Criteria for considering studies for this review

Search methods for identification of studies

Electronic searches
We will perform electronic searches of The Cochrane Library (latest issue), MEDLINE (1966 to present), EMBASE (1988 to present) and CINAHL (1982 to present).

We will also search databases of ongoing trials: Current Controlled Trials (www.controlled‐trials.com ‐ with links to other databases of ongoing trials).
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.

Other sources
We will contact experts in the field in an effort to identify additional unpublished trials.

Reference lists
Bibliographies of papers will be handsearched.

Data collection and analysis

Selection of studies
Two reviewers will independently review the titles, abstract sections and keywords of every record retrieved from the literature searches to identify potentially eligible studies. Articles that clearly do not meet the inclusion criteria will be rejected at this initial review. We will obtain the full text of the remaining articles for further examination. We will assess each study for eligibility for inclusion against the defined selection criteria and eliminate any trial that does not fulfil this criteria, for example was not a randomised controlled trial, did not involve people who have diabetes, had no comparitor, included a co‐intervention, or in which the trial period was less than four weeks. The decision to eliminate a trial will be based on agreement by both reviewers. If there is any difference in opinion we will calculate the inter‐rater agreement for study selection using the kappa statistic (Cohen 1960), and then resolve the differences through discussion. If we exclude a trial after this, we will retain a record of the article, including the reason for its exclusion. An adapted QUOROM (quality of reporting of meta‐analyses) flow‐chart of study selection will be attached (Moher 1999).

Data extraction and management
Two reviewers will independently extract the data on the relevant outcome measures reported in each included study (for details see under 'Additional tables' Table 2; Table 3; Table 4; Table 5; Table 6).

We will extract the following data:

• general information: published or unpublished, title, authors, study setting, funding source, reference or source, contact address, country, language of publication, year of publication, duplicate publication;

• trial characteristics: design, duration, randomisation (and method), allocation concealment (and method), blinding of the outcome assessors.

• intervention and comparitor;

• participants: sampling method, exclusion criteria, total number and number in comparison groups, number who did not consent to participate, sex, age, health status, medication status, type of diabetes, criteria used to diagnose diabetes, similarity of groups at baseline, assessment of compliance, withdrawals or losses to follow‐up (reasons or description), subgroup;

• outcomes: outcomes specified above, including the measures of dispersion; the main outcome assessed in the study; energy intake, any other outcomes assessed, length of follow‐up, quality of outcome reporting;

• results: for outcomes and times of assessment (including a measure of variation), converted to measures of effect if appropriate, intention‐to treat analysis.

We will resolve any differences in data extraction by consensus, referring back to the original paper and discussion. We will contact primary authors when necessary to clarify data or to request additional information.

Assessment of methodological quality of included studies
Two reviewers will independently assess the quality of each included trial. We will calculate the level of inter‐rater agreement using the kappa statistic (Cohen 1960) and then resolve any difference in opinion through discussion. We will explore the influence of individual quality criteria in a sensitivity analysis (see under 'sensitivity analyses').

We will furtheron assess the internal validity of each included trial, based on the Cochrane Handbook for Systematic Reviews of Interventions (Higgins 2005). In particular, the following factors will be studied:

(1) Minimisation of selection bias ‐ a) was the randomisation procedure adequate? b) was the allocation concealment adequate?
(2) Minimisation of attrition bias ‐ a) were withdrawals and dropouts completely described? b) was the analysis by intention‐to treat?
(3) Minimisation of detection bias ‐ were the outcome assessors blind to the intervention?

Blinding of the people administering the intervention, as well as the participants actually eating the food, is generally impossible in dietary intervention trials, so blinding will not be assessed as a quality criterion. Blinding of outcome assessors to the intervention will be recorded.

Based on these criteria, the studies will be subdivided into the following three categories (Cochrane Handbook for Systematic Reviews of Interventions):
A ‐ low risk of bias: all quality criteria met
B ‐ moderate risk of bias: one or more of the quality criteria only partially met
C ‐ high risk of bias: one or more quality criteria not met

If appropriate, we will perform a sensitivity analysis based on this classification to compare the effect of quality on results in studies of high and low quality.

Measures of treatment effect
Dichotomous data
For dichotomous outcomes, we will express the effect size in terms of relative risk with 95% confidence interval (CI).

Continuous data
For continuous outcomes, if appropriate, we will calculate weighted mean differences. We will extract the baseline and post‐intervention means with standard deviations (SD) (or standard error of the mean (SEM) or 95% confidence interval (CI)) for the intervention and control groups, transforming any SEM or 95% CI into SD if appropriate. For absolute changes in outcome between baseline and post‐intervention for the control and intervention groups, mean difference will be calculated, if required, by subtracting the control absolute change from the intervention absolute change. The estimate of variance for each of these changes will equal Vpre + Vpost ‐ 2r(SEpre x SEpost), where Vpre and SEpre are the variance and standard error of the mean baseline value; Vpost and SEpost are the variance and standard error of the mean post‐intervention value; and r is the correlation between baseline and post‐intervention values. The variance of the total change is then the sum of the variance of the change in the intervention group and the variance of the change in the control group. If the value of r is not given, we will assume that r equals 0.5.
When post‐intervention measures of dispersion are not given (for example if the results are presented as percentage change from baseline), the baseline measures of dispersion will also be used as the post‐intervention values. This is a conservative approach, since variation at baseline should be larger than that at post‐intervention, but this approach will only be taken when pre‐ and post‐ measures of dispersion for the same outcome are similar to each other in other trials. If the results are given on different scales, we will use standardised mean differences or develop dichotomous variables. When data are only presented graphically, an estimate of the mean and SD will be obtained from the graph.

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 and per‐protocol 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) 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
We will test for heterogeneity between the trial results using the standard chi‐squared test to examine whether the observed variation in study results could be due to any variation expected by chance alone, with significance set at P < 0.1. Quantification of the effect of heterogeneity will be assessed, if appropriate, by means of I², ranging from 0% to 100% including its 95% confidence interval (Higgins 2002). I² demonstrates the percentage of total variation across studies due to heterogeneity and will be used to judge the consistency of evidence. I² values of 50% and more indicate a substantial level of heterogeneity (Higgins 2003). If heterogeneity is found, we will explore it using subgroup and sensitivity analyses. If summarising the results still seems appropriate (sufficiently similar studies of similar quality), we will use a random effects model which assumes the effect size varies across studies. We will use an intent‐to treat analysis, provided that the required information is obtainable.

Assessment of reporting biases
We will assess funnel plot asymmetry, if feasible, to explore the possibility of, for example, small sample bias (Cooper 1994; Tang 2000).

Data synthesis (meta‐analysis)
All data will initially be analysed with a fixed effect model. We will summarize the data statistically, including meta‐analysis of trial results if appropriate, that ist if the data are available and results are sufficiently homogeneous and of sufficient quality.

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. Subgroup analyses will be mainly used to explore clinical or methodological or statistical heterogeneity. The following subgroup analyses are planned:

• age: less than or equal to 18 years, 19 to 40 years, 41 to 65 years, more than 65 years;

• duration of trial intervention: short term (less than or equal to three months), medium term (three to six months), long term (more than six months)

• difference in the glycaemic index, or load, between the comparitor and trial interventions<

• diagnosis (type 1 or type 2 diabetes);

• duration of diabetes;

• initial body mass,

• follow‐up timing: less than or equal to six months, 6 to 12 months, more than 12 months

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 (risk difference, odds ratio etc.) and different statistical models (fixed and random effects models).