Criteria for considering studies for this review
Types of studies
All RCTs of vitamin E, allocating people with diabetes individually or by cluster, and with a follow-up of at least six months. Non-randomised and quasi-randomised controlled trials will not be eligible for inclusion.
Types of participants
Participants aged 18 years or older, with type 1 or 2 diabetes mellitus without diabetic chronic complications (nephropathy, neuropathy, retinopathy, cardiovascular events).
Diagnostic criteria (diabetes mellitus)
To be consistent with changes in classification and diagnostic criteria of diabetes mellitus through the years, the diagnosis should be established using the standard criteria valid at the time of the beginning of the trial (e.g. ADA 1999; ADA 2008; WHO 1998). Ideally, diagnostic criteria should have been described. If necessary, we will use authors' definition of diabetes mellitus. 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 where the same letters indicate direct comparisons.
(a) Any type of vitamin E supplementation, either in its natural or synthetic form, at any dose and duration, either in monotherapy or in combination with other antioxidants (i.e. lipoic acid, vitamin C).
(a1) No intervention.
(a3) Other antioxidants.
(a4) Mineral supplementation.
In case of combination therapy, we will only include studies in which the effects of vitamin E can be depicted. Therefore, additional interventions have to be the same between intervention and comparator groups.
Types of outcome measures
Method and timing of outcome measurement
Diabetic complications: diabetic complications are defined as nephropathy, neuropathy, retinopathy and cardiovascular events (myocardial infarction, stroke or peripheral vascular disease) measured at least at six months.
Glycaemic control will be measured by HbA1c at least at six months.
Adverse effects of the intervention: for example toxicity, haemorrhage, gastrointestinal effects.
All-cause mortality: defined as death from any cause.
Lipid profile: defined as blood levels of high-density lipoprotein (HDL)-cholesterol, LDL-cholesterol and triglycerides measured at least at six months.
Blood pressure: systolic and diastolic blood pressure, measured at least at six months.
Health-related quality of life: measured by validated instruments such as Diabetes Quality of Life Measure (DQOL), 36-item Short Form (SF-36) V2, EQ-5D.
Socioeconomic effects: direct medical costs or direct medical resource use.
'Summary of findings' table
We will establish a 'Summary of findings' table using the following outcomes listed according to priority.
Health-related quality of life.
Search methods for identification of studies
We will search the following sources from inception to the present.
We will search the OpenSIGLE database to identify grey literature and the ProQuest Dissertations and Theses to retrieve theses related to our topic of interest.
We will also search trial registers including ClinicalTrials.gov (clinicaltrials.gov/), metaRegister of Controlled Trials (www.controlled-trials.com/mrct/), the EU Clinical Trials register (www.clinicaltrialsregister.eu/), and the World Health Organization (WHO) International Clinical Trials Registry Platform Search Portal (apps.who.int/trialsearch/).
For detailed search strategies, see Appendix 1. We will continuously apply PubMed's 'My NCBI' (National Center for Biotechnology Information) email alert service to identify newly published studies using a basic search strategy (see Appendix 1). Four weeks before we submit the final review draft to the Cochrane Metabolic and Endocrine Disorders Group (CMED) for editorial approval, we will perform an updated search on all specified databases. If we identify new studies for inclusion, we will evaluate these and incorporate findings in our review before submission of the final review draft (Beller 2013).
If we detect additional relevant key words during any of the electronic or other searches, we will modify the electronic search strategies to incorporate these terms and document the changes. We will place no restrictions on the language of publication when searching the electronic databases or reviewing reference lists of identified studies.
We will send results of electronic searches to the CMED for databases that are not available at the editorial office.
Searching other resources
We will try to identify other potentially eligible trials or ancillary publications by searching the reference lists of retrieved included trials, (systematic) reviews, meta-analyses and health technology assessment reports.
Data collection and analysis
Selection of studies
We will manage the citations using a reference management software (ProCite). Two review authors (AS, DO) will independently scan the title, abstract or both sections of every record retrieved to select the studies to be assessed further. The review authors will not be blinded about study authors or the name of the publication. We will review all potentially relevant articles as full-text versions. If AS and DO do not agree about selecting a study, a third review author (DR) will resolve the disagreement. If disagreement persists, we will add the article to an 'awaiting assessment list' for further clarification by study authors. We will attach an adapted PRISMA (preferred reporting items for systematic reviews and meta-analyses) flow-chart of study selection (Figure 1) (Liberati 2009).
Data extraction and management
For studies that fulfil inclusion criteria, two review authors (AS, DO) will independently abstract relevant information about population and intervention characteristics using standard data extraction templates (for details see Table 1; Appendix 2; Appendix 3; Appendix 4; Appendix 5; Appendix 6; Appendix 7; Appendix 8; Appendix 9; Appendix 10; Appendix 11; Appendix 12; Appendix 13). We will resolve any disagreements by discussion, or, if required, by consultation with a third review author (DR).
Table 1. Overview of study populations
|Characteristic||Intervention(s) and comparator(s)||Sample sizea||Screened or eligible|
|[N] ITT||Finishing study|
|Randomised finishing study|
|(1) Study ID||I1: vitamin E|| || || || || || || || |
|I2:|| || || || || || || || |
|C1:|| || || || || || || || |
|C2:|| || || || || || || || |
| || ||total:|| || || || || || |
| Grand total|| All interventions || || || ... || || || ... || || |
| All comparators || || || ... || || || ... || || |
| All interventions and comparators || || || ... || || || ... || || |
We will provide information including trial identifier about potentially relevant ongoing studies in the table 'Characteristics of ongoing studies' and in the appendix 'Matrix of study endpoints (trial documents)'. We will try to find the protocol of each included study, either in trial registers, in publications of study designs, or both, and specify data in the appendix 'Matrix of study endpoints (trial documents)'.
We will send an email to all study authors of included studies to enquire whether they are willing to answer questions regarding their trials. We will present the results of this survey in Appendix 14. Thereafter, we will seek relevant missing information on the trial from the primary author(s) of the article, if required.
Dealing with duplicate publications and companion papers
In the event of duplicate publications, companion documents or multiple reports of a primary study, we will maximise yield of information by collating all available data. In case of doubt, we will give priority to the publication reporting the longest follow-up associated with our primary or secondary outcomes.
Assessment of risk of bias in included studies
Two review authors (AS, DO) will assess each trial independently and will resolve possible disagreements by consensus, or with consultation of a third party. In case of disagreement, we will consult the rest of the group and make a judgement based on consensus.
We will assess risk of bias using The Cochrane Collaboration's tool (Higgins 2011a; Higgins 2011b). We will assess the following criteria:
Random sequence generation (selection bias).
Allocation concealment (selection bias).
Blinding (performance bias and detection bias), separated for blinding of participants and personnel, and blinding of outcome assessment.
Incomplete outcome data (attrition bias).
Selective reporting (reporting bias).
We will judge risk of bias criteria as 'low risk', 'high risk' or 'unclear risk' and evaluate individual bias items as described in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will provide a 'Risk of bias' figure and a 'Risk of bias summary' figure.
We will assess outcome reporting bias (Kirkham 2010) by integrating the results of 'Examination of outcome reporting bias' (Appendix 7), 'Matrix of study endpoints (trial documents)' (Appendix 6) and section 'Outcomes (outcomes reported in abstract of publication)' of the 'Characteristics of included studies' table. This analysis will form the basis for the judgement of selective reporting (reporting bias).
We will assess the impact of individual bias domains on study results at endpoint and study levels.
For blinding of participants and personnel (performance bias), detection bias (blinding of outcome assessors) and attrition bias (incomplete outcome data), we intend to evaluate risk of bias separately for subjective and objective outcomes (Hróbjartsson 2013). We will consider the implications of missing outcome data from individual participants.
We define the following endpoints as subjective outcomes.
We define the following outcomes as objective outcomes.
Measures of treatment effect
We will express dichotomous data as odds ratios (ORs) or risk ratios (RRs) with 95% confidence intervals (CIs). We plan to evaluate the risk reduction and use it to estimate the number needed to treat for an additional beneficial outcome (NNTB) whenever it is possible. We will assess continuous outcomes (e.g. blood pressure) using mean difference (MD) or standardised mean difference (SMD) depending on whether the outcomes are measured using the same scales, with 95% CIs. If information is provided in the articles, we will perform an intention-to-treat (ITT) analysis.
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.
Dealing with missing data
We will deal with missing data following guidance in the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a). We will try to obtain relevant missing data from authors, and assess reasons for missing data from published studies. If data are likely to be 'missing at random', we will perform an available data analysis. If data do not seem to be 'missing at random' we will assume that participants with missing values have poor outcomes regardless of the group they were allocated.
Assessment of heterogeneity
In the event of substantial clinical, methodological or statistical heterogeneity, we will not report study results as meta-analytically pooled effect estimates.
We will identify heterogeneity by visual inspection of the forest plots and by using a standard Chi2 test with a significance level of α = 0.1, in view of the low power of this test. We will examine heterogeneity using the I2 statistic, which quantifies inconsistency across studies to assess the impact of heterogeneity on the meta-analysis (Higgins 2002; Higgins 2003), where an I2 statistic of 75% or more indicates a considerable level of inconsistency (Higgins 2011a).
When we find heterogeneity, we will attempt to determine potential reasons for it by examining individual study and subgroup characteristics.
We expect the following characteristics to introduce clinical heterogeneity.
Duration of diabetes.
Assessment of reporting biases
We will use funnel plots where we include 10 studies or more for a given outcome to assess small study effects. Owing to several possible explanations for funnel plot asymmetry we will interpret results carefully (Sterne 2011).
Unless there is good evidence for homogeneous effects across studies, we will primarily summarise low risk of bias data by means of a random-effects model (Wood 2008). We will interpret random-effects meta-analyses with due consideration of the whole distribution of effects, ideally by presenting a prediction interval (Higgins 2009). A prediction interval specifies a predicted range for the true treatment effect in an individual study (Riley 2011). In addition, we will perform statistical analyses according to the statistical guidelines contained in the latest version of the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2011a).
Subgroup analysis and investigation of heterogeneity
We will carry out subgroup analyses and plan to investigate interactions. The following subgroup analyses are planned.
We will perform sensitivity analyses in order to explore the influence of the following factors on effect size.
Restricting the analysis to published studies.
Restricting the analysis taking into account risk of bias, as specified in the section Assessment of risk of bias in included studies.
Restricting the analysis to very long or large studies, to establish how much they influence the results.
Restricting the analysis to studies using the following filters: diagnostic criteria, language of publication, source of funding (industry versus other), country.
We will also test the robustness of the results by repeating the analysis using different measures of effect size (RR, OR, etc.) and different statistical models (fixed-effect and random-effects models).