Diagnostic criteria for people at risk of developing T2DM

To be consistent with changes to the classification of, and diagnostic criteria for dysglycaemia (impaired fasting glucose (IFG), impaired glucose tolerance (IGT) or elevated glycosylated haemoglobin A1c (HbA1c)) that have occurred over the years, a diagnosis should have been established using the standard criteria valid at the trial start (e.g. ADA 1997; ADA 2010; NDDG 1979; or WHO 1999). Ideally, the diagnostic criteria used in each study should have been described. We used the trial authors' definition of risk, but we contacted trial authors for additional information, if necessary. As differences in the glycaemic measurements used to define risk may introduce substantial heterogeneity, we planned to subject the diagnostic criteria used to subgroup analysis.

Intervention

(a) Second‐ or third‐generation sulphonylureas as monotherapy.

(b) Second‐ or third‐generation sulphonylureas as a part of combination therapy.

(c) Meglitinide analogues as monotherapy.

(d) Meglitinide analogues as a part of combination therapy.

Comparator

• Any pharmacological glucose‐lowering intervention (e.g. acarbose, metformin, sodium–glucose cotransporter 2 inhibitors) compared with (a) or (c).

• Any pharmacological glucose‐lowering agent (e.g. acarbose, metformin, sodium–glucose cotransporter 2 inhibitors) compared with (b) or (d) if this glucose‐lowering agent was the same in both the intervention and comparator groups (e.g. meglitinide analogue + metformin versus metformin).

• Behaviour‐changing interventions (e.g. diet, exercise, diet and exercise) compared with (a) or (c).

• Placebo compared with (a) or (c).

• No intervention compared with (a) or (c).

Other concomitant interventions (e.g. educational programmes or additional pharmacotherapy) had to be the same in both the intervention and comparator groups in order to establish a fair comparison.

Minimum duration of intervention

We included trials that investigated the intervention for a duration of 12 weeks or more.

Specific exclusion criteria

• We excluded trials in people diagnosed with the 'metabolic syndrome' as this is a special population which is not representative of people with only intermediate hyperglycaemia. Also, the composite of risk indicators, such as elevated blood lipids, insulin resistance, obesity and high blood pressure, which is termed metabolic syndrome, is of doubtful clinical usefulness and uncertain distinct disease entity. However, if we identified trials investigating participants with any definition of the metabolic syndrome, we intended to summarise some basic trial information in an additional table.

• We excluded trials evaluating participants with intermediate hyperglycaemia in combination with another condition (e.g. cystic fibrosis).

• We excluded trials evaluating participants with intermediate hyperglycaemia due to other medical interventions (e.g. glucocorticoids).

Primary outcomes

• All‐cause mortality

• Incidence of T2DM

• Serious adverse events

Secondary outcomes

• Cardiovascular mortality

• Non‐fatal myocardial infarction

• Non‐fatal stroke

• Congestive heart failure

• Amputation of lower extremity

• Blindness or severe vision loss

• End‐stage renal disease

• Non‐serious adverse events

• Hypoglycaemia

• Health‐related quality of life

• Time to progression to T2DM

• Measures of blood glucose control

• Socioeconomic effects

Dealing with duplicate and companion publications

In the event of duplicate publications, companion documents or multiple reports of a primary trial, we maximised the information by collating all available data and used the most complete data set aggregated across all known publications. We list duplicate publications, companion documents or multiple reports of a primary trial as secondary references under the primary reference of the included or excluded trial.

Random sequence generation (selection bias due to inadequate generation of a randomised sequence) ‐ assessment at trial level

We assessed for each included trial whether the method used to generate the allocation sequence was described in sufficient detail to allow an assessment of whether it should produce comparable groups.

• Low risk of bias: sequence generation was achieved using computer random number generation or a random number table. Drawing of lots, tossing a coin, shuffling cards or envelopes and throwing dice were adequate if performed by an independent person not otherwise involved in the trial. Use of the minimisation technique was considered 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 (e.g. sequence generated by: odd or even date of birth, some rule based on date (or day) of admission, 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; allocation by availability of the intervention). We excluded such trials from our review.

Allocation concealment (selection bias due to inadequate concealment of allocations prior to assignment) ‐ assessment at trial level

We described for each included trial the method used to conceal allocation to interventions prior to assignment, and assessed 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: use of: an open random allocation schedule (e.g. a list of random numbers); assignment envelopes without appropriate safeguards; alternation or rotation; date of birth; case record number; any other explicitly unconcealed procedure. We excluded such trials from our review.

We also evaluated trial baseline data so as to incorporate an assessment of baseline imbalance into the 'Risk of bias' judgement for selection bias (Corbett 2014; Egbewale 2014; Riley 2013). Chance imbalances might also affect judgements on the risk of attrition bias. In case of unadjusted analyses we distinguished between trials rated as at low risk of bias on the basis of both randomisation methods and baseline similarity, and trials rated as at low risk of bias on the basis of baseline similarity alone (Corbett 2014). We reclassified judgements of unclear, low or high risk of selection bias as specified in Appendix 15.

Blinding of participants and study personnel (performance bias due to knowledge of the allocated interventions by participants and personnel during the trial) ‐ assessment at outcome level

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

• Low risk of bias: blinding of participants and key study personnel ensured, and unlikely that the blinding could have been broken; no blinding or incomplete blinding, but the review authors judged that the outcome was not likely to be influenced by lack of blinding.

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

• High risk of bias: no blinding or incomplete blinding, and the outcome was likely to be 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 was likely to be influenced by lack of blinding.

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

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

• Low risk of bias: blinding of outcome assessment ensured, and unlikely that the blinding could have been broken; no blinding of outcome assessment, but the review authors judged that the outcome measurement was not likely to be 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 be 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) ‐ assessment at outcome level

We described for each included trial and for each outcome the completeness of data, including attrition and exclusions from the analysis. We stated whether attrition and exclusions were reported and the numbers included in the analysis at each stage (compared with the numbers of randomised participants per intervention/comparator groups), if reasons for attrition or exclusion were reported, and whether missing data were balanced across groups or were related to outcomes. We considered 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 be introducing 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 not sufficient to have a clinically relevant impact on the intervention effect estimate; for continuous outcome data, plausible effect size (difference in means or standardised difference in means) among missing outcomes not sufficient to have a clinically relevant impact on observed effect size; appropriate methods, such as multiple imputation, 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 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 sufficient to induce clinically relevant bias in intervention effect estimate; for continuous outcome data, plausible effect size (difference in means or standardised difference in means) among missing outcomes sufficient to induce clinically relevant bias in observed effect size; ‘as‐treated’ or similar analysis carried out 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) ‐ assessment at trial level

We assessed outcome reporting bias by integrating Appendix 7 (Matrix of trial endpoints (publications and trial documents) (Boutron 2014; Mathieu 2009) with Appendix 8 (High risk of outcome reporting bias according to ORBIT [Outcome Reporting Bias In Trials]) classification) (Kirkham 2010). This analysis formed the basis for the judgement of selective reporting.

• Low risk of bias: the trial protocol was available and all of the trial’s prespecified (primary and secondary) outcomes that were of interest in the review have been reported in the prespecified way; the study protocol was not available 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 of the trial’s prespecified primary outcomes were reported; one or more primary outcomes was reported using measurements, analysis methods or subsets of the data (e.g. subscales) that were not prespecified; one or more reported primary outcome was not prespecified (unless clear justification for its reporting was provided, such as an unexpected adverse effect); one or more outcomes of interest in the review was reported incompletely so that they could not be entered in a meta‐analysis; the trial report failed to include results for a key outcome that would have been expected to have been reported for such a trial (ORBIT classification).

Other bias (bias due to problems not covered elsewhere) ‐ assessment at trial level

We assessed any other risk of bias that reflected other circumstances that may have threatened the validity of the trial.

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

• Unclear risk of bias: 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: used a potential source of bias related to the specific trial design; had been claimed to have been fraudulent; had some other serious problem.

We established a 'Risk of bias' graph and a 'Risk of bias' summary figure.

We distinguished between self‐reported, investigator‐assessed and adjudicated outcome measures.

We defined the following outcomes as self‐reported.

• Non‐serious adverse events.

• Hypoglycaemia, if reported by participants.

• Health‐related quality of life.

• Blood glucose control, if measured by trial participants.

We required the following outcomes to be investigator‐assessed.

• All‐cause mortality.

• Incidence of T2DM.

• Time to progression to T2DM.

• Serious adverse events.

• Cardiovascular mortality.

• Non‐fatal myocardial infarction.

• Non‐fatal stroke.

• Congestive heart failure.

• Amputation of lower extremity.

• Blindness or severe vision loss.

• End‐stage renal disease.

• Hypoglycaemia, if measured by trial personnel.

• Blood glucose control, if measured by trial personnel.

• Socioeconomic effects.

Summary assessment of risk of bias

Risk of bias for a trial across outcomes: some 'Risk of bias' domains such as selection bias (sequence generation and allocation sequence concealment) may affect the risk of bias across all outcome measures in a trial. Otherwise, we did not perform a summary assessment of the risk of bias across all outcomes for a trial. If we identified a high risk of selection bias, we excluded the trial.

Risk of bias for an outcome within a trial and across domains: we assessed the risk of bias for an outcome measure including all of the entries relevant to that outcome (i.e. both trial‐level entries and outcome‐specific entries). We defined 'low' risk of bias as low risk of bias for all key domains, 'unclear' risk of bias as unclear risk of bias for one or more key domains, and 'high' risk of bias as high risk of bias for one or more key domains.

Risk of bias for an outcome across trials and across domains: these were the main summary assessments that we incorporated in our judgements about the quality of evidence in the 'Summary of findings' table(s). We defined 'low' risk of bias as most information coming from trials at low risk of bias, 'unclear' risk of bias as most information coming from trials at low or unclear risk of bias and 'high' risk of bias as a sufficient proportion of information coming from trials at high risk of bias.

TSA

In a single trial sparse data and interim analyses increase 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 (i.e. the cumulative Z‐curve crosses the monitoring boundaries) (Lan 1983). Likewise, before reaching the planned sample size of a trial, the trial may be stopped due to futility if the cumulative Z‐score crosses the futility monitoring boundaries (Higgins 2011a). Sequential monitoring boundaries for benefit, harm or futility can be applied to meta‐analyses as well (termed trial sequential monitoring boundaries) (Higgins 2010; Wetterslev 2008). In TSA, the addition of each trial in a cumulative meta‐analysis is regarded as an interim meta‐analysis and helps to clarify whether significance or futility is reached, or whether additional trials are needed (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 with the threshold of data associated with statistics. We performed TSA on all outcomes (Brok 2009; Pogue 1997; Wetterslev 2008).

The idea in TSA is that if the cumulative Z‐curve crosses the boundary for benefit or harm before a diversity‐adjusted required information size is reached, a sufficient level of evidence for the anticipated intervention effect has been reached with the assumed type I error and no further trials may be needed. If the cumulative Z‐curve crosses the boundary for futility before a diversity‐adjusted required information size is reached, the assumed intervention effect can be rejected with the assumed type II error and no further trials may be needed. If the Z‐curve does not cross any 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 in a well‐powered single trial and subsequently adjusted for diversity among the included trials in the meta‐analysis (Brok 2009; Wetterslev 2008). We applied TSA as it decreases the risk of type I and II errors due to sparse data and multiple updating in a cumulative meta‐analysis, and it provides us with important information in order to estimate the risks of imprecision when the required information size is not reached. Additionally, TSA provides important information regarding the need for additional trials and the required information size of such trials (Wetterslev 2008).

We applied trial sequential monitoring boundaries according to an estimated clinically important effect. We based the required information size on an a priori effect corresponding to a 10% relative risk reduction (RRR) for beneficial effects of the interventions and a 30% relative risk increase for harmful effects of the interventions.

TSA for continuous outcomes was performed with MDs, by using trials applying the same scale to calculate the required sample size. For continuous outcomes we tested the evidence for the achieved differences in cumulative meta‐analyses.

For adjustment of heterogeneity of the required information size we used the diversity (D²) estimated in the meta‐analyses of included trials. When diversity was zero in a meta‐analysis, we performed a sensitivity analysis using an assumed diversity of 20% when future trials are included, possibly changing future heterogeneity among trials.

Quality of evidence

We presented the overall quality of the evidence for each outcome according to the GRADE approach, which takes into account issues relating not only to internal validity (risk of bias, inconsistency, imprecision, publication bias) but also to external validity, such as directness of results. Two review authors (BH and DS) independently rated the quality of evidence for each outcome. We present a summary of the evidence in the summary of findings Table for the main comparison. This provides key information about the best estimate of the magnitude of the effect, in relative terms and as absolute differences, for each relevant comparison of alternative management strategies, the numbers of participants and trials addressing each important outcome, and rates the overall confidence in effect estimates for each outcome. We created the 'Summary of findings' table on the basis of methods described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a) by means of the table editor in Review Manager (RevMan 2014), and include two appendices (Appendix 17; Appendix 18) providing checklists as guides to the consistency and reproducibility of GRADE assessments (Meader 2014) to help with the standardisation of the 'Summary of findings' tables. Alternatively, we would have used the GRADEproGDT software (GRADEproGDT 2015) and presented evidence profile tables as an appendix. We present results for the outcomes as described in the Types of outcome measures section. If meta‐analysis was not possible, we present the results in a narrative format in the 'Summary of findings' table. We justify all decisions to downgrade the quality using footnotes, and we make comments to aid the reader's understanding of the review where necessary.