We recently read with considerable interest the paper entitled “Healthy dietary indices and risk of depressive outcomes: a systematic review and meta-analysis of observational studies”, by Lassale et al. . We commend the authors for this important research and agree that the data are of considerable public health importance. However, upon reading the paper, we noted a number of methodological limitations with the conduct of this meta-analysis.
First, the authors state in the statistical analysis section on page 2: “For each dietary score (exposure variable), we conducted separate meta-analyses dependent on study design (cross-sectional vs. longitudinal)”. However, it appears from the actual reporting of the results in the figures that the authors pooled data from cross-sectional, case−control and cohort studies together (in addition to separate pooled effect sizes) and produced an overall effect size for all study design types. For example, in Fig. 1, in which the pooled effect size of cohort studies was 0.67 (95% CI: 0.55−0.82) and that of cross-sectional studies was 0.66 (95% CI: 0.35−1.24), the paper also reported a combined pooled effect size (OR = 0.69; 95% CI: 0.59−0.82) . We suggest readers focus predominantly on the pooled effect sizes for the distinct study designs rather than on the overall pooled effect size, given that it is not methodologically correct to pool the study designs in this way.
Second, the authors appear to pool the evidence using ORs and not RRs, which is not in line with the common recommendations in meta-research [2,3,4]. Since HRs are time dependent, they should not be mixed with RRs/ORs (that are not time dependent) . Other authors have reported that the use of RRs instead of ORs should be preferred for better accounting for the different estimates used . Of importance, when an outcome is common (i.e. >10% in the unexposed group), the ORs usually exaggerate the RRs, making findings statistically significant when they are actually not . Contrary to these assumptions, the authors reported the data as ORs, probably introducing a bias in their findings; RRs should have been reported instead.
Third, almost all the results reported in the discussed work are heterogenous (as I2 ≥50%). However, no meta-regression or sensitivity analysis for explaining these results has been reported. For example, the authors pooled together the studies using depressive symptoms and depression, but the agreement between depressive symptoms and clinical depression is often low−moderate . The PRISMA guidelines , followed by the discussed review (page 2) , suggests to explore the sources of heterogeneity with appropriate statistical methods, such as meta-regression or sensitivity analyses .
Finally, the authors reported that “Estimates (beta and standard error) from studies that used depressive symptoms (outcome) as a continuous variable were converted into log odds ratios by multiplying by a factor 1.81 and then exponentiated”, citing the seminal work of Chinn . However, Chinn reports that this conversion is useful when the data are reported as continuous (in his work as SMDs) and not as a result of a linear regression analysis (i.e. as beta) . This concept is also accepted by the Cochrane group in Chapter 12 [10, 11].
In conclusion, we commend the authors on undertaking this work and welcome the findings of this important meta-analysis, but we believe that this paper has a number of potential methodological limitations that preclude any definitive answer on this topic.
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Veronese, N., Smith, L. Reply to ‘Healthy dietary indices and risk of depressive outcomes: a systematic review and meta-analysis of observational studies’. Mol Psychiatry 25, 3119–3120 (2020). https://doi.org/10.1038/s41380-019-0462-9