JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-022-02460-1 (2022)

Title: Comparison the effects and side effects of Covid-19 vaccination in patients with
inflammatory bowel disease (IBD); A systematic scoping review
Version: 0 Date: 21 Jul 2022
Reviewer's report:
I find the subject and study interesting but the study needs revisions:
1. We don’t have “COVID-19 disease”, the disease is itself “COVID-19” and the virus is “SARS-
CoV-2”. Correct in the whole manuscript please.
2. Some sentences are rather long or hard to follow. Check the manuscript language, e.g. the
first sentence of abstract.
3. Regarding the sentence: “Covid-19 disease is a pandemic disease that maybe more severe and
mortal in people with immunodeficiency, such as those with inflammatory bowel disease (IBD),
who are taking immunosuppressive drugs.” I prefer not use the wording “may be”, because
this is rather a certain fact that many immunosuppressive groups of patients have higher risk of
severe COVID-19, yet this is not an important issue just for mentioning.
4. This part is not that important for the abstract: “Total of 212 articles were obtained within the
first step of searching, and 147 ones remained after removing the duplications. Through the title
and abstract screening, 127 were removed.” Only the number of final included studies suffice.
Focus more on the findings.
5. You may want to focus more on the inclusion/exclusion criteria in the methods, e.g. the types
of studies that were excluded (like reviews).
6. It is better to mention the side effects and some more important data in the results section,
rather than only referring to the Table 3.
Review for 10.1186/s12876-022-02460-1 (2022)

Title: Comparison the effects and side effects of Covid-19 vaccination in patients with
inflammatory bowel disease (IBD); A systematic scoping review
Version: 0 Date: 27 Jul 2022
Reviewer's report:
I think this manuscript is pretty interesting. The Authors aimed at evaluating the benefits and
side effects of vaccines in patiens with IBD.
It is really interesting to analyze this events, since  it has already been demonstrated that the
fear of side effects is the most frequent among the reasons given by patients with IBD for their
vaccine hesitancy.
Among these studies, I would cite a big Italian study in which  vaccine hesitancy among IBD
patients was investigated: a survey was sent by patients'association. More than 1200 patients
answered to the survey and the fear of adverse   effects was the main reason for refusal
(approximately 70 %).
A native speaker  could add value to this article.
Did they measure in every studies  antibody  to the spike (rather than to the nucleocapside)?
Which cut off of antibody title was assessed to define immunity ? and when? (2 weeks after
1st dose?)
Did they  evaluated in any study been antibodies in Crohn and RCU separately?
Which were the characteristics of the patients who had an exacerbation of the IBD after the
vaccine? (e.g.,  immunosoppressive therapy, more severe disease activity)
Is there a difference in hospitalization rate after the first dose versus the second dose?
Some other comments:
In the abstract there is a misprint "the studies's findings"
In the discussion the paragraph starting with "The laboratory activity of IBD..." is not clear.
Review for 10.1186/s12876-022-02465-w (2022)

Title: Anatomical pancreatic variants in intraductal papillary mucinous neoplasm patients: a
cross-sectional study
Version: 1 Date: 24 May 2022
Reviewer:  Fumiyoshi Saito
Reviewer's report:
A study of ERCP cases by Nishino et al.(Journal of Gastroenterology 41. 1088-1093, 2006 )
reported that the incidence of IPMN in pancreatic divisum tended to be associated with
IPMN.Therefore, it is expected that the incidence of IPMN will be high in patients with
anatomical pancreatic variants, which is similar to pancreatic divisum.
An important study of the relationship between anatomical pancreatic variants and IPMN.
Review for 10.1186/s12876-022-02465-w (2022)

Title: Anatomical pancreatic variants in intraductal papillary mucinous neoplasm patients: a
cross-sectional study
Version: 1 Date: 09 Jun 2022
Reviewer's report:
This manuscript titled “Anatomical pancreatic variants in intraductal papillary mucinous
neoplasm patients: a cross-sectional study” is intriguing and informative. Although the authors
showed an informative retrospective study where patients with intraductal papillary mucinous
neoplasm (IPMN) have meandering main pancreatic duct (MMPD) more often than those
without IPMN, there were some problems in this manuscript. Therefore, it still needs a
considerable revision to be acceptable for BMC gastroenterology. My suggestions are described
below:
1) In this study, imaging data interpretation was performed by only one radiologist, although
he or she is an experienced radiologist. Therefore, there is no objectiveness in this study. These
imaging data should be diagnosed at least two separate radiologists with sufficient experience.
2) Diagnostic criteria of meandering main pancreatic duct (MMPD) should be described clearly.
For example, when cystic lesion in the pancreatic head oppresses the main pancreatic duct
(MPD) which lead to shaped curved formation of the MPD, do the authors decided it be a
MMPD? It is necessary to explain it in more detail.
3) Location of cystic lesions in patients with IPMN should be shown in table. Furthermore, the
type of IPMN also should be shown.
4) Although the authors showed the association between N-shape MMPD and cystic mural
nodule, the important factor for risk of malignancy in IPMN is the size of mural nodule,
especially diameter #5mm is important. So, they should describe the size of mural nodule in
Table 4.
5) Why the authors compared MMPD and descending type of non-MMPD to calculate odds risk
of accompanying IPMN. They should also compare patients with MMPD and all non-MMPD
patients.
6) In Table 1, the number of each column is inconsistent. For instance, “Duct of Santrini” showed
percentage of Duct of Santrini in MPD variations and “Reverse-Z type” meant the number. They
should be unified.
7) Association file 1 could be removed. Instead, these factors should be described in text.
Review for 10.1186/s12876-022-02479-4 (2022)

Title: Effect of skeletal muscle loss during neoadjuvant imatinib therapy on clinical outcomes
in patients with locally advanced GIST
Version: 1 Date: 06 Jun 2022
Reviewer's report:
This study evaluated the associations between skeletal muscle and postoperative complications,
survival and tumor response in patients with locally advanced gastrointestinal stromal tumors
(LA-GIST) during neoadjuvant therapy with imatinib. Although the findings of the authors are
interesting, I have concerns regarding that the low number of events may lack statistical power
to provide useful information. In addition, there is also lack of analysis of the side effects of
imatinib and muscle change.  My specific comments are as below:
1. The number of events were overall low in pathological response (mild post-op pathological
response (n= 5)), surgical complications (Clavien-Dindo grade III (n=4)), and death (n=8). This
is a critical drawback that I have serious concerns. Multivariate analysis with these low number
of events are not convincible.
2. The information of side effects, dose modification and discontinuation, and compliances
of imatinib are important to this study. I recommend the authors to add these information
and to further analyze their associations with the SMI changes. This can provide more useful
information to potentially improve quality of care and preserve muscle in patients with LA-
GIST during imatinib.
3. The information of software used to measure skeletal muscle showed be provided.
4. In the Figure 5, the number at risk should be provided.
5. What was the duration between CT scans? The comparison of CT durations between patients
with SML and No-SML should be provided.
6. Did these patient occur early resistance to imatinib in these patients? Would patients with
early resistance have shorter duration of CT scans and the SMI change was expanded after
normalization?
Review for 10.1186/s12876-022-02479-4 (2022)

Title: Effect of skeletal muscle loss during neoadjuvant imatinib therapy on clinical outcomes
in patients with locally advanced GIST
Version: 3 Date: 18 Jul 2022
Reviewer:  Jan Peter Marquardt
Reviewer's report:
SUMMARY
The authors have revised their manuscript in a way that tries to address all points. They have
managed to address all minor points mostly to satisfaction. The major points regarding severe
limitations in the statistical analysis seem to be points that the authors will not be able to address
through change in methodology. Modifying the reporting to accurately reflect the extent of
limitations remains crucial to not misguide the scientific community into false confidence in
these findings.
Major points
- The definition of an "optimal cutoff" that is then used in a traditional hypothesis-testing
approach based on the same data set still remains the biggest limitation of statistical power in
the analysis. I would advise not calculating a p-value for significance of the ROC curves being
>0.5 as the assumptions for such a test are not met. At the very least this warrants explicit
mention of severe limitations in interpreting the results in the discussion. Nobody should be
able to mistakenly take these p-values at face value. Along the same vein, the all but guaranteed
overfitting in the multivariable models should be explicitly listed as a severe limitation of the
resulting p-values or better the multivariable analysis be reported without a p-value altogether.
Minor points
- Introduction, third paragraph: The intention of the comments was to rephrase the statements,
not have the comment inserted. In case of the first comment the paragraph now includes two
contradictory statements, please rework into a single statement in line with the comment rather
than including it verbatim.
- Materials and Methods, section Measurement and Definition:  While the used software and
procedures are now more clear, the description seems to imply that all voxels with an HU ranged
-29 to 150 were labelled skeletal muscle.  Given that the figures disprove this, the authors should
include a short statement about the segmentation (who did it, and in what software? manual vs.
machine-assisted?)
Review for 10.1186/s12876-022-02479-4 (2022)

Title: Effect of skeletal muscle loss during neoadjuvant imatinib therapy on clinical outcomes
in patients with locally advanced GIST
Version: 4 Date: 27 Jul 2022
Reviewer:  Jan Peter Marquardt
Reviewer's report:
The authors have addressed all of my points in a satisfactory manner. I find the manuscript much
improved and appropriate to be published in its revised form.
Review for 10.1186/s12876-022-02478-5 (2022)

Title: Ligation of Left Gastric Vein May Cause Delayed Gastric Emptying After
Pancreatoduodenectomy: A Retrospective Study
Version: 1 Date: 17 Apr 2022
Reviewer's report:
The topic is very interesting and original. The analysis that has been conducted is correct with
some interesting results.
In the section METHODS there may be a formal error (line 131) like "dorsal" instead "ventral"
in the comments written in brackets.
In "surgical procedure" authors write "Alimentary tract reconstruction was performed by using
an automatic stapling device, hand-sewn anastomosis, or side-to-side gastroenterostomy", so it
would be interesting that the anastomosis technique is included in the analysis, because it could
affect the development of DGE.
Of the 19 patients who needed the left gastric vein ligation, 12 showed DGE. A more
detailed analysis should be made, focusing on the preoperative, intraoperative and postoperative
characteristics of these patients (perhaps summarized in a table). In particular, the authors should
perform a univariate and multivariate analysis on this group of 19 patients, representing the topic
of their work. In this way you could make their results clearer and immediately interpretable.
Review for 10.1186/s12876-022-02478-5 (2022)

Title: Ligation of Left Gastric Vein May Cause Delayed Gastric Emptying After
Pancreatoduodenectomy: A Retrospective Study
Version: 1 Date: 16 Jun 2022
Reviewer's report:
This is an interesting retrospective study of 105 patients who underwent SSPPD, discussing
postoperative complications from the vascular anatomy. The focus on the relationship between
LGV preservation and DGE is a novel perspective. However, there are some questions about the
method and evaluation. Since LGV ligation can be dependent on vascular anatomy and tumor
factors, the risk factor for DGE development may not be LGV ligation but those factors.
#1. Although many general results such as surgical procedure or postoperative complication are
described, since the purpose of this paper is the relationship between DGE and LGV, it would
have more impact if DGE and LGV were described in more detail.
#2. How do they decide whether or not to ligate the LGV? We assume that the ligation of the
LGV is dictated by the extent of dissection and the progression of the cancer as well as the
vascular running, but is it a surgeon's preference? No mention is made of tumor size, invasion
of organs or blood vessels, or stage of cancer.
#3. Is the running pattern of LGV classification appropriate? Since the authors focus on ligation
of the LGV, an anatomical classification based on the need for ligation of the LGV would be
better. In order to perform #8 lymph node dissection, the LGV running around the CHA is
considered to be resected, while the LGV running around the SpA is not. In addition, there is a
type of LGV that flows into the left branch of the portal vein, but it has not been classified.
#4. Table 4 does not include author’s LGV classification.
#5. Since there are many supplementary tables, it is desirable to summarize the data in the
original tables.
# Authors detected running patter of LGV using computed tomography performed before
surgery and intraoperative findings from operation records. It is advisable to describe the
preoperative and intraoperative findings of the LGV running, respectively.
# How often is octreotide administration given?
# The analysis method in Table 5 is not described, is it logistic regression?
Review for 10.1186/s12876-022-02476-7 (2022)

Title: Major complications after percutaneous biopsy of native or transplanted liver in pediatric
patients: A nationwide inpatient database study in Japan
Version: 1 Date: 20 Jun 2022
Reviewer's report:
The manuscript is well written. As I read it, I had several questions and the answers to some of
these may affect data interpretation:
1. Are patients routinely admitted for liver biopsy in Japan, or does hospital admission correlate
with severe illness that may affect risks? The risks may differ for outpatients.
2. The risks are reported to be lower in transplanted livers, but those patients were also older than
native liver patients. How much of the difference could be attributed to age? Did you compare
outcomes in each group when stratified by age alone, or were other factors age-matched for
comparison, since younger age was a risk factor?
3. Why did you choose +/- 1.28 SD weight to determine over/under weight? Typically the normal
range includes  +/- 2 SD.
4. Was cirrhosis associated with increased bleeding risk? (In kidney biopsies extensive scarring
and fibrosis increases bleeding risk, but I don't know if the same is true for liver biopsies).
Minor:
1. In the background, page 5, end of paragraph 2, should 0.91% OR 1.7% be changed to 0.91%
TO 1.7%?
Review for 10.1186/s12876-022-02476-7 (2022)

Title: Major complications after percutaneous biopsy of native or transplanted liver in pediatric
patients: A nationwide inpatient database study in Japan
Version: 1 Date: 20 Jun 2022
Reviewer's report:
Dear authors;
Thank you for sending your valuable study to BMC Gastroenterology. #t is a very interesting
and new topic about percutaneous liver biopsy. Study desing is well and number of patients and
biopsies are at a satisfactory level. Statistical analyze was made vey well. The major problem
about the manuscript is about language. I think it should be revised by a native speaker. Because
some sentences are too long and are confusing to understand. Except this condition, it is an
interesting topic and it worths publishing.
Best regards.
Review for 10.1186/s12876-022-02475-8 (2022)

Title: NAPSB as a predictive marker for prognosis and therapy associated with an immuno-hot
tumor microenvironment in hepatocellular carcinoma
Version: 1 Date: 12 May 2022
Reviewer's report:
The authors utilized several public datasets and bioinformatics tools to explore the expression
pattern and biological functions of NAPSB in HCC and found NAPSB was downregulated
in HCC, and high NAPSB expression correlated with improved survival outcome, immune
activation, immunomodulators, tumor-infiltrating immune cells (TIICs), T cell inflamed score,
sensitivity to immunotherapy and chemotherapy, tumor cell death. This study is well designed
and the findings are interesting. However it is bioinformatics analysis study and it would be very
nice if these finding can be validated further in own cohort.
Review for 10.1186/s12876-022-02475-8 (2022)

Title: NAPSB as a predictive marker for prognosis and therapy associated with an immuno-hot
tumor microenvironment in hepatocellular carcinoma
Version: 1 Date: 29 Jun 2022
Reviewer's report:
The potential biological functions of NAPSB were comprehensively explored in HCC,
including its differential expression,  prognosis value, and immunological role. We also
reported that high NAPSB expression was related to an immuno-hot TME and sensitive to
immunotherapy/chemotherapy, possibly affecting PANoptosis in HCC. The overall quality of
the article is good. The language is clear, and the logic is excellent. I think it is acceptable after
a minor revision.
1. A, B, C, and D in Figure 1 seem not aligned. Please make adjustments.
2. The font in Figure 5A is too dense. I hope the author can adjust it slightly.
3. The author conducted difference analysis and survival analysis in the Zhong nan cohort,
proving that the author had many samples. I hope the author can add WB or IHC experiments
or searched from the public database to check the expression of NAPSB protein in HCC.
Review for 10.1186/s12876-022-02467-8 (2022)

Title: Efficacy and safety of subanesthetic doses of esketamine combined with propofol in
painless gastrointestinal endoscopy: a prospective, double-blind, randomized controlled trial
Version: 2 Date: 03 Jun 2022
Reviewer's report:
1. English editing is mandatory.
2. I am not sure about the accuracy  of some of the reported P-values. They should be rechecked.
Review for 10.1186/s12876-022-02467-8 (2022)

Title: Efficacy and safety of subanesthetic doses of esketamine combined with propofol in
painless gastrointestinal endoscopy: a prospective, double-blind, randomized controlled trial
Version: 2 Date: 03 Jun 2022
Reviewer's report:
1.       In the abstract's results, this sentence should be deleted " Data from 260 patients were
analyzed.".
2.       In the introduction section, some sentences about pain and its mechanism should be
discussed. these references are strongly advised to be cited:
-          Skovlund, Eva, et al. "Sensitivity of pain rating scales in an endoscopy trial." The Clinical
journal of pain 21.4 (2005): 292-296.
-          Maghbool, Maryam, et al. "The effects of eugenol nanoemulsion on pain caused
by arteriovenous fistula cannulation in hemodialysis patients: a randomized double-blinded
controlled cross-over trial." Complementary therapies in medicine 52 (2020): 102440.
3.       The CONSORT flowchart, the label of analysis stage is incorrect (allocation).
4.       In table 1, what was your aim for the mentioning co-morbidities? Also, there is a typo
[0(1.5%)].
5.       In Table 5, I do not think that p-value for the first 4 rows is 1. Please recalculate it.
Review for 10.1186/s12876-022-02467-8 (2022)

Title: Efficacy and safety of subanesthetic doses of esketamine combined with propofol in
painless gastrointestinal endoscopy: a prospective, double-blind, randomized controlled trial
Version: 2 Date: 10 Jun 2022
Reviewer's report:
1. If the blindless anesthesiologist who administered the drugs was the one who performed
MMSE, how can blindness of the study be ensured?
2. "Phenylephrine 0.1 mg was injected when BP was below 30% of the baseline level" - what
is the rationale for this standard of care?
3. How did you define the procedure time? "procedure time (from the insertion of the gastroscope
to the withdrawal of the colonoscope), " sounds like 2 different procedures.
4. "A total of 260 patients undergoing painless gastrointestinal endoscopy " - how many of them
underwent EGD and how many of them underwent colonoscopy?
5. "No arrhythmia, nausea and vomiting, apnea (Table 4), hallucinations, delirium, depression,
and other psychosocial abnormalities were observed". Not sure if psychosocial abnormalities
the correct term here.
6. Some grammatical corrections (eg: indices instead of indexes, removing a from "Esketamine
is a dextrorotatory structure of ketamine with a twice as great anesthetic effect ... ") need to be
done. Suggest using some grammar correction software for ease.
Review for 10.1186/s12876-022-02467-8 (2022)

Title: Efficacy and safety of subanesthetic doses of esketamine combined with propofol in
painless gastrointestinal endoscopy: a prospective, double-blind, randomized controlled trial
Version: 4 Date: 17 Jul 2022
Reviewer's report:
I do not think all the comments have been addressed. I want to know how many patients
underwent upper GI endoscopy and how many underwent colonoscopy, and if there was any
difference between the 2 groups. The 2 procedures being quite different, it is extremely important
to address the effect of the new drug on the outcome of each individual procedure. Unless we
know the distribution of patients in each category, there is a chance that the results from one
of the procedure skews the entire results, and is mistakenly applied to patients undergoing the
other procedure. Unless this has been addressed, I don't think this is fit for publication.
Review for 10.1186/s12876-022-02474-9 (2022)

Title: The insoluble excretion of multi-matrix system mesalazine preparations in patients with
ulcerative colitis
Version: 3 Date: 21 May 2022
Reviewer's report:
Review Comment
In the manuscript by Ohtaki et al., the authors attempt to examine clinical features related to the
insoluble excretion of multi-matrix system mesalazine (MMX) in patients with ulcerative colitis
(UC). They concluded that defecation frequency and the extent of inflammation could affect the
insoluble excretion of MMX. While this reviewer agrees that the insoluble excretion of MMX
needs to be considered in patients with UC, there are several concerns for this manuscript.
(1) The authors performed the ROC analysis using the defecation frequency at the start of
treatment (DF) for predicting the insoluble excretion of MMX. Since the AUC is 0.687, this
result suggests that DF is not useful for predicting the insoluble excretion of MMX. This
reviewer does not believe this result supports the authors’ conclusion.
(2) The authors performed the multivariate logistic regression analysis employing 3 factors (i.e.,
disease type, stool consistency, and defecation frequency at the start of treatment). However,
given that 15 out of 102 patients experienced the insoluble excretion of MMX in this study,
the multivariate analysis employing 3 factors is not appropriate. The authors are advised to
reconsider the sample size and statistical analyses.
(3) The study design and the patient characteristics need to be described in more detail. Below
are just some examples.
(i) When the colonoscopy and/or other examinations to determine the disease type were
performed?
(ii) The UC disease activity of patients needs to be shown.
(iii) When the excretion of insoluble MMX was examined (e.g., during the first week after
starting treatment)?
(4) The authors need to describe if there were any differences in the clinical efficacy of MMX
between patients who experienced the excretion of insoluble MMX vs. those who did not.
Review for 10.1186/s12876-022-02474-9 (2022)

Title: The insoluble excretion of multi-matrix system mesalazine preparations in patients with
ulcerative colitis
Version: 3 Date: 26 May 2022
Reviewer's report:
Did the authors investigate the taking of H2 blocker or proton pump inhibitor? These drugs are
thought to affect the rate of insoluble exercise.
Clinical and endoscopic severity is also critical to be affected insoluble exercise.
Is there any evidence whether insoluble exercise is associated to clinical outcome?
Review for 10.1186/s12876-022-02474-9 (2022)

Title: The insoluble excretion of multi-matrix system mesalazine preparations in patients with
ulcerative colitis
Version: 3 Date: 28 May 2022
Reviewer:  Sakuma Takahashi
Reviewer's report:
It is my pleasure to review the manuscript entitled "The insoluble excretion of multi-matrix
system mesalazine preparations in patients with ulcerative colitis".
However, I have several concerns that need to be addressed before considering publication.
1) Please read the submission guidelines of BMC Gastroenterology carefully.
For example, the title page should list the full names and institutional addresses for all authors
 and  indicate the corresponding author. Please unify the reference style.
2)  The authors use "P" and "p" to notate "P-value".
Please use the same terminology throughout the document.
3)  The authors use "N" and "n" to notate "number".
Please use the same terminology throughout the document.
4)  I’d recommend that the authors enlarge Figure 1.a (Insoluble MMX tablets in the rectum)
and add arrows to tablets.
5)  The authors write "Bristol Stool Form Scale score at the start of treatment  44 : 32 : 26" in
Table 1. Please specify which scale corresponds to those numbers.
Review for 10.1186/s12876-022-02474-9 (2022)

Title: The insoluble excretion of multi-matrix system mesalazine preparations in patients with
ulcerative colitis
Version: 6 Date: 02 Aug 2022
Reviewer:  Sakuma Takahashi
Reviewer's report:
It is my pleasure to review the manuscript entitled "The insoluble excretion of multi-matrix
system mesalazine preparations in patients with ulcerative colitis".
The manuscript has been revised well. I think this manuscript will be acceptable after some
corrections have been done.
1)  The authors write that "Although the insoluble excretion rate tended to be higher in the
left-sided colitis and extensive colitis groups, the differences among the disease types were not
statistically significant (p=0.053)." If the patients were divided into two or three group, the
insoluble excretion rate might be significantly higher in extensive colitis group.
2) Please correct the description of 20th paper of the references. I can not find the title of the
paper.
Review for 10.1186/s12876-022-02474-9 (2022)

Title: The insoluble excretion of multi-matrix system mesalazine preparations in patients with
ulcerative colitis
Version: 7 Date: 10 Aug 2022
Reviewer:  Sakuma Takahashi
Reviewer's report:
It is my pleasure to review the manuscript entitled "The insoluble excretion of multi-matrix
system mesalazine preparations in patients with ulcerative colitis" again.
The manuscript has been revised well.
I think this manuscript is now acceptable for publication in BMC gastroenterology.
Review for 10.1186/s12876-022-02471-y (2022)

Title: Effectiveness of antiviral treatment in HBeAg-negative chronic hepatitis B patients with
normal or mildly elevated alanine aminotransferase: A retrospective study
Version: 1 Date: 09 Jul 2022
Reviewer:  Tawesak Tanwandee
Reviewer's report:
I have read the manuscript “Effectiveness of antiviral treatment in HBeAg-negative patients
with normal or mildly elevated alanine aminotransferase: a retrospective study” with interest.
There are some questions and comments
1. Since it was retrospective collection and use data from 2 hospitals, how can one control
whether the Fibroscan was done as mentioned? I assumed that all of these data were from patient
charts.
2. What are the criteria for normal and mildly elevated ALT
3. What was the NA treatment? Since baseline HBV DNA was low but response rate was slow.
4. Since Baseline LSM was high, how many patients had significant fibrosis
5. How about improving ALT after receiving treatment?
Review for 10.1186/s12876-022-02470-z (2022)

Title: Feasibility of quantification based on novel evaluation with stool DNA and fecal
immunochemical test for colorectal cancer detection
Version: 4 Date: 24 Dec 2021
Reviewer:  Keita Harada
Reviewer's report:
Recently, as a non-invasive colorectal cancer screening, analyzing fecal DNA has attracted
attention. Since the paper publication by Imperiale et al. (N Engl J Med. 2014 Apr
3;370(14):1287-97), methylation levels of BMP3 and NDRG4 in feces as well as Kras mutation
have been regarded as useful biomarkers for colorectal cancer, and then, test kits named
Cologuard® (Exact Sciences Corporation, WI, USA) have been released.
The novel combination method of stool DNA and fecal immunochemical test was performed
and evaluated in this study. The sensitivity and specificity of the method as CRC screening were
satisfactory. Moreover, it was suggested that it would be useful as monitoring for advanced CRC
treatment. The content of the article was also generally well described. However, there are some
queries for the authors to answer in order to accept the manuscript.
Major points
1. Why the combination of Kras mutation and BMP and NDRG4 methylation was chosen as
sDNA. You have done the PCR yourself instead of using a commercial kit. Did you try several
targets and choose these as the best? Or did you not consider any other options at all?
2. In general, the more factors you combine, the higher the sensitivity and specificity, I think. Is it
possible to get similar results by removing one of Kras mutations, BMP or NDRG4 methylation?
Or did you consider that you could get better results by adding some optional factors?
3. It is difficult to understand how to calculate the combination value. Is it quantitative or
qualitative? If quantitative, I would like to know what percentage of each factor is considered.
Please show a specific formula. I am also not sure how did you determine the threshold of 165
after treatment.
4. The tumors shown in figure 6 were both carcinomas? How did the novel evaluation after
polypectomy? I do not think that it was because of these polyps that the values in two patients
did not decrease after surgery.
Minor points
nothing
Review for 10.1186/s12876-022-02470-z (2022)

Title: Feasibility of quantification based on novel evaluation with stool DNA and fecal
immunochemical test for colorectal cancer detection
Version: 4 Date: 18 Mar 2022
Reviewer's report:
The authors constructed a novel evaluation with stool DNA and fecal immunochemical test(FIT)
for early colorectal cancer (CRC) detection and treatment of CRC.
The study included 14 patients with CRC and 345 patients from the screening population.
Patients had one of the following inclusion criteria: (1) Previous positive history of FOBT;
(2) Family history of colorectal cancer; and (3) Chronic intestinal disease such as diarrhea,
constipation, mucinous bloody stool, appendicitis, and biliary tract disease. Therefore most of
these patients had the indication to directly undergo endoscopy without second-line screening
stool test.
To evaluate the accuracy of the new screening test, a comparison with fist-line FOBT should
be performed.
Review for 10.1186/s12876-022-02470-z (2022)

Title: Feasibility of quantification based on novel evaluation with stool DNA and fecal
immunochemical test for colorectal cancer detection
Version: 5 Date: 26 Apr 2022
Reviewer:  Keita Harada
Reviewer's report:
Thank you for submitting the revised manuscript. The authors sincerely answered our questions
and revised the manuscript. However, it raised new concerns as follows.
Major points
1. The authors clearly stated in the revised version that this study was funded by New Horizon
Health Technology Co. Ltd. Then, althogh the authors declared in page 13 that there was no
potential COI,   there must be some conflict of interest between academia including the authors
and New Horizon Health Technology Co. Ltd. Please disclosure all potential COI.
2. Regarding the previous queri 4 of major points, what do you think was the reason that the
values had not fallen down below the threshould after CRC surgery in the two cases? Figure 6
is not necessary if you consider the residual polyps had nothing to do with the value remaining
positive.
Minor points
1. Please put a registered trade mark on the prodact name ‘ColoClear’, like ColoClear®
Review for 10.1186/s12876-022-02470-z (2022)

Title: Feasibility of quantification based on novel evaluation with stool DNA and fecal
immunochemical test for colorectal cancer detection
Version: 6 Date: 16 May 2022
Reviewer:  Keita Harada
Reviewer's report:
1. The authors clearly stated that this study was funded by New Horizon Health Technology
Co. Ltd. on page 6, line 11. In addition, they also described in revise letter that reagentes for
experiments were provided by NHHT Co. Ltd. Despite those, why is there no COI?? Is this a
matter of amount (too small)? I am not saying that I will not accept the manuscript when they
have COI with corporation. Please disclose to avoid misunderstanding. Othewise, please explain
the details of the contradiction.
2. Because the novel evaluation described in this paper was for detecting cancer, interpreting
that benign polyps were the cause of the marker elevation in these two patients, rather than the
resected advanced cancer, would affect the reliability of this paper. I think you were good to
delete figure 6.
Review for 10.1186/s12876-022-02470-z (2022)

Title: Feasibility of quantification based on novel evaluation with stool DNA and fecal
immunochemical test for colorectal cancer detection
Version: 8 Date: 29 Jul 2022
Reviewer:  Keita Harada
Reviewer's report:
Thank you for full consideration for my comments.
I have no additional comment.
Review for 10.1186/s12876-022-02459-8 (2022)

Title: Expression of Unfolded Protein Response Genes in Post-transplantation Liver Biopsies
Version: 1 Date: 13 Jun 2022
Reviewer's report:
This is a succinct study to examine transcriptome data generated from liver biopsy samples to
provide a link between human hepatic UPR gene expression and human cholestasis. The authors
found that CYP7A1 was increased along with an enrichment of the UPR pathway. The authors
also performed correlation analysis with serum patient information and their findings.  This is
a very well executed study with only a few minor suggestions.
author comments:
was there any correlation between CYP7A1 and serum chemistries?
similarly, since there was a correlation with FGF, did the authors look at FXR correlations?
why do the authors speculate that the ALP did not correlate with the UPR genes - were ALP
levels correlated with any of the examined markers?
Review for 10.1186/s12876-022-02459-8 (2022)

Title: Expression of Unfolded Protein Response Genes in Post-transplantation Liver Biopsies
Version: 1 Date: 24 Jun 2022
Reviewer's report:
I read the study by Liu et al with great interest. The authors sought to understand the unfolded
protein response genes in liver biopsies following liver transplantation. Although I congratulate
the authors' effort, I should admit that the study is very confusing for the following reasons
1- They claim in the abstract and in the main text that there are several genes associated with
CHolestatic liver diseases. However Table 1 clearly indicates that there were only 2 and 3
patients in the group and they where heterogeneous (PSC, PBC, AIH ??). So this claim should
not be correct.
2- Most importantly, these are liver transplant biopsies - considering that these were normal
livers transplanted and the recipient received immunosuppression (induction and maintenance
which could change many things). Timing of liver biopsies is missing. No information regarding
the fat content of livers transplant which could change gene expressions of those biopsies. Did
they correlate the gene profile of livers with donor Total bilirubin to conclude that these are
cholestatic?
3- Were these DCD livers? Which could be due to ischemic cholangiopathy and would change
the gene expression.
These examples can be increased since there were many unknowns. I think those unknowns
make the conclusions of the study very weak and unreliable
Review for 10.1186/s12876-022-02466-9 (2022)

Title: Fully covered self-expandable metal stent for intraprocedural or late-diagnosed Type-II
endoscopic retrograde cholangiopancreatography-related perforations
Version: 0 Date: 26 Jun 2022
Reviewer's report:
Bozbiyik et al. describes that Fully-covered self-expandable metal stent placement (FCSEMS)
for the type-II perforation at endoscopic retrograde cholangiopancreatography (ERCP) is safe
and effective regardless of timeline the perforation is found. They searched a large number
of ERCP cases and finally found 28 cases of type II perforation, which is small sample size.
Although the study is described important experiences, there are several concerns to confirm.
Major Revision:
1. Some endoscopists tend to place nasobiliary drainage tube without metallic stent, or even
after metallic stent placement for safe. How many patients were placed the nasobiliary tube?
Are there any difference of results between patients with and without nasobiliary tube? Please
describe it with additional rows in the table.
2. Additionally, if you place nasobiliary tube in some cases, please correct Methods as well to
describe indications.
3. In page 7, what is “septic-finding on CT”? Please describe with references.
4. In table 1, what is the definition of abnormal papilla anatomy?
5. In table 2, leukocytes and CRPs are analyzed by the highest values in the first 48 hours while
Figure 1 and Figure 2 depicts the first 7 days. I think the values in the tables should be in the
highest values in first 7 days. Please correct the table values to make them consistence.
6. In page 2, “Surgery is frequently used to treat Type-I perforations, whereas conservative
treatment is almost always successful in treating Type-III and Type-IV perforations.” should be
mentioned with references.
7. Most importantly, the authors mentions FCSEMS placement is safe even after the procedure.
However, there should be a golden time. Indeed, they decided to perform consecutive ERCP
within 7 to 48 hours. Therefore, it might be dangerous to perform the next ERCP after 48 hours
of the first ERCP because of severe infection or serious physical conditions. What do you think?
If so, please state a caveat that we should not wait too long until the next ERCP to close type II
perforation and mention rationale golden time with references.
Minor Revision:
1. In the Results of Abstract in Page 2, “whereas in te patients” can be corrected to “whereas
in ten patients”?
2. In table 1, the term "ERCP indication-stone" should be corrected to an appropriate form of
the term.
3. In page 7, the sentence “Oral intake was discontinued, IV hydration was started, antibiotherapy
was initiated, proton-pump inhibitor was initiated, monitorization was performed, full blood
count/biochemistry parameters were monitored, …” should be more concise. For example,
“antibiotherapy, proton-pump inhibitor, and monitorization of vital signs were initiated …”.
Review for 10.1186/s12876-022-02466-9 (2022)

Title: Fully covered self-expandable metal stent for intraprocedural or late-diagnosed Type-II
endoscopic retrograde cholangiopancreatography-related perforations
Version: 1 Date: 22 Jul 2022
Reviewer's report:
The authors have responded to comments from reviewers appropriately. This manuscript has
been well revised according the reviewer's comments.
Review for 10.1186/s12876-022-02466-9 (2022)

Title: Fully covered self-expandable metal stent for intraprocedural or late-diagnosed Type-II
endoscopic retrograde cholangiopancreatography-related perforations
Version: 1 Date: 26 Jul 2022
Reviewer's report:
Authors replied all questions appropriately. Please correct citations in the revised manuscript  so
we can read. Thank you for giving me an opportunity to review the paper.
Review for 10.1186/s12876-022-02464-x (2022)

Title: Consolidative Chemotherapy after Definitive Concurrent Chemoradiotherapy for
Esophageal Squamous Cell Carcinoma Patients: a Population Based Cohort Study
Version: 1 Date: 28 May 2022
Reviewer's report:
the study of consolidative chemotherapy after concurrent chemoradiotharypy in esophageal
squamous cell carcinoma is very valuable.  As we know that the number of chemotherapy
cycles concurrent with radiation has the relationship with the chemotherapy regiments. It is
recommended to add 2-3 cycles after the concurrent chemoradiotherapy with oxaplatin/cisplatin
plus 5-Fu and no addition with taxane in clinical guidelines. Dose the difference in this study
come from the different cycles of chemotherapy or the different regiments of chemotherapy? by
the way, the discussion has no content.
Review for 10.1186/s12876-022-02464-x (2022)

Title: Consolidative Chemotherapy after Definitive Concurrent Chemoradiotherapy for
Esophageal Squamous Cell Carcinoma Patients: a Population Based Cohort Study
Version: 1 Date: 17 Jun 2022
Reviewer:  Tetsuhiro Owaki
Reviewer's report:
It corroborates the results of a systematic review of previously reported population-based cohort
studies of oesophageal squamous cell carcinoma, which found that CCT was associated with a
significant improvement in OS in patients with LA-ESCC treated with dCCRT.
In my opinion, the paper is well methodological and does not raise any major issues.
However, some of the following questions need to be addressed
I presume, for some reason unique to Taiwan, that.
1. the reason for drawing the line at age 58
2. the meaning of the difference between northern and non-northern Taiwan
3. the reason for classifying BMI at 18.5.
The above should be added to the discussion.
Review for 10.1186/s12876-022-02464-x (2022)

Title: Consolidative Chemotherapy after Definitive Concurrent Chemoradiotherapy for
Esophageal Squamous Cell Carcinoma Patients: a Population Based Cohort Study
Version: 2 Date: 21 Jul 2022
Reviewer's report:
As a clinical study on chemoradiotherapy, the chemotherapy regimens and the number of
chemotherapy courses are unavoidable issues. Please describe in detail the chemotherapy
regimen and number of courses of treatment for  two groups of patients.
Review for 10.1186/s12876-022-02409-4 (2022)

Title: Comparison of Anal Dilatation Versus No Dilatation with A Standardized Dilator in
Reducing Pain After Hemorrhoidectomy: A Randomized Control Trial
Version: 4 Date: 24 Mar 2022
Reviewer:  Mohamed El-said
Reviewer's report:
First I would like to thank the authors for this smart and to the point manuscript.
I have few comments:
1- The preoperative continence was not assessed. If all patients were continent preoperatively,
this should be mentioned.
2- The degree of the postoperative FI was not assessed. If all cases who developped FI sufferred
only from minor FI (to flatus and soiling), at least this crude information should be mentioned.
3- If the authors are aware of other studies examining the short term effect (during the first
postoperative week) of anorectal surgeries involving anal dilatation (e.g. TEM) on continence,
discussing the results of some of these studies will enrich the discussion section.
4- The authors argued that preoperative anal dilatation decreases the risk of postoperative
stricture and thus decreasing postoperative pain. I think that too much excision of the anoderm
and rectal mucosa is the factor responsible for anal stricture.
I think this should be omitted from the discussion. Also the sentence discussing the benifit
of preoperative versus postoperative anal dilatation in the prevention and management of anal
stricture.
5- There are many studies that showed that internal sphincterotomy (chemical and surgical)
decreased postoperative anal pain and increase FI when combined with haemorrhoidectomy.
I think the authors should mention some of these studies and compare these methods with
controlled anal dilatation.
Review for 10.1186/s12876-022-02409-4 (2022)

Title: Comparison of Anal Dilatation Versus No Dilatation with A Standardized Dilator in
Reducing Pain After Hemorrhoidectomy: A Randomized Control Trial
Version: 4 Date: 12 Apr 2022
Reviewer's report:
The first point is about the time of dilation that is too long for a minor operation.in the other
studies that anal balloon dilation was done,the maximum time was 6 minutes.
Second:the most important concern about anal dilation is fecal inconsistence.7days is a short
time to evaluate fecal inconsistence.
Review for 10.1186/s12876-022-02409-4 (2022)

Title: Comparison of Anal Dilatation Versus No Dilatation with A Standardized Dilator in
Reducing Pain After Hemorrhoidectomy: A Randomized Control Trial
Version: 9 Date: 02 Jun 2022
Reviewer:  Mohamed El-said
Reviewer's report:
I would like to thank the authors for their response.
I have few comments:
1- Regarding the term "anal stricture", to me and to most English readers it means narrowing
of the anal canal by fibrosis due to excessive excision of the anoderm. I think the authors
use this term to indicate anal spasm which is contraction of anal sphincters in response to
hemorrhoidectomy. I think it is better to replace anal stricture in this manuscript by anal spasm.
2- The authors mentioned a study (reference 14) that assesses internal sphincterotomy
with hemorrhoidectomy and the authors mentioned that internal sphincterotomy could be
complicated by urinary incontinence which is not logical. I have reviewed this study
and it mentioned urinary retention not urinary incontinence as a complication of internal
sphincterotomy. This should be corrected.
3- The figure demonstrating Lord's anal dilatation has no reference and I think the figure is not
necessary; please you can omit this figure or mention its reference if you want to keep it.
Thank you.
Review for 10.1186/s12876-022-02444-1 (2022)

Title: Indocyanine green fluorescence imaging localization-assisted thoracoscopy revision
surgery after repair of esophageal atresia
Version: 2 Date: 23 May 2022
Reviewer:  Rony Sfeir
Reviewer's report:
Introduction :
1/ Delayed primary closure is not defined as a complication after EA repair.
2/ Original use of ICG
Material and methods
1/ Patients sel"e"ction  : Replace indocyanine green fluorescence  by ICG
2/ Surgical procedures :
-In section 1.1, you precised that you placed a two separate layers of flaps without saying what
kind of flaps are they? muscle? pericardium?
-In section 2, maybe you can cite previous surgical history of this patient with secondary repair
in this section and not in the disucssion
-Yo may also add some details about the fluorecence imaging mode. What means turn on and
off? Did we need a special camera or monitor?
Results :
You precise that one patient needed esophageal dilatation, Is that stenosis was prexisting to the
thoracospic procedure? Sometimes a new anastomosis is indicated when treating the recurrent
fistula.
Table 1 : The 9 patients characteristics is a more suitable title in my opinion and you can
delete line 5 in the table. The rate of tracheal stenosis is surprising? How you define it? Was it
independent from tracheomalacia? And twhat happens after the repair?
I found this study very original and interesting. The first condition is to possess this kind of
material.  Avoiding periesophageal and peritracheal injuries is mandatory and this technique
seems to answer to this objective and Im sure that also in open procedures it could help in some
cases.