Types of studies

We will include all randomised controlled trials (RCTs) with parallel (e.g. cluster or individual) or cross‐over design. We will only use data from the first phase of cross‐over studies to avoid the risk of carry‐over effects, as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021a). We will include studies reported as full text, those published as abstract only, and unpublished data. We will not consider quasi‐randomised trials, that is studies in which participants are allocated to intervention groups based on methods that are not truly random such as hospital number or date of birth.

Types of participants

We will include participants of any sex and any age with diabetes mellitus and related foot ulcers (ADA 2020; Van Netten 2019; WHO 2006). We will consider any stage of foot ulcer in people with diabetes, as defined by Van Netten 2019. Although we foresee that most participants will have type 2 diabetes, we will consider all trials involving participants with diabetes mellitus, irrespective of their type of diabetes or method of diagnosis (ADA 2020; WHO 2006). We will not consider participants with foot ulcers where it is not clear whether there is also a diagnosis of diabetes.

For studies with mixed populations where 50% or more of the study population are of interest, we will include all participants in our analysis. We will explore the effect of this decision in a sensitivity analysis. We will exclude studies for which less than 50% of the population are of interest.

Types of interventions

We will consider all types of telemedicine for this review, including interactive consultations, telediagnostic services, internet‐based two‐way video conferencing with the use of personal computers, laptops, tablets, or smartphones, to provide guidance, health care, ulcer care, and others. 'Telemedicine' and 'telehealth' will be considered interchangeable terms and should meet at least the following criteria: the purpose of providing clinical support or the intention of assessing healthcare outcomes (WHO 2010).

Possible comparisons included the following.

• Telemedicine versus standard care (e.g. face‐to‐face medical‐patient examination or ulcer care with dressing or topical agents by a health professional).

• Telemedicine plus standard care versus standard care.

• One type of telemedicine versus another type of telemedicine (both with or without standard care).

Studies where the use of a telemedicine intervention is the only systematic difference between treatment arms will be included.

Types of outcome measures

Reporting one or more of the outcomes listed here in the trial is not an inclusion criterion for the review. Where a published report does not appear to report one of these outcomes, we will access the trial protocol and contact the trial authors to ascertain whether the outcomes were measured but not reported. Eligible trials with no reported review‐relevant outcomes (non‐usable data) will be presented as part of the narrative findings.

We will present the outcomes at two different time points following the start of the intervention if data are available. Our time point of primary interest is the 'early' time point, therefore we intend to produce summary of findings tables only for this time point, but also plan to report the long‐term outcomes at the longest possible time of follow‐up.

If a trial measures an outcome at multiple time points, we will consider outcome measures at 90 days, or as close to this as possible, as being of primary interest to this review (early outcomes), irrespective of the time points specified as being of primary interest by the study. Where a trial only reports a single time point, we will consider that time point in the 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 (Schoonhoven 2007). The choice of 90 days as a time point was arbitrary but is a frequently used time point for reviews of wounds in people with diabetes (McGloin 2021). We will also report long‐term outcomes assessed at time points longer than 90 days. We will use judgement in determining whether time points are similar enough for statistical pooling.

Electronic searches

We will search the following databases to retrieve reports of relevant clinical 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);

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

• Latin American and Caribbean Health Science Information database (LILACS) (from 1982), via bvsalud.org/;

• Indice Bibliográfico Español de Ciencias de la Salud (IBECS), via bvsalud.org/.

We have devised a draft search strategy for CENTRAL, which is displayed in Appendix 1. 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‐maximising version (2008 revision) (Lefebvre 2021). We will combine the Embase search with the Ovid Embase filter terms developed by the UK Cochrane Centre (Lefebvre 2021). We will combine the CINAHL Plus search with the trial filter developed by Glanville 2019. There will be no restrictions of the searches by language, date of publication, or study setting.

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

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

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

Searching other resources

In order to identify further published, unpublished, and ongoing trials for this review, we will also:

• check the included studies and any relevant systematic reviews identified for further references of relevant trials, and use Google Scholar (scholar.google.co.uk/) to forward‐track relevant references;

• contact experts/trialists/organisations in the field to enquire about relevant ongoing or unpublished studies.

Selection of studies

Two review authors (OMP, FCFA) will independently screen the titles and abstracts of the references obtained in the preliminary search, using the Covidence tool to exclude irrelevant reports. Two review authors (OMP, FCFA) will retrieve and independently screen the full‐text articles of the remaining references to identify studies for inclusion in the review, recording any ineligible studies and the reasons for their exclusion. We will contact the authors of the included trials for any possible unpublished data. Any disagreements will be settled by discussion or by consulting a third review author (RLGF) if necessary. We will collate multiple reports of the same study so that each study, and not each reference, is the unit of interest in the review. We will record the selection process and complete a PRISMA flow diagram (Moher 2010).
 

Data extraction and management

Two review authors (OMP, FCFA) will independently extract data from the included studies using a data collection form for study characteristics and outcome data that has been piloted on at least one study in the review. We will extract the following study characteristics.

• Methods: study design, setting, date and total duration of study, number of participating centres, and location.

• Inclusion and exclusion criteria.

• Participants: N randomised, N lost to follow‐up/withdrawn, N analysed, age mean and range, gender, severity of condition (e.g. ulcer grade, duration, area), comorbidities (peripheral arterial disease and smoking), type and duration of diabetes, diagnostic criteria.

• Interventions: type of intervention and any use of concomitant treatments.

• Outcomes: specified and collected primary and secondary outcomes, and time points reported.

• Notes: funding for trial and notable conflicts of interest.

Any disagreements will be settled by consensus or by consulting a third review author (RLGF). One review author (OMP) will transfer data into the Review Manager 5 file (Review Manager 2020). We will double‐check all entered data by comparing the data presented in the systematic review with the data in the extraction form. A second review author (FCFA) will spot‐check study characteristics for accuracy.

Assessment of risk of bias in included studies

Two review authors (OMP, FCFA) will independently assess the risk of bias in each study using the Cochrane risk of bias tool and according to the criteria outlined in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017). Any disagreements will be settled by discussion or by consulting another review author (RLGF). We will assess risk of bias of the included studies based on the following domains.

• Random sequence generation

• Allocation concealment

• Blinding of participants and personnel

• Blinding of outcome assessment

• Incomplete outcome data

• Selective outcome reporting

• Other bias

For cluster‐randomised trials, we will consider the following biases, as recommended in Chapter 8 of the Cochrane Handbook for Systematic Reviews of Interventions: (i) recruitment bias; (ii) baseline imbalance; (iii) loss of clusters; (iv) incorrect analysis; and (v) comparability with individually randomised trials (Higgins 2017). We will grade each potential source of bias as low, high, or unclear and provide a quote from the study report together with a justification for our judgement in the risk of bias table. We will summarise the risk of bias assessment across different studies for each of the domains listed using risk of bias figures. We will also document information on risk of bias related to unpublished data or correspondence with a trialist in the risk of bias table. A detailed description of criteria for a judgement of 'low risk’, 'high risk’, or 'unclear risk’ is shown in Appendix 2.

When considering treatment effects, we will take into account the risk of bias for the studies that contribute to that outcome.

Measures of treatment effect

Where we suspect skewness, and if scale data have finite upper and lower limits, we will use the easy 'rule of thumb' calculation to test for skewness, that is if the standard deviation (SD), when doubled, is greater than the mean, it is unlikely that the mean is the centre of the distribution (Altman 1996); in such a case we plan not to enter the data into any meta‐analysis. If we find relevant data that are skewed, we will present the data in 'Other data' tables as medians and interquartile ranges.

Unit of analysis issues

Th unit of analysis will be the individual. If multi‐arm interventions are present in the included trials, we will take into account only the arms that are relevant to the scope of this review. If multiple intervention groups are described in the study, they will be merged to allow a single, pair‐wise comparison where appropriate. In the case of repeated observations in an included study, we will follow the guidelines in Chapter 23 of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2021a).

Dealing with missing data

We will note levels of attrition for all included trials. We will contact trial authors for missing data; if we receive no response, we will consider the available data.

For all outcomes, we will present available data from the study reports or from information obtained from the study authors. We will carry out analyses of dichotomous data, to the greatest degree possible, on an intention‐to‐treat (ITT) basis, that is we will attempt to include all participants in the groups to which they had been randomised, regardless of whether or not they received the allocated intervention. The denominator for each outcome in each trial will be the number of people randomised. Where a randomised participant is not included in the analysis, we will assume that there is no ulcer healing, that is the person will contribute to the denominator only. Where results are reported for all participants, but it is unclear how many people were originally randomised, we will use available‐case analysis.

Where possible, we will use the Review Manager 5 calculator to calculate missing SDs for continuous outcomes, using other data from the trial, such as confidence intervals or SEs, employing the formula SD = SE x √N (Higgins 2021b). When appropriate, we will estimate the MD using the method reported by Wan 2014 to convert median and interquartile range (IQR) into MD and CIs. We will calculate measures of variance when these are missing, or we will contact the study authors, where possible (Deeks 2021). Where these measures of variation remain unavailable, or data are skewed, we will describe the available data narratively.

Assessment of heterogeneity

Assessment of heterogeneity can be a complex, multifaceted process. We will consider clinical and methodological heterogeneity; that is variation in study participants, interventions, outcomes, and characteristics such as length of follow‐up. This assessment of clinical and methodological heterogeneity will be supplemented where appropriate by information regarding statistical heterogeneity, assessed using the Chi² test in conjunction with the I² measure (Higgins 2021b).

Where data are available and it is appropriate, we will use forest plots to evaluate the direction and magnitude of the effects and the degree of overlap between CIs. We will use the I² measure to compare heterogeneity amongst the trials in each analysis. However, we acknowledge that there may be substantial uncertainty in the value of I² with a small number of studies. In the case that we detect substantial heterogeneity, we will report it and its possible causes where possible.

We will follow the rough guide to the interpretation of I² values in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2021):

• 0% to 40%: might not be important;

• 30% to 60%: may represent moderate heterogeneity;

• 50% to 90%: may represent substantial heterogeneity;

• 75% to 100%: considerable heterogeneity.

When I² lies in an area of overlap between two categories (e.g. between 50% and 60%), we will consider differences in participants and interventions amongst the trials contributing data to the analysis (Deeks 2021). We will also assess statistical heterogeneity using the Chi² test. As we expect relatively few studies to be in the individual meta‐analyses (fewer than 10), we will set the significance level at P < 0.1.

Assessment of reporting biases

We will follow the systematic framework recommended by Page 2021 to assess risk of bias due to missing results (non‐reporting bias) in the meta‐analysis of ulcer incidence data. To make an overall judgement about risk of bias due to missing results, we will:

• identify whether expected outcome data are unavailable by comparing the details of outcomes in trials registers, protocols, or statistical analysis plans, if available, with the reported results. If the above information sources are unavailable, we will compare outcomes in the conference abstracts or 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; and

• 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 we will produce a funnel plot for meta‐analysis to seek more evidence regarding the extent of missing results, provided there are at least 10 included studies (Peters 2008; Salanti 2014).

Data synthesis

We will use Review Manager 5 for data synthesis (Review Manager 2020). Where clinical and methodological heterogeneity is thought to be acceptable, or of interest. We may meta‐analyse even when statistical heterogeneity is high, but will attempt to interpret the causes for this heterogeneity using sub‐group analyses and meta‐regression for that purpose, if possible.

We will address all outcomes in the 'Effects of interventions' section in the Results of the review in the same order as listed in the Types of outcome measures section. In addition, we will include a summary of results from the data synthesis and assessment of certainty of evidence in summary of findings tables for the main comparisons.

We will group findings first by comparison (e.g. telemedicine versus standard care; telemedicine plus standard care versus standard care; one type of telemedicine versus another type of telemedicine) and then by outcome. We will undertake meta‐analyses where we consider studies with the same comparator and reporting the same outcome (and outcome metric) to be reasonably similar in terms with respect to clinical and methodological characteristics. We plan to use a random‐effects model, as there is likely to be some heterogeneity between studies in terms of participant and intervention characteristics. A fixed‐effect approach is unlikely to be appropriate, as the assumption that a single underlying treatment effect is being estimated is unlikely to be correct.

We will use forest plots to present summary estimates (MD, RR or HR) with 95% CI. Where the same outcome is measured using different scales, we will use the SMD (95% CI) as a summary statistic. We will also consider the representation of subgroups in forest plots without overall pooling.

We will summarise results from studies not included in meta‐analyses in tables. We may also use other statistical synthesis methods, as described in Chapter 12 of the Cochrane Handbook for Systematic Reviews of Interventions, when it not possible to undertake a meta‐analysis if sufficient data are available (McKenzie 2021).

Subgroup analysis and investigation of heterogeneity

We will perform the following subgroup analyses for the primary outcomes (complete wound healing and lower limb amputation) if sufficient data are available.

• Age, e.g. children (under 18 years), adults (18 to 64 years), and elderly (65 years and over). Although most people with ulcers and diabetes are adults, there is the possibility that people with early diabetes (e.g. type 1) can develop ulcers earlier; furthermore, older people may face a different risk of complications when using telemedicine (Alam 2021).

We will perform formal testing for differences between subgroups as described in Review Manager 5 (Review Manager 2020), which will also guide the interpretation of results.

We will explore subgroup differences by interaction tests available within Review Manager 5 including the Chi² statistic and P value, and the interaction test I² value (Review Manager 2020).

Sensitivity analysis

We will carry out the following sensitivity analyses for our primary outcomes (complete wound healing and lower limb amputation) where appropriate to determine whether key methodological factors or decisions have affected the main results. We will group these analyses according to study design (individual, cross‐over, or cluster).

• We will only include studies with low risk of bias. We will consider a study as at low overall risk of bias if none of four domains (random sequence, allocation concealment, incomplete outcome data, and selective reporting) are deemed high risk.

• We will evaluate both fixed‐effect and random‐effects model meta‐analyses, examining any differences between the two estimates.

• We will investigate the effects of including studies with mixed populations.

• We will explore the impact of including studies with missing data (proportion of more than 20%) in the overall assessment of the results.

We will present these results and compare them with the overall findings.

Summary of findings and assessment of the certainty of the evidence

We will present summary of findings tables using GRADEpro GDT software (GRADEpro GDT), including results for the following outcomes.

• Proportion of people whose wounds have completely healed

• Time to complete wound healing

• Lower limb amputation

• All‐cause mortality

• Healthcare costs

• Health‐related quality of life of participants

• Adverse events (combined dichotomous outcome)

We will prepare a separate a summary of findings table for each comparison. Two review authors (OMP, FCFA) will independently grade the certainty of the evidence for each outcome using the criteria devised by the GRADE Working Group (Higgins 2021b; Schünemann 2021). We will consider the five GRADE considerations (risk of bias, consistency of effect, imprecision, indirectness and publication bias) to assess the certainty of the body of evidence for each outcome, and to draw conclusions about the certainty of evidence within the text of the review. We will rate the certainty of the evidence as 'high', 'moderate', 'low', or 'very low', and justify any downgrading of the certainty of the evidence in the footnotes, including additional comments where necessary. When evaluating the risk of bias domain, we will downgrade the GRADE assessment when a study is classified as being at high risk of bias for one or more domains, or when the risk of bias assessment for selection bias is unclear (i.e. classified as unclear for random sequence generation and allocation concealment). Since due to the nature of the interventions, blinding of participants or personnel will be unlikely, we will not downgrade the GRADE assessment solely for performance bias. We will only downgrade the certainty of the evidence when we also classify a study as being at high risk of bias for blinding of outcome assessment.