JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-022-02334-6 (2022)

Title: Intestinal fatty acid binding protein is a disease biomarker in paediatric coeliac disease
and Crohn’s disease
Version: 2 Date: 17 Aug 2021
Reviewer's report:
In this paper Logan et al. aim to evaluate the role of intestinal fatty acid binding protein (iFABP)
as a non invasive biomarker (serum+urine samples tested) of celiac disease and Crohn’s disease
in children. The control group included healthy children. Patients with ulcerative colitis were
also enrolled. The paper deals with an interesting topic. However, there are substantial concerns
regarding the definitions of the enrolled patients and the methods for assessing adherence to a
gluten-free diet in celiac patients.
Major concerns
1. The definition of controls should be better clarified. Some children were recruited for
measurement of serum iFABP among those “admitted to hospital…for acute diagnostic
investigations” (page 6, line 133), whereas urinary analysis was conducted on children recruited
from the local community. More details on the baseline clinical features of these children must
be provided, particularly for those admitted to hospital. Did they suffer from gastrointestinal
symptoms? Moroeover, it is not stated whether controls were matched according to age and
gender. This can influence the homogeneity of the populations under investigation.
2. Diagnosis of celiac disease was made by means of a duodenal biopsy (diagnoses predate the
ESPGHAN 2012 criteria). Were antibodies for celiac disease tested?
3. It is not entirely clear to me why the Authors decided to measure iFABP levels also in patients
affected by ulcerative colitis, which by definitions does not involve the small-bowel. Were
patients affected by ulcerative colitis considered as controls?
4. Evaluation of adherence to a gluten-free diet cannot be solely measured by relying on gluten
immunogenic peptides. Although they may represent a promising tool in the follow-up of celiac
patients, assessment of adherence by a skilled dietician and follow-up duodenal biopsy still
remains the best methods to evaluate adherence in celiac patients.
5. I am very sceptical that on the basis of the results provided by this study iFABP can be used
for the non-invasive diagnosis of celiac disease, at least at this stage
Minor concerns:
1. I would suggest adopting different abbreviations, such as CeD for celiac disease and CrD for
Crohn’s disease.
Review for 10.1186/s12876-022-02334-6 (2022)

Title: Intestinal fatty acid binding protein is a disease biomarker in paediatric coeliac disease
and Crohn’s disease
Version: 3 Date: 22 Mar 2022
Reviewer's report:
Thank you for allowing me to review this revised version of the manuscript.
The Authors have carefully addressed the majority of the points raised by me and also by
reviewer 1.
I only still have a few concerns about the  methodology for assessing adherence to a GFD in this
pediatric cohort. I totally understand the aspect about follow-up duodenal biopsies. Assessing
GFD adherence is certainly difficult in adults and it can be even more difficult in children. I see
the points related to Authors' clinical experience and the growing interest on GIPs. However,
GIPs can only identify traces of gluten ingested within 48-72 hours before the test and cannot
be entirely representative of the "whole" degree of adherence. I believe this is a relevant aspect
and I think this should be discussed among the limits of the study.
Review for 10.1186/s12876-022-02282-1 (2022)

Title: Comparison of fully coated anti-reflux metal stenting and per-oral endoscopic myotomy
in patients with achalasia: a propensity score- matched retrospective study
Version: 5 Date: 03 Nov 2021
Reviewer's report:
I have the following suggestions to improve the manuscript:
1) More details on how the PS model was built should be added. The term "capacity" should be
replaced by the more appropriate term "caliper".
2) In this regard, why a 0.1 caliper was used? THis is not in accordance with the standard
recommandations of the statisticians who suggest a caliper of 0.2 of the log of the propensity
score (Austin et al).
3) How were normality assumptions assessed?
4) A figure reporting propensity score jitter or histogram should be added.
5) In the discussion, i recommend to add the following recent references on achalasia:
- PMID: 34447872
- PMID: 34222636
- PMID: 32856150
6) In the introduction (or in the Discussion), the authors should mention briefly that POEM can
be used also in esofageal conditions other than achalasia. In this regard, cite the paper:
- PMID: 34608024
Review for 10.1186/s12876-022-02282-1 (2022)

Title: Comparison of fully coated anti-reflux metal stenting and per-oral endoscopic myotomy
in patients with achalasia: a propensity score- matched retrospective study
Version: 8 Date: 30 Mar 2022
Reviewer:  Yusuke Fujiyoshi
Reviewer's report:
I think the questions  are well answered and understandable. However, the answers for the
questions were not included in the revised manuscript. It would be better if you can include the
summary of your answers to the main document, especially  regarding question 1, 3, 5, 7, 8 and
11 of the reviewer2. I think these information are important to readers also.
Review for 10.1186/s12876-022-02282-1 (2022)

Title: Comparison of fully coated anti-reflux metal stenting and per-oral endoscopic myotomy
in patients with achalasia: a propensity score- matched retrospective study
Version: 9 Date: 09 Apr 2022
Reviewer:  Yusuke Fujiyoshi
Reviewer's report:
I think the manuscript is well revised.
Review for 10.1186/s12876-022-02326-6 (2022)

Title: Ultrasonographic scores for ileal Crohn’s disease assessment: better, worse or the same
as contrast-enhanced ultrasound?
Version: 1 Date: 06 Feb 2022
Reviewer's report:
Dear authors,
thank you for the opportunity to review your manuscript.
The manuscript reports  retrospective data on 50 patients with ileocoecal Crohn's Disease, who
were evaluated with two new ultrasound-based scores, advanced CEUS analyses and endoscopy
using standardized scores to define disease activity.
CEUS and endoscopy showed a good agreement (AUC for CEUS 0.8), whereas the two US-
scores based on conventional ultrasound did not reach a meaningful correlation with endoscopic
assessment.
General impression: This is an interesting work that can enrich the knowledge of IBD
diagnostics. However, the retrospective approach requires careful data assessment and
interpretation.
The interval between endoscopy and US was one month and the statement that medication was
not modified in this period requires explanation, especially in cases with active disease.
Moreover, endoscopy is also not a perfect standard, so information on examiner qualification
would be useful. Also, disease activity is usually assessed with biopsies, but the report does not
comment on histology and does not provide any analysis of histological activity.
Overall, the limitations require more attention and need clear statements in the discussion.
Detailed comments:
The title suggests that CEUS is a reference standard for assessing CD. CEUS may be helpful,
but is not yet a gold standard. Consider changing the title to "comparison with CEUS".
Please give information on baseline characteristics and IBD activity in the abstract. Some
figures/numbers of the results in the abstract require definitions.
Methods: Please define "inadequate ultrasonographic profile". Is this a source of bias, especially
in patients with highly active disease? Who performed the endoscopy (Blinded to ultrasound
results? Experts or novices?)?
Results: Gender distribution: 54% is allmost an equal distribution.
Many important data are just presented by mean and SD. Was there always a normal distribution?
Consider presenting subgroups, and medians / ranges if appropriate. This may be more
informative.
CEUS: Where there any adverse events? If not, please state so.
Discussion: Quite long and redundant in some places. Can be shortened, but enriched by
discussion of limitations (see above).
Review for 10.1186/s12876-022-02326-6 (2022)

Title: Ultrasonographic scores for ileal Crohn’s disease assessment: better, worse or the same
as contrast-enhanced ultrasound?
Version: 2 Date: 23 Mar 2022
Reviewer's report:
Dear authors,
Thank you for clarifying important points on the methodology of your  study. The revision has
been performed carefully, resolving most issues adressed in the first review.
Your report may now contribute to the further development of ultrasound-based IBD monitoring,
but the impact of the data is still limited given the - well described - limitations.
I do not have any further specific comments.
Review for 10.1186/s12876-022-02326-6 (2022)

Title: Ultrasonographic scores for ileal Crohn’s disease assessment: better, worse or the same
as contrast-enhanced ultrasound?
Version: 2 Date: 24 Mar 2022
Reviewer's report:
The reviewer had asked if the ultrasound operator was blinded to the results of the
ileocolonoscopy. Altough the authors explained in their answers that the ultrasound operator
was not the same that performed ileocolonoscopy examinations and the ileocolonocopy
examinations were performed after ultrasonographic examinations by an operator without
experience in ultrasound, this does not necessarily mean that the investigators are blinded. The
authors should only use the expression “blinded”, when US operator and endoscopist haven´t had
access to the reports of the other investigator. The authors should clearly state this.  Otherwise,
they can´use the expression “blinded”.
Review for 10.1186/s12876-022-02327-5 (2022)

Title: Can Visceral Adipose Tissue and Skeletal Muscle PredictRecurrence of Newly Diagnosed
Crohn’s Disease in Different Treatments
Version: 0 Date: 25 Sep 2021
Reviewer's report:
The duration needed to reevaluation was not clear. Author just said that within one year of
relapse. This is a fundemental question of one of two questions.
The second question is "relapse" author said. In general relapse means active to inactive induced
then re-active. Aactive to active within short time is not real relapse it is just not inducing
remission. In addition, active before and after treatment higher activity is not relapse. These
separate condition was not clearly demonstrated in this article. Of course duration of observation
or duration of re-evaluation should be stated clearly. Study protocol or study design should be
much more clear.
Review for 10.1186/s12876-022-02327-5 (2022)

Title: Can Visceral Adipose Tissue and Skeletal Muscle PredictRecurrence of Newly Diagnosed
Crohn’s Disease in Different Treatments
Version: 0 Date: 02 Nov 2021
Reviewer's report:
Body composition has been shown to correlate with disease activity and clinical outcomes,
including response to treatment, in patients with Crohn's disease. In this retrospective cohort
study, patients with a diagnosis of Crohn's disease were separated into groups according to initial
treatment, and body composition parameters derived from  pre-treatment abdominal CT scans
were compared between those who relapsed and those who did not. Some differences were noted
- with excess visceral adiposity and low muscle mass associated with higher rates of relapse.
The concept of the paper is simple, and the analysis generally appropriate - although some
explanation of choice of the LASSO analysis method might be helpful.
I would like to make a few points - the definition of recurrence is strict and includes endoscopic
or radiological endpoints. Are data available to describe these endpoints? Are primary non-
response and secondary loss of response classified the same?
The group of patients treated with biologic drugs were significantly younger, with different body
composition parameters, than the other groups. This may be the reason for a lack of difference
in visceral fat indices between relapsers/non-relapsers in that group, rather than be specific to
biologic drugs.
The use of English language throughout the paper (including the title and running title) requires
significant revision for the purposes of clarity and readability.
Some of the references are repeated in the bibliography.
Review for 10.1186/s12876-022-02327-5 (2022)

Title: Can Visceral Adipose Tissue and Skeletal Muscle PredictRecurrence of Newly Diagnosed
Crohn’s Disease in Different Treatments
Version: 4 Date: 10 Jan 2022
Reviewer's report:
I have read the revised manuscript.
I have many questions on the aims and results of this study.
1. Is primary treatment and maintenance treatment the same including doses?
2. This study seems to compare the effectiveness of 5-ASA and steroid plus azathioprine because
biologics group did not show any predictive factors.
3. Authors are discussing the significance of adipose tissue around gut (VAT) and skeletal
muscle through this study but strong treatment by biologics did noy show the merit of measuring
these factors.
4.  At the first treatment how authors select treatments? Based on disease activity including
CDAI? We do not see the policy of these selection in this study
5. What is the most important message to clinician who are responsible on the treatment of CD
patients to select or change treatment as appropriate time point.
Review for 10.1186/s12876-022-02327-5 (2022)

Title: Can Visceral Adipose Tissue and Skeletal Muscle PredictRecurrence of Newly Diagnosed
Crohn’s Disease in Different Treatments
Version: 4 Date: 16 Jan 2022
Reviewer's report:
Thank you for your attention to the points I raised. I think that the paper has been improved by the
modifications you have made. There are still some spelling errors (eg. "structuring" rather than
"stricturing") and grammatical mistakes, but these may be addressed at the proofreading stage.
Review for 10.1186/s12876-022-02327-5 (2022)

Title: Can Visceral Adipose Tissue and Skeletal Muscle PredictRecurrence of Newly Diagnosed
Crohn’s Disease in Different Treatments
Version: 6 Date: 04 Mar 2022
Reviewer's report:
I re-reviewed the munascript as below;
Author concluded that the visceral adipose tissue (VAT) and skeletal muscle (SM) were
associated with the recurrence within one year for Crohn’s disease (CD) patients treated by 5-
amino salicylic (5-ASA) or azathioprine + steroids, but not in biologics.
1, How the meaning or usefulness of this measurement in clinical setting? We do not think 5-
ASA is the useful treatment in CD as you do think (nearly fifty percent of effectiveness) because
the patient we are seeing has many refractoriness.
2, CD is treated as stepwise way as you agree; 5-ASA is the first choice then to steroid is the
second choice and biologics is the final or third step. I think author has selected treatments as
your guideline recommends.
As retrospective study has to setup or build firm cohorts in a proper timeline as due. In this
study old cohort (2015-) was treated and then changed to be second group, and in the era of
biologics (2019-) the third cohort was set up. Were they treated with double or triple regimens
(5-ASA at first and covered with steroid second and then biologics added)? In other words, did
patients treated by biologics have a history of 5-ASA treatment or steroid treatment? If it is right
several cohorts have different background refractoriness because disease course progressed and
several attacks experienced then the intestinal wall will be thickened and increased stiffness
by continued inflammation. Does author think your cohorts are comparable and completely
different? Did they have continuity in timeline?
3, Finally does author think VAT measured in this study was useful in only the first attack of
CD but was not useful after several attack of CD in predicting effectiveness?
4, VAT and SM should be measured before and after treatment because these parameters are
presumed to be changeable and then true prediction or feasibility of VAT will be demonstrated.
Review for 10.1186/s12876-022-02327-5 (2022)

Title: Can Visceral Adipose Tissue and Skeletal Muscle PredictRecurrence of Newly Diagnosed
Crohn’s Disease in Different Treatments
Version: 7 Date: 29 Mar 2022
Reviewer's report:
Additional comments to the revision
1, Title should be changed to “Can visceral adipose tissue and skeletal muscle predict
Recurrence of newly diagnosed Crohn’s disease in different treatments”
2, If the patient selected to the study is only newly diagnosed patients Author should describe
in Patents Section “duration of disease”, “previous treatment”, and “concomitant treatment” and
in Table 1.
Review for 10.1186/s12876-022-02327-5 (2022)

Title: Can Visceral Adipose Tissue and Skeletal Muscle PredictRecurrence of Newly Diagnosed
Crohn’s Disease in Different Treatments
Version: 9 Date: 18 Apr 2022
Reviewer's report:
The revised manuscript have described  duration of Crohn's symptoms, previous treatment and
concomitant treatments. There are questions on the selection of treatment  with 5-ASA, steroid
and biologics. You have said that you have selected each treatment  according to treatment
guideline  in China. According to your step wise selection system before selecting  biologics
you have used 5-ASA and steroid to patients who failed to respond.
But, in this manuscript  you have not described previous treatments as 5-ASA or steroid.
How do you explain these selection you choosed.
Review for 10.1186/s12876-022-02329-3 (2022)

Title: Association of Neutrophil to Lymphocyte Ratio with Preterm Necrotizing Enterocolitis:
A Retrospective Case-control Study
Version: 2 Date: 15 Mar 2022
Reviewer's report:
The paper titled "Association of Neutrophil to Lymphocyte Ratio with Preterm Necrotizing
Enterocolitis: A Retrospective Case-control Study" has been reviewed. Although it is well
written, there are some  issues hat require revisions.
1. Title, abstract and keywords are adequate.  Authors may consider adding "inflammation" as
an additional keyword.
2. Introduction is too long, yet lacks adequate background data about  NLR.
NLR is a novel marker of inflammation derived from routine blood count test.
Its association with inflammation has been reported in inflammatory bowel disease
(Wiener klinische Wochenschrift (2015)127:262-265. DOI 10.1007/s00508-014-0683-5),
irritable bowel disease (Fam Med Prim Care Rev 2020; 22(2): 107–110. DOI: 10.5114/
fmpcr.2020.95311. ), diabetes mellitus type 2 (Aging Male, 2020;23(5):923-927. DOI:
10.1080/13685538.2019.1632283), thyroiditis (Rev Assoc Med Bras 2017; 63(12):1065-1068.
DOI: 10.1590/1806-9282.63.12.1065), and Covid-19 infection (Rev Assoc Med Bras
2021;67(Suppl 1):1-2. DOI: 10.1590/1806-9282.67.Suppl1.20200678.). All these conditions are
inflammatory processes alike with NEC. Background should be improved adequately.
3. Methods were expressed well and statistics are mostly accurate. However, normality analysis
of the study variables was not mentioned. Did authors conduct Kolmogorov-Smirnov or Shapiro
wilk test for this analysis?
4. Results presented systematically and Discussion is fair enough. Only # can suggest adding a
sentence or two about possible clinical utility of the study findings in discussion.
Overall, I recommend publication after suitably revised.
Review for 10.1186/s12876-022-02329-3 (2022)

Title: Association of Neutrophil to Lymphocyte Ratio with Preterm Necrotizing Enterocolitis:
A Retrospective Case-control Study
Version: 2 Date: 16 Mar 2022
Reviewer's report:
Necrotizing enterocolitis (NEC) is the most common and potentially devastating multifactorial
life-threatening condition affecting the gastrointestinal tract (GIT) in premature infants and is a
leading cause of morbidity and mortality in infants born between 23 and 28 weeks of gestation.
Author found that  the NLR  predict preterm NEC along with other biomarkers. Timely NEC
prediction would not only allow for high-risk neonates to receive preventive treatments such as
early exposure to the mother’s colostrum, careful nutritional consideration, use of probiotics,
and increased skin-to-skin care, but also decrease unnecessary antibiotic therapy or even surgical
interventions. There are many factors that can affect the parameter and these have not been
sufficiently addressed.There are many studies in the literature on the subject and there is no
additional contribution.
Review for 10.1186/s12876-022-02329-3 (2022)

Title: Association of Neutrophil to Lymphocyte Ratio with Preterm Necrotizing Enterocolitis:
A Retrospective Case-control Study
Version: 2 Date: 04 Apr 2022
Reviewer's report:
1. It is based on an interesting issue.
2. The rationale for the introduction is good.
3.  The methodology is appropriate.
4.  The results are accurate and sound.
5. The discussion is discussed in detail.
6.  The supporting information in the manuscript is reliable and validated.
7. The manuscript contains innovations.
Review for 10.1186/s12876-022-02329-3 (2022)

Title: Association of Neutrophil to Lymphocyte Ratio with Preterm Necrotizing Enterocolitis:
A Retrospective Case-control Study
Version: 2 Date: 04 Apr 2022
Reviewer's report:
The introduction provides sufficient background and includes all relevant references.
The research design is appropriate.
The methods are adequately described.
The results are clearly presented.
The conclusions are supported by the results.
Review for 10.1186/s12876-022-02329-3 (2022)

Title: Association of Neutrophil to Lymphocyte Ratio with Preterm Necrotizing Enterocolitis:
A Retrospective Case-control Study
Version: 4 Date: 26 Apr 2022
Reviewer's report:
The paper entitled "Association of Neutrophil to Lymphocyte Ratio with Preterm Necrotizing
Enterocolitis: A Retrospective Case-control Study" is read and re-reviewed. Authors were
responsive to my previous comments in first review round. I see that substantial improvement
acquired after revisions that applied by the authors. No further alterations are needed. Therefore,
I think  the paper would be accepted for publication.
Review for 10.1186/s12876-022-02329-3 (2022)

Title: Association of Neutrophil to Lymphocyte Ratio with Preterm Necrotizing Enterocolitis:
A Retrospective Case-control Study
Version: 4 Date: 29 Apr 2022
Reviewer's report:
The authors were able to answer the questions sufficiently.
I agree with the publication.
Review for 10.1186/s12876-022-02324-8 (2022)

Title: The molecular characteristics of gastric cancer patients living in Qinghai-Tibetan Plateau
Version: 4 Date: 04 Apr 2022
Reviewer:  EDOARDO VIRGILIO
Reviewer's report:
Please consider the following:
Introduction:
- "The incidence of gastric cancer in China ranks third in the world, and the mortality rate among
malignant tumors ranks first [7]. " It is not clear if you are talking about China or the rest of
the world. Please, rephrase.
- "Here, for better understanding the molecular mechanism of gastric cancer patients living in
and offer the targeted therapeutic strategies specially designed for patients living in QTP, we
collect ...": I do not understand when you say "offer". Please, rephrase.
- "We found that, these 31 patients are among 40 to 70 years old, most of them are male,
tumors are always located in antrum. By sequenced 31 paired tumor and normal bio-samples,
we found that, most of single nucleotide polymorphisms (SNP) are in chromosome 7 with C->T
and G->A as the most common alteration types, and the very different cancer driver genes from
western patients. The further analysis on driver genes indicates there is no significant differences
between minor ethnic groups and Han Chinese. Using an adapted kernel-based learning model
and a compilation of pharmacogenomics data of 462 patient-derived tumor cells (PDCs) that
illustrate the diverse genetic and molecular backgrounds of cancer patients [13], the specific
targeted therapeutics for these 31 sequenced patients are suggested." I would remove this part
from Introduction section.
- In general, please align the verb tenses in this section.
Methods:
- Tumor specimens and their paired normal bio-samples: Please, revise witing only  one sentence
about the compliance with ethical standards.
Results
- Clinical characteristics: Please, align the verb tenses.
Review for 10.1186/s12876-022-02324-8 (2022)

Title: The molecular characteristics of gastric cancer patients living in Qinghai-Tibetan Plateau
Version: 4 Date: 16 Apr 2022
Reviewer's report:
This work attempts research the molecular characteristics of gastric cancer patients living in
Qinghai-Tibetan Plateau. They collected about 30 patients from Qinghai Provincial People’s
Hospital, and identified the molecular variations via whole exome sequencing. They found some
special characteristics for those gastric patients living in Qinghai-Tibetan Plateau, including
younger initial diagnosis age, most variations found in chromosome 7, et al. There are some
issues have to be addressed before publication.
1. The authors should link the molecular characteristics with some clinical features, for instance
talk about the differences in molecular variations between different minority nationality and Han
Chinese, the differences in molecular variations among different tumor stages, et al.
2. More clinical features should be discussed here, like tumor stage, survival, et al.
3. The authors should discuss the difference between patients living in Qinghai-Tibetan Plateau
and patients living in low-altitude place.
4. Double check the typos and grammar issues.
Review for 10.1186/s12876-022-02295-w (2022)

Title: Development and evaluation of a Japanese prediction model for low anterior resection
syndrome after rectal cancer surgery
Version: 1 Date: 25 Nov 2021
Reviewer's report:
The authors aim to clarify risk factors for LARS following rectal cancer surgery in Japanese
patients. Analysis has been conducted in 160 patients. They were retrospectively identified.
Patients were operated between 2017 and 2020.
- Background, Line 12-15. Authors cite work by Battersby et al, Gut 2018, 67(4):688-696 and
explain that published nomogram is based on European patients. Here it's adopted to Japanese
patients with same conditions. Aim is to clarify the risk factors in Japanese cohort. Since study
design is different (Age cutoff 75 years instead of 80, not TME vs PME, ISR vs HAR/LAR ...)
It's maybe better to analyze the research question and discuss within the discussion section of
the manuscript differences between publications. Maybe at the end, some differences maybe
accountable to ethnicity.
- Table 3, I guess there is a mistake. ISR was 13 and HAR,LAR 102. Please correct.
- What was the indication for ISR, given the median distance from anal verge of 10 cm?
- LAR would have more common with ISR than wit HAR. Why authors do not group LAR
with ISR and compare with HAR? Or best would be to exclude ISR. This would enhance the
comparability with other studies but is only possible with sufficient patient number in groups.
However, this is presently not the case and that is a major limitation of this analysis.
- language revision by native speaker is recommended.
Review for 10.1186/s12876-022-02295-w (2022)

Title: Development and evaluation of a Japanese prediction model for low anterior resection
syndrome after rectal cancer surgery
Version: 1 Date: 30 Dec 2021
Reviewer's report:
"PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses a testable research
question(s) (brief or other article types: is there a clear objective)?
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with technical rigor to allow
confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
No - there are issues with the statistics in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Is the current version of this work technically
sound? If not, can revisions be made to make the work technically sound?
Probably - with minor revisions
PEER REVIEWER COMMENTS:
GENERAL COMMENTS:
This is a standard nomogram analysis that uses logistic regression along with area under the
curve (AUC) statistics to predict low anterior resection syndrome after rectal cancer surgery.
Splitting the learning and validation set based on time period is a nice approach. The paper
is missing some calibration details which are commonly presented in nomogram papers.
Otherwise, the comments are relatively minor overall.
REQUESTED REVISIONS:
Comment 1) The authors could present a calibration plot or other justification that their
nomogram is well calibrated.
Comment 2) The authors could describe how quickly LARS develops. If there are significant
lag times to the development of LARS, the authors could better account for the time to event
aspect by using a Cox proportional hazards or similar regression to create the nomogram. A Fine
& Gray model would be appropriate if death is a significant competing risk.
Comment 3) There are some typos in the document (e.g. “patinets” and “propotion” in Results).
Using Word spell check would be useful.
Comment 4) The regression coefficients or related odds ratios that were used to create the
nomogram could be included in the paper if not already there. Table 4 presents a model with
intersphincteric resection, which was omitted from the final nomogram model due to lack of
statistical significance.
ADDITIONAL REQUESTS/SUGGESTIONS:
No further comments."
Review for 10.1186/s12876-022-02295-w (2022)

Title: Development and evaluation of a Japanese prediction model for low anterior resection
syndrome after rectal cancer surgery
Version: 3 Date: 19 Apr 2022
Reviewer's report:
"PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: This is a nice paper. My initial concerns were modest. The authors
have been responsive to my comments. I have no further comments.
ADDITIONAL REQUESTS/SUGGESTIONS:
No further comments"
Review for 10.1186/s12876-022-02325-7 (2022)

Title: Risk factors related to age at diagnosis of pancreatic cancer: A retrospective cohort pilot
study
Version: 2 Date: 23 Mar 2022
Reviewer's report:
The Authors determined in a pilot study,  the feasibility of a large study that would compare the
age at diagnosis of pancreatic cancer among patients with different risk factors. Sixteen out of
24 (67%) subjects showed  known genetic factors and/or had smoking and/or drinking habits.
Significant correlation between the age at which alcohol consumption was started and the age
at diagnosis of pancreatic cancer, was found.
The topic is interesting and the manuscript is well-written. The main problem is the small number
of subjects with pancreatic cancer included in the study and the difficulty to recognize patients
at high risk to develop pancreatic cancer. So, how this pilot study may be validated in larger
studies?
Review for 10.1186/s12876-022-02325-7 (2022)

Title: Risk factors related to age at diagnosis of pancreatic cancer: A retrospective cohort pilot
study
Version: 2 Date: 28 Mar 2022
Reviewer's report:
This manuscript evaluated the correlation between age of first exposure to risk factors and
pancreatic cancer onset. This manuscript states some important issues regarding pancreatic
cancer onset. However further discussion would be required to confirm this conclusion.
Therefore, authors would clarify several matters that mentioned below.
1. Authors reported about a significant correlation between the age at which alcohol consumption
was started and the age at diagnosis of pancreatic cancer. However, alcohol intake might be more
important than alcohol consumption regarding pancreatic cancer onset. Even if the age of alcohol
consumption was earlier, there are many people who don’t drink very much. Some studies
reported that alcohol abuse is risk factor of pancreatic cancer onset. Authors could classify What
is the etiology of pancreatic cancer due to the age at which alcohol consumption?
2. In the first place, what is the meaning about the age of alcohol consumption among patients
with pancreatic cancer? Epidemiologically, shouldn't authors discuss the age at which alcohol
begins between people with pancreatic cancer and those without pancreatic cancer?
3. There seems to be severe bias due to too small sample size in this study. However, as authors
said, this pilot study might demonstrate the feasibility of a large study based on this study
design. Therefore, author could provide the specific protocol which includes sample size based
on evidence for setting cases in Discussion.
Review for 10.1186/s12876-022-02325-7 (2022)

Title: Risk factors related to age at diagnosis of pancreatic cancer: A retrospective cohort pilot
study
Version: 3 Date: 07 May 2022
Reviewer's report:
This manuscript is written well  based on reviewer's comments. This study will provide useful
information regarding risk factors for diagnosis of pancreatic cancer.  I have no additional
comments.
Review for 10.1186/s12876-022-02304-y (2022)

Title: Combination of Serological Biomarkers and Clinical Features to predict Mucosal Healing
in Crohn’s Disease: A Multicenter Cohort Study
Version: 2 Date: 23 Mar 2022
Reviewer's report:
I am very pleased to have had the opportunity to review this manuscript.
The purpose of this study is to construct a model using serological biomarkers to predict mucosal
healing of Crohn's disease (CD). The strength of this model is that the serological biomarkers
used are tests that can be performed at many facilities. However, this study may require the
following amendments.
Major revision
#Why was the inclusion criterion "(2) Corticosteroids had been discontinued for more than 12
weeks" set (page 5, line 105)?
#Why was the exclusion criterion "A previous history of taking aspirin or warfarin" set (Page
5, line 105)?
#In this study, endoscopic examinations were performed to evaluate mucosal state. Which
endoscopic examinations (colonoscopy, capsule endoscopy, or double-balloon enteroscopy)
were performed?
#The main purpose of this study is to build a model for predicting mucosal healing. However,
the definition of mucosal healing seems to be inadequate (page 6, line 135). Was the endoscopic
score, which assesses the endoscopic activity of Crohn's disease, evaluated?
#This study focuses only on IFX for advanced therapy. Were there any patients treated with other
advanced therapies, such as adalimumab (ADA), ustekinumab (UST), or vedolizumab (VDZ)?
For example, did the group of patients who were not administered IFX include patients treated
with advanced therapies other than IFX?
#There is no table of basic characteristics of all the 348 patients. Since we do not know the
characteristics of the patients in this study, a table of baseline characteristics should be added
that includes items from Table 1, such as age, disease duration, HBI, and therapeutic agents.
#Please enter the unit for each blood test in Table 2.
#Which patient groups (the pre-treatment group, the post-treatment group, or both groups) were
evaluated by the model?
#This analysis shows that the evaluation of MH in the primary model is excellent; however, this
evaluation item includes the presence or absence of IFX. Currently, in addition to IFX, there are
various other advanced therapies, such as ADA, UST, and VDZ. I think that the fact that only
the presence or absence of IFX is an evaluation item is a major constraint on the evaluation of
CDs for which there are various other treatments available.
Minor revisions
#Tables 1 and 3 do not include explanations of abbreviations.
#MH and non-MH in Table 1 are sub-groups, respectively. It should be written in lowercase
as N # n.
#P value should be described as follows; P=0.006 # P = 0.006
#Please italicize P in line 166.
Review for 10.1186/s12876-022-02304-y (2022)

Title: Combination of Serological Biomarkers and Clinical Features to predict Mucosal Healing
in Crohn’s Disease: A Multicenter Cohort Study
Version: 2 Date: 06 Apr 2022
Reviewer's report:
I have read with great interest this manuscript. It is interesting and well written.
Excellent statistical analyses.
I have a few minor suggestions:
- Introduction: "We analyzed the pre-treatment and post-treatment data individually and
explored their relationship with MH after treatment in patients with CD." I think that here
and in the entire manuscript the authors need to better specify which kind of treatment.
Immunomodulators, steroids and IFX? Only IFX? This point is not clear.
- Please, in the Discussion Section specify as a limitation that this is a retrospective study (there
could be errors in storing serums and collecting data).
Review for 10.1186/s12876-022-02304-y (2022)

Title: Combination of Serological Biomarkers and Clinical Features to predict Mucosal Healing
in Crohn’s Disease: A Multicenter Cohort Study
Version: 4 Date: 18 Apr 2022
Reviewer's report:
Thanks to the authors for their response to my comments.
However, most of these replies are not reflected in the text.
Is it possible to indicate the revision for major revision 1 to 5 in the text?
I hope the authors will consider this revision.
Review for 10.1186/s12876-022-02304-y (2022)

Title: Combination of Serological Biomarkers and Clinical Features to predict Mucosal Healing
in Crohn’s Disease: A Multicenter Cohort Study
Version: 5 Date: 26 Apr 2022
Reviewer's report:
I am very grateful for the additional entries in the manuscript for my peer review.
This paper is now worthy of publication.
I pray for further research by the authors.
Review for 10.1186/s12876-022-02309-7 (2022)

Title: Relationship between HER2 overexpression and long-term outcomes of early gastric
cancer: A prospective observational study with a 6-year follow-up
Version: 1 Date: 06 Mar 2022
Reviewer:  Akio Kaito
Reviewer's report:
Dear authors,
Thank you very much for giving me such a great opportunity of reviewing valuable manuscripts.
Your current study seemed well written and worth publishing on this journal, because prognostic
significance of HER2 status in early gastric cancer had not been clarified  yet. The recurrence
rate for HER2 positive EGC in the current study was surprisingly high compared to those of
HER2 negative and other recurrence rate in the multicenter study  such as JCOG0607 (Hasuike,
et al. Gastric cancer, 2017).
Major comments:
1. The recurrence pattern would be stated on your manuscript. Does recurrence included not only
metastatic extra-gastric lesion but metachronous  gastric cancer? If so, these two lesions should
be classified. Recurrence rate for HER2 positive EGC in this study was very high compared
to those of previous reports, granted metachronous lesions were not included as recurrence in
the current study.
Review for 10.1186/s12876-022-02323-9 (2022)

Title: Diagnostic Yield of Inpatient Capsule Endoscopy
Version: 3 Date: 12 Nov 2021
Reviewer's report:
I read with interest this relevant paper on Diagnostic Yield of Inpatient Capsule Endoscopy.
The study provide innovative data and it is well developed. I have just minor suggestios, which
are as follows:
i understand the study group is limited to inpatients , however i suspected elderly age might
influence diagnostic yields rather than other factors. In addition, i suggested the Authors' to
reported some references in the discussion related to age at CE and diagnostic yield.
Review for 10.1186/s12876-022-02313-x (2022)

Title: methylated Septin9 has moderate diagnostic value in colorectal cancer detection in
Chinese population: a multicenter study
Version: 1 Date: 06 Apr 2022
Reviewer's report:
Lu and colleagues have evaluated the diagnostic potential of methylated SEPT9 in colorectal
cancer and compared to that of FIT and other tests. As authors mentioned diagnostic potential
of mSEPT9 has been evaluated previously in multiple studies. However, a direct comparison
between mSEPT9 to FIT and other CRC tests in the matching cohort provides meaningful data.
Authors should provide additional data on the comparison between mSEPT9 and FIT.
A title that reflects the outcome of the study may be more meaningful to reader than the current
generic title. While mSEPT9 may not have outperformed FIT for CRC diagnosis, it is an
important data and worth reflecting in your title.
Can you provide additional diagnostic values for different cancer stages for mSEPT9 and FIT
and compare their efficacy? For example, looking at their efficacy for stages 1-2 and 3-4 and
evaluate which assay performs better.
What was the statistical test used to compare AUCs of mSEPT9 and FIT? Method does not seem
to be included in the methodology. Please add the comparison method in the methods section.
Review for 10.1186/s12876-022-02313-x (2022)

Title: methylated Septin9 has moderate diagnostic value in colorectal cancer detection in
Chinese population: a multicenter study
Version: 1 Date: 07 Apr 2022
Reviewer's report:
1) Cost effectiveness of SEPTIN9  assay for CRC detection should be discussed.
2) Table 1; Why Platelet count in CRC group was higher?
3) Table 1; What is the difference of Polyp and Adenoma?
4) Table 2; In clinical feature, tumor size should be included.
Review for 10.1186/s12876-022-02312-y (2022)

Title: Convolutional neural network-based system for endocytoscopic diagnosis of early gastric
cancer
Version: 2 Date: 03 Feb 2022
Reviewer's report:
The authors constructed an early stage gastric cancer diagnosis system by combining ECS with
CNN, and reported the usefulness of their system by comparing it with experienced endoscopists.
Although this is an interesting report of a first attempt, there are some concerns.
First of all, in the text, it is stated that “our CNN for ECS showed higher accuracy and specificity
in diagnosing EGC compared to trained endoscopists”, but I think the accuracy was not higher,
is that right? The accuracy of CNN was equal to that of endoscopists, but when examined lesion
by lesion, the accuracy of CNN was inferior to that of endoscopists. With these results, I feel
that the authors need to be a little more cautious in concluding that CNN is useful. How about
comparing it to Trainee, or showing the time advantage?
Second, it is unclear what non-cancerous gastric mucosa (NGM) refers to.
The authors state that all ECS images were retrospectively collected from patients who
underwent ECS for the diagnosis of EGC, but it is not clear whether NGM is the mucosa
surrounding the cancer, or a benign tumor mistaken for cancer.
Has the pathology of NGM been proven?
A specific description is recommended.
Third, how were the total of ECS images used for validation selected?
Were they consecutive cases over a period of time?
A specific explanation and mention of possible selection bias would be appreciated.
Fourth, the authors state in the abstract that The trained CNN required 7.0 s to analyze the test
dataset. However, this is not stated in the text.
The difference in time with the endoscopists should be stated.
Fifth, it is not clear in which comparison there is a statistical difference. The p-value should be
stated in the text of the table and results.
Review for 10.1186/s12876-022-02312-y (2022)

Title: Convolutional neural network-based system for endocytoscopic diagnosis of early gastric
cancer
Version: 3 Date: 06 Mar 2022
Reviewer's report:
Thank you for your response and correction to my comments.
The authors state that " The validation data was selected randomly from all images by engineers
of AI Medical Service Inc.”
Does that mean that training images are also included in the validation data?
I think training images should not be used for validation.
Is this a mistake in the description?
Review for 10.1186/s12876-022-02317-7 (2022)

Title: Analysis of Antiviral Efficacy after Switching from Brand to Generic Entecavir in patients
with treatment-naïve chronic hepatitis B
Version: 2 Date: 25 Jan 2022
Reviewer's report:
In this Paper, the Authors aimed to evaluate the antiviral activity and safety of entecavir generic
drugs (ETV-Generic) in comparison to entecavir-brand-name drugs (ETV-Brand) in chronic
hepatitis B (CHB) patients. The Authors found that, in clinical real-life setting, the efficacy and
safety profiles of switching from ETV- Brand to ETV-Generic had no difference in treatment-
naïve CHB patients.
There are few real-world data regarding the clinical efficacy of switching from ETV-Brand
to ETV-Generic, therefore the topic is of interest. The paper is well written. Despite several
limitations regarding the small sample size, the retrospective nature of a single center study, I
feel that the Paper can be considered for publication after minor revisions.
Minor comments:
In the Abstract, please change to: Entecavir (ETV) can suppress hepatitis B virus replication
as a…
In the Abstract, please change to: For the treatment of chronic hepatitis B (CHB), affordable…
In the Abstract, Conclusion, please change to: In treatment-naïve CHB-patients, the efficacy
and…
In the Results, Baseline characteristics: please add the range to the mean treatment period
From text and Table 1, I understand that at baseline all 175 patients had normal ALT levels, but
no patients had undetectable HBV DNA levels despite more than 48 weeks of ETV treatment…
could the Authors explain this?
Throughout the text, please change from “patients with CHB” to “CHB-patients”
Review for 10.1186/s12876-022-02317-7 (2022)

Title: Analysis of Antiviral Efficacy after Switching from Brand to Generic Entecavir in patients
with treatment-naïve chronic hepatitis B
Version: 2 Date: 07 Feb 2022
Reviewer's report:
Dear Authors
“Analysis of Antiviral Efficacy after Switching from Brand to Generic Entecavir in patients with
treatment-naïve chronic hepatitis B”.
This is study was to evaluate the antiviral activity and safety of ETV-Generic in comparison to
ETV-Brand in patients with CHB. However, there is a major problem that is difficult to accept
this manuscript.
1. The reader should read the article that is new or interesting, but there is no new or interesting
content in this manuscript.
2. This is a small retrospective study. If you want to confirm your suggestion, you need to do
a prospective study with two groups.
3. It does not fit the format of this journal for tables and figures to enter the middle of the
manuscript.
Review for 10.1186/s12876-022-02317-7 (2022)

Title: Analysis of Antiviral Efficacy after Switching from Brand to Generic Entecavir in patients
with treatment-naïve chronic hepatitis B
Version: 4 Date: 31 Mar 2022
Reviewer's report:
Good job.
After this revision, I feel that now the manuscript can be considered for publication
Review for 10.1186/s12876-022-02317-7 (2022)

Title: Analysis of Antiviral Efficacy after Switching from Brand to Generic Entecavir in patients
with treatment-naïve chronic hepatitis B
Version: 4 Date: 18 Apr 2022
Reviewer's report:
Dear Authors
“Analysis of Antiviral Efficacy after Switching from Brand to Generic Entecavir in patients with
treatment-naïve chronic hepatitis B”.
This is a study was to evaluate the antiviral activity and safety of ETV-Generic in comparison
to ETV-Brand in patients with CHB. However, this manuscript is still difficult to accept.
1. The reader should read the article that be new or interesting, but there is no new or interesting
content in this manuscript.
2. It cannot be evaluated that there is no difference in effectiveness with only 175 patient data
3. Taiwan is not undeveloped country but developed country.