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We included published and unpublished randomised controlled trials (RCTs), including multi‐armed studies, cluster‐RCTs and cross‐over trials, regardless of the language of publication.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 people with a diagnosis of pressure ulcer of any stage (EPUAP/NPIAP/PPPIA 2019), managed in any care setting. We accepted study authors' definitions of pressure ulcer stage. Where study authors used grading scales other than NPIAP, we mapped these to the NPIAP scale (EPUAP/NPIAP/PPPIA 2019).

Types of interventions

We included studies that assessed beds and mattresses (i.e. integrated bed systems, mattresses and overlays) (see Description of the intervention). The types of bed and mattress support surfaces we planned to cover included:

• alternating pressure (active) air surfaces (e.g. alternating pressure air mattress, dynamic low‐air‐loss mattresses, Softform Premier Active air mattresses);

• foam surfaces;

• reactive air surfaces (e.g. Sofflex static air overlay);

• reactive fibre surfaces (e.g. Silicore fibre overlay);

• reactive gel surfaces (e.g. a gel pad used on an operating table);

• reactive sheepskin surfaces (e.g. Australian Medical Sheepskins overlay); and

• reactive water surfaces.

We planned to include studies where two or more bed and mattress support surfaces were used sequentially over time or in combination, where the beds or mattresses of interest would have been included in one of the study arms. However, we did not identify such studies.

We included studies comparing eligible beds, overlays and mattresses against any comparator defined as a bed, overlay or mattress. Comparators were not limited to any specific type of support surfaces. They could be either different from, or the same type as, the eligible bed, overlay or mattress of interest. 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

Electronic searches

We searched the following 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);

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

• Embase Ovid (1974 to 14 November 2019);

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

The search strategies for the Cochrane Wounds Specialised Register, CENTRAL, MEDLINE Ovid, Embase Ovid and EBSCO CINAHL Plus can be found in Appendix 2. We combined the MEDLINE Ovid 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 checked all RCTs included in the Cochrane Review McInnes 2018 against our eligibility criteria.

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 2018, the review authors of McInnes 2018 contacted experts in the field of wound care to enquire about potentially relevant studies that were ongoing or recently published. In addition, the review authors of McInnes 2018 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.

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

Selection of studies

One review author (CS) re‐checked the RCTs included in McInnes 2018 for eligibility. Two review authors (CS and AJB) 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 resolved disagreements through discussion or by involving a third review author (JCD), if necessary.

Data extraction and management

One review author (CS) checked data from the studies included in McInnes 2018, and extracted additional data where necessary. A second review author or researcher (SR, AJB, VR, EM, Zhenmi Liu, Gill Norman, or Melanie Stephens) checked any new data extracted. For new included studies, one review author (CS) independently extracted data and another review author or researcher (SR, AJB, VR, EM, Zhenmi Liu, Gill Norman, or Melanie Stephens) checked all data (Differences between protocol and review). Any disagreements were resolved through discussion or, if necessary, by involving another review author (JCD). Where necessary, we contacted the authors of included studies (or referred to relevant publications) 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 the stage of pressure ulcers at baseline);

• bed and mattress 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;

• proportion of participants with pressure ulcers healed;

• data on time to pressure ulcer healing (e.g. Kaplan Meier plot, hazard ratio (HR) and 95% confidence interval (CI));

• comfort/discomfort outcome data;

• adverse event outcome data;

• health‐related quality of life outcome data; and

• cost‐effectiveness outcome data.

We (CS and NC) classified specific beds and mattresses in the included studies into intervention groups using the NPIAP S3I terms and definitions related to support surfaces (NPIAP S3I 2007). Therefore, to accurately assign specific beds and mattresses 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 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, AJB, VR, 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, by implementing strict protocols to maximise consistency of co‐interventions between groups to reduce the risk of performance bias. We also noted that complete pressure ulcer healing 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 factors such as extreme baseline imbalance and unit of analysis under the domain of 'other issues' (see Appendix 3). 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 2018, one review author (CS) checked the 'Risk of bias' judgements and, where necessary, updated them. A second review author or researcher (SR, AJB, VR, 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, or by involving another review author (JCD) 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 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 trial by all of the 'Risk of bias' items. Once judgements had been given for all domains, the overall risk of bias for each study was judged 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 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, or by involving another review author (JCD) 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 2016; Higgins 2019) (Appendix 3). However, we did not include any studies with a cluster design.

Measures of treatment effect

For meta‐analysis of data on the proportion of participants with pressure ulcers healed, we present the risk ratio (RR) with its 95% confidence interval (CI). For continuous outcome data (e.g. healing rate in terms of change in the area of the ulcers), we present the mean difference (MD) with 95% CIs for studies that used 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 (e.g. time to pressure ulcer healing), we present the hazard ratio (HR) with its 95% CI. If included studies reporting time‐to‐event data did not report an HR, then, 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 the pressure ulcer or at the level of participants. We also recorded whether the same participant was reported as having multiple pressure ulcers. Where studies randomised at the participant level and outcomes were measured at the level of the ulcer, we considered the participant as the unit of analysis if the number of ulcers observed appeared to be equal to the number of participants (e.g. one pressure ulcer per person).

Unit of analysis issues may occur if studies randomise at the participant level but the healing of multiple pressure ulcers is observed and data are presented and analysed at the level of the ulcer (clustered data). We noted whether data regarding multiple ulcers on a participant were (incorrectly) treated as independent within a study, or were analysed using within‐participant 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 (see below) 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 introduce 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 the proportion of participants with pressure ulcers healed we assumed that participants with missing data had ulcers healed 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). Where 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 24 weeks (medium‐term); and

• more than 24 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 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 will 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 intervals 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 data on the proportion of participants with pressure ulcers healed. To make an overall judgement about risk of bias due to missing results, we:

• identified whether the missing outcome 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 outcome 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, beds and mattresses 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% CI. 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 the proportion of participants with pressure ulcers healed.

• Impact of the selection of healing outcome measure. The proportion of pressure ulcers completely healed was the primary outcome measure for this review but we also analysed time to pressure ulcer healing, where data were available.

• Impact of missing data. The primary analysis assumed that the ulcers of participants with missing data had healed; we also analysed healing by only including data for the participants for whom we had endpoint data (complete cases).

• 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 for binary outcome data) 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 alternating pressure (active) air surfaces versus the another type of alternating pressure (active) air surfaces (Differences between protocol and review). We presented these outcomes in the 'Summary of findings' tables:

• proportion of participants with pressure ulcers healed;

• time to pressure ulcer healing;

• patient support‐surface‐associated 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).