Types of studies

We will include RCTs regardless of their publication status or language of publication.

Types of participants

Adults (aged 18 or older) with T2DM.

Diagnostic criteria for type 2 diabetes mellitus

In order to be consistent with changes in the classification of and diagnostic criteria for diabetes mellitus over the years, the diagnosis should be established using the standard criteria valid at the time of the trial commencing (for example, ADA 2003; ADA 2008; WHO 1998). Ideally, trial authors should have described the diagnostic criteria. We will use the trial authors' definition of diabetes mellitus if necessary.

Because changes in diagnostic criteria did not appear after 2003, and the vast majority of RCTs on m‐health have taken place after 2003, we do not expect that diagnostic criteria will produce significant variability in the clinical characteristics of the participants included as well as in the results obtained. Trials involving participants with comorbid disorders will be eligible for inclusion as long as the primary focus of the intervention is DSME/S. Trials involving a broader population (e.g. in individuals with a chronic illness) can only be included when they present results for T2DM patients separately. When these data are not available we will request separate data from the authors.

Types of interventions

Definition of m‐health interventions

Mobile health (m‐health) interventions that provide diabetes self‐management education (DSME) and/or diabetes self‐management support (DSMS). An m‐health intervention is eligible when DSME/S is provided either via short message service (SMS), text messages, voice messages or via a smartphone application, and studied as the main intervention. We include SMS because from a conceptual point of view, we think that messages delivered by SMS and by a smartphone app will have the same effect, differing only in technical aspects. So although the SMS technique may soon become obsolete, the results of studies on DSME/S delivered by SMS still contribute to the body of evidence on m‐health. All mobile devices are eligible vehicles for the intervention: mobile phones, smartphones, tablets and other mobile devices. Wearables will be only included when DSME/S is delivered directly to the wearable, or when DSME/S is delivered to a mobile phone, smartphone or other mobile device that is connected to the wearable.

Definition of diabetes self‐management education

Diabetes self‐management is "the ongoing process of facilitating the knowledge, skill, and ability necessary for diabetes self‐care" (Powers 2015). The ultimate goal of DSME is to improve clinical outcomes, health status and quality of life by means of activating patients towards informed decision making, self‐care behaviours, problem solving, and active collaboration with the healthcare team (Powers 2015).

Definition of diabetes self‐management support

Diabetes self‐management supports are "activities that assist the person with diabetes in implementing and sustaining the behaviours needed to manage his or her condition on an ongoing basis" (Powers 2015).This can be behavioural, educational, psychosocial or clinical support.

Definition of usual care

Usual care is defined as standard care that individuals with T2DM should receive according to national guidelines.

We plan to investigate the following comparisons of intervention versus control/comparator.

Intervention

• M‐health intervention that provides DSME

• M‐health intervention that provides DSMS

• M‐health intervention that provides DSME/S

Comparator

• Attention placebo control (APC) compared with any eligible intervention. Since the m‐health intervention may have a psychosocial component, the classical design of an active treatment versus a control group might not be appropriate. To test the effect of the psychosocial intervention, an APC can be included. This APC group does not receive the actual psychosocial intervention but receives an intervention that covers the same amount of time and attention as the experimental group receives (Popp 2015).

• Usual care (no intervention) compared with any intervention.

Note: we will perform a subgroup analysis to investigate any differences in effect estimates between studies with an APC group and studies with a usual care control group (see the Subgroup analysis and investigation of heterogeneity section).

Concomitant interventions will have to be the same in both the intervention and comparator groups to establish fair comparisons.

Minimum duration of intervention

The clinically meaningful minimal duration of the intervention will be two months.

Minimum duration of follow‐up

Minimal duration of follow‐up will be two months after start of the intervention, that is, we will include effects measured immediately after the end of the intervention.

We will define extended follow‐up periods (also called open‐label extension studies) for outcomes measured once the original trial, as specified in the trial protocol, has been terminated. However, such studies are frequently of an observational nature, and we will primarily evaluate them for adverse events (Buch 2011; Megan 2012).

Summary of specific exclusion criteria

• Trials in individuals aged less than 18 years.

• Trials including pregnant women.

• Trials investigating a mixture of type 1 and type 2 diabetes participants, when the results for type 1 and type 2 diabetes participants are not presented separately (when these data are not available we will request separate data from the authors) or when fewer than 75% of the participants have T2DM.

• Trials investigating personal communication by mobile phones only, such as telephone calls with healthcare professionals.

• Trials investigating non‐automated interventions, such as tailored feedback on glucose values from healthcare professionals instead of an automated algorithm.

• Trials investigating personal records, data entries or diaries.

• Trials investigating m‐health interventions targeted at healthcare workers.

Types of outcome measures

We will not exclude trials that do not report on one or several of our primary or secondary outcome measures. We will exclude trials failing to report on any our primary or secondary outcomes, but we will provide some basic information in an additional table.

We will consider most outcomes measured at the end of the intervention or within 30 days after the end of the intervention (short‐term follow‐up), between one month and six months after the end of the intervention (medium‐term follow‐up), or more than six months after the end of the intervention (long‐term follow‐up). However, we will consider adverse events and all‐cause mortality at any time after randomisation.

Electronic searches

We will search the following sources from the year 2000 to the specified date and will place no restrictions on the language of publication. In 2000, approximately one in three inhabitants in the United States had a mobile phone subscription (Little 2012).

• Cochrane Central Register of Controlled Trials (CENTRAL) via the Cochrane Register of Studies Online (CRSO).

• MEDLINE Ovid (Epub Ahead of Print, In‐Process & Other Non‐Indexed Citations, Ovid MEDLINE(R) Daily and Ovid MEDLINE(R)).

• Embase Ovid.

• PsycINFO Ovid.

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

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

We will continuously apply a MEDLINE (via Ovid SP) email alert service to identify newly published trials using the same search strategy as described for MEDLINE (for details on search strategies, see Appendix 1). Should we identify new trials for inclusion, we will evaluate these, incorporate the findings into our review and resubmit another review draft (Beller 2013).

Searching other resources

We will try to identify other potentially eligible trials or ancillary publications by searching the reference lists of included trials, systematic reviews, meta‐analyses and health technology assessment reports. In addition, we will contact authors of included trials to identify any additional information on the retrieved trials and further trials that we may have missed.

We will not use abstracts or conference proceedings for data extraction, because this information source does not fulfil the Consolidated Standards of Reporting Trials (CONSORT) requirements, which is "an evidence‐based, minimum set of recommendations for reporting randomized trials" (CONSORT 2010; Scherer 2007), unless we can obtain full data from trial authors. We will list key data of abstracts in an appendix. We will show key information on abstracts or conference proceedings in the 'Characteristics of studies awaiting classification' table.

Selection of studies

Two review authors (AMB, RV) will independently screen the abstract, title or both, of every record we retrieve in the literature searches, to determine which trials we should assess further. We will obtain the full‐text of all potentially relevant records. We will resolve any disagreements through consensus or by recourse to a third review author (GR). If we cannot resolve a disagreement, we will categorise the trial as a 'study awaiting classification' and will contact the trial authors for clarification. We will present an adapted PRISMA flow diagram to show the process of trial selection (Liberati 2009). We will list all articles excluded after full‐text assessment in a 'Characteristics of excluded studies' table and will provide the reasons for exclusion.

Data extraction and management

For trials that fulfil our inclusion criteria, two review authors (AMB, RV) will independently extract key participant and intervention characteristics. We will describe interventions using the 'template for intervention description and replication' (TIDieR) checklist (Hoffmann 2014; Hoffmann 2017). We will report data on efficacy outcomes and adverse events using standardised data extraction sheets from the Cochrane Metabolic and Endocrine Disorders Group. We will resolve any disagreements by discussion or, if required, we will consult a third review author (GR).

We will provide information about potentially relevant ongoing trials, including the trial identifiers, in the 'Characteristics of ongoing trials' table and in a joint appendix 'Matrix of trial endpoint (publications and trial documents)'. We will try to find the protocol for each included trial and will compare primary, secondary and other outcomes described there and in the full‐text study reports in a joint appendix.

We will email all authors of included trials to enquire whether they would be willing to answer questions regarding their trials. We will present the results of this survey in an appendix. We will thereafter seek relevant missing information on the trial from the primary trial author(s), if required.

Dealing with duplicate and companion publications

In the event of duplicate publications, companion documents or multiple reports of a primary trial, we will maximise the information yield by collating all available data, and we will use the most complete data set aggregated across all known publications. We will list duplicate publications, companion documents, multiple reports of a primary trial and trial documents of included trials (such as trial registry information) as secondary references under the study identifier (ID) of the included trial. Furthermore, we will also list duplicate publications, companion documents, multiple reports of a trial and trial documents of excluded trials (such as trial registry information) as secondary references under the study ID of the excluded trial.

Data from clinical trial registers

If data from included trials are available as study results in clinical trial registers such as ClinicalTrials.gov or similar sources, we will make full use of this information and extract the data. If there is also a full publication of the trial, we will collate and critically appraise all available data. If an included trial is marked as a completed study in a clinical trial register but no additional information (study results, publication or both) is available, we will add this trial to the table 'Characteristics of studies awaiting classification'.

Assessment of risk of bias in included studies

Two review authors (AMB, RV) will independently assess the risk of bias for each included trial. We will resolve any disagreements by consensus or by consulting a third review author (GR). In case of disagreement, we will consult the rest of the review author team and make a judgement based on consensus. If adequate information is unavailable from the trials or trial protocols, we will contact the trial authors to recover missing data on 'Risk of bias' items.

We will use the Cochrane 'Risk of bias' assessment tool and assign judgments of low, high or unclear risk of bias (Higgins 2011a; Higgins 2011b). We will evaluate individual bias items as described in the Cochrane Handbook for Systematic Reviews of Interventions according to the criteria and associated categorisations contained therein(Higgins 2011b).

Random sequence generation (selection bias due to inadequate generation of a randomised sequence)

For each included trial we will describe the method used to generate the allocation sequence in sufficient detail to enable assessment of whether it should produce comparable groups.

• Low risk of bias: the trial authors achieved sequence generation using computer‐generated random numbers or a random numbers table. Drawing of lots, tossing a coin, shuffling cards or envelopes, and throwing dice are adequate if an independent person performed this who was not otherwise involved in the trial. We will consider the use of the minimisation technique as equivalent to being random.

• Unclear risk of bias: insufficient information about the sequence generation process.

• High risk of bias: the sequence generation method was non‐random or quasi‐random (e.g. 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; allocation by judgement of the clinician; allocation by preference of the participant; allocation based on the results of a laboratory test or a series of tests; or allocation by availability of the intervention).

Allocation concealment (selection bias due to inadequate concealment of allocation prior to assignment)

We will describe for each included trial the method used to conceal allocation to interventions prior to assignment, and we will assess whether intervention allocation could have been foreseen in advance of or during recruitment, or changed after assignment.

• Low risk of bias: central allocation (including telephone, interactive voice‐recorder, Internet‐based and pharmacy‐controlled randomisation); sequentially numbered drug containers of identical appearance; sequentially numbered, opaque, sealed envelopes.

• Unclear risk of bias: insufficient information about the allocation concealment.

• High risk of bias: using an open random allocation schedule (e.g. a list of random numbers); assignment envelopes were used without appropriate safeguards; alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure.

We will also evaluate trial baseline data to incorporate assessment of baseline imbalance into the 'Risk of bias' judgement for selection bias (Corbett 2014). Chance imbalances may also affect judgements on the risk of attrition bias. In the case of unadjusted analyses, we will distinguish between trials we rate as being at low risk of bias on the basis of both randomisation methods and baseline similarity, and trials we judge as being at low risk of bias on the basis of baseline similarity alone (Corbett 2014). We will re‐classify judgements of unclear, low or high risk of selection bias as specified in Appendix 2.

Blinding of participants and study personnel (performance bias due to knowledge of the allocated interventions by participants and personnel during the trial)

We will evaluate the risk of detection bias separately for each outcome (Hróbjartsson 2013). We will note whether endpoints were self‐reported, investigator‐assessed or adjudicated outcome measures (see below).

• Low risk of bias: blinding of participants and key study personnel is ensured, and it is unlikely that the blinding could have been broken; no blinding or incomplete blinding, but we judge that the outcome is unlikely to have been influenced by lack of blinding.

• Unclear risk of bias: insufficient information about the blinding of participants and study personnel; the trial does not address this outcome.

• High risk of bias: no blinding or incomplete blinding, and the outcome is likely to have been influenced by lack of blinding; blinding of trial participants and key personnel attempted, but likely that the blinding could have been broken, and the outcome is likely to be influenced by lack of blinding.

Blinding of outcome assessment (detection bias due to knowledge of the allocated interventions by outcome assessment)

We will evaluate the risk of detection bias separately for each outcome (Hróbjartsson 2013). We will note whether endpoints were self‐reported, investigator‐assessed or adjudicated outcome measures (see below).

• Low risk of bias: blinding of outcome assessment is ensured, and it is unlikely that the blinding could have been broken; no blinding of outcome assessment, but we judge that the outcome measurement is unlikely to have been influenced by lack of blinding.

• Unclear risk of bias: insufficient information about the blinding of outcome assessors; the trial did not address this outcome.

• High risk of bias: no blinding of outcome assessment, and the outcome measurement is likely to have been influenced by lack of blinding; blinding of outcome assessment, but likely that the blinding could have been broken, and the outcome measurement is likely to be influenced by lack of blinding.

Measures of treatment effect

When at least two included trials are available for a comparison and a given outcome, we will try to express dichotomous data as a risk ratio (RR) or odds ratio (OR) with 95% confidence interval (CI). For continuous outcomes measured on the same scale (e.g. weight loss in kg) we will estimate the intervention effect using the mean difference with 95% CI. For continuous outcomes that measure the same underlying concept (e.g. health‐related quality of life) but use different measurement scales, we will calculate the standardised mean difference (SMD). We will express time‐to‐event data as a hazard ratio (HR) with 95% CI.

Unit of analysis issues

We will take into account the level at which randomisation occurred, such as cross‐over trials, cluster‐randomised trials and multiple observations for the same outcome. If more than one comparison from the same trial is eligible for inclusion in the same meta‐analysis, we will either combine groups to create a single pair‐wise comparison or appropriately reduce the sample size so that the same participants do not contribute more than once (splitting the 'shared' group into two or more groups). While the latter approach offers some solution to adjusting the precision of the comparison, it does not account for correlation arising from the same set of participants being in multiple comparisons (Higgins 2011c).

We will attempt to reanalyse cluster‐RCTs that have not appropriately adjusted for potential clustering of participants within clusters in their analyses. The variance of the intervention effects will be inflated by a design effect. Calculation of a design effect involves estimation of an intra‐cluster correlation (ICC). We will obtain estimates of ICCs through contact with the trial authors, impute them using estimates from other included trials that report ICCs, or use external estimates from empirical research (e.g. Bell 2013). We plan to examine the impact of clustering using sensitivity analyses.

Dealing with missing data

If possible, we will obtain missing data from the authors of the included trials. We will carefully evaluate important numerical data such as screened, randomly assigned participants as well as intention‐to‐treat, and as‐treated and per‐protocol populations. We will investigate attrition rates (e.g. dropouts, losses to follow‐up, withdrawals), and we will critically appraise issues concerning missing data and use of imputation methods (e.g. last observation carried forward).

In trials where the standard deviation (SD) of the outcome is not available at follow‐up or cannot be recreated, we will standardise by the average of the pooled baseline SD from those trials that reported this information.

Where included trials do not report means and SDs for outcomes and we do not receive the necessary information from trial authors, we will impute these values by estimating the mean and variance from the median, range, and the size of the sample (Hozo 2005).

We will investigate the impact of imputation on meta‐analyses by performing sensitivity analyses, and we will report which trials were included with imputed SDs for each outcome.

Assessment of heterogeneity

In the event of substantial clinical or methodological heterogeneity, we will not report trial results as the pooled effect estimate in a meta‐analysis.

We will identify heterogeneity (inconsistency) by visually inspecting the forest plots and by using a standard Chi² test with a significance level of α = 0.1. In view of the low power of this test, we will also consider the I² statistic, which quantifies inconsistency across trials to assess the impact of heterogeneity on the meta‐analysis (Higgins 2002; Higgins 2003).

When we find heterogeneity, we will attempt to determine the possible reasons for it by examining individual trial and subgroup characteristics.

Assessment of reporting biases

If we include 10 or more trials that investigate a particular outcome, we will use funnel plots to assess small‐trial effects. Several explanations may account for funnel plot asymmetry, including true heterogeneity of effect with respect to trial size, poor methodological design (and hence bias of small trials) and publication bias. Therefore we will interpret the results carefully (Sterne 2011).

Data synthesis

We plan to undertake (or display) a meta‐analysis only if we judge participants, interventions, comparisons and outcomes to be sufficiently similar to ensure an answer that is clinically meaningful. Unless good evidence shows homogeneous effects across trials, we will primarily summarise low risk of bias data using a random‐effects model (Wood 2008). We will interpret random‐effects meta‐analyses with due consideration to the whole distribution of effects and present a prediction interval (Borenstein 2017a; Borenstein 2017b). A prediction interval needs at least three trials to be calculated and specifies a predicted range for the true treatment effect in an individual trial (Riley 2011). For rare events, occurring at rates below 1%, we will use Peto's odds ratio method, provided that there is no substantial imbalance between intervention and comparator group sizes and intervention effects are not exceptionally large. In addition, we will also perform statistical analyses according to the guidelines presented in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2011).

Subgroup analysis and investigation of heterogeneity

We expect the following characteristics to introduce clinical heterogeneity, and we plan to carry out subgroup analyses including investigation of interactions (Altman 2003).

• Sex: we expect men and women to respond differently to DSME delivered via m‐health.

• Age: because age may be highly correlated to computer literacy, we expect age to be a potential effect modifier. We will use 60 years as the cut‐off age, analysing those under 60 and those aged 60 or older separately.

• Ethnicities: minorities within a country may have language issues that result in decreased comprehension.

• Socioeconomic status: people with a low socioeconomic status may have less prior knowledge on DSME.

• Treatment groups (insulin versus oral glucose‐lowering therapy and behaviour changing advice only): in people who use insulin, baseline HbA1c is likely to be higher, and the risk of weight gain and hypoglycaemia is higher. Besides, their prior DSME knowledge will differ from the DSME knowledge in people not on insulin therapy.

• Levels of metabolic control: in study populations with higher average baseline HbA1c level (poor metabolic control), the effect size of the intervention might be larger. As a cut‐off point for poor metabolic control we will use: HbA1c of more than 64 mmol/mol (> 8%) versus HbA1c of 64 mmol/mol or less (≤ 8%).

• Type of control group: studies with an APC group versus studies with a usual care control group (see 'Comparator' within the 'Types of interventions' section).

Sensitivity analysis

We plan to perform sensitivity analyses to explore the influence of the following factors (when applicable) on effect sizes by restricting analysis to the following.

• Published trials.

• The effect of risk of bias, as specified in the Assessment of risk of bias in included studies section.

• Very long (≥ 12 months) or large trials (≥ 200 participants) to establish the extent to which they dominate the results.

• Using the following filters: imputation, language of publication, source of funding (industry versus other), or country.

We will also test the robustness of results by repeating the analyses using different measures of effect size (RR, OR, etc.) and different statistical models (fixed‐effect and random‐effects models).