Criteria for considering studies for this review

Search methods for identification of studies

Electronic searches
We will use electronic search strategies to identify relevant trials (as defined under 'type of studies'), as well as reviews/meta‐analysis (for identification of additional trials). The following databases will be searched:

• The Cochrane Library (latest issue);

• MEDLINE (until recent);

• EMBASE (until recent).

We will also search databases for ongoing trials:

• Current Controlled Trials (http://www.controlled‐trials.com)

• UK National Research Register (http://www.update‐software.com/national/nrr‐frame.html)

• Center Watch Clinical Trials Listing Service (http://www.CenterWatch.com/)

• National Institute of Health (http://clinicalstudies.info.nih.gov/)

The described search strategy (see for a detailed search strategy under 'Additional tables' ‐ Table 1) will be used for MEDLINE. For use with EMBASE and The Cochrane Library this strategy will be slightly adapted.

Handsearching
We will try to identify additional studies by searching the reference lists of relevant trials and reviews identified.

Other search strategies
We will contact the manufacturers of various insulin preparations (Ely Lilly, Novo Nordisk). In addition, we will try to identify and contact researchers conducting ongoing trials.

Search for identification of studies will not be restricted by language.

Data collection and analysis

Selection of studies
Two authors (MV, AN) will independently scan the titles, abstract sections and keywords of every record retrieved. Full articles will be retrieved for further assessment if the information given suggests that the study fulfills the insertion criteria and does not meet the exclusion criteria. If there is any doubt regarding these criteria from the information given in the title and abstract, the full article will be retrieved for clarification. Interrater agreement for study selection will be measured using the kappa statistic (Cohen 1960). Where differences in opinion exist, they will by resolved through open discussion. In the case of further dispute, the article will be added to those 'awaiting assessment' and the authors will be contacted for clarification. If no clarification is provided, the review group editorial base will be consulted. Upon inclusion‐ these trials will be subjected to a sensitivity analysis. An adapted QUOROM (quality of reporting of meta‐analyses) flow‐chart of study selection will be attached (Moher 1999).

Data extraction and management
For studies that fulfil inclusion criteria, two authors (MV, AN) will independently abstract relevant population and intervention characteristics using standard data extraction templates (for details see 'Characteristics of included studies' and Table 2; Table 3; Table 4; Table 5; Table 6 under 'Additional tables') with any disagreements to be resolved by discussion, or if required by a third party.
The following data will be extracted:
(1) General information: author, title, publication (type, unpublished), language of publication, year of publication, country, complete reference or source, contact details, duplicate publication, multiple publication, rural or city, single centre versus multicentre, setting, stated aim of the study, sponsor, ethic committee approval and description of conflict of interests.
(2) Trial design: prospective study, control group, parallel study, placebo controlled, active medication controlled, cross‐over study, run‐in period, wash‐out period (for cross‐over trials), carryover effect described (for cross‐over trials), period effect described, sampling method, power calculation, selection bias (randomisation, unit of randomisation and allocation concealment adequacy), performance bias (blinding of patients and caregivers, method of blinding, check of blinding, check of blinding method), attrition bias (intention‐to‐treat analysis, withdrawals description, drop‐outs description, losses to follow‐up description, change of groups (cross‐overs), number of drop‐out and withdrawals and losses to follow‐up, reasons for drop‐outs or withdrawals or losses to follow‐up description), detection bias (blinding of outcome assessors), overall quality assessment, definition of inclusion criteria, definition of exclusion criteria, specification of exclusion criteria, predefined subgroups, posthoc defined subgroups and specification of subgroups.
(3) Participants: diabetes mellitus diagnostic criteria description, diabetes mellitus diagnostic criteria validity, exclusion criteria definition, baseline characteristics i.e. number of participants, age, gender, race, body mass index, glycated haemoglobin, fasting plasma glucose, fasting blood glucose, preprandial glucose, bedtime glucose, duration of diabetes mellitus, age of diabetes mellitus onset, diabetes mellitus related complications (neuropathy, nephropathy, retinopathy, large vessel disease), diabetes mellitus related treatment (i.e. insulin treatment duration, total daily insulin dose, total daily basal insulin dose, number of daily basal insulin injections, total daily bolus insulin injections, number of daily bolus insulin injections), comorbidities, other medications, identical treatment of groups (apart from intervention).
(4) Intervention: nature of basal and bolus insulin therapy (type of insulin preparation, premixed or not), basal and bolus insulin dose, basal and bolus insulin daily injections, basal insulin schedule, duration of therapy, length of follow‐up, compliance.
(5) Outcomes (assessed for short, intermediate and long terms as defines above): glycaemic control (i.e. glycaeted haemoglobin, fasting plasma glucose, fasting blood glucose, preprandial glucose, bedtime glucose), adverse effects (i.e. hypoglycaemia, nocturnal hypoglycaemia, weight gain, injection site pain), treatment related mortality, diabetic related mortality and all cause mortality. For long term timepoint we will also collect data regarding diabetic related complications (i.e. non‐fatal myocardial infarction, angina, heart failure, stroke, peripheral vascular disease, renal failure, amputation (of at least one digit), vitreous haemorrhage, retinal photocoagulation, blindness in one eye or cataract extraction).
(6) Effect modifiers: compliance, change of concomitant medication.

Any relevant missing information on the trial will be sought from the original author(s) of the article, if required.

Assessment of methodological quality of included studies
The quality of reporting each trial will be assessed based largely on the quality criteria specified by Schulz and by Jadad (Jadad 1996; Schulz 1995). In particular, the following factors will be studied:
(1) Minimisation of selection bias ‐ was the randomisation procedure adequate? was the allocation concealment adequate?
(2) Minimisation of performance bias ‐ were the patients and people administering the treatment blind to the intervention? Performance bias is anticipated due to the different nature of insulin preparations (for example, clear versus cloudy).
(3) Minimisation of attrition bias ‐ were withdrawals and dropouts completely described? was analysis by intention‐to‐treat?
(4) Minimisation of detection bias ‐ were outcome assessors blind to the intervention?

Based on these criteria, studies will be broadly subdivided into the following three categories:
(A) all quality criteria met: low risk of bias;
(B) one or more of the quality criteria only partly met: moderate risk of bias; and
(C) one or more criteria not met: high risk of bias.

This classification will be used as the basis of a sensitivity analysis. Additionally, we will explore the influence of individual quality criteria in a sensitivity analysis.
Each trial will be assessed independently by two reviewers (MV. AN). Interrater agreement for concealment of allocation will be calculated using the kappa statistic, and reported (Cohen 1960). In cases of disagreement, judgment will be made based upon consensus. Clinical quality criteria‐ none known.

Measures of treatment effect
The main outcome data, i.e. glycaemic control assessed through measurements of glycated haemoglobin and blood or plasma glucose, are expected to be of continuous nature. Other data are anticipated to be presented as counts or rates, for example number of adverse episodes.

Dichotomous data
Effect measures for count and rates data will be assessed according to their prevalence. Rare events such as death or long term complications will be measured with the rate‐ratio statistic, after undergoing log transformation for symmetrical considerations. The rate‐ratio compares the rate of events in the two groups by dividing one by the other. More common events such as the number of hypoglycaemic episodes will presumably be measured as continuous data. Weighted mean difference will be used to assess the difference in the mean number of events per group of patients per unit of time.

Continuous data
Effect measures for continuous data will be assessed through measurements of the mean difference (weighted mean difference), as results are expected to be on a unified scale (e.g. glycated haemoglobin level). It may be logical to consider the change from baseline rather than the numerical value itself, or the percentage of change from baseline values, for statistical analysis. This can limit the differences between studies populations with regards to their baseline diabetes status. However, we will consider change from baseline as a statistical parameter only if the change is reported in the original article as mean and standard deviation. The weighted mean difference will be used for each of the parameters assessed, after assuring parameters reported by the different trials point towards a single direction. If this is not the case, direction will be reversed by multiplying the mean values by (‐1). Whenever dichotomizing results will seem statistically feasible and clinically logical, we will use effect measurements for dichotomous data, i.e. risk ratio and odds ratio.

Short‐, intermediate‐ and long‐term (six months, six months to three years, and over three years, respectively) assessment of effect in the case of repeated observations will be performed.

Intention‐to‐treat analysis aims to include all participants randomised into a trial irrespective of what happened subsequently. This means that ideally, trial participants should be analysed in the group to which they were randomised regardless of which treatment they actually received or other protocol irregularities and all participants should be included regardless of whether their outcomes were actually collected. In this review we adopt an available‐case‐analysis, in which only the former criterion is met, and analysis is performed for every participant for whom data are available, thus filling‐in for missing data will not be conducted. Special attention will be given for three types of exclusions:
(a) participants excluded for predefined exclusion criteria using information collected before randomisation‐ will be considered as legitimate;
(b) participants excluded immediately after randomisation‐ illegitimate;
(c) very high dropout rates or inconsistency across study groups, which may indicate low quality of trial conduction.

Dealing with missing data
Relevant missing data will be obtained from authors, if feasible. Evaluation of important numerical data such as screened, eligible and randomised patients as well as intention‐to‐treat (ITT) and per‐protocol (PP) population will be carefully performed. Drop‐outs, misses to follow‐up and withdrawn study participants will be investigated. Issues of last‐observation‐carried‐forward (LOCF), ITT and PP will be critically appraised and compared to specification of primary outcome parameters and power calculation.

Dealing with duplicate publications
In the case of duplicate publications and companion papers of a primary study, we will try to maximise yield of information by simultaneous evaluation of all available data. In cases of doubt, the original publication (usually the oldest version) will obtain priority.

Assessment of heterogeneity
Heterogeneity is a term used to describe variability among trials encountered in a meta‐analysis. In our review, we anticipate some clinical diversity, e.g. baseline diabetes status and treatment, as well as methodological diversity, both giving rise to statistical heterogeneity. On the one hand, the scope of our review is relatively confined; therefore heterogeneity is not inherently large. On the other hand, disease status may be variable among participants and bolus insulin injections in the study groups may be differ by type and intensity. Methodologically there is no promise for comparable quality.
Heterogeneity will be identified using the formal chi‐square test, which is intended to assess whether observed differences in results are compatible with chance alone. Chi‐squared test have low power when trials have small sample size or are few in number. Therefore a P value of 0.10 will be considered statistically significant. We will also try and quantify the amount of heterogeneity and its impact on the meta‐analysis by describing the percentage of the variability in effect estimates that is due to heterogeneity rather than chance (Higgins 2002; Higgins 2003). I² values of 50% and more indicate a substantial level of heterogeneity (Higgins 2003). When heterogeneity is found, we will attempt to determine potential reasons for it by examining individual study characteristics and those of subgroups of the main body of evidence. A negative chi‐square will not necessarily mean that no heterogeneity exists or should not be further explored. In this view, a subgroup analysis will be performed as discussed below.

Assessment of reporting biases
Publication bias will be analysed with the funnel plot method. Funnel plot asymmetry will be assessed statistically. It is, however, important to realise that publication bias is only one of a number of possible causes of funnel‐plot asymmetry.

Data synthesis (meta‐analysis)
Data will be summarised statistically if they are available, sufficiently similar and of sufficient quality. Statistical analysis will be performed according to the statistical guidelines referenced in the newest version of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2005).
In case of significant heterogeneity, it is unreasonable to assume that there is one 'true' effect underlying the data, that is constant across different populations, and therefore a random effects model will be used, if appropriate. Otherwise, a fixed‐effect meta‐analytic model will be conducted, ignoring heterogeneity. However, as stated above, if heterogeneity will prove to be substantial, it may be unwise to perform a meta‐analysis.
When addressing continuous data, inverse variance method will be utilized for conducting a fixed‐effect analysis, whereas DerSimonian and Laird method will be utilized for a random‐effect meta‐analysis.
For counts and rates data with rare prevalence of events, the generic inverse variance method will be used to combine the log transformation of the rate‐ratio across trials. For more common events for which the summery statistic is the weighted mean difference, analysis will be performed as in the case of continuous data.
In the case of dichotomous data types, we will express the effect of treatment with relative effect measures, i.e. risk‐ratio and odds‐ratio, which are more consistent than absolute measures. These will be calculated for an event (rather then for a non‐event) and re‐expressed as absolute measures which are more interpretable by clinicians.

Subgroup analyses and investigation of heterogeneity
Subgroup analyses will only be performed if one of the primary outcome parameters demonstrates statistically significant differences between treatment groups. To further explore heterogeneity and investigate the effect modification of participants and treatment types, we will perform a subgroup analysis, according to the following clinically logical predefined groups. If more than ten articles are available for each of the following characteristics, a meta‐regression model will be used. Otherwise, standard subgroup analysis will be followed. It is noted that if additional meaningful characteristics will be found, a posthoc analysis will be conducted.

(1) Participants
a. gender ‐ male versus female;
b. diabetes status‐ mild to moderate versus severe (according to clinical status and treatment).
(2) Intervention
a. number of daily basal intermediate acting insulin injections (reflecting routine versus tight control);
b. type of long acting insulin preparation‐ glargine versus ultralente;
c. type of intermediate insulin preparation‐ NPH versus lente;
d. type of short acting insulin‐ regular versus insulin analogues;
e. type of insulin treatment‐ separate basal and bolus injections versus mixed preparations.

A dose‐response analysis will not be performed, nor any indirect comparisons between groups not directly evaluated head to head in a clinical trial.

Sensitivity analyses
We will perform sensitivity analyses in order to explore the influence of the following factors on effect size:
repeating the analysis excluding unpublished studies;
repeating the analysis taking account of study quality, as specified above;
repeating the analysis excluding any very long or large studies to establish how much they dominate the results;
repeating the analysis excluding studies using the following filters: diagnostic criteria, language of publication, source of funding (industry versus other), country.

The robustness of the results will also be tested by repeating the analysis using different measures of effects size (relative risk, odds ratio etc.) and different statistical models (fixed and random effects models).