Types of studies

In this review we intended to include published and unpublished randomised controlled trials (RCTs), including cluster‐randomised trials and cross‐over RCTs, irrespective of language of report. We planned to exclude studies using quasi‐randomisation.

Types of participants

We intended to include studies in adults who remain seated for extended periods of time, undertaken in any care setting: this might have included health, rehabilitation and social care settings, and places of residence in which people may spend their day. We planned to include people at risk of developing new pressure ulcers, which may have included those with existing pressure ulcers at baseline when pressure ulcer incidence was measured in the study. We excluded children and people whose only form of seating was a wheelchair or seat cushion. 

Types of interventions

We planned to include any type of pressure redistributing static chair. This could have included, but would not have been limited to, static arm chairs, riser recline chairs, tilt‐in‐space chairs, recline chairs, and hybrid chairs. We did not plan to consider comparisons of static chairs with wheelchairs, or of different wheelchairs with each other in this review, as wheelchairs are mobility aids. Nor was the focus of this review the effects of different types of pressure redistributing cushions, as these are included in a Cochrane Review focused on support surfaces (McInnes 2015). We intended to include trials where the only systematic difference between trial arms was the use of a specific static chair type.

We anticipated that comparisons might include but not be limited to:

• pressure redistributing chairs compared with a standard chair (used in a ward or residential setting), which may have included:

  • pressure redistributing static chair compared with standard chair;

  • pressure redistributing recline chair compared with standard chair;

  • pressure redistributing riser recline chair compared with standard chair;

  • pressure redistributing tilt‐in‐space chair compared with standard chair;

  • pressure redistributing hybrid chair compared with standard chair;

• comparison of different types of pressure redistributing chairs, which may have included, but not been limited to, any combination of the chair types noted above.

Classification of intervention type would have been based on information presented in the paper. Standard chairs used in a ward or residential setting can have a high or low back, arm rests, front cross bars (horizontal support element joining the legs), removable seat cushions, custom‐moulded seat inserts, with or without wings and side infill. We planned to use the authors' definition of standard chair unless it was clear this was very different to this general definition.

Types of outcome measures

We list primary and secondary outcomes below. If a study was otherwise eligible (i.e. correct study design, population, and intervention/comparator) but did not report a listed outcome, then we would have contacted the study authors where possible to establish whether an outcome of interest here was measured but not reported.

We intended to report outcome measures at the latest time point available (assumed to be length of follow‐up if not specified) and the time point specified in the methods as being of primary interest (if this was different from the latest time point available). For all outcomes we would have classed assessment of outcome measures as:

• < 1 week to 8 weeks as short term;

• > 8 weeks to 26 weeks as medium term; and

• > 26 weeks as long term.

Electronic searches

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

• the Cochrane Wounds Specialised Register (searched 23 June 2021);

• the Cochrane Central Register of Controlled Trials (CENTRAL; 2021, Issue 5) in the Cochrane Library (searched 23 June 2021);

• Ovid MEDLINE including In‐Process & Other Non‐Indexed Citations (1946 to 23 June 2021);

• Ovid Embase (1974 to 23 June 2021);

• EBSCO CINAHL Plus (Cumulative Index to Nursing and Allied Health Literature; 1937 to 23 June 2021).

The search strategies for the Cochrane Wounds Specialised Register, CENTRAL, Ovid MEDLINE, Ovid Embase and EBSCO CINAHL Plus can be found in Appendix 1. We combined the Ovid MEDLINE search with the Cochrane Highly Sensitive Search Strategy for identifying randomised trials in MEDLINE: sensitivity‐maximising version (2008 revision) (Lefebvre 2021). We combined the Embase search with the Ovid Embase filter terms developed by the UK Cochrane Centre (Lefebvre 2021). We combined the CINAHL Plus search with the trial filter developed by Glanville 2019. There were no restrictions of the searches by language, date of publication or study setting.

We also searched the following clinical trials registries:

• US National Institutes of Health Ongoing Trials Register ClinicalTrials.gov (www.clinicaltrials.gov) (searched 23 June 2021);

• World Health Organization (WHO) International Clinical Trials Registry Platform (who.int/clinical-trials-registry-platform) (searched 23 June 2021).

Search strategies for clinical trial registries can be found in Appendix 1.

Searching other resources

• Searching reference lists of included trials and relevant reviews: we aimed to identify other potentially eligible trials or ancillary publications by searching the reference lists of retrieved included trials, as well as relevant systematic reviews, meta‐analyses and health technology assessment reports.

• Searching by contacting individuals or organisations: when necessary, we planned to contact authors of key papers and abstracts to request further information about their trials.

• Adverse effects: we did not perform a separate search for adverse effects of interventions used, we considered adverse effects described in included studies only.

Selection of studies

Two review authors independently assessed the titles and abstracts of the citations retrieved by the searches for relevance. After this initial assessment, we obtained full‐text copies of all studies considered to be potentially relevant. Two review authors independently checked the full papers for eligibility; they resolved disagreements by discussion and, where required, with the input of a third review author. We did not need to contact study authors to query any study details with regard to eligibility. We recorded all reasons for exclusion of studies obtained as full text and most relevant to the review. We completed a PRISMA flowchart to summarise this process (Liberati 2009).

Where studies had been reported in multiple publications/reports, we planned to obtain all available publications. Whilst we planned to include each study once in the review, we planned to extract data from all reports to ensure we would obtain maximal relevant data.

Data extraction and management

We intended to extract and summarise details of the eligible studies using a data extraction sheet. Two review authors would have extracted data independently and would have resolved disagreements by discussion, consulting a third review author where required. If data were missing from reports, we intended to contact the study authors to obtain these. If we had included a study with more than two intervention arms, we planned to only extract data from intervention and control groups that met the eligibility criteria.

We intended to extract the following data where possible by treatment group for the prespecified interventions and outcomes in this review. We planned to collect outcome data for relevant time points as described in the Types of outcome measures section:

• country of origin;

• type of setting;

• trial design and unit of randomisation: whether randomisation was undertaken at the participant level or at the level of a ward, care home, or other location;

• unit of analysis: how clustered data were addressed in the analysis;

• care setting;

• number of participants randomised to each trial arm;

• eligibility criteria and key baseline participant data (participant age, gender, and skin status where recorded);

• details of treatment regimen received by each group;

• duration of treatment;

• details of any co‐interventions;

• primary and secondary outcome(s) (with definitions);

• outcome data for primary and secondary outcomes (by group);

• duration of follow‐up;

• number of withdrawals (by group);

• publication status of study; and

• source of funding for trial.

Assessment of risk of bias in included studies

Two review authors planned to independently assess the risk of bias in included studies by using the Cochrane risk of bias tool RoB1 (Higgins 2017). This tool addresses six specific domains: sequence generation, allocation concealment, blinding, incomplete data, selective outcome reporting, and other issues. In this review we intended to record issues with unit of analysis, for example where a cluster‐randomised trial has been undertaken but analysed at the individual level in the study report (Appendix 2).

We planned to assess blinding and completeness of outcome data for each of the review outcomes separately. We were aware that, since pressure ulcer incidence is a subjective outcome, it can be at high risk of measurement bias when outcome assessment is not blinded. Therefore, we intended to consider studies without blinded outcome assessment of ulcer incidence at high risk of detection bias. It would have been unlikely that studies were able to blind health professionals or participants to treatment received, meaning that most or all studies would have been regarded as being at high risk of performance bias. However, where studies had documented their processes to minimise differences in performance, for example with protocol‐guided delivery of co‐interventions, we would have considered making a judgement of unclear or low risk of bias. We planned to present our assessment of risk of bias using two risk of bias summary figures: one was to have been a summary of bias for each item across all studies, and the second would have shown a cross‐tabulation of each trial by all risk of bias items. We planned to class studies with an assessment of low risk of bias for selection bias (both domains of sequence generation and allocation concealment), detection bias, and attrition bias, and no assessment of high risk of bias in any other domain, to be at overall low risk of bias (for specified outcome). Studies with a high risk of bias assessment in any domains would have been classed as being at high risk of bias.

For cluster‐randomised trials, we planned to consider the risk of bias in terms of: recruitment bias, baseline imbalance, loss of clusters, incorrect analysis, and comparability with individually randomised trials (Higgins 2021; Appendix 3).

Measures of treatment effect

For dichotomous outcomes we would have sought to calculate the risk ratio (RR) with 95% confidence intervals (CI). For continuously distributed outcome data, we intended to use the mean difference (MD) with 95% CIs where trials utilised the same or similar assessment scale. Wherever trials used different assessment scales, we proposed to use the standardised mean difference (SMD) with 95% CIs. We sought to only consider mean time to healing without survival analysis as a valid outcome if reports specified that all wounds healed (i.e. if the trial authors regarded time to healing as a continuous measure as there was no censoring). We intended to report time‐to‐event data (e.g. time to pressure ulceration), as hazard ratios (HR) where possible, in accordance with the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2021). If studies reporting time‐to‐event data did not report a HR, then, where feasible, we planned to estimate this using other reported outcomes, such as the numbers of events, through the application of available statistical methods (Parmar 1998); however, this was not necessary.

Unit of analysis issues

Where studies randomised by participant, but analysed by wound outcome, with the numbers of participants and wounds being equal (i.e. one wound per participant), we intended to treat the participant as the unit of analysis. There may have been instances of clustered data, where a proportion of trial participants had outcome data collected and reported on multiple wounds. Since not all participants would have multiple wounds this is not a cluster trial per se, but rather a trial that incorrectly includes a mixture of individual and clustered data (Schultz 2010). We planned to note such trials and record the issue in the risk of bias assessment. Data would have been extracted and presented but would not have been the subject of any further analyses.

We intended to only incorporate correctly designed and analysed full cluster‐randomised trials into meta‐analyses. If it had been possible, we intended to approximate the correct analyses with guidance from the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021), using information on:

• the number of clusters randomised to each intervention, or the mean size of each cluster;

• outcome data ignoring cluster design for the total number of individuals; and

• an estimate of the intracluster correlation coefficient (ICC).

If we could not analyse the study data correctly, we planned to extract and present the data without further analysis.

We aimed to ensure there were no unit of analysis issues with double counting of controls when using studies with multiple intervention arms.

Where repeated observations were recorded on the same participant (e.g. discomfort scales over time), we intended to define time points and analyse accordingly. Where multiple recordings were available within these time points, we planned to incorporate all available data for an overall mean where possible.

Dealing with missing data

It is common for data to be missing from trial reports. Excluding randomised participants from the analysis or ignoring those participants who are lost to follow‐up compromises the randomisation, and potentially introduces bias into the trial. Where we thought data were missing we planned to contact the relevant study authors to request these data.

Where data were missing for the 'proportion of participants developing a new pressure ulcer' outcome for analysis, we intended to assume that if randomised participants were not included in an analysis, they did not have an incident ulcer (i.e. they would be considered in the denominator but not the numerator). We planned to explore this in a sensitivity analysis where the impact of no imputation (complete case analysis) was considered (see Sensitivity analysis).

In a time‐to‐pressure ulceration analysis using survival analysis methods, dropouts should be accounted for as censored data so we did not plan to take any action regarding missing data.

For all secondary outcomes, we intended to present available data from the study reports/study authors and did not plan to impute missing data. Where measures of variance were missing, we planned to calculate these where possible. If calculation was not possible, we planned to contact the study authors for further information. Where these measures of variance were not available, we aimed to exclude the study from any relevant meta‐analyses that we conducted.

Assessment of heterogeneity

Assessment of heterogeneity can be a complex, multi‐faceted process. We planned to consider clinical and methodological heterogeneity; that is the degree to which the included studies varied in terms of participant, intervention, outcome, and characteristics such as length of follow‐up. We aimed to supplement this assessment of clinical and methodological heterogeneity with information regarding statistical heterogeneity, assessed using the Chi² test (we would have considered a significance level of P < 0.10 to indicate statistically significant heterogeneity) in conjunction with the I² measure (Higgins 2003). The I² measure examines the percentage of total variation across RCTs that is due to heterogeneity rather than chance (Higgins 2003). In general, I² values of 25% or less may mean a low level of heterogeneity (Higgins 2003), and values of more than 75% indicate very high heterogeneity (Deeks 2021). However, these figures are only a guide, and it is recognised that statistical tests and metrics may miss important heterogeneity. Whilst we planned to assess these, the overall assessment of heterogeneity would have looked at these measures in combination with the methodological and clinical assessment of heterogeneity. Where there was evidence of high heterogeneity, we aimed to explore this further by checking for errors and subgroup analysis or meta‐regression.

Assessment of reporting biases

Reporting biases arise when the dissemination of research findings is influenced by the nature and direction of results. Publication bias is one of a number of possible causes of 'small study effects', that is, a tendency for estimates of the intervention effect to be more beneficial in smaller RCTs. Funnel plots allow a visual assessment of whether small study effects may be present in a meta‐analysis. A funnel plot is a simple scatter plot of the intervention effect estimates from individual RCTs against some measure of each trial’s size or precision (Page 2021). We planned to present funnel plots for meta‐analyses comprising 10 RCTs or more using Review Manager 5 (RevMan 5) (Review Manager 2020).

Data synthesis

We intended to combine details of included studies in a narrative review according to type of comparator, possibly by location/type of wound, and then by outcomes by time period. We planned to consider clinical and methodological heterogeneity and to undertake pooling when studies appeared appropriately similar in terms of wound type, intervention type, duration of follow‐up, and outcome type.

We could not pre‐specify the amount of clinical, methodological, and statistical heterogeneity in the included studies, but it may have been extensive. Thus, we anticipated using a random‐effects approach for meta‐analysis. Conducting meta‐analysis with a fixed‐effect model in the presence of even minor heterogeneity may provide overly narrow CIs. We planned to only use a fixed‐effect approach when clinical and methodological heterogeneity would be considered to be minimal, and the assumption that a single underlying treatment effect is being estimated holds. We planned to use Chi² and I² measures to quantify heterogeneity but did not intend to use these to guide choice of model for meta‐analysis. We planned to exercise caution when meta‐analysed data were at risk of small study effects, because a random‐effects model may have been unsuitable. In this case, or where there were other reasons to question the selection of a fixed‐effect or random‐effects model, we planned to assess the impact of the approach using sensitivity analyses to compare results from alternate models. We aimed to report any evidence that suggested that the use of a particular model might not be robust. We planned to meta‐analyse even when there was thought to be extensive heterogeneity. We planned to attempt to explore the causes behind this using meta‐regression, if possible (Thompson 1999).

We intended to present data using forest plots where possible. For dichotomous outcomes we planned to present the summary estimate as an RR with 95% CI. Where continuous outcomes were measured in the same way across studies, we planned to present a pooled MD with 95% CI; we planned to pool SMD estimates where studies measured the same outcome using different methods. For time‐to‐event data, we planned to plot (and, if appropriate, pool) estimates of HRs and 95% CIs as presented in the study reports using the generic inverse variance method in RevMan 5 (Review Manager 2020).

Where time to pressure ulceration was analysed as a continuous measure but it was not clear if all pressure ulcers developed, we planned to document use of the outcome in the study but not to summarise data or use them in any meta‐analysis.

We aimed to obtain pooled estimates of treatment effect using RevMan 5 (Review Manager 2020).

Subgroup analysis and investigation of heterogeneity

Whilst we anticipated conducting an analysis of pressure redistributing chairs compared with standard chairs, we planned to assess potential heterogeneity with specific reference to the type of pressure redistribution chair being used. Where there was evidence of between‐trial heterogeneity, we envisaged conducting a subgroup analysis by chair type.

Where possible, we planned to also present a subgroup analysis of trials which would include incidence of all grades of ulcers compared with trials which only measured ulcers of grade II and above.

Where possible, we planned to perform subgroup analyses of the overall risk of bias category of a study (a binary comparison of studies at low or unclear risk of bias compared with studies classed at high risk of bias).

Sensitivity analysis

Where possible, we planned to perform sensitivity analyses to explore the effect of the following criteria:

• use of a fixed‐effect versus a random‐effects model;

• the impact of missing data: our base case analysis would have assumed that participants with missing data did not develop new pressure ulcers. In this sensitivity analysis we aimed to explore the impact of this assumption by undertaking the analysis with complete‐case data only.

Summary of findings and assessment of the certainty of the evidence

We planned to present the main results of the review in summary of findings tables. These tables present key information concerning the certainty of the evidence, the magnitude of the effects of the interventions examined, and the sum of the available data for the main outcomes (Schünemann 2021). The summary of findings tables also include an overall grading of the evidence related to each of the main outcomes 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 certainty of a body of evidence involves consideration of within‐trial risk of bias (methodological quality), directness of evidence, heterogeneity, precision of effect estimates, and risk of publication bias. We planned to present the following outcomes in the summary of findings tables:

• proportion of participants developing a new pressure ulcer;

• time to complete ulcer development, where analysed using an appropriate survival analysis method;

• participant health‐related quality of life/health status;

• participant comfort;

• cost effectiveness.

For review outcomes reported for comparisons not listed above, we aimed to present a GRADE assessment without a summary of findings table.

When evaluating the risk of bias domain, we planned to downgrade the GRADE assessment only when we classified a study as being at high risk of bias for one or more domains, or when the risk of bias assessment for selection bias was unclear (i.e. classified as unclear for either the generation of the randomisation sequence or the allocation concealment domain). We did not plan to downgrade for unclear risk of bias assessments in other domains.

We planned to select an informal optimal information size of 300 for binary outcomes, following the GRADE default value (Guyatt 2011). We aimed to follow GRADE guidance and downgrade twice for imprecision when there were very few events and CIs around effects included both appreciable benefit and appreciable harm (considered GRADE 'default' of below 0.75 and above 1.25).

For calculating absolute risk differences for dichotomous and time‐to‐event outcomes, we planned to use the median of the risks in the control groups at particular time points.

We have based elements of this Methods section on the standard Cochrane Wounds protocol template.