PROTOCOL: Effects of Rehabilitation and Behavioural Interventions for Post-stroke Cognitive Impairment on Quality of Life: Protocol for a Systematic Review of Randomised Controlled Trials

Abstract

This protocol is for a Campbell systematic review. The objectives are as follows: to determine the effects of rehabilitation and behavioural interventions for post-stroke cognitive impairment on quality of life.

Background

Stroke survival has improved globally; however, stroke is one of the leading causes of long-term disability among adults, with over 60 million disability-adjusted life years (DALYs) in 2021 (Feigin et al., 2024, 2025). Post-stroke cognitive impairment (PSCI) is a common disability of stroke and affects approximately 60% of stroke survivors globally (El Husseini et al., 2023; Mtambo et al., 2025). PSCI broadly refers to cognitive impairment identified following stroke, whether arising after stroke or reflecting worsening of pre-existing cognitive impairment, regardless of cause (Quinn et al., 2021). PSCI notably increases carer needs and affects survivors’ quality of life (QOL), requiring effective interventions to improve outcomes (Stolwyk et al., 2024).

QOL is a multidimensional concept encompassing individuals’ perceptions of their position in life within their cultural context and value systems (The Whoqol Group, 1998). PSCI may compromise physical functioning, psychological well-being, social participation, environmental aspects, and overall life satisfaction, challenging adaptation processes (Stolwyk et al., 2024). Research on PSCI management has included alternative, behavioural, complementary, neuromodulation, pharmacological, rehabilitation, and traditional approaches. Rehabilitation and behavioural interventions (RBIs) are commonly used because they can be tailored to individual needs and align with the multidimensional approach required to optimise functional outcomes post-stroke (Li et al., 2026). Rehabilitation is a range of interventions designed to optimise functioning and minimise disability in individuals with health conditions within their environments (World Health Organization, 2024). Meanwhile, behavioural interventions are strategies designed to influence individuals’ health-related actions (Cutler, 2004). RBIs have synergistic effects, as functional recovery inherently incorporates behavioural components that modify habits, motivation, and healthy coping strategies. These further enhance engagement with treatment and support continued healthy lifestyle changes aimed at continued improvements of conditions. These practical approaches can be embedded in survivors’ daily lives through primary care and community initiatives that support long-term recovery, making them applicable in all settings, including low-resourced settings (LRSs).

RBIs also rely on self-management strategies, which may be more practical for long-term health outcomes and warrant a deeper understanding of their role in PSCI recovery. Evidence indicates that RBIs improve cognitive function in stroke survivors (Liu et al., 2024); however, the effects of RBIs for PSCI on QOL and their safety are unclear. A clearer understanding of the relationship between RBIs for PSCI on QOL outcomes is needed to support community-based rehabilitation and behavioural strategies, as well as future PSCI research. Synthesising evidence from randomised controlled trials (RCTs) on RBIs for PSCI and their associated QOL outcomes may be a practical way to address this gap.

The Interventions

We focus on rehabilitation and behavioural interventions (RBIs) as a subset of non-pharmacological interventions. We define RBIs as integrated strategies that aim to optimise functioning by targeting body functions, activities, participation, and health-related behaviours. RBIs are a reviewer-defined operational term; hence, unclear or overlapping interventions will be classified on a case-by-case basis. Eligibility will be determined according to the intervention’s stated therapeutic aim, principal active therapeutic component, and hypothesised mechanism of action as described by the study authors. Eligible RBIs will be classified into four clinically meaningful categories: cognitive rehabilitation interventions, exercise-based interventions, nutritional and lifestyle interventions, and psychosocial interventions. Classification will be based on the intervention’s primary active therapeutic component, defined as the component expected to produce the principal treatment effect, as described by the study authors and judged by reviewers. Where interventions comprise multiple components, classification will be based on the dominant active therapeutic component. If no dominant component can be identified, the intervention will be classified according to its overarching therapeutic approach and reported as a multicomponent intervention during synthesis.

Cognitive rehabilitation interventions include structured programmes such as cognitive training, memory retraining, and domain-specific therapies that aim to improve cognitive function through practice and compensatory strategies. These may be delivered by interdisciplinary teams of healthcare professionals (HCPs) or adapted for home-based use, including technology-assisted formats such as virtual reality (VR). Additionally, augmented reality (AR), computerised training, tele-rehabilitation, and artificial intelligence (AI)-supported tools may also be used. Exercise-based interventions include aerobic, resistance, and balance training delivered in clinical, community, or home settings, either in-person or via telehealth methods. They are delivered by HCPs or trained carers, with some interventions AI-supported and often delivered over extended periods. Nutritional and lifestyle interventions include dietary modifications such as the Dietary Approaches to Stop Hypertension (DASH) and the Mediterranean–DASH Intervention for Neurodegenerative Delay (MIND) diets. Others include specific nutritional supplementation and behavioural changes such as smoking and vaping cessation, sleep hygiene, and alcohol reduction, typically delivered by HCPs, carers or AI-supported over an extended period. Psychosocial interventions target the emotional and social determinants of recovery, including cognitive-behavioural therapy (CBT). These also include mindfulness and social support programmes, delivered individually or in groups by HCPs, including AI-assisted, in clinical, community, or home settings; in-person or using telehealth methods. Overall, interventions vary by type, delivery mode, provider, and duration, and may be single or combination therapy.

How the Interventions Might Work

Theoretical Underpinnings

It is hypothesised that, as PSCI is associated with reduced QOL, interventions that improve cognitive function may improve QOL. Cognitive rehabilitation is based on neuroplasticity, behavioural, and cognitive reserve theories, aiming to restore or compensate for impairments in cognitive processes such as attention, memory, and executive function. Exercise-based interventions suggest that increased cerebral blood flow and neurotrophic factors, such as brain-derived neurotrophic factor (BDNF) and vascular endothelial growth factor (VEGF), support neurogenesis and cognitive recovery.

Nutritional and lifestyle interventions are based on theories of vascular, oxidative stress, and the gut–brain axis, focusing on modifiable risk factors that influence brain health and cognitive decline. Psychosocial interventions are grounded in cognitive-behavioural and social-cognitive theories and target emotional regulation. These interventions further work by reducing stress and increasing motivation and engagement in rehabilitation, which may, in turn, indirectly enhance cognitive outcomes. Table 1 presents a logic model linking intervention components, mechanisms, immediate outcomes, and long-term outcomes.

Table 1.

The Logic Model of Connections Between the Intervention and Outcomes

Intervention	Pathways	Short-term outcomes	Long-term outcomes
Cognitive rehabilitation	↑ synaptic plasticity; ↑ compensatory strategy use; ↑ attention and executive control; ↑environmental adaptation; ↑ task generalisation	↑ task-specific performance; ↑ strategy adoption; ↑ cognitive efficiency	Improved cognitive function; ↑ independence in ADLs/IADLs; ↑ QOL
Exercise-based	↑ BDNF and VEGF; ↑ cerebral perfusion; ↓ systemic inflammation; ↑ cardiovascular fitness; ↑ insulin sensitivity	↑ neurogenesis; ↑ functional connectivity; ↑ physical function	Improved cognitive function; ↓ vascular risk; ↑ functional independence; ↑ QOL
Nutritional and lifestyle	↑ antioxidant capacity; ↑ vascular function ↓ metabolic and vascular risk; ↓ oxidative stress; ↓ neuroinflammation	Improved metabolic health; improved endothelial function; ↑ vascular regulation	↓ stroke recurrence risk; ↓ vascular risk; ↑ cognitive resilience; ↓ cognitive decline; ↑participation; ↑ QOL
Psychosocial	↑ social support; ↑ positive stress management; ↑ self-efficacy; ↑ cognitive stimulation; ↑ behavioural activation; ↓ social isolation	↑ engagement in rehabilitation; ↑ motivation; ↓ psychological distress	Improved cognitive engagement; improved participation; ↑ QOL

Note. ↑ increase; ↓ decrease; ADLs = activities of daily living; IADLs = instrumental activities of daily living; BDNF = brain-derived neurotrophic factor; VEGF = vascular endothelial growth factor.

Why is it Important to do This Review?

There are numerous completed RCTs, umbrella reviews, narrative reviews, systematic reviews, and meta-analyses on interventions for PSCI, attached as Appendix 1. Additionally, ongoing trials are investigating a brain-computer interface (BCI)-based cognitive training program (Niu et al., 2026), and a sequence of transcranial direct current stimulation (tDCS) combined with computerised cognitive training on PSCI (Wei et al., 2026). Other ongoing RCTs are on home-based computerised adaptive cognitive training (Soni et al., 2025) and acupuncture for PSCI (Cheng et al., 2025). Furthermore, a recent review indicated that Baduanjin exercise ranked highest, followed by tDCS, for improving cognitive function in stroke survivors, but QOL outcomes were not explicitly assessed (Li et al., 2026). A further review reported that robot-assisted rehabilitation may improve general cognition and executive function in post-stroke patients, but QOL was not explicitly assessed (Qiu et al., 2026). Lastly, a recent review by Teng et al. (2026) identified QOL as an outcome, but only cognitive outcomes were reported in detail. Rehabilitation aims to restore and support individuals in achieving optimal physical, psychological, and social functioning within their environments (World Health Organization, 2024). Meanwhile, behaviour change is central to the successful engagement in rehabilitation and to sustaining long-term healthy lifestyle practices among survivors. PSCI interacts with QOL domains; hence, QOL outcomes should be considered when evaluating management strategies (Stolwyk et al., 2024). This review aims to address this gap by synthesising RCTs to examine the effects of RBIs for PSCI and QOL. The findings may inform policies for community-based rehabilitation practice and future research, and support decision-making for interest holders involved in PSCI management, including those in LRSs.

Review Questions

This review will aim to answer the following overarching question:

What are the effects of rehabilitation and behavioural interventions for post-stroke cognitive impairment on quality of life in randomised controlled trials?

Additionally, where evidence is sufficient, the review will aim to answer the following sub-questions:

• (1) How do rehabilitation and behavioural interventions’ characteristics, including intervention subtype, intervention structure (single-component vs multi-component/combination therapy), initiation time and total intervention dose influence the effects of rehabilitation and behavioural interventions for post-stroke cognitive impairment on quality of life?

• (2) What adverse events are associated with rehabilitation and behavioural interventions for post-stroke cognitive impairment on quality-of-life outcomes?

Objectives of the Review

The main objective of this review is to determine the effects of rehabilitation and behavioural interventions for post-stroke cognitive impairment on quality of life using evidence from randomised controlled trials.

Additionally, where sufficient evidence exists, the following sub-objectives will support addressing the previously stated sub-questions:

• (1) To examine whether characteristics of rehabilitation and behavioural interventions for post-stroke cognitive impairment, including intervention subtype, intervention structure, timing of initiation and total intervention dose, influence their effects on quality-of-life outcomes.

• (2) To identify the adverse events reported in studies evaluating the effects of rehabilitation and behavioural interventions for post-stroke cognitive impairment on quality of life.

Methods

This protocol follows the Methodological Expectations of Campbell Collaboration Intervention Reviews (MECCIR) guidelines (Aloe et al., 2024); Appendix 4 is the completed checklist. We also considered the Preferred Reporting Items for Systematic Reviews and Meta-Analyses-protocol (PRISMA-P) (Moher et al., 2015), the PRISMA search guidelines (Rethlefsen et al., 2021), and consulted the Cochrane Handbook (Higgins et al., 2024).

Criteria for Considering Studies for This Review

Types of Studies

Only RCTs, including pragmatic and explanatory trials, from any setting that report on both cognitive function and QOL will be included. RCTs provide the strongest control for threats to internal validity and may generate credible evidence to address the review questions (Higgins et al., 2024). Eligible studies must report both cognitive and QOL outcomes measured at follow-up, as post-intervention scores, change-from-baseline scores, or other effect estimates comparing intervention and control groups. PSCI is associated with reduced QOL, and interventions that affect cognitive function may also affect QOL. However, how changes in cognitive function translate to changes in QOL are unclear, and studies that report both outcomes are needed to address this gap. The review will include individually randomised and cluster-randomised controlled trials using parallel-group, crossover, or factorial designs, with no restriction on the number of intervention arms. Cluster RCTs are particularly appropriate when the intervention is delivered at the service or facility level, where individual randomisation is impractical and increases the risk of contamination (Slenders et al., 2025). For crossover trials, only data from the first treatment period will be included, where carryover effects cannot be excluded. All other study designs will be excluded because they are less likely to have control for threats to the internal validity of findings.

Types of Participants

Participants must be confirmed stroke survivors as defined by the World Health Organisation (WHO) (Coupland et al., 2017), and aged 18 years or older. In this review, PSCI is defined as cognitive deficits identified after stroke, ranging from mild cognitive impairment to dementia, irrespective of its presumed aetiology (El Husseini et al., 2023; Quinn et al., 2021). Participants will be included regardless of their pre-stroke cognitive status or prior management of cognitive impairment, because this information may not be reliably collected from trial publications. Transient ischaemic attack survivors, cognitive deficits due to other cerebrovascular diseases and participants with mixed dementia will be excluded. Studies that include both eligible and ineligible participants will be included only if data for eligible participants can be extracted separately. Where necessary, authors will be contacted to obtain disaggregated data and given 30 days to respond. Survivors will be included regardless of stroke severity or duration; interventions initiated within 0–6 months post-stroke will be classified as early PSCI interventions, and those initiated after 6 months will be classified as late PSCI interventions.

Types of Interventions

We will include RBIs, categorised into the four previously stated categories. For session-based interventions, total planned doses will be calculated and expressed in hours as the primary measure of intervention dose. Overall programme duration will be recorded in weeks to indicate how the intervention was distributed over time. For each eligible comparison, the intervention being evaluated will be referred to as the intervention under investigation (IUI), and the alternative condition will be referred to as the comparator. In parallel-group trials, participants allocated to these conditions will constitute the intervention and comparator groups, respectively. In crossover trials, they will be referred to as the intervention and comparator periods and defined separately for multi-arm and factorial trials.

Comparison Groups

All comparator types will be eligible except for historical comparators, as this review is restricted to RCTs. Comparator conditions will be classified as inactive or active based on their reported content. Inactive comparators will be defined as conditions that contain no therapeutic components intended to improve cognition or QOL, such as no intervention, waitlist, usual/standard care, minimal intervention, placebo or sham intervention, attention control, and education-only control. Active comparators will be defined as alternative interventions containing therapeutic components intended to improve cognition or QOL. The primary synthesis will compare RBIs with inactive comparators, and comparisons against active comparators will be synthesised and presented separately. For each eligible comparison, the effect estimate will compare outcomes between participants receiving the IUI and those receiving the designated comparator.

Multi-component or combined therapy RCTs, defined as interventions comprising two or more distinct components delivered together (Özbe et al., 2019), will be included if compared with eligible comparator groups. All RBIs delivered concurrently will be analysed as a single package, where individual effects cannot be disentangled. Components will be described and, where possible, explored in subgroup analyses; however, studies will be excluded where non-RBI and RBI components cannot be separated. In multi-arm RCTs, only arms meeting the intervention or comparator eligibility criteria will be included. Sufficiently similar eligible arms will be combined; otherwise, shared comparator groups will be divided across relevant comparisons to avoid double-counting, in accordance with Higgins et al. (2024).

Types of Outcome Measures

The primary outcome is QOL, measured using validated stroke-specific, health-focused, or broader QOL instruments. We define QOL as self-reported perceived well-being across physical, psychological, social, environmental and, where applicable, spiritual or religious domains, as operationalised by the instruments used. Tools may include the Stroke-Specific Quality of Life Scale, WHOQOL-BREF, and EuroQol Five-Dimension Questionnaire. Both self- and proxy-reported QOL measures will be included; where both are available, self-reported measures will be prioritised.

The first secondary outcome is cognitive function, assessed using validated instruments measuring global cognitive performance or specific cognitive domains. Eligible tools include, but are not limited to, the Montreal Cognitive Assessment and Mini-Mental State Examination. Objective global cognitive measures will be prioritised because they provide standardised, performance-based assessments of cognitive function. Subjective and observer-reported measures will also be included, comprising participant-reported, proxy/informant-reported, and clinician-rated measures. These measures may capture perceived or observed cognitive difficulties in everyday life, providing complementary information on patient-relevant outcomes. The second secondary outcome will be adverse events, extracted as reported, including counts, proportions, rates, severity, withdrawals due to adverse events, and questionnaire-based measures.

Locally developed tools will be included if they have undergone a clearly reported validation process within the study context, recognising that validation may be context specific. Studies with unvalidated tools will be excluded, as this limits comparability across studies and may compromise the robustness and credibility of the synthesis.

Duration of Follow-Up

No minimum follow-up period beyond the end-of-intervention assessment will be required. The primary analysis will use outcomes measured at intervention completion or at the scheduled assessment closest to the final intervention session. This time point provides the most direct and consistently reported estimate of the effect of completing the intervention. Follow-up outcomes will be analysed separately to assess whether intervention effects are sustained. Follow-up duration will be calculated from intervention completion to outcome assessment and categorised as ≤1 month, >1–6 months, >6–12 months, or >12 months. Where multiple follow-up assessments are reported within the same category, the assessment closest to the upper boundary will be selected.

Types of Settings

The review will include reports conducted in any setting, grouped into the following categories:

• (1) Healthcare settings (hospital, inpatient rehabilitation, or outpatient clinic)

• (2) Community settings/non-clinical

• (3) Home-based settings

• (4) Residential care

• (5) Mixed (specify)

• (6) Other (specify)

• (7) Unclear/not reported

Search Methods for Identifying Studies

The literature search will use multiple methods to maximise sensitivity and identify both published and unpublished studies, following established guidelines (Kugley et al., 2017; MacDonald et al., 2024). The search will cover records from the database’s inception, with no date or setting restrictions, and will include only English-language records because the review team is proficient only in English and translation resources are unavailable. This restriction may introduce language bias and will be considered when interpreting the review findings. Keywords, subject headings, and synonyms will be combined using Boolean operators and concept blocking with search strategies from previous PSCI reviews adapted where appropriate (Luo et al., 2024; O'Donoghue et al., 2022; Stolwyk et al., 2024; Zheng et al., 2016). The intervention concept will be excluded to maximise retrieval of RCTs, as relevant interventions are broad and may be difficult to capture; therefore, the search will be structured with four core concepts.

(cerebrovascular disease* OR stroke*) AND (cogniti* OR dement*) AND (quality of life OR Health-related quality of life OR wellbeing OR well-being) AND (random* OR randomi?ed controlled trial).

Published systematic reviews will be used to create a “known article set” (gold set) to test and refine the search strategy. Validated search filters from the Cochrane Collaboration will be adapted to improve search precision and identify RCTs in humans (Glanville et al., 2006; McGill University Library, 2025). MLM will conduct all searches in consultation with the review team, and a school librarian (A.H.A) will iteratively peer-review the search strategies.

Electronic Searches

Database Search

There are eight databases and their platforms that will be searched through the Monash University library services. This includes APA (American Psychological Association) PsycInfo via Ovid, Cumulative Index to Nursing and Allied Health Literature (CINAHL Ultimate) via EBSCOhost, Cochrane Central Register of Controlled Trials via Ovid, Excerpta Medica Database (Embase) Classic + Embase via Ovid, PubMed, Scopus (Elsevier), Social Science Database (SSD) via ProQuest, and Web of Science Core Collection. Appendix 2 provides the full search strategies for APA PsycInfo (Ovid), Embase Classic + Embase (Ovid), PubMed, and Scopus (Elsevier). The search strategy was initially developed and validated in Embase via Ovid, and then adapted for use across other databases.

Searching Other Resources

Trial Registry Search

The WHO International Clinical Trials Registry Platform and ClinicalTrials.gov will be searched separately.

Internet Searches

We will screen the first 20 pages of Google Scholar and the first five pages of Google Search, applying page limits because results are ranked by relevance. Evidence shows that most relevant studies are typically found within the first 200–300 Google Scholar results (Haddaway et al., 2015). Additionally, we will search the Directory of Open Access Journals to identify relevant studies published in journals not indexed in major databases using the previously stated concepts.

Searching Other Sources

Citation Searching

We will further search the reference lists of systematic reviews, meta-analyses and umbrella reviews on PSCI.

Contact With Experts

All authors with three or more identified eligible reports will be contacted to inquire about any unpublished or ongoing studies. All identified trial registrations will be checked for study status and the availability of results. Investigators will be contacted for completed trials without published or posted results and for trials with no registry status update for five years or more. If no response is received, a reminder will be sent after 2 weeks, and the enquiry will be closed after 30 days. If no additional information is obtained, the trial will be excluded because it lacks sufficient information to assess eligibility for the review.

Data Collection and Analysis

Description of Methods Used in Primary Research

Studies are expected to employ RCT designs for RBIs, with cognitive function and QOL outcomes assessed using a range of standardised measures, and with variation in settings, intervention durations, and follow-up periods.

Selection of Studies

All retrieved records will be exported from each database in Research Information Systems (RIS) format and imported directly into Covidence (Covidence Systematic Review Software, 2025) for each database. Covidence will automatically identify and flag duplicate records, which will be reviewed and removed before study selection proceeds (Covidence Systematic Review Software, 2025). Two stages of title and abstract screening, followed by full-text assessment, will be used, with humans involved only at all stages of this review.

Phase one: title and abstract screening

MLM and FIA will independently screen the titles and abstracts of retrieved records in Covidence to identify potentially eligible studies, and records that clearly do not meet the inclusion criteria will be excluded. Disagreements will be resolved through team consultation; if consensus is not reached, DM, as one of the senior reviewers with the most content expertise, will adjudicate, and relevant records will proceed to full-text assessment.

The following inclusion criteria will be used during title and abstract screening:

• (1) Empirical study involving primary or secondary data collection.

• (2) RCTs.

• (3) Conducted among human stroke survivors, not exclusively animals, carers, or HCPs

• (4) Has cognition and quality-of-life outcomes.

Phase Two: Full-Text Evaluation

MLM and FIA will independently retrieve and assess the full texts of all records deemed potentially eligible during title and abstract screening. If a full text cannot be retrieved, efforts will be made to contact the original authors and to seek alternative access through Monash University library services, including interlibrary loan. If the full text is still unavailable, the report will be excluded because full eligibility cannot be completed, and the retrieval attempts will be documented. Where multiple reports relate to the same study, all available reports will be reviewed together to determine eligibility. Full-text reports will be assessed against predefined eligibility criteria relating to the population, intervention, comparator, outcomes, study design, and additional study factors (PICOS-ASF). Each reviewer will independently rate studies for inclusion or exclusion and record the reasons for exclusion in Covidence. Studies rated by both reviewers as “exclude” for the same reason will be excluded, and disagreements will be resolved through team discussions. If disagreement persists after discussions, DM, as one of the senior reviewers with the most content expertise, will adjudicate and make the final decision. The study selection process will be documented and reported using a PRISMA flow diagram to ensure transparency and reproducibility (Page et al., 2021).

The following inclusion criteria will be used during full-text evaluation.

• (1) Participants are adult stroke survivors aged 18 years or older. Where adults and paediatric populations are included, adult-specific data can be extracted separately.

• (2) The study is an RCT in which individuals or clusters are randomised, using a parallel-group, crossover, or factorial design

• (3) The eligible intervention was initiated after the stroke.

• (4) The study includes at least one eligible comparator.

• (5) The study reports both cognitive function and QOL at one or more post-intervention time points. Post-intervention scores, adjusted estimates, change-from-baseline scores and narrative comparisons will all be eligible.

• (6) Cognitive function and QOL are assessed using validated instruments. Objective or subjective cognition measures and self- or proxy-reported quality-of-life measures will be eligible.

• (7) The intervention meets the review’s definition of an RBI; other intervention types will be excluded.

• (8) For factorial trials, the effect of the eligible RBI is presented separately from any non-RBI components.

• (9) For crossover trials, first-period data can be extracted separately.

• (10) For studies including mixed stroke and non-stroke populations, stroke-specific data can be extracted separately.

• (11) For multi-arm studies that include non-RBIs, data for the eligible intervention and comparator arms can be extracted separately.

• (12) A full-text report is available in English.

Data Extraction and Management

First, MLM will check each included study for retractions and corrections, record the status as of that date, exclude any retracted studies and use the most recently corrected version. Appendix 3 contains the Excel data extraction sheet that MLM and AA will use. MLM will extract general study characteristics, which AA will check for accuracy and completeness. Additionally, MLM and AA will independently extract outcome data; discrepancies will be resolved through review team discussions, with DM as one of the senior reviewers with the most context expertise, adjudicating.

The following information will be extracted:

• (1) General study information, including authorship, publication type, publication status, funding sources, and conflicts of interest.

• (2) Study characteristics, including study design, setting, eligibility criteria, unit of allocation, and study duration (start and end dates).

• (3) Participant characteristics, including sample size; demographics (age, sex, ethnicity, and level of education).

• (4) Intervention and comparator details, including type, components, delivery mode (including AI-assisted), duration, frequency, providers, adherence (if reported), and any co-interventions.

• (5) Outcome information, including measures of cognitive function, QOL, and adverse events. This will also include measurement scale values, direction of interpretation, time points measured and reported, and the validation status of instruments. Numerical outcome data, including means, standard deviations (SDs) or other measures of variability, event counts, and effect estimates, will also be extracted. We will also specify whether results are reported as post-intervention or as a change from baseline.

• (6) Methodological characteristics relevant to inform the Risk of bias 2 assessment, such as the randomisation process, allocation concealment, and baseline comparability. Additionally, we will collect participant and personnel awareness of assigned interventions, outcome assessor blinding, deviations from intended interventions, and the analysis population. Missing outcome data and reasons for missingness, outcome measurement methods, and trial registration will be collected. Lastly, the availability of the protocol, statistical analysis plan, and information relevant to the selection of the reported result will also be recorded.

• (7) Statistical and analytical information, including statistical methods used, software and the population used for the analysis.

• (8) Subgroup and additional analyses, including any subgroup analyses conducted or reported, such as by age, stroke severity, or intervention characteristics.

• (9) Reported resources required for intervention delivery.

All reports from the same study will be used, and data will be coded as reported; where possible, they will be transformed into a common set of categories for analysis. These will include the number of treatment sessions per week, the total treatment duration in weeks, and the individual treatment time in minutes. The data extraction form will be pilot-tested and refined to ensure clarity, consistency, and completeness, and any modifications to the form or extraction procedures will be documented and reported.

Assessment of Risk of Bias in Included Studies

MLM and FIA will independently assess risk of bias in the selected results of included studies using the Cochrane Risk of Bias 2 (RoB 2) tool for individually randomised parallel-group trials and the RoB 2 variant for cluster-randomised trials (RoB 2 CRT), as appropriate (Eldridge et al., 2021; Higgins et al., 2024; Sterne et al., 2019). The versions dated 22 August 2019 and 18 March 2021, respectively, will be implemented using the corresponding Excel tools. Assessments will be conducted for the selected cognition and quality-of-life results from each study, defined by the outcome measure and time point, and will address the effect of assignment to intervention. All sources used to inform each assessment will be documented.

The standard RoB 2 tool comprises five domains assessing bias arising from the randomisation process, bias due to deviations from intended interventions, bias due to missing outcome data, bias in measurement of the outcome, and bias in selection of the reported result (Sterne et al., 2019). For cluster-randomised trials (CRTs), the RoB 2 CRT additionally assesses bias arising from the timing of participant identification or recruitment relative to cluster randomisation (Eldridge et al., 2021). MLM and FIA will pilot-test the tools to ensure consistency in their interpretation and application, and disagreements will be resolved through discussion. When consensus cannot be reached, KFQ, as the senior reviewer with expertise in quantitative methods, will adjudicate. Risk-of-bias findings will be summarised by domain and overall judgement, with detailed result-specific assessments presented in tables and figures in supplementary files.

Measures of Treatment Effect

Continuous outcomes will be regarded as the primary measure of treatment effects, and dichotomous outcomes will be secondary. This is because continuous outcome measures retain more statistical information, enhance sensitivity to change, and allow more precise estimation of intervention effects (Higgins et al., 2024). All continuous outcomes will be analysed using mean differences (MDs) when studies use the same measurement scale, and standardised mean differences (SMDs) with 95% confidence intervals (CIs) when studies use different scales. In the meta-analysis, for continuous outcomes measured with different instruments, SMDs will be calculated using Hedges’ g with corresponding 95% CIs to correct for potential small-sample bias. Higher scores will consistently reflect improvement in cognitive function and QOL and worsening of adverse effects. Where available, adjusted effect estimates, such as from analysis of covariance, will be preferred and synthesised using the generic inverse-variance method. Dichotomously reported outcomes will be interpreted using odds ratios (ORs) with 95% CIs, and log ORs will be used for meta-analysis, with back-transformed ORs reported for interpretation. ORs are the preferred dichotomous outcome effect measure because baseline risk differences across studies have less influence on them and are more suitable for pooling in meta-analyses with heterogeneous populations (Higgins et al., 2024). OR-to-SMD conversions may be considered using Chinn’s formula when the underlying outcome is conceptually equivalent, and the assumptions of the conversion method are met (Chinn, 2000).

Where studies report outcomes based on the minimal clinically important difference (MCID), these will be treated as dichotomous outcomes and analysed using ORs with 95% CIs. Where alternative effect measures, such as risk ratios (RRs) or risk differences (RDs), are reported, these will be analysed and presented separately where conversion to a common metric is not appropriate. Where appropriate, pooled estimates for dichotomous outcomes will be calculated using the Mantel–Haenszel method. For studies with zero events in one arm, treatment-arm continuity corrections will be applied where appropriate. Studies with zero events in both arms will be excluded from the meta-analysis and summarised narratively using the synthesis without meta-analysis (SWiM) approach (Higgins et al., 2024). For studies reporting correlations between cognitive function and QOL, correlation coefficients (r) will be Fisher-transformed for synthesis, converted back for interpretation, and reported separately.

Random-effects meta-analysis will be used to account for expected clinical and methodological heterogeneity. In particular, heterogeneity is expected due to differences in intervention types, modes of delivery, comparator conditions, and outcome measures. We will estimate effect sizes using inverse-variance weighting and estimate between-study variance using the restricted maximum likelihood method, as it provides unbiased estimates (Higgins et al., 2024). Change-from-baseline and endpoint data will be synthesised together where MDs can be calculated, and synthesised separately if SMDs are required. Additionally, where appropriate, relative effects will be translated into absolute effects to aid interpretation for applicable dichotomous outcomes. Specifically, the number needed to treat (NNT) will be calculated from the absolute risk reduction (ARR) derived from pooled effect estimates and an assumed control event rate (CER). A network meta-analysis is not planned because the assumption of transitivity cannot be confidently met. Review Manager Web (RevMan Web) and R will be used for data management and statistical analyses, and a two-sided p-value <0.05 will be considered statistically significant for the intervention effect.

Unit of Analysis Issues

The unit of analysis will be individual participants, including in studies where clusters or body parts are randomised. Where studies randomise or analyse body parts, data will be aggregated or adjusted to ensure each participant contributes only once to the analysis. For cluster RCTs, we will adjust for clustering using the intra-cluster correlation coefficient (ICC); where ICCs are not reported, estimates from similar studies will be used where appropriate (Higgins et al., 2024).

Criteria for the Determination of Independent Findings

Where a study reports multiple eligible results for cognition or QOL because it includes multiple comparators, time points, instruments, scores, or analyses, one result will be selected for each planned synthesis using the following considerations:

• (1) The end-of-intervention assessment will be selected for the primary analysis. Follow-up assessments will be analysed separately within the prespecified follow-up categories. Where a study reports more than one assessment within the same follow-up category, the assessment closest to the upper boundary of that category will be selected.

• (2) An overall or total QOL score will be prioritised over component, domain, subscale, or individual-item scores. Among measures at the same level, validated, self-reported stroke-specific QOL measures will be prioritised over generic proxy-reported health-related QOL measures.

• (3) A validated objective measure of global cognitive function will be prioritised over objective domain-specific measures. Objective measures will be prioritised over subjective or proxy, or clinician-rated cognitive assessments. Where objective global cognition measures remain tied, the measure most used in the included studies will be selected.

• (4) One cognition result and one QOL result will be selected to represent each study as the primary result and be used for the risk of bias assesment. Where no global cognition or overall QOL score is available, and multiple domain-specific measures are reported, the domain explicitly identified as primary by the study authors will be selected. If no primary domain is specified, the most reported eligible domain across the included studies will be selected.

• (5) If measures remain tied, the measure with the strongest evidence of validity and reliability in stroke populations will be selected.

• (6) Analyses estimating the effect of assignment to the intervention, preferably based on the intention-to-treat population, will be prioritised over per-protocol or completer analyses.

• (7) A continuous measure will be prioritised over a dichotomised version of the same outcome. Comparisons with inactive controls will be prioritised over active controls.

• (8) Estimates that appropriately account for the study design, including clustering where applicable, will be used. Estimates adjusted for the baseline value of the outcome and prespecified baseline covariates will be prioritised over unadjusted estimates.

• (9) Change-from-baseline data will be prioritised when the required summary statistics are available; otherwise, post-intervention data will be used.

• (10) Reports relating to the same trial will be collated and treated as a single study. Data will be obtained across all reports, with the most complete outcome used as the primary source.

• (11) Where multiple eligible intervention arms are sufficiently similar, they will be combined. Where combining the arms is not clinically appropriate, they will be retained as separate comparisons, and the shared group(s) will be divided, or another method accounting for the dependency between groups will be used.

• (12) The tool providing directly usable numerical data for meta-analysis will be prioritised over one requiring data conversion or additional assumptions.

• (13) The tool providing numerical data will be prioritised over one from which no numerical data is presented.

• (14) If none of these criteria identifies a single measure to represent the study’s cognition and QOL outcomes the measure reported first in the Methods or Result section will be selected as a reproducible, non-data-driven tiebreaker.

Any post-hoc decisions will be transparently documented and justified in the final review.

Dealing With Missing Data

When outcome data or summary statistics are missing, we will first check the supplementary materials and contact the study authors. Where sufficient information is available, missing standard deviations (SDs) will be calculated from standard errors (SEs), CIs, t statistics, exact p values, or appropriate F statistics following Cochrane guidance (Higgins et al., 2024). When continuous outcomes are reported using the sample size, median, range, and/or interquartile range, the mean and SD will be estimated where appropriate (Wan et al., 2014). We will not impute missing participant outcome data for the primary analysis; the study will be excluded from the meta-analysis for that outcome, but may be described narratively, using the SWiM approach. We will consider the potential impact of missing participant data in the RoB assessment and, where feasible, explore it in sensitivity analyses. All attempts to obtain or derive missing data in sensitivity analyses, as well as all assumptions made, will be documented and included in the final report.

Assessment of Heterogeneity

Forest plots will be visually inspected for variation in the magnitude and direction of effect estimates. Statistical heterogeneity will be assessed using Cochran’s Q (Chi²) test, with p < 0.10 considered evidence of heterogeneity. Between-study variance will be quantified using tau-squared (τ²), and inconsistency will be quantified using I²; I² values of 80%–100% may indicate considerable heterogeneity. However, I² will be interpreted alongside the magnitude and direction of effects, clinical and methodological diversity, τ², and the Chi² test (Higgins et al., 2024).

Assessment of Reporting Biases

A comprehensive search strategy will be conducted across multiple databases and grey literature sources to identify both published and unpublished studies. Clinical trial registries will be searched to identify completed but unpublished studies and to compare registered outcomes with reported outcomes. Where discrepancies are identified, the study authors will be contacted for clarification, and the authors with three or more included studies will also be contacted to identify any additional unpublished results. We will consider the potential for publication bias arising from excluded conference abstracts that do not subsequently lead to full-text publication and from completed trials with no publicly available results. We will further consider reporting bias for outcomes included in protocols that were not reported in publications and for which clarifications could not be obtained despite attempts to contact the authors or for which no author contact information is available.

Small-study effects will be assessed separately for each meta-analysis containing at least 10 studies with sufficient variation in study size. Because effect estimates will be expressed as Hedges’ g, sample-size-based funnel plots will be visually examined, and the Pustejovsky–Rodgers test will be used to assess funnel plot asymmetry. A p-value <0.10 will indicate potential small-study effects (Pustejovsky & Rodgers, 2019). Funnel plot asymmetry will not be interpreted as definitive evidence of publication bias because it may also arise from clinical or methodological heterogeneity, artefactual associations, or chance (Higgins et al., 2024).

Data Synthesis

We will conduct meta-analyses when two or more studies are sufficiently homogeneous with respect to PICOS-ASF, and we will include only studies reporting both cognitive function and QOL in the synthesis. Cognition and QOL will be analysed separately, and pooled estimates for each outcome will be compared and jointly interpreted according to their direction, magnitude, and consistency. To explore whether changes in cognition are associated with changes in QOL, a study-level random-effects meta-regression will be conducted when 10 or more studies contribute effect estimates for both cognition and QOL to the same meta-analysis. The study-specific effect estimate for cognition will be included as the explanatory variable, and the corresponding study-specific effect estimate for QOL as the dependent variable. The meta-regression will be performed using inverse-variance weighting and the restricted maximum likelihood estimator to account for between-study heterogeneity, and we will report the regression coefficient, 95% CIs, and p-value. Because the analysis uses study-level effect estimates rather than individual participant data, the findings will be interpreted only as observational. Adverse events will be analysed separately and considered during interpretation to assess the overall benefit–harm balance. No vote counting will be used; where meta-analysis is not feasible, the SWiM approach will be used to summarise the evidence. Cognition and QOL findings will be compared study by study to assess whether intervention effects are concordant, discordant, or mixed within and across studies, with results presented using harvest plots (Thomson & Campbell, 2020). Where ICCs are unavailable and cannot be obtained from authors or external sources, those studies will be synthesised using SWiM approaches, and we will explore a range of plausible ICC values in sensitivity analyses. Analyses will be conducted using RevMan Web and R; MLM will lead the analysis with support from the review team.

Subgroup Analysis and Investigation of Heterogeneity

When substantial heterogeneity is identified, and sufficient data are available, we will conduct subgroup analyses based on prespecified study and participant characteristics to explore potential sources of heterogeneity, including:

• (1) Initiation of the intervention after stroke (≤6 months vs > 6 months post-stroke): Interventions initiated early (≤6 months) may coincide with the period of heightened neuroplasticity.

• (2) Where sufficient studies are available, the total planned intervention dose will be examined as a continuous variable using meta-regression, as it may affect the intervention’s effect.

• (3) Duration of follow-up categorised as ≤1 month, >1–6 months, >6–12 months, >12 months. Short-term follow-up may capture early improvements following the intervention. Longer follow-up periods (>6 months) are necessary to determine whether the intervention effects are sustained and whether any long-term adverse outcomes occur.

• (4) Single-component vs multi-component/combination interventions - Combination interventions may target multiple mechanisms underlying PSCI; they may have differential effects on cognitive function and QOL outcomes while requiring greater implementation resources.

• (5) Within each intervention subtype, compare the four categories to inform clinical practice.

The subgroup analyses will identify potential effect modifiers and interactions that may explain why the intervention outcomes vary, all treated as observational (Higgins et al., 2024).

Sensitivity Analysis

Where sufficient data are available, we will conduct sensitivity analyses to assess the robustness of the findings to methodological and analytical decisions. These will include:

• (1) Using an alternative effect measure for dichotomous outcomes, such as risk ratios instead of odds ratios.

• (2) Repeating analyses after excluding studies judged to be at high overall ROB.

• (3) Comparing random-effects and fixed-effect meta-analysis models.

• (4) Repeating analyses after excluding studies for which summary outcome statistics were imputed or estimated where appropriate.

• (5) Comparing analyses based on intention-to-treat data with those based on per-protocol or completer data.

• (6) Applying a range of plausible ICC values when cluster-randomised trials have not accounted for clustering and an ICC is unavailable.

Treatment of Qualitative Research

We do not plan to include qualitative research findings in this review.

Summary of Findings and Assessment of the Certainty of the Evidence

The findings will be presented using forest plots where a meta-analysis is used and Summary of Findings tables to present effect estimates and certainity of evidence, focusing on the direction and magnitude of effects between cognitive outcomes and QOL. To enhance practical relevance, we will indicate whether the evidence adequately addresses the review questions or requires further research. Interventions may be further categorised by structure, subtype, timing of initiation, total intervention dose, and follow-up duration. The certainty of the evidence will be assessed using the Grading of Recommendations Assessment, Development and Evaluation (GRADE) approach, following the guidance of Higgins et al. (2024). Five domains will be evaluated: risk of bias, inconsistency, indirectness, imprecision, and publication bias. Concerns in each domain will be assessed from no concerns to very serious concerns, as illustrated in Figure 1.

Figure 1.

The Continuum for Evaluating Each Domain in the GRADE Framework. Alt text: A Horizontal Gradient Arrow Illustrating the Continuum of Certainty of Evidence, Ranging From No Concerns to Very Serious Concerns

Serious concerns in one domain will result in a one-level downgrade in the certainty of the evidence, while very serious concerns will result in a two-level downgrade. If several domains present minor concerns, they may collectively justify downgrading the certainty by one level. All decisions regarding downgrading will be justified to ensure transparency and facilitate interpretation. Based on these assessments, the overall certainty of evidence for each outcome will be classified as high, moderate, low, or very low. MLM, FIA and AA will conduct the GRADE assessment independently for each meta-analysed effect estimate; disagreements will be resolved through team discussions, with KFQ adjudicating if no consensus is reached. Harvest plots will be presented for SWiM (Higgins et al., 2024), and a plain-language summary will be provided to improve accessibility.

The discussion will focus on changes in cognitive function and their corresponding effects on QOL and safety outcomes, emphasising the magnitude, precision, and consistency of effect estimates. Effect estimates will be interpreted with caution when studies are judged to be at high RoB or when evidence of publication bias is detected. Findings will be further interpreted in light of statistical heterogeneity, clinical and methodological variability. Directness of the evidence will involve assessing the extent to which the PICOS-ASF in the included studies align with those specified in this review. Generalisations of the findings across different settings will take into account the characteristics of the included studies and healthcare systems.

Implications for practice and future research will be identified based on the strength, consistency, and applicability of the evidence. Practice recommendations will be made cautiously, with evidence gaps highlighted, including limitations in the review’s methodological implementation and decisions, to inform future review priorities. Current limitations include the inclusion of RBIs only, the inclusion of only English-language reports, and the requirement that studies report both cognitive function and QOL outcomes. Moreover, the meta-regression will examine only the study-level observed effects between cognitive function and QOL and cannot establish causality. Additionally, variation in cognitive and quality-of-life measures may limit opportunities for quantitative synthesis. Lastly, categorising interventions into rehabilitation and behavioural groups, as well as active or inactive comparators may be subjective and may be open to debate. Two outputs will be produced: a comprehensive full report and a concise journal article, both of which will be made freely available. The reports will be published in English, and translations into other languages will be welcomed, subject to prior editorial approval. Appendix 5 provides a list of abbreviations, and Appendix 6 presents definitions of terms used in this protocol to assist with clarity and interpretation. All Appendices are included in the Supplementary Materials.

Data Availability Statement

Data sharing is not applicable to this article because no datasets were generated or analysed during the preparation of this protocol.*