Types of studies

We included published and unpublished randomised controlled trials (RCTs), including multi‐armed studies, cluster‐RCTs and cross‐over trials, regardless of the language of publication. We excluded studies using quasi‐random allocation methods (e.g. alternation).

Types of participants

We included studies in any population, including those defined as being at risk of ulceration, as well as those with existing pressure ulcers at baseline (when the study measured pressure ulcer incidence).

Types of interventions

This review focused on reactive air beds or mattresses in general. Eligible studies included a specific bed, overlay or mattress with reactive or static pressure redistribution capabilities. These included, but were not limited to, specific reactive air mattresses identified in Shi 2018a; namely:

• powered or non‐powered reactive air mattresses (e.g. Sofflex static air mattress); or

• powered or non‐powered reactive low‐air‐loss mattresses (e.g. low‐air‐loss Hydrotherapy); or

• powered or non‐powered reactive air‐fluidised mattresses (e.g. Clinitron air‐fluidised bed).

We included studies where two or more support surfaces were used sequentially over time or in combination, where the support surface(s) of interest were included in one of the study arms.

We included studies comparing eligible reactive air beds, overlays or mattresses against any comparator defined as a support surface. Comparators could be:

• non‐reactive air surfaces, including: alternating pressure (active) air surfaces such as alternating pressure (or dynamic) air mattresses, foam mattresses, and non‐foam and non‐air‐filled surfaces (e.g. reactive gel surfaces such as a gel pad used on an operating table, reactive fibre surfaces such as Silicore fibre overlay, reactive water surfaces, reactive sheepskin surfaces such as Australian Medical Sheepskins overlay), or

• a different type of reactive air surface.

We included studies in which co‐interventions (e.g. repositioning) were delivered, provided that the co‐interventions were the same in all arms of the study (i.e. interventions randomised were the only systematic difference).

Types of outcome measures

We considered the primary and secondary outcomes described below. If a study did not report any review‐relevant outcomes but was otherwise eligible (i.e. eligible study design, participants and interventions), we contacted the study authors (where possible) to clarify whether they had measured a relevant outcome but did not report it. We considered the study as 'awaiting classification' if we could not establish whether it measured an outcome or not. We excluded the study if the study authors confirmed that they did not measure any review‐relevant outcomes.

If a study measured an outcome at multiple time points, we considered the outcome measures at three months to be the primary endpoint for this review (Schoonhoven 2007), regardless of the time points specified as being of primary interest by the study. If the study did not report three‐month outcome measures, we considered those closest to three months. Where a study only reported a single time point, we included this in this review. Where the study did not specify a time point for outcome measurement, we assumed this was the final duration of follow‐up noted.

Electronic searches

We searched the following electronic databases to identify reports of relevant clinical trials:

• the Cochrane Wounds Specialised Register (searched 14 November 2019);

• the Cochrane Central Register of Controlled Trials (CENTRAL; 2019, Issue 10) in the Cochrane Library (searched 14 November 2019);

• Ovid MEDLINE including In‐Process & Other Non‐Indexed Citations (1946 to 14 November 2019);

• Ovid Embase (1974 to 14 November 2019);

• EBSCO CINAHL Plus (Cumulative Index to Nursing and Allied Health Literature; 1937 to 14 November 2019).

The search strategies for the Cochrane Wounds Specialised Register, CENTRAL, Ovid MEDLINE, Ovid Embase and EBSCO CINAHL Plus can be found in Appendix 2. We combined the Ovid MEDLINE search with the Cochrane Highly Sensitive Search Strategy for identifying randomised trials in MEDLINE: sensitivity‐ and precision‐maximising version (2008 revision) (Lefebvre 2019). We combined the Embase search with the Ovid Embase filter developed by the UK Cochrane Centre (Lefebvre 2019). We combined the CINAHL Plus search with the trial filter developed by (Glanville 2019). There were no restrictions with respect to language, date of publication or study setting.

We also searched the following clinical trials registries:

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (clinicaltrials.gov) (searched 20 November 2019);

• World Health Organization (WHO) International Clinical Trials Registry Platform (https://www.who.int/clinical-trials-registry-platform) (searched 20 November 2019).

Search strategies for clinical trials registries can be found in Appendix 2.

Searching other resources

For previous versions of McInnes 2015, the review authors of McInnes 2015 contacted experts in the field of wound care to enquire about potentially relevant studies that are ongoing or recently published. In addition, the review authors of McInnes 2015 contacted manufacturers of support surfaces for details of any studies manufacturers were conducting. This approach did not yield any additional studies; therefore, we did not repeat it for this review.

We identified other potentially eligible studies or ancillary publications by searching the reference lists of retrieved included studies, as well as relevant systematic reviews, meta‐analyses and health technology assessment reports.

When necessary, we contacted authors of key papers and abstracts to request further information about their trials.

We did not perform a separate search for adverse effects of interventions used. We considered adverse effects described in included studies only.

Selection of studies

One review author re‐checked the RCTs included in McInnes 2015 for eligibility (CS). Two review authors or researchers (CS and Asmara Jammali‐Blasi, or JCD) independently assessed the titles and abstracts of the new search results for relevance using Rayyan (Ouzzani 2016) (Differences between protocol and review), and then independently inspected the full text of all potentially eligible studies. The two review authors or researchers (CS and Asmara Jammali‐Blasi, or JCD) resolved any disagreements through discussion or by involving another review author if necessary.

Data extraction and management

One review author checked data from the studies included in McInnes 2015 and extracted additional data where necessary (CS). A second review author or researcher checked any new data extracted (SR, VL, EM, Zhenmi Liu, Gill Norman, or Melanie Stephens). For new included studies, one review author (CS) independently extracted data and another review author or researcher checked all data (SR, VL, EM, Zhenmi Liu, Gill Norman, or Melanie Stephens) (Differences between protocol and review). Any disagreements were resolved through discussion and, if necessary, with the involvement another review author. Where necessary, we contacted the authors of included studies to clarify data.

We extracted these data using a pre‐prepared data extraction form:

• basic characteristics of studies (first author, publication type, publication year and country);

• funding sources;

• care setting;

• characteristics of participants (trial eligibility criteria, average age in each arm or in a study, proportions of participants by gender and participants’ baseline skin status);

• support surfaces being compared (including their descriptions);

• details on any co‐interventions;

• duration of follow‐up;

• the number of participants enrolled;

• the number of participants randomised to each arm;

• the number of participants analysed;

• participant withdrawals with reasons;

• the number of participants developing new ulcers (by ulcer stages where possible);

• data on time to pressure ulceration;

• support‐surface‐associated patient comfort;

• adverse event outcome data;

• health‐related quality of life outcome data; and

• cost‐effectiveness outcome data.

We (CS and NC) classified specific support surfaces in the included studies into intervention groups using the NPIAP S3I support surface‐related terms and definitions (NPIAP S3I 2007). Therefore, to accurately assign specific support surfaces to intervention groups, we extracted full descriptions of support surfaces from included studies, and when necessary supplemented the information with that from external sources such as other publications about the same support surface, manufacturers’ or product websites and expert clinical opinion (Shi 2018b). If we were unable to define any of the specific support surfaces evaluated in an included study, we extracted available data and reported these as additional data outside the main review results.

Assessment of risk of bias in included studies

Two review authors or researchers (CS and SR, VL, EM, Zhenmi Liu, Gill Norman, or Melanie Stephens) independently assessed risk of bias of each included study using the Cochrane 'Risk of bias' tool (see Appendix 3). This tool has seven specific domains: sequence generation (selection bias), allocation concealment (selection bias), blinding of participants and personnel (performance bias), blinding of outcome assessment (detection bias), incomplete data (attrition bias), selective outcome reporting (reporting bias), and other issues (Higgins 2017). We assessed performance bias, detection bias and attrition bias separately for each of the review outcomes (Higgins 2017). We noted that it is often impossible to blind participants and personnel in device trials. In this case, performance bias may be introduced if knowledge of treatment allocation results in deviations from intended interventions, differential use of co‐interventions or care between groups not specified in the study protocol that may influence outcomes. We attempted to understand if, and how, included studies compensated for challenges in blinding; for example, implementing strict protocols to maximise consistency of co‐interventions between groups to reduce the risk of performance bias. We also noted that pressure ulcer incidence is a subjective outcome. Compared with blinded assessment, non‐blinded assessment of subjective outcomes tends to be associated with more optimistic effect estimates of experimental interventions in RCTs (Hróbjartsson 2012). Therefore, we judged non‐blinded outcome assessment as being at high risk of detection bias. In this review, we included the issues of differential diagnostic activity and unit of analysis under the domain of 'other issues'. For example, unit of analysis issues occurred where a cluster‐randomised trial had been undertaken but analysed at the individual level in the study report.

For the studies included in McInnes 2015, one review author (CS) checked the 'Risk of bias' judgements and, where necessary, updated them. A second review author or researcher (SR, VL, EM, Zhenmi Liu, Gill Norman, or Melanie Stephens) checked any updated judgement. We assigned each 'Risk of bias' domain a judgement of high, low, or unclear risk of bias. We resolved any discrepancy through discussion and by involving another review author where necessary. Where possible, useful and feasible, when a lack of reported information resulted in a judgement of unclear risk of bias, we planned to contact study authors for clarification.

We present our assessment of risk of bias for the proportion of participants developing a new pressure ulcer outcome using two 'Risk of bias' summary figures. One is a summary of bias for each item across all studies, and the second shows a cross‐tabulation of each study by all of the 'Risk of bias' items.

Once we had given our judgements for all 'Risk of bias' domains, we judged the overall risk of bias for each outcome across studies as:

• low risk of bias, if we judged all domains to be at low risk of bias;

• unclear risk of bias, if we judged one or more domains to be at unclear risk of bias and other domains were at low risk of bias but no domain was at high risk of bias; or

• high risk of bias, as long as we judged one or more domains as being at high risk of bias, or all domains had unclear 'Risk of bias' judgements, as this could substantially reduce confidence in the result.

We resolved any discrepancy between review authors through discussion and by involving another review author where necessary. For studies using cluster randomisation, we planned to consider the risk of bias in relation to recruitment bias, baseline imbalance, loss of clusters, incorrect analysis and comparability with individually randomised studies (Eldridge 2019; Higgins 2019; Appendix 3). However, we did not include any studies with a cluster design.

Measures of treatment effect

For meta‐analysis of pressure ulcer incidence data, we present the risk ratio (RR) with its 95% confidence interval (CI). For continuous outcome data, we present the mean difference (MD) with 95% CIs for studies that use the same assessment scale. If studies reporting continuous data used different assessment scales, we planned to report the standardised mean difference (SMD) with 95% CIs. However, this was not undertaken in the review.

For time‐to‐event data (time to pressure ulcer incidence), we present the hazard ratio (HR) with its 95% CI. If included studies reporting time‐to‐event data did not report an HR, when feasible, we estimated this using other reported outcomes (such as numbers of events) through employing available statistical methods (Parmar 1998; Tierney 2007).

Unit of analysis issues

We noted whether studies presented outcomes at the level of cluster (e.g. ward, research site) or at the level of participants. We also recorded whether the same participant was reported as having multiple pressure ulcers.

Unit of analysis issues may occur if studies randomise at the cluster level but the incidence of pressure ulcers is observed and data are presented and analysed at the level of participants (clustered data). We noted whether data regarding participants within a cluster were (incorrectly) treated as independent within a study, or were analysed using within‐cluster analysis methods. If clustered data were incorrectly analysed, we recorded this as part of the 'Risk of bias' assessment.

If a cluster‐RCT was not correctly analysed, we planned to use the following information to adjust for clustering ourselves where possible, in accordance with guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2019).

• The number of clusters randomly assigned to each intervention, or the average (mean) number of participants per cluster.

• Outcome data ignoring the cluster design for the total number of participants.

• Estimate of the intra‐cluster (or intra‐class) correlation coefficient (ICC).

However, we did not identify any cluster‐RCTs in this review.

Dealing with missing data

Data are commonly missing from study reports. Reasons for missing data could be the exclusion of participants after randomisation, withdrawal of participants from a study, or loss to follow‐up. The exclusion of these data from analysis may break the randomisation and potentially introduces bias.

Where there were missing data, and where relevant, we contacted study authors to pose specific queries about these data. In the absence of other information, for pressure ulcer incidence we assumed that participants with missing data did not develop new pressure ulcers for the main analysis (i.e. we added missing data to the denominator but not the numerator). We examined the impact of this assumption through undertaking a sensitivity analysis (see Sensitivity analysis). When a study did not specify the number of randomised participants prior to dropout, we used the available number of participants as the number randomised.

Assessment of heterogeneity

Assessing heterogeneity can be a complex, multifaceted process. Firstly, we considered clinical and methodological heterogeneity; that is, the extent to which the included studies varied in terms of participant, intervention, outcome, and other characteristics including duration of follow‐up, clinical settings, and overall study‐level 'Risk of bias' judgement (Deeks 2019). In terms of the duration of follow‐up, in order to assess the relevant heterogeneity, we recorded and categorised assessment of outcome measures as follows:

• up to eight weeks (short‐term);

• more than eight weeks to 16 weeks (medium‐term); and

• more than 16 weeks (long‐term).

We supplemented this assessment of clinical and methodological heterogeneity with information regarding statistical heterogeneity assessed using the Chi² test. We considered a P value of less than 0.10 to indicate statistically significant heterogeneity given that the Chi² test has low power, particularly in the case where studies included in a meta‐analysis have small sample sizes. We carried out this statistical assessment in conjunction with the I² statistic (Higgins 2003), and the use of prediction intervals for random‐effects meta‐analyses (Borenstein 2017; Riley 2011).

The I² statistic is the percentage of total variation across studies due to heterogeneity rather than chance (Higgins 2003). Very broadly, we considered that I² values of 25% or less may indicate a low level of heterogeneity and values of 75% or more may indicate very high heterogeneity (Higgins 2003). For random‐effects models where the meta‐analysis had more than 10 included studies and no clear funnel plot asymmetry, we also planned to present 95% prediction intervals (Deeks 2019). We planned to calculate prediction intervals following methods proposed by Borenstein 2017.

Random‐effects analyses produce an average treatment effect, with 95% confidence intervals indicating where the true population average value is likely to lie. Prediction intervals quantify variation away from this average due to between‐study heterogeneity. The interval conveys where a future study treatment effect estimate is likely to fall based on the data analysed to date (Riley 2011). Prediction intervals are always wider than confidence intervals (Riley 2011).

It is important to note that prediction intervals reflect heterogeneity of any source, including from methodological issues as well as clinical variation. For this reason some authors have suggested that prediction intervals are best calculated for studies at low risk of bias to ensure intervals that have meaningful clinical interpretation (Riley 2011). We had planned to calculate prediction intervals for all analyses to assess heterogeneity and then to explore the impact of risk of bias in subgroup analysis stratified by study risk of bias assessment as detailed below. However, we did not calculate any prediction interval because all conducted meta‐analyses contained fewer than 10 studies.

Assessment of reporting biases

We followed the systematic framework recommended by Page 2019 to assess risk of bias due to missing results (non‐reporting bias) in the meta‐analysis of pressure ulcer incidence data. To make an overall judgement about risk of bias due to missing results, we did the following.

• Identified whether pressure ulcer incidence data were unavailable by comparing the details of outcomes in trials registers, protocols or statistical analysis plans (if available) with reported results. If the above information sources were unavailable, we compared outcomes in the conference abstracts or in the methods section of the publication, or both, with the reported results. If we found non‐reporting of study results, we then judged whether the non‐reporting was associated with the nature of findings by using the 'Outcome Reporting Bias In Trials' (ORBIT) system (Kirkham 2018).

• Assessed the influence of definitely missing pressure ulcer incidence data on meta‐analysis.

• Assessed the likelihood of bias where a study had been conducted but not reported in any form. For this assessment, we considered whether the literature search was comprehensive and planned to produce a funnel plot for meta‐analysis for seeking more evidence about the extent of missing results, provided there were at least 10 included studies (Peters 2008; Salanti 2014).

However, we did not produce a funnel plot for any meta‐analysis because all analyses in this review had fewer than 10 included studies.

Data synthesis

We summarised the included studies narratively and synthesised included data by using meta‐analysis where applicable. We structured comparisons according to type of comparator and then by outcomes, ordered by follow‐up period.

We considered clinical and methodological heterogeneity and undertook pooling when studies appeared appropriately similar in terms of participants, support surfaces, and outcome type. Where statistical synthesis of data from more than one study was not possible or considered inappropriate, we conducted a narrative review of eligible studies.

Once the decision to pool was made, we used a random‐effects model, which estimated an underlying average treatment effect from studies. Conducting meta‐analysis with a fixed‐effect model in the presence of even minor heterogeneity may provide overly narrow confidence intervals. We used the Chi² test and I² statistic to quantify heterogeneity but not to guide choice of model for meta‐analysis (Borenstein 2009). We exercised caution when meta‐analysed data were at risk of small‐study effects because use of a random‐effects model may be unsuitable in this situation. In this case, or where there were other reasons to question the choice of a fixed‐effect or random‐effects model, we assessed the impact of the approach using sensitivity analyses to compare results from alternate models (Thompson 1999).

We performed meta‐analyses largely using Review Manager 5.4 (Review Manager 2020). We presented data using forest plots where possible. For dichotomous outcomes, we presented the summary estimate as a RR with 95% CIs. Where continuous outcomes were measured, we presented the MD with 95% CIs; we planned to report SMD estimates where studies measured the same outcome using different methods. For time‐to‐event data, we presented the summary estimates as HRs with 95% CIs.

Subgroup analysis and investigation of heterogeneity

Sensitivity analysis

We conducted sensitivity analyses for the following factors, to assess the robustness of meta‐analysis of data on pressure ulcer incidence.

• Impact of the selection of pressure ulcer incidence outcome measure. The proportion of participants developing a new pressure ulcer was the primary outcome measure for this review but we also analysed time to pressure ulcer development, where data were available.

• Impact of missing data. The primary analysis assumed that participants with missing data did not develop new pressure ulcers. We also analysed pressure ulcer incidence by only including data for the participants for whom we had endpoint data (complete cases). We noted that when a study only had complete case data (i.e. missing data or the numbers of participants randomised were not reported), complete case data were considered in the related main analysis (Differences between protocol and review).

• Impact of altering the effects model used. We used a random‐effects model for the main analysis followed by a fixed‐effect analysis.

Summary of findings and assessment of the certainty of the evidence

We presented the main, pooled results of the review in 'Summary of findings' tables, which we created using GRADEpro GDT software. These tables present key information concerning the certainty of evidence, the magnitude of the effects of the interventions examined and the sum of available data for the main outcomes (Schünemann 2019). The tables also include an overall grading of the certainty of the evidence associated with each of the main outcomes that we assessed using the GRADE approach. The GRADE approach defines the certainty of a body of evidence as the extent to which one can be confident that an estimate of effect or association is close to the true quantity of specific interest.

The GRADE assessment involves consideration of five factors: within‐trial risk of bias, directness of evidence, heterogeneity, precision of effect estimates, and risk of publication bias (Schünemann 2019). The certainty of evidence can be assessed as being high, moderate, low or very low; RCT evidence has the potential to be high‐certainty. We did not downgrade the certainty of evidence for the risk of bias factor in a specific circumstance. That is, if the blinding of participants and personnel was the only domain resulting in our judgement of overall high risk of bias for the included studies; however for these studies it was impossible to blind participants and personnel.

When downgrading for imprecision, we followed the methods described in Guyatt 2011: either considering both the optimal information size (OIS) and the 95% CI of each meta‐analysis if they were estimable; or considering the sample size, the number of events and other effectiveness indicators if the calculation of OIS and undertaking a meta‐analysis were not applicable. Where necessary, we used the GRADE 'default' minimum important difference values (RR = 1.25 and 0.75) as the thresholds to judge if a 95% CI was wide (imprecise) so as to include the possibility of clinically important harm and benefit (Guyatt 2011).

We presented a separate 'Summary of findings' table for all but one comparison evaluated in this review. The exception was the comparison of reactive air surfaces versus another type of reactive air surface (Differences between protocol and review). We presented these outcomes in the 'Summary of findings' tables:

• proportion of participants developing a new pressure ulcer;

• time to pressure ulcer incidence;

• support‐surface‐associated patient comfort;

• all reported adverse events;

• health‐related quality of life; and

• cost‐effectiveness.

We prioritised the time points and method of outcome measurement specified in Types of outcome measures for presentation in ‘Summary of findings’ tables. Where we did not pool data for some outcomes within a comparison, we conducted a GRADE assessment for each of these outcomes and presented these assessments in a narrative format in 'Summary of findings' tables (Differences between protocol and review).