Review for "Unexpected Early Proteomic Changes in Alzheimer's Disease Model Mice Synaptosomes"

Completed on 12 Aug 2017

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Comments to author

In the currently reviewed manuscript by Ball et al, synaptic preparations of WT and transgenic AD model mosue brains at 3 ages are compared by quantitative label-free mass spectrometry which is surprisingly deep given that the platform used was an LTQ Orbitrap. Statistics are applied judiciously, and after stepwise, qualitative, views of the overall data are examined. This is appropriate, given that sample number for each of the Tg-AD age groups is only N=3. The study nicely demonstrates a qualitative-quantitative workflow of analysis, and that combining the time series analysis (STEM) with differential expression statistical approaches improves robusthess of pathway analysis. I list some concerns below but think if these are addressed, the manuscript would be suitable for publication in the journal GigaScience and I support that the study provides insight into AD and particularly the AD model examined.

Concerns to address:

1) It is not clear why the ELISA does not pick up highly elevated soluble AB42, if indeed as the authors claim that high soluble AB species is the cause for the stark differences observed already in the 3m AD-Tg mice synaptosomes. Can the authors provide insight in the referenced ELISA methods, discussion, or additional experimental characterization which would elucidate whether soluble AB species are driving the increase in 3m Tg-AD mice? I.e., is the AB42 increase at 3 months in Tg-AD vs WT mice due to mostly soluble AB42, whereas more aged mice contribute insoluble AB42 to what is measured by ELISA? Along these lines, statistics on Fig1, panel A would be welcomed.

2) Fig2C, y axes on histograms should be labeled "Frequency" or similar to make it readily apparent these are histograms on first inspection. In the legend "WT_x - WT_average", e.g., should be labeled "individual_WT_sample_measurement minus WT_average (N=9)" for clarity, and N=8 or 9, whichever number was used, which is not clear. Similarly, the descriptions of other histogram color codes should be more clearly labeled and the N for the average measurements specified explicitly.

3) The lack of downregulated synatposome proteins in Tg-AD mice at 9M in Fig3C volcano indicates a probable systematic bias in that equal peptide weight of synaptic material had to be loaded for LC-MS/MS, but those peptides are probably coming from a larger amount of equivalent tissue, since bulk synaptic loss occurs by this age. It should be noted in discussion that this study focuses on relative changes of proteins in a fixed amount of prepared synaptic peptides rather than on the already well established gross synaptic loss known to occur in AD models and actual AD patients.

4) I do not find the "Availability of data and materials" section in the text of the manuscript, only in the header of the PDF for review. It would be beneficial if the RAW LC-MS/MS data, analysis code, etc. were readily available during the final review process.

Additional specific correction suggestions:

line 167-168 & line 444-445 "Bengamini-Hochburg" method of course should be Benjamini-Hochburg for FDR determination.

line 237 "in comparison the FDR only" should read "in comparison to the FDR only"

line 281 "are biological efficacious" should read "are biologically efficacious"

line 338 "found to be dysregulated in the pre-clinical 3m Tg-AD model" would be better worded to reflect that changes measured were solely in the synaptic proteome, e.g.: "found to be dysregulated in synaptosomes of the pre-clinical 3m Tg-AD model"

line 351-352 Please specify what was the controlled/matched sex of all the mice used.

line 434 "Razor peptides were used for quantification" should read "Unique plus razor peptides were used for quantification", as there is no option in Maxquant to use razor peptides without unique peptides.