Overview of Gene Expression Analysis in Gastric Disease Infected with Helicobacter pylori: CLDN1 and MMP9 Could Be Biomarkers for Early Diagnosis of Gastric Cancer

Round 1

Reviewer 1 Report

This study aimed to determine gene-expression patterns in the progress of chronic atrophic gastritis to gastric cancer and to identify potential biomarkers for early diagnosis of gastric cancer. The study is well-designed and executed and paper generally well-written. I do have a few edit suggestions and concerns though:

• two poor expressions: 1) "genetic expression", use rather gene expression. 2) "RNA wholeness", use rather RNA Integrity.
• The section 3.3. Results are hard to follow purely based on the text, I suggest to re-write this paragraph so that it is easy to understand w/o needing to look at the Supplementary Figures. 
• The lack of concordance between the microarray and qPCR results for the main 5 genes of interest is both surprising and disappointing. Is there possibly a problem with the qPCR data analysis? W/o seeing the raw Ct data I can't judge if the ddCt calculations and fold change calculations were done correctly. I would expect positive validation results by qPCR for at least 80% of the genes (4/5 studied). Instead, the GC vs CAG results were systematically inverse to the microarray results. Also it is not clear how the "fold change" values on Table 5 were derived for CAG and GC in both analyses (are they fold changes or rather normalized expression levels)? If they are fold changes, then fold changes compared to what? The "vs" columns makes more sense.
• I congratulate the authors for having done the IHC on an extensive set of FFPE tissue samples. The results for MMP9 and CLDN1 are convincing and "save" the paper. 

Author Response

Please see the attachment.

Author Response File: Author Response.docx

Reviewer 2 Report

Rivas-Ortiz and her colleagues have written a study with the purpose of identifying genes whose expression might be used as early diagnosis markers for gastric cancer (GC) in the context of a chronic Helicobacter pylori infection. The usefulness of such biomarkers have been well explained by the authors, as H. pylori can cause GC, and late detection of such GCs increases the risk of dying.

The authors have analyzed Claudin 1 and 7 (CLDN1, CLDN7), Matrix Metalloproteinase 9 (MMP9) and Myc proto-oncogene (C-MYC) as potential biomarkers, using their results of gene expression microarrays and RT-PCR. They suggest using CLDN1 and MMP9 as biomarkers after further analysis by immunohistochemistry.

Unfortunately, I find that their results are not sufficient for such a claim and require some more data.

Main issues:

My main issue with the findings is that the results from the microarray data are very much discrepant with that of the RT-PCR data. This is very worrying as it seems to indicate that at least one of the two techniques, maybe both, have not produced reliable data. Furthermore, immunohistochemistry was only carried out for 2 of the 5 proteins in question. This does appear to confirm the microarray data. The authors should confirm their findings with the 3 other proteins at least, as we cannot be sure in which direction the three other protein levels will go.

RNA is known to be very unstable, even when stored in proper conditions. Did the authors produce the cDNA for RT-PCR just after extraction of RNA for the microarray experiments or later, when the microarray results have been analyzed? If it’s the latter case, I would suggest, if possible, to try and find fresh biopsy samples to cross-validate their microarray results by RT-PCR.

From a methodological point of view, although the selected genes do make sense based on their already published roles in cancer, other genes would have been a good choice, such as GKN1 and 2, TFF1 and 2. The problem with CLDN1 and MMP9 is that from the results of the authors, they are both increased in CAG and CG, and therefore can differentiate these from follicular gastritis or healthy tissue, but it is more difficult to differentiate GC from CAG, which would be useful. Selecting a protein whose expression changes between CAG and CG (such as the 4 mentioned, but the authors have listed others that might be more practical) could be used to indicate if the CAG has progressed to CG or not and aid the medical practitioner in deciding which course of action he should take. Ideally, such genes should be regulated in one direction in CAG vs control, and in the opposite direction in CG vs CAG or CG vs control.

 

Suggestions:

The authors have listed some genes upregulated or downregulated in both CAG and GC, but did not list these. These should be added as supplementary data, as it could be very useful for future studies.

Another information that could be of use, is to compare the findings of the authors with the findings of cited similar studies (Hippo et al. [8] and Kim et al. [9]), this could help determine the specificity of evolution towards GC in a H. pylori infection context. I encourage the authors to do such a comparison in the discussion, especially if there are genes with a notably different behavior.

 

Secondary issues:

The authors should add in the material and methods section how H. pylori infection has been diagnosed in the biopsies and if the archived samples have an H. pylori infection diagnosis.

In the RT-PCR section of the materials and methods, the Applied Biosystems primer/probe sets also include a set for B2M (Hs00984230_m1). It is not listed in the above gene list, nor do we have any data concerning it. It should either be removed, or data should be presented.

Table 2: the labels should be detailed. Which P-value and % are we talking about? The enrichment is fold change? Readers should be able to understand at a glance what the figures are.

 

Tables show GO enrichment only, why not include GSEA analysis? Also, the main text often refers to main results that are described in supplementary figures. I suggest that the authors put the figures with main findings as main figures. Supplementary materials should contain annex data, not main findings (for example, CLDN7 lines 266-267 refer to sup. Figure 5 or line 325-326, MMP9 refers to sup fig. 7).

Figures S2 and S4 legends should be more precise. Titles especially, S2 is not very concise, S4 should indicate the top diseases and functions in which the genes are enriched, and that it was made using IPA (I suppose?).

Line 343 mentions a supplementary table 4, I did not find any such table.

Figure 3: the authors should indicate the area where the selected inserts come from (with a small rectangle, for example).

In the discussion:

The role and importance of Claudin 1 in GC is not clear in the references cited, the authors rightly note that aspect. However, in line 388, the authors put references with conflicting results (notably Jung et al.) saying that there is indication that CLDN1 correlates with progression.

In other cancers, such as colorectal cancers, CLDN1 appear to be protumoral, since most of the authors’ cancer samples are of the intestinal type, could this explain that they have higher levels of CLDN1?

Line 418-419: The authors’ sentence is misleading when citing Ichiyasu et al.: Claudin 1 does not affect MMP9 in that article. It is the other way around: MMP9 status affects Claudin 1 levels.

Line 417-419: supplementary figure 7 does not show any Claudin 1. The link with the sentence is not clear.

 

I commend the authors for their discussion which is well researched. Figure 4 is a good example of how their results could be explained. It remains however hypothetical, and future studies should confirm that. Also, not a lot is said about CLDN7 and OLFM4, which are described in cancers (albeit not in GC). Perhaps a few lines on these genes could be added. Also, CLDN7 has been shown to possibly interact with OLFM4 in a two-hybrid assay. I am unsure of the relevance of this interaction in GC, but since both proteins appear in the authors’ study, perhaps there is something to explore here. If the authors could do a proximity ligation assay (PLA) on the archived samples at their disposal, there might be an interesting finding to do (for the current or a future study).

 

 

English language suggestions:

The English is understandable, however, there are many errors or typos here and there. Also, some sentences are unnecessarily complicated and could cause confusion. I suggest the authors review the English. Especially in the following lines: 21-24, 29-31, 105-107, 214-216, 220-222, 238-240, 250-251, 264-267, 274, 323-326.

Line 29 “notorious” should be “notable”

There are a lot of words separated by “–“, I suppose this could be due to editing. The authors should check this.

Line 220: “subexpressed” should be “overexpressed”? It is otherwise not consistent with the previous findings.

Many occurrences of “Contrasts” should be changed to “comparison”.

Many occurrences of “Expressed” should be changed to “found”, to avoid confusion between the actual expression levels, and the author’s findings.

Line 330: “real time” should be “real time PCR” to avoid confusion.

 

Author Response

Please see the attachment.

Author Response File: Author Response.docx

Round 2

Reviewer 2 Report

Although the authors have not addressed all of my concerns, they have sufficiently improved their manuscript for publication.