Criteria for considering studies for this review
Types of studies
We will include individually and cluster randomised controlled trials (RCTs), controlled clinical trials (CCTs), controlled before and after studies (CBAs), and interrupted time series (ITS) studies. Educational interventions are often complex and include multiple approaches that may not be have been evaluated by RCTs. The inclusion of the CCT, CBA and ITS designs will enable us to capture these other studies. We will exclude all other types of studies.
Types of participants
Healthcare staff including medical and nursing staff, allied health professionals, foot-care assistants and others that are involved in frontline management of people with diabetes at risk of foot ulceration in any healthcare setting (e.g. hospital, clinic, or care establishment). In order to differentiate between types of healthcare professionals we will use existing descriptions from included studies. This review is centred on continuing professional development for health-service staff, and will excluded all students who are being trained in the healthcare setting.
Types of interventions
We will consider interventions of education programmes, or programmes that include distribution of educational materials, workshops, short courses, and open learning (didactic, interactive or mixed) delivered to qualified healthcare professionals either individually or as groups. We will include trials comparing additional training with no additional training or standard practice, or those that compare knowledge transfer (passive forms of intervening such as distribution of educational materials) with programmes directed at changing healthcare professional behaviour.
The review will include, but will not be limited to, studies specifically targeting education for behaviour change or clinical outcomes with regard to the management of diabetic foot problems. Interventions described in the included studies will be categorised as either foot-care specific interventions, or composite diabetes interventions (education or behaviour change for improving diabetes control and reducing complications).
We will consider the following comparisons:
Educational intervention compared with no intervention or usual practice.
Transfer of knowledge intervention (e.g. pamphlets, brochures, online newsletters and continuing medical education) compared with intervention aimed at behaviour change (e.g. face-to-face training, workshops, webinars etc.).
Types of outcome measures
The outcomes of this review fall into two major categories, namely: (1) new foot complications, or change in foot complications in people with diabetes, and (2) and change in knowledge and practice of healthcare professionals. For all outcomes we will accept standard measures of assessment of foot complications or use of validated instruments (e.g. swab cultures, bone scans, probe-to-bone, red blood cell (erythrocyte) sedimentation rate, labelled monoclonal antibody, magnetic resonance imaging (MRI), plain radiographs, labelled bone scintigraphy, and wound-based clinical scoring systems). Outcome assessment will include both foot-specific outcomes (ulcers, amputations etc.) as well as healthcare provider behaviour change. All primary outcomes and selected secondary outcomes will be used to populate the summary of findings table. To ensure a temporal relationship between intervention and foot complication outcomes we will measure the time between baseline evaluation, intervention and outcome in order to determine whether the observed outcome was most probably due to the intervention.
The primary outcomes are outcomes of clinical importance to people with diabetes:
Incidence of new foot ulcers, or ulcer recurrence.
Incidence of amputations classified as major amputations (above knee or below knee amputation), and minor amputations (across the foot (trans-metatarsals) or toe removal (digital)).
Where data are available we will assess the impact of the intervention on the time to ulcer development, or amputation, using hazard ratios.
The secondary outcomes will include:
Occurrence of bacterial or fungal foot infections (assessed by clinical observation by physician, and or laboratory confirmed swab cultures).
Number, and duration, of hospital admissions for diabetic foot problems.
Change in patients' knowledge and behaviour pre- and post-intervention.
Change in healthcare professionals' knowledge and behaviour (pre- and post-test assessments following intervention).
Change in healthcare professionals' practice (e.g. routine foot inspection, educating patients on foot-care practices).
New onset neuropathic osteoarthropathy (Charcot's foot), or its precursors.
Development of hard skin (callus) (i.e. presence of lesions, or detailed description of the number, location or diameter of lesions).
Resolution of callus.
Visits to healthcare provider for foot infections.
Search methods for identification of studies
We will search the following electronic databases to identify reports of relevant randomised clinical trials:
The Cochrane Wounds Group Specialised Register (most recent);
The Cochrane Central Register of Controlled Trials (CENTRAL) (The Cochrane Library, latest issue);
Ovid MEDLINE (1946 to present);
Ovid EMBASE (1974 to present);
EBSCO CINAHL (1982 to present).
We will use the following provisional search strategy in The Cochrane Central Register of Controlled Trials (CENTRAL):
#1 MeSH descriptor Education, Professional explode all trees
#2 MeSH descriptor Education, Continuing explode all trees
#3 (professional* NEAR/5 (educat* or training)):ti,ab,kw
#4 ((nurs* or doctor* or physiotherap* or therapist* or surgeon* or practitioner* or podiatr*) NEAR/5 (educat* or training)):ti,ab,kw
#5 ((education* or training) NEXT program*):ti,ab,kw
#6 (seminar* or workshop* or course* or open learning):ti,ab,kw
#7 ((written or printed or oral) NEXT information):ti,ab,kw
#8 (leaflet* or booklet* or pamphlet* or poster*):ti,ab,kw
#9 (#1 OR #2 OR #3 OR #4 OR #5 OR #6 OR #7 OR #8)
#10 MeSH descriptor Foot Ulcer explode all trees
#11 MeSH descriptor Diabetic Foot explode all trees
#12 (diabet* NEAR/5 ulcer*):ti,ab,kw
#13 (diabet* NEAR/5 (foot or feet)):ti,ab,kw
#14 (diabet* NEAR/5 wound*):ti,ab,kw
#15 (diabet* NEAR/5 amputat*):ti,ab,kw
#16 (#10 OR #11 OR #12 OR #13 OR #14 OR #15)
#17 (#9 AND #16)
We will adapt this strategy to search Ovid MEDLINE, Ovid EMBASE and EBSCO CINAHL. 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 developed by the UK Cochrane Centre (Lefebvre 2011). We will combine the CINAHL searches with the trial filters developed by the Scottish Intercollegiate Guidelines Network (SIGN 2011). We will not restrict studies with respect to language, date of publication or study setting.
We will search the following clinical trials registries:
Searching other resources
We will search the bibliographies of all included trials identified by the above strategies for further relevant studies.
Data collection and analysis
Selection of studies
Study titles and abstracts of articles retrieved by the electronic and handsearches will be read independently by two review authors (TF and SJ). These will be assessed for eligibility, according to the inclusion criteria above. Full copies of all references deemed potentially eligible by any of the review authors will be retrieved for closer examination. All studies that initially appear to meet the inclusion criteria from this first screening, but on closer inspection (full text) do not, will be detailed in the Table of Excluded Studies with reasons for their exclusion. We will include a PRISMA flowchart of the data management phase of the review (Liberati 2009).The full text review will be done independently by two review authors (TF and SJ). Disagreements will be settled by a third review author (PL).
Data extraction and management
Data will be extracted by up to four review authors (PL, SJ, TF, and DF) independently, who will review each other's work, in order to minimise data abstraction errors. Data abstraction forms will be developed: they will be based on the data collection forms from the Cochrane Effective Practice and Organization of Care (EPOC) review group (EPOC 2000), and will be modified for the purposes of this review. We will extract data on study design, description of the intervention, details about participants (including number in each group), length of intervention, definition of diabetic foot ulcer, all primary and secondary outcomes, setting, and statistical analysis used. Where possible, we will record relevant socio-demographic variables, including geographic location, gender, age of person, and category of healthcare professional.
Assessment of risk of bias in included studies
Two review authors (DF and CC) will independently assess the risk of bias for each study using the following criteria:
For RCTs and CCTs, the methodological quality of study will be assessed and recorded using the Cochrane Collaboration's tool for assessing risk of bias (Higgins 2011a). The tool addresses six specific domains:
Selection bias (random sequence generation, allocation concealment).
Performance bias (blinding of participants and personnel).
Detection bias (blinding outcome assessment).
Attrition bias (incomplete outcome data).
Reporting bias(selective outcome reporting).
To determine the risk of bias of included studies, we will evaluate the adequacy of information and likelihood of potential bias for each criterion. The judgement for each criterion will be assessed as 'low risk', 'high risk', or 'unclear risk' of bias. In a consensus meeting, we will discuss and resolve disagreements among the review authors. If consensus cannot be reached, a third review author (VW) will make the final decision(s). When important study information is missing from trial reports, we will contact trial authors to request the information using open-ended questions.
For CBAs, we will use the Risk of Bias Tool from the Cochrane EPOC Group (EPOC 2013). This tool covers allocation sequence, similarity of baseline outcome measurement, similarity of baseline characteristics, incomplete outcome data, blinding of allocation, protection against contamination, selective outcome reporting, and other risks of bias.
Our appraisal criteria for ITS studies will be adapted from the 'Risk of bias' checklist developed by the Cochrane EPOC Group (EPOC 2013). In assessing risk of bias in the ITS designs, we will consider protection against secular changes (including intervention independent of other changes, appropriate data analysis, and reason for number of pre and post points given), effect on data collection, knowledge of allocated interventions, incomplete outcome data, selective outcome reporting, and other biases. Minimum methodological inclusion criteria across all designs will be:
Objective measurement of performance or provider behaviour on a health, or patient, outcome in a clinical, rather than a test, situation.
Relevant and interpretable data are presented or can be obtained.
Measures of treatment effect
The data extracted from the studies will be entered into Review Manager 5 (RevMan 2011). A summary table describing the study characteristics will be completed.
For dichotomous data, a 2 x 2 contingency table will be compiled including the number of participants with each outcome event and risk ratios (RR) with 95% confidence intervals (CI).
Continuous data will be analysed if means and standard deviations are available, and there is no clear evidence of significant skewness (i.e. skewness with a value greater than one) in the distribution. For continuous outcomes measured identically across studies, an overall mean difference (MD) and 95% CI will be calculated. Otherwise, we will use an overall standardised mean difference (SMD) and 95% CI. SMDs will be calculated using Hedges g as described in the Cochrane Handbook for Systematic Reviews of Interventions (Section 7.7.3) (Higgins 2011b).
Unit of analysis issues
Multiple outcomes and designs
We have a number of different outcomes and study designs. Conceptually, these outcomes and designs cannot be combined (for example, CBA and RCTs ). Therefore, a meta-analysis will be conducted separately for each outcome. Furthermore, for each outcome, we will meta-analyse the following separately: 1) developing versus developed countries (defined as developed/high income or developing/low and middle income according to the World Bank classification World 2011); 2) different study designs (ITSs, RCTs, CCTs, and CBAs). We have chosen to analyse developing versus developed countries as the two settings are very different in terms of incidence and prevalence of our primary outcomes, standard of care, and other contextual factors (follow-up visits, availability of continuing education to healthcare professionals etc.).
Cluster randomised trials
Where trials have used clustered randomisation, we anticipate that the study investigators would have controlled appropriately for clustering effects (for example, variance-inflated standard errors, and hierarchical linear models) before presenting their results. We expect, however, that some cluster RCTs may not account for cluster effect in analysis, leading to unit of analysis errors in which P values can be artificially extreme and confidence intervals overly narrow. If sufficient data are presented, we will re analyse studies with potential unit of analysis errors using the Cochrane Handbook methods to calculate the variance-inflation factor. We will search for appropriate intra-class correlation coefficients (ICCs) from the included studies or authors, or from other published studies when ICCs are not available from the included studies. If a comparison is re analysed, we will annotate it as 're analysed'. Following this, effect sizes and standard errors will be meta-analysed in RevMan using the generic inverse method described in the Cochrane Handbook for Systematic Reviews of Interventions (Section 16.3) (Higgins 2011a).They will be combined with estimates from individual level trials.
We will use sensitivity analyses to assess the potential biasing effects of using the intra-class correlation coefficients that have been derived in different ways (for example, based on individual patient data, estimated from other studies).
We will use time series regression to re analyse each comparison when accounting for unit of analysis errors in ITS designs.
Pre- and post-tests
When baseline data are not available, results will be expressed as the relative or absolute difference between intervention and control group at follow up (difference between post-intervention values in the education intervention and control groups expressed as a percentage of post-intervention values in the control group).
Dealing with missing data
Authors will be contacted to supply missing or unreported data, such as incidence or rate of infection, standard deviations, details of attrition or details of education interventions received by the intervention groups. If outcome data are only reported for participants completing the trial or who followed protocol, then authors will be contacted for additional information to enable an analysis to be conducted according to intention-to-treat principles. Missing data and attrition will be described for each included study in the Risk of Bias table. If missing data are unobtainable, the extent to which the results or conclusions of the review might be affected by this will be assessed and discussed.
Assessment of heterogeneity
Heterogeneity between trial results will be tested using a standard Chi2 test, to assess whether observed differences in results are compatible with chance alone. The I² test will be used to examine the percentage of total variation across studies due to heterogeneity rather than due to chance. Values over 75% indicate a high level of heterogeneity (Higgins 2003). If substantial heterogeneity is detected, studies will be combined by narrative summary only, and heterogeneity explored by conducting predefined subgroup analyses.
If heterogeneity exists, we will examine potential sources using the following steps:
Assessment of reporting biases
If sufficient studies are found (at least 10 studies), funnel plots will be drawn to investigate any relationship between effect size and trial size. Asymmetry in the plots could be due to publication bias, but could also be due to a real relationship between trial size and effect size, for example, when larger trials have lower compliance, and compliance is positively related to effect size. In the event that we find such a relationship, we will examine clinical diversity of the studies (Section 10.4) (Higgins 2011b). As a direct test for publication bias, we will compare results extracted from published journal reports with results obtained from other sources (including correspondence).
RCTs, CCTs, and CBAs
To perform meta-analyses of continuous data, we will input data on means, standard deviations, and the number of participants for each outcome in each group. It is important to note that, in all cases, these means and standard deviations will be unadjusted for confounders, however, they will be adjusted for clustering when needed.
Where baseline data are available from RCTs, CCTs and CBAs, pre-intervention and post-intervention means and scores will be reported for both the educational intervention(s) and control groups and the absolute change from baseline will be calculated (change in study group values minus change in control group values), along with standard deviations and 95% CI where possible. If standard deviations (SD) for change are not given, we will calculate them. In performing our meta-analysis, we will use the inverse-variance random-effects model.
For discrete outcomes (for example, increase in knowledge score versus no increase in knowledge), we will present the relative risk of the outcome compared to the control group. We will also calculate the risk difference, that is, the absolute difference in the proportions in each intervention group. Finally, we will calculate the number needed to treat for an additional beneficial outcome such as prevention of one incidence of diabetic foot ulceration or amputation.
'Summary of findings' tables
We will construct 'Summary of findings' (SoF's) tables for the primary outcomes and for the first five of the secondary outcomes listed earlier. Provided there is an adequate number of studies from developing versus developed countries (i.e. three or more in each group), we will develop separate tables for developing and developed country settings and for significant subgroups using the GRADE protocol (Guyatt 2011).
Data will be synthesised for all studies. If the included studies are not sufficiently homogeneous to combine in a meta-analysis, we will use the methods described in the Cochrane Handbook for Systematic Reviews of Interventions (section 220.127.116.11) (Higgins 2011a) to present the data . We will display the results of included studies in a forest plot, but suppress the pooled estimate, while sorting studies by design feature and according to the developing versus developed country categories.
Subgroup analysis and investigation of heterogeneity
We will conduct subgroup analyses based on a priori clinical knowledge, and possible sources of variation among studies suggested by Deeks 2011. Additionally, we will also perform subgroup analyses based on the intervention-specific categories listed below:
Developed versus developing country as defined by the World Bank (World 2011).
Healthcare setting (e.g. podiatry clinics versus general hospitals versus general practice).
Category of healthcare professional (medical doctor versus other).
Foot-care specific intervention versus composite diabetes interventions.
If heterogeneity is an issue, we will conduct meta-regression to assess the relation of size of effect to characteristics of the trials. The characteristics we will include in the meta-regression will be country, healthcare setting, and category of healthcare professionals (as above).
We will use sensitivity analyses (1) to assess the robustness of results by including only studies at overall low risk of bias, and (2) to assess the robustness of results to variations in the estimated values of ICC.