JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-023-02716-4 (2023)

Title: Glepaglutide, a novel glucagon-like peptide-2 agonist, has anti-inflammatory and mucosal
regenerative effects in an experimental model of inflammatory bowel disease in rats
Version: 1 Date: 12 Dec 2022
Reviewer's report:
Authors studies Glepaglutide anti-inflammatory and intestinotrophic effects  in a rat model
of small intestinal inflammation.  demonstrationg that Glepaglutide co- and post-treatment
significantly reduced  inflammation,  increased small intestinal mass, indicating intestinal
regenerative effects.
The introduction is clear and well written, I have no commet about it.
I suggest to perform hystology on intestine in order to assess the inflammatory infiltrate and
changes in mucosa aspects.
I think that the paper is of interest after these enrichment in results
Review for 10.1186/s12876-023-02716-4 (2023)

Title: Glepaglutide, a novel glucagon-like peptide-2 agonist, has anti-inflammatory and mucosal
regenerative effects in an experimental model of inflammatory bowel disease in rats
Version: 3 Date: 10 Feb 2023
Reviewer's report:
the authors responded comprehensively to the reviewers' requests by making significant changes
to the manuscript.
I consider the work done to be satisfactory and I believe that the paper is ready for publication.
Review for 10.1186/s12876-023-02716-4 (2023)

Title: Glepaglutide, a novel glucagon-like peptide-2 agonist, has anti-inflammatory and mucosal
regenerative effects in an experimental model of inflammatory bowel disease in rats
Version: 3 Date: 09 Mar 2023
Reviewer's report:
I do not have any further comments.
Review for 10.1186/s12876-023-02718-2 (2023)

Title: Behavioral abnormalities in C57BL/6 mice with chronic ulcerative colitis induced by DSS
Version: 1 Date: 26 Dec 2022
Reviewer's report:
1. In the materials section, please provide a serial or material number. Not batch number.
2. Figure 1d and Figure 2d, please provide at least 2-3 colon samples for each group to compare
the length. It will be more convincing for readers.
3. Figure 2, Please specifically indicate what control 2 means.
4. Figure 5,6, I don't see much of a difference between chronic and acute colitis H/E results.
Please provide more convincing data to show how the chronic model showed the effects of
DSS treatment. It will be helpful to add arrows on images to explain what makes the difference
between the two colitis models.
Review for 10.1186/s12876-023-02718-2 (2023)

Title: Behavioral abnormalities in C57BL/6 mice with chronic ulcerative colitis induced by DSS
Version: 1 Date: 15 Jan 2023
Reviewer's report:
We often encounter patients with ulcerative colitis who are mentally stressed or prone to
mental disorders. It is very interesting that the author reported the association between intestinal
inflammation, behavioral abnormalities, and the hippocampus using an experimental animal
model mouse.
I have a major or several minor questions with the report that the author has presented.
1) Should the authors do an objective scoring of enteritis and hippocampal pathology. Frankly,
I do not see any difference between the CONTROL and DSS groups. To substantiate this, an
objective score should be provided.
At the risk of repeating myself, the author notes in his discussion that the hippocampal pathology
in the 3% DSS group was not significantly different versus the control group. How does the
author conclude that there was no significant difference, something that is not quantified?
2) Does the unpaired t test (two-tailed) mentioned in the statistical methods section mean the
same thing as the T test (and nonparametric tests)? Would it be different? I suggest you correct
it, as it is difficult for the reader to understand. Or please check with a statistician.
3) (Fig 3 e) If you found a significant difference in sucrose water consumption, the author should
show it on the graph. Was there a significant decrease in sucrose water drinking? Or was there
no significant difference in it?
4) In the conclusion, the author states that both the acute and chronic enteritis models
cause behavioral abnormalities. In the acute enteritis model, enteritis symptoms cause
behavioral abnormalities. In the chronic enteritis model, psychological stress causes behavioral
abnormalities. However, based on the results presented by the authors, can we say that in the
chronic enteritis model, enteritis symptoms are not the cause?
5) The sucrose preference test; what does it mean that the acute enteritis model has reduced
preference and the chronic enteritis model does not? The authors should discuss that in the
discussion.
6) In the discussion, "Therefore, we speculated whether the mice in the DSS-induced UC model
had behavioral abnormalities, and hoped to improve the However, there is no experimental
system (whether or not enteritis is improved) in which a therapeutic drug (antipsychotic) was
used on mice in the DSS-induced UC model in this study. There is a disconnect between the
objectives and conclusions.
7) What the author states in the conclusion of the abstract is different from what is presented
in the results. Didn't both models, acute and chronic enteritis models, cause behavioral
abnormalities? Don't you want to state that the causes of the behavioral abnormalities are
different? The abstract should correct the conclusions in the body of the text.
Review for 10.1186/s12876-023-02718-2 (2023)

Title: Behavioral abnormalities in C57BL/6 mice with chronic ulcerative colitis induced by DSS
Version: 3 Date: 15 Feb 2023
Reviewer's report:
1)
In the method, “In the sucrose preference experiment, the consumption of purified water and
sucrose water was significantly reduced in the 3% DSS group.” Isn't it only sucrose water that
has decreased significantly? In the figure, purified water is indicated as n.s.. Which is correct?
Also in the discussion, it is stated that ''in the sucrose preference test, the pure water drinking
amount of the 3% DSS model group was slightly reduced while the sucrose water drinking, the
amount is greatly reduced.''
2)
In the method, the author describes "the sucrose preference experiment" as a method of
behavioral evaluations. However, in the discussion, it states that: In the 3% DSS model, the
reason for the decrease in the amount of sucrose consumed was considered to be pain due to
enteritis. In the 1.5% DSS model, despite behavioral changes other than "the sucrose preference
test," the amount of sucrose drinking was not reduced because the enteritis was mild. Again, isn't
the sugar water preference test assessing behavioral change as in the method? In other words,
in the 1.5% DSS model, why does sugar water consumption not decrease despite all behavioral
changes occurring except for the sugar water preference test? Or is there any literature that shows
it?
Review for 10.1186/s12876-023-02719-1 (2023)

Title: The Prognostic Role of the AST/ALT Ratio in Hepatocellular carcinoma Patients
Receiving Thermal Ablation Combined with Simultaneous TACE
Version: 0 Date: 10 Aug 2022
Reviewer's report:
In this study, the authors aimed to assess the prognostic value of the pre-treatment aspartate
transaminase (AST)/alanine transaminase (ALT) ratio in hepatocellular carcinoma (HCC)
patients receiving radiofrequency ablation (RFA)/microwave ablation (MWA) combined with
simultaneous TACE.
The endpoint of prognosis was overall survival (OS).
They found that  AST/ALT ratio cut-off value for OS prediction was 0.89, and patients with
a higher AST/ALT ratio had poorer overall survival. The median OS for the high-value AST/
ALT group was not reached, while the median OS for the low-value AST/ALT group was 48.5
months (P=0.0047). The univariate and multivariate analysis showed that AST/ALT ratio, AFP,
and tumor numbers were independent prognostic indicators for OS. The integrated nomogram
showed higher predictive accuracy for OS .
They concluded that the preoperative AST/ALT ratio can be a prognostic indicator for HCC
patients receiving thermal ablation combined with simultaneous TACE.
The study is of clinical interest. I have only a point requiring to be addressed. The
transaminase value has been previously investigated as prognostic indicator of HCC treatments.
In particular, the authors in the discussion should discuss the recent findings of transient
hypertransaminasemia after TACE as significantly related to the objective radiological response
(TRANS-TACE: Prognostic Role of the Transient Hypertransaminasemia after Conventional
Chemoembolization for Hepatocellular Carcinoma. J Pers Med. 2021 Oct 17;11(10):1041. ).
In my opinion, this study further supports the potential use of transaminase serum levels as
prognostic markers in HCC patients who underwent locoregional treatments.
Review for 10.1186/s12876-023-02719-1 (2023)

Title: The Prognostic Role of the AST/ALT Ratio in Hepatocellular carcinoma Patients
Receiving Thermal Ablation Combined with Simultaneous TACE
Version: 0 Date: 19 Feb 2023
Reviewer's report:
This is a retrospective, single-center study investigating the prognostic value of aspartate
transaminase (AST)/alanine transaminase (ALT) ratio in hepatocellular carcinoma (HCC)
patients undergoing same-session RFA or MWA and TACE.
Advantages: The manuscript is well-written and the outcomes are supported by the
methodology. It is a valuable addition to the literature.
Disadvantages: Retrospective, single-center, with limited number of patiens. These limitations
are correctly reported by the authors.
General comments:
1. Some grammatical errors are found in the text. The authors should proofread the manuscript.
2. How were the variables for univariate analysis selected?
3. How the follow-up times were chosen
4. The exclusion criteria might be more detailed
5. Please briefly describe and explain how to build the nomogram model.
Review for 10.1186/s12876-023-02698-3 (2023)

Title: A new modality of colorectal cancer screening based on chronic disease management
Version: 2 Date: 17 Dec 2022
Reviewer's report:
Very interesting study. The statistics also seems robust and adequate.
My main concern is on the lack of validation of these results. This aspect should be properly
commented by the authors in the Discussion.
The authors should also briefly comment on the potential implications of this new modality also
in the surveillance (cite the paper PMID: 27005802)
Review for 10.1186/s12876-023-02698-3 (2023)

Title: A new modality of colorectal cancer screening based on chronic disease management
Version: 2 Date: 30 Dec 2022
Reviewer:  Harishankar Gopakumar
Reviewer's report:
Dear Authors,
It was a pleasure to read your work titled “A new modality of colorectal cancer screening based
on chronic disease management"
I commend the Authors on their well-researched and relevant work in the field of colorectal
cancer screening, especially in resource limited settings.
There are a few concerns that I have outlined below.
Minor
#1 Although this is a well-designed study, I am afraid this lacks novelty. It is well known that
awareness and education improve adherence to disease screening programs as a whole and is
not unique to colorectal cancer screening. As such the outcomes can be considered very much
predictable
# 2 In keeping with the above, it seems that the title "A new modality for colorectal cancer
screening" is not the most accurate as this study does not describe a new screening tool, but
demonstrates how education and awareness improves reception from the community.
Overall, I feel this study highlights the importance to good quality patient education and ongoing
doctor-patient relationship as a major determinant of success of any preventive/screening
program.
Review for 10.1186/s12876-023-02653-2 (2023)

Title: PRIMIS: Design of a pivotal, randomized, phase 3 study evaluating the safety and efficacy
of the nonsteroidal farnesoid X receptor agonist cilofexor in noncirrhotic patients with primary
sclerosing cholangitis
Version: 1 Date: 08 Dec 2022
Reviewer's report:
The design of a randomized, double-blind, placebo-controlled phase 3 trial on safety and
efficacy of the nonsteroidal farnesoid X receptor agonist cilofexor in noncirrhotic PSC patients
is described. Sites in 16 countries have been activated and a long follow-up period with up to 96
weeks is planned. The topic is of high interest since there is no proven pharmacologic treatment
for PSC that slows progression of the disease. The study is well designed, comprehensible
presentation of the implementation of the phase 3 trial is shown.
Review for 10.1186/s12876-023-02653-2 (2023)

Title: PRIMIS: Design of a pivotal, randomized, phase 3 study evaluating the safety and efficacy
of the nonsteroidal farnesoid X receptor agonist cilofexor in noncirrhotic patients with primary
sclerosing cholangitis
Version: 1 Date: 15 Dec 2022
Reviewer:  Debjyoti Kundu
Reviewer's report:
The manuscript by Trauner et al describes a double -blind  placebo controlled phase 3 clinical
trial  study of an FXR agonist on non-cirrhotic PSC patients.
The manuscript  has been revised adequately addressing all the comments from the previous
review. It would have been indeed insightful to have preliminary data included, but the
manuscript contributes as an effective study design for a clinical trial of a drug that targets an
incredibly complex and heterogenous  biliary pathology per se. No further concern exists  for
this manuscript.
Review for 10.1186/s12876-023-02689-4 (2023)

Title: Comprehensive Analysis of the Biological Function and Immune Infiltration of SLC38A2
in Gastric Cancer
Version: 1 Date: 31 Dec 2022
Reviewer:  Tianyi Fang
Reviewer's report:
This manuscript reported the possibility of SLC38A2 as a biomarker of gastric cancer. It was
verified by bioinformatics, vivo and vitro experiments. This research is satisfactory and the
results are reliable. Publishing can be considered after minor revision.
1. I think immunohistochemistry is not satisfactory. At least the expression of SLC38A2
in pathological sections of gastric cancer with different degrees of differentiation should be
included. In addition, I think the hematoxylin staining  is not enough, resulting in low contrast.
2.The discussion part of the manuscript is too simple. The complex interaction between
SLC38A2 and immune cells should be a highlight of this study and should be discussed in depth.
3.Why is the subcutaneous model of animal experiment not verified by immunohistochemistry?
At least SLC38A2 expression should be detected.
Review for 10.1186/s12876-023-02689-4 (2023)

Title: Comprehensive Analysis of the Biological Function and Immune Infiltration of SLC38A2
in Gastric Cancer
Version: 1 Date: 09 Jan 2023
Reviewer's report:
This study revealed the prognostic value and expression of SLC38A2 in GC by bioinformatics
analysis and experimental skills. Specifically, colony formation, cell counting kit-8, wound
healing, transwell, and tumor formation assays were performed to assess the biological function
of SLC38A2. Furthermore, the potential regulatory mechanisms of SLC38A2 and its role in
tumor immune infiltration were explored. The article had a clear idea, a complete framework, a
certain degree of innovation and good results. However, some details still need to be adjusted.
1: This study adopted collected gastric cancer samples and multiple bioinformatics analysis
databases. I suggest that the corresponding flow chart is provided, which makes it easier for
readers to understand.
2: In the method section "Public database analysis", the author's description of the screening
process of the public database is too simple, for example, the description "The protein-protein
network of SLC38A2 was constructed using the GeneMANIA database" on page 8, line 12.
More detailed descriptions and screening criteria are necessary, we don't know how to screen
out related proteins. Other analysis procedures on public databases also need to be added.
3: In Figure 4C, the p-value is 0, which is not significant. The authors need to make a new
addition to the figure.
4: On the eighth page, it is written in the methods: "Moreover, enrichment analysis using Gene
Ontology (GO) annotations and Kyoto Encyclopedia of Genes and Genomes (KEGG) pathways
was performed using LinkedOmics (17)", while in the results section,  the authors said: "GSEA
was used to examine GO annotations and KEGG pathways".  The authors need to recheck the
front and back descriptions of the manuscript to ensure consistency. In addition, the genes used
for GO and KEGG analysis were not found, and again, all analysis procedures and screening
criteria should be fully described.
5: Why use LinkedOmics to analyze miRNA and transcription factor targets of SLC38A2 in
GC? What role do these miRNAs and transcription factors play in gastric cancer?
6: In this study, it can be seen that SLC38A2 is associated with the infiltration of multiple
immune cells in gastric cancer, but in the discussion section, the author only discussed
macrophages. The authors should complement other relevant immune cells. Furthermore, how
is the infiltration of these immune cells related to the prognosis of gastric cancer patients?
Combining the relationship between immune cells and the prognosis of patients with gastric
cancer and the correlation of SLC38A2 will help to accurately analyze the relationship between
SLC38A2 and immune cell infiltration.
7: The manuscript needs further English polishing and some obvious grammatical problems
have been found.
Review for 10.1186/s12876-023-02689-4 (2023)

Title: Comprehensive Analysis of the Biological Function and Immune Infiltration of SLC38A2
in Gastric Cancer
Version: 5 Date: 14 Feb 2023
Reviewer:  Tianyi Fang
Reviewer's report:
The author has answered my question and is generally satisfactory, and I have no further
questions. I think the manuscript can be published in its current form.
Review for 10.1186/s12876-023-02689-4 (2023)

Title: Comprehensive Analysis of the Biological Function and Immune Infiltration of SLC38A2
in Gastric Cancer
Version: 5 Date: 20 Feb 2023
Reviewer's report:
The author provides good answers to the questions raised, and some suggestions have been well-
revised. After making these modifications, the quality of this study has been improved. I think
the conditions for acceptance are met and it can be published.
Review for 10.1186/s12876-022-02623-0 (2023)

Title: Preoperative CA19-9 and GGT ratio as a prognostic indicator in ampullary carcinoma
Version: 4 Date: 29 Oct 2022
Reviewer's report:
The authors present a thought provoking manuscript on the utility of a new prognostic indicator
for ampullary adenocarcinoma by creating a ratio of  CA 19-9 and GTT to increase the specificity
of each. I congratulate them on their efforts on this endeavor. I have several questions I would
like addressed.
-In the introduction of the manuscript, the authors list a variety of conditions that increase the
GGT in patients.  Was this laboratory value adjusted in participants with comorbidities that
lower the specificity of GGT?
-The final paragraph of the introduction where the authors state their hypothesis also appears to
hold a conclusion statement for the study. May require rewording so it is stated as a question
they look to answer.
-It is unclear when the laboratory data calculating the CA 19-9/GTT ratio is being collected. The
results state after hospitalization but is that at diagnosis or post-operatively? And why was this
time point chosen as the best time to make the prognostic measurements?
-One of the exclusion criteria, states that participants that died of “other diseases” were excluded.
Was this within a certain time frame after surgery? How was it determined that their disease
could not be contributed to ampullary cancer? Often the sequalae of ampullary cancer treatment
lead to death which would still result in ampullary cancer being the ultimate cause of death.
-The methods lists a variety of “predictors factors that may affect survival”. Is there any data
you can site as to why you chose these factors opposed to others such as positive lymph node
ratio or resection margin status?
-The authors state in the methods that AJCC 8th edition was used for staging. The AJCC staging
updated from the 7th edition to the 8th edition during the study period. Was staging of earlier
participants updated by a pathologist or the authors?
-The results state “8 cases of urine yellow” as the presenting symptoms. I would ask for
clarification on this symptom as I am not familiar with it.
-The results state that “some” patients received adjuvant therapy. What percentage of patients
received therapy and was it accounted for in the multi-variate analysis of recurrence free survival
and overall survival?
-Limitations of the study need to be expanded to include the fact that they had limited number
of patients to investigate and as such did not have a validation cohort for their nomogram.
The retrospective nature of the study limits their ability to assess a variety of variables such as
ampullary cancer subtype and adjuvant therapy regimens.
-I do not believe the data supports the conclusion made by the authors. The study suggests that
CA 19-9/GTT may be a useful tool in prognosis of ampullary cancer but this data has not been
validated even within their own patient population much less externally.
-Recommend reading through the manuscript for grammatical errors.
Review for 10.1186/s12876-022-02623-0 (2023)

Title: Preoperative CA19-9 and GGT ratio as a prognostic indicator in ampullary carcinoma
Version: 4 Date: 12 Nov 2022
Reviewer's report:
With the present paper the Authors aimed at assess the prognostic significance  of CA19.9-GGT
ratio in ampullary cancer  patients undergoing radical resection.
Even if the retrospective design of the study and the relatively small number of patients enrolled
could affect the power of the study, I think that the topic is interesting and the statistical analysis
is very well performed and therefore it deserved to be published.
However I have some comments:
- In the results section is written that jaundice was present in 67  patients. Few lines later is
written that jaundice was present in 138 patients. Pleas check.
- How the authors decided to measure the CA 19.9/GGT the first day after surgery?  should be
useful assess its modification during the next days?
- What about dose it before surgery? Could it have some predictive value?
- Given the possible influence of biliary obstruction and cholestasis on the CA 19.9 and GGT
maybe it could be more indicate  to conduct a different analysis considering patients with
jaundice and patients without it.
Review for 10.1186/s12876-022-02623-0 (2023)

Title: Preoperative CA19-9 and GGT ratio as a prognostic indicator in ampullary carcinoma
Version: 6 Date: 30 Nov 2022
Reviewer's report:
The authors have answered my comments in an exhaustive way.
With few revision in the language the paper is ready for publication.
Thanks
Review for 10.1186/s12876-023-02693-8 (2023)

Title: Change of monocytes/macrophages in ulcerative colitis patients with symptoms of anxiety
and depression
Version: 1 Date: 18 Sep 2022
Reviewer's report:
The authors conducted a study focusing on the relationship between patients with ulcerative
colitis and anxiety/depressive symptoms and showed that patients with anxiety/depressive
symptoms tend to have worse QOL and worse clinical symptoms of ulcerative colitis. It
was also shown that concentrations of inflammatory cytokines such as TNF-#, IL-1#, and
IL-6 were significantly higher in UC patients with anxiety/depressive symptoms. Furthermore,
patients with anxiety and depressive symptoms had a higher percentage of CD14++CD16+ and
CD14+CD16++ monocytes, a higher percentage of CD68+ cells in the intestinal mucosal layer,
and a higher M1/M2 ratio.
These are very interesting results, but some additional confirmation is needed at the time of
publication.
1) Could you please tell me if the patients in your study had any history of anxiolytic use or
psychiatric consultation?
2) Since you mentioned that there was a difference in steroid use between the two groups, what
was the dose and duration of steroid use?
Review for 10.1186/s12876-023-02693-8 (2023)

Title: Change of monocytes/macrophages in ulcerative colitis patients with symptoms of anxiety
and depression
Version: 1 Date: 06 Dec 2022
Reviewer's report:
This paper examines the mental state of ulcerative colitis using data.
Unfortunately, this paper does not deserve acceptance.
Linking mental state with blood cell data is too forced and has no basis.
There is no reason to deny that the result of the relationship was the result of chance.
Review for 10.1186/s12876-023-02693-8 (2023)

Title: Change of monocytes/macrophages in ulcerative colitis patients with symptoms of anxiety
and depression
Version: 1 Date: 31 Dec 2022
Reviewer's report:
The presented manuscript describes UC patients with symptoms of anxiety/depression suffered
worse disease, and possible mechanisms. This study provides an interesting perspective.
However, it requires some revisions as listed below.
#The authors are requested to analyze the relationship between the degree of anxiety and
depression and the degree of disease activity of UC.
#How many UC patients were treated for anxiety and/or depression? The authors are needed to
describe this information, as it is important as basic data.
#How many UC cases were treated for anxiety/depression and had decreased disease activity?
The authors are recommended to please describe them, if you have data.
Review for 10.1186/s12876-023-02693-8 (2023)

Title: Change of monocytes/macrophages in ulcerative colitis patients with symptoms of anxiety
and depression
Version: 3 Date: 16 Feb 2023
Reviewer's report:
This paper is appropriately revised, but I ask that the following points be added.
#Figure 1B in Figure legends. The authors are needed to provide the abbreviations for HADS-
A and HADS-B.
Review for 10.1186/s12876-023-02700-y (2023)

Title: Prognostic Assessment Capability of a Five-Gene Signature in Pancreatic Cancer: A
Machine Learning Based-Study
Version: 2 Date: 26 Jan 2023
Reviewer:  Abedalrhman Alkhateeb
Reviewer's report:
The author proposed 5-gene panel (ANKRD22, ARNTL2, DSG3, KRT7, PRSS3) as
prognostics biomarkers for pancreatic cancer. The work is based on classification and regression
models, it is comprehensive,  evaluated by KM survival and AUCROC, and may gain so many
interests. However, I have minor suggestions:
- The literature is missing similar methods such as (PMID: 35845587) and comparison with it,
machine learning prognostics models (PMID: 35205681 and/or PMID: 30890858).
- The parameter of the regression and classification could be added ( if available).
- The authors may conduct a pathway analysis using KEGG or GO enrichment analysis tools.
Review for 10.1186/s12876-023-02700-y (2023)

Title: Prognostic Assessment Capability of a Five-Gene Signature in Pancreatic Cancer: A
Machine Learning Based-Study
Version: 2 Date: 30 Jan 2023
Reviewer:  Jeong Hoon Lee
Reviewer's report:
Dear Authors, many thanks for the opportunity to read your valuable paper.
Pancreatic cancer is a type of cancer with very rare data and a very poor prognosis.
Survival analysis using mRNA expression in TCGA database has been performed quite a lot.
However, due to the absence of normal samples in the TCGA database,
comparative studies with cancer and normal samples from the same organ were lacking.
In this study, mRNA prognostic markers of pancreatic cancer were identified by merging
multiple databases.
This manuscript is very well written, easy to read and understand.
I have only to suggest to you some minor comments, and some my question.
1. Pege 5, 3.3. Removing batch effects.
Have you performed PCA on all 20,000 genes?
If possible, could you provide a figure utilizing umap rather than PCA?
And there are no Abbreviations for PCA.
Removing the batch effect is very important, but I am curious whether it is right or wrong that
there is no difference between the cancer sample and the normal sample in the PCA results.
2. Regarding Figure 1, 3 and 5, 6, can you make it a little prettier?
It is unfortunate that the size of the lines and dotted lines is unbalanced.
But the content of the w is very good.
In particular, kaplan meier is too long vertically.
3. Regarding fig 6 and fig 7.
When specificity increases, but there is a section where sensitivity increases.
This is very strange.
4. In a database where TNM stages are available, can you provide the results of coxph regression
analysis of 5 genes and TNM stages together?
TNM stage is one of the most powerful prognosis factors, but I wonder if gene expression can
complement TNM stage.
Review for 10.1186/s12876-023-02706-6 (2023)

Title: A novel nomogram for identifying candidates for adjuvant chemotherapy in patients with
stage IB gastric adenocarcinoma
Version: 1 Date: 25 Aug 2022
Reviewer's report:
The authors reported “A novel nomogram for identifying candidates for adjuvant chemotherapy
in patients with stage IB gastric adenocarcinoma”. The authors concluded that the prognostic
nomogram in this study presented great prediction ability for these patients.
However, there are many problems in this paper, I think.
1. The authors should present the #-coefficient value in the Tables. #-coefficient is the most
important value, with which nomogram can be constructed. X axis should be started Zero point
in each variable.
2. From the graphical viewpoint, the graphical presentation of nomogram is uncommon.
3. I think continuous variables (age) should be modeled as (3-knot) restricted cubic splines for
potential nonlinear effect.
4. The authors categorized RNE factor. Harrell’s guideline (Harrell FE. Regression Modeling
Strategies: With Applications to Linear Models, Logistic Regression, and Survival Analysis.
2nd edition. New York: Springer; 2015) emphasized avoiding the categorization of continuous
variables because some categorical variables are subjective and hard to standardize and do not
contain the same amount of statistical information as continuous variables.
5. From the nomogram of CSS, chemotherapy did not seem important prognostic variables
compared to other factors.
6. Given the results of this paper, it is hard to reach the conclusion. The authors should perform
below-mentioned survival analysis. First, the authors should divide 3 groups (low, intermediate,
high) based on total points obtained by nomogram. The authors should draw Kaplan-Meier
survival curves in each risk group.
Review for 10.1186/s12876-023-02706-6 (2023)

Title: A novel nomogram for identifying candidates for adjuvant chemotherapy in patients with
stage IB gastric adenocarcinoma
Version: 1 Date: 07 Sep 2022
Reviewer's report:
Dear editors, It's my honor to be invited to review this article, which was titled as "A novel
nomogram for identifying candidates for adjuvant chemotherapy in patients with stage IB gastric
adenocarcinoma."
The authors presented a nomogram typical study for the prediction of the prognosis of
patients with gastric cancer. I recommend dispelling doubts and some necessary revision before
publication.
1#As far as I know, similar articles have been published (Development and Validation of a
Nomogram to Predict the Benefit of Adjuvant Radiotherapy for Patients with Resected Gastric
Cancer/A SEER population analysis of stage IB resected gastric cancer: who can benefit from
adjuvant therapy?).It is suggested to supplement previous similar studies and elaborate the
original intention of the author to carry out the study again.
2#In this study, the author used logistic regression analysis and multivariate Cox regression.
In my opinion, this is repetitive work. In fact, I prefer the method of Wang et al. To establish
nomogram and distinguish high-risk and low-risk groups through Cox regression analysis.(A
SEER population analysis of stage IB resected gastric cancer: who can benefit from adjuvant
therapy?)
3#There are many pictures in this manuscript that can't be read, so that I can't evaluate the
accuracy of the study. I don't know if this is the problem of my computer. What I care
most about is that the independent predictors included in the nomogram do not seem to be
statistically significant in the multivariate regression analysis (P < 0.05).Gender(0.059),Tumor
size(0.097),Primary site(0.034/0.163/0.557)
Review for 10.1186/s12876-023-02706-6 (2023)

Title: A novel nomogram for identifying candidates for adjuvant chemotherapy in patients with
stage IB gastric adenocarcinoma
Version: 3 Date: 13 Oct 2022
Reviewer's report:
The authors have not answered the following questions, so I cannot accept this paper.
6. Given the results of this paper, it is hard to reach the conclusion. The authors
should perform below-mentioned survival analysis. First, the authors should divide
3 groups (low, intermediate, high) based on total points obtained by nomogram. The
authors should draw Kaplan-Meier survival curves in each risk group.
Response: According to your idea, I made further analysis using x-tile and divided
all the patients into three groups (low, intermediate, high) based on the total points
obtained by nomogram. The cut-off points were 99 and 133. However, there were no
significant outcomes. So, I don't think this is an effective method in this study. In this
article, we constructed a predictive nomogram to identify potential ACT-beneficial
cases based on the multivariable logistic regression model. The total score was
calculated by summing the scores corresponding to the six parameters. Then the model
could be used to predict the beneficial probability of ACT.  So I think this was a better
way than the risk-stratification method in this research.
Review for 10.1186/s12876-023-02706-6 (2023)

Title: A novel nomogram for identifying candidates for adjuvant chemotherapy in patients with
stage IB gastric adenocarcinoma
Version: 3 Date: 23 Dec 2022
Reviewer's report:
"PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: The overall impression of the manuscript is that it sounds very good.
The information provided are complete. The analysis is detailed conducted and the results are
pretty significant. The authors responded to the reviewers’ comments with precision adding
many details that enrich the manuscript. I agree with the observations of the reviewers and the
authors have done a good job. I believe that the efforts for the results obtained are visible and
that the results themselves are of great importance to better understand the correct way for the
management of gastric adenoca."
Review for 10.1186/s12876-023-02706-6 (2023)

Title: A novel nomogram for identifying candidates for adjuvant chemotherapy in patients with
stage IB gastric adenocarcinoma
Version: 5 Date: 24 Feb 2023
Reviewer's report:
"STATISTICAL REVIEWER ASSESSMENT:
Is the study design appropriate for the research question (considering whether the analyzed
population accurately reflects the design and whether you see any problems with control/
comparison groups, e.g., likely confounders)?
Yes - overall design, population, and control groups are appropriate
Are methodologies adequate and well implemented (considering whether assumptions are
addressed and whether analyses are robust)?
Yes - methodologies are adequate and well implemented, assumptions are addressed, analysis
is robust
Are the analyses adequately communicated (considering whether reporting details are adequate
and whether figures and tables are well labeled and described)?
Yes - important reporting details are present, analyses are adequately communicated, figures
and tables are well labeled and described
Does the interpretation accurately reflect the analyses without overstatement (considering
whether limitations/bias are acknowledged and whether accurate descriptors, e.g., 'significant',
are used)?
Yes - interpretation accurately reflects analyses, limitations/bias are acknowledged, accurate
descriptors are used
Could an appropriately REVISED version of this work represent a statistically sound
contribution?
Yes - current version has sound statistics
STATISTICAL REVIEWER COMMENTS:
The authors have generally been responsive to my previous comments. The authors have added
simple clarifications to the manuscript that make it easier to understand. The investigators use
relatively sophisticated statistical methods, which makes the paper interesting.
REQUESTED REVISIONS:
I have no further comments.
ADDITIONAL REQUESTS/SUGGESTIONS:
I have nothing more to add."
Review for 10.1186/s12876-023-02709-3 (2023)

Title: Esophageal motility disorders in symptomatic patients and its relation to age
Version: 3 Date: 28 Jan 2023
Reviewer's report:
This is a prospective analytical study to understand esophageal motility disorders in
symptomatic patients and is relation to age. It is a very interesting study, with great
methodology to explain esophageal motility disorders. Congratulations for your efforts and
science contribution.
1) A language revision should be done. Some phrases are confusing.
Example: Lower basal lower esophageal sphincter tone.
2) The introduction is excessively long and repetitive. The objective of the study is to search
for a relation between age, symptoms, and motility disorder. It isn´t necessary to describe all
the diseases and elderly frails.
3) Inclusion criteria was symptomatic patients who were submitted to Upper digestive
endoscopy. It should be interesting to describe the UDE findings an its relations to symptoms
and manometry.
4) The authors inclusion criteria was symptoms like heartburn, dysphagia, dyspepsia,
odynophagia, and GERD symptoms. What you mind when talking about GERD Symptoms?
Heartburn and dysphagia are esophageal GERD symptoms. I would like to understand better
what are the “GERD symptoms”.
5) In the elderly group the prevalent symptom was dysphagia, statically much higher than
the youngers. It could be a BIAS when interpretating the results. At the same time, elderly
related diseases and medications should interfere with the symptoms and maybe the manometric
findings. Another BIAS. My recommendation is to call attention to this potential weakness in
the study.
Minor
1) Were all the selected patients able to be submitted to esophageal manometry? We know that
this is a study that sometimes are difficult to perform, and patients may not tolerate then.
2) The conclusions should focus on the relation between symptoms and Manometric findings.
Maybe elderly have more dysphagia related to achalasia and other related diseases which can
explain the different manometric findings comparing to the “A” group. A conclusion paragraph
should be written to elucidate the topic.
3) The writing structure is sometime confusing. Maybe, it should be better to be more concise
and logical in the text organization.
Review for 10.1186/s12876-023-02709-3 (2023)

Title: Esophageal motility disorders in symptomatic patients and its relation to age
Version: 3 Date: 28 Jan 2023
Reviewer's report:
The authors present an analysis of the different rates of motility disorders, particularly achalasia,
in older patients ( >65 years) compared with younger patients referred for esophageal motility
based on symptoms of heartburn, regurgitation, and/or dysphagia.  They found that the rate of
achalasia in older patients were significantly higher than that of the younger group, and that
these patients were more likely to be malnourished.
This paper does make some interesting points in what is a relatively straightforward study.  There
are a number of issues that need either clarification or could be improved, outlined by section
below:
1. In the Introduction, there is a lengthy section covering cognitive decline in the elderly which
is not directly related to the study in the manuscript.  This can be condensed for more clarity
in the overall paper.
2. In the Methods, the detail of which manometric system was used needs to be more toward
the beginning of the Methods section.  Notably, this is an outdated manometric measurement
system and what is described should be referred to as “conventional manometry” to distinguish
it from high resolution manometry.
3. In the Methods it would also be helpful to indicate the time period during which these 385
manometric studies were performed.
4. Also in the Methods, there is detail of older definitions of esophageal motility disorders that
are currently considered out of date. There is a brief mention of high resolution manometry in
the Discussion, but since the definitions have changed relatively dramatically since 2008 as high
resolution manometry has become widely used, there needs to be some acknowledgement of
this and the implications on the results.
5. In the Results the authors indicate that the rate of achalasia in the patients of the older
group was 43%, and that of the younger group was 29%.  These rates are extremely high,
particularly given that these patients were not all referred for the symptom of dysphagia.  The
overall incidence of achalasia around the world is generally considered to be 1 to 2 individuals
per 100,000, with a prevalence of approximately 1 in 10,000.  Among patients referred to
our esophageal manometry lab over the last approximately 20 years, only 1 in 20 or so has a
manometric diagnosis of achalasia.  Further, achalasia tends to be more easily recognized with
high resolution manometry techniques, since conventional manometry can sometimes misread
axial LES movement as pseudo-relaxation.  Therefore it will be important to for the authors to
comment on this very high incidence of achalasia in their referred patients in the Discussion
section of the paper.
Review for 10.1186/s12876-023-02709-3 (2023)

Title: Esophageal motility disorders in symptomatic patients and its relation to age
Version: 4 Date: 25 Feb 2023
Reviewer's report:
This revision is much improved from the initial submission;  the writing is more clear and the
suggestions made by reviewers have largely been incorporated.  There are still a few things that
can be modified to make this paper stronger:
1.  It is not necessary to include any statements about conventional vs. high resolution
manometry in the methods, other than to state that conventional manometry equipment and
definitions of motility disorders were used; the detail about high resolution manometry vs.
conventional manometry should really only be in the discussion.
2.  The full definitions and criteria for motility disorders are helpful, but probably should be
put into a table rather than being detailed in the Methods section as they are now.  It would be
better to state in the Methods that conventional manometry definitions for the various motility
disorders were used (see Table x).
3.  In the Methods there is a statement that patients with inflammatory GERD were not included
in the study.  Does this mean that patients with erosive esophagitis were excluded?  Since many
of the patients did have heartburn it is likely that there were some GERD patients in the study
population.  This would be good to clarify.
4.  The very high incidence of achalasia in this study is still somewhat mysterious, since it is
so much higher than is generally seen among motility laboratories; the authors have added a
statement, per reviewer's suggestion, that this could be due to differences between conventional
manometry and high resolution manometry, however it is usually believed that achalasia is more
likely to be identified on high resolution manometry, rather than  on conventional manometry.
It would be helpful for the authors to included something in the discussion that speculates why
the rate of achalasia is so high in their population (and apparently was high in another study
cited by the authors).
5.  The conclusion at the end of the paper includes, "Possible causes are higher LES resting
pressure, impaired esophageal peristalsis, and incomplete LES relaxation."  What is described
here are the manometric features of achalasia, not the cause of anything, so this conclusion can
be strengthened by removing this sentence.
Review for 10.1186/s12876-023-02674-x (2023)

Title: Use of ramucirumab for various treatment linesin real-world practice of patients with
advanced hepatocellular carcinoma
Version: 0 Date: 25 Nov 2022
Reviewer:  Seogsong Jeong
Reviewer's report:
Kanogawa et al. reported a case series of advanced HCC. Although the study population is not
sufficient to evaluate the effectiveness of ramucirumab, the reported real-world evidence may
strengthen the pre-existing knowledge on the treatment of advanced HCC. I have some concerns
that may improve the quality of the manuscript and the driven results.
1. Inclusion and exclusion criteria for the inclusion of study participants are not given. Did any
patient undergo TACE, PMCT, etc.?
2. Basic information is not given. Providing AFP, CEA, HBV DNA, liver cirrhosis, tumor
differentiation, smoking, etc. may support a better understanding of the study population.
3. The major weakness of this study is no consideration of potential confounding factors. Since
this study is non-RCT, attempts to balance the treatment groups need to be made even if the
study population is insufficient. Listing the median OS or PFS in tumor size-stratified groups
or any other potential confounding factors-stratified groups may be necessary before making
conclusions.
4. Efficacy is valid for well-controlled studies, such as RCT. From my point of view, this study
evaluated the effectiveness, not efficacy.
5. Better discussion regarding the underlying mechanisms of ramucirumab against advanced
HCC is needed.
6. Elucidations regarding the strengths and limitations of this study is needed.