Metformin monotherapy for adults with type 2 diabetes mellitus

Abstract

This is a protocol for a Cochrane Review (Intervention). The objectives are as follows:

To assess the effects of metformin monotherapy in adults with type 2 diabetes mellitus.

Background

Description of the condition

According to the International Diabetes Federation (IDF), 382 million people worldwide had diabetes in 2013, and this number is expected to increase to 592 million by 2035 (Guariguata 2014). Type 2 diabetes mellitus (T2DM) is a condition characterised by insulin resistance and a relative deficiency of insulin secretion (Triplitt 2015). Long‐term complications of T2DM are microvascular (e.g. nephropathy, retinopathy, neuropathy) as well as macrovascular (e.g. ischaemic heart disease, stroke, and ischaemia of the lower extremities). Mortality is increased among individuals with T2DM compared to the non‐diabetic population. The main cause of the increased mortality is macrovascular disease (Almdal 2004; de Marco 1999; Stamler 1993).

Description of the intervention

People with T2DM are initially advised to follow behaviour‐changing ('lifestyle') interventions including weight loss and increased physical activity (ADA/EASD 2015). However, over time the majority of people with T2DM will require additional glucose‐lowering pharmacological interventions. Currently, metformin is the recommended first‐line, glucose‐lowering medication (ADA/EASD 2009). The pivotal trial underlying the recommendation of metformin as the first‐line, glucose‐lowering drug of choice was the UK Prospective Diabetes Study (UKPDS), which compared metformin as monotherapy with chlorpropamide, glyburide and insulin in a subgroup of overweight participants (n = 342 out of a total number of included participants of 4075) (UKPDS 1998). Intensive glycaemic control with metformin decreased the risk of diabetes‐related outcomes compared with other glucose‐lowering agents. Metformin is a biguanide originating from the plant Galega officinalis (Witters 2001). First described in 1922, it was administered to humans for the first time in France in 1957. In 1972, Canada approved its use for T2DM and later, in 1994, it received approval for use in T2DM by the US Food and Drug Administration (FDA) (Corey 2007).

Previously we reviewed the effects of metformin plus insulin versus insulin alone for T2DM (Hemmingsen 2012). We found no firm evidence for improved all‐cause mortality or cardiovascular mortality following combined metformin and insulin treatment compared with insulin alone. Interpretation was limited by lack of data for patient‐relevant outcomes and by poor bias control in included trials (Hemmingsen 2012).

Adverse effects of metformin

The most common adverse effects of metformin are gastrointestinal disturbances, which are reported in 20% to 30% of people using this drug. However, the gastrointestinal disturbances only necessitate discontinuation of the drug in less than 5% of the affected individuals (DeFronzo 1999).

A potential complication of metformin use is lactic acidosis, a rare, but potentially fatal, metabolic condition that can occur whenever substantial tissue hypoxia exists (Kreisberg 1980). Lactic acidosis is characterised by elevated blood lactate concentrations (exceeding 5.0 mmol/L) and decreased blood pH (less than 7.35). The mortality is estimated to be about 50% (Huang 2016). A Cochrane Review found no firm evidence of metformin being associated with an increased risk of lactic acidosis or elevated lactate levels when compared to other glucose‐lowering drugs (Salpeter 2010). However, several case reports of lactic acidosis in metformin‐treated people have been published subsequently (Kalantar‐Zadeh 2013; Schousboe 2012).

How the intervention might work

The exact mechanism(s) of action of metformin are not clearly elucidated. However, metformin is known to alter carbohydrate metabolism by reducing basal hepatic glucose production (gluconeogenesis), improving insulin sensitivity in the liver and peripheral tissues, as well as increasing insulin‐stimulated glucose uptake and utilisation in peripheral tissues (AHFS 1999). It has been proposed that its prime mode of action is via activation of the 5' adenosine monophosphate‐activated protein kinase (AMPK) enzyme (Cho 2015; Duca 2015).

Why it is important to do this review

A recently published systematic review on sulphonylurea monotherapy versus metformin monotherapy in people with T2DM did not show superiority of metformin monotherapy (Hemmingsen 2014). However, no updated review on metformin monotherapy compared with other glucose‐lowering interventions in people with T2DM exists. In 2005 a Cochrane Review about metformin monotherapy was published (Saenz 2005). However, this systematic review is more than 10 years old and was consequently withdrawn. Therefore, a new systematic review with updated searches and newer methodology is warranted.

Objectives

To assess the effects of metformin monotherapy in adults with type 2 diabetes mellitus.

Methods

Criteria for considering studies for this review

Types of studies

We will include only randomised clinical trials (RCTs). By excluding quasi‐randomised trials and observational studies, especially to assess harms, we are aware that our present review may not give a full evaluation of the balance between benefits and harms.

Types of participants

Adults (18 years or more) with type 2 diabetes mellitus (T2DM). We will include participants regardless of the presence of comorbidities.

Diagnostic criteria for 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, the diagnostic criteria should have been described. We will use the trial authors' definition of diabetes mellitus if necessary. We plan to subject diagnostic criteria to a sensitivity analysis.

Types of interventions

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

Intervention

Metformin monotherapy

Comparator

• Placebo

• No intervention

• Diet

• Other glucose‐lowering drugs or combinations of glucose‐lowering drugs

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

If a trial includes multiple arms, we will include any arm that meets the review inclusion criteria.

Minimum duration of intervention and follow‐up

We will only include trials with at least one year's duration, irrespective of the post‐intervention follow‐up. The reason is that we are primarily interested in patient‐important clinical outcomes and not in short‐term biochemical responses.

We will define extended follow‐up periods (also called open‐label extension studies) as follow‐up of participants 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 report these studies in a separate table (Buch 2011; Megan 2012).

Summary of specific exclusion criteria

• Intervention period less than one year

Types of outcome measures

We will not exclude a trial if they fail to report one or several of our primary or secondary outcome measures. If none of our primary or secondary outcomes is reported in the trial, we will not include the trial but provide some basic information in an additional table.

We will investigate the following outcomes using the methods and time points specified below.

Primary outcomes

• All‐cause mortality

• Serious adverse events

• Health‐related quality of life

Secondary outcomes

• Cardiovascular mortality

• Non‐fatal myocardial infarction

• Non‐fatal stroke

• End‐stage renal disease

• Blindness

• Severe hypoglycaemia

Explorative outcomes

• Anthropometric measures

• Glycaemic control

• Amputation of lower extremity

• Congestive heart failure

• Cardiac revascularisation.

• Peripheral revascularisation

• Socioeconomic effects

Method of outcome measurement

• All‐cause mortality: defined as death from any cause

• Serious adverse events: defined according to the International Conference on Harmonization Guidelines as, "any event that leads to death, that is life‐threatening, required in‐patient hospitalisation or prolongation of existing hospitalisation, resulted in persistent or significant disability, and any important medical event which may have had jeopardised the patient or required intervention to prevent it" (ICH 1997) or as reported in trials.

• Health‐related quality of life: defined as mental and physical quality of life and evaluated by a validated instrument such as Short‐Form 36.

• Cardiovascular mortality, non‐fatal myocardial infarction, non‐fatal stroke, blindness: defined as reported in trials.

• End‐stage renal disease: defined as dialysis, renal transplantation: defined as reported in trials.

• Severe hypoglycaemia: requiring assistance from another person.

• Anthropometric measures: defined as weight in kg or body mass index (BMI).

• Glycaemic control: defined as glycosylated haemoglobin A1c (HbA1c) or fasting plasma glucose (FPG).

• Lactic acidosis: defined as reported in trials.

• Amputation of lower extremity: defined as reported in trials.

• Congestive heart failure: defined as reported in trials.

• Cardiac revascularisation: defined as reported in trials.

• Peripheral revascularisation: defined as reported in trials.

• Socioeconomic effects: such as direct costs defined as admission/readmission rates, average length of stay, visits to general practitioner, accident/emergency visits; medication consumption; indirect costs defined as resources lost due to illness by the participant or their family member.

Timing of outcome measurement

• At the end of the intervention period: health‐related quality of life, anthropometric measures, glycaemic control

• Any time after participants were randomised to intervention/comparator groups: all other outcomes.

Search methods for identification of studies

Electronic searches

Recently, the Agency for Healthcare Research and Quality (AHRQ) published a systematic review and meta‐analysis (Maruthur 2016) based on an extensive AHRQ report (Bolen 2016), in which the authors evaluated the comparative effectiveness and safety of glucose‐lowering interventions for people with T2DM, including metformin therapy. This report included search results from several databases up to April 2015 and a further update of the MEDLINE search up to December 2015.

We will base our search on the results of this systematic AHRQ report and add new references identified by a revised search strategy from 2014 onwards, in the following literature databases. We will place no restrictions on the language of publication.

• 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.

Additionally we will search the following trials registers and place no restrictions on the date of the record.

• 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 established by Cochrane Metabolic and Endocrine Disorders (CMED) to identify newly published trials using the same search strategy as described for MEDLINE (Appendix 1). After we submit the final review draft for editorial approval, CMED will perform a complete search update on all databases available at the editorial office and will send the results to the review authors. Should we identify new trials for inclusion, we will evaluate these, incorporate the findings into our review and resubmit another Cochrane 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 of metformin monotherapy and health technology assessment reports. In addition we will contact authors of included trials to identify any additional information on the retrieved trials and to determine if further trials exist, which we may have missed.

We will also search databases from regulatory agencies (European Medicines Agency (EMA), US Food and Drugs Administration (FDA)) (Hart 2012; Schroll 2015).

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

Data collection and analysis

Selection of studies

Two review authors (FG and LK or AT) will independently scan 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 (AT). If we cannot resolve a disagreement, we will categorise the trial as a 'study awaiting classification' and 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 inclusion criteria, two review authors (FG and LK or AT) will independently extract key participant and intervention characteristics. We will describe interventions according to 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 CMED data extraction sheets. We will resolve any disagreements by discussion or, if required, by consultation with a third review author (AT).

We will provide information about potentially relevant ongoing trials, including the trial identifier 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 we will report primary, secondary and other outcomes in comparison with data in publications 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 trials registry information) as secondary references under the study 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 trials registers

If data from included trials are available as study results in clinical trials 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 trials 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

Three review authors (FG and LK or AT) will independently assess the risk of bias of each included trial. We will resolve any disagreements by consensus, or by consultation with a fourth review author (BH). In cases of disagreement, we will consult the remainder of the review author team and make a judgment based on consensus. If adequate information is unavailable from the publications, trial protocols or other sources, we will contact the trial authors for more detail to request missing data on 'Risk of bias' items.

We will use the Cochrane 'Risk of bias' assessment tool (Higgins 2017; Higgins 2011a), assigning assessments of low, high or unclear risk of bias. 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 2011a).

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 allow an 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 judgment 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) ‐ assessment at trial level

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, web‐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: used an open, random allocation schedule (e.g. a list of random numbers); assignment envelopes 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' judgment for selection bias (Corbett 2014). Chance imbalances may also affect judgments on the risk of attrition bias. In the case of unadjusted analyses, we will distinguish between trials that we rate as being at low risk of bias on the basis of both randomisation methods and baseline similarity, and trials that we judge as being at low risk of bias on the basis of baseline similarity alone (Corbett 2014). We will reclassify 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 was ensured, and it was 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 was 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 was likely to be influenced by lack of blinding.

Incomplete outcome data (attrition bias due to amount, nature or handling of incomplete outcome data)

For each included trial and/or each outcome, we will describe the completeness of data, including attrition and exclusions from the analyses. We will state whether the trial reported attrition and exclusions, and report the number of participants included in the analysis at each stage (compared with the number of randomised participants per intervention/comparator groups). We will also note if the trial reported the reasons for attrition or exclusion and whether missing data were balanced across groups or were related to outcomes. We will consider the implications of missing outcome data per outcome such as high dropout rates (e.g. above 15%) or disparate attrition rates (e.g. difference of 10% or more between trial arms).

• Low risk of bias: no missing outcome data; reasons for missing outcome data unlikely to be related to true outcome (for survival data, censoring unlikely to introduce bias); missing outcome data balanced in numbers across intervention groups, with similar reasons for missing data across groups; for dichotomous outcome data, the proportion of missing outcomes compared with observed event risk was not enough to have a clinically relevant impact on the intervention effect estimate; for continuous outcome data, plausible effect size (mean difference or standardised mean difference) among missing outcomes was not enough to have a clinically relevant impact on observed effect size; appropriate methods, such as multiple imputation, were used to handle missing data.

• Unclear risk of bias: insufficient information to assess whether missing data in combination with the method used to handle missing data were likely to induce bias; the trial did not address this outcome.

• High risk of bias: reason for missing outcome data was likely to be related to true outcome, with either imbalance in numbers or reasons for missing data across intervention groups; for dichotomous outcome data, the proportion of missing outcomes compared with observed event risk enough to induce clinically relevant bias in the intervention effect estimate; for continuous outcome data, plausible effect size (mean difference or standardised mean difference) among missing outcomes enough to induce clinically‐relevant bias in observed effect size; 'as‐treated' or similar analysis done with substantial departure of the intervention received from that assigned at randomisation; potentially inappropriate application of simple imputation.

Selective reporting (reporting bias due to selective outcome reporting)

We will assess outcome reporting bias by integrating the results of the appendix 'Matrix of trial endpoints (publications and trial documents)' (Boutron 2014; Jones 2015; Mathieu 2009), with those of the appendix 'High risk of outcome reporting bias according to the Outcome Reporting Bias In Trials (ORBIT) classification' (Kirkham 2010). This analysis will form the basis for the judgement of selective reporting.

• Low risk of bias: the trial protocol was available and all the trial's prespecified (primary and secondary) outcomes that were of interest to this review were reported in the prespecified way; the study protocol was unavailable, but it was clear that the published reports included all expected outcomes (ORBIT classification).

• Unclear risk of bias: insufficient information about selective reporting.

• High risk of bias: not all the trial's prespecified primary outcomes were reported; one or more primary outcomes were reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not prespecified; one or more reported primary outcomes were not prespecified (unless clear justification for their reporting was provided, such as an unexpected adverse effect); one or more outcomes of interest in the Cochrane Review were reported incompletely so that we cannot enter them in a meta‐analysis; the trial report failed to include results for a key outcome that we would expect to have been reported for such a trial (ORBIT classification).

Other bias

• Low risk of bias: the trial appears to be free from other sources of bias.

• Unclear risk of bias: there was insufficient information to assess whether an important risk of bias existed; insufficient rationale or evidence that an identified problem introduced bias.

• High risk of bias: the trial had a potential source of bias related to the specific trial design used; the trial was claimed to be fraudulent; or the trial had some other serious problem.

Summary assessment of risk of bias

We will present a 'Risk of bias' graph and a 'Risk of bias' summary figure.

We will distinguish between self‐reported and investigator‐assessed and adjudicated outcome measures.

We will consider the following to be self‐reported outcomes.

• Health‐related quality of life

• Severe hypoglycaemia, as reported by participants

• Anthropometric measures, as reported by participants

• Glycaemic control, as reported by participants

We will consider the following outcomes to be investigator‐assessed.

• All‐cause mortality

• Serious adverse events

• Cardiovascular mortality

• Non‐fatal myocardial infarction

• Non‐fatal stroke

• End‐stage renal disease

• Blindness

• Amputation of lower extremity

• Cardiac revascularisation

• Peripheral revascularisation

• Severe hypoglycaemia

• Anthropometric measures

• Glycaemic control

• Lactic acidosis

• Amputation of lower extremity

• Congestive heart failure

• Cardiac revascularisation

• Peripheral revascularisation

• Socioeconomic effects

Risk of bias for a trial across outcomes

Some 'Risk of bias' domains, such as selection bias (sequence generation and allocation sequence concealment), affect the risk of bias across all outcome measures in a trial. In case of high risk of selection bias, we will mark all endpoints investigated in the associated trial as being at high risk. Otherwise, we will not perform a summary assessment of the risk of bias across all outcomes for a trial.

Risk of bias for an outcome within a trial and across domains

We will assess the risk of bias for an outcome measure by including all entries relevant to that outcome (i.e. both trial‐level entries and outcome‐specific entries). We consider low risk of bias to denote a low risk of bias for all key domains, unclear risk to denote an unclear risk of bias for one or more key domains and high risk to denote a high risk of bias for one or more key domains.

Risk of bias for an outcome across trials and across domains

These are the main summary assessments that we will incorporate into our judgments about the quality of evidence in the 'Summary of findings' tables. We will define outcomes as at low risk of bias when most information comes from trials at low risk of bias, unclear risk when most information comes from trials at low or unclear risk of bias and high risk when a sufficient proportion of information comes from trials at high risk of bias.

Measures of treatment effect

When at least two trials are available for a comparison and a given outcome we will express dichotomous data as a risk ratio (RR) or odds ratio (OR) with 95% confidence interval (CI) and with Trial Sequential Analysis (TSA)‐adjusted CI if the diversity‐adjusted required information size is not reached. For continuous outcomes measured on the same scale (e.g. HbA1c) we will estimate the intervention effect using the mean difference (MD) with 95% CI. For continuous outcomes measuring the same underlying concept (e.g. health‐related quality of life) but using different measurement scales, we will calculate the standardised mean difference (SMD) but will not use TSA. The scales measuring health‐related quality of life may go in different directions. In some scales, values increase with improved health‐related quality of life, whereas in other scales, values decrease with improved health‐related quality of life. To adjust for the different directions of the scales, we will multiply scales that report better health‐related quality of life using decreasing values by –1. We intend to re‐express the SMDs into the unit of the Short Form‐36 (SF‐36) questionnaire. This will be done by using standard deviations from a clinical trial in participants with T2DM providing data for a pooled standard deviation for baseline and change from baseline. The pooled effect of SMDs will then be re‐expressed as units of the Short Form‐36. On these data, we will conduct TSA.

We will express time‐to‐event data as hazard ratio (HR) with 95% CI. We will calculate HRs with the generic inverse variance method with 95% CI.

We will adjust thresholds for statistical significance for the primary outcomes in order to decrease the risk of type I errors (Jakobsen 2014). Different methods are available for adjusting for multiple primary outcomes, which are correlated. However, the degree of correlation is unknown. We have chosen the family‐wise error rate (FWER) adjustment in order not to declare that the intervention has an effect on one or more of the primary outcomes when this is in fact due to an increased risk of random error because of multiple co‐primary outcomes. As the co‐primary outcomes are correlated, a strict Bonferroni adjustment would be too conservative and no adjustment too relaxed. We therefore intend to adjust the significance level with an adjustment factor in between the Bonferroni adjustment factor of 1/3 and a no‐adjustment factor of 1, which is a factor of 1/2. As we have three primary outcomes, it means that the threshold for statistical significance will be 0.025 instead of the conventional threshold for statistical significance of 0.05 (Jakobsen 2016).

For the secondary outcomes we will apply an α = 0.05 / ((1+6)/2) = 0.014.

We will not perform FWER and TSA on explorative outcomes.

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 data to the meta‐analysis 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 2011b).

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 intracluster correlation coefficient (ICC). We will obtain estimates of ICCs through contact with authors or impute them by using either estimates from other included trials that report ICCs or 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 of the outcome is not available at follow‐up or cannot be recreated, we will standardise by the average of the pooled baseline standard deviation from those trials in which this information was reported.

Where included trials do not report means and standard deviations (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 per outcome which trials were included with imputed SDs.

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 (Deeks 2017). In view of the low power of this test, we will also consider the I² statistic (Higgins 2003), which quantifies inconsistency across trials to assess the impact of heterogeneity on the meta‐analysis (Higgins 2002)).

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 investigating 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 of different methodological quality, 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; Higgins 2009). 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 such as event rates below 1%, we will use the 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 perform statistical analyses according to the statistical guidelines presented in the Cochrane Handbook for Systematic Reviews of Interventions (Deeks 2017).

Trial Sequential Analysis

In a single trial, interim analysis increases the risk of type I and type II errors. To avoid type I errors, group sequential monitoring boundaries are applied to decide whether a trial could be terminated early because of a sufficiently small P value, that is, the cumulative Z‐curve crosses the monitoring boundaries. Likewise, before reaching the planned sample size, the trial may be stopped due to futility if the cumulative Z‐score crosses the futility monitoring boundaries (Lan 1983). Sequential monitoring boundaries for benefit, harm, or futility can be applied to meta‐analysis as well, called trial sequential monitoring boundaries (Higgins 2010; Wetterslev 2008). In Trial Sequential Analyses (TSA), the addition of each trial in a cumulative meta‐analysis is regarded as an interim meta‐analysis and helps to clarify if significance is reached or futility is reached or whether additional trials are needed (Higgins 2017; Wetterslev 2008). TSA combines a calculation of the diversity‐adjusted required information size (cumulated meta‐analysis sample size to detect or reject a specific relative intervention effect) for meta‐analysis, using the model‐based variance, with the threshold of statistical significance (Brok 2009; Pogue 1997; Thorlund 2009; Wetterslev 2008; Wetterslev 2012).

The idea in TSA is that if the cumulative Z‐curve crosses the boundary, a sufficient level of evidence for the anticipated intervention effect has been reached and no further trials may be needed. If the Z‐curve does not cross the boundary, then there is insufficient evidence to reach a conclusion. To construct the trial sequential monitoring boundaries, the required information size is needed and is calculated as the least number of participants needed and the corresponding number of required trials (Kulinskaya 2014), in a well‐powered single trial, and subsequently adjusted for diversity among the included trials in the meta‐analysis (Pogue 1997; Wetterslev 2008; Wetterslev 2009). We will apply TSA since it decreases the risk of type I and 2 errors due to sparse data and potential multiple updating in a cumulative meta‐analysis (Imberger 2015; Imberger 2016; Wetterslev 2017), and it provides us with important information in order to estimate the level of evidence of the experimental intervention. Additionally, TSA will provide important information regarding the need for additional trials and possibly the required information size. We will apply trial sequential monitoring boundaries according to an information size based on an a priori effect Kulinskaya 2016) corresponding to a numbers needed to treat (NNTB) or harm (NNTH) for an additional beneficial outcome of 50 to 100 patients. This includes a 10% relative risk reduction (RRR) for benefit and a 30% relative risk increase for harm using (e.g. serious adverse events) an overall FWER of 5% (α = 0.05, for the co‐primary outcomes this corresponds to an α = 0.025 and for the secondary outcomes an α = 0.01) and a type II error level of 10% (ß = 0.10 with power = 90%). We will perform TSA for health‐related quality of life with MD, by using the trials applying the same scale to calculate the required sample size. We will use the control event proportion estimated from the control groups of the included trials. For the required information size we will use the model variance‐based approach (corresponding to the diversity (D²) adjustment, based on a D² calculated from the included trials in the meta‐analysis, because the I² statistic underestimates heterogeneity among trials in a meta‐analysis regarding the required information size (Wetterslev 2009; Wetterslev 2017). Diversity is an estimate of heterogeneity of the trials included in the meta‐analysis, and represents the relative variance reduction when the meta‐analysis model is changed from a random‐effects to a fixed‐effect model (Wetterslev 2009; Wetterslev 2017). If the actual measured diversity in the meta‐analysis is zero we will perform TSA with a diversity of 20%, as heterogeneity may likely increase when further trials are included in the cumulative meta‐analysis.

Subgroup analysis and investigation of heterogeneity

We expect the following characteristics to introduce clinical heterogeneity, and plan to carry out the following subgroup analyses with investigation of interactions.

• Comparing trials of long duration (two years or longer) to trials of short duration (less than two years).

• Comparing trials including exclusively obese participants (defined as BMI equal to or greater than 30) to trials including obese and non‐obese participants.

• Comparing trials at low risk of bias to trials at high risk of bias.

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

• Very long or large trials to establish the extent to which they dominate the results.

• Trials using the following filters: diagnostic criteria, 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).

Quality of evidence

We will present the overall quality of the evidence for each outcome specified under 'Types of outcome measures: Summary of findings' according to the GRADE approach (Guyatt 2008). The GRADE approach appraises the quality of a body of evidence based on the extent to which one can be confident that an estimate of effect or association reflects the item being assessed. The quality measure of a body of evidence considers within‐study risk of bias, the directness of the evidence, heterogeneity of the data, precision of effect estimates (Jakobsen 2014), and risk of publication bias. Two review authors (FG and LK or AT) will independently rate the quality of evidence for each outcome.

Summary of findings table

We will present a summary of the evidence in a 'Summary of findings' table according to the GRADE approach (Guyatt 2008). We will include an appendix entitled 'Checklist to aid consistency and reproducibility of GRADE assessments', to help with standardisation of the 'Summary of findings' tables (Meader 2014). Alternatively, we will use the GRADEpro Guideline Development Tool (GDT) software and will present evidence profile tables as an appendix (GRADEproGDT 2015). We will present results for the outcomes as described in the Types of outcome measures section. If meta‐analysis is not possible, we will present the results in a narrative format in the 'Summary of findings' table. We will justify all decisions to downgrade the quality of trials using footnotes and we will make comments to aid the reader's understanding of the Cochrane Review where necessary.

Our primary 'Summary of findings' tables and conclusions will be based on the results of trials with a low risk of bias in all risk of bias domains (Gluud 2006; Gluud 2008; Lundh 2017; Moher 1998; Savovic 2012; Schulz 1995; Wood 2008). We will report the following outcomes, listed according to priority.

• All‐cause mortality

• Serious adverse events

• Health‐related quality of life

• Cardiovascular mortality

• Non‐fatal myocardial infarction

• Non‐fatal stroke

• End‐stage renal disease

Appendices

Appendix 1. Search strategies

MEDLINE (OvidSP)

1. exp Diabetes Mellitus, Type 2/ 2. (MODY or NIDDM or T2D*).tw. 3. (non insulin* depend* or noninsulin* depend* or noninsulin?depend* or non insulin?depend*).tw. 4. ((typ? 2 or typ? II or typ?2 or typ?II) adj3 diabet*).tw. 5. (((late or adult* or matur* or slow or stabl*) adj3 onset) and diabet*).tw. 6. or/1‐5 7. Metformin/ 8. metformin*.tw. 9. or/7‐8 10. 6 and 9 [11‐22: Cochrane Handbook 2008 RCT filter ‐ sensitivity maximizing version] 11. randomized controlled trial.pt. 12. controlled clinical trial.pt. 13. randomi?ed.ab. 14. placebo.ab. 15. drug therapy.fs 16. randomly.ab. 17. trial.ab. 18. groups.ab. 19. or/11‐18 20. exp animals/ not humans/ 21. 19 not 20 22. 10 and 21 [23: Wong 2006a – systematic reviews filter – SensSpec version] 23. meta analysis.mp,pt. or review.pt. or search*.tw. 24. 10 and 23 25. 22 or 24 26. (2014* or 2015* or 2016* or 2017*).dc. 27. 25 and 26 28. ..dedup 27

Cochrane Central Register of Controlled Trials (CENTRAL) (Cochrane Register of Studies Online)

1. MESH DESCRIPTOR Diabetes Mellitus, Type 2 EXPLODE ALL TREES 2. (MODY OR NIDDM OR T2D*):TI,AB,KY 3. (non insulin* depend* OR noninsulin* depend* OR noninsulin?depend* OR non insulin?depend*):TI,AB,KY 4. ((typ? 2 OR typ? II OR typ?2 OR typ?II) ADJ3 diabet*):TI,AB,KY 5. (((late OR adult* OR matur* OR slow OR stabl*) ADJ3 onset) AND diabet*):TI,AB,KY 6. #1 OR #2 OR #3 OR #4 OR #5 7. MESH DESCRIPTOR Metformin 8. metformin*:TI,AB,KY 9. #7 OR #8 10. #6 AND #9 11. 2014 TO 2017:YR 12. #10 AND #11

Embase (Ovid SP)

1. non insulin dependent diabetes mellitus/ 2. (MODY or NIDDM or T2D*).tw. 3. (non insulin* depend* or noninsulin* depend* or noninsulin?depend* or non insulin?depend*).tw. 4. ((typ? 2 or typ? II or typ?2 or typ?II) adj3 diabet*).tw. 5. (((late or adult* or matur* or slow or stabl*) adj3 onset) and diabet*).tw. 6. or/1‐5 7. Metformin/ 8. metformin*.tw. 9. or/7‐8 10. 6 and 9 [11: Wong 2006b "sound treatment studies" filter – best balance version] 11. random*.tw. or placebo*.mp. or double‐blind*.tw. 12. 10 and 11 13. (2014* or 2015* or 2016* or 2017*).dc. 14. 12 and 13 15. conference*.pt. 16. 14 not 15 17. ..dedup 16

ClinicalTrials.gov (Advanced search)

Conditions: diabetes OR diabetic OR diabetics OR "type 2" OR "type II" OR T2D OR T2DM OR NIDDM Interventions: metformin Study Type: Interventional Studies Age Group: Adult, Senior

WHO International Clinical Trials Registry Platform (ICTRP) Search Portal (Standard search)

diabet* AND metformin* OR T2D* AND metformin* OR NIDDM AND metformin*

Appendix 2. Selection bias decisions

Selection bias decisions for trials that reported unadjusted analyses: comparison of results obtained using method details alone with results using method details and trial baseline informationa
Reported randomisation and allocation concealment methods	Risk of bias judgement using methods reporting	Information gained from study characteristics data	Ris of bias using baseline information and methods reporting
Unclear methods	Unclear risk	Baseline imbalances present for important prognostic variable(s)	High risk
		Groups appear similar at baseline for all important prognostic variables	Low risk
		Limited or no baseline details	Unclear risk
Would generate a truly random sample, with robust allocation concealment	Low risk	Baseline imbalances present for important prognostic variable(s)	Unclear riskb
		Groups appear similar at baseline for all important prognostic variables	Low risk
		Limited baseline details, showing balance in some important prognostic variablesc	Low risk
		No baseline details	Unclear risk
Sequence is not truly randomised, or allocation concealment is inadequate	High risk	Baseline imbalances present for important prognostic variable(s)	High risk
		Groups appear similar at baseline for all important prognostic variables	Low risk
		Limited baseline details, showing balance in some important prognostic variablesc	Unclear risk
		No baseline details	High risk
aTaken from Corbett 2014; judgements highlighted in bold indicate situations in which the addition of baseline assessments would change the judgement about risk of selection bias, compared with using methods reporting alone. bImbalance identified that appears likely to be due to chance. cDetails for the remaining important prognostic variables are not reported.

Contributions of authors

All protocol authors read and approved the final protocol draft.

Declarations of interest

Filip Gnesin (FG): none known.

Lise Katrine Kähler (LK): none known.

Anne Cathrine Thuesen (AT): has previously been employed by a subsidiary company of Novo Nordisk.

Sten Madsbad (SM): Advisory Boards: Novartis Pharma, Novo Nordisk, Merck Sharp & Dome, Sanofi‐Aventis, AstraZeneca, Johnson & Johnson, Astra‐Zeneca, Boehringer‐Ingelheim, E. Lilly, Intarcia Therapeutics, Bristol‐Meyer Squibb. Fee for lectures: Novo Nordisk, Merck, Sharp & Dome, Astra‐Zeneca, Sanofi‐Aventis, Novartis Pharma, E. Lilly, Bristol‐Meyer Squibb, Boeringer‐Ingelheim, E.Lilly. Grants for research: Novo Nordisk.

Christian Gluud (CG): investigator in the Copenhagen Insulin and Metformin Therapy (CIMT) trial (not a metformin monotherapy trial).

Bianca Hemmingsen (BH): investigator in the Copenhagen Insulin and Metformin Therapy (CIMT) trial (not a metformin monotherapy trial).

Notes

We have based parts of the Methods, as well as Appendix 1 and Appendix 2 of this Cochrane protocol on a standard template established by Cochrane Metabolic and Endocrine Disorders.

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