Objectives
This is a protocol for a Cochrane Review (intervention). The objectives are as follows:
To assess the effects of beds and mattresses on pressure ulcer healing in people with pressure ulcers of any stage, in any setting.
Background
Description of the condition
Pressure ulcers — also known as pressure injuries, pressure sores, decubitus ulcers and bed sores — are localised injuries to the skin or underlying soft tissue (or both), caused by unrelieved pressure, shear or friction (EPUAP/NPIAP/PPPIA 2019). Pressure ulcer severity is generally classified as follows, using the National Pressure Injury Advisory Panel (NPIAP) system (NPIAP 2016).
Stage 1: intact skin with a local appearance of non‐blanchable erythema
Stage 2: partial‐thickness skin loss with exposed dermis
Stage 3: full‐thickness skin loss
Stage 4: full‐thickness skin and tissue loss with visible fascia, muscle, tendon, ligament, cartilage or bone
Unstageable pressure injury: full‐thickness skin and tissue loss that is obscured by slough or eschar so that the severity of injury cannot be confirmed
Deep tissue pressure injury: local injury of persistent, non‐blanchable deep red, maroon, purple discolouration or epidermal separation revealing a dark wound bed or blood‐filled blister
The stages described above are consistent with those described in another commonly used system, the International Classification of Diseases for Mortality and Morbidity Statistics (World Health Organization 2019).
Pressure ulcers are complex wounds that are relatively common, affecting people across different care settings. A systematic review found that prevalence estimates for people affected by pressure ulcers in communities of the UK, USA, Ireland and Sweden ranged from 5.6 to 2300 per 10,000 depending on the nature of the population surveyed (Cullum 2016). A subsequent cross‐sectional survey of people receiving community health services in one city in the UK estimated that 1.8 people per 10,000 have a pressure ulcer (Gray 2018). Estimates of pressure ulcer prevalence in hospitals range from 470 to 3210 per 10,000 patients in the UK, USA and Canada (Kaltenthaler 2001).
Pressure ulcers confer a heavy burden in terms of personal impact and use of health‐service resources. Having a pressure ulcer may impair physical, social and psychological activities (Gorecki 2009). Ulceration impairs health‐related quality of life (Essex 2009); can result in longer institution stays (Graves 2005); and increases the risk of systemic infection (Livesley 2002). There is also substantial impact on health systems: a 2015 systematic review of 14 studies across a range of care settings in Europe and North America showed that costs related to pressure ulcer treatment ranged from EUR 1.71 to EUR 470.49 per person, per day (Demarré 2015). In the UK, the annual average cost to the National Health Service for managing one person with a pressure ulcer in the community was estimated to be GBP 1400 for a Stage 1 pressure ulcer and more than GBP 8500 for more severe stages (2015/2016 prices; Guest 2018). In Australia, the annual cost of treating pressure ulcers was estimated to be AUD 983 million (95% confidence interval (CI) 815 million to 1151 million) at 2012/13 prices (Nguyen 2015). The serious consequences of pressure ulceration have led to an intensive focus on their prevention.
Description of the intervention
Pressure ulcers are considered treatable. Support surfaces are specialised medical devices designed to relieve and/or redistribute pressure on the body, in order to prevent and treat pressure ulcers (NPIAP S3I 2007). Beds and mattresses are support surfaces that are widely used for treating pressure ulcers. These include, but are not limited to, integrated bed systems, mattresses and overlays (NPIAP S3I 2007).
The NPIAP Support Surface Standards Initiative (S3I) terms and definitions related to support surfaces can be used to classify types of support surface (NPIAP S3I 2007). According to this system, beds and mattresses may:
be powered (i.e. require electrical power to function) or non‐powered;
passively redistribute body weight (i.e. reactive pressure redistribution), or mechanically alternate the pressure on the body (i.e. active pressure redistribution);
be made of a range of materials, including but not limited to: air cells, foam materials, fibre materials, gel materials, sheepskin for medical use, and water bags; and
be constructed of air‐filled cells that have small holes on the surface for blowing out air to dry skin (i.e. low air‐loss feature) or have fluid‐like characteristics via forcing filtered air through ceramic beads (i.e. air‐fluidised feature), or have neither of these features.
Full details of bed and mattress classifications are listed in Appendix 1. Various types of beds and mattresses can be applied for treating pressure ulcers, including alternating pressure (active) air surfaces, reactive air surfaces, high‐specification reactive foam surfaces, and alternative reactive support surfaces that are made of neither foam materials or air cells.
How the intervention might work
The aim of using support surfaces to treat pressure ulceration is to redistribute pressure beneath the body, thereby increasing blood flow to tissues and relieving distortion of the skin and soft tissue (Wounds International 2010). Active support surfaces achieve pressure redistribution by frequently changing the points of contact between the surface and body, reducing the duration of the pressure applied to each anatomical site (Clark 2011;NPIAP S3I 2007). This contrasts with the mode of action of reactive support surfaces, which is more passive and includes immersion (i.e. 'sinking' of the body into a support surface) and envelopment (i.e. conforming of a support surface to the irregularities in the body); these devices distribute the pressure over a greater area, thereby reducing the magnitude of the pressure at specific sites (Clark 2011).
Why it is important to do this review
Beds and mattresses are the focus of recommendations in international and national guidelines (EPUAP/NPIAP/PPPIA 2019; NICE 2014). Since the publication of the Cochrane Review, 'Support surfaces for treating pressure ulcers' (McInnes 2018), there has been international recognition of the NPIAP S3I terms and definitions related to support surfaces (NPIAP S3I 2007). It is important to update this review to ensure that the review is contemporaneous with current guidelines and other reviews in the field.
In this update we will consider all types of beds and mattresses (instead of including other types of support surfaces e.g. cushions, as in McInnes 2018) because beds and mattresses are the primary focus in pressure ulcer guidelines (EPUAP/NPIAP/PPPIA 2019; NICE 2014). We therefore changed the title of this review to 'Beds and mattresses for treating pressure ulcers'.
Objectives
To assess the effects of beds and mattresses on pressure ulcer healing in people with pressure ulcers of any stage, in any setting.
Methods
Criteria for considering studies for this review
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
Primary outcomes
The primary outcome of this review is complete pressure ulcer healing. We will include studies that measure complete pressure ulcer healing. Trialists use a range of different methods for measuring and reporting this outcome. RCTs that report one or more of the following will be considered as providing the most relevant and rigorous measures of ulcer healing.
Time to complete pressure ulcer healing (correctly analysed using survival, time‐to‐event approaches or median (or mean) time to healing, if it was clear that all ulcers were healed at follow‐up)
Proportion of participants with pressure ulcers completely healed during follow‐up
We will use the study authors' definitions of complete pressure ulcer healing, and will report these where possible. Where both the complete‐healing outcome measures listed above are reported for a study, we will consider the proportion of participants with pressure ulcers healed as the primary outcome for this review. Our preferred measure is time to pressure ulcer healing, however we do not expect it to be reported in many studies; we will extract and analyse time‐to‐event data but focus on the binary outcome in our conclusions. Should an included study have only recruited people with Stage 1 ulcers and reported the outcome of the resolution of Stage 1 ulcers, we will term the resolution outcome as complete pressure ulcer healing in this review. We will use the same method to consider the resolution outcome where an included study has recruited both participants with pressure ulcers of Stage 1 and those with more severe ulcers.
Note that we will record any other healing outcome measures reported in the included studies, e.g. rate of change in the area/volume of the ulcers. However, we will not consider them as primary outcome measures and their data will not be analysed because these measures are less clinically relevant than complete healing.
Secondary outcomes
Patient support‐surface‐associated comfort. We will consider patient comfort outcome data in this review only if the evaluation of patient comfort is pre‐planned and is systematically conducted across all participants in the same way in a study. The definition and measurement of this outcome may vary from one study to another; for example, the proportion of participants who report comfort, or comfort measured by a scale with continuous (categorical) numbers. We will include these data with different measurements in separate meta‐analyses.
All reported adverse events (measured using survey/questionnaire/data capture process or visual analogue scale). Study authors should specify a clear method for collecting adverse event data; and where available, we will extract data on all serious and all non‐serious adverse events as an outcome. This methodology should make it clear whether events were reported at the participant level or whether multiple events per person are reported, in which case appropriate adjustments need to be made for data clustering (Higgins 2019a). We will consider the assessment of any event in general defined as adverse by participants, health professionals, or both.
Health‐related quality of life (measured using a standardised generic questionnaire such as EQ‐5D (Herdman 2011), 36‐item Short Form (SF‐36; Ware 1992), or pressure ulcer‐specific questionnaires such as the PURPOSE Pressure Ulcer Quality of Life (PU‐QOL) questionnaire (Gorecki 2013), at noted time points). We will not include ad hoc measures of quality of life because these measures are unlikely to be validated.
Cost effectiveness: within‐trial cost‐effectiveness analysis comparing mean differences in effects with mean cost differences between the two arms; we will extract data on incremental mean cost per incremental gain in benefit (incremental cost‐effectiveness ratio (ICER)). We will also consider other measures of relative cost‐effectiveness (e.g. net monetary benefit, net health benefit).
Other outcome considerations
If a study does not report any review‐relevant outcomes but is otherwise eligible (i.e. eligible study design, participants and interventions), we will contact the study authors (where possible) to clarify whether they measured a relevant outcome but did not report it. We will consider the study as ' awaiting classification' if we cannot establish whether it measured an outcome or not. We will exclude the study if the study authors confirm that they did not measure any review‐relevant outcomes.
If a study measured an outcome at multiple time points, we will consider outcome measures at three months as of primary interest to this review (Bergstrom 2008), regardless of the time points specified as being of primary interest by the study. If the study does not report three‐month outcome measures, we will consider those closest to three months.
Where a study only reports a single time point, we will consider that time point in this review. Where the study does not specify a time point for their outcome measurement, we will assume that its time point is the length of follow‐up.
Search methods for identification of studies
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.
Data collection and analysis
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).
Cross‐over trials
For cross‐over trials, we will only consider outcome data at the first intervention phase (i.e. prior to cross‐over) as eligible.
Studies with multiple treatment groups
If a study has more than two eligible study groups, we will combine results across all eligible intervention groups and compare them with, where available, the combined results across all eligible control groups, and make single pair‐wise comparisons (Higgins 2019b).
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
Investigation of heterogeneity
When important heterogeneity occurs, we will follow steps proposed by Cipriani 2013 to investigate further. We will:
check the data extraction and data entry for errors and possible outlying studies;
if outliers exist, perform sensitivity analysis by removing them; and
if heterogeneity is still present, perform subgroup analyses for study‐level characteristics (see below) in order to explain heterogeneity as far as possible.
Subgroup analysis
We will investigate heterogeneity using the methods described in Section 10.11 of the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2019). We will perform subgroup analyses to determine whether the size of treatment effects is influenced by the following two study‐level characteristics:
risk of bias (binary: low or unclear risk of bias; and high risk of bias (Schulz 1995)); and
settings (categorical: acute care and other hospital settings; long‐term care settings; operating theatre setting; and intensive care unit).
We will compare subgroups using the analysis option of the 'Test for Subgroup Differences’ in Review Manager 5.3 (Review Manager 2014). We will not perform subgroup analysis when the number of studies included in the meta‐analysis is not reasonable (e.g. fewer than 10).
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.
History
Protocol first published: Issue 5, 2020
Acknowledgements
The authors would like to thank Jessica Sharp for copy‐editing this protocol and to Denise Mitchell for additional copy edit feedback.
Elements of this Methods section are based on the standard Cochrane Wounds protocol template.
Appendices
Appendix 1. Full details of support surfaces classifications
Overarching class of support surface (as used in this review) | Corresponding subclasses of support surfaces used inShi 2018b | Descriptions of support surfaces | Selected examples (with example brands where possible) |
Reactive air surfaces | Powered/non‐powered reactive air surfaces | A group of support surfaces constructed of air cells, which redistribute body weight over a maximum surface area (i.e. has reactive pressure redistribution mode), with or without the requirement for electrical power | Static air mattress overlay, dry flotation mattress (e.g. Roho, Sofflex), static air mattress (e.g. EHOB), and static mode of Duo 2 mattress |
Powered/non‐powered reactive low‐air‐loss air surfaces | A group of support surfaces made of air cells, which have reactive pressure redistribution modes and a low‐air‐loss function, with or without the requirement for electrical power | Low‐air‐loss Hydrotherapy | |
Powered reactive air‐fluidised surfaces | A group of support surfaces made of air cells, which have reactive pressure redistribution modes and an air‐fluidised function, with the requirement for electrical power | Air‐fluidised bed (e.g. Clinitron) | |
Foam surfaces | Non‐powered reactive foam surfaces | A group of support surfaces made of foam materials, which have a reactive pressure redistribution function, without the requirement for electrical power | Convoluted foam overlay (or pad), elastic foam overlay (e.g. microfluid static overlay), polyether foam pad, foam mattress replacement (e.g. MAXIFLOAT), solid foam overlay, viscoelastic foam mattress/overlay (e.g. Tempur, CONFOR‐Med, Akton, Thermo) |
Alternative reactive support surfaces (non‐foam or air‐filled): reactive fibre surfaces | Non‐powered reactive fibre surfaces | A group of support surfaces made of fibre materials, which have a reactive pressure redistribution function, without the requirement for electrical power | Silicore (e.g. Spenco) overlay/pad |
Alternative reactive support surfaces (non‐foam or air‐filled): reactive gel surfaces | Non‐powered reactive gel surfaces | A group of support surfaces made of gel materials, which have a reactive pressure redistribution function, without the requirement for electrical power | Gel mattress, gel pad used in operating theatre |
Alternative reactive support surfaces (non‐foam or air‐filled): reactive sheepskin surfaces | Non‐powered reactive sheepskin surfaces | A group of support surfaces made of sheepskin, which have a reactive pressure redistribution function, without the requirement for electrical power | Australian Medical Sheepskins overlay |
Alternative reactive support surfaces (non‐foam or air‐filled): reactive water surfaces | Non‐powered reactive water surfaces | A group of support surfaces based on water, which has the capability of a reactive pressure redistribution function, without the requirement for electrical power | Water mattress |
Alternating pressure (active) air surfaces | Powered active air surfaces | A group of support surfaces made of air cells, which mechanically alternate the pressure beneath the body to reduce the duration of the applied pressure (mainly via inflating and deflating to alternately change the contact area between support surfaces and the body; i.e. alternating pressure, or active, mode), with the requirement for electrical power | Alternating pressure‐relieving air mattress (e.g. Nimbus II, Cairwave, Airwave, MicroPulse), large‐celled ripple |
Powered active low‐air‐loss air surfaces | A group of support surfaces made of air cells, which have the capability of alternating pressure redistribution as well as low air loss for drying local skin, with the requirement for electrical power | Alternating pressure low‐air‐loss air mattress | |
Powered hybrid system air surfaces | A group of support surfaces made of air cells, which offer both reactive and active pressure redistribution modes, with the requirement for electrical power | Foam mattress with dynamic and static modes (e.g. Softform Premier Active) | |
Powered hybrid system low‐air‐loss air surfaces | A group of support surfaces made of air cells, which offer both reactive and active pressure redistribution modes as well as a low‐air‐loss function, with the requirement for electrical power | Stand‐alone bed unit with alternating pressure, static modes and low air‐loss (e.g. TheraPulse) | |
Standard hospital surfaces | Standard hospital surfaces | A group of support surfaces made of any materials, used as‐usual in a hospital and without reactive nor active pressure redistribution capabilities, nor any other functions (e.g. low‐air‐loss, or air‐fluidised). | Standard hospital (foam) mattress, NHS Contract hospital mattress, standard operating theatre surface configuration, standard bed unit and usual care |
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Appendix 2. Cochrane Central Register of Controlled Trials (CENTRAL) draft search strategy
#1 MeSH descriptor: [Beds] explode all trees #2 mattress*:ti,ab,kw #3 (foam or transfoam):ti,ab,kw #4 overlay*:ti,ab,kw #5 "pad" or "pads":ti,ab,kw #6" gel":ti,ab,kw #7 (pressure next relie*):ti,ab,kw #8 (pressure next reduc*):ti,ab,kw #9 (pressure next alleviat*):ti,ab,kw #10 ("low pressure" near/2 device*):ti,ab,kw #11 ("low pressure" near/2 support):ti,ab,kw #12 (constant near/2 pressure):ti,ab,kw #13 "static air":ti,ab,kw #14 (alternat* next pressure):ti,ab,kw #15 (air next suspension*):ti,ab,kw #16 (air next bag*):ti,ab,kw #17 (water next suspension*):ti,ab,kw #18 sheepskin:ti,ab,kw #19 (turn* or tilt*) next (bed* or frame*):ti,ab,kw #20 kinetic next (therapy or table*):ti,ab,kw #21 (net next bed*):ti,ab,kw #22 {or #1‐#21} #23 MeSH descriptor: [Pressure Ulcer] explode all trees #24 (pressure next (ulcer* or sore* or injur*)):ti,ab,kw #25 (decubitus next (ulcer* or sore*)):ti,ab,kw #26 ((bed next sore*) or bedsore*):ti,ab,kw #27 {or #23‐#26} #28 (#22 and #27) in Trials
Appendix 3. Risk of bias
1 'Risk of bias' assessment in individually randomised controlled trials
1. Was the allocation sequence randomly generated?
Low risk of bias
The study authors describe a random component in the sequence generation process, such as referring to a random number table, using a computer random number generator, coin tossing, shuffling cards or envelopes, throwing dice, drawing of lots.
High risk of bias
The study authors describe a non‐random component in the sequence generation process. Usually, the description would involve some systematic, non‐random approach, for example, sequence generated by odd or even date of birth, sequence generated by some rule based on date (or day) of admission, sequence generated by some rule based on hospital or clinic record number.
Unclear
Insufficient information about the sequence generation process to permit judgement of low or high risk of bias.
2. Was the treatment allocation adequately concealed?
Low risk of bias
Participants and study authors enrolling participants could not foresee assignment because one of the following, or an equivalent method, was used to conceal allocation: central allocation (including telephone, web‐based and pharmacy‐controlled randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes.
High risk of bias
Participants or study authors enrolling participants could possibly foresee assignments and thus introduce selection bias, e.g. allocation was based on using an open random allocation schedule (e.g. a list of random numbers), assignment envelopes were used without appropriate safeguards (e.g. if envelopes were unsealed or non opaque or not sequentially numbered), alternation or rotation, date of birth, case record number, any other explicitly unconcealed procedure.
Unclear
Insufficient information to permit judgement of low or high risk of bias. This is usually the case if the method of concealment is not described or not described in sufficient detail to allow a definite judgement, for example if the use of assignment envelopes is described, but it remains unclear whether envelopes were sequentially numbered, opaque and sealed.
3. Blinding: was knowledge of the allocated interventions by participants and personnel adequately prevented during the study?
Low risk of bias
Any one of the following.
No blinding, but the review authors judge that the outcome is not likely to be influenced by lack of blinding.
Blinding of participants and key study personnel ensured, and unlikely that the blinding could have been broken.
High risk of bias
Any one of the following.
No blinding or incomplete blinding, and the outcome is likely to be influenced by lack of blinding.
Blinding of key study participants and personnel attempted, but likely that the blinding could have been broken.
Either participants or some key study personnel were not blinded, and the non‐blinding of others is likely to introduce bias.
Unclear
Any one of the following.
Insufficient information to permit a judgement of low or high risk of bias.
The study did not address this outcome.
4. Blinding: was knowledge of the allocated interventions by outcome assessors adequately prevented during the study?
Low risk of bias
Any one of the following.
No blinding, but the review authors judge that the outcome measurement is not likely to be influenced by lack of blinding.
Blinding of outcome assessment ensured, and unlikely that the blinding could have been broken.
High risk of bias
Any one of the following.
No blinding or incomplete blinding, and the outcome measurement is likely to be influenced by lack of blinding.
Blinding of outcome assessment attempted, but likely that the blinding could have been broken.
Unclear
Any one of the following.
Insufficient information to permit a judgement of low or high risk of bias.
The study did not address this outcome.
5. Were incomplete outcome data adequately addressed?
Low risk of bias
Any one of the following.
No missing outcome data.
Reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to be introducing bias).
Missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups.
For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk is not sufficient to have a clinically relevant impact on the intervention effect estimate.
For continuous outcome data, the plausible effect size (difference in means or standardised difference in means) among missing outcomes is not sufficient to have a clinically relevant impact on observed effect size.
Missing data have been imputed using appropriate methods.
High risk of bias
Any one of the following.
Reason for missing outcome data is likely to be related to the true outcome, with either imbalance in numbers or reasons for missing data across intervention groups.
For dichotomous outcome data, the proportion of missing outcomes compared with observed event risk is sufficient to induce clinically relevant bias in intervention effect estimate.
For continuous outcome data, the plausible effect size (difference in means or standardised difference in means) among missing outcomes is sufficient to induce clinically relevant bias in the observed effect size.
‘As‐treated’ analysis done, with substantial departure of the intervention received from that assigned at randomisation.
Potentially inappropriate application of simple imputation.
Unclear
Any one of the following.
Insufficient reporting of attrition/exclusions to permit judgement of low or high risk of bias (e.g. number randomised not stated; no reasons for missing data provided).
The study did not address this outcome.
6. Are reports of the study free of suggestion of selective outcome reporting?
Low risk of bias
Any of the following.
The study protocol is available and all of the study’s prespecified (primary and secondary) outcomes that are of interest in the review have been reported in the prespecified way.
The study protocol is not available but it is clear that the published reports include all expected outcomes, including those that were prespecified (convincing text of this nature may be uncommon).
High risk of bias
Any one of the following.
Not all of the study’s prespecified primary outcomes have been reported.
One or more primary outcomes are reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not prespecified.
One or more reported primary outcomes were not prespecified (unless clear justification for their reporting is provided, such as an unexpected adverse effect).
One or more outcomes of interest in the review are reported incompletely so that they cannot be entered in a meta‐analysis.
The study report fails to include results for a key outcome that would be expected to have been reported for such a study.
Unclear
Insufficient information to permit judgement of low or high risk of bias. It is likely that the majority of studies will fall into this category.
7. Other sources of potential bias
Low risk of bias
The study appears to be free of other sources of bias.
High risk of bias
There is at least one important risk of bias. For example, the study:
had a potential source of bias related to the specific study design used; or
has been claimed to have been fraudulent; or
had some other problem.
Unclear
There may be a risk of bias, but there is either:
insufficient information to assess whether an important risk of bias exists; or
insufficient rationale or evidence that an identified problem will introduce bias.
2 'Risk of bias' assessment in cluster‐randomised controlled trials (cluster‐RCTs)
1. Recruitment bias
Recruitment bias (or identification bias) is the bias that occurs in cluster‐RCTs if the personnel recruiting participants know individuals’ allocation, even when the allocation of clusters has been concealed appropriately. The knowledge of the allocation of clusters may lead to bias because the individuals' recruitment in cluster trials is often behind the clusters' allocation to different interventions; and the knowledge of allocation can determine whether individuals are recruited selectively.
This bias can be judged through considering the following questions.
Were all the individual participants identified/recruited before randomisation of clusters?
Is it likely that selection of participants was affected by knowledge of the intervention?
Were there baseline imbalances that suggest differential identification or recruitment of individual participants between arms?
2. Baseline imbalance
Baseline imbalance between intervention groups can occur due to chance, problems with randomisation, or identification/recruitment bias. The issue of recruitment bias has been considered above.
In terms of study design, the risk of chance baseline imbalance can be reduced by the use of stratified or pair‐matched randomisation. Minimisation — an equivalent technique to randomisation — can be used to achieve better balance in cluster characteristics between intervention groups if there is a small number of clusters.
Concern about the influence of baseline imbalance can be reduced if studies report the baseline comparability of clusters, or statistical adjustment for baseline characteristics.
3. Loss of clusters
Similar to missing outcome data in individually randomised trials, bias can occur if clusters are completely lost from a cluster‐RCT, and are omitted from the analysis.
The amount of missing data, the reasons for missingness and the way of analysing data given the missingness should be considered in assessing the possibility of bias.
4. Incorrect analysis
Data analyses, which do not take the clustering into account, in cluster‐RCTs will be incorrect. Such analyses lead to a 'unit of analysis error' and over‐precise results (overly small standard error) and overly small P values. Though these analyses will not result in biased estimates of effect, they (if not correctly adjusted) will lead to too much weight allocated to cluster trials in a meta‐analysis.
Note that the issue of analysis may not lead to concern any more and will not be considered substantial if approximate methods are used by review authors to address clustering in data analysis.
5. Comparability with individually randomised trials
In the case that a meta‐analysis includes, for example, both cluster‐randomised and individually randomised trials, potential differences in the intervention effects between different trial designs should be considered. This is because the 'contamination' of intervention effects may occur in cluster‐RCTs, which would lead to underestimates of effect. The contamination could be known as a 'herd effect': that is, within clusters, individuals' compliance with using an intervention may be enhanced, which in return affects the estimation of effect.
Contributions of authors
Chunhu Shi conceived the review question; developed the protocol; co‐ordinated the protocol development; produced the first draft of the protocol; contributed to writing and editing the protocol; approved the final version of the protocol prior to submission; and is guarantor of the protocol.
Jo C Dumville conceived the review question; developed the protocol; co‐ordinated the protocol development; secured funding; contributed to editing the protocol; advised on the protocol; and approved the final version of the protocol prior to submission.
Nicky Cullum conceived the review question; co‐ordinated the protocol development; contributed to editing the protocol; advised on the protocol; and approved the final version of the protocol prior to submission.
Sarah Rhodes contributed to editing the protocol; advised on the protocol; and approved the final version of the protocol prior to submission.
Elizabeth McInnes performed previous work that was the foundation of the current protocol; conceived the review question; contributed to editing the protocol; advised on the protocol; and approved the final version of the protocol prior to submission.
Contributions of the editorial base
Gill Norman (Editor): edited the protocol; advised on methodology, interpretation and content; approved the final protocol prior to submission. Gill Rizzello (Managing Editor): coordinated the editorial process; advised on content; edited the protocol. Sophie Bishop (Information Specialist): designed the search strategy and edited the search methods section. Tom Patterson (Editorial Assistant): edited the reference section of the protocol.
Sources of support
Internal sources
Division of Nursing, Midwifery and Social Work, School of Health Sciences, Faculty of Biology, Medicine and Health, University of Manchester, UK
External sources
National Institute for Health Research (NIHR), UK
This research is independent research funded by the National Institute for Health Research (NIHR) under its Research for Patient Benefit (RfPB) Programme (Grant Reference Number PB‐PG‐1217‐20006). The views expressed are those of the author(s) and not necessarily those of the NIHR or the Department of Health and Social Care.
NIHR Manchester Biomedical Research Centre (BRC), UK
This research was co‐funded by the NIHR Manchester BRC. The views expressed in this publication are those of the authors and not necessarily those of the NHS, the National Institute for Health Research or the Department of Health and Social Care.
National Institute for Health Research (NIHR), UK
This project was supported by the National Institute for Health Research, via Cochrane Infrastructure funding to Cochrane Wounds. The views expressed are those of the authors and not necessarily those of the NIHR or the Department of Health and Social Care.
National Institute for Health Research Collaboration for Leadership Applied Health Research and Care (NIHR CLAHRC), Greater Manchester, UK
Nicky Cullum and Jo Dumville’s work on this project was partly funded by the NIHR CLAHRC, Greater Manchester. The funder had no role in the preparation of the manuscript or the decision to publish. However, the review may be considered to be affiliated to the work of the NIHR CLAHRC Greater Manchester. The views expressed herein are those of the authors and not necessarily those of the NHS, NIHR or the Department of Health and Social Care.
Declarations of interest
Chunhu Shi: I received research funding from the National Institute for Health Research (Research for Patient Benefit, Evidence synthesis for pressure ulcer prevention and treatment, PB‐PG‐1217‐20006). I received support from the Tissue Viability Society to attend conferences unrelated to this work. The Doctoral Scholar Awards Scholarship and Doctoral Academy Conference Support Fund (University of Manchester) also supported a PhD and conference attendance respectively, both were unrelated to this work.
Jo Dumville: I received research funding from the National Institute for Health Research (NIHR) UK for the production of systematic reviews focusing on high‐priority Cochrane Reviews in the prevention and treatment of wounds. This research was co‐funded by the NIHR Manchester Biomedical Research Centre and partly funded by the NIHR Collaboration for Leadership in Applied Health Research and Care (NIHR CLAHRC) Greater Manchester. Nicky Cullum: I received research funding for wounds‐related research and systematic reviews from the NIHR for the production of systematic reviews focusing on high‐priority Cochrane Reviews in the prevention and treatment of wounds. This research was co‐funded by the NIHR Manchester Biomedical Research Centre, and partly funded by the NIHR Collaboration for Leadership in Applied Health Research and Care (NIHR CLAHRC) Greater Manchester.
We have previously received research grant funding from the NHS Research and Development programme, Health Technology Assessment Programme for systematic reviews of beds and mattresses and for an RCT comparing a mattress and an overlay. This RCT would not be eligible for inclusion in this review as it was not a treatment study.
Sarah Rhodes: my salary is funded from three NIHR grants and a grant from Greater Manchester Cancer.
Elizabeth McInnes: none known.
New
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