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Thank you for your submission to PeerJ. I am writing to inform you that your manuscript, "Associations between the human intestinal microbiota, Lactobacillus rhamnosus GG and serum lipids indicated by integrated analysis of high-throughput profiling data" (#2012:11:101:1:0:REVIEW), has been accepted for publication.
Our production staff will be in touch with you shortly with any publication-related queries, to clarify any details required to move the manuscript forward, and to set a publication date.
Congratulations and thank you for your submission.
Academic Editor for PeerJ
5 January 2013
Dear Dr. de Vos,
Firstly, the good news is that the two outside expert reviewers of your manuscript both agree this is “good stuff” and subsequent to revision should be published in our new journal PeerJ. Their detailed (and supportive and incisive) comments are below.
Next my apologies that it has taken as long as it has: PeerJ intends to be timely and quick, as well as thorough and supportive of authors’ goals. Here it has taken longer than we wish, for a variety of reasons high amongst which were the holidays and people being unavailable.
As you said on submission, this report furthers that in two reports form your groups, Kekkonen RA, Sysi-Aho M, Seppanen-Laakso T, Julkunen I, Vapaatalo H, Oresic M, Korpela R. 2008a. Effect of probiotic Lactobacillus rhamnosus GG intervention on global serum lipidomic profiles in healthy adults. World J Gastroenterol. 14(20):3188-3194. and Kekkonen RA, Lummela N, Karjalainen H, Latvala S, Tynkkynen S, Jarvenpaa S, Kautiainen H, Julkunen I, Vapaatalo H, Korpela R. 2008b. Probiotic intervention has strain-specific anti-inflammatory effects in healthy adults. World J Gastroenterol. 14(13): 2029-2036, both of which I printed and read in addition to the 39 pp manuscript (9ncluding abstract, figures and tables) itself.
Please revise the manuscript – quite minor – taking in to account the comments of the two outside reviewers plus myself (who cannot resist making suggestions, if I am reading). You as authors might have two goals: (1) firstly to get this on record as normal EU process in a form that no one is ever expected to read but you can cite as being on record. Or (2) as experienced scientists you may wish to communicate to your colleagues interested in the topic just what they should be thinking and taking in to regard. Unless the manuscript is seriously revised (and of course with 8 authors and the EU practices, none of these has really thought this through adequately), I promise you this will fit into the first class and be ignored except by the authors. Of course, a modern editor is not usually so blunt – she or he merely shuffles papers or files. However, I hope to help PeerJ set a high standard, as I have in previous efforts with a hand-full of other journals. Therefore a 3rd set of comments are attached, dealing primarily with the figures and tables (of course, the data) and to a much less extent the writing.
Good luck in your effort. It would be wonderful if all authors were required to be involved and learn and work together. It is our hope that after taking longer than wished-for in the initial review, the revised manuscript should be accepted for publications within a day or two of posting.
Academic Editor, email@example.com
Suggestions from the Editor:
1) Minor, but remove “lipidome” and “lipidomic” et alia. and other novel “omics” terms. A meta-genomics PhD student here suggested that the journal should charge 700€ for every “ome” or “omics” beyond the most-used 3-5. There are actually hundreds now and I recall when a new genomics centre was being started when I was at the University of Cape Town, in order to gain support for the Centre, it started with “nose-omics” for a mouse researcher in the Zoology Department) and “root-omics” for someone interested in gene expression in flooded maize fields. It is bad enough that we are probably stuck with metabolomics, but we do not need vitaminomics, sugaromics, aminoacidomics, et alia as well as lipomics. You have “mixOmics” from previous papers.
There are 3 Figures and 2 Tables, each of which could communicate its meaning much easier than now:
Fig. 1 legend of course has a trivial capitalizing error that none of the 8 authors considers one’s responsibility. There are three times for sampling and that information absolutely must be in the legend, as well as a simple statement of what “signal” is intended – as by telegraph? The sentence in the legend on “significance” should be moved from there to the text itself and the “bar” should be defined as for example +/- SD (N-x). The significant increase was only for the 2nd time data and not for the 1st or 3rd (earlier and later) time points, or else this reader does not understand the figure. Is the editor wrong or the authors just not careful?
2) For Figure 2, “correlation heatmap” is neither science nor English. It does not made clearer by the first hit in google.com “Significance level added to matrix correlation heatmap using ggplot2 “. How does “q” less than 5% differ from the most usually used “p” less than 5% standard for weakly significant and for example on line 154, p. 7? And of course when the authors say in the legend of Figure 2 that “abbreviations of lipid names, see the Methods section”, that is false, as line 141 on p. 7 says to look at the authors’ 2008 paper for this list. Again, either the editor is making a major mistake or the 8 authors have failed to read their own manuscript. That long long list needs to be added to the Fig. 2 legend if any reader is expected to gain any understanding from it.
3) For Fig. 3, “et rel” again is horrible narrow jargon and google.com shows it is used by microbiologists and USA government legal courts in different meanings. Which is intended here? Say it in words. Better of course is to use precise words and not confusing jargon. “Cross plots” is again jargon rather than language. And any author with a sense of statistical meaning would be impressed with the “scatter” of data in Fig. 3A and B, and so “highly correlated” is a poor choice of words. There is a significant correlation and you can calculate an R value for this, but mostly there is wide scatter of the data. Of course we do not know what TG54:5 means. [TG is measured in our doctors’ offices.] Much the same is for Fig. 4 with a lot of scatter more than a “positive association” being most visible and we do not know what ChoE920:5) is, although LDL is familiar.
4) The problems continue with the Tables. “Pearson correlation” is unfamiliar to most journal readers, most microbiologists and most “omics” researchers. It is in fact a measure of the scatter r that we are not given for Figs. 3 and 4. For Table 1, please say what those times are, 1 hour, 1 week or 1 month? “Between subjects can be said once; it is not said 3x? And the4 correlations all look quite tight with small scatter.
4) Table 2 is again a Table that cannot be read by intended readers and has the sole purpose of allowing the authors to get something that can not be understood on record. Are these )probably) Pearson correlations again? -- we are not told. The values are a bit lower than in Table 1, and some correlations are negative. Bacteriodes would be “genus level” and not two separate subgroups listed with species “et rel”, which is not defined. Please try again.
Of course, we all wish the authors would do their jobs carefully, so that outside peer reviewers can deal more with larger issues (a they have here with enthusiasm) and editors can not try to substitute for statisticians et rel. Good luck.
This is a well written study by experienced investigators in the field demonstrating several findings:
First, the absence of an impact of LGG administration on the fecal microbiota, as measured by HITChip and quantitative PCR, with the exception of the Lactobacillus quantities.
Second, the absence of an impact of LGG on serum lipid profiles.
Third, the correlation between certain bacterial phylotypes and lipid classes.
The negative findings support those of previously published studies and the positive findings are hypothesis generating and should lead to further research.
Here I have only one suggestion, and that is to clarify whether subjects were instructed not to consume store-bought probiotics during the study period, whether subjects were questioned on compliance with the intervention and with abstinence from store-bought probiotics, and to clarify not just the average excretion of LGG in the placebo group, but the range, so that the reader can ascertain whether the treatment and placebo groups were indeed distinct in their exposure to probiotics.
Because most of the latest studies in this field are using pyrosequencing technology, some discussion of how these results might be expected to differ or be the same if that technology had been used of HITChip instead would be very helpful.
The authors present a two compelling study that demonstrates, firstly, that there was no impact of a probiotic containing “L. rhamnosus GG” on the diversity and composition of the native gut community or the blood chemistry of 11 individuals versus 14 individuals given a placebo; secondly, the authors go onto to explore potential correlations between the microbial taxa detected in the study and blood serum lipids. Overall the manuscript is well written and presents an interesting study. It fulfills all the requirements of the journal.
I have one small criticism. The correlations in the second part of the paper, while based on 22 observations, are still only correlations between 2 time points. I know very well that you can generate such correlations and they do indeed turn out to be meaningful. However, in this current manuscript, as the authors themselves say, these correlations are deemed to be hypothesis generating. With this in mind, the authors need to statement to the methods (statistics section) and a paragraph to the discussion, which explicitly deals with the limitations of the experimental design for exploring such correlations. Even with the statistical tests applied, the correlation across 2 time points could be indicative of many other variables – the authors go so far as to suggest diet – but this is the tip of the iceberg. To get proper statistical power you would need to explore a more resolved longitudinal analysis. The authors absolutely need to expand on the limitations of their study. Especially, also toning down the rhetoric in the abstract, the final sentence of which is simply untrue “Our results suggest that several members of the Firmicutes,
Actinobacteria and Proteobacteria are involved in the metabolism of dietary and endogenous lipids”
See experimental design, the findings are valid if you accept that the experimental design is a little bit strained.
Ln 35 – ‘affecting’ not ‘affect’.
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