Types of studies

We will include published and unpublished randomised controlled trials (RCTs) that evaluate the effect of different dressings and securement methods on the protection and stabilisation of peripheral ACs. We will include controlled clinical trials (CCTs) if there is an absence of RCTs. CCTs refer to quasi‐randomised studies in which an intervention and control are tested with concurrent enrolment and follow‐up, but without strict randomisation (Lefebvre 2011). In order to minimise potential bias, we will include cross‐over trials only if they report outcome data at the conclusion of the first treatment period, and will not include cluster‐randomised trials (Reeves 2013).

Types of participants

We will include any studies in which participants of any age required a peripheral AC (in the arm, leg or head) in any healthcare setting. We will include all brands/types of peripheral AC. We will exclude participants who had ACs inserted through skin burns due to their predisposition to CR‐BSIs and an altered skin surface that limits the adhesiveness of dressing and securement products.

Types of interventions

We will include any trial comparing any type of dressing or securement method with another type of dressing or securement method for the protection or stabilisation of an AC. We will consider dressings and devices that are made from any type of product (e.g. polyurethane, gauze).

Dressings

• Gauze and tape

• Transparent SPU or BPU dressings

• Antimicrobial dressings

• Hydrocolloid dressings

Securement products

• External SSDs

• Subcutaneous securement devices

• Combined dressing and securement products

• Tissue adhesive

• Sutures (stitches)

Types of outcome measures

Follow‐up time for all outcomes will be until AC removal, with the exception of CR‐BSIs, which will be followed‐up for 48 hours post AC removal, as CR‐BSIs occurring in this timeframe would be considered to result from AC management if there is no other source (Mermel 2009). We will record the duration of follow‐up for all outcome data.

Electronic searches

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

• the Cochrane Wounds Specialised Register (to date);

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

• Ovid MEDLINE (including In‐Process & Other Non‐Indexed Citations, MEDLINE Daily and Epub Ahead of Print) (from 1946 onwards);

• Ovid Embase (from 1974 onwards);

• EBSCO CINAHL Plus (Cumulative Index to Nursing and Allied Health Literature 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 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 2011). We will combine the Embase search with the Ovid Embase filter terms developed by the UK Cochrane Centre (Lefebvre 2011). We will combine the CINAHL Plus search with the randomised trials filter developed by the Scottish Intercollegiate Guidelines Network (SIGN 2017). There will be no restrictions with respect to language, study setting or date of publication.

We will also search the following clinical trials registries for ongoing and unpublished studies:

• ClinicalTrials.gov (www.clinicaltrials.gov);

• World Health Organisation International Clinical Trials Registry Platform (ICTRP) (www.who.int/trialsearch);

• ISRCTN registry (www.isrctn.com/);

• Hong Kong Clinical Trials Register (www.hkclinicaltrials.com);

• Indian Clinic Trials Registry (ctri.nic.in/Clinicaltrials/login.php).

Searching other resources

We aim 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. We will also contact experts in the field and ask for information relevant to this review, and contact dressing and securement device manufacturers, such as 3M, Smith and Nephew, and Centurion, to access possible unpublished data so as to avoid publication bias.

Selection of studies

Two review authors (HR and AU) will independently assess the titles and abstracts of the citations retrieved from the searches for relevance. Following an initial assessment, we will retrieve full‐text versions of all the potentially eligible studies and the same review authors will continue independent review, checking these papers for eligibility. We will resolve discrepancies between the review authors by discussion. If differences of opinion can not be resolved by consensus, we will consult a third independent review author (EA). We will include a list of all studies including exclusions and reasons for exclusion, in the review in order to maintain a transparent approach, using a PRISMA flowchart (Liberati 2009). If studies have been reported in multiple publications, we will extract data from all the reports to ensure we capture all available and relevant data; however, we will include such studies only once in the review.

Data extraction and management

We will extract and summarise details from the eligible studies using a data extraction sheet. Two review authors (HR and AU) will perform independent data extraction using a predesigned checklist, followed by cross‐checking for accuracy and agreement. We will resolve any discrepancies through discussion and arbitration by a third review author, as necessary. For any studies reported in duplicate publications, we will extract the maximum amount of data from all relevant publications. We will make attempts to contact the authors to retrieve any missing data. We will include RCTs that are reported only in abstract form provided the available data are sufficient for reasonable extraction from either the abstract or the study authors.

For studies with more than two intervention arms, we will extract only data from intervention and control groups that meet our eligibility criteria.

We intend to extract the following data:

• bibliographic data;

• participant characteristics including age, sex/gender, culture and socioeconomic status, and specified inclusion and exclusion criteria;

• country of origin;

• study dates;

• setting;

• type of AC;

• type of dressing, securement device, or both;

• unit of investigation (participant or dressing/securement intervention);

• co‐interventions;

• trial design;

• care setting;

• number of participants randomised to each trial arm and number included in final analysis;

• duration of treatment;

• outcomes;

• duration of follow‐up;

• number of withdrawals by group;

• information regarding ethics approval, consent and declared conflicts of interest;

• publication status; and

• source of funding.

Assessment of risk of bias in included studies

Two review authors (HR and AU) will independently perform an assessment of quality and bias for each eligible study using the Cochrane Handbook for Sytematic Reviews of Interventions 'Risk of bias' assessment tool (Appendix 3). We will assess seven specific domains, namely sequence generation, allocation concealment, blinding of participants and personnel, blinding of outcome assessment, incomplete outcome data, selective outcome reporting, and other issues that potentially may bias the study (Higgins 2011a). We will complete a 'Risk of bias' table for all eligible studies. Where information on risk of bias relates to unpublished data or correspondence with trialists, we will note this in the 'Risk of bias' table. We will perform separate assessments of blinding and completeness of outcome data for self‐reported and objective outcome measures. We will resolve any differences or discrepancies between the review authors (HR and AU) through discussion. If consensus is not reached, we will consult a third independent review author (EA). We will present our findings and judgements in two 'Risk of bias' summary figures. One of the summary figures will be a summary of bias for each item across all studies; the second summary figure will show a cross tabulation of each study by all 'Risk of bias' items. This presentation of internal validity will indicate the weight that can be given to the results of each study. We anticipate that blinding of participants and clinical staff may not be possible in many of the comparisons; however, some blinded outcome assessments, such as CR‐BSI, may still be possible.

Measures of treatment effect

We will calculate risk ratio (RR) for dichotomous outcomes and mean differences (MD) for continuous outcomes. Where final and change scores are reported for continuous outcomes, we will give the final score preference over change score. When outcomes are measured on ordinal scales, we will convert these to continuous data and analyse the data using standardised mean differences (SMD) (Anzures‐Cabrera 2011). We may encounter the use of different tools to measure the same outcome (e.g. skin damage). We will collect data only from studies that use a standard assessment tool, and will use the SMD as the summary statistic in any meta‐analysis of such data. We will present treatment comparisons with 95% confidence intervals (CI). We will analyse time to event (e.g. time to the development of an occlusion). We will analyse time‐to‐event data as hazard ratios and we will calculate the hazard ratios where they are not reported, but calculable (Parmar 1998; Tierney 2007)

Unit of analysis issues

We do not anticipate any unit of analysis issues, expecting that the RCTs and CCTs included will have randomised participants and not ACs. For studies in which ACs and not participants have been randomised, we will include only the first AC per participant. We will include only those cross‐over trials with outcome data reported at the conclusion of the first treatment period. We will not include cluster‐randomised trials. In studies where two or more interventions are used in one treatment arm (e.g. tissue adhesive plus polyurethane dressing), we will analyse this as a combined intervention. If individuals undergo more than one intervention or there are multiple observations for the same outcome (e.g. repeated measurements and recurring events), we will contact the study authors for participant‐ and device‐level data and then perform multilevel regression to calculate the adjusted effect. If additional data are unavailable we will exclude such studies from meta‐analysis. In accordance with Higgins 2011b, for included studies that involve the comparison of multiple interventions using a single control, we will split the ’shared’ control group to avoid additional unit of analysis issues. This is to distribute the appropriate study weight and maintain independent comparisons fairly. To prevent unit of analysis errors, participant satisfaction data will be included at the time of study completion only (i.e. not repeated observations). We will undertake time‐to‐event analyses for the outcome of catheter failure as hazard ratios.

Dealing with missing data

The existence of missing data may be due to the exclusion of participants from analysis post‐randomisation or participants lost to follow‐up. This potentially introduces bias into the trial. When the evidence shows that data are missing, we will make every attempt to contact the study authors to request the missing information. If the required data are not supplied after multiple attempts, we will analyse only the available data. Where measures of variance are missing, we will calculate these where possible (Higgins 2011a). If we are not able to calculate measures of variance, we will document this, but exclude from the meta‐analysis. We will consider the impact of the missing data on the findings of the review in the discussion. If there are sufficient data, we will investigate the impact of missing data using a sensitivity analysis, excluding the studies with missing data to assess how this will affect the results.

Assessment of heterogeneity

We will undertake an assessment of comparability of the studies with regard to clinical, methodological and statistical heterogeneity prior to meta‐analysis. We will visually inspect the meta‐analytic model, and consider the Chi² and I² statistics in order to assess the likelihood that the variance across the studies is due to heterogeneity rather than chance (Higgins 2003). If we find significant heterogeneity using these criteria, we will explore heterogeneity through subgroup and sensitivity analyses (including and excluding outlying studies). An I² statistic of more than 50% may represent moderate heterogeneity, and a value of 0 to 40% may suggest that heterogeneity is not important (Kontopantelis 2012; Kontopantelis 2013; Ryan 2016). If the level of these statistics cannot be improved through subgroup or sensitivity analyses, with the P value of the Chi² test being less than 0.1 or the I² statistic greater than 50%, we will consider not performing a meta‐analysis (Higgins 2011a; Higgins 2011b). The importance of the observed value of the I² statistic depends on the magnitude and direction of effects and the strength of evidence for heterogeneity (e.g. the P value from the Chi² test, or a confidence interval for the I² statistic).

Assessment of reporting biases

We will use funnel plots to assess reporting bias using Review Manager 5 (RevMan 5) (Review Manager 2014) if sufficient studies (at least 10 RCTs) are included in a meta‐analysis. We will visually inspect a funnel plot for asymmetry, and will test funnel plot asymmetry statistically using a linear regression test (Egger 1997). A P value of less than 0.1 could be an indication of publication bias or small study effects.

Data synthesis

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

In terms of meta‐analytical approach, we are unable to pre specify the amount of clinical, methodological and statistical heterogeneity in the included studies, but it might be extensive. Thus, we anticipate 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 confidence intervals. We will use a fixed‐effect approach only when we assess clinical and methodological heterogeneity to be minimal, and the assumption that a single underlying treatment effect is being estimated holds. We will use the Chi² and I² statistics to quantify heterogeneity but we will not use them to guide the choice of model for meta‐analysis. We will exercise caution when meta‐analysed data are at risk of small study effects, because a random‐effects model may be unsuitable. In this case, or where there are other reasons to question the selection of a fixed‐effect or random‐effects model, we will assess the impact of the approach using sensitivity analyses to compare results from the alternate models. We will report any evidence that suggests that the use of a particular model might not be robust. We may conduct meta‐analyses even when we think there is extensive heterogeneity. We will attempt to explore the causes behind any heterogeneity using meta‐regression, if possible (Thompson 1999).

We will present data using forest plots, where possible. For dichotomous outcomes we will present summary estimates as risk ratio (RR) with 95% confidence intervals (CIs). Where continuous outcomes are measured in the same way across studies, we plan to present pooled mean difference (MDs) with 95% CIs; we plan to pool standardised mean difference (SMD) estimates where studies measure the same outcome using different methods. For time‐to‐event data, we plan to plot (and, if appropriate, pool) estimates of hazard ratios and 95% CIs as presented in the study reports using the generic inverse variance method in RevMan (Review Manager 2014). Where time to healing is analysed as a continuous measure but it is not clear whether all wounds healed, we will document the use of the outcome in the study but we will not summarise data and not subject it to meta‐analysis.

We will obtain pooled estimates of treatment effects using RevMan (Review Manager 2014).

Subgroup analysis and investigation of heterogeneity

We will assess heterogeneity across the subgroups listed below and conduct subgroup analyses to investigate differences between the subgroups. We will perform a standard test for heterogeneity across subgroup results rather than across individual study results. We will use a fixed‐effect inverse‐variance weighted average approach for meta‐analysis, which is equivalent to the test described by Deeks 2001. We will also compute the I² statistic for subgroup differences:

• adult participants versus paediatric participants versus neonatal participants;

• AC dwelling (less than 48 hours versus 48 hours or longer): if participants require ACs for more than 48 hours, this suggests higher acuity, with increased needs for securing devices in relation to physical status (e.g. increased perspiration making dressing adhesion difficult); there also may be a greater infection risk over time;

• ACs inserted in the operating theatre as part of a surgical procedure versus those inserted in intensive care. Operating theatre‐inserted ACs may be subject to different forces requiring different methods of securement to those inserted in an ICU (e.g. people undergoing surgery are initially immobile, are then transferred within the hospital and have ACs removed within 1 to 2 days, whereas those in the ICU remain immobile and usually require an AC for longer);

• winged versus non‐winged AC designs. Some ACs have plastic tabs/wings extending from the sides of the catheter and this may impact on the effectiveness of securement method

Sensitivity analysis

We will test our protocol for the impact of the following study characteristics in sensitivity analyses:

• study size (less than or greater than 100 participants); small studies of less than 100 participants will be removed to assess the contribution to overall effect size.

• studies classified as having 'high' risk of selection bias, reported as 'high' bias within either randomisation or allocation concealment, will be removed to assess the influence on the results;

• missing data, with consideration of best (all missing cases failed in control group and not failed in intervention group) and worst (all missing cases failed in intervention group and not failed in control group) case scenarios;

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

Elements of this Methods section are modelled on the standard Cochrane Wounds Protocol Template.