Introduction

Delirium is a frequent complication after cardiac surgery affecting between one-quarter and one-half of all patients.1 It is a clinical syndrome characterised by a disturbance in attention, awareness and cognition, which usually starts on postoperative days 1–5 and can fluctuate in severity throughout the day.2 Peak incidence is on the second postoperative day. It has been categorised as either hyperactive, hypoactive or mixed. Individuals with hyperactive delirium have heightened arousal and can be agitated and restless, whereas those with hypoactive delirium are withdrawn and lethargic. Its aetiology is multifactorial, resulting from the interaction of patient risk factors and perioperative insult. Patient risk factors include surgical risk, older age, prior neurological or psychiatric disease, and previous substance abuse. Perioperative risk factors include length of cardiopulmonary bypass (CPB)3 and type of surgery performed; valve surgery is associated with an increased incidence of delirium compared with coronary artery bypass grafting (CABG) surgery.4 Experiencing delirium after cardiac surgery is associated with poor outcomes, including over twice the risk of short-term and long-term mortality,1 decreased functional status5 and increased risk of long-term cognitive dysfunction.6 It also adds around $10 000 to the hospital costs per patient.7

Many of the risk factors for delirium after cardiac surgery are non-modifiable.3 A number of interventions have been tried to prevent delirium after cardiac surgery. These include both pharmacological and non-pharmacological approaches. Pharmacological approaches include antipsychotic medications such as haloperidol and risperidone.8 Other pharmacological approaches have included different anaesthesia and postoperative regimens such as dexmedetomidine,9 avoidance of benzodiazepines10 and use of ketamine.11 Non-pharmacological approaches include preoperative cognitive training,12 use of sleep protocols, early mobilisation, cognitive stimulation and encouraging sensory normalisation with glasses and hearing aids.13 Many of the interventions are often used together in multi-component interventions,14 although these complex interventions are rarely fully validated and tested.

The mechanisms of action of these interventions on delirium postcardiac surgery are complex and not fully understood. Since the biochemical changes of delirium are widespread, the interventions target a broad range of mechanisms. Non-pharmacological interventions work by encouraging sensory normalisation (eg, giving patients their glasses and hearing aids), providing the correct environmental stimuli that people are used to (eg, maintaining day/night orientation with adequate lighting and noise management, using calendar and clocks, getting patients out of bed as quickly as possible, and explaining to patients what is being done to them). Pharmacological interventions are centred around minimising the duration and depth of sedation (both intraoperatively and after surgery), preventing agitation and optimising physiological status (eg, maintaining normal fluid-electrolyte balance, body temperature, oxygenation, blood sugar and blood pressure).

Individuals who experience delirium after cardiac surgery are at increased risk of short-term and long-term complications, leading to a reduced quality of life and a significant economic burden. In the short term, patients often have prolonged mechanical ventilation, prolonged length of hospital and intensive care unit (ICU) stay and increased risk of hospital mortality.15 Longer term, patients are at increased risk of cognitive decline and its associated morbidity as well as increased overall long-term mortality.1 Because delirium may be preventable, attention has moved to strategies to reduce its incidence. Therefore, identifying effective preventive interventions is important. A number of interventions have been investigated. However, the literature is extensive and can be conflicting, making an optimal approach unclear. As a result, the interventions used to prevent delirium vary within and between institutions and a unanimous approach is lacking. This review aims to provide a comprehensive, up-to-date overview of all interventions (both pharmacological and non-pharmacological) to prevent delirium after cardiac surgery.

The specific objectives are to:

Identify all randomised controlled trials (RCTs) investigating interventions to prevent delirium after cardiac surgery.

Compare the effectiveness of different interventions on the incidence and duration of delirium after cardiac surgery using standard meta-analysis and, where feasible, network meta-analysis.

Describe the safety of the different interventions.

Methods and analysis

This systematic review will follow guidance from the Preferred Reporting Items for Systematic Reviews and Meta-Analyses (PRISMA)16 and the PRISMA extension for Network Meta-Analyses.17

Types of studies

We will include all published and unpublished RCTs, including trials with more than two groups (eg, comparing different interventions or different dosing regimens of the same intervention). RCTs will be included irrespective of design and date and will not be restricted to the English language. Non-English studies will be translated into English.

Types of participants

Adults (≥18 years) who are undergoing cardiac surgery—CABG surgery, heart valve surgery and thoracic aortic surgery. We will exclude patients who are emergencies (requiring surgery before the start of the next working day) or have pre-existing delirium. Less than 1% of cardiac surgery is emergency surgery and they represent a separate cohort of patients to the majority of patients who undergo cardiac surgery. They may already be under anaesthesia or sedation, have an acute illness severity that is significantly higher, and they are more likely to need prolonged ventilation and sedation than most patients undergoing cardiac surgery.

Types of interventions

We will include both pharmacological and non-pharmacological delirium prevention/treatment interventions delivered before, during or after the surgery.

We will include trials that compare any intervention with placebo (eg, pharmacological) or usual care (eg, non-pharmacological interventions) and trials that compare different interventions against each other (eg, two pharmacological strategies, different dosing regimens of the same drug, etc). We will also include multi-group studies that compare multiple interventions or multiple doses of an intervention against a placebo/usual care/another drug regimen. We will carefully document information about any group defined as usual care since we know that different institutions have markedly different usual care pathways in terms of intraoperative protocols, ICU sedation protocols, etc.

Types of outcome measures

While there are core outcomes sets for ICU delirium, there is no core outcome set for cardiac surgery specifically. However, there is a substantial cross-over between our chosen outcomes and those of the core outcome set for ICU.

Primary outcomes

Incidence of delirium within 7 days of surgery.

Secondary outcomes

Duration of postoperative delirium (days).

All-cause mortality (30 days and up to 1 year).

Length of postoperative hospital stay (days).

Length of postoperative ICU stay (days).

Postoperative neurological complications other than delirium (eg, seizures, stroke).

Health-related quality of life (up to 1 year).

Intervention-specific adverse events (AEs).

Intervention specific outcomes (eg, pain scores for a postoperative pain prevention intervention).

Feasibility and implementation outcomes (eg, to what extent interventions were delivered as intended, adherence to the intervention protocols, etc).

Electronic searches

We will search the following electronic databases using relevant keywords, subject headings (controlled vocabularies) and search syntax. We will not restrict the search by date, language or publication status.

CLib:CDSR (Reviews) (Issue 5, May 2022).

CLib:CENTRAL (Trials) (Issue 5, May 2022).

MEDLINE Ovid (1946–23 May 2022).

Embase Ovid (1974–23 May 2022).

PsycINFO Ovid (1806–May week 3 2022).

We will search the following trial registers for ongoing or unpublished trials:

US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (www.clinicaltrials.gov/; all available years).

WHO International Clinical Trials Registry Platform (apps.who.int/trialsearch/; all available years).

Our search strategy is available in online supplemental additional material.18

Selection of studies

Using Rayyan,19 seven review authors (BG, MP, ECdC, JDB, TW-S, RP, RK) will independently screen batches of titles and abstracts to identify potentially eligible studies. Each title and abstract will be screened independently by two review authors, each of whom will code it as either included, excluded or maybe. If there are any disagreements, a third review author will arbitrate. Full-text papers will be retrieved for all studies deemed eligible or studies that do not provide sufficient information to exclude at the screening stage. Teams of two review authors will independently screen each full-text paper; studies not meeting the inclusion criteria will be excluded and the reasons for exclusion will be recorded. Disagreements will be resolved by discussion and consensus with a third review author. The study selection process will be presented in a PRISMA flow diagram.

Data extraction and management

Two review authors will independently extract data from each included study onto a prespecified data extraction form. Disagreements will be resolved through discussions with a third review author. The following data will be extracted from each study:

Publication details (authors, title, date of publication, country of origin, language if not published in English, funding source, authors’ conflicts of interest).

Methods: total duration of study, number of study centres, study setting, study design, withdrawals and date of study.

Participants: demographics, inclusion and exclusion criteria, comorbidities, number of participants randomised to each group, whether intention-to-treat analysis was performed.

Procedure characteristics: type of surgery (eg, CABG, valve surgery, combined CABG and valve surgery, thoracic aorta surgery), elective or urgent pathway.

Interventions: intervention(s) and comparator. These will be intervention specific. Drug, dose, duration.

Outcomes: number of participants assessed for the primary and secondary outcomes specified and the time points at which they were reported. The procedure for diagnosing delirium and the instrument used for diagnosis will also be collected.

We will contact the trial authors for information if any of the above data items are missing.

Assessment of risk of bias in included studies

Risk of bias for each included study will be assessed independently by at least two review authors. We will use The Cochrane Collaboration’s new tool (RoB2)20 for assessing risk of bias and rate the quality of each trial (low risk, high risk and some concern) in overall risk of bias. We will assess the risk of bias according to the following domains:

Bias arising from the randomisation process.

Bias due to deviations from the intended interventions.

Bias due to missing outcome data.

Bias in measurement of the outcome.

Bias in selection of the reported result.

Blinding of participants and healthcare professionals in trials of non-pharmacological interventions is difficult and complete blinding may not be possible. To account for outcome-specific variation in the bias domains affected by lack of blinding (2 and 4 above), we will group our outcomes for the purpose of risk of bias assessment for these bias domains as follows.

For the primary outcome (incidence of delirium), knowledge of intervention status, particularly for non-pharmacological interventions, may lead to deviations from the intended interventions, for example, healthcare professionals may inadvertently change aspects of care in ways that could influence the likelihood of developing delirium. Delirium diagnosis is highly likely to be subjective (if the assessor does not use the assessment instrument correctly or consistently or is influenced by knowledge of the intervention status of the patient). Therefore, we will judge a study at high risk of bias for domain 2 and 4 if healthcare professionals looking after the patients or those assessing the delirium outcome are not blinded, and some concern if this information is not provided.

All-cause mortality, hospital readmission and length of stay (ICU/hospital) are objective, easy to measure and less likely to be influenced by deviations from intended interventions or by lack of blinding of outcome assessors. These will be judged as low risk of bias for bias domains 2 and 4 regardless of whether participants, healthcare personnel or outcome assessors are blinded or not.

Health-related quality of life, although a patient-reported outcome that may be prone to bias if the patient is not blinded to their intervention status, will be judged at low risk of bias as patients will likely complete questionnaires after they receive the intervention and recover from delirium, so knowledge of intervention status is less likely to influence how they respond.

Assessment of bias in conducting the systematic review

We will conduct the systematic review according to the published protocol and report and deviations from it in the ‘Differences between protocol and review’ section of the review.

Measures of treatment effect

We will calculate pooled risk ratios and 95% CIs for dichotomous outcomes (eg, delirium, mortality, stroke). For continuous outcomes (eg, patient-reported outcomes), we will calculate pooled mean differences and 95% CIs when results are reported on the same scale (or can be converted to the same scale), or standardised mean differences and 95% CI if results are reported on different scales. Where mean and SD are not reported, we will derive these from the reported test statistics (eg, SD from SEs or 95% CIs) or estimate them from other summary statistics (eg, mean and SD from median and range). Some studies may report means but not SDs; in this case, we will estimate SD from the mean of the SDs reported in other similar studies (assessing a similar intervention) within that treatment arm. If no appropriate data are available, then the outcome will be reported narratively. Medians and ranges will be transformed into means and SDs using the method of Hozo, Djulbegovic and Hozo.21

Unit of analysis issue

If we identify any cluster trials, we will take into account statistical clustering in our analyses. Where trials include multiple intervention groups and a single control group, we will only use data from the intervention groups that meet our inclusion criteria. If both intervention groups are eligible for inclusion, we will divide the number randomised to the control group in half to use as a denominator for each intervention group, but we will keep the means and SDs for the control group the same.

Dealing with missing data

If the study authors do not report the required data in the publication, we will first attempt to back-calculate from data presented (eg, numerator or denominator from percentages; SD from SE or 95% CI). If this is not possible, we will attempt to contact the study authors to request the missing data. Where this is not possible and missing data are thought to introduce serious bias, we will explore the impact of including such studies in the overall assessment of results by a sensitivity analysis .

Assessment of heterogeneity

We will assess clinical heterogeneity across studies by examining variability in the details of participants, baseline data, interventions and outcomes to determine whether studies are similar, and visually inspecting forest plots. The I2 statistic will be calculated to quantify and interpret statistical heterogeneity.22

We will apply the following thresholds for the interpretation of the I2 statistic:

0%–40%, might not be important.

30%–60%, may represent moderate heterogeneity.*

50%–90%, may represent substantial heterogeneity.*

75%–100%, represents considerable heterogeneity.*

*The importance of the observed value of the I2 statistic depends on (a) the magnitude and direction of effects and (b) the strength of evidence for heterogeneity (eg, p value from the χ2 test, or a CI for the I2 statistic). If our I2 statistic value indicates that heterogeneity is a possibility and either the Tau2 is greater than zero or the p value is low (less than 0.10), heterogeneity may be due to a factor other than chance.

If we identify substantial heterogeneity (see notes on interpreting the I2 statistic value above), we will report it and explore possible causes by prespecified subgroup analyses (see the Subgroup analyses and investigation of heterogeneity section).

Reporting biases

For all analyses in which treatment effects from 10 or more RCTs are synthesised, we will use funnel plots and the Egger test to examine small study bias for the primary outcomes.23

Data synthesis

Given the array of interventions to prevent delirium after cardiac surgery, we will undertake meta-analyses only when there are three or more studies where the treatments, participants and underlying clinical question are similar enough for pooling to make sense. However, even with similar interventions, there is likely to be substantial heterogeneity in the interventions and their delivery. Given this likely clinical heterogeneity, we will use random effects meta-analysis models for our primary analysis to pool data across trials. However, since random effect models upweight small studies which may be at higher risk of bias, we will undertake a sensitivity analysis and repeat all analyses with statistically significant results using a fixed-effects meta-analysis model. The findings from the included studies will be summarised in narrative form, following the Synthesis Without Meta-analysis guideline24 if we do not find trials that are sufficiently similar to justify a meta-analysis. We will perform the data synthesis using Review Manager (Review Manager 2014) and STATA (StataCorp 2020). A draft summary of findings tables are available in online supplemental additional tables.18

Network meta-analysis

If appropriate, we will conduct a network meta-analysis of interventions based on direct comparisons to generate indirect comparisons of interventions across trials. This will return rankings for the interventions in terms of their effectiveness.

Subgroup analyses and investigation of heterogeneity

If there is sufficient data available, we will perform the following subgroup analyses using stratified meta-analysis and/or meta-regression:

Type of surgery—CABG versus valve versus both.

Intervention pathway—urgent versus elective (urgent surgery—surgery performed as an inpatient, usually after a precipitating event for example, acute coronary syndrome. Elective surgery—surgery performed at a time to suit both the patient and the surgeon).

Sensitivity analyses

We will use sensitivity analysis to assess the robustness of the results and for situations where it might affect the interpretation of significant results. The sensitivity analysis will allow us to evaluate the impact of including studies at risk of bias or missing data such as impact of borderline decisions. We plan to carry out the following sensitivity analyses.

Including only trials classified as having overall low risk of bias rating.

Excluding trials with more than 20% drop out rate to assess the impact of missing data on results and conclusions.

Including only trials with ≥100 participants.

Including only published trials (not abstracts).

Conducting fixed-effects meta-analyses for any analyses with statistically significant results using the random-effects model.

If we believe that there is a large amount of missing data that will lead to serious bias, then we will explore the impact of including such studies by a sensitivity analysis (dealing with missing data).

We will assess the overall risk of bias using The Cochrane Collaboration’s new tool (RoB2).20 Low risk of bias is defined as ‘low risk of bias’ in all domains for this outcome.

Summary of findings and assessment of certainty of evidence

We will use GRADEProfiler software to assess the certainty of evidence for all outcomes reported in the review (GRADEpro GDT). We will downgrade the evidence from high certainty by one level for each of the following factors: indirectness of evidence, unexplained heterogeneity, publication bias, risk of bias due to study design limitations and imprecision of results.25