JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-022-02185-1 (2022)

Title: Administration of Probiotics to Healthy Volunteers – Effects on Reactivity of Intestinal
Mucosa and Systemic Leukocytes
Version: 4 Date: 21 Oct 2021
Reviewer:  Jayesh Ahire
Reviewer's report:
1. Line 60-62: Provide clarity to the sentences. After ingestion of what?
2. Line 62: change the sentence for better understanding, “Blood tests were sampled”
3. Study start date (January 2006)/actual primary completion date (March 2006) and actual study
completion (February 2012) dates are too old. Please justify the reason behind the delay (in
what?)? Publication?
4. Besides this, study indicated as retrospectively registered. Justify the reason in manuscript.
5. Provide statement in the manuscript that “All ongoing and related trials for this intervention
are registered”.
6. Line 113: Provide human ethics committee approval date.
7. Line 114: as per the clinical trial registration data, the dates appear different. Justify.
8. Line 125: correct sentence construction error.
9. Provide manufacturing details like batch number and date for probiotics used in this study.
10. Line 133: The gastrointestinal function scale is validated scale? Provide reference for the
same.
11. Line 242-243: The label claim is evaluated for the probiotic product? The product is stable at
room temperature or 4 oC. The required conditions were maintained to keep label claim strength
of the bacteria?
12. Line 314: Bifidobacteria capable to grow well in MRS supplemented with 0.1% L-Cysteine,
without cysteine it is hard to cultivate them.
13. Why placebo is not included in the study? In my opinion, placebo results are must to confirm
the finding and effects of probiotics.
14. It could be nice, if authors can add histology images.
15. Figure 2 a and b: properly label the “Y” axis.
Review for 10.1186/s12876-022-02185-1 (2022)

Title: Administration of Probiotics to Healthy Volunteers – Effects on Reactivity of Intestinal
Mucosa and Systemic Leukocytes
Version: 4 Date: 02 Nov 2021
Reviewer's report:
This is a nicely written study showing the beneficial effect of probiotics in heathy subjects. I
have only minor comments:
* Please add sources of probiotics.
* Are there any units to include in Table 2?
* The authors should consider showing representative histology before and after probiotic
administration.
* Please include brief discussion on strain specificity in the effects of probiotics.
* Please include in brief how TNF-alpha stimulation leads to IL-6 secretion in the discussion.
* Please add statistics on Fig. 2b.
Review for 10.1186/s12876-022-02185-1 (2022)

Title: Administration of Probiotics to Healthy Volunteers – Effects on Reactivity of Intestinal
Mucosa and Systemic Leukocytes
Version: 6 Date: 15 Feb 2022
Reviewer:  Jayesh Ahire
Reviewer's report:
Authors addressed all my queries and revised the manuscript extensively. Therefore, I hereby
recommend to accept the revised version.
Review for 10.1186/s12876-022-02172-6 (2022)

Title: Methylated septin 9 gene is an important prognostic marker in stage II and stage III
colorectal cancer for evaluating local recurrence or distant metastasis after surgery
Version: 1 Date: 15 Nov 2021
Reviewer's report:
Major points
1) 2.1 Patients, line 2. Two-year DFS has been analyzed even though the end of the case
enrollment period is January 2020, which is less than two years. The Median follow up period
should be indicated. Also, in Figure 4, Patients at risk should be shown.
2) The Adjuvant chemotherapy regimen should be stated. It is not common to perform advanced
chemotherapy in all Stage II cases.
3) Tables 1, 2, 3. Not only the classification of Colon and Rectum, but also the sideness of colon
should be classified.
4) Table 2. It is strange that colon and rectum are not prognostic factors.
5) Discussion. From Table 1, mSEPT9 and microsatellite status seem to be closely related, but
that is not discussed.
6) Discussion. The limitation of this study is not mentioned.
Minor point
7) 2.1 Patients, exclusion criteria, (III). No adjuvant treatment # neoadjuvant treatment
Review for 10.1186/s12876-022-02172-6 (2022)

Title: Methylated septin 9 gene is an important prognostic marker in stage II and stage III
colorectal cancer for evaluating local recurrence or distant metastasis after surgery
Version: 1 Date: 16 Dec 2021
Reviewer's report:
I am very honored to be peer-reviewed this time. This study shows that the Methylated septin
9 gene may be a prognostic factor in post-curative Stage II and III colorectal cancer cases.
Interesting results, but with some questions.
Major comment)
What are the details of the located areas of colon cancer?
What are the details of the surgical procedure for rectal cancer cases?
I would like to know the CRM status in rectal cancer cases.
How do you interpret that there is a significant difference between the T stage and the M stage,
but not the N stage?
How do you interpret the high number of positives in the lower rectum?
Minor comment)
Are there cases of lateral lymph node metastasis in rectal cancer cases? How many cases have
had lateral lymph node dissection?
Review for 10.1186/s12876-022-02172-6 (2022)

Title: Methylated septin 9 gene is an important prognostic marker in stage II and stage III
colorectal cancer for evaluating local recurrence or distant metastasis after surgery
Version: 3 Date: 02 Feb 2022
Reviewer's report:
There is no comment because author  answered the question from here firmly.
Review for 10.1186/s12876-022-02172-6 (2022)

Title: Methylated septin 9 gene is an important prognostic marker in stage II and stage III
colorectal cancer for evaluating local recurrence or distant metastasis after surgery
Version: 3 Date: 15 Feb 2022
Reviewer's report:
Questions are well answered. Spelling mistake of 'Right' was found in Table 1.
Review for 10.1186/s12876-022-02175-3 (2022)

Title: The methylation of SDC2 and TFPI2 defined three methylator phenotypes of colorectal
cancer
Version: 1 Date: 10 Jan 2022
Reviewer:  Isabel Portillo
Reviewer's report:
Dear authors,
I am pleased to review your manuscript. I consider very useful your study. But I would like to
remark:
row 98: " All objects recruited signed...." Are patients objects? Maybe is most respecful: All
patients, all participants....
Figures are not very well explained and some times is difficult to interpret them.
row 270: "CRCs also differs in age and gender.." In that case the appropriate word is sex". And
¿could you explain better the differences, please?
Conclusions: Could you give a practical guidance for clinicians, please?
Thanks a lot
Review for 10.1186/s12876-022-02175-3 (2022)

Title: The methylation of SDC2 and TFPI2 defined three methylator phenotypes of colorectal
cancer
Version: 3 Date: 16 Feb 2022
Reviewer's report:
I have really appreciated that the authors fully answered to all the raised questions and modified
the text accordingly.
Just one minor point : change the world "between" in lines 233 and 235 with "among" because
three groups were compared
Thank you
Review for 10.1186/s12876-022-02171-7 (2022)

Title: RECENT ADVANCES IN THE DIAGNOSIS OF INTESTINAL TUBERCULOSIS
Version: 3 Date: 19 Oct 2021
Reviewer:  Guofang Deng
Reviewer's report:
The review examined the advance in the field of diagnosis of intestinal tuberculosis. The subject
is interesting .The title and abstract cover the main aspect of work and the flow is quite clear.
But as a review about the diagnosis of ITB. The most difficult thing is to distinguish intestinal
tuberculosis (ITB) from Crohn's disease (CD). A positive interferon-# release assay could give
us a clue to look for TB evidence, especially in a low-Tb setting. I suppose that this part about
IGRAs should be included in the manuscript. Some important citations were missing in the
review. Like:
1. Limsrivilai J, Shreiner AB, Pongpaibul A, Laohapand C, Boonanuwat R, Pausawasdi
N, Pongprasobchai S, Manatsathit S, Higgins PD. Meta-Analytic Bayesian Model For
Differentiating Intestinal Tuberculosis from Crohn's Disease. Am J Gastroenterol. 2017
Mar;112(3):415-427. doi: 10.1038/ajg.2016.529. Epub 2017 Jan 3. PMID: 28045023; PMCID:
PMC5551982.
2. Ng SC, Hirai HW, Tsoi KK, Wong SH, Chan FK, Sung JJ, Wu JC. Systematic review
with meta-analysis: accuracy of interferon-gamma releasing assay and anti-Saccharomyces
cerevisiae antibody in differentiating intestinal tuberculosis from Crohn's disease in Asians. J
Gastroenterol Hepatol. 2014 Sep;29(9):1664-70. doi: 10.1111/jgh.12645. PMID: 24910240.
On the other hand, it had been demonstrated that GeneXpert Ultra is more sensitive than
GeneXpert MTB/RIF in detecting TB even in extrapulmonary specimens. Do authors have any
evidence to support it in the diagnosis of ITB?  Please search for more citations to enrich this
part.  And the sentence described that” where sensitivity can reach 100% by using specimens
such as sputum or bronchoalveolar lavage” is not right. The pooled sensitivity of Xpert should
be corrected according to the reference.
Review for 10.1186/s12876-022-02171-7 (2022)

Title: RECENT ADVANCES IN THE DIAGNOSIS OF INTESTINAL TUBERCULOSIS
Version: 3 Date: 27 Oct 2021
Reviewer's report:
This article is aim to review the latest diagnosis tools in clinic for the intestinal tuberculosis.
Although the article demonstrates the effectiveness of different diagnostic techniques, the paper
is too simple. The statistical and analytical data and discussion need further improve.
1-ABSTRACT
The results section simply lists the sensitivity and specificity of different detection methods,
which is not appropriate. It should show the range of sensitivity and specificity, since results
are  different in different reports.
The conclusion section “Recent modalities such as multiplex PCR and immunological marker
examinations have the highest sensitivity and specificity values and more evidence is expected
to support the application of this examination shortly soon”-highest specificity values is not
appropriate.
2-INTRODUCTION
“In 2017, 10 million cases of tuberculosis were reported worldwide with a mortality rate of
13%.”-should update the newest data.
3-RESULT
A.CLINICAL MANIFESTATIONS OF INTESTINAL TUBERCULOSIS
The results of this paper will be better compared with the results of imaging.
B.Immunological Markers
This manuscript lack the appropriate context to this part. For example, several articles have been
published this year defining some immunological markers to diagnosis of intestinal tuberculosis ,
such as CD73.
Scand J Gastroenterol. Oct-Nov 2018;53(10-11):1217-1221.
Dig Dis Sci. 2013 Aug;58(8):2301-7. doi: 10.1007/s10620-013-2667-0.
4-DISCUSSION
The discussion part is too simply, some questions need to discuss: What are the reason of defects
in different testing methods? What is the guiding effect for clinicians?What is the future of
diagnostic technology?
Review for 10.1186/s12876-022-02177-1 (2022)

Title: Total polyp number may be more important than size and histology of polyps for
prediction of metachronous high-risk colorectal neoplasms
Version: 1 Date: 15 Oct 2021
Reviewer:  Jun Arimoto
Reviewer's report:
This study investigated the total polyp number for the risk of metachronous HR-CRN. This is a
well written study, however, this study has several limitations in the following areas.
1. How many times in a lifetime is the index colonoscopy in this study in each patient? Is the
first colonoscopy for everyone? If not, the data of this study is not reliable. Past history of
colonoscopy in each patient might affect the results of this study. Although authors described
about this issue, I think it is not enough. This is a prospective study. If this study was performed
as a truly prospective study, I think that Past history of colonoscopy in each patient can be found
by interviewing patients. Why did not authors ask the patients? Is this really a prospective study?
2. Authors described ‘after adjusting for risk factors, such as obesity, diabetes, and smoking.’
Male are one of the risk factors for colorectal neoplasms. Why did not authors include this
variable?
3. Why did authors exclude patients >75 years?
4. The description about endoscopists is not enough. More detail clinical information of
colonoscopy is required. If authors usually performed CSP at the time of the colonoscopy, it
means that authors could not to use the magnifying scope in all cases. However, if authors did not
remove the polyps in the first Colonoscopy, authors have been able to observe with magnifying
scope in all cases. It is desirable that every polyp was examined in detail with the magnifying
scope to determine the appropriateness of its resection using CSP or not (EMR, HSP, ESD). It
is important issue in clinical practice. In addition, Authors should add the description about the
endoscopists (skill, number of experiences, ADR, etc).
5. In this study, surveillance colonoscopy was performed within one year. Are all lesions really
metachronous? Is it really possible that you missed it?
6. How did authors distinguish between missed lesion and newly developed lesion?
7. Why did authors set the cutoff value for 5 or more polyps? I think that it is not a prospective
study unless the cutoff value is decided from the beginning. I think that patients just recruited
as prospectively, study design is retrospective.
Review for 10.1186/s12876-022-02177-1 (2022)

Title: Total polyp number may be more important than size and histology of polyps for
prediction of metachronous high-risk colorectal neoplasms
Version: 1 Date: 06 Nov 2021
Reviewer:  Yuusaku Sugihara
Reviewer's report:
The authors evaluated whether the risk of metachronous high-risk colorectal neoplasm (HR-
CRN) differs according to the indication for surveillance colonoscopy. And the result the risk
of metachronous HR-CRN did not differ according to the main indications for surveillance
colonoscopy. The presence of 5 or more polyps at index colonoscopy was the only risk factor
for metachronous HR-CRN.
 This report represents an effort to accomplish this, as these data will most likely prove to be
a unique resource well into the future. I think this paper should be published. But I have some
suggestions to add. The author states in the conclusion that follow CS should be implemented
within 3 years, but this paper does not emphasize the grounds for within 3 years.
Review for 10.1186/s12876-022-02177-1 (2022)

Title: Total polyp number may be more important than size and histology of polyps for
prediction of metachronous high-risk colorectal neoplasms
Version: 2 Date: 04 Dec 2021
Reviewer:  Yuusaku Sugihara
Reviewer's report:
The author has properly corrected the points I pointed out. This paper is meaningful to the reader
and deserves publication. I am honored to be able to review such a wonderful paper.
Review for 10.1186/s12876-022-02177-1 (2022)

Title: Total polyp number may be more important than size and histology of polyps for
prediction of metachronous high-risk colorectal neoplasms
Version: 2 Date: 07 Dec 2021
Reviewer:  Jun Arimoto
Reviewer's report:
Authors have tried best to revise the manuscript according to my comments. Thank  you.
Review for 10.1186/s12876-022-02177-1 (2022)

Title: Total polyp number may be more important than size and histology of polyps for
prediction of metachronous high-risk colorectal neoplasms
Version: 2 Date: 23 Jan 2022
Reviewer's report:
Comments to the Author
This manuscript evaluates which factors best predict the risk of metachronous high-risk
colorectal neoplasms. Currently, intervals between colonoscopies are based on the size, number
and histopathology of retrieved polyps. However, risk stratification is not precise enough due
to a lack of strong evidence.
The manuscript has some drawbacks especially in his methodology.
A one-year follow-up colonoscopy in the population group defined as high risk according to the
different follow-up guidelines aims to ensure a complete resection of neoplasms (missed polyps
and incomplete resection of large polyps) before starting surveillance. Above all, I believe that in
order to draw robust conclusions about which are the variables that most influence the indication
for surveillance colonoscopy at one year, a prospective and ideally randomized study should be
carried out (comparing the results at 3 years in two cohorts: 1) cohort with review colonoscopy
at 1 year and surveillance at 3 years 2) cohort with colonoscopy at 3 years)), which would avoid
excluding patients.
Where exactly the included individuals come from: CRC population screening program?
colonoscopies performed for another reason?
To guarantee the homogeneity of the sample, it should be described if baseline colonoscopies
were performed following an identical protocol of quality standards. In addition, the fact of not
knowing if the index colonoscopy was the first one or if others had already been performed does
not guarantee the homogeneity of the sample either.
Patients with sessile serrated lesions (serrated polyps # 10 mm or with dysplasia including
traditional sessile adenomas) that appear to be associated with an increased risk of neoplasms or
metachronous CRC should be offered a surveillance colonoscopic examination at 3 years (East
JE Gut 2017). The authors should address that serrated polyps with dysplasia are also considered
high-risk lesions.
No mention is made to the morphological characteristics (Paris) of the resected lesions, which
is especially important in large lesions (# 20 mm).
The exclusion of patients with colonoscopy less than 12 months after index colonoscopy to rule
out patients with probable missed lesions is somewhat doubtful. It would be desirable that the
reason for performing it before a year be detailed: to ensure a complete resection of large polyps?
poor preparation? incomplete colonoscopies?
It would be interesting to know if the quality of the colonoscopy was appropriate (and not only
if the endoscopists were experts), as well as an estimate of the subsequent polyps’miss rate.
The patient inclusion period should be in Methodology and not in Results.
The conclusions should be taken with caution because it is a retrospective single-center study.
As mentioned, more precise methodology and a larger number of cases included in the study
could have helped to obtain more relevant results.
Review for 10.1186/s12876-022-02177-1 (2022)

Title: Total polyp number may be more important than size and histology of polyps for
prediction of metachronous high-risk colorectal neoplasms
Version: 3 Date: 12 Feb 2022
Reviewer's report:
I believe that the authors of the manuscript have made the appropriate corrections and therefore
its publication in the journal should be considered.
Review for 10.1186/s12876-022-02182-4 (2022)

Title: Machine Learning-Based Survival Rate Prediction of Korean Hepatocellular Carcinoma
Patients using multi-center data
Version: 4 Date: 09 Jul 2021
Reviewer's report:
Very interesting, novel and important study!
Just want to clarify, any impact with the more widespread use of targeted therapy and
immunotherapy in recent years?
Review for 10.1186/s12876-022-02182-4 (2022)

Title: Machine Learning-Based Survival Rate Prediction of Korean Hepatocellular Carcinoma
Patients using multi-center data
Version: 4 Date: 20 Jul 2021
Reviewer's report:
The authors have done an interesting work on developing machine learning-based prognostic
models for patients with HCC. They have developed and compared several machine learning
models using a large dataset from Korean registry. The following are my comments and
suggestions:
Major comments
1. Please describe which groups of patients/hospitals (primary, secondary, tertiary care, …) were
included in the registry.
2. Please provide HCC stages (e.g., BCLC staging) of the enrolled patients. This would enable
readers to gain a picture of HCC spectrum in this patient cohort, and determine whether the
finding in this study can be applied to their patients.
3. Since the authors excluded cases that had >30% missing input features, the author should
provide the number of cases that were excluded, along with the proportion of outcomes in
the group of excluded cases. This is to explore whether the missing cases were either Missing
completely at random (MCAR), Missing at random (MAR), or Missing not at random (MNAR),
which would affect the predictive performance of the model.
4. In this work, the authors modeled prognostic outcome as a binary variable (<60 or >60 months’
survival). When the outcome was modeled as a binary variable, lost-to-follow-up cases is an
important issue to be addressed as this can result in either better or poorer outcomes. The authors
should set criteria for lost to follow up, and report the numbers, as well as the reasons for lost
to follow up.
5. The authors performed 5-fold cross validation without a separate test set. The reported
performance based on 5-fold cross validation alone can therefore be overestimated, due to
“hyperparameter overfitting” (which is different from “parameter overfitting”). Hyperparameter
overfitting occurs when a model’s hyperparameters are adjusted several times until good
performance is achieved. I think the dataset is large enough to be divided into a test set first,
then the author use the remaining data for the 5-fold cross validation. Finally, the authors can
use the best model (from 5-fold cross validation) to evaluate performance on the test set.
Minor comments
1. Grammar errors and typos exist throughout the manuscript. Writing style has to be improved.
For example,
- There is a typo in Line 8 under Patients subsection. “hyper hancement” should be spelled as
“hyper-enhancement”
- The statement “then we got the average of accuracy, precision, sensitivity and F1 score” was
duplicated. (under the subsection: Data splits for machine learning processing)
2. The authors may want to specifically use the term “F1 score” instead of “F score” in the
manuscript body. There is a family of F scores available, e.g., F1, F0.5, F2, which weigh
precision and recall differently.
3. In the method section, the authors describe the details of each model very extensively. This
is more appropriate for the Review article but not for the Original article.
Review for 10.1186/s12876-022-02182-4 (2022)

Title: Machine Learning-Based Survival Rate Prediction of Korean Hepatocellular Carcinoma
Patients using multi-center data
Version: 6 Date: 27 Dec 2021
Reviewer's report:
Researchers use a variety of machine learning algorithms to predict the survival rate of patients
with hepatocellular carcinoma, which has certain significance for assessing the accuracy of the
machine learning method, but the clinical value is not very significant enough. In addition, there
are some obscurers in writing, some methodological parts of the paper are not clear enough.
Moreover, there are many obvious problems such as inappropriate punctuations and repetitive
text. The content and language of the article that require deep polishing. What’s more, the
figures and tables typography are also not standard enough. Particularly, in Fig.3 and Fig.4 I
cannot understand the processing method corresponding to each picture. The characteristics of
the patients are not consistent but disordered. I believe it is not very difficult to arrange the
features in each picture in the same order. In addition, the authors shall provide more detailes of
the methods and decribe them with logical approach. In short, the article needs to make extensive
revisions.
Review for 10.1186/s12876-022-02182-4 (2022)

Title: Machine Learning-Based Survival Rate Prediction of Korean Hepatocellular Carcinoma
Patients using multi-center data
Version: 6 Date: 10 Jan 2022
Reviewer's report:
The authors propose machine learning approaches to predict the outcome of Hepatocellular
Carcinoma survival in Korean cohort of patients. The work is interesting and may gain many
interests. However, I have minor concerns:
- Naming this method as big data is inaccurate. Big data is a terminology that has been used for
3Vs type of data(Velocity, Volume, Variety). The authors may argue that 2,000 records is big,
but it actually not. Big data through the manuscript can be changed to be datasets, and I think
it must be removed from the title.
- The imbalanced data section may highlight more on the used approach.mentionening the ratio
is good, but more details about the algorithm is needed. The Authors may also highlight it more
in the Introduction and highlight some other imbalanced data handling algorithm such as:
https://ieeexplore.ieee.org/document/7508607
Review for 10.1186/s12876-022-02174-4 (2022)

Title: Fecal indicator bacteria along multiple environmental exposure pathways (water, food,
and soil) and intestinal parasites among children in the rural northwest Ethiopia
Version: 1 Date: 05 Dec 2021
Reviewer's report:
I have few minor comments:
1. The author may describe  or compare the sanitation  or WASH status of the  studies (Ref
21,22, 23, 24) with the present study.
2. In the bar  histogram, the  authors my  provide value of 95% CI
3. The  public health measures  as described to avert the problem  of enteric infection  in the
discussion  need to be strengthened.
Review for 10.1186/s12876-022-02174-4 (2022)

Title: Fecal indicator bacteria along multiple environmental exposure pathways (water, food,
and soil) and intestinal parasites among children in the rural northwest Ethiopia
Version: 3 Date: 18 Jan 2022
Reviewer's report:
I would like to thank the authors for their receptiveness towards the reviewer comments, I see
that the suggestions were answered appropriately and significant changes were made to the
manuscript. There are improvements to grammar and sentence structure that can be made still
with this revised manuscript (e.g. lines 61-62, 251, 274).
Specifically, in lines 77-79: "human boundary (external exposure assessment  to those that
estimate a dose after the contaminant has been taken up into the body (internal exposure
assessment) and measurement of host interaction with the environment, as documented by
Goddard FG, et al" there is a ")" parenthesis missing.
Another suggestion would be to review the use of the STH abbreviation defined in line 59. The
authors use it for "soil-transmitted helminth infections (STHs)  in 2020" but repeatedly use it
for solely "soil-transmitted helminth (STH)..." afterwards (see line 62 as an example).
I would suggest that the authors refrain from using first person language for the Methods and
Results sections as those should be written in third person (extensive use of "we").
After organisms are written once in full genus and species, the authors can abbreviate the genus
to the first letter. See the Intestinal parasitic infections in children section (lines 331-339),
parasite names can be abbreviated as they were already mentioned in the Methods section.
Similarly, the authors can abbreviate gram to "g" as it is standard understanding as a unit of
measurement (see lines 186 and 204 as examples).
Overall, I appreciate the efforts made by the authors to improve this manuscript for acceptance.
Review for 10.1186/s12876-022-02174-4 (2022)

Title: Fecal indicator bacteria along multiple environmental exposure pathways (water, food,
and soil) and intestinal parasites among children in the rural northwest Ethiopia
Version: 3 Date: 27 Jan 2022
Reviewer:  Nuhu Amin
Reviewer's report:
Dear Author,
Thanks for addressing most of my comments and incorporating them in the revised version.
Overall the manuscript looks organized. However,  the discussion section needs to be improved
further by adding some limitations. Such as the generalizability of the results, contamination
may vary in different settings,  Self-reported data may not be reliable etc.
Thanks
Review for 10.1186/s12876-022-02178-0 (2022)

Title: Efficacy of Sigmoidoscopy for Evaluating Disease Activity in Patients with Ulcerative
Colitis
Version: 2 Date: 07 Dec 2021
Reviewer's report:
I am very pleased to have been given the opportunity to review this study.
Assessing mucosal status via colonoscopy for the evaluation of disease activity in patients with
ulcerative colitis (UC) is important in guiding treatment decisions, but it is often difficult to
perform total colonoscopy. While this study managed to discuss the evaluation of activity in UC
using colonoscopy, it requires the following considerations and revisions.
Major Comments
Background
#MES stands for Mayo Endoscopic Subscore, not Mayo Endoscopic Score. Please ensure that
this abbreviation is corrected in the main text, abstract, tables, and figures.
Methods
# CRP and fecal calprotectin were evaluated in this study, but there are several methods to
measure fecal calprotectin. Given that this was a multicenter study, please clarify whether a
uniformed approach used to measure fecal calprotectin levels? At what timepoint were CRP and
fecal calprotectin measured?
Results
#Table 1 should also show fecal calprotectin and CRP values for the assessment of UC activity
in all cases. Please provide the clinical activity index if the data are available.
# Multiple colonoscopies have been performed in a single patient. What is the maximum number
of colonoscopies that were performed in a patient?
#In Table 4, what do 0 and 1 in topical 5-ASA represent?
#The MES and UCEIS of 7.6% and 8.6%, respectively, were more severe in the proximal
colon area than in the rectosigmoid colon area. In these cases, however, performing multiple
colonoscopies in the same patient will have a significant influence on the results. Out of the
percentages provided, how many colonoscopy findings were from the same patient?
#It was stated that "as an endoscopic evaluation for disease activity in patients with ulcerative
colitis, MES #2 or UCEIS #5 is evaluated as active disease, and escalation of drugs should be
considered" (Page 7, Line 159). The reference or basis for these endoscopic cutoff values should
be provided in the Methods section.
# Table 4 presents a comparison of cases in which sigmoidoscopy and colonoscopy can be
evaluated. This table presents an important comparison for exploring the factors that require
colonoscopy in this study; it was pointed out that disease extent is an important criterion to
consider, which is also realized in clinical practice. However, this notion is extremely simplistic,
and more criteria should be analyzed to accurately determine which specific factors result in the
need for colonoscopy. Please show the results of other factors such as sex, age, and duration
of illness.
Minor Comments
#The notation in Table 1 should be modified as follows: Male (n, %) # Male, n (%)
#It should be explained what the median age and disease duration of Table 1 are ± 17.78 and
± 48.88, respectively.
#Please indicate the units of CRP and fecal calprotectin in Table 4.
Review for 10.1186/s12876-022-02178-0 (2022)

Title: Efficacy of Sigmoidoscopy for Evaluating Disease Activity in Patients with Ulcerative
Colitis
Version: 2 Date: 11 Dec 2021
Reviewer's report:
The study on the concordance of endoscopic activity between the distal and proximal parts of
the colon in ulcerative colitis is clinically significant, because colonoscopy is associated with
the burden and risk to patients. And the high rate of concordance between the two is a clinically
important result.
However, it is judged that the following points need to be reconsidered and the contents revised.
The purpose of this study is to investigate the homology of endoscopic activity between the
distal and proximal portions of the colon in patients with ulcerative colitis.
(1) Therefore, it is more appropriate to classify the types of ulcerative colitis into proctitis type,
distal colitis type, left-sided colitis type, and total colitis type, and to study patients with total
colitis and left-sided colitis types, excluding proctitis and distal colitis types.
This is because in ulcerative colitis, especially in proctitis type, distal colitis type, and left-sided
colitis type, skip lesion and appendiceal lesion may be observed, but in general, most lesions are
not observed in the colon more proximally than the continuous lesion.
(2) For the proctitis and distal colitis types, it is preferable to show the proportion of patients
with gross skip lesions or appendiceal lesions in the colon more proximally than the sigmoid
or descending colon and the proportion of patients with proximal expanded lesions at the time
of relapse, and to describe the correlation between the main lesion in the distal colon and the
proximal lesion for those cases.
3) The authors also mentioned in their discussion that there is a possibility of selection bias
in this study for severe cases where full colonoscopy observation is difficult. In severe cases
of ulcerative colitis requiring hospitalization, rectal sparing and more worsen lesions in the
proximal colon are often present.
Therefore, it is desirable to clarify whether colonoscopy is performed in an inpatient or outpatient
setting. In addition, if possible, clinical disease activity at the time of colonoscopy, such as Mayo
score, is expected to be shown for flare-up cases.
Review for 10.1186/s12876-022-02148-6 (2022)

Title: Helicobacter pylori infection is not an independent risk factor of non-alcoholic fatty liver
disease in China
Version: 4 Date: 18 Oct 2021
Reviewer:  Yoshio Sumida
Reviewer's report:
The relationship between NAFLD and H.Pylori is interesting. This manuscript clearly showed
no association between H.Pylori and NAFLD. I strongly agree this conclusion.
The association between histological finding (especially hepatocyte ballooning) and H.Pylori
should be explored in the near future.
Review for 10.1186/s12876-022-02148-6 (2022)

Title: Helicobacter pylori infection is not an independent risk factor of non-alcoholic fatty liver
disease in China
Version: 4 Date: 31 Oct 2021
Reviewer's report:
The authors investigated the association between H pylori and NAFLD. While the results are
interesting, I have some questions and comments.
1. In the multivariate models, the authors failed to account for multicollinearity. For example,
total cholesterol and triglyceride levels or IFG and HbA1c. These exert a high amount of
influence on each other and should not be included in the same model unless they are shown
to be completely independent.
2. Table 1 suggests that metabolic factors (cholesterol, HbA1c, BP, etc) are indeed associated
with HP. However, due to the cross-sectional nature of the study, it is difficult to determine
whether HP is the culprit behind these differences. As the study numbers seem sufficient, I
suggest a further analysis using propensity matching to account for the more influential factors
such as BP and BMI, etc.
3. H pylori is not always in italics while some are. Please unify according to BMC guidelines.
Also, some are  reported as HP while some use H. pylori. Please unify these as well.
Review for 10.1186/s12876-022-02148-6 (2022)

Title: Helicobacter pylori infection is not an independent risk factor of non-alcoholic fatty liver
disease in China
Version: 7 Date: 05 Jan 2022
Reviewer's report:
The authors have answered the reviewers' comments somewhat satisfactorily. However, in
regard to the propensity matching, PS should not be just done at the Table 1 level, but in the
multivariable analysis as well. Only then can we find out if the differences are statistically
relevant after PS matching.
Review for 10.1186/s12876-022-02164-6 (2022)

Title: Models to predict the short-term survival of acute-on-chronic liver failure patients
following liver transplantation
Version: 1 Date: 08 Dec 2021
Reviewer's report:
Summary of research:
Yang and co-authors reported here the results of a retrospective study in which they investigated
the application of different ML models to predict short-term outcomes in ACLF patients
following LT.
Comments to the Author:
In my opinion, there are some minor corrections to be done:
1) On page 4, line 77: the authors report about some recent studies investigating the use of ML
models in the LT setting. While the validation study by Alyllon et al. 2018 is correctly cited,
there’s no mention regarding the original study of Briceno et al. from 2014, which should be
in my opinion added.
2) On page 4, line 77: “my team” should be changed with “our team”. On page 7, line 140
“performed to obtain” instead of “performed obtain”. On page 12, line 257: “methods to predict”
instead of “methods to predicting”.
3) Although on page 8, line 159 death within 90 days after LT is mentioned to define the two
groups (survival vs death), if the “short-term” evaluation is the main object of this study as it
is supposed to be, a proper definition of short-term should be provided previously within the
methods section.
4) I found a little bit confounding on page 13, line 277 where 5 parameters are reported to be
the selected preoperative variables of the study, but finally you list 6. Please specify it clearly
here (LYM vs NEUT, or both?).
Review for 10.1186/s12876-022-02164-6 (2022)

Title: Models to predict the short-term survival of acute-on-chronic liver failure patients
following liver transplantation
Version: 1 Date: 30 Dec 2021
Reviewer's report:
Yang et al provide the analysis of short-term survival risk factors of a single-center cohort of
132 patients transplanted for ACLF  then develop a machine-learning approach to identify the
best predictive model using easy to obtain clinical and biological data.
The subject is trendy and the cohort is significant. However, many weaknesses limit the scope
of the study.
MAJOR issues:
-APASL ACLF criteria was chosen however most studies recently published about this subject
use CLIF-ACLF criteria so the conclusions are difficult to transpose.
-CLIF-ACLF grade (1/2/3) is not explicited.
-Regarding the biological data: Which value was computed? The last before LT or the worst?
It has been shown that the evolution of ACLF in the first 72h after ICU admission are crucial
and that outcomes are very different betxeen "improvers" vs "worseners" in this timeframe.
-Major clinical data missing: How many patients were on ICU vs conventional hospitalization?
How many patients were on renal replacement therapy? And mechanical ventilation? An d
the cause for mechanical ventilation?  Pre-LT arterial lactate levels?  Recent infection from
multidrug resistant organisms? (previously shown as risk-factors for mortality after LT for
ACLF)
-Mortality rate is rather high, probably due to the large inclusion period: was the mortality rate
influenced by the timeframe? Less mortality in more recent years? (after 2016 for example).
-No data on the donor (age/donor risk index/steatosis/cold ischemia time).
Minor issues:
-English editing needed, mostly for the Discussion section.
-Some citations missing: Artru et al J Hepatol 2017, Belli  et al J Hepatol 2021.
-Data on other etiologies for LT (besides HBV infection is needed)
-Flowchart is misguiding: patients "excluded" are actually patient snot meeting inclusion
criteria.
-Some graphs were generated with GraphPad Prism, however this software is not mentioned in
the methods section.
Review for 10.1186/s12876-022-02165-5 (2022)

Title: Elevated Average Maximum Intrabolus Pressure on High-Resolution Manometry is
Associated with Esophageal Dysmotility and Delayed Esophageal Emptying on Timed Barium
Esophagram
Version: 2 Date: 28 Dec 2021
Reviewer's report:
The report demonstrate that an elevated AM-IBP is associated with abnormal TBE findings
of esophageal tablet retention and/or bolus stasis. The finding is novel and supported with
detailed case studies and statistical results. The only comment for the revision is on the method.
Specifically, with the advance of HRM, the IBP could be visualized as moving region along
with the peristaltic wave. Hence, how is the IBP region defined? The second question is about
the time window to compute AM-IBP. A normal bolus transit includes several phases, so does
this time window include all phases or only phases related bolus emptying (i.e after transition
zone)?  With the advance of impedance manometry, impedance could more naturally identify
and track the intra-bolus region. Can the author add comment on this? Thanks.
Review for 10.1186/s12876-022-02165-5 (2022)

Title: Elevated Average Maximum Intrabolus Pressure on High-Resolution Manometry is
Associated with Esophageal Dysmotility and Delayed Esophageal Emptying on Timed Barium
Esophagram
Version: 2 Date: 03 Jan 2022
Reviewer's report:
The study  evaluated the association between the elevated average maximal intrabolus pressure
and esophageal dysmotility , as well as the delayed esophageal emptying on timed barium
esophagram. It showed that the  abnormal AM-IBP  was associated with a higher probability of
retaining liquid bolus or barium tablet arrest on TBE and esophageal dysmotility on HRM. IBP
has been neglected in CC 3.0, and re-introduced in CC4.0.  I have the following concerns.
1.   The current study used the timed barium esophagram as a comparison to confirm the clinical
implication of IBP.  However, the clinical significance of elevated IBP would rely on the scenario
where IRP was elevated with clinical associated symptom including dysphagia and chest pain.
Thus the inclusion and sub-grouping of the included patients should be re-arranged according
to both the IRP and symptom, because the IBP alone would not be the determined factor in
clinical decision.
2. The symptoms and the past history of the included patients have not been introduced in detail.
3.Using excel as the statistical analysis tool is not usual, maybe the authors should think
about shifting using  the SPSS or SAS. During the logistic regression, two many factors were
introduced in the model, the sample size might not be enough for the analysis.
Review for 10.1186/s12876-022-02165-5 (2022)

Title: Elevated Average Maximum Intrabolus Pressure on High-Resolution Manometry is
Associated with Esophageal Dysmotility and Delayed Esophageal Emptying on Timed Barium
Esophagram
Version: 3 Date: 27 Jan 2022
Reviewer's report:
The authors have addressed all the questions clearly. The current revision is good to be accepted.
Review for 10.1186/s12876-022-02165-5 (2022)

Title: Elevated Average Maximum Intrabolus Pressure on High-Resolution Manometry is
Associated with Esophageal Dysmotility and Delayed Esophageal Emptying on Timed Barium
Esophagram
Version: 3 Date: 03 Feb 2022
Reviewer's report:
Thanks for athour's reply.  I have no more questions for this article.
Although this paper was not particularly innovative and clinically significant, it was a rigorous
and solid research, which does provide some useful information.
Review for 10.1186/s12876-022-02159-3 (2022)

Title: Identification of a Novel m6A-related lncRNA Pair Signature for Predicting the Prognosis
of Gastric Cancer Patients
Version: 4 Date: 20 Dec 2021
Reviewer's report:
RE: Identification of a novel m6A-Related lncRNA pairs Signature for Predicting the Prognosis
in Gastric Cancer Patients
N6-methyladenosine (m6A) is the most common form modification on mRNA, and m6A
modification gene could be a potential markers in diagnosis and prognosis of several cancers.
This study utilized the TCGA dataset to construct and validate a m6A-related lncRNA pairs
signature (m6A-LPS) for predicting the prognosis of GC patients. The signature established by
paring m6A-related lncRNAs regardless of expression levels showed a highly and independently
clinical prediction value in GC patients. This manuscript has certain novelty and provides a new
insight into m6A-related lncRNAs for GC prognosis, however, the validation was inadequate
and there were some major revisions are required.
1.In Abstract, the method should describe the details in the selection of m6A-related lncRNA
pairs, otherwise it is quite difficult to understand the prognostic model.
2.In my opinion, one of the advantage of the signature is established by paring m6A-related
lncRNAs, which is rather robust to batch effect and more suitable for clinical individualized
application. It would be better to highlight this advantage in the introduction or discussion
sections, which could be refereed to the literature (PMID:16646797, PMID:26254430 etc. ).
3.In Materials and Methods section on page 6: “Total of 21 m6A regulators were acquired from
published studies, and 10 of 21 m6A regulators with hazard ratio (HR)>1 and p<0.05 in GC
patients were further screened in Kaplan-Meier Plotter” The result should not be described in
the methods section.
4.In Materials and Methods section on page 6: “Where the Expr is the expression level of m6A-
related lncRNA pairs” Here, the expression level of lncRNA pairs should be defined more
clearly.
5.The training and validation sets used in this study were derived from the same dataset (TCGA).
The prognostic performance of the model should be validated in multiple independent datasets,
which could be obtained from public databases (such as GEO, ArrayExpress). More important,
the treatment strategy for patients in TCGA should be described more clearly, which is an
important factor for prognosis.
6.Some statistical results should be represented in the main text. For example, the result on page
12: “The results revealed that the dendritic cells resting, macrophage M2, monocytes, and T cell
CD4 memory resting are positively correlated with the risk score, while T cells CD4 memory
activated is just opposite in CIBERSORT dataset (Figure 9).” The p values and correlation
coefficients should be represented.
Review for 10.1186/s12876-022-02159-3 (2022)

Title: Identification of a Novel m6A-related lncRNA Pair Signature for Predicting the Prognosis
of Gastric Cancer Patients
Version: 6 Date: 08 Feb 2022
Reviewer's report:
The author has provided the point-by-point response to the raised comments. The answers are
satisfactory.
Review for 10.1186/s12876-022-02152-w (2022)

Title: Clinical implications and molecular mechanisms of Cyclin-dependent kinases 4 for
patients with hepatocellular carcinoma
Version: 4 Date: 28 Sep 2021
Reviewer's report:
Very well written manuscript.
I suggest to add a brief comment in the introduction or discussion on hepatocarcinogenesis
arising from NAFLD progression. On this regard, cite the study:
PMID: 29220698
Likewise, add a brief comment on hepatocarcinogenesis in diabetic patients. In this regard, cite
the study: PMID: 23845075
Finally, comment potential implications on molecular mechanisms in anticancer therapy for
HCC. In this regard, cite the studies: PMID: 25974743; PMID: 25915713; PMID: 25085684
Review for 10.1186/s12876-022-02152-w (2022)

Title: Clinical implications and molecular mechanisms of Cyclin-dependent kinases 4 for
patients with hepatocellular carcinoma
Version: 4 Date: 12 Nov 2021
Reviewer's report:
Overall, the statistical analysis seems to be appropriately conducted. However, I have a few
comments that need to be addressed.
Are the following results correct (the p-values suggest statistical significance whereas the text
does not)?
Lines 249-151: ROC curve analysis suggested that CDK4 had a statistically better predictive
value (Figure9E, AUC = 0.744, P < 0.001), but CDK1 was not (Figure9B, AUC = 0.702, P <
0.001).
There is mention in the results of a validation cohort – but what this is is not clear. Is it for
example lines 74-76: “A total of 58 pairs of tumor and adjacent normal liver tissues (>3 cm
margin from tumor) of patients pathologically diagnosed as HCC in The First Affiliated Hospital
of Guangxi Medical…”
The results of the survival analysis are much weaker in the validation cohort – particularly
for CDK1 which is not significant (p=0.075) in the (unadjusted) log-rank test (lines 252-254).
This is not highlighted in either the abstract (no description of the p-values or HR’s) or the
main text (discussion section only mentions this in lines 327-329). Given that the validation
cohort is the real test for predictive power, what is the take-home message in regard to each
gene-expression type? Should CDK1 be disregarded as an independent predictor? Indeed, if a
correction for multiple comparisons was performed in the validation cohort, neither CDK1 nor
CDK4 (p=0.042) would be statistically significant, perhaps inferring that whilst the 2 training
cohorts are hypothesis generating, the results cannot be confirmed in a separate cohort.
Similarly, did the authors perform a similar interaction analysis to assess if the joint-effects
observed in the 2 training cohorts could be repeated in the validation cohort?