Information or education interventions for adult intensive care unit (ICU) patients and their carers

Types of studies

We will include randomised controlled trials (RCTs) or quasi-RCTs (i.e. trials in which randomisation is attempted but subject to potential manipulation, such as allocating participants by day of the week, date or birth, or sequence of entry into trial), with a parallel design. We will include cluster RCTs to enable inclusion of studies that assign the ICU, rather than individual patients, to the intervention or control group/arm.

Types of participants

Adult (aged 18 years and above) ICU patients and critically-ill patients in high-dependency care units regardless of their status (e.g. conscious, unconscious, intubated) or length of stay. We will also include carers of these patients (whether relatives or non-relatives) because the psychological status of both can be affected by a patient’s critical illness and stay in the ICU (Davidson 2007; Haines 2015; Kross 2015).

If studies include adults and children, we will include the study if the mean age of participants is 18 years or above.

Types of interventions

We will include information or education interventions, which we define as any intervention designed to improve a patient or carer's knowledge or understanding of the prognosis, treatment plan or challenges likely to affect the patient during their transition from the ICU. Information or education interventions may be delivered in different formats, such as written (e.g. leaflet), verbal (e.g. counselling), or digital (e.g. phone or tablet application, recorded message). We acknowledge the difficulties associated with delineating the definitions of information and education interventions (Kaufman 2013); and for the purpose of this review we will essentially consider them as variants of the same thing. The intervention should be additional or different to that provided in the comparator group (e.g. information pamphlet versus no information pamphlet). We require the intervention to be delivered by treating clinicians, nurses, or support teams.

We will also include studies of more complex interventions, if a component of the intervention involves the provision of information with the aim of improving a patient’s knowledge or understanding of the topics listed above and provision is more than that delivered in the comparator group (i.e. if the effects of the information or education intervention can be isolated from the rest of the complex intervention). Finally, we will also include studies that employ ‘sham’ controls (e.g. where patients are assigned to receive an ICU-specific pamphlet versus a non-specific pamphlet).

We will include the following comparisons:

1. information or education interventions versus no information or education interventions;

2. information or education interventions as a component of a complex intervention (e.g. information or education intervention plus drug therapy) versus complex intervention without the information or education intervention component (e.g. drug therapy alone).

The intervention may be presented to either the patient, carer or both.

Types of outcome measures

Electronic searches

We will search the following electronic databases:

• the Cochrane Central Register of Controlled Trials (CENTRAL);

• MEDLINE (OvidSP);

• Embase (OvidSP);

• PsycINFO (OvidSP);

• CINAHL (EBSCO host);

• ISI Web of Science; and

• LILACS (BIRERME interface).

We will also search Clinicaltrials.gov (www.clinicaltrials.gov) and the World Health Organization (WHO) trials portal (www.who.int/ictrp/en/) for ongoing and recently completed studies. All databases will be searched from their date of inception until present, with no restriction on region or language of publication. We present the strategy for MEDLINE (OvidSP) in Appendix 1. We will tailor strategies to other databases and report them in the review.

Searching other resources

We will check the references of all relevant primary studies and review articles (from 2010 onwards) to identify additional studies that may be relevant to the review. We will contact experts in the field and authors of included studies for advice about other relevant studies. 

Selection of studies

Two authors will independently screen all titles and abstracts identified from searches to determine which of them meet the inclusion criteria. We will retrieve in full text any papers identified as potentially relevant. Two review authors will independently screen full-text articles for inclusion or exclusion, with discrepancies resolved by discussion and by consulting a third author if necessary to reach consensus. All potentially-relevant papers excluded from the review at this stage will be listed as excluded studies, with reasons provided in the ‘Characteristics of excluded studies’ table. We will also provide citation details and any available information about ongoing studies, and collate and report details of duplicate publications, so that each study (rather than each report) is the unit of interest in the review. We will report the screening and selection process in an adapted PRISMA flow chart (Liberati 2009).

Data extraction and management

Two review authors will extract data independently from included studies. Any discrepancies will be resolved by discussion until consensus is reached, or through consultation with a third author where necessary. We will develop and pilot a data extraction form using the Cochrane Consumers and Communication Data Extraction Template (available at: cccrg.cochrane.org/author-resources). We will extract the following details of the included studies: funding source, declaration of interests for the primary investigators, aim of intervention, study design and duration, study setting, description of intervention and comparator (to include whether it is generic or personalised and frequency of intervention); and the following participant characteristics by intervention/comparator group: number randomised, number excluded from analyses, age, body mass index, measure of illness (e.g. APACHE-II score, Glasgow Coma score, SOFA score), health literacy and intubation status. We will use this information to populate the ‘Characteristics of included studies’ table. We will also extract outcome data from the results of the included studies (see Primary outcomes and Secondary outcomes). All extracted data will be entered into RevMan (RevMan 2014) by one review author, and will be checked for accuracy against the data extraction sheets by a second review author working independently.

Assessment of risk of bias in included studies

We will assess and report on the methodological risk of bias of included studies in accordance with the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011) and the Cochrane Consumers and Communication guidelines (Ryan 2013), which recommend the explicit reporting of the following individual elements for RCTs: random sequence generation; allocation sequence concealment; blinding (participants, personnel); blinding (outcome assessment); completeness of outcome data, selective outcome reporting; and other sources of bias (e.g. imbalances in baseline characteristics of intervention and comparator groups). We will consider blinding separately for different outcomes where appropriate (for example, blinding may have the potential to differently affect subjective versus objective outcome measures). For cluster RCTs we will also assess and report the risk of bias associated with an additional domain: selective recruitment of cluster participants. We will judge each item as being at high, low or unclear risk of bias as set out in the criteria provided by Higgins 2011, and provide a quote from the study report and a justification for our judgement for each item in the 'Risk of bias' table. We will assess and report quasi-RCTs as being at a high risk of bias on the random sequence generation item of the 'Risk of bias' tool.

Studies will be deemed to be at the highest risk of bias if they are scored as being at high or unclear risk of bias for either the sequence generation or allocation concealment domain, based on growing empirical evidence that these factors are particularly important potential sources of bias (Higgins 2011). We will conduct sensitivity analyses (excluding studies at unclear or high risk) to investigate the effects of this decision on effect estimates.

In all cases, two authors will independently assess the risk of bias of included studies, with any disagreements resolved by discussion to reach consensus. We will contact study authors for additional information about the included studies, or for clarification of the study methods as required. We will incorporate the results of the 'Risk of bias' assessment into the review through standard tables, and systematic narrative description and commentary about each of the elements, leading to an overall assessment of the risk of bias of included studies and a judgement about the internal validity of the review’s results.

Measures of treatment effect

For RCTs, quasi-RCTs and cluster RCTs, we will analyse continuous outcome data (i.e. potentially all of the primary and secondary outcomes) based on the mean, standard deviation (SD) and number of people assessed for both the intervention and comparison groups, to calculate mean difference (MD) and 95% CI. If the MD is reported without individual group data, we will use this to report the study results. If more than one study measures the same outcome using different tools, we will calculate the standardised mean difference (SMD) and 95% CI using the inverse variance method in RevMan (RevMan 2014). If necessary, we will analyse the dichotomous outcomes based on the number of events and the number of people assessed in the intervention and comparison groups; we will calculate risk ratios and 95% CI, or Mantel-Haenszel odds ratio (OR) when the outcome is an infrequent event (approximately less than 10%), or Peto OR when the outcome is very rare (e.g. < 1%). We will provide a narrative description of skewed data reported as medians and interquartile ranges.

Unit of analysis issues

We will not include cross-over trials in this review. Where multiple trial arms are reported in a single trial, we will include only the relevant arms. If two comparisons (e.g. intervention A versus no intervention and intervention B versus no intervention) are combined in the same meta-analysis, we will halve the control group (e.g. no intervention) to avoid double-counting. If cluster RCTs are included we will check for unit of analysis errors. If errors are found, and sufficient information is available, we will re-analyse the data using the appropriate unit of analysis, by taking account of the intra-cluster correlation (ICC). We will obtain estimates of the ICC by contacting authors of included studies, or impute them using estimates from external sources. If it not possible to obtain sufficient information to re-analyse the data we will report effect estimates and annotate "unit of analysis error".

Dealing with missing data

We will attempt to contact study authors to obtain missing data (participant, outcome, or summary data). For participant data, we will, where possible, conduct analysis on an intention-to-treat basis; otherwise data will be analysed as reported. We will report on the levels of loss to follow-up and assess this as a source of potential bias.

For missing outcome or summary data we will impute missing data where possible (for methods relevant to dichotomous data, see Higgins 2008) and report any assumptions in the review. We will investigate, through sensitivity analyses, the effects of any imputed data on pooled effect estimates.

Assessment of heterogeneity

Where studies are considered to be sufficiently similar (based on consideration of populations, interventions and setting) for pooling of data using meta-analysis, we will assess the degree of heterogeneity by visual inspection of forest plots and by examining the Chi² test for heterogeneity. Heterogeneity will be quantified using the I² statistic. An I² value of 50% or more will be considered to represent substantial levels of heterogeneity, but this value will be interpreted in light of the size and direction of effects and the strength of the evidence for heterogeneity, based on the P value from the Chi² test (Higgins 2011).

Where we detect substantial clinical, methodological or statistical heterogeneity across included studies we will not report pooled results from meta-analysis but will instead use a narrative approach to data synthesis. In this event we will attempt to explore possible clinical or methodological reasons for this variation by grouping studies that are similar in terms of populations, intervention features, or other factors, to explore differences in intervention effects.

Assessment of reporting biases

We will assess reporting bias qualitatively based on the characteristics of the included studies (e.g. if only small studies that indicate positive findings are identified for inclusion), and if information that we obtain from contacting experts and authors or studies suggests that there are relevant unpublished studies.

If we identify sufficient studies (at least 10) for inclusion in the review we will construct a funnel plot to investigate small study effects (Sterne 2011), which may indicate the presence of publication bias. We will formally test for funnel plot asymmetry, with the choice of test made based on advice in Higgins 2011, and bearing in mind that there may be several reasons for funnel plot asymmetry when interpreting the results.

Data synthesis

We will decide whether to meta-analyse data based on whether the interventions in the included trials are similar enough in terms of participants, settings, intervention, comparison and outcome measures to ensure meaningful conclusions from a statistically pooled result. Due to the anticipated variability in the populations and interventions of included studies, we will use a random-effects model for meta-analysis.

If we are unable to pool the data statistically using meta-analysis we will conduct a narrative synthesis of results. We will present the major outcomes and results, organised by intervention categories according to the major types of the identified interventions (e.g. verbal, written, digital). Within these categories we will explore the main comparisons of the review. Depending on the assembled research we may also explore grouping the data based on other categories (e.g. by population). Within each category we will present the data in tables and narratively summarise the results.

Subgroup analysis and investigation of heterogeneity

The effect of an information or education intervention might be expected to vary with different characteristics of the intervention itself, such as format (e.g. brochure versus one-to-one education session), frequency (e.g. a single verbal counselling session versus six, monthly sessions), specificity (e.g. tailored versus non-tailored information) or information provider (e.g. doctor or nurse). The condition of the participant may also affect the participant's ability to receive or comprehend the information or education. For example, intubation status may influence the effectiveness of information interventions that are designed to be bidirectional between patient and healthcare provider, as the intubated patient would likely find it more difficult to communicate questions to the physician or nurse. We consider it unlikely that consciousness level would influence the results (and will not perform a subgroup analysis by consciousness level) in as much as it would not be possible to deliver an information intervention to an unconscious patient. We have not excluded this population of patients as the intervention may have a beneficial effect on the unconscious patient's carer. Therefore we will perform the following subgroup analyses to investigate these potential effect modifiers:

1. type of intervention: tailored versus non-tailored;

2. type of intervention platform: verbal versus written versus digital;

3. category of information provider: doctor versus nurse versus psychologist versus support worker;

4. frequency of intervention: once (e.g. one-off verbal counselling session) versus multiple sessions (e.g. six, monthly verbal counselling sessions); and

5. intubation status of the participant: intubated versus non-intubated patients.

If it is not possible to pool data statistically, or if there are too few included studies to warrant statistical subgroup analyses, we will present a narrative form of subgroup analyses.

Sensitivity analysis

We plan to carry out the following sensitivity analyses:

1. unpublished data (i.e. no peer-reviewed full-text paper available);

2. trials with inadequate or unclear methods of random sequence generation or allocation concealment (i.e. high risk or unclear risk of selection bias);

3. studies with missing data (e.g. to examine the effect of imputed data or data based on assumptions);

4. treatment effect: random-effects model versus fixed-effect model; and

5. dichotomous outcomes: Mantel-Haenszel OR versus Peto OR.