JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 1 Date: 25 Aug 2024
Reviewer's report:
The trial is interesting, and based on research
I have some comments;
2.2 Study Selection  please add (((Advanced stage))) to gastric cancer, or gastroesophageal
junction cancer.
3.4Safety results: Please delete second paragraph.  Also, it is worth adding more information
about certain side effects which were specifically higher in Nivolumab group, if possible.
Discussion:
Please compare your study to the study of Oyenuga et al; 2022,
https://ascopubs.org/doi/10.1200/JCO.2022.40.16_suppl.e16060
And reflect more on how your trial added to the current research,
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 1 Date: 28 Aug 2024
Reviewer:  Toshimitsu Tanaka
Reviewer's report:
In a meta-analysis, the authors found prolonged OS and PFS with nivolumab treatment for
advanced gastric cancer and esophagogastric junction cancer. They also found that adverse
events were more common with nivolumab treatment. The author has a serious problem that
needs to be resolved before publication.
Regarding the trials extracted in the meta-analysis of the current study, all four trials extracted
for Nivolumab vs placebo are the ATTRACTION-2 trial, a phase III trial. Subgroup analyses
and long-term follow-ups are included, but all the same trials are extracted. In addition, five
studies were selected for Nivolumab+chemotherapy vs. chemotherapy: three studies from the
phase III CheckMate 649 trial and two studies from the phase II and III ATTRACTION-4 trials.
In other words, the extracted trials are the results of long-term follow-ups and subgroup analyses
of almost the same clinical trials. Therefore, if it is Nivolumab alone, only the results of the
ATTRACTION-2 trial are being looked at. Furthermore, if it is Nivolumab plus chemotherapy,
there are only two trials, the CheckMate649 trial and the ATTRACTION-4 trial. With these
results, I think it is hard to call it a meta-analysis analysis. At least concerning nivolumab
monotherapy, it is the same clinical trial.
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 1 Date: 29 Aug 2024
Reviewer's report:
This manuscript is reporting a meta-analysis of the latest studies testing Nivolumab in advanced
gastric cancer.
This study is gathering trials with Nivolumab monotherapy and Nivolumab combined with
chemotherapy which are different settings, leading to subgroup analyses. These phase III trials
which led to approval and answered the question about the interest of Nivolumab in advanced
gastric cancer. The main interest of the study is to make a focus on Nivolumab monotherapy.
The study is rigorously conducted, and the results are well-presented.
One main limit is that this study includes both Janjigian 2024 and Janjigian 2021. Janjigian 2024,
JCO is the survival update with longer follow-up from Checkmate 649 reported in Janjigian
2021, meaning that those patients are included twice in the present study. Running the analyses
including only Janjigian 2024 and discarding Janjigian 2021 would seem more accurate.
In the Discussion section:
The main result is the strong result of Nivolumab monotherapy as compared with placebo, which,
despite several positive trials,  is not approved in all countries. The applicability of this result
should be further discussed.
Prescription of Nivolumab is linked to biomarkers such as PDL1 expression in Europe. This
should be discussed.
As getting more averse events under treatment than under placebo is an expected results, this
part could be reduced.  Expanding on Nivolumab combined with chemotherapy bringing the
same rates of AEs but more grade III AEs and with a different toxicity profile would bring some
interest.
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 2 Date: 13 Sep 2024
Reviewer:  Kazuo Kobayashi
Reviewer's report:
The manuscript, "Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal
Junction Cancer: A Meta-Analysis of Randomized Controlled Trials," has been revised
thoroughly in response to the reviewer’s comments. The authors have addressed all concerns
appropriately and made significant improvements to the manuscript.
Reviewer Comments Addressed
Clarification of Methodology: The authors have adequately clarified the methodology,
especially regarding the inclusion and exclusion criteria and the rationale behind the study
selection, making the study more transparent.
Improved Discussion: The discussion has been expanded to address specific clinical
recommendations, especially regarding the use of Nivolumab monotherapy versus combination
therapy, as well as the management of adverse events. This has enhanced the clinical relevance
of the findings.
Reduction of Redundancy: The authors have made adjustments to avoid redundancy in the data
analysis by excluding overlapping studies, which strengthens the validity of the meta-analysis.
Overall, the authors have made substantial improvements to the manuscript, and it is now ready
for acceptance.
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 2 Date: 16 Sep 2024
Reviewer's report:
I thank the authors for having taking into accounts my comments about Janjigian 2021 and
Janjigian 2024.
However, thanks to comments from Reviewer 3 , I figured out that the authors also included
redundant analyses for ATTRACTION-2 and ATTRACTION-4 trials. These redundancies are
not adressed in the  revised manuscript as the analyses still includes the redundant data about
those trials.
A subgroup analysis cannot be considered as a different study from the original one.
Therefore, I don't believe this study is bringing more information than ATTRACTION-2 itself.
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 2 Date: 22 Sep 2024
Reviewer:  Toshimitsu Tanaka
Reviewer's report:
The presented manuscript is revised adequately. The exclusion of the same studies reduced bias
as much as possible and improved the quality of the meta-study. Furthermore, the quality of this
study was also ensured by highlighting the study's limitations. Thank you for the revisions to
the points raised.
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 4 Date: 11 Oct 2024
Reviewer's report:
Thanks to the authors for taking into account my concerns about ATTRACTION-02 and
ATTRACTION-04 trials and including the limitations of their study in the discussion section.
For the record, the following meta-analysis which just came out and should be discussed is
taking into account only  ATTRACTION-4 and concludes that anti-PD1/anti-PDL1 efficiency
is not shown in advanced gastric cancer.
Beshr MS, Beshr IA, Al Hayek M, Alfaqaih SM, Abuajamieh M, Basheer E, Wali
AK, Ekreer M, Chenfouh I, Khashan A, Hassan ET, Elnaami SM, Elhadi M. PD-1/
PD-L1 Inhibitors in Combination With Chemo or as Monotherapy vs. Chemotherapy
Alone in Advanced, Unresectable HER2-Negative Gastric, Gastroesophageal Junction, and
Esophageal Adenocarcinoma: A Meta-Analysis. Clin Oncol (R Coll Radiol). 2024 Sep
21:S0936-6555(24)00385-6. doi: 10.1016/j.clon.2024.09.007. Epub ahead of print. PMID:
39384455.
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 4 Date: 14 Oct 2024
Reviewer:  Kazuo Kobayashi
Reviewer's report:
Thank you for your revised submission titled "Efficacy and Safety of Nivolumab in Advanced
Gastric and Gastroesophageal Junction Cancer: A Meta-Analysis of Randomized Controlled
Trials."
Upon reviewing the revised manuscript, I am pleased to inform you that all the comments
and suggestions raised during the initial review have been addressed comprehensively. The
clarification of methodology, expansion of the discussion, and reduction of redundancy have
significantly enhanced the quality of the manuscript. The supplementary data, as well as the
point-by-point responses to the reviewers' concerns, are thorough and well-articulated.
At this point, I do not have any further comments or recommendations for revision, as the
manuscript now meets the necessary standards for publication.
Thank you again for your diligence in addressing the feedback. I look forward to seeing the final
published version.
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 4 Date: 15 Oct 2024
Reviewer:  Toshimitsu Tanaka
Reviewer's report:
I appreciate the authors for their collaboration. Thank you for responding to my comment.
Review for 10.1186/s12876-024-03508-0 (2024)

Title: Efficacy and Safety of Nivolumab in Advanced Gastric and Gastroesophageal Junction
Cancer: A Meta-Analysis of Randomized Controlled Trials
Version: 5 Date: 21 Oct 2024
Reviewer's report:
Thanks to the author who integrated all my remarks, especially the reference [Beshr MS,
et al. Clin Oncol (R Coll Radiol). 2024 Sep21:S0936-6555(24)00385-6. doi: 10.1016/
j.clon.2024.09.007] I suggested and discussed it thoroughly.
The authors nicely highlighted not only the limits of their work but also the important
differences between Asian and non-Asian populations regarding gastric cancers characteristics
and outcome. This way they underlined how the present manuscript complements the latest
publications on this hot topic.
This manuscript is ready for publication.
Review for 10.1186/s12876-024-03483-6 (2024)

Title: The effect of propranolol on gastrointestinal motility and permeability in patients with
cirrhosis and significant portal hypertension
Version: 0 Date: 01 May 2024
Reviewer's report:
Congratulations on your original manuscript on a very interesting and clinically relevant topic.
I have raised several queries which I hope will help add value to your manuscript.
Please have the manuscript reviewed by a native english speaker as there are grammatical and
phrase constructions errors.
Review for 10.1186/s12876-024-03483-6 (2024)

Title: The effect of propranolol on gastrointestinal motility and permeability in patients with
cirrhosis and significant portal hypertension
Version: 0 Date: 05 Jun 2024
Reviewer's report:
It is interesting study that beta blocker can enhance bowel motility and improved the bacterial
overgrowth in cirrhosis patients. In terms of gut mobility, beta-blocker is well studied in previous
reports.
This paper not only describes the hemodynamic changes of beta-blockers but also discusses
the changes in gastrointestinal motility and their implications, making it an interesting topic.
However, it lacks explanatory power to draw conclusive findings, and its results diverge
somewhat from previous studies, yet this deviation adds significance to the topic. It suggests that
this area remains relatively unexplored, indicating the potential for further research and deeper
analysis to enhance understanding.
Review for 10.1186/s12876-024-03483-6 (2024)

Title: The effect of propranolol on gastrointestinal motility and permeability in patients with
cirrhosis and significant portal hypertension
Version: 2 Date: 07 Jul 2024
Reviewer's report:
Thank you for the answer to my queries.
I am however, unhappy with the way patient selection has been explained.
They way you have described it, leaves a lot of room for selection bias!
Please add the reply to query No. 3 to the discussion with respective reference.
Please add the reply to query No. 5 and 6 in the discussion with respective references.
Review for 10.1186/s12876-024-03483-6 (2024)

Title: The effect of propranolol on gastrointestinal motility and permeability in patients with
cirrhosis and significant portal hypertension
Version: 2 Date: 14 Jul 2024
Reviewer's report:
Thank you for addressing most of the issues raised
1. Pertaining to footnote in Table 2, I now understand what the authors meant. The footnote is
still incorrect and it should read "Values for permeabilities are expressed as median and range
in parenthesis".
2. I raised the query on subgroup analysis of OCTT, IP, inflammatory markers and BT, on how
the increase or decrease was defined. Based on the authors' clarification, if one hypothetical
study participant's LPS level was 6.1pg/ml at baseline and 6.0pg/ml after NSBB, the authors
would consider this study participant's LPS to have decreased? My concern is, if this was the
case, then would the minimal 0.1pg/ml decrease clinically relevant or significant? Using an
unrelated example of response to NSBB, if a patient has HVPG 15mmHg at baseline off NSBB
and 14mmHg on NSBB, the patient would have been regarded as having a decrease in HVPG
but this is clinically not significant because response required at least 10% decline rather than
any decline. Please clarify.
3. I may have missed the authors' clarification under Discussion on the contradictory results of
this study with regards to change in LPS and other inflammatory markers compared to reference
27. Could the authors discuss the differences between the results of the 2 studies and suggest
the reasons for the findings (dose of propranolol as the authors had suggested).
4. Thank you for putting forward the hypothesis on how NSBB affects the paracellular pathway.
I was hoping for the authors to include their response into Discussion as it is very pertinent to
findings of the study.
Review for 10.1186/s12876-024-03483-6 (2024)

Title: The effect of propranolol on gastrointestinal motility and permeability in patients with
cirrhosis and significant portal hypertension
Version: 2 Date: 16 Jul 2024
Reviewer's report:
The author revised the manuscript as I recommended and well reply to the reviewer’s point.
There is no other point that required to revise.
Review for 10.1186/s12876-024-03483-6 (2024)

Title: The effect of propranolol on gastrointestinal motility and permeability in patients with
cirrhosis and significant portal hypertension
Version: 3 Date: 07 Aug 2024
Reviewer's report:
Thank you for replying to my queries.
The presentation of patient selection is better but not optimal.
Optimally, a flow chart showing number of patients initially evaluated and those excluded with
reasons for exclusion should have been presented in this manuscript.
Review for 10.1186/s12876-024-03483-6 (2024)

Title: The effect of propranolol on gastrointestinal motility and permeability in patients with
cirrhosis and significant portal hypertension
Version: 3 Date: 21 Aug 2024
Reviewer's report:
Thank you for addressing the issues raised.
With regards to the issue raised on specific cut-off for increase or decrease in OCTT, IP,
inflammatory markers and BT, the authors clarified that no cut-off was used and all patients had
more than 10% change in pre- and post-NSBB values. It then be very helpful for the authors
to state under Methods that no cut-off was used to define increase or decrease. It would also
help the readers of this manuscript if the authors could add range of percentage change in the
pre- and post-NSBB values. That way, the readers can see for themselves the value change was
significant.
Review for 10.1186/s12876-024-03506-2 (2024)

Title: Survival outcomes of population-wide colonoscopy screening: Reanalysis of the NordICC
data
Version: 1 Date: 11 Sep 2024
Reviewer's report:
Dear authors,
The manuscript entitled "Survival outcomes of population-wide colonoscopy screening:
Reanalysis of the NordICC data" re-evaluates the data from a study that has been the topic of
extensive debate.  My concerns are as follows:
- Clarify the rationale behind the use of RMST/RMTL methods over traditional hazard ratios
(HR) and why this approach is crucial given the limitations of the original NordICC study.
Specifically, it should address why these methods are superior in the context of the violated
proportional hazards assumption.
- The discussion should include a more balanced analysis of why colonoscopy may not show
survival benefits, considering other factors such as improvements in treatment options or the
declining incidence of colorectal cancer.
-  Some sections, particularly in the introduction and discussion, need better clarity and flow. For
example, the introduction could more clearly articulate the gap this reanalysis is filling. At the
same time, the discussion could benefit from more detailed explanations of statistical concepts
for readers who may not be familiar with RMST or RMTL.
Kind regards
Review for 10.1186/s12876-024-03506-2 (2024)

Title: Survival outcomes of population-wide colonoscopy screening: Reanalysis of the NordICC
data
Version: 1 Date: 30 Sep 2024
Reviewer's report:
The manuscript entitled “Survival outcomes of population-wide colonoscopy screening:
Reanalysis of the NordICC data” re-analyses the results coming from a really discussed paper
(NordICC trial) reenforcing and confirming a reduced role for screening colonoscopy. The
authors use a different statistical analysis (restricted-mean survival time) to overcome some
described issues posed by hazard ratio. The authors should better specify the rational behind the
use of this tool instead of HRs.
Moreover, a better and comprehensive comment in the discussion section evaluating why
colonoscopy seems not to show those benefits in their study should be added.
In my opinion, the content of this manuscript would be more suitable for an editorial or letter
to the editor.
Review for 10.1186/s12876-024-03493-4 (2024)

Title: Association of serum albumin-to-creatinine ratio with in-hospital mortality in patients
with severe acute pancreatitis: a retrospective study
Version: 2 Date: 13 Aug 2024
Reviewer's report:
I am delighted to review an article entitled " Association of serum albumin-to-creatinine ratio
with in-hospital mortality in patients with severe acute pancreatitis: a retrospective study." This
manuscript is a paper which examined the prognosis of patients with SAP. This paper revealed
that usefulness of serum albumin-to-creatinine ratio with the in-hospital death of SAP. This
manuscript is very interesting. However, author should consider several points.
Major point
We agree that the serum albumin indirectly reflects inflammation and is a useful prognostic
factor for pancreatitis. However, in Table 1, creatinine and sACR were significantly different
in the survivors and non-survivors, while albumin levels were not significantly different. Is
creatinine the greater contributor to in-hospital mortality in SAP patients? The authors performed
ROC analysis only for sACR, we suggest additional ROC analysis for the creatinine with
significant difference. In addition, ROC analysis of the BISAP score, which has already been
shown to be useful, may allow comparison of its usefulness with the sACR.
Minor point
Because SAP is the condition requiring intensive care, the SOFA and APACHE2 score should
also be mentioned in Table 1 and 2.
Review for 10.1186/s12876-024-03493-4 (2024)

Title: Association of serum albumin-to-creatinine ratio with in-hospital mortality in patients
with severe acute pancreatitis: a retrospective study
Version: 2 Date: 20 Aug 2024
Reviewer's report:
I have read with interest this article.
The topic is unique, and the result is quite useful to conform to clinical practice.
Yet, I have some concerns about the process of review.
1. Please mention the other prognostic tool for SAP and compare the effectiveness of prognostic
mortality. AIC is not so high and SAP has various prognostic factors such as sarum Ca level.
As sACR is not specific for SAP, you need to reveal more information of the effectiveness of
sACR in this manuscript.
Review for 10.1186/s12876-024-03493-4 (2024)

Title: Association of serum albumin-to-creatinine ratio with in-hospital mortality in patients
with severe acute pancreatitis: a retrospective study
Version: 3 Date: 08 Sep 2024
Reviewer's report:
Comment 1
Thank you for very important considerations.  Although the study highlights the association
between sACR and in-hospital mortality, parallel considerations of Creatine (multivariate and
ROC analysis) should be added to the main text. Even if the points are added, sACR remains
useful marker. It is necessary to clarify questions that readers may have.
Comment 2
Thank you for your response to the comment.
Review for 10.1186/s12876-024-03493-4 (2024)

Title: Association of serum albumin-to-creatinine ratio with in-hospital mortality in patients
with severe acute pancreatitis: a retrospective study
Version: 4 Date: 05 Oct 2024
Reviewer's report:
I'm grateful for your revising the manuscript. I checked the authors have properly revised the
manuscript.
Review for 10.1186/s12876-024-03493-4 (2024)

Title: Association of serum albumin-to-creatinine ratio with in-hospital mortality in patients
with severe acute pancreatitis: a retrospective study
Version: 4 Date: 15 Oct 2024
Reviewer:  Ting-Chia Chang
Reviewer's report:
Comments to the Author
Dear Editor,
The study investigated the association between serum albumin-to-creatinine ratio (sACR) and
in-hospital mortality in patients with severe acute pancreatitis, presenting several important
findings. Overall, the study is well executed. I have one minor suggestions for improvement.
The data presented in tables should not be rewritten to the results section.
Review for 10.1186/s12876-024-03493-4 (2024)

Title: Association of serum albumin-to-creatinine ratio with in-hospital mortality in patients
with severe acute pancreatitis: a retrospective study
Version: 4 Date: 19 Oct 2024
Reviewer's report:
The authors have answered the revised comments and added appropriate information in the
supplement figure and manuscript. Thus, the revised manuscript is warranted to be accepted.
Review for 10.1186/s12876-024-03493-4 (2024)

Title: Association of serum albumin-to-creatinine ratio with in-hospital mortality in patients
with severe acute pancreatitis: a retrospective study
Version: 5 Date: 03 Nov 2024
Reviewer:  Ting-Chia Chang
Reviewer's report:
The authors responded well, so I have no more comments.
Review for 10.1186/s12876-024-03492-5 (2024)

Title: Endoscopic resection for esophageal granular cell tumors: report of 62 cases
Version: 3 Date: 24 Sep 2024
Reviewer:  Ippei Tanaka
Reviewer's report:
In this study, the clinical manifestations, endoscopic features, pathological features, endoscopic
resection, and prognosis of esophageal granular cell tumors (GCTs) are clarified. It is a well-
organized and insightful paper, but I believe some improvements are necessary.
Major Comments
1. I feel that R1 resections are relatively frequent. What do you think is the reason for this? If
possible, please analyze the risk factors that lead to R1 resection. Does a larger tumor increase
the likelihood of R1 resection, or is it related to the choice of endoscopic treatment technique?
2. Regarding the selection of different treatment methods, the following is mentioned in the
Methods section:
“The treatment strategies depended on the size and the depth of infiltration of the esophageal wall
and also on local expertise. Three superficial lesions originating from the mucosal muscle layer
were resected by snare excision, 52 lesions originating from the mucosal muscle or submucosal
layer were resected by ESD, and seven lesions originating from the muscularis propria layer
were resected by STER.”
Are these findings based on postoperative pathological diagnoses? If so, how were these
diagnoses made preoperatively? Was it through EUS or endoscopic findings? On the other
hand, if these are preoperative findings, how did you diagnose the origin of the tumor? And, in
the end, were the preoperative diagnoses of the tumor origin consistent with the postoperative
pathological diagnoses?
3. Related to the above question, how does the author believe the different treatments (EMR,
ESD, STER) should be selected? Please describe the criteria based on the specific preoperative
findings.
Minor Comments
1. What was the follow-up duration? Please provide the average follow-up period.
2. It is mentioned that there were no complications during and after the endoscopic treatments.
Given that cases with MP invasion required muscle layer dissection, did no perforation occur?
3. On page 3, line 18, "the 1rd" is written. Is this a mistake for "the 1st"?
4. In your study, there were 11 symptomatic cases. Did the patients who reported especially
choking or difficulty swallowing show improvement after treatment?
Review for 10.1186/s12876-024-03492-5 (2024)

Title: Endoscopic resection for esophageal granular cell tumors: report of 62 cases
Version: 3 Date: 25 Sep 2024
Reviewer's report:
Dear Author(s).
This article presents a summary of 63 granular cell tumors of the esophagus.
The description is well written and easy to read for the reader. However, the article does not
contain any new findings compared to previous reports. It is understandable that the number of
cases is limited because this disease is not so commonly encountered in daily practice, but it
would be desirable for the contents to be more distinctive.
Review for 10.1186/s12876-024-03492-5 (2024)

Title: Endoscopic resection for esophageal granular cell tumors: report of 62 cases
Version: 3 Date: 28 Sep 2024
Reviewer's report:
The authors presented “Endoscopic resection for esophageal granular cell tumors: report of
62 cases”. You have done excellent study! However, I have some concerns following below
comments.
Major:
1) What is the accuracy rate of EUS depth? Pathological depth is final depth. Is EUS depth in
accordance with pathological depth?
2) You reported the strategy of endoscopic treatment according to the origin layer of esophageal
GCTs, which depends on EUS depth. Is there any characteristic endoscopic finding according
pathological depth or EUS depth?
Minor:
1) Please check if what you wrote in the Figure Legends section is correct.
Fig.1
(f) Medium echoic occupancy of the mucosal muscle seen by ultrasound endoscopy.
(j) Hypoechoic occupancy of the mucosal muscle seen by ultrasound endoscopy.
Fig.2
(i) EFTR of an esophageal GCT.
Review for 10.1186/s12876-024-03492-5 (2024)

Title: Endoscopic resection for esophageal granular cell tumors: report of 62 cases
Version: 3 Date: 01 Oct 2024
Reviewer's report:
Thank you for the opportunity to review this manuscript.
Your paper presents the clinical and histopathological characteristics of esophageal granular
cell tumors, which are clinically rare lesions. It is noteworthy that endoscopic resection is
demonstrated to be a safe and effective method for both diagnosis and treatment of esophageal
GCTs. Most importantly, this study indicates that a microscopic positive tumor margin may not
necessarily increase the rate of recurrence.
I believe this paper is well-written.
I have only one comment.
Please provide the meaning of the abbreviation 'EFTR' in the Figure Legends.
Review for 10.1186/s12876-024-03492-5 (2024)

Title: Endoscopic resection for esophageal granular cell tumors: report of 62 cases
Version: 4 Date: 21 Oct 2024
Reviewer:  Ippei Tanaka
Reviewer's report:
Thank you for answering my questions in such detail. However, I believe there is one point that
should be revised, so I would like you to consider it.
In the "Intervention" section of the Methods, it is written as follows: "Three superficial
lesions originating from the mucosal muscle layer were resected by snare excision, 52 lesions
originating from the mucosal muscle or submucosal layer were resected by ESD, and seven
lesions originating from the muscularis propria layer were resected by STER." I believe this
sentence should be revised.
The reason is that the origin of the tumor from specific layers is determined by postoperative
pathological results, and it is not a factor that influences the decision-making process for
the intervention method prior to the procedure. The factors that influenced the preoperative
treatment strategy were limited to the findings of conventional endoscopy, EUS and CT.
Therefore, I believe it would be preferable to state, "In cases where EUS suggested the
lesion originated from the mucosal muscle layer, snare excision or ESD was selected, whereas
for esophageal lesions suspected to originate from the muscularis propria layer, submucosal
tunneling endoscopic resection (STER) was chosen."
Review for 10.1186/s12876-024-03492-5 (2024)

Title: Endoscopic resection for esophageal granular cell tumors: report of 62 cases
Version: 4 Date: 21 Oct 2024
Reviewer's report:
1) I knew that the accuracy rate of tumor origin was actually very high for the cases with
preoperative EUS. However, there were some cases without preoperative EUS. You should
describe the accuracy rate of preoperative EUS in the Result section.
2) Preoperative endoscopic findings according to the depth was very interesting. You should it
in the Method section. In addition, you also should describe the accuracy rate of preoperative
endoscopic findings in the Result section.
If you revise as I pointed out, your manuscript will attract more reader.
Review for 10.1186/s12876-024-03492-5 (2024)

Title: Endoscopic resection for esophageal granular cell tumors: report of 62 cases
Version: 4 Date: 27 Oct 2024
Reviewer's report:
The reviewers' comments were carefully answered point by point, and I think this paper is well
written.
I have no questions regarding this paper.
Review for 10.1186/s12876-024-03492-5 (2024)

Title: Endoscopic resection for esophageal granular cell tumors: report of 62 cases
Version: 5 Date: 31 Oct 2024
Reviewer:  Ippei Tanaka
Reviewer's report:
Thank you for your revision.
I have no additional comment, and I think this manuscript is worth acceptance.
Review for 10.1186/s12876-024-03487-2 (2024)

Title: Safety Comparison of Single-Donor and Pooled Fecal Microbiota Transfer Product
Preparation in Ulcerative Colitis: Systematic Review and Meta-Analysis
Version: 2 Date: 29 Jul 2024
Reviewer's report:
Interesting research topic. Some comments.
1.  METHODS -  Search strategy and selection criteria. As stated in this subheading, the the
authors should report the search strategy first in this section and the selection criteria after.
2.  METHODS - It is highly recommended that the literature search is completed within the
last 12 months before submission to ensure the review includes the most up-to-date evidence.
Would suggest updating the search.
3.  METHODS -  Most of the manuscript is a description of the methods. I would suggest
focusing more on results and discussion, which could be improved with more detail, and moving
sections from methods to supplementary materials.
4. RESULTS- Main findings from individual studies. The authors talk about "characteristics of
the 44 eligible studies..."please clarify, there were 44 identified studies, 29 of them excluded
and 15 deemed eligible.
5. RESULTS - Synthesis of results:safety assessment. Given the main goal is to assess safety,
it would be interesting to see what the AEs and SAEs were reported more frequently in these
studies.
6.  RESULTS -  The authors state: "Regarding the 8 studies with available SAE comparison,
results indicate increased risk  (RRs [95% CIs]) of SAE occurrence with both MDN and SDN
versus control, 1.56 ([0.39; 6.25], P=0.533) and 1.77 ([0.90; 3.49], P=0.100), respectively. The
risk of SAE occurrence in MDN and SDN was similar (RR [95% CI]): 0.88 ([0.19; 4.14],
P=0.871)." These results are not statistically significant at the 95% confidence level, for which
you cannot say there is an increased risk of SAE occurrence. Same when the authors say, "MDN
had a higher benefit-risk ratio compared to SDN [95% CI]: 1.18 ([-0.36; 2.72], P=0.133)."
7.  DISCUSSION- As a general comment, most of the discussion is quite vague and based on
mentioning results from other studies and not related to discussing the results from the present
study.
8. CONCLUSION - Based on the reported results, it is not correct to state that MDN has a
positive benefit-risk ratio compared to SDN (see comment above).
Review for 10.1186/s12876-024-03487-2 (2024)

Title: Safety Comparison of Single-Donor and Pooled Fecal Microbiota Transfer Product
Preparation in Ulcerative Colitis: Systematic Review and Meta-Analysis
Version: 2 Date: 01 Aug 2024
Reviewer's report:
This systematic review and meta-analysis by Laperrousaz et al builds on a prior meta-analysis
conducted by the same group in 2023 that evaluated the efficacy of single donor (SDN) and
multi-donor (MDN) strategies of fecal microbiota transplantation (FMT) for patients with
ulcerative colitis (UC).
In the current manuscript, they now assess the safety of SDN and MDN FMT for patients with
UC by evaluating the number of adverse events and severe adverse events encountered by studies
they included. They found similar safety profiles for both strategies, though MDN FMT was
seen to have a greater risk-ratio as compared to SDN FMT.
While this study is thorough and organized, the main concern stems from the variability of how
an adverse event and a serious adverse event is defined in each included study. The authors do
not have their own criteria of defining these events. Moreover, the timeframe in which these
events occur, is also prudent to truly understand the safety profile of these two different FMT
formulations.
The authors have recognized this fact as their limitation. Perhaps they could consider softening
the conclusions and advising a word of caution to the readers into interpreting the results.
Review for 10.1186/s12876-024-03487-2 (2024)

Title: Safety Comparison of Single-Donor and Pooled Fecal Microbiota Transfer Product
Preparation in Ulcerative Colitis: Systematic Review and Meta-Analysis
Version: 3 Date: 22 Sep 2024
Reviewer's report:
The objectives of the study are clear. The rationale to consider differences in AE from MDN
v SDN needs clearer explanation.
The methodology is rigorous and well performed, but the manuscript still focuses too heavily
on methods that could be described in supplementary materials.
The authors need to describe how differences in number and frequencies of MDN or SDN might
affect the outomes analysed rather than MDN or SDN and how this is accounted for in the
analysis.
It is confusing to state "results indicate a non-significantly increased risk"- this would suggest
the risk is not increased.
likewise "a non-significantly higher benefit-risk ratio.." is a confusing term.
It would seem the results show no difference in risk or risk/benefit ratio with MDN.
It would be useful to clarify the timescale of AEs and limitations of follow up durations.
Review for 10.1186/s12876-024-03487-2 (2024)

Title: Safety Comparison of Single-Donor and Pooled Fecal Microbiota Transfer Product
Preparation in Ulcerative Colitis: Systematic Review and Meta-Analysis
Version: 3 Date: 25 Sep 2024
Reviewer's report:
These study builds on earlier research investigating the efficacy of MDN vs SDN FMT strategies
for ulcerative colitis. The authors appear to have addressed the previous reviewer comments
appropriately, hence I won't revisit those.
The paper's results focus more broadly on overall AE and SAE rates for SDN vs MDN. As
has been mentioned previously, more granular analysis of the rates of individual AEs or SAEs
would be more informative. If the included studies do not uniformly stratify the overall AE/SAE
rates into individual AE/SAEs then this analysis will be difficult to perform. Having noted this
weakness, I would accept the manuscript in its current form.
Review for 10.1186/s12876-024-03487-2 (2024)

Title: Safety Comparison of Single-Donor and Pooled Fecal Microbiota Transfer Product
Preparation in Ulcerative Colitis: Systematic Review and Meta-Analysis
Version: 4 Date: 25 Oct 2024
Reviewer's report:
I am satisfied that the authors have adequately addressed the feedback from previous reviewers,
with one requested amendment. The abstract states that there is a lower risk of safety events
for MDN vs SDN but the p value not significant. This has been amended in the body of the
text on the advice of a previous reviewer but this assertion remains in the abstract and should
be corrected.
Review for 10.1186/s12876-024-03490-7 (2024)

Title: Prognostic Impact of a 3-week Multimodal Prehabilitation Program on Frail Elderly
Patients Undergoing Elective Gastric Cancer Surgery:  A Randomized Trial
Version: 2 Date: 14 Aug 2024
Reviewer's report:
I was asked to review a manuscript entitled: "Prognostic Impact of a 3-week Multimodal
Prehabilitation Program on Frail Elderly Patients Undergoing Elective Gastric Cancer Surgery:
A Randomized Trial". In this trial the authors assess the impact of a 3 week prehabilitation
intervention on postoperative complications, 6mwt and other secondary outcomes. The results of
the study go in line with different prehabilitation studies published where we see a trend towards
decreased overall complications, with a major significant decrease in medical complications
(especially cardio-respiratory complications). The authors also conclude that prehab patients
return to baseline functional capacity faster than the control group, a finding also in line
with other prehabilitation publications. The authors should be congratulated on the initiative,
especially  considering the lack of funding for the study.  Here are a few points that, in my
opinion, should be addressed.
- Introduction, Page 5, the sentence !Nonetheless, definitive evidence on multimodal
rehabilitation specifically tailored to this vulnerable population is lacking." I believe the sentence
should read prehabiliation and not rehabilitation.
- Methodology section: the intervention needs to be more detailed. Please specify if it was home-
based program or if it was performed in a community based facility or in the hospital. Also
specify if patients were supervised during their exercises and what kind of supervision they were
subjected to (sports medicine, kinesiology, physiotherapy, ...?).
- On the same page, the sentence. "A designated physical therapist supervises the resistance
exercises and offers corrective guidance" should be written in past tense, like the rest of the
paragraph.
- What do authors refer to when they say "Respiratory training"? Is it inspiratory muscle training
or is it an incentive inspirometry? Please detail this intervention.
- Nutrition: was any screening or assessment tool for malnutrition used?
- Adherence or fidelity to the intervention is not specified anywhere in the manuscript, but in the
discussion the authors explain that the non-compliant patients were excluded. Could you clarify
this? if data for adherence or fidelity to each component is available, it would be interesting to
show it, since most prehabilitation interventions in the eldery systematically have difficulties
due to compliance to HIIT.
- Linked to the previous comment: was the analysis performed as an intention to treat or as a
per protocol analysis? Please specify.
Review for 10.1186/s12876-024-03490-7 (2024)

Title: Prognostic Impact of a 3-week Multimodal Prehabilitation Program on Frail Elderly
Patients Undergoing Elective Gastric Cancer Surgery:  A Randomized Trial
Version: 2 Date: 26 Aug 2024
Reviewer's report:
Dear authors,
Thank you for the interesting work. I have provided my comments within the document.
Thank you.
Review for 10.1186/s12876-024-03490-7 (2024)

Title: Prognostic Impact of a 3-week Multimodal Prehabilitation Program on Frail Elderly
Patients Undergoing Elective Gastric Cancer Surgery:  A Randomized Trial
Version: 3 Date: 08 Sep 2024
Reviewer's report:
All points have been addressed correctly.
Review for 10.1186/s12876-024-03490-7 (2024)

Title: Prognostic Impact of a 3-week Multimodal Prehabilitation Program on Frail Elderly
Patients Undergoing Elective Gastric Cancer Surgery:  A Randomized Trial
Version: 4 Date: 23 Oct 2024
Reviewer's report:
The authors have done a good job revising their manuscript. In their revision, they have changed
the co-primary outcomes to make postoperative outcomes the sole primary outcome. However,
this is not consistent with the trial registration. I suggest the authors clarify that this is a post-
hoc decision to ensure transparency about the deviation from the registration. Alternatively,
they could maintain the co-primary outcomes but make it clear in the statistics section that no
correction for multiple testing has been performed
Review for 10.1186/s12876-024-03490-7 (2024)

Title: Prognostic Impact of a 3-week Multimodal Prehabilitation Program on Frail Elderly
Patients Undergoing Elective Gastric Cancer Surgery:  A Randomized Trial
Version: 5 Date: 28 Oct 2024
Reviewer's report:
The authors have done a proper job revising their manuscript.
Review for 10.1186/s12876-024-03491-6 (2024)

Title: Celiac disease autoimmunity among Nigerian children and adolescents with type 1
diabetes mellitus
Version: 2 Date: 14 May 2024
Reviewer's report:
General Comments:
This manuscript titled "Celiac disease among Nigerian children and adolescents with type 1
diabetes mellitus" presents a valuable contribution to the field by investigating the prevalence
of Celiac Disease (CD) in a population where little data currently exists. The topic is significant
and the findings could have important implications for the management of children with Type
1 Diabetes Mellitus (T1DM) in Nigeria and similar regions.
Specific Comments:
1. Introduction:
The introduction clearly outlines the rationale for the study and provides a good background.
However, it could benefit from a brief discussion on the potential biological mechanisms linking
T1DM and CD.
2. Methods:
The study design is appropriate for the objectives. However, the manuscript would benefit
from more detailed descriptions of the diagnostic criteria used for CD, especially regarding the
thresholds for the antibody tests.
Please clarify the method used for selecting the seven tertiary health facilities involved in the
study. Was there a specific reason for choosing these facilities?
3. Results:
The results are well-presented, but there are areas where additional statistical details could be
beneficial. For example, the manuscript reports p-values but does not always provide confidence
intervals or effect sizes, which could help in understanding the clinical significance of the
findings.
Table 2 and Table 3 could be more clearly formatted to enhance readability and quick reference.
4. Discussion:
The discussion provides a good synthesis of the findings in relation to the existing literature.
However, it would be strengthened by addressing potential limitations more comprehensively,
such as the potential bias introduced by the hospital-based study design.
Consider discussing the implications of these findings for pediatric practice in Nigeria and
similar settings.
5. Conclusion:
The conclusions are well-supported by the data but consider adding recommendations for future
research or policy changes based on the study's findings.
6. Ethical Considerations:
The manuscript notes ethical approval and consent procedures, which is commendable. Ensure
that these are sufficiently detailed to meet international guidelines, as this enhances the
credibility and replicability of the study.
7. Language and Presentation:
The manuscript is generally well-written. Minor grammatical and typographical errors should
be corrected to improve readability. For instance, consider a thorough proofread to correct any
spelling inconsistencies.
Recommendation:
I recommend this manuscript for acceptance after minor revisions, as suggested. The study adds
valuable information to the field and could significantly impact clinical practices in managing
children with T1DM.
Review for 10.1186/s12876-024-03491-6 (2024)

Title: Celiac disease autoimmunity among Nigerian children and adolescents with type 1
diabetes mellitus
Version: 2 Date: 22 May 2024
Reviewer:  Glauce Hiromi Yonamine
Reviewer's report:
General comments:
The study is interesting because it is multicentric and aims to estimate the prevalence of celiac
disease in children and adolescents with type 1 diabetes. However, there are doubts regarding
the methods, that should be clarified.
Introduction:
Please review the English: Downs syndrome, Turner's syndrome, and Williams syndrome.
Some reference citations are incorrect, for example: [1].1
I this sentence: “In Nigeria, where bread, a gluten-rich diet...." Should you use, “a gluten-rich
food?”
Methods:
Is the term “proforma” correct?
The information: “Endoscopy and duodenal biopsy were performed on participants with celiac
antibodies.” Not all children had endoscopy. I suggest changing the text.
“Participants' nutritional status was determined using BMI-for-age and interpreted using WHO
Child Growth Standards [17].”
As there were children under 5 years old, it is necessary to include the reference for the
classification of these age group.
“Families were assigned a socio-economic class based on parents' occupations and education,
with mean scores falling within the 1-5 range. Those with 1 and 2 scores were upper class, while
those with 3, 4, and 5 scores were lower class [18].”
Does this instrument only classify into upper and lower class? Is there no middle class?
What about the diet of the participants? Were they consuming gluten regularly? This is an
important information for diagnosis.
Was it assessed whether the variables had parametric and non-parametric distribution?
If the variables were non-parametric, it should be described as median and interquartile range.
Results:
As stated in the methods section: “The study was carried out at seven tertiary hospitals in Nigeria
that have pediatric endocrinologists and access to children with type 1 diabetes mellitus.” In
the results section, I recommend excluding adults from the sample, focusing solely on children
and adolescents.
Table 2: Is the title correct? I think it is confusing. Were all the 10 participants considered with
low serum total IgA? They have serum IgA within laboratory reference values.
Conclusion:
I think the conclusion could address the importance of having surveillance for celiac disease
in children and adolescents with type 1 diabetes, especially in female and when there are
gastrointestinal symptoms.