JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-021-02021-y (2021)

Title: The effect of menopausal hormone therapy on gastrointestinal cancer risk and mortality
in South Korea: a population based cohort study
Version: 4 Date: 05 Jun 2021
Reviewer's report:
I appreciate the authors for their previous revisions. Now I only have a suggestion about the
propensity score matching, which was also indicated by Reviewer#2.
I agree with Reviewer#2 that the methods for propensity score matching should be described
in more detail. Although the authors argued that only age, income, and region were matched in
order to simplify the propensity score matching as much as possible, I do not think including
other variables to calculate the propensity score is a complex work that should be simplified. To
my knowledge, a propensity score is calculated by a logistic regression model to estimate the
probability of receiving MHT in this study. Suppose other variables in Table 1 may influence
the probability of receiving MHT or maybe possible confounders. In that case, I suggest also
put them into the logistic regression model to calculate the propensity score.
Further, the propensity score matching details were still not mentioned in the revised manuscript
(e.g., the algorithm for matching, using caliper for matching or not, with/without replacement).
I suggest providing the relevant details in the Method section.
Review for 10.1186/s12876-021-02021-y (2021)

Title: The effect of menopausal hormone therapy on gastrointestinal cancer risk and mortality
in South Korea: a population based cohort study
Version: 5 Date: 27 Jul 2021
Reviewer's report:
The authors did not address my previous comments. The authors agree with the comment
that the variables in Table 1 should be put into the logistic regression model to calculate the
propensity score (including Charlson comorbidity index). However, the authors did not do
so. The study conclusion is that menopausal hormone therapy (MHT) was associated with a
decreased diagnosis of GI cancer, especially for CRC and GC, and was significantly associated
with decreased mortality from CRC and GC. According to Table 1, the Charlson comorbidity
index (CCI) score was significantly lower in the MHT group than the non-MHT group. As the
CCI was initially designed to predict the mortality risk, the difference of CCI between treatment
and control groups could be an important source of bias by confounding effect. If possible, I
would like to know the study results in which the CCI was also considered in the propensity
score matching method. Did the study results and conclusions become different?
In addition, regarding the propensity score matching method, the authors only mentioned that
“The algorithm used a caliper matching without replacement.” Please clearly specify the caliper
widths and the algorithm types. The authors could refer to the reference (Stat Med. 2014 Mar
15;33(6):1057-69. DOI: 10.1002/sim.6004).
Review for 10.1186/s12876-021-01990-4 (2021)

Title: Clinicopathological significance of HSP70 expression in gastric cancer: a systematic
review and meta-analysis
Version: 0 Date: 11 Aug 2021
Reviewer's report:
In this manuscript, Wang et al tried to show the clinicopathological meaning of HSP70 in GC
by meta-analysis. In general, the manuscript showed some work, the methods is fine. However,
the most recent included study for meta-analysis were published 5 years ago. Thus, it maybe
useless to publish such a meta-analysis. I suggest a review on the meaning of HSP70 in GC and
included most recent studies is more useful. My detailed comments is as followed:
1. The most recent included study for meta-analysis were published 5 years ago in 2016. Since
2016, many studies have also discussed the meaning of HSP70 in GC. Maybe unable to include
these studies in meta-analysis, the author could consider a review on this topic and provide more
information for readers.
2. The NOS score should be provided in detail by table.
3. The results “Association between HSP70 expression and TNM stage” should be provided in
detail. Are included studies used some criteria to define high and low TNM stage?
Review for 10.1186/s12876-021-01990-4 (2021)

Title: Clinicopathological significance of HSP70 expression in gastric cancer: a systematic
review and meta-analysis
Version: 0 Date: 14 Sep 2021
Reviewer's report:
Wang et al included 9 studies with 1,307 gastric cancer patients to explore clinicopathological
significance of HSP70 expression in gastric cancer using meta-analysis. They found that HSP70
expression was significantly correlated with higher differentiation degrees, intestinal gastric
cancer, and lymphovascular invasion but no significant correlation between HSP70 expression
and overall survival of gastric cancer patients. In generally, this meta-analysis was firstly
reported in current database, thus it has certain novelty, but there are some major concerns need
to address.
1. In the method part, the authors did not mention the time when the search on the database
was began.
2. The authors are from China, but they only search the English database, why they don’t search
Chinese databases to enlarger the number of included study.
Review for 10.1186/s12876-021-02014-x (2021)

Title: Fishing line assisted endoscopic placement of multiple plastic biliary stents for
unresectable malignant hilar biliary obstruction: a retrospective study
Version: 0 Date: 14 Aug 2021
Reviewer's report:
The study entitled “Fishing line assisted endoscopic placement of multiple plastic biliary stents
for unresectable malignant hilar biliary obstruction: a retrospective study” demonstrated an
interesting technique to prevent upward stent migration during the deployment of the following
stent(s) when performing multiple plastic stenting. Although this is a smart way to prevent it,
the number of cases and the design of this study could not convince to the conclusion that
recommended this as the preferred technique. I afraid this may not be the flavor for BMC
Gastroenterology. I would recommend this manuscript to submit as a video series of special
technique in the endoscopy related journal.
Minor points:
1. Unclear introduction, stent migration, upward or downward? How this developed? And the
real incidence? The introduction does not demonstrate the problem that can lead to the remedy
that the authors planned to do.
2. Methods: should explained more details of the technique.
3. Outcome: technical success may not be a good surrogate to compare as the stent insertion is
almost always successful no matter what technique is employed.
4. Time: the time spent for assemble the thread should be counted and I wonder this still makes
the FLA technique still faster or not.
Review for 10.1186/s12876-021-02014-x (2021)

Title: Fishing line assisted endoscopic placement of multiple plastic biliary stents for
unresectable malignant hilar biliary obstruction: a retrospective study
Version: 0 Date: 22 Sep 2021
Reviewer's report:
The aim of this study was to evaluate the feasibility and efficiency of the fishing line assisted
(FLA) method for preventing the complication.
However, this manuscript has some issues that need to be addressed.
1) As the authors mentioned, straight biliary stents are easier to migrate during multiple plastic
biliary stents placement. However, single pig-tail stent or inside stent may have prevented stent
migration without FLA method.
2) The idea of using fishing line to prevent stent migration is interesting. However, the use of
fishing lines in endoscopic therapy may be ethically problematic.
3) Types and size of plastic stents used in this study are unclear.
4) Details of patients’ characteristics are unclear.
5) How did the author make the side hole at the distal end of the plastic stents?
6) It is difficult to understand the process of retrieving the fishing line from the first  plastic
biliary stent  in Video1.
7) Specific P-value should be presented in the Tables.
Review for 10.1186/s12876-021-02014-x (2021)

Title: Fishing line assisted endoscopic placement of multiple plastic biliary stents for
unresectable malignant hilar biliary obstruction: a retrospective study
Version: 4 Date: 18 Oct 2021
Reviewer's report:
The authors still did not answer about the step of FLA technique clear enough in the methods.
This is very important for the readers to follow. I recommend to put figures that show the step of
FLA starting from stent insertion to the scope channel and so on with finishing with the fishing
line removal.
Lastly, as I mentioned the technical success would not be a good surrogate markers for this, the
authors should emphasise and display on the stent migration rate, cost and time spent for this
FLA technique by comparing with the conventional method.
Review for 10.1186/s12876-021-02014-x (2021)

Title: Fishing line assisted endoscopic placement of multiple plastic biliary stents for
unresectable malignant hilar biliary obstruction: a retrospective study
Version: 4 Date: 22 Oct 2021
Reviewer's report:
This manuscript is well revised.
Please round p-values to two significant figures/digits in Table1 and 2. ex) 0.938#0.94
Review for 10.1186/s12876-021-02014-x (2021)

Title: Fishing line assisted endoscopic placement of multiple plastic biliary stents for
unresectable malignant hilar biliary obstruction: a retrospective study
Version: 5 Date: 29 Oct 2021
Reviewer's report:
This revision is now good for publication. Thank you very much for your point-by-point editing.
Review for 10.1186/s12876-021-02020-z (2021)

Title: PNPLA3 genotype and fibrosis-4 index predict cardiovascular diseases of Japanese
patients with histopathologically-confirmed NAFLD
Version: 1 Date: 09 Oct 2021
Reviewer's report:
This is a retrospective analysis of risk factors for CVD, malignancy and liver-related events
in histo-pathologically confirmed NAFLD patients. The results showed that FIB4-index # 2.67
was a risk factor for the occurrence of each event.
(Major comments)
It is very interesting that the PNPLA3 CC type has a higher risk of cardiovascular events.
It would be great if you could tell us if there is a tendency for patients with PNPLA3 CC type
to have more complications related to CVD risk, for example DM or dyslipidemia. In the past,
it has been reported that fasting glucose and TG levels are higher in PNPLA3 CC patients[1].
It is necessary to adjust for these values in the analysis.
[1] Hotta K, Sekine A: Association of the rs738409 polymorphism in PNPLA3 with liver damage
and the development of nonalcoholic fatty liver disease. BMC Med Genet 2010, 11:172.
This study is a single-center analysis. I would be grateful if you could reanalyze the results in
a multi-center validation.
Is this a retrospective study of all patients, or only of those with adequate follow-up, as described
in the "Follow-up" section? Either way, as it is a retrospective study, it has one bias that needs
to be mentioned in the limitations.
Why did you not evaluate the association between histopathology, such as fibrosis, and the
event?
It would be better to state whether or not NAFLD has been diagnosed by an independent central
histological review.
The total number of histopathological findings in Table 1 is different from the total number in
Table 2, which should be reviewed.
(Minor comments)
Fib-4 index is not official; FIB-4 is the correct notation.
Does "stage" in Table 1 refer to the fibrosis stage? It needs to be corrected.
I think "diagnoss" in Page 10, Line 169 is a mistake, so please correct it.
Review for 10.1186/s12876-021-02020-z (2021)

Title: PNPLA3 genotype and fibrosis-4 index predict cardiovascular diseases of Japanese
patients with histopathologically-confirmed NAFLD
Version: 1 Date: 12 Oct 2021
Reviewer's report:
Summary
The aim of this study was to test the association of noninvasive metrics with the development
of cardiovascular disease (CVD), any cancer, and liver-related events in patients with
nonalcoholic fatty liver disease (NAFLD). The cohort comprised n=477 Japanese patients with
histopathologically confirmed NAFLD, followed for a median of 5.9 years. Main findings were
that a high baseline Fib-4 was  associated with increased rates of CVD, cancer, and liver-related
events. The PNPLA3 CC-genotype (that associates with lowest risk of NAFLD compared to CG
and GG) was associated with increased risk of CVD development in the cohort.
Comments
1) How were the clinical events defined? Please describe in Methods.
2) It was not clear why liver cancer is excluded as a cancer outcome. Please consider including
liver cancer as a separate outcome.
3) The limited number of events during follow-up limits statistical power. This should be
acknowledged.
3) Table 3: please include numbers of events and participants.
4) Figures: Consider removing the ticks denoting censoring on the KM-curves. They obscure
the lines.
5) page 13, bottom:
‘Mendelian randomization analysis recently indicated that the PNPLA3 genetic variant might
not be causally associated with the risk of CVDs.’
Please provide citation: PMID: 29228164, in addition to ref #22.
6) might the association between PNPLA3 CC and increased CVD rate be due to collider
bias? Please see https://www.nature.com/articles/s41467-020-19478-2 among other places for
the reasoning behind this comment.
7) The paper is easy to understand, and the figures and tables are clearly designed. Nevertheless,
the paper would benefit from revision for language and grammar.
Review for 10.1186/s12876-021-02020-z (2021)

Title: PNPLA3 genotype and fibrosis-4 index predict cardiovascular diseases of Japanese
patients with histopathologically-confirmed NAFLD
Version: 3 Date: 07 Nov 2021
Reviewer's report:
Thank you for the answers and corrections.
We have all questions answered carefully.
We look forward to further research to validate this study.
Review for 10.1186/s12876-021-02015-w (2021)

Title: Fecal Microbiota Profiling in Irritable Bowel Syndrome and Inflammatory Bowel Disease
Patients with Irritable Bowel Syndrome-Type Symptoms
Version: 2 Date: 05 Feb 2021
Reviewer:  Cesare Cremon
Reviewer's report:
This is a study assessing the role of intestinal microbiota in symptom generation in patients with
inflammatory bowel disease (IBD) in remission with or without irritable bowel syndrome (IBS)-
like symptoms, as compared with patients with IBS or healthy controls.
As compared with patients with Crohn’s disease (CD) in remission, patients with CD in
remission and IBS-like symptoms had an increase of Faecalibacterium and a decrease of
Fusobacterium, while no microbial differences were found in patients with ulcerative colitis
(UC) in remission with or without IBS-like symptoms.
The study is interesting; however there are several flaws that reduce the quality of the
manuscript:
IBS is characterized by abdominal pain and not by abdominal analgesia, as reported in Methods,
Participants and Setting, IBS patients. In addition, since 2016 diagnostic gold standard is
represented by the Rome IV criteria. Due to wrong definition and use of old criteria (Rome
III criteria), it is not clear who population with IBS is represented in this study. In addition, is
unclear why the authors used the old Rome III criteria for the identification of patients with IBS
and the new Rome IV criteria for the identification of patients with IBD in remission with IBS-
like symptoms.
This study was not controlled for age, sex, diet, medications. This information is of great value
since all these factors may impact on gut homeostasis and consequently on gut microbiota.
Although the manuscript is easy to read and understand, there are a few of typos in the text,
English language is sometimes poor and needs consistent revision.
In conclusion, data presented in this study, although interesting and promising, lack of some
consistence due to the study design, and further research is needed. Probably this study is better
suited to a Microbiology Journal.
Review for 10.1186/s12876-021-02015-w (2021)

Title: Fecal Microbiota Profiling in Irritable Bowel Syndrome and Inflammatory Bowel Disease
Patients with Irritable Bowel Syndrome-Type Symptoms
Version: 2 Date: 21 Apr 2021
Reviewer's report:
As stated in the conclusion, variety of microbioma and of ibs clinical data cause "inconclusive-"
conclusions. But this in unavoidable and related to the studied matter
Review for 10.1186/s12876-021-02015-w (2021)

Title: Fecal Microbiota Profiling in Irritable Bowel Syndrome and Inflammatory Bowel Disease
Patients with Irritable Bowel Syndrome-Type Symptoms
Version: 2 Date: 22 Jun 2021
Reviewer's report:
I carefully reviewed the manuscript by Cui et al.
The paper is interesting and well written.
However, it could be improved:
1) in the abstract the authors stated that IBS patients were diagnosed according to Rome IV
criteria, but in the main text they indicated Rome III criteria with regard for IBS patients and
Rome IV for IBD-IBS patients. I think that the same criteria should be used for every cohort
including IBS patients.
2) Fecal calprotectin levels should be assessed in order to evaluate remission of IBD patients,
especially in case of the concomitant presence of IBS symptoms, which could be confused with
an IBD flare
3) Dietary habits could modify intestinal microbiota. It is necessary to indicate what advices
were given to patients in order to avoid modifications related to diet.
Review for 10.1186/s12876-021-02015-w (2021)

Title: Fecal Microbiota Profiling in Irritable Bowel Syndrome and Inflammatory Bowel Disease
Patients with Irritable Bowel Syndrome-Type Symptoms
Version: 5 Date: 27 Oct 2021
Reviewer's report:
It is obviously difficult to obtain a definite result when you work on microbiota, due to the great
number of bacterial strains
Review for 10.1186/s12876-021-02016-9 (2021)

Title: Impact of Chemotherapy and Radiotherapy on the Survival of Elderly Esophageal Cancer
Patients Undergoing Surgery: A SEER Database Analysis
Version: 3 Date: 10 Mar 2021
Reviewer's report:
This is a retrospective study examining the benefit of additional radiotherapy or chemotherapy
after surgery of esophageal cancer in 1221 elderly patients.  Although various statistical methods
have been applied to reduce selection bias, this type of study is not free from inherent limitation.
1. first of all, I wonder if it is appropriate to include M1 patients for this study.
2. how the authors verify that radiotherapy or chemotherapy had been performed after surgery?
It is believed that the present conclusion can be maintained under the title presented only when
this problem is properly resolved.
3. Can patients with both radiotherapy and chemotherapy be considered patients treated with
concurrent chemoradiation? It is thought that comparison of chemoradiation vs. chemotherapy
would be important for choosing radiotherapy in situations where chemo is more commonly
administered when adjuvant Tx is required.
4. also, perioperative treatment usually differed by the primary tumor location, but the analysis
according to this had not been performed
5. margin status was also unknown, but the analysis is thought to be limited because there is no
appropriate record in SEER database. It should be further described in discussion and limitation
with more detail.
6. in fig 3 nomogram, why are Tx factors (radiotherapy/chemotherapy) missing?
minor point
1. many figures : fig 4,5, and one of 6/7 may be moved to supplementary figures.
2. some typos, e.g. trail -> trial
Review for 10.1186/s12876-021-02016-9 (2021)

Title: Impact of Chemotherapy and Radiotherapy on the Survival of Elderly Esophageal Cancer
Patients Undergoing Surgery: A SEER Database Analysis
Version: 6 Date: 17 May 2021
Reviewer's report:
- please describe 'the elderly' also in the abstract
- overall, English language editing are required
Review for 10.1186/s12876-021-02016-9 (2021)

Title: Impact of Chemotherapy and Radiotherapy on the Survival of Elderly Esophageal Cancer
Patients Undergoing Surgery: A SEER Database Analysis
Version: 6 Date: 26 May 2021
Reviewer's report:
In the revised manuscript titled “Impact of Chemotherapy and Radiotherapy on the Survival
of Elderly Esophagus Cancer Patients after Surgery: A SEER Database Analysis”, the authors
made improvement in this paper. There are some more edits should be addressed.
1. It should be 0.703 in the sHR in Results of the abstract. sHR: 0.535, 95%CI: 0.407-703,
P<0.001
2. Figure 1 of the cohort selection is confusing. Please list the number of patients in each
of the rectangles, and exclude patients step by step. The split of “propensity matching” and
“randomization” can be removed from the diagram. Please indicate the CRT and non-CRT as
the final cohort in the diagram. The matched cohort and training and validation cohort can be
described in the text.
2. Please limit your hazard ratio or p-value to two decimal points or two-digits to simplify the
text.
3. The term “crow” is awkward. Please replace it with patients. The term “cases” is used several
times in the text. If it is used to represent CRT patients, then it should be defined in the text. If
not, please replace it with “patients”.
4. In Fig 2, what is the difference between probability of CSD and survival probability? Is Fig 2A
the cancer cause specific probability of death predicted from the competing risk Cox regression
model? In Fig 2B, please label which line represent CRT and non-CRT. Also, please use equal
number of months such as 60 months for x-axis for Fig 2A and 2B.
5. In Fig4,  is Fig4C the survival probability estimated from the total study sample of 1099
patients? Fig 4A, and 4B were CRT treatment. It was labeled as Chemotherapy.
6. In the matched cohort, what is the 5-year survival probability for the CRT and non-CRT
group, is the difference different in the two groups?
Review for 10.1186/s12876-021-02016-9 (2021)

Title: Impact of Chemotherapy and Radiotherapy on the Survival of Elderly Esophageal Cancer
Patients Undergoing Surgery: A SEER Database Analysis
Version: 7 Date: 25 Aug 2021
Reviewer's report:
This is a retrospective study examining the benefit of additional radiotherapy or chemotherapy
after surgery of esophageal cancer in 1221 elderly patients.  Although various statistical methods
have been applied to reduce selection bias, this type of study is not free from inherent limitation.
1. first of all, I wonder if it is appropriate to include M1 patients for this study.
2. how the authors verify that radiotherapy or chemotherapy had been performed after surgery?
It is believed that the present conclusion can be maintained under the title presented only when
this problem is properly resolved.
3. Can patients with both radiotherapy and chemotherapy be considered patients treated with
concurrent chemoradiation? It is thought that comparison of chemoradiation vs. chemotherapy
would be important for choosing radiotherapy in situations where chemo is more commonly
administered when adjuvant Tx is required.
4. also, perioperative treatment usually differed by the primary tumor location, but the analysis
according to this had not been performed
5. margin status was also unknown, but the analysis is thought to be limited because there is no
appropriate record in SEER database. It should be further described in discussion and limitation
with more detail.
6. in fig 3 nomogram, why are Tx factors (radiotherapy/chemotherapy) missing?
minor point
1. many figures : fig 4,5, and one of 6/7 may be moved to supplementary figures.
2. some typos, e.g. trail -> trial
Review for 10.1186/s12876-021-02016-9 (2021)

Title: Impact of Chemotherapy and Radiotherapy on the Survival of Elderly Esophageal Cancer
Patients Undergoing Surgery: A SEER Database Analysis
Version: 7 Date: 07 Sep 2021
Reviewer's report:
To authors: The paper is improved in its clarity and readability after the revision. There a few
minor comments for the paper.
1. In the method session, since the specific number of patients excluded in the study was reported
in figure 1, authors need not to repeat it in the method session.
2. What is median age and the interquartile of age?
3. In Table 2, please spell out sHR and CSD in the title.
Review for 10.1186/s12876-021-02016-9 (2021)

Title: Impact of Chemotherapy and Radiotherapy on the Survival of Elderly Esophageal Cancer
Patients Undergoing Surgery: A SEER Database Analysis
Version: 10 Date: 21 Sep 2021
Reviewer's report:
Overall, the authors addressed the reviewer's comment mostly. Thanks for your efforts.
However, one remnant issue remained: In the last paragraph of results section, the authors
described 'the superiority of the nomogram model over the TNM model' but the presented c-
indexes were very similar and did not seemed statistically significant. This sentence would better
be revised.
Review for 10.1186/s12876-021-02016-9 (2021)

Title: Impact of Chemotherapy and Radiotherapy on the Survival of Elderly Esophageal Cancer
Patients Undergoing Surgery: A SEER Database Analysis
Version: 10 Date: 06 Oct 2021
Reviewer's report:
The revised paper improved its clarity and quality. Here are two minor comments:
1. In the result session with subtitle of "Analysis in Pre-match Cohort", the following sentences
"... histological grade ("poorly or un-differentiation grade"...) repeated all the hazard ratio listed
in the results table. I'd suggest to remove those repeated result and simplify it as "... poorly or
un-differentiated grade, tumor size #33 mm, T stage >T1, positive lymph nodes, and metastasis
diseases had associated with increased risk of death.".
2. In the 3rd paragraph of the discussion session, I'd suggest to delete the following sentence
since these are results. The discussion should focus on why CRT treatment in low-risk patients.
Here are the sentences that can be removed "Using the variables mentioned above, a nomogram
was established to estimate the risk score for every patient, and the high- and low-risk groups
were derived from the whole-population cohort. With a series of analyses, CRT was shown to
decrease the probability of CSD and to improve the survival in the high-risk group, indicating
that elderly patients with EC characterized as middle- and upper-third of tumor location, poorly-
and undifferentiated of histological grade, # 33 mm of tumor size, advanced T stage, positive
lymph node, and/or metastasis tend to benefit from the relatively aggressive treatment. ".
Review for 10.1186/s12876-021-02011-0 (2021)

Title: Independent associations of thyroid-related hormones with hepatic steatosis and insulin
resistance in euthyroid overweight/obese Chinese adults
Version: 1 Date: 18 Jul 2021
Reviewer's report:
I think this study is interesting because it addresses the relationship between NAFLD and thyroid
function in middle-aged adults with normal thyroid function. We also appreciate that the analysis
was carried out using a simple and less invasive test. However, as the authors state in the
discussion, it will be important to compare thyroid function in non-obese and non-NAFLD
patients with a similar patient background. In addition, since CAP and FLI have their limitations,
it would be important to test whether they correlate with hepatic steatosis assessed by other
modalities such as L/S ratio using CT, MRI and liver biopsy.
What are your views on the following two points?
1. Reference 26 demonstrates that the mRNA expression of leptin and D1, and activity of D1
in adipocytes are increased in obese patients compared to non-obese patients. In this study, did
you measure serum leptin? This may support your hypothesis that compensatory elevated FT3
increase energy expenditure and maintain metabolic homeostasis in obese middle-aged adults
with normal thyroid function.
2.  Do you think that supplementation with liothyronine or levothyroxine improves hepatic
steatosis, or do you have data or reports to this effect?
Review for 10.1186/s12876-021-02011-0 (2021)

Title: Independent associations of thyroid-related hormones with hepatic steatosis and insulin
resistance in euthyroid overweight/obese Chinese adults
Version: 1 Date: 24 Sep 2021
Reviewer's report:
Authors give in the Discussion section some interpretations of thyroid hormones involved in
NAFLD, but they should honestly recognise that the inner mechanism underlying NAFLD are
far from being clarified, thus many pieces of research are still needed as evident in....J. Clin.
Med. 2020, 9(1), 15; https://doi.org/10.3390/jcm9010015
Cumulative data of all the patients with overweight/obesity should be firstly presented to
appreciate the characteristic of the selected population.
How many patients were diagnosed suffering from NAFLD by FLI and how many with CAP
or both ?
What about diet and physical activity of the selected patients and how was this evaluation
performed?
Review for 10.1186/s12876-021-02022-x (2021)

Title: Outcomes of endoscopic submucosal dissection for gastroesophageal reflux disease
(ESD-G) for medication-refractory gastroesophageal reflux disease: 35 cases underwent ESD-
G including 15 cases followed more than 5 years.
Version: 1 Date: 06 Jun 2021
Reviewer's report:
The inclusion criteria of ESD-G are not clear. The PPI refractory GERD might include
Functional heartburn (FH) and Reflux hypersensitivity (RH). Both the 24 hour-pH and
impedance monitoring are necessary for the exclusion of these diseases. Furthermore, 24 hour-
pH monitoring is also required for checking the insufficient effect of PPI. Therefore, the PPI
refractory GERD in this study might include several functional esophageal disorders, and I
concern about that the patients with FH and RH might be performed ESD-G in this study.
The way of evaluation is not unified. Despite containing many patients with NERD, it is strange
to evaluate the effect of ESD-G by endoscopy. FSSG is also not effective for the evaluation of
FH and RH. The evaluation of gastric acid secretion suppressants is not sufficient in the cases
without 24 hour-pH monitoring.
Review for 10.1186/s12876-021-02022-x (2021)

Title: Outcomes of endoscopic submucosal dissection for gastroesophageal reflux disease
(ESD-G) for medication-refractory gastroesophageal reflux disease: 35 cases underwent ESD-
G including 15 cases followed more than 5 years.
Version: 1 Date: 18 Jun 2021
Reviewer's report:
This manuscript reported the utility of ESD-G for refractory GERD.
This technique seems to be useful for this kind of situation. However, there are some problems
before publication.
1. In this manuscript, there are few tables. So the results of this study is difficult to understand.
Author should make representative table for easy understanding.
2. In this method, how to decide the area to resect is important. Author should state the method
of this treatment more clearly.
3. The indication of this treatment is very important. Author should state the indication of this
treatment in the method section.
4. In this manuscript, author submitted the figure of endoscopic images before and after this
procedure in the antegrade position. I think endoscopic image of retrograde position is also
important, so author should provide the image of retrograde position.
Review for 10.1186/s12876-021-02022-x (2021)

Title: Outcomes of endoscopic submucosal dissection for gastroesophageal reflux disease
(ESD-G) for medication-refractory gastroesophageal reflux disease: 35 cases underwent ESD-
G including 15 cases followed more than 5 years.
Version: 1 Date: 20 Aug 2021
Reviewer:  Shiko Kuribayashi
Reviewer's report:
Summary
“Long-term outcomes of endoscopic submucosal dissection for gastric esophageal reflux disease
for medication-refractory gastroesophageal reflux disease” reported effectiveness of ESD-G for
medication-refractory GERD not only for short term but also for long term. I am impressed by
the challenging treatment, but I have several comments.
Major comments
1. As authors noted, the effects of ESD-G may be a placebo effect. No change of the number
of reflux events after ESD-G and the improvement of dysmotility scores represent the placebo
effect. Authors should confirm the effectiveness of ESD-G with a sham treatment.
2. Since there are too many missing data, results are difficult to be evaluated. Impedance-pH
monitoring was performed in less than half of patients. In addition, long term effects of ESD-G
were evaluated in only less than half of patients, which is the primary outcome of this manuscript.
3. Did you perform impedance-pH monitoring on PPI or off PPI? Moreover, did you perform
esophageal manometry before impedance-pH manometry? Furthermore, how did you locate
esophageal pH sensor without manometry if you did not perform esophageal manometry. How
was esophageal motility in enrolled patients if you perform esophageal manometry? Authors
should describe details about it.
4. What kinds of patients were enrolled in the study? Since impedance-pH monitoring
was performed, patients could be categorized as reflux esophagitis, true NERD, reflux
hypersensitivity or functional heartburn. In addition, were the outcomes of ESD-G among these
patients different?
5. If the strength of the study is long-term outcome, authors should focus on it. If authors want
to discuss both short-term and long-term effects, the relationship between short-term and long-
term should be discussed. Current form of the manuscript is not suitable.
Minor comment
1. “gastric esophageal reflux” in the title should be “gastroesophageal reflux”.
Review for 10.1186/s12876-021-02022-x (2021)

Title: Outcomes of endoscopic submucosal dissection for gastroesophageal reflux disease
(ESD-G) for medication-refractory gastroesophageal reflux disease: 35 cases underwent ESD-
G including 15 cases followed more than 5 years.
Version: 4 Date: 21 Sep 2021
Reviewer:  Shiko Kuribayashi
Reviewer's report:
Authors did not answer my questions appropriately. I ask them one more time which should be
answered adequately.
Major comments
1. Authors answered that a sham treatment cannot be performed; however, I think that it can be
performed. Just endoscopy is performed without resection, which must be the sham treatment.
2. Since there are too many missing data, results are difficult to be evaluated. Impedance-pH
monitoring was performed in less than half of patients. In addition, long term effects of ESD-G
were evaluated in only less than half of patients, which is the primary outcome of this manuscript.
This limitation should be noted in the discussion section clearly.
3. Did you perform impedance-pH monitoring on PPI or off PPI? Moreover, did you perform
esophageal manometry before impedance-pH manometry? Furthermore, how did you locate
esophageal pH sensor without manometry if you did not perform esophageal manometry? How
was esophageal motility in enrolled patients if you perform esophageal manometry? Authors
should describe details about it. Authors did not answer this question at all.
4. What kinds of patients were enrolled in the study? Since impedance-pH monitoring
was performed, patients could be categorized as reflux esophagitis, true NERD, reflux
hypersensitivity or functional heartburn. In addition, were the outcomes of ESD-G among these
patients different? Authors did not answer this question appropriately.
5. If the strength of the study is long-term outcome, authors should focus on it. If authors want
to discuss both short-term and long-term effects, the relationship between short-term and long-
term should be discussed. Current form of the manuscript is not suitable. Authors’ answer was
not appropriate.
Review for 10.1186/s12876-021-02022-x (2021)

Title: Outcomes of endoscopic submucosal dissection for gastroesophageal reflux disease
(ESD-G) for medication-refractory gastroesophageal reflux disease: 35 cases underwent ESD-
G including 15 cases followed more than 5 years.
Version: 4 Date: 05 Oct 2021
Reviewer's report:
I understood authors' explanation.
This paper is sufficient to be accept.
Review for 10.1186/s12876-021-02022-x (2021)

Title: Outcomes of endoscopic submucosal dissection for gastroesophageal reflux disease
(ESD-G) for medication-refractory gastroesophageal reflux disease: 35 cases underwent ESD-
G including 15 cases followed more than 5 years.
Version: 5 Date: 21 Oct 2021
Reviewer:  Shiko Kuribayashi
Reviewer's report:
Authors answered my questions; however, their answers were not enough.
Major comments
1. How did you recognize location of the EGJ? X-ray could not help to recognize the location
of the EGJ. HRM was performed in all patients? Data regarding HRM (diagnoses of esophageal
motility) and impedance-pH monitoring (number of acid and non-acid reflux events and
relationship between symptom and reflux event) should be shown in Table 1. Although there
were several limitations in the study, these data can be shown according to your explanation.
This is very important to understand indications of ESD-G.
Review for 10.1186/s12876-021-02022-x (2021)

Title: Outcomes of endoscopic submucosal dissection for gastroesophageal reflux disease
(ESD-G) for medication-refractory gastroesophageal reflux disease: 35 cases underwent ESD-
G including 15 cases followed more than 5 years.
Version: 6 Date: 08 Nov 2021
Reviewer:  Shiko Kuribayashi
Reviewer's report:
Although there are many limitations, authors stated these limitations in the manuscript. I think
that the manuscript is now ready for publication.
Review for 10.1186/s12876-021-02002-1 (2021)

Title: Imaging Features of Intrahepatic Cholangiocarcinoma Mimicking a Liver Abscess: An
Analysis of 8 Cases
Version: 0 Date: 13 Sep 2021
Reviewer's report:
The complete final  morphological and histopathological  diagnosis of each cases would made
this MS more interesting .
Review for 10.1186/s12876-021-02002-1 (2021)

Title: Imaging Features of Intrahepatic Cholangiocarcinoma Mimicking a Liver Abscess: An
Analysis of 8 Cases
Version: 0 Date: 21 Sep 2021
Reviewer's report:
This manuscript aims to provide clarity on a frequently encountered clinical conundrum in the
practice of hepatobiliary Oncology, which is to accurately differentiate between a pyogenic liver
abscess and intrahepatic cholangiocarcinoma.
Three cases were discussed with excellent quality images from diagnostic ultrasound, CT scan
and an MRI. Based on these cases certain unique radiologic features were defined that could help
identify intrahepatic cholangiocarcinoma mimicking a liver abscess.  These features include lack
of prominent blood supply to the lesion, associated lymphadenopathy, a single hepatic artery
supplying the wall of the lesion and the marginal parenchyma, a rough and irregular inner wall of
the lesion, and rapid increase and then decrease in enhancement of the wall with phase contrast.
Notably, none of the lesions had the classic double target sign associated with liver abscesses.
Potential limitations of this study include a very small number of patients and lack of inclusion
of lesions that were atypical presentation of liver abscesses. Furthermore, the reviewer would
recommend inclusion of cases  where the lesion in question was smaller in size than the ones
presented on the manuscript.
Review for 10.1186/s12876-021-02012-z (2021)

Title: TPH1 gene polymorphism rs211105 is associated with serotonin and tryptophan
hydroxylase 1 concentrations in acute pancreatitis patients
Version: 1 Date: 14 Oct 2021
Reviewer's report:
This is a well-written manuscript that presents novel data on an important topic. The
methodology was robust, and the conclusions were drawn appropriately. Therefore, I have no
hesitation in recommending this manuscript for publication.
Review for 10.1186/s12876-021-02012-z (2021)

Title: TPH1 gene polymorphism rs211105 is associated with serotonin and tryptophan
hydroxylase 1 concentrations in acute pancreatitis patients
Version: 1 Date: 17 Oct 2021
Reviewer's report:
The results did not provide evidence that rs211105 has a "causal effect"  on acute pancreatitis
because the study design is a cross-sectional study. Maybe some adjustment for the title
from "TPH1 gene polymorphism rs211105 influences serotonin and tryptophan hydroxylase
1 concentration in acute pancreatitis patients" to  "TPH1 gene polymorphism rs211105 is
associated with serotonin and tryptophan hydroxylase 1 concentration in acute pancreatitis
patients" is more appropriate.
Review for 10.1186/s12876-021-02000-3 (2021)

Title: Management of post-operative pancreatic fistulas following Longmire-Traverso pylorus-
preserving pancreatoduodenectomy by endoscopic vacuum-assisted closure therapy
Version: 2 Date: 13 Sep 2021
Reviewer:  Antonino Granata
Reviewer's report:
The manuscript is well written and built. The data are well collected and described.
In my opinion the proposed handmade device can be very hazardous in clinical practice even in
skilled hands. at the best of my knowledge, are available on the market dedicated devices with
“CE” mark, why did the authors decide to use a handmade device?
Vacuum therapy can be helpful in treatment in upper- GI fistula even pancreatic, but in
my opinion, the authors should compare with other well-established techniques available in
literature to exalt the proposed data.
I’s a very small court of patient this is a major limitation of the study.
Please explain the issues about the exitus of the "patient 8"
Review for 10.1186/s12876-021-02000-3 (2021)

Title: Management of post-operative pancreatic fistulas following Longmire-Traverso pylorus-
preserving pancreatoduodenectomy by endoscopic vacuum-assisted closure therapy
Version: 2 Date: 13 Sep 2021
Reviewer's report:
Dear Editors and Authors,
thank you for the possibility to revise this Manuscript.
The study is well written, with a nice overview of the problem and the “unmet clinical needs”.
The authors describe the technique accurately, with adequate iconography and sufficient details
of the patients characteristics and outcomes. Moreover, they adequately discuss the limits of
their proof-of-concept study.
I suggest accepting this paper.
I have however the following comments:
Major:
- The term “Pancreatogastric Insufficiency” is somehow misleading (as for example it could
theoretically also describe an insufficiency due to a stenosis). Even if I perfectly understood the
concept, is this a universally accepted definition? Can other terms better describe the situation
(e.g. “pancreatogastric fistula or dehiscence or leak). Furthermore, notwithstanding the chosen
definition, the authors should formalize the definition with a sentence (as for example “In our
paper PI is defined as a continuity defect….”)
- Can you please further discuss the role of EVT in the bleeding of Patient 8? How was it
diagnosed? Did a CT scan show the source of the bleeding? Is the absence of upper GI bleeding
sufficient to exclude a role of EVT in this episode? I think the Authors should maintain a more
cautious attitude when discussing this point. Can the Authors also discuss the film versus sponge
topic in this case? Isn’t the sponge more traumatic? This (and the fact that a lower pressure [100
mmHg] was used) might corroborate the unlikelihood of a correlation. Also in the abstract the
“not related to EVT” should be smoothened for a more dubitative sentence. (e.g. There were no
adverse events directly attributable to EVT, but one patient… unlikely related… )
Minor:
- In the Introduciton, a “partial” pancreaticoduodenectomy sounds misleading;
pancreaticoduoenectomy is a partial pancreasectomy.
- Please tone down the term “promising” in the Discussion (it can be acceptable in the abstract
and conclusions). As perfectly underlined, the study has no “control” group and some of the
patients might have also recovered without EVT
Review for 10.1186/s12876-021-02000-3 (2021)

Title: Management of post-operative pancreatic fistulas following Longmire-Traverso pylorus-
preserving pancreatoduodenectomy by endoscopic vacuum-assisted closure therapy
Version: 5 Date: 24 Oct 2021
Reviewer's report:
Dear Authors,
thank you for this revised Mauscript. All comments by my side were addressed.
Review for 10.1186/s12876-021-01995-z (2021)

Title: Clinical outcomes of surgical resection versus radiofrequency ablation in very-early#stage
hepatocellular carcinoma: A propensity score matching analysis
Version: 1 Date: 13 Oct 2021
Reviewer's report:
I have the following comments:
1) Which method was used for propensity score matching? reading the paper i suppose authors
used the nearest neighbour method but his should be specified.
2) why a caliper of 0.02 was used?
3) i have some concerns on the collinearity of some variables used for the propensity score
matching (particularly, cirrhosis and albumin.....)
4) Was there any impact of eventual post-treatment adjuvant therapies? in this regard, cite the
paper PMID: 25974743
5) The concept of post-recurrence survival after radical therapies should be at least mentioned
in the discussion. In this regard, cite the study PMID: 25085684
Review for 10.1186/s12876-021-01998-w (2021)

Title: Diagnostic yield of esophagogastroduodenoscopy, colonoscopy, and small bowel
endoscopy in Thai adults with chronic diarrhea
Version: 1 Date: 30 May 2021
Reviewer's report:
Dear the Editor and authors,
I have reviewed the manuscript submission ID 35d401d3-bc5b-4dd1-8f8c-65051bed6548
entitled “Diagnostic performance of esophagogastroduodenoscopy, colonoscopy, and small
bowel endoscopy in Thai adults with chronic diarrhea” with interest. However, there are many
major concerns as the following items;
Major concerns
1. The main limitation of this study was an irrelevant data of recruitment period of patients with
negative EGD and colonoscopy and patients underwent small bowel study. Why did the authors
include the patients with chronic diarrhea from January 2008 to December 2012 but evaluate
patients who underwent subsequent small bowel endoscopy from January 2018 to December
2018? The authors should collect the data of patients with chronic diarrhea from 2008 to 2018
and analyzed the diagnostic performance of all endoscopic methods which had been performed
in that period.
2. The diagnostic performance of any instrument should be based on the gold standard of disease
diagnosis and presented as sensitivity, specificity, PPV, and NPV. What is the gold standard for
diagnosing chronic diarrhea of this study? If the authors would like to present only the positive
rate of each method, they should revise the title and methodology.
3. As the author mentioned in the discussion part that Ref. 7 have shown the predictors for
small bowel mucosal diseases, the following sentences should be revised; “Furthermore, since
small bowel endoscopy is invasive and not widely available, a decision to perform small bowel
endoscopy should be carefully made. Therefore, we evaluated predictive factors for small bowel
mucosal diseases in patients with negative EGD and colonoscopy who underwent small bowel
endoscopy in which diagnostic endoscopy would be of benefit.”
4. In Table 1, how did the authors prove that “Self-limiting colitis” was from infectious process?
5.  All numbers of patients in the result should be demonstrated as n/N (%) to make the readers
to follow the manuscript easier.
6. Dose the “PE” on page 11 stand for push enteroscopy? If yes, please put it in the bracket
behind the original word before using it.
7. In discussion part, the author said that “Furthermore, all positive findings were also detected if
ileocolonoscopy was performed,…….” This information is different from the result which said
that “All patients whose EGD found positive findings also had abnormal colonoscopic findings
except for one with lymphoma who underwent only EGD.” Please clarify.
8. Because this study was a retrospective study and collected small sample size from a sole
hospital, this may not proper to propose the Figure 3. Please consider omit the Figure 3 until
the data from prospective study with larger included patients is conducted and confirmed your
hypothesis.