Beds and mattresses for treating pressure ulcers (2024)

Types of studies

We will include published and unpublished randomised controlled trials (RCTs), including multi‐armed studies, cluster‐RCTs and cross‐over trials, regardless of the language of publication.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

Types of participants

We will include studies in people with a diagnosis of pressure ulcer of any stage (EPUAP/NPIAP/PPPIA 2019), managed in any care setting. We will accept study authors' definitions of pressure ulcer stage. Where study authors used grading scales other than NPIAP, we will attempt to map these to the NPIAP scale (EPUAP/NPIAP/PPPIA 2019).

Types of interventions

We will include 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 will include are:

• alternating pressure (active) air surfaces;

• high‐specification reactive foam surfaces;

• reactive air surfaces;

• reactive fibre surfaces;

• reactive gel surfaces;

• reactive sheepskin surfaces; and

• reactive water surfaces.

We will include studies where two or more bed and mattress support surfaces are used sequentially over time or in combination, where the beds or mattresses of interest are included in one of the study arms.

We will include studies comparing eligible beds and mattresses against any comparator that can be defined as a bed or mattress. We will include studies in which co‐interventions (e.g. repositioning) are delivered, provided that we can assume that the co‐interventions are the same in all arms of the study (i.e. interventions randomised are the only systematic difference).

Types of outcome measures

Electronic searches

We will check all RCTs included in the current version of the Cochrane Review (McInnes 2018) against our eligibility criteria. This will be supplemented by a new updated search.

We will search the following databases to retrieve reports of relevant trials:

• the Cochrane Wounds Specialised Register;

• the Cochrane Central Register of Controlled Trials (CENTRAL) in the Cochrane Library (latest issue);

• Ovid MEDLINE (from 1946 onwards);

• Ovid Embase (from 1974 onwards); and

• EBSCO Cumulative Index to Nursing and Allied Health Literature (CINAHL Plus); from 1937 onwards.

We have devised a draft search strategy for CENTRAL, which is displayed in Appendix 2. We will adapt this strategy to search the Cochrane Wounds Specialised Register, Ovid MEDLINE, Ovid Embase and EBSCO CINAHL Plus. We will combine 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 will combine the Embase search with the Ovid Embase filter terms developed by the UK Cochrane Centre (Lefebvre 2019). We will combine the CINAHL Plus search with the trial filter developed by Glanville 2019. We will not restrict the searches with respect to language, date of publication or study setting.

We will also search the following clinical trials registries for ongoing studies and completed studies that may not have been published:

• ClinicalTrials.gov (clinicaltrials.gov); and

• World Health Organization (WHO) International Clinical Trials Registry Platform (apps.who.int/trialsearch).

Searching other resources

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

We will try to identify 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.

Selection of studies

One review author (CS) will re‐check the RCTs included in the original version of this review for eligibility. Two review authors will independently assess the titles and abstracts of the new search results for relevance using Covidence, and will then independently inspect the full text of all potentially eligible studies. The two review authors will resolve disagreements by discussion and by involving a third review author, if necessary.

Data extraction and management

One review author (CS) will check data from the studies included in the original version of this review (McInnes 2018) and extract additional data where necessary. A second review author will check any new data extracted. For new included studies, two review authors will independently extract data. Any disagreements will be resolved by discussion and, if necessary, with the involvement of a third review author. Where necessary, we will contact the authors of included studies to clarify data.

We will extract the following 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 will classify 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 will extract full descriptions of support surfaces from included studies, and when necessary will supplement 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 2018a).

Assessment of risk of bias in included studies

Two review authors will independently assess 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 2011). We will assess performance bias, detection bias, and attrition bias separately for each of the review outcomes (Higgins 2011). We note 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 will attempt 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 note that complete pressure ulcer healing is a subjective outcome; and 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 will judge non‐blinded outcome assessment as being at high risk of detection bias. In this review we will include 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 will occur where a cluster‐randomised trial has been undertaken but analysed at the individual level in the study report.

For the studies included in the previous version of this review, one review author (CS) will check the 'Risk of bias' judgements and, where necessary, update them. A second review author will check any updated judgement. We will assign each 'Risk of bias' domain a judgement of high, low, or unclear risk of bias. We will resolve any discrepancy between two review authors by discussion and by involving a third review author where necessary. Where possible, when a lack of reported information results in a judgement of unclear risk of bias, we will contact study authors for clarification.

We will present our assessment of risk of bias using two 'Risk of bias' summary figures; one will be a summary of bias for each item across all studies, and the second will show a cross‐tabulation of each trial by all of the 'Risk of bias' items. Once judgements have been given for all domains, the overall risk of bias for each study will be judged as:

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

• unclear risk of bias, if we judge one or more domains to be unclear risk of bias but no domain is at high risk of bias; or

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

We will resolve any discrepancy between review authors by discussion and by involving another review author where necessary. For studies using cluster randomisation, we will 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 2019b) (Appendix 3).

Measures of treatment effect

For meta‐analysis of data on the proportion of participants with pressure ulcers healed, we will 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 will present the mean difference (MD) with 95% CIs for studies that use the same assessment scale. If studies reporting continuous data use different assessment scales, we will report the standardised mean difference (SMD) with 95% CIs.

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

Unit of analysis issues

We will note whether studies present outcomes at the level of the pressure ulcer or at the level of participants. We will also record whether the same participant is reported as having multiple pressure ulcers. Where studies randomise at the participant level and outcomes are measured at the level of the ulcer, we will consider the participant as the unit of analysis if the number of ulcers observed appears 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 will note 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 are incorrectly analysed, we will record this as part of the 'Risk of bias' assessment.

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

• 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; and

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

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 are missing data, and where relevant, we will contact 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 will assume that participants with missing data had ulcers healed for the main analysis (i.e. we will add missing data to the denominator but not the numerator). We will examine the impact of this assumption through undertaking a sensitivity analysis (see Sensitivity analysis). Where a study does not specify the number of randomised participants prior to dropout, we will use the available number of participants as the number randomised.

Assessment of heterogeneity

Assessing heterogeneity can be a complex, multifaceted process. Firstly, we will consider clinical and methodological heterogeneity; that is, the extent to which the included studies vary 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 will record and categorise 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 will supplement this assessment of clinical and methodological heterogeneity with information regarding statistical heterogeneity assessed using the Chi² test. We will consider 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 size. We will carry 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 will consider 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 has more than 10 included studies and no clear funnel plot asymmetry, we will also present 95% prediction intervals (Deeks 2019). We will 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). As prediction intervals consider a wider scope of variation they 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). However, we will not consider the risk of bias of these studies here because the intervals are to assess heterogeneity, and we will perform subgroup analysis by risk of bias as detailed below.

Assessment of reporting biases

We will follow 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 will do the following.

• Identify whether the missing outcome data are 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 are unavailable we will compare outcomes in the conference abstracts or in the methods section of the publication, or both, with the reported results. If we find non‐reporting of study results, we will then judge whether the non‐reporting is associated with the nature of findings by using the 'Outcome Reporting Bias In Trials' (ORBIT) system (Kirkham 2018).

• Assess the influence of definitely missing outcome data on meta‐analysis.

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

Data synthesis

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

We will consider clinical and methodological heterogeneity and undertake pooling when studies appear appropriately similar in terms of participants, beds and mattresses and outcome type. Where statistical synthesis of data from more than one study is not possible or considered inappropriate, we will conduct a narrative review of eligible studies.

Once the decision to pool is made we anticipate using a random‐effects model, which will estimate 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 will use the Chi² test and I² statistic to quantify heterogeneity but not to guide choice of model for meta‐analysis (Borenstein 2009). We will exercise caution when meta‐analysed data are 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 are other reasons to question the choice of a fixed‐effect or random‐effects model, we will assess the impact of the approach using sensitivity analyses to compare results from alternate models (Thompson 1999).

We will perform meta‐analyses largely using Review Manager 5.3 (Review Manager 2014), as well as Stata: Release 14 (Stata 2015), or R (R Core Team 2019), where necessary. We will present data using forest plots where possible. For dichotomous outcomes, we will present the summary estimate as a RR with 95% CI. Where continuous outcomes were measured, we will present the MD with 95% CIs; we will report SMD estimates where studies measured the same outcome using different methods. For time‐to‐event data, we will present the summary estimates as HRs with 95% CIs.

Subgroup analysis and investigation of heterogeneity

Sensitivity analysis

We will conduct 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 considering time to pressure ulcer healing as the primary outcome measure. We will do this by considering time to pressure ulcer healing as the primary outcome measure in this review (i.e. analysing the included data on the proportion of participants with pressure ulcers healed for the main analysis, followed by a repeated analysis with time to pressure ulcer healing data).

• Impact of missing data. We will do this by repeating the analysis using complete case data (instead of assuming that participants with missing data had ulcers healed, as in the main analysis).

• Impact of altering the effects model used. We will do this by repeating the analysis using a different effects model (i.e. using a random‐effects model for the main analysis, followed by a repeated analysis with a fixed‐effect model).

Summary of findings and assessment of the certainty of the evidence

We will present the main, pooled results of the review in 'Summary of findings' tables, which we will create 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 will also include an overall grading of the certainty of the evidence associated with each of the main outcomes that we will assess 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. Where applicable (e.g. for pressure ulcer healing outcomes), we will not downgrade the certainty of evidence for risk of bias if blinding of participants and personnel is the only domain resulting in our judgement of overall high risk of bias for those studies in which it is impossible to blind participants and personnel.

We will present a separate 'Summary of findings' table for each comparison evaluated in this review. We will present the following 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 will prioritise the time points and method of outcome measurement specified in Types of outcome measures for presentation in ‘Summary of findings’ tables. Where we do not pool data for some outcomes within a comparison, we will conduct a GRADE assessment for each of these outcomes and present these assessments in a narrative format within the 'Results' section, without presenting them in separate 'Summary of findings' tables.

1 'Risk of bias' assessment in individually randomised controlled trials

2 'Risk of bias' assessment in cluster‐randomised controlled trials (cluster‐RCTs)

Bergstrom 2008

Borenstein 2009

Borenstein 2017

Cipriani 2013

Clark 2011

Covidence [Computer program]

Cullum 2016

Deeks 2019

Demarré 2015

Eldridge 2016

EPUAP/NPIAP/PPPIA 2019

Essex 2009

Glanville 2019

Gorecki 2009

Gorecki 2013

GRADEpro GDT [Computer program]

Graves 2005

Gray 2018

Guest 2018

Herdman 2011

Higgins 2003

Higgins 2011

Higgins 2019a

Higgins 2019b

Hróbjartsson 2012

Kaltenthaler 2001

Kirkham 2018

Lefebvre 2019

Livesley 2002

McInnes 2018

Nguyen 2015

NICE 2014

NPIAP 2016

NPIAP S3I 2007

Page 2019

Parmar 1998

Peters 2008

R Core Team 2019 [Computer program]

Review Manager 2014 [Computer program]

Riley 2011

Salanti 2014

Schulz 1995

Schünemann 2019

Shi 2018a

Shi 2018b

Stata 2015 [Computer program]

Thompson 1999

Tierney 2007

Ware 1992

World Health Organization 2019

Wounds International 2010