JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-024-03443-0 (2024)

Title: The early biomarker of immature granulocyte count in predicting right-side colonic
complicated acute diverticulitis: A retrospective cohort study
Version: 2 Date: 05 Sep 2024
Reviewer's report:
First of all, I would like to commend the authors for their efforts to investigate immature
granulocyte (IG) count as a potential diagnostic tool for predicting complications in right-sided
diverticulitis. The search for novel biomarkers that can enhance diagnostic accuracy and aid
clinical decision-making is of great importance in the medical field. This study represents a
valuable attempt to contribute to this critical area.
1. Major Points
1.1 Lack of Novelty and Clinical Significance
This study presents immature granulocyte (IG) count as a predictor for complications (cAD) in
right-sided diverticulitis. However, the study faces significant issues regarding both its novelty
and clinical significance. The use of IG count as a diagnostic marker for severe infections is
already well-established, and the study does not clearly articulate what new insights it offers
by focusing specifically on right-sided diverticulitis. Additionally, while the study proposes IG
count as an alternative to CT scans, the potential clinical impact of this approach is inadequately
discussed. The paper does not sufficiently explain how IG count influences clinical decision-
making, such as its role in guiding antibiotic use or early surgical intervention. A more detailed
discussion on the practical applications of IG count in clinical settings, including its specific
impact on patient outcomes, is necessary to emphasize its relevance in medical practice.
Furthermore, the study mentions the utility of IG count in children and pregnant women, but
these groups are either excluded from the study or not clearly identified (e.g., no mention of
pregnancy status). As a result, these claims lack solid grounding, and the overall clinical value of
using IG count as a substitute or complement to CT remains unclear. The discussion also contains
inconsistencies, further complicating the ability of readers to fully understand and accept the
study's conclusions.
2. Minor Points
2.1 Small Sample Size in the cAD Group
With only 31 patients in the complicated acute diverticulitis (cAD) group, there may be a lack of
statistical power, increasing the risk of overfitting in regression analyses. This could affect the
reliability of the results, and this limitation should be carefully considered in the interpretation
of the study's findings.
2.2 Lack of Univariate Analysis Results in Tables
Although both univariable and multivariable logistic regression analyses were conducted, the
provided tables do not clearly distinguish between the results of these analyses. Including
univariate analysis results explicitly would make the interpretation of the findings easier and
more transparent.
Review for 10.1186/s12876-024-03443-0 (2024)

Title: The early biomarker of immature granulocyte count in predicting right-side colonic
complicated acute diverticulitis: A retrospective cohort study
Version: 3 Date: 20 Sep 2024
Reviewer's report:
The authors replied well to my comments. I think this manuscript adds  to the general knowledge
about lab markers and rt sided diverticulitis
Review for 10.1186/s12876-024-03437-y (2024)

Title: Construction and Validation of a Predictive Model for the Return to Work of Patients
with Permanent Colorectal Stoma: a cross-sectional study
Version: 1 Date: 18 Jul 2024
Reviewer:  Chun Hin Angus Lee
Reviewer's report:
Thank you for the opportunity for me to review this article which proposed a predictive model
incorporating two validated scores (ostomy acceptance and psychosocial adaptation) for return
to work after having colorectal surgery with permanent ostomy in China.
Comments:
1. Selection criteria for colorectal cancer in terms of type and stage were not clear in methodoloy .
For clarify I would suggest to include colon vs rectum; distance from anal verge in rectal cancer;
use of neoadjuvant therapy should be included
2. Household income : in Chinese currency I assume?
3. Complementary therapy:  is this alternative medicine or adjuvant therapy for cancer?
4. Definition for stomal complications should be included in methodology
5. Definition of nature of work should be included. Is it based on previous study?
6. Can author explain why there was such high rate of permanent stoma despite most people
had early stage colorectal cancer?  How many of those were low recall cancer involving anal
sphincter ? How many were permanent ileostomy ?
7. Definition of return to work : does it imply return to pre-existing occupation ? how about
transiting to new occupation  ?
Minor:
1. There were several punctuation errors: extra space after hyphenation; no space after semicolon
etc.
Please spell check
Overall I found this study quite interesting. I applauded the authors’ effort in identity factors that
have impacting on social aspect of patients with permanent stoma which is often overlooked.
Due to patients demographic, the validated tool may not be applicable in other countries.
Review for 10.1186/s12876-024-03437-y (2024)

Title: Construction and Validation of a Predictive Model for the Return to Work of Patients
with Permanent Colorectal Stoma: a cross-sectional study
Version: 1 Date: 06 Aug 2024
Reviewer's report:
In this manuscript, the authors constructed a model to predict the return to work in patients with
permanent colorectal stoma. I have some comments and concerns about the results of this study.
1. The authors should clarify the definition of “return to work”. If a patient returned to work
after 2 years from surgery, is this patient a candidate? Or what if the patient returned to work,
but in a different job?
2. The authors should provide the results of the univariate analysis for variables in Table 2. Also,
Table 3 is not a general style to show the results of multivariable analysis.
3. I think adjuvant therapy and recurrence also influence the rate of return to work. Why were
these factors not analyzed?
4. The rate of return to work was very low in this study. The authors should focus on this point
because this is a crucial problem. The support of companies and society plays an important role
in this. Please investigate these factors.
5. Finally, this study needs a validation cohort.
Review for 10.1186/s12876-024-03437-y (2024)

Title: Construction and Validation of a Predictive Model for the Return to Work of Patients
with Permanent Colorectal Stoma: a cross-sectional study
Version: 2 Date: 27 Aug 2024
Reviewer's report:
Thank you for this fine written manuscript. I really appreciate your choice of the statistical tests.
I have some questions in the Methods:
Is the sample non normal distributed? In such case why you didn’t use wilcoxon log rank for
categorical variables?
I suggest moving the tables from the methods section  to results section.
Results section:
I appreciate your efforts to summarise the most important results. However, it is better to avoid
repeating and focus only on statistically significant results.
Some results are kind of expected such as delays to return to work for patient with complications
after stoma surgery.
If you may clarify tables 1 and 3 captions and where multivariate analysis was used.
Discussion section:
This section takes into consideration the Chinese culture and reports clearly the implications
of this study. However, it is advisable to minimise repetition of the results and to keep the
assumption based on statistically significant results.
Limitations of the study: I would suggest to add more about selection bias.
General notes: English language revision is advisable.
Review for 10.1186/s12876-024-03437-y (2024)

Title: Construction and Validation of a Predictive Model for the Return to Work of Patients
with Permanent Colorectal Stoma: a cross-sectional study
Version: 2 Date: 30 Aug 2024
Reviewer's report:
The authors addressed my comments. I have one additional comment about the Tables.
Please combine Tables 1 and 3, deleting columns of statistical value, B, SE, Wald, and df. I
recommend the authors to refer tables in clinical research papers.
Review for 10.1186/s12876-024-03437-y (2024)

Title: Construction and Validation of a Predictive Model for the Return to Work of Patients
with Permanent Colorectal Stoma: a cross-sectional study
Version: 3 Date: 16 Sep 2024
Reviewer:  Chun Hin Angus Lee
Reviewer's report:
The authors have addressed reviewers' comments adequately. I have no further comment.
Review for 10.1186/s12876-024-03437-y (2024)

Title: Construction and Validation of a Predictive Model for the Return to Work of Patients
with Permanent Colorectal Stoma: a cross-sectional study
Version: 4 Date: 26 Sep 2024
Reviewer's report:
The statistical methods were corrected  perfectly. I recommend the publication for the revised
manuscript.
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 3 Date: 12 Jul 2024
Reviewer:  Islam H. Shawali
Reviewer's report:
Dear authors, I have read your paper with great interest.
In my opinion,  the study addresses an important patients group with a good approach to improve
prognostic predictions.
However it is difficult to understand how the DEB-TACE applied pre-transplanatation  can be
referred as an effective and safe option for HCC wihtout considering the PVTT and child pugh.
Are other types of LRT applicable in such group of patients and if not you should have refereed
to the edge  that DEB-TACE has in such cases
Inclusion and exclusion criteria have to be more clear.
There is no enough data concerning if the differentiation of the tumor affected the results.
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 3 Date: 12 Jul 2024
Reviewer:  A. H. Kamel Abdelmaksoud
Reviewer's report:
Authors analyzed retrospectively 40 patients with different stages of HCC who underwent DEB-
TACE before liver transplantation (beyond Hangzhou  criteria) regarding demographics, disease
characteristics, treatment response, and adverse events.
The article is well written, yet I have some points to ask about:
1. According to results I don’t think all patients are “beyond Hangzhou  criteria” as the title
indicates because there are 50% of patients less than 8cm, 67.5% with AFP less than 400ng/mL
and 29% are well differentiated tumors. (Table 1)
2. Authors didn’t mention they performed biopsies to know the tumor differentiation.
3. Authors also stated the transplanted 22 (55%) of patients who had portal invasion at a time,
yes not all PV cases has distant metastasis but it’s a very crucial point to make sure its absence,
so authors should mention if they performed an imaging before transplant to verify no metastasis
occur before transplantation.
4. Timing after the BED-TACE session and transplant should be also mentioned and if there
was an intended delay in patients with PV thrombosis
I think the article has a main weakness that it analyzes a very wide disease nature with very
small sample size, this make the results data very shallow and can’t provide a solid strong
recommendation.
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 3 Date: 14 Jul 2024
Reviewer:  Mohamed Hashim
Reviewer's report:
There are some limitations that are acknowledged by the authors.  Small sample size,
retrospective nature of the study, lack of control group.
In the method section: Aetiology of liver disease should be mentioned and its relation to survival.
Milan and Hangzhou criteria should be explained.
What is about other factors affecting survival post transplant such as type of
immunosuppression, .........
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 3 Date: 14 Jul 2024
Reviewer's report:
Although the title sounds interesting, the sample size is small and the results are not novel enough
and even worse to standardize or generalize such an idea
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 3 Date: 16 Jul 2024
Reviewer's report:
1- Title:  It is better to be modified.
2- Abstract: It is better to write the full word before the abbreviation ( ??? AE , ??? MAV).
3- Introduction: Needs English editing.
4- Methods:
# It is better to perform flow chart for all of the patients during the study period and to illustrate
the inclusion and the exclusion criteria.
# It is better to add BCLC classification for all of the patients.
# The duration between chemoembolization and liver transplantation should be mentioned in
this section , not in the results section.
# The authors mentioned the baseline characters before the procedures , What about the
characters of the patients after the procedure ( any changes occurred as regard child score , portal
vein thrombosis , performance status).
# How can you consider Liver transplantation for those patients with progressive disease after
TACE?
5- Discussion:
# It is better to be modified.
# Limitations of the study : Retrospective , short term of follow up.
6- References:
More recent references better to be added.
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 4 Date: 12 Aug 2024
Reviewer:  Islam H. Shawali
Reviewer's report:
No specific comments
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 4 Date: 14 Aug 2024
Reviewer:  Refaat Kamel
Reviewer's report:
it is accepted but as you mention the only problem is that it is a retrospective analysis with a
rather small number
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 4 Date: 15 Aug 2024
Reviewer:  Gustavo Nari
Reviewer's report:
Dear authors, I have read the paper with great interest, the previous reviewers have made
excellent contributions and I note that they have included them in the paper. I consider that
the weaknesses of the study and as mentioned are the low number of cases and that it is a
retrospective study. In any case, the authors state that they are preparing multicenter studies in
this sense.
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 4 Date: 16 Aug 2024
Reviewer:  Mohamed Hashim
Reviewer's report:
The authors responded to reviewers comments.
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 4 Date: 19 Aug 2024
Reviewer:  A. H. Kamel Abdelmaksoud
Reviewer's report:
thanks for your response yet just adding you did CT / MRI is not enough to make sure there
is no distant mets specially you worked on patients with vascular invasion, usually we do PET
CT or chest CT + bone scan
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 4 Date: 19 Aug 2024
Reviewer's report:
Despite the small sample size, the authors observed interesting data but still the conclusion is
too short and subjective (kindly revise)
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 4 Date: 23 Aug 2024
Reviewer:  Ehab Elmongui
Reviewer's report:
Dear Authors,
I would like to commend you on your research efforts and excellent presentation of the results.
I acknowledge the difficulties you might encounter in recruiting sufficient sample size and that
you said it is a preliminary study that needs to be reproduced in a RCT with larger sample size.
The sample size of the current study is underpowered to detect medium effect sizes for the
included covariates. The table in the attached file presents the relationship between the event
rate in the reference group, the hazard ratio (HR) equivalent to a medium effect size, and
the minimum required sample size for a univariate Cox proportional hazard regression model
1. The minimum required sample sizes here were calculated for different event rates in the
reference category for any binary covariate assuming no correlation with other covariates using
the ‘ssizeEpi.default’ function from the ‘powerSurvEpi’ package in R 2. The parameters used
were the postulated hazard ratios equivalent to a medium effect size (theta) , a square of the
correlation between the covariate of interest and another covariate (rho²) of 0, a proportion of the
population in the reference category for any covariate (p) of 0.5, an event rate in the reference
group (psi), and a desired power of 0.8.
Ehab Elmongui, BPharmSc, PharmD, MSc, PhD (c)
Biostatistician
Review for 10.1186/s12876-024-03434-1 (2024)

Title: Is DEB-TACE  as  locoregional  therapy  before  liver  transplantation  for  hepatocellular
  carcinoma effective?
Version: 5 Date: 15 Sep 2024
Reviewer:  Mohamed Hashim
Reviewer's report:
The authors responded to reviewer comments and acknowledged the limitations  of the study
Review for 10.1186/s12876-024-03417-2 (2024)

Title: Prognostic Implications of CK19 Positivity in Patients with Early
Recurrent Hepatocellular Carcinoma after Hepatic Resection Undergoing Transarterial
Chemoembolization
Version: 1 Date: 05 Feb 2024
Reviewer's report:
In the manuscript entitled “Prognostic Implications of CK19 Positivity in Patients
with Early Recurrent Hepatocellular Carcinoma after Hepatic Resection Undergoing
Transarterial Chemoembolization”, the authors examined the survival outcomes of transarterial
chemoembolization (TACE) between patients with early recurrent hepatocellular carcinoma
(rHCC) after hepatic resection, stratified by cytokeratin (CK) 19 expression.
They concluded that in patients with early rHCC after hepatic resection, those with CK19-
positive expression had poorer survival outcomes following TACE compared to CK19-negative
patients. They also suggested the need for additional therapies to improve survival in CK19-
positive individuals. The result of this study was very interesting and informative, but there are
several concerns about this study.
[Major comments]
1. The major concern of this study was that this study is the retrospective study conducted by
single institution and the number of cases is 62 patients and it was too small to state the definitive
conclusion.
2. The surgical procedure and tumor information of initial resection for HCC were unclear.
These information could influence the patients’ prognosis.
3. The radiological imaging follow-up was unclear. The modalities of follow-up could influence
the tumor recurrence. Moreover, the cause of death of the enrolled patients was unclear. The
information of death, cancer-related or not, was important.
4. In Table 2, the univariate and multivariate analysis using a Cox model was conducted. In
univariate analysis, the factor of CK19 was not significant. Why did the authors apply the factor
of CK19 into the multivariate analysis?
5. The author stated that TACE may be more effective in rHCC patients with CK19-negative
expression. However, in order to state this hypothesis, the comparison of the survival outcomes
between rHCC patients who did not undergo TACE and who underwent TACE stratified by
CK19 expression would be necessary.
Review for 10.1186/s12876-024-03417-2 (2024)

Title: Prognostic Implications of CK19 Positivity in Patients with Early
Recurrent Hepatocellular Carcinoma after Hepatic Resection Undergoing Transarterial
Chemoembolization
Version: 1 Date: 30 Mar 2024
Reviewer:  Tsuyoshi Kobayashi
Reviewer's report:
1) There have been many previous reports of CK19 being a poor prognostic factor for HCC.
Although this analysis is limited to cases of early intrahepatic recurrence after HCC resection
and TACE, it is not surprising that CK19 positivity is a poor prognostic factor for HCC.
2) TACE unsuitability should be discussed.
3) DPHCC is not a generally accepted concept and seems abrupt. It is not logical that it is used
in the subgroup analysis of this study and that it is a negative result.
Review for 10.1186/s12876-024-03417-2 (2024)

Title: Prognostic Implications of CK19 Positivity in Patients with Early
Recurrent Hepatocellular Carcinoma after Hepatic Resection Undergoing Transarterial
Chemoembolization
Version: 1 Date: 03 Apr 2024
Reviewer's report:
Review of the manuscript entitled “Prognostic Implications of CK19 Positivity in Patients with
Early Recurrent Hepatocellular Carcinoma after Hepatic Resection Undergoing Transarterial
Chemoembolization”
It has been reported that CK19-high expressing hepatocellular carcinoma has a poor prognosis.
The author reports on CK19 expression and prognosis after TACE treatment in early recurrence.
The authors state that they are investigating the expression of CK19 and the therapeutic effect
of TACE, but since there is no description of the type of recurrence, I believe that they are
merely showing the relationship between CK19 expression and the prognosis of hepatocellular
carcinoma.
1. Please describe the reason for setting the cutoff for CK19 at 5%.
2.Please create a histogram of CK19 using figure.
3. Surgical specimens are stained for CK19, and although it has been reported that CK19 is
associated with prognosis, why was CK19 not associated with the period until postoperative
recurrence?
4. The authors indicate PFS, but does PFS only mean recurrence in the TACE treatment area? If
extrahepatic and intrahepatic recurrence in areas other than the treated area is included in PFS,
it may not be a result of the relationship between CK19 and TACE treatment effects, but rather
a relationship between CK19 and prognosis. The recurrence format should also be stated.
Review for 10.1186/s12876-024-03417-2 (2024)

Title: Prognostic Implications of CK19 Positivity in Patients with Early
Recurrent Hepatocellular Carcinoma after Hepatic Resection Undergoing Transarterial
Chemoembolization
Version: 5 Date: 01 Jun 2024
Reviewer's report:
The authors well revised the manuscript in the re-submitted paper. There will be no problem to
be accepted in BMC Gastroenterology.
Review for 10.1186/s12876-024-03415-4 (2024)

Title: The Reflux Symptom Score has good screening value for Laryngopharyngeal Reflux
Version: 1 Date: 04 Jul 2024
Reviewer's report:
I congratulate the authors for the quality of their work.
The aims of the study are well stated.
The limitations of the study are honestly exposed.
The more positive morning saliva test result is correlated with literature data.
I don't have any particular observation.
The article can be published without restriction
Review for 10.1186/s12876-024-03415-4 (2024)

Title: The Reflux Symptom Score has good screening value for Laryngopharyngeal Reflux
Version: 1 Date: 05 Jul 2024
Reviewer's report:
Exciting work. The greatest value of this work is in the repeated detection of pepsin during the
day.
I would like to see more comments on this in the discussion to explain why the most positive
tests are in the morning and early evening. Should this mean patients should be advised to collect
saliva only in the morning?
Limiting factors are well explained, the work would certainly have much more value if a
questionnaire about eating habits was also used in the research, so we would have much more
data to analyze and comment on.
Review for 10.1186/s12876-024-03415-4 (2024)

Title: The Reflux Symptom Score has good screening value for Laryngopharyngeal Reflux
Version: 1 Date: 07 Jul 2024
Reviewer's report:
This article compared RSS and salivary pepsin of LPR patients, investigated the consistency
of RSS and its screening value in diagnosing LPR.   The topic made sense in applying RSS in
China LPR patients, as RSI and RFS have their limitations, pH monitoring cannot be widely
used because the fee, uncomfortable, invasiveness etc. So  I  suppose this article to be published.
But I have several questions and opinions:
1. In the inclusion criteria, the patients had long-term LPR symptoms, so how long did they have
them? Is there a criteria in the case history?
2. In the exclusion criteria, were the  patients included, if they had surgery, trauma, acupuncture
recently?
3. The article said all patients had electronic laryngoscope  examination, then what were the
results and how were their RFS?
4. As all patients had RSS, how their RSI, as RSS included all RSI items?
5. As the salivary pepsin series were performed by patients themselves, how the consistency  of
the procedure was kept, as this can directly affect the results?
Review for 10.1186/s12876-024-03415-4 (2024)

Title: The Reflux Symptom Score has good screening value for Laryngopharyngeal Reflux
Version: 1 Date: 08 Jul 2024
Reviewer's report:
Thank you for the opportunity to review this well-written article. The authors sought to explore
the agreement between RSS and Pepsin test, and to investigate the screening value of the RSS for
LPR by receiver operating characteristic (ROC) analysis using Pepsin test as diagnostic standard.
However, there are some issues that need further addressed by the authors:
1. The salivary pepsin test is generally accepted to be a first-line screening test (doi: 10.1016/
j.bjorl.2022.10.050.). A positive pepsin test can be regarded as direct evidence of the presence
of reflux to the larynx. But referring it as diagnosis for LPR seems to be somewhat overreaching.
As mentioned as a limitation, I think the authors could elaborate more on the pros and cons of
24-h MII-pH monitoring and the reasoning why it is not incorporated in the current study. Also,
the authors might reflect on the title “The Reflux Symptom Score has good screening value for
Laryngopharyngeal Reflux”. Again, it seems overreaching. I do believe the idea of concurrent
with a structured questionnaire and Pepsin test for better screening /diagnostic accuracy. And
it is interesting and of importance that these two screening tools with different aspect had good
agreement. But using Pepsin test as gold standard may not be optimal.
2. Although it had been shown that a single detection of salivary pepsin in the morning is more
economical, the sensitivity is too low, and it is necessary to detect it multiple times a day.
As explained in the Method section: All subjects underwent multiple time-point saliva pepsin
detection within a single day (the first sample was collected in the morning before brushing teeth
and eating, followed by hourly collections starting at 8 a.m. until 6 p.m., totaling 12 times), and
saliva sample collection was conducted in the hospital. Were the participant in-hospital patient or
recruited from out-patient clinic? Did the participant report to the hospital hourly for performing/
submitting the test? The process is confusing and undermine the applicability of generalizing
the results. Also, study had showed that when the number of tests were further increased beyond
combining with the waking, 1 and 2 h after breakfast and lunch, and 1 h after dinner tests, the
diagnostic value did not improve significantly.( doi: 10.1002/lary.30408.)
3. Was Salivary pepsin detected on the day of RSS?
4. For inclusion, the definition of ”longterm” should be further delineated.
Review for 10.1186/s12876-024-03415-4 (2024)

Title: The Reflux Symptom Score has good screening value for Laryngopharyngeal Reflux
Version: 2 Date: 28 Jul 2024
Reviewer's report:
In this article, the author had written all patients had electronic laryngoscope examination,
but there were nothing related in the results, so what is the meaning and significance of this
examination in this study?
Review for 10.1186/s12876-024-03415-4 (2024)

Title: The Reflux Symptom Score has good screening value for Laryngopharyngeal Reflux
Version: 2 Date: 15 Aug 2024
Reviewer's report:
I would like to congratulate the authors for this study which is well structured and written, of
course about a very common presentation especially for ENT.
Abstract: Please add type of the study in the methods.
Introduction: Well written and informative.
Methods: Again the authors need to mention the type of the study and the sampling method used
for sample size calculation. I guess in a study related to LPR, risk factors like smoking, alcohol
consumption and spicy food should have been mentioned in the exclusion criteria although
I understand these risk factors would be there for both methods of assessment but I would
personally exclude them at least excessive smoking and alcohol.
Results: Well structured and clear. Please mention the relation of the LPR and obesity.
Discussion: The first paragraph till the objective of this study is repeated as it has been mentioned
in the introduction. The authors should start straight away with the objective of the study.
Conclusion: well written.
Again,  your efforts in the study are obvious. Please address these comments.
Review for 10.1186/s12876-024-03415-4 (2024)

Title: The Reflux Symptom Score has good screening value for Laryngopharyngeal Reflux
Version: 2 Date: 25 Aug 2024
Reviewer's report:
Dear editors,
Thank you for inviting me to review this interesting report correlating results of multi-temporal
salivary pepsin assay with the reflux symptom scale. The authors have made appropriate
modifications in response to the prior reviewers’ recommendations. The authors adequately
acknowledge the limitations of their study design and contextualize the findings. I do have
several minor points to address.
Page 3, line 41: use of etc. is inappropriate.
Page 3, line 50: MII-pH testing does not use visual documentation of reflux
Page 4, line 64: it is not appropriate or correct to say RSS is scored in a more scientific manner
Page 6, line 111: “occurred every day in the” is repeated unnecessarily
Page 7-10: The discussion section should be better referenced. I generally agree with the
assertions made throughout much of the discussion, but many are unsupported by references to
the literature. There is ample prior work to reference with respect to timing of salivary pepsin
analysis, for example, but none are cited by the authors.
Page 10, line 204: I am not clear on what the authors mean by “multisite” pepsin test.
Page 10, line 207: I am not clear on why the sample size is considered a major limitation,
as the study showed a significant finding and clear predictive value between RSS and pepsin
positivity. Perhaps it would be more accurate to say that the population studied was not diverse
(e.g. included very few women)?
Page 10, line 207-212: the authors mix punctuation between different “bullet points” (semi-
colons and full-stops). It would be preferable to pick one or the other, and may be easier to
follow if the numerals were eliminated or followed by a close parenthesis instead of a full-stop.
Table 2: The authors report the RSI, an earlier, well-validated alternative to the newer RSS which
is falling out of favor based on data supporting the RSS's superiority for screening for LPR as
confirmed by MII-pH. Prior work has demonstrated a correlation of the RSI to salivary pepsin.
The authors should perform a similar analysis of the RSI’s predictive power for diagnosis of
LPR (with salivary pepsin as the “standard”) and compare this to the RSS.
Review for 10.1186/s12876-024-03337-1 (2024)

Title: Lead poisoning as a differential diagnosis in pediatric patients with chronic abdominal
pain: A case-control study in Tehran#Iran
Version: 3 Date: 28 Sep 2023
Reviewer:  Ahed J Alkhatib
Reviewer's report:
Abstract:
- The metod's section did not include  study design,sample size, sampling technique, analytical
method of lead,  and statistical analysis.
- The first part of conclusion is difficult to be mentioned as it is, instead of that, lead poisoning
should be investigated.
Background:
- It will be useful for the readers if the authors added two paragraphs about lead levels  in globally
and another paragraph about heavy metal poisoning in Iran including lead.
Methods:
- Sample size was not determined in this section.
- sampling technique was not mentioned in this section.
References:
Most references are old, please try to update them
Review for 10.1186/s12876-024-03337-1 (2024)

Title: Lead poisoning as a differential diagnosis in pediatric patients with chronic abdominal
pain: A case-control study in Tehran#Iran
Version: 3 Date: 12 Oct 2023
Reviewer's report:
Dear authors,
The manuscript is valuable but there are some grammatical and punctuation errors.
It needs to revise.
I think the authors should extend discussion section.
The sample size is small.
How you determined the sample size?
Please explain how you selected the case and control patients?
How many patients were eligible or excluded during study?
You should explain all excluded cases by simple algorithm.
What is the lowest  and highest BLL in each groups?
Are there BLL  atomic absorption test in your hospital?
How you stored  Blood tube at -80oC?
Review for 10.1186/s12876-024-03337-1 (2024)

Title: Lead poisoning as a differential diagnosis in pediatric patients with chronic abdominal
pain: A case-control study in Tehran#Iran
Version: 7 Date: 07 Mar 2024
Reviewer's report:
Dear authors,
I read the revised version of your manuscript carefully. I appreciate your time and effort involved
in conducting this study and revising the manuscript. In my opinion, your study had excellent
study design, data analysis, and scientific writing.  It can assist clinicians to better understand
the etiology of chronic abdominal pain. Thus, it can be accepted for publications.
Bests,
Review for 10.1186/s12876-024-03337-1 (2024)

Title: Lead poisoning as a differential diagnosis in pediatric patients with chronic abdominal
pain: A case-control study in Tehran#Iran
Version: 12 Date: 20 Jul 2024
Reviewer:  Leila Barati
Reviewer's report:
Dear Authors;
I appreciate your efforts, I read the revised version of the manuscript,  all of the comments were
revised carefully.  This manuscript can be accepted for publication.
Best regards
Review for 10.1186/s12876-024-03409-2 (2024)

Title: Comprehensive Evaluation of Immunological Attributes and Immunotherapy Responses
of Positive T Cell Function Regulators in Colorectal Cancer
Version: 1 Date: 22 Jun 2024
Reviewer's report:
This study developed a PTFR risk model based on differentially expressed genes (DEGs),
evaluating its predictive ability for survival outcomes, clinical variables, TME characteristics,
tumor mutations, microsatellite instability (MSI), Cell Stem Cell (CSC) index, and responses
to chemotherapy, targeted therapy, and immunotherapy. The PTFR risk model demonstrated
robust performance across various facets of CRC, including immune cell composition,
HLA expression, immune checkpoint expression, mutation profiles, CSC characteristics, and
immunotherapeutic efficacy. Overall, this study provides valuable insights into PTFRs in CRC
prognosis and their potential utility in personalized treatment strategies, suggesting further
validation in larger cohorts or clinical trials to strengthen the findings and clarify their clinical
implications. Additionally, more detailed mechanistic studies could elucidate the specific roles
of PTFRs in shaping the TME and modulating therapeutic responses.
However, the cutoff values for the two subtypes across different datasets may not be consistent.
The authors should clearly define the cutoff values for both subtypes. Additionally, it is essential
to validate the authors' conclusions using an independent validation dataset.
Review for 10.1186/s12876-024-03409-2 (2024)

Title: Comprehensive Evaluation of Immunological Attributes and Immunotherapy Responses
of Positive T Cell Function Regulators in Colorectal Cancer
Version: 3 Date: 12 Aug 2024
Reviewer's report:
The authors have improved the manuscript. I would still suggest to include a clarification such
as "here abbreviated as PTFRs for simplicity" since they use it for the first time.
Review for 10.1186/s12876-024-03409-2 (2024)

Title: Comprehensive Evaluation of Immunological Attributes and Immunotherapy Responses
of Positive T Cell Function Regulators in Colorectal Cancer
Version: 3 Date: 28 Aug 2024
Reviewer's report:
This study examines the role of positive T-cell function regulators (PTFRs) in colorectal cancer
(CRC), identifying 33 top-ranked PTFRs that enhance the proliferation and activation of CD4+
and CD8+ T-cells. The authors utilized comprehensive bioinformatics analyses to demonstrate
these PTFRs' impact on immune cell function, including the secretion of cytokines and resistance
to T-cell exhaustion. The study suggests that overexpression of these genes could improve the
efficacy of CAR-T cell therapies by mitigating exhaustion and enhancing antitumor activity.
The study is commendable for its innovative approach and thorough bioinformatics analyses,
which provide valuable insights into the potential of PTFRs in enhancing immunotherapy
outcomes. However, the absence of an appropriate training and validation cohort raises concerns
about the robustness of the proposed prognostic implications. While the bioinformatics analysis
is strong, further experimental validation, such as RT-PCR, is needed to solidify the findings.
Overall, the research presents meaningful contributions to the understanding of PTFRs in CRC
and could be considered for publication in BMC Gastroenterology, where it would serve as a
valuable resource for researchers in the field.
Review for 10.1186/s12876-024-03441-2 (2024)

Title: Clinical outcomes of drug-coated balloons dilatation for benign esophageal stricture
Version: 2 Date: 10 Sep 2024
Reviewer's report:
Congratulations on your manuscript on the creative and innovative way to solve this very hard
to solve problems we commonly face. Despite this, I think your manuscript should be more
thorough on describing the technique, if the technique should be replicated by others.
Review for 10.1186/s12876-024-03441-2 (2024)

Title: Clinical outcomes of drug-coated balloons dilatation for benign esophageal stricture
Version: 2 Date: 14 Sep 2024
Reviewer's report:
In this study, DCB dilatation, typically used for coronary vascular disease, was innovatively
applied to the treatment of refractory benign esophageal stenosis. A single-arm, retrospective
study included 18 patients, revealing a clinical success rate of 84.2% for DCB dilatation.
However, several issues need to be addressed before considering publication. If these concerns
are adequately resolved, this reviewer believes that the contributions of this paper are significant
for the treatment of refractory benign esophageal stenosis.
1. Upper gastrointestinal endoscopy allows for scar dissection and dilation under direct
visualization, providing short-term symptom relief for esophageal strictures, which is a simpler
and safer approach. In comparison, the clinical significance of radiological DCB dilatation
appears limited. Further elaboration on the clinical significance of DCB dilatation is required.
2. Post-dilation indicators include stricture diameter and length, dysphagia scores, and stricture
indices. The images presented were taken a few days after DCB dilatation, and there is a lack of
long-term postoperative imaging data. Moreover, it remains unclear whether the dysphagia score
and the stenosis index correspond to the same time frame as the chest CT and esophagography.
3. The background section does not specifically address the types and effects of antiproliferative
drugs used in DCB balloons. While these drugs are known to inhibit endothelial cell
proliferation, there is insufficient literature supporting their effectiveness in treating esophageal
stenosis. If there is no distinct effect, the dilation efficacy of DCBs may not differ from that of
conventional balloon dilation. This aspect could be improved.
4. The article and table indicate a total of 18 patients; however, the methods section of the
abstract states, “From May 2020 to August 2023, 19 patients underwent DCB dilatation for
benign esophageal strictures.” Please verify the original data to rectify this discrepancy.
5. The conclusion of this study asserts that “DCBs dilatation can be a safe, effective, and
feasible treatment for benign esophageal strictures,” which contradicts the term “refractory
benign esophageal strictures” used in the title. Please align the terminology between the title
and the content.
6. The inclusion criteria specify that patients must have “failed in repeated push-type dilators or
balloon dilation,” implying that all included patients should have undergone at least one prior
dilation attempt. However, only 10 patients (52.6%) received non-DCB dilation, and 2 patients
underwent bougienage before DCB dilatation. Please provide clarification on this matter.
Review for 10.1186/s12876-024-03441-2 (2024)

Title: Clinical outcomes of drug-coated balloons dilatation for benign esophageal stricture
Version: 3 Date: 26 Sep 2024
Reviewer:  Lianyong Li
Reviewer's report:
The authors conducted a study on a potential treatment for benign esophageal strictures using
drug-coated balloons (DCBs) for dilatation. They demonstrated that this method was both safe
and effective in a group of 18 patients. The authors have addressed each review comment
thoroughly and satisfactorily. Based on these considerations, I believe the manuscript should be
accepted for publication.
Review for 10.1186/s12876-024-03421-6 (2024)

Title: Adenocarcinoma of the esophagogastric junction: characteristics of female patients
and young adult patients based on a 12-year retrospective and prospective multicenter
clinicoepidemiological cohort study in Japan
Version: 3 Date: 30 May 2024
Reviewer:  Masayuki Watanabe
Reviewer's report:
The authors conducted a multicenter clinicoepidemiological cohort study on the characteristics
of female and young adult patients with adenocarcinoma of the EGJ. Patients without any known
associated factors, including obesity, smoking, hiatal hernia, and male, accounted for 53% of
female patients, and they had significantly more undifferentiated tumors than those with at
least one associated factor. Also, young adult patients had more undifferentiated tumors than
middle-aged and elderly patients. This manuscript may provide important clinical information
for readers. Several changes will improve the quality of this manuscript.
1. The discussion seems too long and redundant. As the essential findings of this study were the
characteristics of female and young adult patients with AEGJ, I recommend the authors make
the discussion concise by focusing only on these findings.
2. The conclusion is also redundant, as the authors repeated the same things that were said in
the discussion. Please make it concise so readers understand it better.
3. It is hard to understand the trend of the male-to-female ratio in Figure 1. A 100% component
bar chart combined with a line of total numbers is better for visualizing the trend.
4. The same things happen in Figure 3. I recommend using a 100% component bar chart to
demonstrate the trend in the age groups.
Review for 10.1186/s12876-024-03421-6 (2024)

Title: Adenocarcinoma of the esophagogastric junction: characteristics of female patients
and young adult patients based on a 12-year retrospective and prospective multicenter
clinicoepidemiological cohort study in Japan
Version: 3 Date: 01 Jun 2024
Reviewer:  Elfriede Bollschweiler
Reviewer's report:
The authors analysed data from Japanese patients with adenocarcinoma of the gastroesophageal
junction.  This tumour entity is not common in Asian region in contrast to Western industrial
nations. Therefore, epidemiological data are of interest. Of course, the case numbers are very
low for really valid results.
I have no further comments.
Review for 10.1186/s12876-024-03421-6 (2024)

Title: Adenocarcinoma of the esophagogastric junction: characteristics of female patients
and young adult patients based on a 12-year retrospective and prospective multicenter
clinicoepidemiological cohort study in Japan
Version: 3 Date: 05 Jun 2024
Reviewer's report:
Interesting analysis of patients with AEG type I and II in gender and age aspects.
What is the reason for more advanced carcinoma in the younger group in your opinion?
The screening in patients without BE and hernia is difficult to organize, what are the suggestions?
What are the risk factors for the female patients to develop an AEG carcinoma?
Review for 10.1186/s12876-024-03421-6 (2024)

Title: Adenocarcinoma of the esophagogastric junction: characteristics of female patients
and young adult patients based on a 12-year retrospective and prospective multicenter
clinicoepidemiological cohort study in Japan
Version: 4 Date: 20 Jun 2024
Reviewer:  Elfriede Bollschweiler
Reviewer's report:
The authors had answered to all remarks of the reviewers. Threfore, I think the manuscript is of
interesting for the readers of the journal. I have no further commentary.
Review for 10.1186/s12876-024-03421-6 (2024)

Title: Adenocarcinoma of the esophagogastric junction: characteristics of female patients
and young adult patients based on a 12-year retrospective and prospective multicenter
clinicoepidemiological cohort study in Japan
Version: 4 Date: 08 Jul 2024
Reviewer:  Masayuki Watanabe
Reviewer's report:
The authors revised the manuscript according to the reviewers' comments. However, the
conclusion remains redundant. The first two sentences are enough to conclude this study.
Review for 10.1186/s12876-024-03421-6 (2024)

Title: Adenocarcinoma of the esophagogastric junction: characteristics of female patients
and young adult patients based on a 12-year retrospective and prospective multicenter
clinicoepidemiological cohort study in Japan
Version: 5 Date: 27 Aug 2024
Reviewer:  Masayuki Watanabe
Reviewer's report:
I have no additional comments.
Review for 10.1186/s12876-024-03421-6 (2024)

Title: Adenocarcinoma of the esophagogastric junction: characteristics of female patients
and young adult patients based on a 12-year retrospective and prospective multicenter
clinicoepidemiological cohort study in Japan
Version: 5 Date: 28 Aug 2024
Reviewer:  Elfriede Bollschweiler
Reviewer's report:
According to my opinion this manuscript is of interest for the reader of BMC Gastroenterology.
Explain this by the main points:
1. This is a prospective study, only the follow-up was retrospective collected.
2. The data are from a defined region, therefore  the selection bias is minimized.
3. Adenocarcinoma of the gastrointestinal junction are not so often seen in East
Asia compared to Western region.  Results from Japan for this tumour are rare. To compare data
from East and West these data are of interest.
4. The follow-up seems to be easier and as a consequence more exact according to the reasons
of death.
Of course, there may be some problems:
- small number of patients, especially in the subgroups
- non-significance may be caused by this fact.
- the description of the main findings are difficult, and so on.
My conclusion, the paper is of interest
I have two additional remarks:
1. Please,  add to the tables the therapeutic procedure for the tumor
e.g. Endoscopic - EMR or ESD
Surgery: Esophagectomy or Gastrectomy.
and a description of the main  procedures in the part "material and methods"
2. Please add a calculation of the overall survival
Review for 10.1186/s12876-024-03421-6 (2024)

Title: Adenocarcinoma of the esophagogastric junction: characteristics of female patients
and young adult patients based on a 12-year retrospective and prospective multicenter
clinicoepidemiological cohort study in Japan
Version: 6 Date: 11 Sep 2024
Reviewer:  Elfriede Bollschweiler
Reviewer's report:
I have read the latest version of the manuscript with the revisions. Again, the data are of interest.
And of course, there are additional open questions.
But now the manuscript is of interest for the readers of the journal. I have no additional
comments.