Types of studies

We will consider all randomised controlled trials (RCTs) and quasi‐randomised studies, as we anticipate that there may not be many properly randomised controlled trials looking at different intervention formats. Quasi‐randomised trials are those in which randomisation is attempted but subject to potential manipulation, such as allocating participants by day of the week, date of birth, or sequence of entry into trial.

We will also include cluster‐randomised studies in which groups of individuals rather than individuals are randomised. The groups or clusters may be formed by different hospitals or different surgeons.

Types of participants

We will include trials of people aged over 16 years undergoing elective surgery requiring general, spinal or epidural anaesthesia. Studies will be eligible for inclusion if the majority of the participants were aged over 16 years. Trials of people undergoing emergency surgery will not be included as the time and planning of any educational intervention will be limited. We are restricting the study population to those undergoing surgical operations requiring general, spinal or epidural anaesthesia as the process of anaesthesia itself is a source of anxiety and we wish to minimise the differences between studies.

Types of interventions

We will include studies delivering an educational intervention within three months before the planned surgery in one of the following formats:

• printed written material

• audio intervention or telephone call

• video/digital video disc (DVD)

• computer ‐ web‐based learning

• mobile‐phone based ‐ text message

The educational intervention should provide procedural or sensory information about the planned surgery, anaesthetic, the expected postoperative course and symptoms to be expected. The information delivered may also include behavioural instruction such as suggestions of physical exercises. This information may be in combination with other psychological interventions but we will not include any intervention offering only psychological skills training.

Types of outcome measures

Electronic searches

We will search the following electronic databases:

• The Cochrane Central Register of Controlled Trials (CENTRAL, The Cochrane Library, latest issue);

• MEDLINE (OvidSP) (1980 to present);

• EMBASE (OvidSP) (1980 to present);

• CINAHL (EBSCO) (1980 to present).

• PsycINFO (EBSCO) (1980 to present).

• ProQuest Dissertations & Theses (1980 to present)

We present the strategy for MEDLINE (OvidSP) in Appendix 1. We will tailor this strategy to other databases and report them in the review.

We will include any publication that reports study data, including abstracts, letters and articles. There will be no language restrictions but we will start searching from 1980 onwards. We do not think that earlier studies will be relevant due to restricted range of possible formats before 1980. Changes in health service delivery since 1980 mean that studies of different timing of interventions may not be applicable to the current healthcare situation with its emphasis on day surgery.

Searching other resources

We will also search trial registers such as www.clinicaltrials.gov, Current Controlled Trials (http://www.controlled‐trials.com/) and the International Clinical Trials Registry Platform (http://apps.who.int/trialsearch/) for ongoing trials and recently completed studies. We will undertake forward citation tracking for key review articles and eligible articles identified from the electronic resources using IS Web of Science. We will also carry out backward citation tracking by checking the reference lists of key review articles and eligible articles. We will contact experts in the field and authors of included studies for advice as to other relevant studies. 

Selection of studies

Results of the searches will be collated and duplicates removed. The selection of eligible articles will take place in two stages.

All titles and abstracts will be screened by Amanda Nicholson (AN) and Sharon Lewis (SL) to remove studies that are very unlikely to be eligible. A pilot of 100 titles will be performed before all titles are reviewed in order to clarify criteria for discarding articles at this stage. If no abstract is available but the title may be relevant, we will obtain the full text of the article.

When all titles and abstracts have been screened, the full text of potentially‐relevant studies will be assessed by two of the five investigators and recorded on the study eligibility form. A pilot of 10 papers will be read and then the investigators will meet to compare results and modify the form as required. All potentially‐relevant papers will then be read and the two investigators will meet to compare results. Differences that cannot be resolved will be referred to Anna Lee (AL)/Andrew Smith (AS)/Chris Coldwell (CC). The numbers of papers retrieved and exclusions at each stage – with reasons for those reviewed in full text – will be recorded in a PRISMA flowchart (Liberati 2009). Reasons for excluding ineligible papers which are well‐known or might appear to be eligible will be summarised in the Characteristics of Excluded Studies table.

Data extraction and management

Data will be extracted from eligible studies by two investigators working independently using a paper extraction form developed and piloted using the Cochrane Consumers and Communication Review Group Data Extraction Template (available at: http://cccrg.cochrane.org/author‐resources). This form will be reviewed after data from the first three papers have been entered, and modified as required. If there are duplicate publications from the same study, we will create a composite dataset from all the eligible publications. Data to be extracted will include the following items:

• Study design: randomisation unit, cluster or patient; sequence generation or other randomisation method.

• Power calculations, baseline risk and effect size assumed.

• Patient group: age, demographic, type of surgical operation, baseline anxiety and other coping styles.

• Content of educational intervention (classified as procedural information, sensory information and/or behavioural information)

• Intervention group format and timing details such as duration of video, size of pamphlet, format and timing, training of any staff delivering interventions.

• Comparison group: format and timing of intervention, additional features.

• Co‐interventions; other training given alongside educational intervention.

• Outcomes: outcomes and timepoints i. collected, ii. reported. For each outcome: definition, unit of measurement, timing.

• Subgroups measured and reported.

• Results: numbers of participants (and number of clusters) assigned to each intervention group. For each outcome: sample size, summary data for each intervention (two by two table where possible for dichotomous data, means and standard deviations for continuous data), P values and confidence intervals. If results are reported separately for subgroups, data will be extracted.

• Funding sources and declarations of interests.

All extracted data will be entered into RevMan (Review Manager 2012) by one review author, and will be checked for accuracy against the data extraction sheets by a second review author working independently. If relevant information or data are not available in the paper, we will contact the lead author to request the additional details. Disagreements will be resolved by discussion and if necessary by consultation with AL/AS. We will display the different formats, components and timepoints of the educational interventions within included studies in an additional table to allow an overview across studies.

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 (Higgins 2011) and the guidelines of the Cochrane Consumers and Communication Review Group (Ryan 2011), 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. We will consider blinding separately for different outcomes where appropriate (for example, blinding may have the potential to affect subjective versus objective outcome measures differently). 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.

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, allocation concealment or performance bias domains, based on growing empirical evidence that these factors are particularly important potential sources of bias (Higgins 2011). 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. For cluster‐RCTs we will also assess and report on the risk of bias associated with an additional domain: selective recruitment of cluster participants. It is impossible for participants in these studies to be blinded to their allocation so when assessing performance bias we will pay particular attention to the content of the educational intervention and whether this was likely to have varied between different formats or timings. Studies where we felt there was a high risk that the content of intervention differed between formats will be considered to be at high risk of bias.

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 judgment about the internal validity of the review’s results.

Measures of treatment effect

Many of the outcomes for this review are continuous measures, measured on validated or widely‐used scales such as the STAI for anxiety and visual analogue scales for pain or satisfaction. For continuous measures, we will analyse data 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% confidence interval (CI). If the MD is reported without individual group data, we will use this to report the study results. For anxiety we will analyse studies which have used the same scale together initially. 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 Review Manager 5 (Review Manager 2012). Costs of the educational intervention will be standardised to UK pounds in 2012 using the Cochrane ‘CCEMG – EPPI‐Centre Cost Converter’ (v.1.2) and the standardised values used in the review (http://eppi.ioe.ac.uk/costconversion/default.aspx).

Some studies may use scales for anxiety or knowledge to create binary outcomes by classifying all participants above or below a certain level as high and/or low. For these and other dichotomous outcomes, such as cancellation, we will analyse data based on the number of events and the number of people assessed in the intervention and comparison groups. We will use these to calculate the risk ratio (RR) and 95% CI.

Unit of analysis issues

For any cluster trials included in the review, we will extract data directly from the publication only if the analysis used accounts for the cluster design with a method such as multi‐level modelling or generalised estimating equations. If these adjustments are not made within the report, we will undertake approximate analyses by recalculating standard errors or sample sizes based on the design effect and intraclass correlation (ICC). We will obtain estimates of the ICC by contacting authors of included studies, or impute them using estimates from external sources. The resulting effect estimates and their standard errors will be analysed using the generic inverse variance method in RevMan. If it is not possible to obtain sufficient information to reanalyse the data we will report effect estimates and annotate with ‘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. If data allow, we will perform sensitivity analyses to compare the effect of complete case analysis, worst case scenario and last observation carried forward options on the results of individual studies and any meta‐analyses.

Assessment of heterogeneity

For each comparison, for example video versus written material, we expect that the findings for any given outcome may differ between studies included in the review. This heterogeneity may be due to:

• Differences in the study population, including age, geographical and cultural context, literacy and familiarity with digital technology, baseline anxiety and coping style, type of operation

• Details of format, e.g. differences in duration of video, size of pamphlet

• Content of educational intervention (classified as procedural information, sensory information and behavioural information) and co‐interventions

• Timing of intervention (for studies of different format)

• Format of intervention (for studies of different timing)

Where studies are considered similar enough on the above factors to allow 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 study population and content and precise format details of the intervention features 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 of 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, 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. Heterogeneity between studies may lead to asymmetry and we will consider this possibility when reviewing results.

Data synthesis

The comparisons included in the review will depend on the final included studies. For each format group considered, such as printed written material, we will not pool studies with different comparison groups. For example, studies in which written material was replaced by video will not be pooled with studies in which video was used in addition to written material. For each comparison, we will pool data only if the included trials are similar enough to ensure meaningful conclusions from a statistically pooled result. We will consider variation in participants, settings, intervention, comparison and outcome measures as well as statistical measures of heterogeneity described above (Assessment of heterogeneity). Due to the anticipated variability in the populations of included studies, we will use a random‐effects model for meta‐analysis.

If we do not have adequate comparable data to pool the data statistically using meta‐analysis for some comparisons, we will present a narrative synthesis of results. We will present the major outcomes and results, organised by intervention/comparison categories.

Subgroup analysis and investigation of heterogeneity

The acceptability of different formats and delivery will vary across different groups of participants. The content of education material will vary between surgical procedures, and visual information or diagrams may be more important in some topics than others. We will consider the effect of the intervention on subgroups organised by:

• content of educational intervention (classified as procedural information, sensory information and behavioural information)

• age and gender

• educational level

• type of surgery

We will use subgroup data as reported by study authors but will note whether subgroups were specified a priori and whether the randomisation was stratified on the subgroup variable. We will investigate heterogeneity and the difference in effect sizes between subgroups using the test for heterogeneity between groups in RevMan software. If we have sufficient data we will investigate further using random‐effects meta‐regression.

Sensitivity analysis

We will assess the robustness of our results using sensitivity analyses. We will assess the impact of studies assessed as being as high risk of bias on our results by removing them from pooled analyses, paying particular attention to studies at high risk of bias for sequence generation. If we have made assumptions about missing outcome data, we will run analyses with alternative assumptions to compare results.