On 2016 Nov 03, Darren L Dahly commented:

Because BMC has not actually linked the original reviews to this paper on their site, I have posted my original review here. Some but not all of my concerns were addressed in the final manuscript.

Major Compulsory Revisions

The paper is entirely exploratory and this should be emphasized by the authors. There are no specific hypotheses being tested here, nor are there any theory based predictions that the observed results can be compared against. While exploratory analyses can of course be helpful, the utility here is seriously limited by the observational nature of the data, the crudeness with which key covariates are measured (by survey) and represented (by dichotomization), and the use of modelling technique that will be unfamiliar to most readers. Consequently, almost any result obtained from this analysis could be explained, or explained away, fairly easily. Given the results obtained, the authors claim the research can inform out understanding of the aetiology and prevention of obesity, but notably fail to provide even one concrete example of how.

My concerns are amplified in light of how the modelling of BMI SD scores has been reported in the paper. First and foremost, the paper doesn’t report the exact form of the growth mixture model (i.e. exactly what is the set of parameters being estimated), or the values of any of the estimates obtained (nor any indication of the uncertainly in these estimates). It is thus not possible to fully evaluate the work that has been done, and this must be corrected before any final decision on the paper could be made.

Based on what I can infer about the model from the text, I have some additional concerns for the authors that I hope are useful. The authors only state that the variances of the latent growth factors are “fixed.” This could mean they are fixed to any specific value, or that they are estimated but fixed to be equal across classes. Based on the text, I will assume they were fixed as zero. This means that 100% of the variance in BMI SD scores is explained by group membership, and the final model reported includes two groups, each with similar intercepts but different slopes (one increasing and one decreasing). The model being reported (assuming I am correctly guessing the exact form of the model) precludes any variation in the degree of these changes. Thus, if the model was a faithful, complete representation of how these children are growing, then the exact same grouping could be discovered by simply dividing the sample into children with increasing BMI SDs and those with decreasing scores. I find this hard to believe. Ironically, to justify the use of growth mixture modelling, the authors state that it is useful for better understanding heterogeneity in growth – but they then go on to describe a model that describes all of that heterogeneity with a binary classification. I predict that the variability in the BMI SD scores at any single time point is more informative than the binary classification resulting from the “complex” model being reported.

The authors should report how differences in the exact ages of measurement were handled. There are several options. The authors might have assumed everyone was measured at the same age at times 1, 2, and 3, which could be a considerable source of error depending on the variances of the ages of measurement. It seems more likely they have used the Mplus time-scores option, and if so, this needs to be described along with other details of the model. The authors might have also smoothed the individual curves prior to modelling, in which case the details of the procedure used should be reported.

The use of BMI SDs scores could be problematic. One the one hand, it has the advantage of normalising the BMI measures and simplifying the functional form of the growth curve (though BMI change is fairly linear from the age of 4 years anyway). However, it introduces a new challenge to interpreting the result, as it’s hard to distinguish the degree to which the model is describing changes in BMI within children over time, and differences between the observed sample and the reference population.

The 2 stage modelling process employed is sub-optimal. It ignores the uncertainty inherent in the classification and thus subsequent standard errors of the estimated relationships between class memberships and other covariates are artificially reduced. Mplus is very capable of estimating the models being reported here in a single model that avoids this limitation (and has several other options for relating class membership to covariates that are also likely more appropriate).

The authors state that the “clinical interpretation” of the models was an important factor in determining the number of classes included in the final, reported models, but give no indication or example of what this term means in this specific context. This should be clarified.

There are some serious limitations, independent of the growth mixture modelling, that bear consideration by the authors. The first is that there is no consideration of the role of puberty, or recognition of the distinction between developmental time vs calendar time. Second, there is no consideration of the children’s heights, and even if BMI is defined as a measure of mass that is roughly independent of height, it’s hard to say anything useful about a child’s growth while ignorant of how tall he/she is.

The description of how missing data was handled is insufficient and I would point the authors to several guidelines that I hope they find helpful (doi 10.1186/1471-2288-12-96).

The sample is not described in sufficient detail. At the very least, the overall response rate should be provided. I would suggest that the authors refer to an established reporting guideline (e.g. STROBE) to help avoid this kind of reporting error.

The paper overemphasizes the novelty of this analysis based solely on the use of growth mixture models. There the hundreds of existing population based studies of BMI in children and no reason to think this particular analysis is more informative than many/most of these.

The term “confounding” is found nowhere in the paper. To have any utility regarding identified risk factors, the authors should have something to say about the exchangeability of groups being compared.

On 2016 Nov 03, Darren L Dahly commented:

Because BMC has not actually linked the original reviews to this paper on their site, I have posted my original review here. Some but not all of my concerns were addressed in the final manuscript.

Major Compulsory Revisions

The paper is entirely exploratory and this should be emphasized by the authors. There are no specific hypotheses being tested here, nor are there any theory based predictions that the observed results can be compared against. While exploratory analyses can of course be helpful, the utility here is seriously limited by the observational nature of the data, the crudeness with which key covariates are measured (by survey) and represented (by dichotomization), and the use of modelling technique that will be unfamiliar to most readers. Consequently, almost any result obtained from this analysis could be explained, or explained away, fairly easily. Given the results obtained, the authors claim the research can inform out understanding of the aetiology and prevention of obesity, but notably fail to provide even one concrete example of how.

My concerns are amplified in light of how the modelling of BMI SD scores has been reported in the paper. First and foremost, the paper doesn’t report the exact form of the growth mixture model (i.e. exactly what is the set of parameters being estimated), or the values of any of the estimates obtained (nor any indication of the uncertainly in these estimates). It is thus not possible to fully evaluate the work that has been done, and this must be corrected before any final decision on the paper could be made.

Based on what I can infer about the model from the text, I have some additional concerns for the authors that I hope are useful. The authors only state that the variances of the latent growth factors are “fixed.” This could mean they are fixed to any specific value, or that they are estimated but fixed to be equal across classes. Based on the text, I will assume they were fixed as zero. This means that 100% of the variance in BMI SD scores is explained by group membership, and the final model reported includes two groups, each with similar intercepts but different slopes (one increasing and one decreasing). The model being reported (assuming I am correctly guessing the exact form of the model) precludes any variation in the degree of these changes. Thus, if the model was a faithful, complete representation of how these children are growing, then the exact same grouping could be discovered by simply dividing the sample into children with increasing BMI SDs and those with decreasing scores. I find this hard to believe. Ironically, to justify the use of growth mixture modelling, the authors state that it is useful for better understanding heterogeneity in growth – but they then go on to describe a model that describes all of that heterogeneity with a binary classification. I predict that the variability in the BMI SD scores at any single time point is more informative than the binary classification resulting from the “complex” model being reported.

The authors should report how differences in the exact ages of measurement were handled. There are several options. The authors might have assumed everyone was measured at the same age at times 1, 2, and 3, which could be a considerable source of error depending on the variances of the ages of measurement. It seems more likely they have used the Mplus time-scores option, and if so, this needs to be described along with other details of the model. The authors might have also smoothed the individual curves prior to modelling, in which case the details of the procedure used should be reported.

The use of BMI SDs scores could be problematic. One the one hand, it has the advantage of normalising the BMI measures and simplifying the functional form of the growth curve (though BMI change is fairly linear from the age of 4 years anyway). However, it introduces a new challenge to interpreting the result, as it’s hard to distinguish the degree to which the model is describing changes in BMI within children over time, and differences between the observed sample and the reference population.

The 2 stage modelling process employed is sub-optimal. It ignores the uncertainty inherent in the classification and thus subsequent standard errors of the estimated relationships between class memberships and other covariates are artificially reduced. Mplus is very capable of estimating the models being reported here in a single model that avoids this limitation (and has several other options for relating class membership to covariates that are also likely more appropriate).

The authors state that the “clinical interpretation” of the models was an important factor in determining the number of classes included in the final, reported models, but give no indication or example of what this term means in this specific context. This should be clarified.

There are some serious limitations, independent of the growth mixture modelling, that bear consideration by the authors. The first is that there is no consideration of the role of puberty, or recognition of the distinction between developmental time vs calendar time. Second, there is no consideration of the children’s heights, and even if BMI is defined as a measure of mass that is roughly independent of height, it’s hard to say anything useful about a child’s growth while ignorant of how tall he/she is.

The description of how missing data was handled is insufficient and I would point the authors to several guidelines that I hope they find helpful (doi 10.1186/1471-2288-12-96).

The sample is not described in sufficient detail. At the very least, the overall response rate should be provided. I would suggest that the authors refer to an established reporting guideline (e.g. STROBE) to help avoid this kind of reporting error.

The paper overemphasizes the novelty of this analysis based solely on the use of growth mixture models. There the hundreds of existing population based studies of BMI in children and no reason to think this particular analysis is more informative than many/most of these.

The term “confounding” is found nowhere in the paper. To have any utility regarding identified risk factors, the authors should have something to say about the exchangeability of groups being compared.