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Cochrane Database of Systematic Reviews Protocol - Intervention

Exercise therapy for the treatment of delirium in the intensive care unit

Authors' declarations of interest

Version published: 25 March 2024 Version history

https://doi.org/10.1002/14651858.CD015830
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Abstract

Objectives

This is a protocol for a Cochrane Review (intervention). The objectives are as follows:

To assess the effects of exercise therapy for the treatment of delirium in critically ill adults in the intensive care unit.

Background

Description of the condition

The fourth edition of the American Psychiatric Association (APA) Diagnostic and Statistical Manual of Mental Disorders (DSM‐IV) defines delirium as a disturbance in attention, awareness, and cognition that develops over a short period of time (hours to days) and fluctuates in severity over the course of a day (American Psychiatric Association 2013). Delirium in the intensive care unit (ICU) is a syndrome characterised by the acute onset of cerebral dysfunction with a change or fluctuation in baseline mental status, inattention, and either disorganised thinking or an altered level of consciousness (Barr 2013). The pathophysiology of delirium is not entirely understood, although it is related to neuroinflammation, an aberrant stress response, neurotransmitter imbalances, and neuronal network alterations (Barr 2013; Zaal 2012). People in the ICU have an increased risk of developing delirium due to several factors, such as benzodiazepine use, blood transfusions, dementia, prior coma, pre‐ICU surgery, trauma, multi‐system illnesses, comorbidities, use of psychoactive medications, and age, with especially poor outcomes in people aged over 65 years (Devlin 2018; Ely 2001a; Gao 2021; Li 2020). The prevalence of delirium reported in different ICU cohort studies varies from 15% to 74%, depending on the severity of the illness, the specific ICU setting (i.e. surgical/postoperative, medical or mixed populations), and the diagnostic tool used (Ali 2023; Haußmann 2023; Paixao 2021; Sadaf 2023; Salluh 2010; Vasilevskis 2012). Most cases of delirium go undiagnosed in ICUs that do not use regular screening tools (Hayhurst 2016; Serafim 2020).

There are several validated instruments to assess delirium in critically ill people, with the Confusion Assessment Method for the Intensive Care Unit (CAM‐ICU) and the Intensive Care Delirium Screening Checklist (ICDSC) being the most widely studied (Khan 2020; Rose 2021). Given the fluctuating course of delirium, regular assessment is crucial (e.g. every six hours), as an assessment at any given point in time may not capture the complete symptomatology (Hayhurst 2016). Delirium can present with three subtypes according to psychomotor behaviour (hyperactive, hypoactive, and mixed delirium; Girard 2008). These subtypes may have different prognoses: compared with hyperactive delirium, hypoactive delirium has been associated with a greater risk for complications such as pressure ulcers or hospital‐acquired infections that lead to prolonged length of stay and increased mortality (Hayhurst 2016). Hypoactive delirium (more common in older adults) is characterised by slowed mentation, lethargy, and decreased movement, whereas hyperactive delirium is characterised by agitation, restlessness, and emotional lability (Girard 2008; Hayhurst 2016). Pure hyperactive delirium is rare (less than 2%), whereas approximately 43% of people with delirium in the ICU have the purely hypoactive subtype, and approximately 54% have mixed delirium (Girard 2008; Hayhurst 2016; Hayhurst 2020).

Delirium in critically ill people is recognised as a significant public health problem (Barr 2013). It can disturb patients and relatives and is associated with worse outcomes, much longer ICU and hospital stays, and much higher costs (Slooter 2017). The estimated annual healthcare cost attributable to delirium in the USA is USD 182 billion (Rose 2021). The impact of delirium on relevant clinical outcomes is not restricted to the hospital setting, as delirium is also an independent predictor of six‐month mortality and long‐term cognitive impairment (Ely 2004a; Girard 2010). Despite this evidence, delirium is still underdiagnosed, and clinicians often do not recognise modifiable risk factors such as those related to the critical illness and its treatment or the environment in the ICU (Ely 2004b; McPherson 2013; Patel 2009; Van Rompaey 2009).

Description of the intervention

Exercise therapy is a set of interventions designed to decrease immobility while facilitating the movement of people in the ICU, with the ultimate goal of improving survival and other outcomes, such as the ability to meet basic functions, carry out the activities of daily living (ADL), and live independently (Amidei 2012; Storch 2008).

In the critical care setting, exercise therapy usually involves activities that enhance ventilation, central and peripheral perfusion, circulation, muscle metabolism, and alertness. It includes passive and active turning, moving in bed, active‐assisted mobility exercises, use of cycling pedals in or out of bed, sitting over the edge of the bed, standing in place, transferring out of bed to a chair, and walking (Doiron 2018; Gosselink 2008).

Exercise therapy is usually provided by ICU staff and can be implemented alone or in the context of a multicomponent intervention, also known as a bundle of care, as suggested by the 2018 Clinical Practice Guidelines (CPG) for the Prevention and Management of Pain, Agitation/Sedation, Delirium, Immobility, and Sleep Disruption in Adult Patients in the ICU (Devlin 2018). One of the most disseminated and implemented bundles is the ABCDEF bundle, which includes the following components (Marra 2017).

  • Assess, prevent, and manage pain

  • Both spontaneous awakening trials and spontaneous breathing trials

  • Choice of analgesia and sedation

  • Delirium: assess, prevent, and manage

  • Early mobility and exercise

  • Family engagement and empowerment

This bundle has clearly defined individual components that are flexible to implement and that help empower multidisciplinary clinicians and families in the shared care of critically ill people while promoting optimal resource utilisation. The measures can help ICU patients to control their pain and participate in higher‐order physical and cognitive activities at the earliest point in their critical illness (Marra 2017).

For clinicians to safely implement early progressive mobilisation and exercise therapy in an ICU setting, with minimal risk of adverse events, they must carefully assess patients in advance, following objective respiratory, cardiovascular, and neurological safety criteria. These criteria, along with the patient's strength and endurance, usually determine the intensity of the exercise therapy (Hodgson 2014).

How the intervention might work

Reducing immobility through early rehabilitation interventions such as exercise therapy or physical therapy may be beneficial as part of delirium management strategies (Devlin 2018). A structured and repetitive exercise therapy plan not only helps to maintain physical functions and prevent or delay disability, but may also protect against cognitive decline or even reverse the cognitive impairment associated with hospitalisation of older people (Gual 2020). Furthermore, neurobiological studies suggest that exercise therapy influences the brain by stimulating angiogenesis, neurogenesis, and synaptogenesis at a supramolecular level, or by producing changes in molecular growth factors such as brain‐derived neurotrophic factor, which plays a crucial role in neuroplasticity and neuroprotection at a molecular level (Gual 2020).

Why it is important to do this review

Exercise therapy is of particular interest in the ICU setting as an approach to mitigating the consequences of immobility and inflammation arising from a critical illness. In critical care, exercise therapy has recently garnered a great deal of attention as a measure to improve outcomes (Amidei 2012), contributing to a shift in ICU clinical practice, where people who once would have received mandatory bed rest are now less restricted and receive early progressive mobilisation and exercise therapy (Hodgson 2014).

The 2018 CPG for the Prevention and Management of Pain, Agitation/Sedation, Delirium, Immobility, and Sleep Disruption in Adult Patients in the ICU suggests implementing a multicomponent, nonpharmacologic intervention focused on (but not limited to) reducing modifiable risk factors for delirium, improving cognition, and optimising sleep, mobility, hearing, and vision in critically ill adults (Devlin 2018).

While strong evidence indicates delirium is partially preventable through multicomponent nonpharmacologic approaches (Burry 2021; Chen 2022; Deng 2020; Rose 2021; Ryu 2022), the role of such approaches after the diagnosis of delirium remains unknown. Because delirium almost always has a multifactorial aetiology, multicomponent interventions are plausibly more promising than single interventions. However, there is uncertainty regarding the effectiveness of each component (Devlin 2018), as clear descriptions of the benefit of exercise therapy in treating delirium are lacking (Amidei 2012). Studies on exercise therapy early in critical illness suggest this approach is safe, feasible, and cost‐effective (Foster 2013), and several studies implementing exercise therapy (alone or as a bundle of care) have shown improvement in cognitive functions and a reduction in delirium (Devlin 2018). This review will aim to synthesise the available evidence on the effect of exercise therapy on delirium in people in the ICU.

Objectives

To assess the effects of exercise therapy for the treatment of delirium in critically ill adults in the intensive care unit.

Methods

Criteria for considering studies for this review

Types of studies

We will include randomised controlled trials (RCTs), including cluster‐RCTs. We will not include cross‐over RCTs as they are not relevant to our review question. Quasi‐RCTs are ineligible.

We will include studies reported as full text as well as those published as abstracts only. We will include unpublished data where it is possible to establish study eligibility for inclusion.

Types of participants

We will include studies of people aged 18 years or older treated in the ICU of any speciality (trauma, surgical, medical, cardiac, etc.) for critical illness, with or without mechanical ventilation, with a diagnosis of delirium after ICU admission based on a validated delirium assessment tool such as the CAM‐ICU (Ely 2001a; Ely 2001b), or the ICDSC (Bergeron 2001). In addition, we will include people with subsyndromal delirium (ICDSC score between 1 and 3), as they are usually managed with a similar approach to people with full delirium syndrome (Devlin 2018).

If we identify studies in which only a subset of participants is relevant to this review, we will include the studies if they provide separate data for eligible participants, or if more than 80% of participants meet our eligibility criteria.

Types of interventions

We will include studies that evaluate exercise therapy focused on reducing immobility (e.g. early rehabilitation/mobilisation) versus the following comparators.

  • No intervention or usual care

  • Any pharmacological treatment, such as alpha‐2 agonists (e.g. clonidine, dexmedetomidine), antidepressants (e.g. fluoxetine), antipsychotics (typical agents like haloperidol or atypical agents like quetiapine), or hydroxymethylglutaryl‐CoA (HMG‐CoA) reductase inhibitors, also known as statins (Burry 2019; Devlin 2018).

We will consider studies that implement the following types of exercise therapy (Doiron 2018).

  • Bed mobility activities (e.g. bridging, rolling, lying to sitting), including active, active‐assisted, and passive exercises

  • Cycle ergometer

  • Transfer training

  • Pre‐gait exercises (including marching on the spot)

  • Ambulation‐like exercises

  • Any other mobility‐based intervention as defined by the study authors

We will include studies that implement these strategies as single interventions or as a bundle of care (Marra 2017; Malik 2021). We will include any intervention dose, frequency, duration, and provider (e.g. ICU or family members under an ABCDEF‐like bundle of care), as defined by study authors. The 'Characteristics of included studies' table will present these details (see Data collection and analysis). We will include studies where exercise therapy would not be offered routinely as part of the care management during the recovery phase of the health condition being treated (e.g. trauma surgery).

We will include co‐interventions, provided they are not part of the randomised treatment and are consistent across groups.

Types of outcome measures

Reporting of the outcomes of interest for this review will not be a study eligibility criterion.

Primary outcomes

  • Duration of delirium/time to delirium resolution: defined as the number of days a participant tests positive for delirium based on validated tools like the CAM‐ICU or the ICDSC (Khan 2020; Rose 2021). As there is no official definition for delirium termination, and given the fluctuating course of the disease, we will consider that participants have delirium if they test positive for delirium at any assessment point in a day (Pisani 2009), or we will accept study authors' definitions. Alternatively, we will consider delirium‐ and coma‐free days as an inverse measure of the same outcome (Page 2013), but we will analyse this measure separately.

  • Health‐related quality of life (HRQOL): measured by validated scales, such as the 36‐Item Short‐Form Health Survey (SF‐36; Ware 1992), or the EuroQol five‐dimension questionnaire (EQ‐5D; Herdman 2011). If a study reports several scales for this outcome, we will select the most reported scale across the included studies, following guidelines in the Cochrane Handbook for Systematic Reviews of Interventions (Table 9.3.c; McKenzie 2023a).

  • Adverse events: defined as any unexpected or harmful occurrence in the participant, such as catheter removal, endotracheal tube removal, pain leading to discontinuation of therapy, or arterial hypotension or hypertension, reported in absolute numbers or proportions (Hodgson 2014). We will report non‐serious and serious adverse events separately.

Secondary outcomes

  • Delirium severity: measured by validated scales such as the CAM‐ICU‐7 Delirium Severity Scale (Khan 2017; Krewulak 2020), or other tools as defined by study authors

  • Cognition/cognitive function: defined as the intellectual or mental process whereby an organism obtains knowledge, assessed with the Montreal Cognitive Assessment (MoCA) or the Mini‐Mental State Examination (MMSE) tools (Pinto 2019; Rose 2021)

  • Mortality in the ICU (Rose 2021)

  • ICU length of stay: defined as the number of days participants remain hospitalised in the ICU until first leave or death (Blackwood 2019; Rose 2021)

  • Hospital length of stay: defined as the number of days participants remain hospitalised in a healthcare institution until first leave or death (Blackwood 2019; Rose 2021).

Timing of outcome measurement

We will consider outcomes measured up to 30 days after randomisation as short‐term outcomes and those measured more than 30 days after randomisation as long‐term outcomes. When studies report multiple results for each outcome, we will include the longest follow‐up in each category.

Minimally important differences

There is no reported threshold for dichotomous outcomes; therefore, we will consider the minimally important difference (MID) for these outcomes as a relative risk reduction of at least 25% (Guyatt 2011). For HRQOL, we will consider the MID to be a mean change of 0.074 in EQ‐5D (Walters 2005). For other continuous outcomes without an established MID, we will consider an MID of 0.5 standard deviations (Salas Apaza 2021).

Search methods for identification of studies

Electronic searches

We will search the following sources from inception to the date of the search without restrictions on the date, language, or status of publication.

  • Cochrane Central Register of Controlled Trials (CENTRAL; current issue) in the Cochrane Library (Appendix 1)

  • MEDLINE Ovid SP and Epub Ahead of Print, In‐Process, In‐Data‐Review & Other Non‐Indexed Citations, Daily and Versions (1946 onwards; Appendix 2)

  • Embase Ovid (1974 onwards; Appendix 3)

  • Cumulative Index to Nursing and Allied Health Literature (CINAHL) EBSCOhost (1937 onwards; Appendix 4)

  • PsycINFO via Proquest (1967 onwards; Appendix 5)

We will also search the U.S. National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (clinicaltrials.gov) and the World Health Organization (WHO) International Clinical Trials Registry Platform search portal (apps.who.int/trialsearch/) using the search strategy described in Appendix 6.

Searching other resources

We will check the reference lists of all included studies and relevant review articles for additional references. We will contact authors of included studies and experts in the field to identify additional unpublished materials. We will search for errata or retractions of included studies.

Data collection and analysis

Selection of studies

Two review authors (of DI, GO, MB, and LG) will independently screen the titles and abstracts of all records returned by the search and eliminate those that are clearly irrelevant. Next, we will retrieve the full‐text publications of all potentially eligible records, and two review authors (of DI, GO, MB, and LG) will independently assess them against our eligibility criteria, recording reasons for exclusion of ineligible studies. We will resolve any disagreements through discussion or, if required, by consulting a third review author (JVAF). We will identify and exclude duplicates and collate multiple reports of the same study so that each study, rather than each report, is the unit of interest in the review.

We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Page 2021). We will use Covidence software for study selection (Covidence).

Data extraction and management

To extract study characteristics and outcome data, we will use a data collection form that we have piloted on at least one included study. One review author (of DI, GO, MB, and LG) will extract the following study characteristics.

  • Methods: study design, total duration of the study, details of any 'run‐in' period, number of study centres and location, study setting, withdrawals, date of the study

  • Participants: number, mean age, age range, sex, severity of the condition, delirium diagnostic criteria, inclusion and exclusion criteria

  • Interventions: intervention type (passive/active mobilisation, use of cycle‐ergometer, ambulation‐type exercise, etc.), intervention characteristics (doses, frequency, duration, intervention provider), comparison, co‐interventions, excluded medications

  • Outcomes: primary and secondary outcomes specified and collected, time points reported

  • Notes: funding for the trial, notable conflicts of interest of trial authors

Two review authors (of DI, GO, MB, and LG) will independently extract outcome data from the included studies. We will note in the 'Characteristics of included studies' table if outcome data are not reported in a usable way. We will calculate or convert the reported data into the required format for meta‐analysis when needed, following guidance from Chapters 5 and 6 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2023a). We will resolve disagreements by consensus or by involving a third review author (JVAF). One review author (LG) will transfer data into Review Manager (RevMan) software (RevMan Web 2022). A second review author (JVAF) will double‐check correct data entry by comparing the outcome data presented in the systematic review with the study reports. JVAF will also spot‐check study characteristics against the trial reports.

Assessment of risk of bias in included studies

Two review authors (of DI, GO, MB, and LG) will independently assess the risk of bias for our main outcomes (those included in the 'Summary of findings' table, see Summary of findings and assessment of the certainty of the evidence) in each study using the Cochrane risk of bias tool (RoB 2; Flemyng 2023; Higgins 2023a; Sterne 2019). We will resolve any disagreements by discussion or by involving another review author (JVAF). We will assess the risk of bias according to the following domains.

  • The randomisation process

  • Deviations from intended interventions

  • Missing outcome data

  • Measurement of the outcome

  • Selection of the reported results

Answers to signalling questions and supporting information will collectively lead to a domain‐level judgement ('low risk of bias', 'some concerns', or 'high risk of bias'). These domain‐level judgements will inform an overall risk of bias judgment for the outcome. We will consider the algorithm‐proposed judgements and provide a quote from the study report together with a justification for our judgement in the risk of bias table. We will also provide reasons for judgements that do not follow the algorithm. We will summarise the risk of bias judgements across different studies for each of the domains listed. When judging 'Bias due to deviations from intended interventions', we will focus the analyses on the effect of assignment to intervention (Flemyng 2023; Higgins 2023b). We will aim to source published study protocols for the assessment of selective reporting. Where information on the risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the risk of bias table.

For cluster‐RCTs, we will use the dedicated version of RoB 2 (available at www.riskofbias.info), as recommended in Chapter 23 of the Cochrane Handbook for Systematic Reviews of Interventions (section 23.1.2 and Table 23.1.a; Higgins 2023c). In addition to the domains listed above, RoB 2 for cluster‐RCTs covers bias arising from the timing of identification and recruitment of participants.

We will make summary assessments of the risk of bias for each short‐ and long‐term result for each outcome (across domains) within and across studies (Higgins 2023b).

We will use the RoB 2 Excel tool to manage the data supporting the answers to the signalling questions and risk of bias judgements (available at www.riskofbias.info/). All these data will be publicly available as supplementary material in the Open Science Framework platform (osf.io/).

When considering treatment effects, as part of the GRADE methodology, we will take into account the risk of bias in the studies that contribute to the outcome.

Measures of treatment effect

We will enter the outcome data for each study into the data tables in RevMan to calculate the treatment effects (RevMan Web 2022).

We will analyse dichotomous data as risk ratios (RRs) and continuous data as mean differences (MDs), each with its corresponding 95% confidence interval (CI). Where different studies measure the same continuous outcome in different ways, we will pool the results using the standardised mean difference (SMD) and 95% CI. We will enter data presented as a scale with a consistent direction of effect. If necessary, we will combine final values and change‐from‐baseline scores for continuous outcomes. We will ensure that higher scores for continuous outcomes have the same meaning for the particular outcome, explain the direction to the reader, and report where the directions are reversed if this is necessary. We will express time‐to‐event data as hazard ratios (HRs) with 95% CIs.

Unit of analysis issues

Where a single trial has multiple trial arms, we will include only the treatment arms relevant to the review topic. If two comparisons (e.g. exercise intervention A versus usual treatment and exercise intervention B versus usual treatment) are combined in the same study, we will follow the guidance in section 6.2 of the Cochrane Handbook for Systematic Reviews of Interventions to avoid double‐counting (Higgins 2023d). Our preferred approach will be to combine groups to create a single pairwise comparison. For cluster‐RCTs, we will consider the cluster as the unit of analysis, not the individual participants, to avoid unit‐of‐analysis errors, as described in section 23.1.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2023c). If the effect measure for the cluster is not determined by appropriate methods in the included studies, we will multiply the standard error of the effect estimate (from an analysis ignoring clustering) by the square root of the design effect, calculated using an intracluster (or intraclass) correlation coefficient (ICC) of 0.02, following guidance in sections 23.1.4 and 23.1.5 of the Cochrane Handbookfor Systematic Reviews of Interventions (Higgins 2023c).

Dealing with missing data

We will contact investigators or study sponsors to verify key study characteristics and obtain missing numerical outcome data as needed (e.g. when a study is identified as abstract only). If we are unable to obtain continuous outcome data from the investigators or study sponsors, we will impute the mean from the median (i.e. consider the median as the mean) and the standard deviation from the standard error, interquartile range, or P values, according to methods presented in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2023a). We will assess the impact of including such studies through sensitivity analysis. If we are unable to calculate the standard deviation from the standard error, interquartile range, or P values, we will impute the standard deviation as the highest standard deviation in the remaining trials included in the outcome. For our primary analyses, we will conduct available‐case analyses, considering these issues when assessing the risk of bias and the certainty of the evidence.

Assessment of heterogeneity

We will investigate whether participants, interventions, comparisons, outcomes, and study designs are sufficiently similar to ensure a clinically meaningful answer to the review question.

We will use the I² statistic to measure statistical heterogeneity amongst the trials in each analysis. If we identify substantial heterogeneity, we will report it and explore possible causes by prespecified subgroup analyses. We will also assess heterogeneity by visual inspection of forest plots, evaluating the direction and magnitude of effects and the degree of overlap between CIs.

We will use the following rough guide to interpret I² values, as outlined in Chapter 10 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2023).

  • 0% to 40%: might not be important.

  • 30% to 60%: may represent moderate heterogeneity.

  • 50% to 90%: may represent substantial heterogeneity.

  • 75% to 100%: represents considerable heterogeneity.

We will avoid using absolute cut‐off values, but will interpret I² in relation to the size and direction of effects and strength of evidence for heterogeneity. We will perform random‐effects meta‐analysis, which accounts for between‐study heterogeneity.

Assessment of reporting biases

We will attempt to obtain study protocols to assess the presence of selective outcome reporting.

If we are able to pool more than 10 trials, we will create and examine funnel plots to explore possible small‐study and publication biases. As the presence of asymmetry in funnel plots may have several explanations besides publication bias, we will interpret the results carefully. If searches identify trial protocols, clinical trial registrations, or abstracts indicating the existence of unpublished studies, we will attempt to determine their status by contacting the investigators.

We will consider outcome reporting bias in our risk of bias assessments.

Data synthesis

Meta‐analysis of numerical data

If more than one study provides usable data in any single comparison, we will perform a meta‐analysis using RevMan (RevMan Web 2022). We will undertake meta‐analyses only if the treatments, participants, and the underlying clinical question are sufficiently similar for pooling to make sense. We will use a random‐effects model, as this is usually a more conservative approach. For dichotomous outcomes, we will use the Mantel‐Haenszel method; for continuous outcomes, we will use the inverse variance method.

We will include all studies in the primary analysis, and we will explore the effect of bias in sensitivity analyses (see Sensitivity analysis).

Synthesis using other methods

If meta‐analysis is not possible due to incompletely reported outcome data or clinical and methodological diversity, we will perform a narrative synthesis of the available quantitative data following guidance in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions (McKenzie 2023b), as well as the latest guidance on Synthesis Without Meta‐analysis (SWiM; Campbell 2020). When available, we will report the absolute number of events for each outcome and the corresponding statistics (P values). If sufficient data are available, we will report RRs or HRs and their 95% CIs or risk differences when the absolute risk in both groups is below 1%. We will summarise the results using vote counting based on the direction of effect, prioritising the findings from larger studies and, when available, studies at low risk of bias. In this scenario, we will assess heterogeneity qualitatively, and we will follow GRADE methods for assessing the overall certainty of evidence, presenting results in a summary of findings table.

Subgroup analysis and investigation of heterogeneity

We plan to carry out subgroup analyses based on the following factors.

  • Age (< 65 years, ≥ 65 years), as delirium is reported to have especially harmful outcomes in people older than 65 years, and this may alter the effects of the intervention (Gao 2021; Li 2020)

  • Different ICU populations (medical only, surgical only, mixed populations; Vasilevskis 2012)

  • Delirium subtype (hyperactive, hypoactive, mixed), as different subtypes of delirium have different prognoses and associated complications that may affect patients' ability to undertake progressive mobilisations or exercises (Girard 2008; Hayhurst 2016; Hayhurst 2020)

  • Pre‐existing dementia (yes/no)

  • Characteristics of the intervention (stand‐alone intervention or care bundle)

We will assess the influence of the factors listed above on the following outcomes.

  • Duration of delirium/time to delirium resolution

  • HRQOL

  • Adverse events

  • Delirium severity

We will use the formal Chi2 test for subgroup differences to test for subgroup interactions.

Sensitivity analysis

We will perform sensitivity analysis of our primary outcomes to assess the robustness of our conclusions. The sensitivity analysis will involve excluding studies with an overall high risk of bias.

Summary of findings and assessment of the certainty of the evidence

We will create a summary of findings table for the following comparisons using GRADEpro GDT software (GRADEpro GDT).

  • Exercise therapy versus no intervention or usual care

  • Exercise therapy versus any pharmacological treatment

Each summary of findings table will present the following outcomes.

  • Duration of delirium/time to delirium resolution (long term)

  • HRQOL (long term)

  • Adverse events (long term)

  • Delirium severity (long term)

  • ICU length of stay (long term)

Two reviewers (of DI, GO, MB, and LG) will use the GRADE approach, as described in Chapter 14 of the Cochrane Handbook for Systematic Reviews of Interventions,to assess the certainty of the body of evidence based on the studies that contribute data to the meta‐analyses for each outcome (Schünemann 2023). With GRADE, evidence from RCTs is considered to be high certainty initially, but can be downgraded by one or two levels based on limitations related to five considerations (risk of bias, inconsistency, imprecision, indirectness, and publication bias). We will downgrade evidence once if a GRADE consideration is serious and twice if very serious. For the risk of bias consideration, we will follow the guidance in Table 14.2.a of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2023). We will consider a partially contextualised approach when downgrading for imprecision (Hultcrantz 2017). We will resolve any disagreements by discussion or by involving another review author (JVAF).

We will justify all decisions to downgrade or upgrade the certainty of evidence in the footnotes and provide comments to aid the reader's understanding of the review where necessary. We will consider whether there is additional outcome information that was not incorporated into the meta‐analyses, note this in the comments, and state if it supports or contradicts the information from the meta‐analyses.

If meta‐analysis is not possible, we will present results in a narrative summary of findings table, providing key information about the best estimate of the magnitude of the effect in relative terms and absolute differences for each relevant comparison, numbers of participants and studies addressing each outcome, and the rating of the overall confidence in effect estimates for each outcome, following guidance in section 14.1 of the Cochrane Handbook for Systematic Reviews of Interventions (Schünemann 2023).

We will formulate statements for the findings and certainty of the evidence using wording templates that combine the size and certainty of an effect to improve the clarity of communication (Santesso 2020).