be conducted by stratifying studies according to instrument type:

• Fatigue-specific validated instruments
• Fatigue subscales from multidimensional instruments

Assessment of publication bias.

If we can pool more than 10 studies in a meta-analysis, we will create and examine a funnel plot to explore possible small-trial and publication biases. Egger’s test will also be employed to quantify the bias.

Confidence in cumulative estimates.

Two reviewers will independently undertake an assessment of the certainty and confidence in evidence from the quantitative syntheses of the primary outcome, with recourse to a third to resolve any discrepancies as needed [38].

We will use Cochrane’s GRADE approach (Grading of Recommendations Assessment, Development and Evaluation) [38] to judge the available evidence and categorise them into four levels of certainty by outcome: High, moderate, low, and very low. Five domains will be considered during the assessment process, which include: Risk of bias, inconsistency, indirectness, imprecision, and publication bias. Assessment of indirectness will include consideration of the representativeness of the study samples from the perspective of equality, diversity and inclusion.

Qualitative evidence synthesis.

To synthesise qualitative findings, we will use the approach described by Thomas and Harden et al. (2008) [29]. Briefly, synthesis will follow three iterative stages: 1. line-by-line coding of the findings of primary studies; 2. The construction of descriptive themes which will be used to organise these initial codes and; 3. the development of ‘analytical’ themes which go beyond the descriptive themes to specifically address the review questions. This final stage will be conducted independently by two reviewers, before discussing, revising and agreeing these analytical themes, with recourse to the wider review team as required [29]. The synthesis process will be facilitated by NVivo (QSR International Ltd 2022, Version 20).

Integration of quantitative evidence and qualitative evidence.

To integrate quantitative and qualitative evidence we will adopt a convergent segregated approach [39]. The separate quantitative and qualitative syntheses will be combined into a second level synthesis. Because the qualitative data extraction focuses on the perceived effectiveness of interventions which address fatigue from the perspective of people living with CKD, we anticipate that this integrated synthesis will only focus on results relating to the effectiveness of these treatments. A joint display will be used to combine the findings in a tabulated form. This display will be used to assess the ways in which the data sets agree (confirmed), complement (offered an expanded explanation) or contradict each other and outline how the qualitative results expand and contextualise the key results from the quantitative results [39,40].

Review status and timelines.

Information sources were searched and results uploaded to Covidence for screening in July 2025. We anticipate that record screening will be completed in January 2025, and the results of the review are expected in July 2026.