Types of studies

We will include randomised trials reported as full‐text studies, conference abstracts and unpublished data, irrespective of their publication status and language of publication.

Types of participants

All types of healthcare providers (i.e. professionals, paraprofessionals and lay health workers) providing client care through mobile‐based technologies. We will include studies targeting patients with any condition, regardless of their location, setting, diagnoses, or demographic factors such as age. We will not include studies where the primary purpose is education or training.

Types of interventions

We will include trials comparing healthcare delivered through a mobile device versus standard care, which we define as usual care for the setting where the study took place, including face‐to‐face exchanges and communication through other non‐digital channels.

By mobile‐based technologies for healthcare providers to communicate and manage clients, we mean healthcare providers who are geographically separated using information and communication technologies. We will focus exclusively on engagement where the healthcare provider enquiry receives a response in real‐time or as immediate as clinically appropriate.

We will focus exclusively on clinical information that professionals can exchange over wireless and mobile technologies, mobile phones of any kind (but not analogue landline telephones), tablets, personal digital assistants and smartphones. Communication channels via mobile device can include text messaging, video messaging, social media, voice calls, voice over Internet Protocol (VoIP), and videoconferencing, through software such as Skype, WhatsApp or Google Hangouts.

We will include:

• studies in which the healthcare provider uses telemedicine to seek clinical guidance and support from other qualified healthcare providers in order to deliver direct patient care. This would include coordination of referrals and requests for expert opinion and diagnosis;

• studies in which the provider(s) seeking guidance is at a different location from the provider(s) offering guidance; and

• studies in which the provider(s) seeking guidance transmits clinical information via a mobile device and the provider(s) offering guidance responds on any device, including stationary devices.

We will include studies assessing unspecified types of communication devices for transmitting the clinical information, since studies often fail to report this detail.

We will include all health issues and will not restrict the content of clinical health information exchanged. We will include studies where the digital component of the intervention is delivered as part of a wider package if we have judged it to be the core component of the intervention.

We will exclude:

• pilot and feasibility studies (pilot study defined as "a version of the main study that is run in miniature to test whether the components of the main study can all work together" and feasibility study as "pieces of research done before a main study"; Arain 2010);

• studies that compare different technical specifications of telecommunication technologies (e.g. different communication channels, software, etc.);

• studies in which the use of telecommunications technology is not directly linked to patient care;

• studies in which the primary purpose is education/training;

• studies assessing the accuracy of a portable medical device.

Types of outcome measures

Electronic searches

An information specialist developed the search strategies in consultation with the review authors and WHO content experts. We will use a minimum cutoff search date of 2000, based on the increased availability and penetration of mobile devices used for telemedicine from that date on (ITU 2017). Appendix 1 lists the search strategy for MEDLINE. We will search the following databases.

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

• MEDLINE Ovid.

• Embase Ovid.

• POPLINE.

• WHO Global Health Library.

Searching other resources

Selection of studies

We will download all titles and abstracts retrieved by electronic searching to a reference management database and remove duplicates. For title and abstract screening, we will use a machine learning classifier that is able to assign a probability score that a given record describes, or does not describe, a randomised trial (Wallace 2017). Two review authors (of BB, NH, NM) will screen titles and abstracts of studies with at least a 10% probability of being a randomised trial, and one review author will screen those with less than a 10% probability. We will retrieve the full‐text study reports/publication of all potentially eligible reports, and two review authors (of BB, NH, NM) will independently screen the full text to identify studies for inclusion and to identify and record reasons for excluding the ineligible studies. We will resolve any disagreement through discussion, and if required we will consult a third review author (DGB or SS).

We will list studies that initially appeared to meet the inclusion criteria but that we later excluded in the 'Characteristics of excluded studies' table. We will collate multiple reports of the same study so that each study rather than each report is the unit of interest in the review. We will also provide any information we can obtain about ongoing studies. We will record the selection process in sufficient detail to complete a PRISMA flow diagram (Liberati 2009).

Data extraction and management

We will use the EPOC standard data collection form and adapt it for study characteristics and outcome data (EPOC 2017a); we will pilot the form on at least one study in the review. Two review authors (of BB, NH, NM) will independently extract the following characteristics from the included studies.

1. Methods: study design, unit of allocation, location and study setting, withdrawals.

2. Participants: number, mean age, age range, sex, inclusion criteria, exclusion criteria, other relevant characteristics.

3. Interventions: function of the intervention (monitoring, consultation, therapy), intervention components (including type of technology and mode of delivery, frequency of data transmission), comparison, fidelity assessment. For this review, we defined monitoring as the continuous evaluation of the progress of symptoms or a condition over a period of time; consultation as an exchange between the healthcare provider and the client, where the provider discusses the client's health status and provides guidance, support, or information; and therapy as the ongoing management and care of a client, to counteract a disease or disorder.

4. Outcomes: main outcomes specified and collected, time points reported.

5. Notes: funding for trial, ethical approval.

Two review authors (of BB, NH, NM) will independently extract outcome data from included studies. We will contact authors of included studies to seek missing data. We will note in the 'Characteristics of included studies' table if outcome data are reported in an unusable way. We will resolve disagreements by consensus or by involving a third review author (DGB or SS). We will group the studies by health condition being targeted. We will create a miscellaneous category for studies focusing on rare conditions and single studies of a condition, for which we will extract basic study information and descriptive data, but not outcome or risk of bias data.

Assessment of risk of bias in included studies

Two review authors (of BB, NH, NM) will independently assess risk of bias for each study using the criteria outlined in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2017), plus the guidance from the EPOC group (EPOC 2017b). We will resolve any disagreement by discussion or by involving a third review author (DGB or SS). We will assess the risk of bias according to the following domains.

1. Random sequence generation.

2. Allocation concealment.

3. Blinding of participants and personnel.

4. Blinding of outcome assessment.

5. Incomplete outcome data.

6. Selective outcome reporting.

7. Baseline outcomes measurement.

8. Baseline characteristics.

9. Other bias.

We will judge the risk of each potential source of bias as being high, low or unclear and provide a quotation from the study report together with a justification for our judgment in the 'Risk of bias' table. We will summarise the 'Risk of bias' judgments across different studies for each of the domains listed. We will consider blinding separately for different key outcomes where necessary (e.g. for unblinded outcome assessment, risk of bias for all‐cause mortality may be very different than for a patient‐reported pain scale). We will assess incomplete outcome data separately for different outcomes. Where information on risk of bias relates to unpublished data or correspondence with a trialist, we will note this in the 'Risk of bias' table. We will not exclude studies on the grounds of their risk of bias but will clearly report the risk of bias when presenting the results of the studies.

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

We will conduct the review according to this published protocol and report any deviations form it in the 'Differences between protocol and review' section of the systematic review.

Measures of treatment effect

We will estimate the effect of the intervention using risk ratios and associated 95% confidence intervals for dichotomous data, and standardised mean differences and 95% confidence intervals for continuous data (Higgins 2011). We will ensure that readers can interpret an increase in scores for continuous outcomes in the same way for each outcome, explain the direction of effect, and report where the directions were reversed if this were necessary.

Unit of analysis issues

We will control for unit of analysis errors by reanalysing results after adjusting for clustering. If there is not enough information to reanalyse the results, we will try to contact the study authors in order to obtain the necessary data. If we are not able to access all the data we will not report confidence intervals or P values (EPOC 2017c).

Dealing with missing data

We will contact investigators in order to verify key study characteristics and obtain missing outcome data where possible (e.g. when a study report is only available as an abstract). We will try to compute missing summary data from other reported statistics. Whenever it is not possible to obtain data, we will report the level of missingness and consider how that might impact the certainty of the evidence.

Assessment of heterogeneity

If we find a sufficient number of studies we will conduct a meta‐analysis. We will use the I² statistic to measure heterogeneity among the trials in each analysis. If we identify substantial heterogeneity, we will explore it by pre‐specified subgroup analysis.

Assessment of reporting biases

We will attempt to contact study authors, asking them to provide missing outcome data. Where this is not possible, and we consider that the missing data can introduce serious bias, we will explore the impact of including such studies in the overall assessment of results. If we are able to pool more than 10 trials, we will create and examine a funnel plot to explore possible publication biases, interpreting the results with caution (Sterne 2011).

Data synthesis

We will undertake meta‐analyses only where this is meaningful, that is, if the treatments, participants, and underlying clinical question are similar enough for pooling to make sense (Borenstein 2009). A common way that trialists indicate the presence of skewed data is by reporting medians and interquartile ranges. When we encounter this we will note that the data are skewed and consider the implications. Where a single trial reports multiple trial arms, we will include only the relevant arms. If two comparisons (e.g. intervention A versus usual care and intervention B versus usual care) must be entered into the same meta‐analysis, we will halve the control group to avoid double‐counting.

Subgroup analysis and investigation of heterogeneity

We plan to carry out the following subgroup analyses.

1. Healthcare provider type (e.g. lay versus professional healthcare provider). Lay health workers (LHW) often provide healthcare in settings where healthcare resources are scarcer, for example targeting epidemics in low‐ and middle‐income countries and the specific health needs of minority communities in high‐income countries (Lewin 2010). Because LHW have no formal professional tertiary education, their knowledge and beliefs might moderate the effects of the intervention (Akinlua 2016).

2. Type of communication channel (e.g. voice, SMS, interactive voice response, image exchange). Different communication channels might be used differently and serve distinct purposes (Ventola 2014), as well as providing a more comprehensive and realistic opportunity for communication.

3. Setting/income level (e.g. low‐income versus high‐income settings). Traditionally, the quality of healthcare is lower in low‐ and middle‐income countries (Mills 2014), which might increase heterogeneity and preempt the pooled analysis of studies conducted in different settings.

We will use the following outcomes in subgroup analysis.

1. Providers' adherence to recommended practice, guidelines or protocols (for example, providing the service at the recommended time, linkage to referrals as recommended).

2. Time between presentation and appropriate management.

3. Clients' health status and well‐being.

We will use the formal statistical techniques of Mantel‐Haenszel and regression to test for subgroup interactions (Mantel 1959).

Sensitivity analysis

We will perform sensitivity analyses defined a priori to assess the robustness of our conclusions and explore the impact on effect sizes. This will involve restricting the analysis to published studies and to studies at low risk of bias.