JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-023-02954-6 (2023)

Title: Acute cholecystitis in old adults: the impact of advanced age on the clinical characteristics
of the disease and on the surgical outcomes of laparoscopic cholecystectomy
Version: 1 Date: 11 May 2023
Reviewer's report:
I would congratulate with the authors for the nice manuscript which highlights the risk factors
associated with laparoscopic cholecystectomy in elderly patients with acute cholecystitis. I
would agree that patients' selection is key to provide safe surgical care in this group of patients.
This is an important take home message.
I have some points I would like to raise, as follows:
Methods
1)  I have not clear if all the subjects included in the study underwent emergency LC. Can the
authors clarify, please?
2) If patients underwent emergency surgery, what was the mean time between admission and
LC?
3) Given that some had PTGBD first, I would imagine LC was performed at a later stage. In
such cases, was LC performed during the same admission or electively?
Results
1) Male sex was more represented in the whole study population. It is common evidence that
AC occurs more frequently in female patients, at least in Western countries. Is the epidemiology
of AC different in the authors' area?
2) Subjects in group 3 had higher ASA and CCI. The Tokyo guidelines state that ASA > 3 and
CCI > 6 are risk factors of poor surgical outcomes, in case urgent LC was taken into account.
Can the authors clarify if patients with high ASA and CCI received emergency surgery or if
they were optimised before having LC?
2) Given that CCI scores increases with age, I think it is not surprising that group 3 had higher
CCI. May I suggest that the authors mention that in the discussion.
3) In those patient who had PTGBD first, what was the mean time between PTGBD and LC?
4) The estimated blood loss was higher in group 3. Can the authors explain why?
5) The authors mentioned that 353 patients were found having CBD stones. How were they
treated, with ERCP followed by LC or LC and CBD exploration?
5a) In case of preoperative ERCP, what was the mean time between ERCP and LC? I think   this
information should be mentioned in the results.
5b) If patients underwent CBD exploration, how was that performed, via the trans cystic or
trans choledochal route? Did they develop postoperative complications? I think that would be
mentioned as well.
6) The hospital stay was longer in group 3. I would imagine that such a result was secondary
to the higher rate of complications. However, in common practice elderly subjects would likely
need physiotherapy to improve their postoperative mobilization. Also, it is not infrequent to deal
with social issues in this category of patients (i.e., those who live alone and need support in their
daily care). I think these aspects would account for a longer hospital stay too. Can the author
comment on that, please? I would also suggest to comment this aspect in the discussion.
Review for 10.1186/s12876-023-02954-6 (2023)

Title: Acute cholecystitis in old adults: the impact of advanced age on the clinical characteristics
of the disease and on the surgical outcomes of laparoscopic cholecystectomy
Version: 1 Date: 23 Jun 2023
Reviewer's report:
Study design is flawed.
Study was aimed to compare complication/outcome between three age groups .There are so
many confounding variables between the groups which need to be matched before drawing
conclusions authors have drawn.
Authors should thoroughly review literature on the subject.
In case authors need to identify poor risk factors in patients with acute cholecystitis then they
should design study accordingly.
Review for 10.1186/s12876-023-02954-6 (2023)

Title: Acute cholecystitis in old adults: the impact of advanced age on the clinical characteristics
of the disease and on the surgical outcomes of laparoscopic cholecystectomy
Version: 2 Date: 05 Aug 2023
Reviewer's report:
General
I am grateful for the replies of the authors. That helps greatly in achieving a better comprehension
of their analysis.
I think the study results are interesting as they quantify the factors that increase the outcomes
of surgery in old adults with acute cholecystitis. Although aspects such the increased incidence
of gallbladder cancer and adverse surgical outcomes in the elderly are known, this large series
interprets patients’ characteristics and frames them into practical conclusions. Moreover, the
large study population allows to draw evidence-based remarks. Finally, I appreciate the authors’
comments on some potential study limitations, such as the selection bias. Nevertheless, I think
that can be overcome by the impact that results may have on the daily practice.
Below are some comments on specific sections of the study,  which would suggest minor
amendments to the text.
Other than that, I would be happy to recommend the publication of the study.
Title
Page 1, lines 1-2. Can the authors explain what “clinical characteristics” refer to? If they refer to
the clinical characteristics of AC, I would  suggest to rephrase the title i.e., “Acute cholecystitis
in old adults: the impact of advanced age on the clinical characteristics of the disease and on the
surgical outcomes of laparoscopic cholecystectomy”.
Background
Page 4, line 51. I would suggest to use “gallstones” instead of “gallbladder stones”.
Page 4, line 62. Can the authors clarify what “clinical characteristics” refer to? Is that clinical
characteristic of AC? if so, can they rephrase the sentence, please?
Results
Page 8, line 150. “…median interval from PTGBD to LC of 5 days.” Can the authors describe
the range (minimum and maximum n. of interval days), please?
Review for 10.1186/s12876-023-02954-6 (2023)

Title: Acute cholecystitis in old adults: the impact of advanced age on the clinical characteristics
of the disease and on the surgical outcomes of laparoscopic cholecystectomy
Version: 4 Date: 09 Sep 2023
Reviewer's report:
Thank you for your replies. I am happy with them and congratulations for your excellent work.
Review for 10.1186/s12876-023-02892-3 (2023)

Title: Can balloon-assisted enteroscopy predict disease outcomes in patients with small-bowel
crohn’s disease?
Version: 1 Date: 21 May 2023
Reviewer's report:
1. In introduction (paragraph 3), authors mentioned "Therefore, this study was designed to
determine the role of BAE in the endoscopic assessment of disease activity and the predictive
value for the risk of surgery in small bowel CD patients."
However in materials and method (outcomes and covariates), authors stated  "primary outcome
was the evaluation of the risk of surgery according to the small-bowel SES-CD (0–6 vs #7). The
secondary outcome was the assessment of the association of the enteroscopic finding (presence
of any ulcer and degree of stricture) with surgery. In addition, we tried to identify the predictors
of surgery in the overall patient cohort."
--> State directly in paragraph 3, for an example: "Therefore, this study was designed to assess
surgery risk in small bowel CD patients based on BAE findings using validated small bowel
SES-CD........."Mention also the secondary and tertiary outcome clearly in introduction.
2. In materials and method (Balloon-assisted enteroscopy, assessment index, and follow-up),
authors wrote "The examination was performed under conscious sedation."
--> Is conscious sedation the standard anesthesia method for enteroscopy in your center?  I am
asking this because enteroscopy is time consuming, technically demanding and potentially make
patients uncomfortable.
3. Please add total enteroscopy rate in all subjects. Data shows that total enteroscopy is relatively
difficult to achieve with single ballon enteroscopy,yet in this study all segments of small bowel
should be evaluated thoroughly.
4. In materials and method (Balloon-assisted enteroscopy, assessment index, and follow-up)
paragraph 3, authors stated "The small-bowel SES-CD values ranged from 0 to 12 and were
divided into of 0–6 vs #7, in which a cutoff of 7 points was set by a receiver operating
characteristics curve"
--> Please describe the detailed reason why authors set 7 as cut-off point. The statistical analysis
of ROC curve can be added.
Review for 10.1186/s12876-023-02892-3 (2023)

Title: Can balloon-assisted enteroscopy predict disease outcomes in patients with small-bowel
crohn’s disease?
Version: 3 Date: 11 Jul 2023
Reviewer's report:
1. Why did the authors not include the multivariate HR, including small bowel SES-CD and CD
duration, within the Abstract?
2. Since total enteroscopy was not performed, how did the authors ensure that the selected
segment represented the most severe condition? In response to this, please consider adding the
following or an appropriate sentence in the Materials and Methods section “During the baseline
assessment of small-bowel CD patients, small-bowel SES-CD is checked for each segment by
inserting the enteroscopy as deep as possible, considering the estimated location on the CSI and
patient tolerability.” Should this be regarded as a limitation of the study?
Review for 10.1186/s12876-023-02960-8 (2023)

Title: Comparison of the efficacy and safety between rivaroxaban and dabigatran in the
treatment of acute portal vein thrombosis in cirrhosis
Version: 2 Date: 17 Jun 2023
Reviewer's report:
This retrospective study compared the efficacy and safety of rivaroxaban and dabigatran in the
treatment of acute portal vein thrombosis in cirrhosis.
Major
During the follow-up period, what is the frequency for follow-up imaging? How to define
recanalization or persistent occlusion?
What is the median follow-up time for the included patients.
Did the included patients continuous taking anticoagulation? Otherwhile, there is no meaning
of the long-term follow-up result for the comparison of these two drugs.
The improvement of child-pugh score and meld score did not equal to the improvement of
cirrhosis, please clarify.
Did any patients suffered from the intestinal necrosis that required surgery? This information
was not shown in the study.
Minor
As mentioned in the inclusion criteria: acute PVT: developed symptoms <60 days and in the
absence of portal cavernoma or portal hypertension. Did the author exclude patients with portal
hypertension? However, most of the included patients had esophageal varices.
How did the author mean by low-dose anticoagulation, please give the detailed definition.
There is something wrong with the Ethics approval document, please reupload the updated
version.
Isolated thrombosis of superior mesenteric vein or splenic vein was excluded, but not showed
in the study flow chart.
Review for 10.1186/s12876-023-02960-8 (2023)

Title: Comparison of the efficacy and safety between rivaroxaban and dabigatran in the
treatment of acute portal vein thrombosis in cirrhosis
Version: 5 Date: 23 Jul 2023
Reviewer's report:
As the author mentioned that all patients underwent esophagoscopy prior anticoagulation, Please
showed the details of the gastroesophageal varices. Please add the severity of esophageal varices.
How many patients had prior banding for prophylaxis of variceal bleeding? How many patients
had a history of variceal bleeding and underwent endoscopic treatment?
As for the duration of anticoagulant therapy, it is obviously non-normally distribution. Please
show the median (IQR) rather than mean±SD.
Which imaging was used to evaluate the recanalization of PVT? Please show how many patients
had MRI, CTA or ultrasound?
Figure 1 (Study flow chart) should be showed according to the STROBE guideline.
The latest guideline should be BAVENO VII, please re-checked.
Table 2 and Table 3 are meaningless. In addition, some variables had interaction with each other.
Review for 10.1186/s12876-023-02960-8 (2023)

Title: Comparison of the efficacy and safety between rivaroxaban and dabigatran in the
treatment of acute portal vein thrombosis in cirrhosis
Version: 6 Date: 26 Aug 2023
Reviewer's report:
I prefer to keep supplementary table 1 and 2 as the main table the manuscript.
Maybe supplementary table 3 and 4 could be removed.
Review for 10.1186/s12876-023-02877-2 (2023)

Title: Serum liver fibrosis markers predict hepatic decompensation in compensated cirrhosis
Version: 1 Date: 10 Apr 2023
Reviewer's report:
The authors assessed whether the serum liver fibrosis markers are predictive of the occurrence
of hepatic decompensation in 688 cirrhotic patients with varying etiologies. They showed that
collagen IV (CIV) is reliable predictor for liver decompensation. I have some considerable
concerns.
#1. The etiology of cirrhosis of the patients is heterogeneous. The occurrence of decompensation
differs considerably among the diseases. It is lowest in HBV related cirrhosis (7.2%) and highest
in alcoholic cirrhosis (31.8%). In addition, the triggers of decompensation are likely to differ
among cirrhosis of different etiology. The heterogeneity must have caused confusion of the
results. Thus they should assess the predictors of decompensation in the cirrhosis of single
etiology, especially hepatitis B.
#2. When they study the patients with HBV, they should assess activity of hepatitis, anti-viral
treatment, and viral load (HBsAg, HBeAg,and HBVDNA).
#3. When they study the patients with alcohol abuse, they should assess the abstinence.
#4. They assessed the three different decompensation events (ascites, esophageal bleeding, and
hepatic encephalopathy) simultaneously. The triggers of these three events are likely to differ.
Thus they should assess the predictors of each event separately, especially ascites.
#5. When they study ascites, they should assess alcohol intake and activity of liver disease (AST,
ALT, and GGT)
#6. Table 1. The separate data of three events of decompensation should be added.
Review for 10.1186/s12876-023-02877-2 (2023)

Title: Serum liver fibrosis markers predict hepatic decompensation in compensated cirrhosis
Version: 1 Date: 15 Apr 2023
Reviewer's report:
Chen et al have demonstrated that serum liver fibrosis markers, particularly in collagen IV,
predicted liver decompensation in patients with compensated cirrhosis.
The comments are listed below:
1. In the section of “follow-up and study outcomes” (Page 5, Line 4), the authors defined variceal
bleeding as portal hypertension related bleeding requiring hospital admission. However, portal
hypertension related bleeding included variceal bleeding or bleeding from portal hypertensive
gastropathy. The definition should be addressed clear.
2. Regarding etiologies of cirrhosis, HBV and HCV accounts for 70.6% and 13.8%, respectively.
Did those patients receive anti-viral agents?
3. The authors analyze the predictive values of liver fibrosis markers, and LN and CIV
independently predict hepatic decompensation. There are some noninvasive indexes could
represent the severity of liver fibrosis including FIB-4 and APRI. Are those markers superior to
FIB-4 or APRI in prediction of hepatic decompensation?
Review for 10.1186/s12876-023-02877-2 (2023)

Title: Serum liver fibrosis markers predict hepatic decompensation in compensated cirrhosis
Version: 1 Date: 20 Apr 2023
Reviewer's report:
This original manuscript arouses interest for readers and provides an important clue to estimate
or predict a transition from compensated phase to decompensated phase using convenient
and non-invasive serum fibrosis markers in patients with cirrhosis. However, there are some
problems that should be addressed or altered.
(1) There are many fibrosis markers and indices for estimating the degree or stage of fibrosis
in chronic liver disease. Could you please specify why authors selected the four serum fibrosis
markers in the revised version? In addition, authors should explain why they were able to
measure all four markers at the same time. Were the four markers routinely measured using
medical insurance?
(2) Each of these four markers is different in what it reflects. Meanwhile, as the present and
other study cohorts include patients with various etiologies, it is conceivable that results will
vary among study populations. Are these markers comparable for populations with different
etiologies? Authors should address this issue in the Discussion section.
(3) Blood samples were taken after overnight fasting. Are these fibrosis markers influenced by
diet?
(4) Dis patients with compensated cirrhosis receive treatment specific to the etiology? If so,
what were the treatments?
(5) Variables with p < 0.10 or 0.15 in univariate analysis should be entered into multivariate
analysis. Data in Table 2 should be analyzed using the Cochran-Armitage trend test.
(6) Authors should specify what factors were the data in Table 3 adjusted for? Where are
unadjusted results of multivariate analysis in Table 3? Which univariate or multivariate analysis
are the adjusted results derived from in Table 3?
(7) What are “univariate and multivariate analyses” in Table 4? Were these data obtained using
the log-rank test or Cox regression analysis?
(8) What software did authors use to draw Figure 2? Please specify the statistical soft. In addition,
authors should analyze the Figure 2 data using the post-hoc Bonferroni or Holm method. Authors
must accurately statistical analysis methods including the log-rank test in the revised text.
Review for 10.1186/s12876-023-02877-2 (2023)

Title: Serum liver fibrosis markers predict hepatic decompensation in compensated cirrhosis
Version: 2 Date: 11 Jun 2023
Reviewer's report:
Comments: The authors assessed whether the serum liver fibrosis markers are predictive of the
occurrence of hepatic decompensation in 688 cirrhotic patients with varying etiologies. They
showed that collagen IV (CIV) is reliable predictor for liver decompensation. However, there
are some problems that should be addressed or altered.
#1#In the Discussion section, the authors said "Only a small number of studies for these markers
and their combination were designed to assess disease progression [31-34]". However, reference
33 suggested that CIV, LN, and HA levels were significantly associated with the severity of
liver dysfunction, but might be inappropriate for the prognostic assessment of liver cirrhosis.
You should cite them more accurately.
#2#In the Discussion section, the authors said " In the Discussion section, the authors said "We
assessed the three different decompensation events (ascites, esophageal bleeding, and hepatic
encephalopathy) simultaneously". Please support the above description by adding relevant
references.
#3#In the Discussion section, the authors said "We assessed the three different decompensation
events (ascites, esophageal bleeding, and hepatic encephalopathy) simultaneously". The word
"hepatic encephalopathy" should be revised as "HE".
#4#The conclusion section should be supplemented in the main text.
#5#The description regarding the post-hoc Bonferroni method and Cochran-Armitage trend test
should be recorded in the Materials and Methods section.
#6#The description of staging of HE, FIB-4 index and MELD score should be supplemented in
the Materials and Methods section.
#7#Please add the titles of Figures 1 and Figures 2.
Review for 10.1186/s12876-023-02877-2 (2023)

Title: Serum liver fibrosis markers predict hepatic decompensation in compensated cirrhosis
Version: 3 Date: 27 Jun 2023
Reviewer's report:
The authors carefully prepare for the manuscript. But there are still some problems, which are
also shown in the Comments to the Authors.
1#The authors should add a conclusion section and add a subtitle at the end of the manuscript.
2#In the Discussion section, the authors had deleted reference 33 in revised manuscript.
However, reference 33 suggested that CIV, LN, and HA levels were significantly associated
with the severity of liver dysfunction, but might be inappropriate for the prognostic assessment
of liver cirrhosis. The  conclusions of the two studies were inconsistent. You should discuss
them in the discussion section instead of deleting it.
Review for 10.1186/s12876-023-02961-7 (2023)

Title: Long non-coding RNA CASC7 is a promising serum biomarker for hepatocellular
carcinoma
Version: 1 Date: 23 Aug 2023
Reviewer's report:
By analysing the expression of the serum lncRNA CASC7 in normal humans, HBC as well as
HCC in different clinicopathological indices, the potential ability of CASC7 was demonstrated
and it is expected to be a new biomarker. However, there are some issues that need to be
addressed; in Figure 3, when the absolute value of r is less than 0.3, it is usually not considered
relevant, so the authors are asked to explain or revise it. Furthermore, what is the survival
analysis of lncRNA CASC7 in HCC? The authors are requested to describe it.
Review for 10.1186/s12876-023-02961-7 (2023)

Title: Long non-coding RNA CASC7 is a promising serum biomarker for hepatocellular
carcinoma
Version: 1 Date: 28 Aug 2023
Reviewer's report:
An interesting and well written paper.
A few minor editorial changes are required for example
page 8, line 8, which might also lead
page 9, line 9, small sample size
page 9, line 16 In conclusion, the increased
Review for 10.1186/s12876-023-02944-8 (2023)

Title: A novel role for Helicobacter pylori cytotoxin-associated gene A in negative regulation
of autophagy in human gastric cells.
Version: 1 Date: 29 Mar 2023
Reviewer's report:
This original article found that CagA negatively regulates autophagy and promotes the
production of inflammatory cytokines by down-regulating BECN1. However, there were some
limitations in the experiment design, there are some questions that need to be answered.
1.The description of statistical methods is not clear. What software is used for statistical analysis?
2. Figure 4A The fourth group added autophagy inhibitor and enhancer, Figure 4B the fourth
group added autophagy inhibitor twice, which will affect the cell state, the significance of this
grouping?
3.This study was only verified at the cell level, but it was not verified in clinical samples.
4. The results of ATG5, ULK1 and P62 were not analyzed.
Review for 10.1186/s12876-023-02944-8 (2023)

Title: A novel role for Helicobacter pylori cytotoxin-associated gene A in negative regulation
of autophagy in human gastric cells.
Version: 3 Date: 17 Jun 2023
Reviewer's report:
I think the authors revised their manuscript well according to my suggestions. I think this
manuscript is suitable to be published in BMC Gastroenterology after dealing with the following
point:
I asked authors to provide a description about P62 data, and authors explained the reason
why they didn't as below. I agree with the authors' point and I suggest authors to provide
the explanation not only to me but also to future readers by including the explanation in the
manuscript.
------------------
Comment 8: Fig 1B: P62 also is an important marker of autophagy. It would be better if a
description about P62 data is provided.
Response: As you mentioned, P62 is a marker of autophagy. However, we were concerned
that we did not measure it in subsequent experiments and could not provide P62 data in
the manuscript. We did not measure it for several reasons. First, we believe that the most
valuable evaluation of autophagic flux is the assessment of the formation and degradation
of autophagosomes, and we assessed autophagic flux using interpretation data from LC3-II
immunoblotting. Second, the timing of the increase or decrease in P62 does not necessarily
coincide with that of LC3. Third, factors other than autophagy may be involved in the production
and decrease of P62.
------------------
Review for 10.1186/s12876-023-02944-8 (2023)

Title: A novel role for Helicobacter pylori cytotoxin-associated gene A in negative regulation
of autophagy in human gastric cells.
Version: 3 Date: 01 Jul 2023
Reviewer's report:
This original article found that CagA negatively regulates autophagy and promotes the
production of inflammatory cytokines by down-regulating BECN1. The author has answered
and revised the review comments. It is recommended to modify the following questions before
publication
1.It is suggested to add abbreviations: RGM1, BECN1,RT-PCR, etc
2. Standard Helicobacter pylori writing: e.g Helicobacter pylori (H. pylori), (page 3, lines 55).
Review for 10.1186/s12876-023-02956-4 (2023)

Title: Clinical features and prognosis of acute-on-chronic liver failure in patients with
recompensated cirrhosis
Version: 1 Date: 14 Feb 2023
Reviewer:  David N Perdigoto
Reviewer's report:
Interesting manuscript concerning a relevant hot topic.
The data analysed is significant, but conclusions drawn should be interpreted cautiously because
of the particularities of the sample in study, namely almost half (49.2%) of the studied patients
have cirrhosis due to B hepatitis.
Studying the recompensated population is important. To understand better the recompensation
in the studied patients the authors should reveal the criteria used to define recompensation.
The manuscript requires revision of the language, some sentences need to be changed, for
instance: “Patients with recompensated cirrhosis had occured decompensation event(s), most
studies regarded them as decompensated cirrhosis patients.”
Review for 10.1186/s12876-023-02956-4 (2023)

Title: Clinical features and prognosis of acute-on-chronic liver failure in patients with
recompensated cirrhosis
Version: 1 Date: 12 Mar 2023
Reviewer:  Tawesak Tanwandee
Reviewer's report:
1. What is the definition of so call ACLF with compensated cirrhosis, ACLF with
recompensation and ACLF with decompensated liver cirrhosis? Did you mean development
of ACLF in the patients who had cirrhosis, decompensated cirrhosis with recompensation and
decompensated cirrhosis, respectively? In case of recompensation, how long after the patients
became recompensated before they developed ACLF event?
2. Since it was retrospective study, did you have information in ACLF in those decompensated
cirrhosis whether it was ACLF or part of decompensation with for example infection, etc.?
3. Hepatitis B reactivation in percent was calculated out of total population, in discussion the
author should also mention that contributed to how many percentages out of the patients with
hepatitis B
Review for 10.1186/s12876-023-02956-4 (2023)

Title: Clinical features and prognosis of acute-on-chronic liver failure in patients with
recompensated cirrhosis
Version: 3 Date: 17 May 2023
Reviewer:  Tawesak Tanwandee
Reviewer's report:
I have read the revised version of manuscript ” Clinical features and prognosis of acute-on-
chronic liver failure in patients with recompensated cirrhosis”. This revised version is good for
publication.
Review for 10.1186/s12876-023-02932-y (2023)

Title: Correlation between SDF-1#, CD34 positive hematopoietic stem cells and CXCR4
expression with liver fibrosis in CCl4 rat model
Version: 1 Date: 27 Jun 2023
Reviewer:  Si-Wen Chen
Reviewer's report:
This study reported the effect of CXCR4/ SDF-1# axis and hematopoietic stem cells (HPSCs) on
the progression/regression of liver fibrosis. The authors believe that the future scoring methods
including these parameters can be used to evaluate the efficiency of anti-fibrotic drugs in the
treatment of hepatic fibrosis and the prognosis of liver illness. The study is interesting, but there
are also several issues that need to be reminded to the author:
1. The format of references is not standardized or unified, please revise one by one. For example:
Reference 6: Nagasawa T, Hirota S, Tachibana K, et al. Defects of B-cell lymphopoiesis and
bone-marrow myelopoiesis in mice lacking the CXC chemokine PBSF/SDF-1. Nature. Aug 15
1996;382(6592):635-8. doi:10.1038/382635a0
Reference 41: Wang S, Gao S, Li Y, Qian X, Luan J, Lv X. Emerging importance of chemokine
receptor CXCR4 and its ligand in liver disease. Frontiers in cell and developmental biology.
2021;9:716842.
2. Some statements are not standardized. Please correct them. For example:
It would be better to change the sentence “Interestingly up to our knowledge our findings were
the first that …....” in Line 526 to “Interestingly up to our knowledge, our findings were the
first that …....”.
It would be better to change the sentence “Bone marrow and liver samples were taken for
evaluation of mRNA SDF-1# by PCR.” in Line 55-56 to “Bone marrow and liver samples were
taken for evaluation of SDF-1# mRNA by PCR.”.
3. In Line 362-363, “The percent of CD34+ cells in the peripheral blood and the liver was 8.98%
±0.51 and 3.1%±0.09 respectively (Fig. 4A, B and Table 4).” refers to which group?
4. For the first time, abbreviations should be accompanied by full names, while when it appeared
again, it must be abbreviations. Such as “pseudo lobules (PS)” in Line 773, may not appeared
as “pseudo lobules (PS)” again in Line 774.
5. As we know, SDF-1# binding to CXCR4 receptors on HSCs can induce HSCs activation,
which play key roles in the pathogenesis of liver fibrosis. In this study, the authors confirmed
that CXCR4/ SDF-1# axis induce HPSCs homing to the liver for repairing the fibrotic liver.
It is interesting, CXCR4/ SDF-1# axis involved in the generation of fibrous septa and the
damage repair of hepatocyte at the same time. If you simultaneously detect the distribution and
proportion of HPSCs and HSCs in fibrotic liver, that will be very meaningful.
6. In the regression of liver fibrosis unit, why the rats in the “Spontaneous reversion group” did
not get IP injections of olive oil?
Review for 10.1186/s12876-023-02932-y (2023)

Title: Correlation between SDF-1#, CD34 positive hematopoietic stem cells and CXCR4
expression with liver fibrosis in CCl4 rat model
Version: 1 Date: 08 Jul 2023
Reviewer's report:
The manuscript wrote by Sara Abubakr is scientific and interesting, But there are some questions
to be addressed.
Major:
1.  the main question is that liver fibrosis may be reversed especially in rat model, but  not in
mice model. So, the conclusions in this manuscript may be not scientific.
2.  there  is not any relationships among these markers, authors should address it.
Minor:
1. Tables in this manuscript need to be rectified.
2. there are many mistakes in writing.  Line 450, Line 489.
3. Some words may be missing. line 152
Review for 10.1186/s12876-023-02932-y (2023)

Title: Correlation between SDF-1#, CD34 positive hematopoietic stem cells and CXCR4
expression with liver fibrosis in CCl4 rat model
Version: 3 Date: 29 Jul 2023
Reviewer:  Si-Wen Chen
Reviewer's report:
1.Thank you for your careful revision in reference.
2.Thank you for your correction in some statements.
3.Thank you for your explanation.
4.Thank you for your correction in the abbreviations.
5.Thank you for your explanation. I look forward to your future research on the interaction
between HPSCs and HSCs in the process of liver fibrosis progression/ reversion.
6.Thank you for your explanation.
Review for 10.1186/s12876-023-02947-5 (2023)

Title: A Large-Scale Study on the Prevalence of Intestinal Parasites in Patients Referred to
Medical Laboratories in Urmia, Northwest Iran
Version: 2 Date: 07 Jul 2023
Reviewer:  Aki Ronkainen
Reviewer's report:
The authors have  conducted a study titled "A Large-Scale Study on the Prevalence of Intestinal
Parasites in Patients Referred to Medical Laboratories in Urmia, North West of Iran". The
reviewer is impressed with the  scale of  study as well as the study aim.
The reviewer is concerned with insufficient description of the materials and methods. The
description does not include a thorough description of sampling and sample analysis. What type
of container and fixative (if any) was used preserve the specimens? How were the wet mount
preparations made? All this is crucial when interpreting the results. Please  revise the manuscript
by including a step-by-step description of the sample collection and analysis.
As for the results, the authors should pay attention when addressing pathogenic and apathogenic
parasites. For example, when addressing  species such as Blastocystis spp., Endolimax nana,
Entamoeba coli, Iodamoeba butschlii, and Chilomastix mesnili, the use of term "infection"
is a overstatement as these organisms are usually considered apathogens. The author would
recommend using the term colonization with respect to these organisms. In the discussion, there
is line "Interestingly, it is reported from 10 patients with diarrhea which is resolved after treating
E. coli infection [19]. ", suggesting that E. coli is a pathogen. However, the authors refer to a
study from 1991, and does not reflect the current view on the organism's status as pathogen.
The reviewer is suprised that the study does not report any helmints besides Enterobius
vermicularis that may occasionally be found in stool samples. The reviewer suggest that the
word "interestingly" to be omitted from the discussion. Furthermore, the authors do not report
any Entamoeba histolytica/dispar or Entamoeba hartmanni cases. All this underlines the need to
update the materials and methods for the readers to scrutinize the results.
The reviewer does not agree as such with the conclusions "According to the results of the present
study, the prevalence of intestinal parasitic infections in West Azerbaijan province, northwest
of Iran, is not considered very high, yet seems significant. Most intestinal protozoa are still
prevalent in the area, granted in low prevalence. Moreover, in terms of helminthic infections,
no soil-transmitted helminth was detected thus, West Azerbaijan is in decent condition. " These
claims require some comparisons.  To state that something is not high, what is the reference?
How is the low-prevalence defined?
Review for 10.1186/s12876-023-02947-5 (2023)

Title: A Large-Scale Study on the Prevalence of Intestinal Parasites in Patients Referred to
Medical Laboratories in Urmia, Northwest Iran
Version: 4 Date: 16 Aug 2023
Reviewer's report:
Thank you for responding reviewer comments.
However, there are some still simple corrections in the manuscript needed to be addressed.
Comment #1
- Sometimes abbreviation of intestinal parasitic infections is written as IPI or  IPIs>>> should
be unified all over the whole manuscript as IPIs>>> Please correct
Comment #2
Page 3 Line 13 ……Wet mont >>> correct as mount
Comment #3
Page 3 Line 21……modified cold strong Ziehl–Neelsen staining>>>> delete the word 'strong'
Comment #4
Page 10 Line 5 ….. that did not perform in the present study>>>  correct to 'that wasn’t
performed'
Comment #5
Line 12-24……. The added paragraph should be summarized and be concise to the point.
Comment #6
Some references mentioned in Page 10 line 12-24 are too old and non-logic to be used for
comparison. It had passed more than 50 years to be mentioned here
For example, Ref 15 Arfaa F, Ghadirian E (1977); Ref 16 Mohammad K, Zalie MR (1970) and
Ref 19 Hazrati-Tapeh et al. (1970) >>>>> delete and replace with updated references.
Review for 10.1186/s12876-023-02947-5 (2023)

Title: A Large-Scale Study on the Prevalence of Intestinal Parasites in Patients Referred to
Medical Laboratories in Urmia, Northwest Iran
Version: 4 Date: 17 Aug 2023
Reviewer:  Aki Ronkainen
Reviewer's report:
The reviewer is delighted that the authors have addressed the main concerns regarding the
manuscript. Concerning the revised manuscript, the reviewer would like to suggest a few
corrections.
Page 1, Lines 19-20 (Abstract): Please transfer the percent (%) symbol after the numbers.
Page 1, Lines 26-29 (Abstract): Suggestion to enhance readability: Results: 209 intestinal
parasites were identified in 184 out of 2845 (6.5%) patients of which 136 out of 2174 males
(6.3%) and 48 out of 671 females (7.2%) were positive. Some patients had tested positive for
multiple protozoa.
Page 2, Lines 3-4 (Abstract): "granted are indices for water and food hygienic status in the area"
Please clarify and rephrase.
Page 2, Line 25 (Introduction): the multiple infection -> co-infection with multiple parasites
The reviewer is pleased with revised description of materials and methods, especially adding
the section "Limitations of the study".
Page 3, Line 13 (Materials and Methods): Please clarify the sentence. Were the samples
suspended in formalin and PVA after  sample collection by the patients or when they arrived
in the laboratory? Meaning, were the samples transported without preservative? Were the wet
mount preparations made from unfixed samples?
As for the limitations of the study, it should be mentioned and emphasised that the samples
WERE NOT treated with ethyl-acetate concentration. This is important as this procedure
enhances identification of intestinal parasites. For instance, the eggs of Ascaris lumbricoides
and Taenia spp. may be missed in the presence of debris present in wet mount preparations. This
should also be clearly stated in the discussion.
Page 5 Line 3 (Results): Blastocystis spp. Please correct spp. to non-italics.
In the result section, please use arabic numbers for numbers more than 10 in stead of writing them
(e.g. page 9 line 1, twenty-one -> 21) to enhance readability. Furthermore, place the percentages
after the numbers (e.g. 21 (11,41%) out of 184 patients -> 21 out of 184 patients (11,41 %)).
Page 10 Line 2 (Discussion): Chilomastixmesnili -> Chilomastix mesnili
Page 10 Line 4-5 (Discussion): which diagnosis is not a stool examination, but the cellulose tape
(adhesive cellophane tape) [12] that did not perform in the present study. -> which is regularly
analysed either from  adhesive cellophane tape or swab sample that were not performed in this
study.
Page 10 Line 11 (Discussion): The reference 17 used in comparison states, although somewhat
ambiguously, the use of formalin-ether concentration. It should be stated that the methodology
differed from this study.
Page 10 Line 22-24 (Discussion): This dramatic reduction in the prevalence of intestinal
parasites is LIKELY the result of the recent improvement in hygienic status, sanitation, and
health education in society.
Review for 10.1186/s12876-023-02955-5 (2023)

Title: Network meta-analysis of adjuvant treatments for patients with hepatocellular carcinoma
after curative resection
Version: 1 Date: 20 Jun 2023
Reviewer:  Ken Shirabe
Reviewer's report:
Comments:
It is an interesting and this paper is well structured and will give useful information to
the readers .However, it requires a modification in the following points
Major comments
1. Some trials in this study, include HCC patients with vascular invasion, Surgical margins
are diverse for different trails. Especially, vascular invasion is a strong factor that affects HCC
recurrence and survival. The authors should discuss the effects and bias, affecting the results by
the background difference.
2. The primary outcome was the prevention of recurrence between different procedures. The
second outcomes were one-year survival, three-year survival and five-year survival. By timing
of outcome, the results are different. The authors should discuss about the reason in differences
in the impact of procedures on survival and recurrence.
Minor comment
1. You should correct one-year survival to three-year survival, on page 5 line 206.
Review for 10.1186/s12876-023-02955-5 (2023)

Title: Network meta-analysis of adjuvant treatments for patients with hepatocellular carcinoma
after curative resection
Version: 1 Date: 04 Jul 2023
Reviewer's report:
The prevention of recurrence for patients with hepatocellular carcinoma after curative resection
is still a great challenge in clinical practice. In this article, the authors compared the efficacy
between different reported treatments by network meta-analysis. Generally, this is an interesting
and well-organized study. I have only a few suggestions.
In the conclusion of abstract, you mentioned that ‘Large scale of RCTs are needed to verify it.’
It is redundant, please remove.
Has this meta-analysis been registered?
You may consider additionally perform Q test to assess heterogeneity.
I noticed that the authors missed a few important studies regarding the background of
HCC. For example, Biosci Trends. 2022 Dec 26;16(6):405-425. doi: 10.5582/bst.2022.01109;
J Cell Physiol. 2019 Feb;234(2):1062-1070. doi: 10.1002/jcp.27324; J Cell Physiol. 2019
Aug;234(8):12116-12121. doi: 10.1002/jcp.28019. Epub 2019 Jan 15.
Review for 10.1186/s12876-023-02955-5 (2023)

Title: Network meta-analysis of adjuvant treatments for patients with hepatocellular carcinoma
after curative resection
Version: 2 Date: 08 Sep 2023
Reviewer's report:
The prevention of recurrence for patients with hepatocellular carcinoma after curative resection
is still a great challenge in clinical practice. In this article, the authors compared the efficacy
of different reported treatments by network meta-analysis. Generally, this is an interesting and
well-organized study. In the latest version, the authors have revised it as I requested. Therefore,
I recommend to accept in this version.
Review for 10.1186/s12876-023-02935-9 (2023)

Title: Patient-Reported Outcome Measures in Functional Dyspepsia: A Systematic Review and
COSMIN Analysis
Version: 3 Date: 27 Mar 2023
Reviewer:  Nicholas J. Talley
Reviewer's report:
Patient reported outcomes matter in symptomatic disorders including  functional dyspepsia, and
a number of PROs have been published although none have met with  FDA approval, an issue
the authors should further comment on.
The current  study was conducted according to the Preferred Reporting Items for Systematic
Reviews and Meta-Analyses (PRISMA) with searching of four to find any relevant PROs.
The investigators assigned an overall rating based on COSMIN guidelines, and the Grading of
Recommendations Assessment, Development, and Evaluation (GRADE) approach was used to
assess the level of evidence for psychometric properties of included PROMs. The paper is clear
and well written.
The current work is an extension of a reasonably recent meta-analysis as the authors cite. They
did identify more PROs and did a more comprehensive psychometric review than the 2018 study.
However the broad conclusions are otherwise similar.
Smeets F G M, Masclee A a M, Conchillo J M, et al. Systematic review: Disease-
specific instruments to assess gastrointestinal symptoms in functional dyspepsia[J].
Neurogastroenterology and Motility, 2018, 30(8).
Why was the focus on symptoms not quality of life? Surely both sets of domains should be
included?
Review for 10.1186/s12876-023-02935-9 (2023)

Title: Patient-Reported Outcome Measures in Functional Dyspepsia: A Systematic Review and
COSMIN Analysis
Version: 3 Date: 30 Mar 2023
Reviewer:  Sami Hoque
Reviewer's report:
well written article .
line 16 : could  you say DBGI?
line 128:  imprecision what are the sample size base on.? please elaboarte a bit.
In abstract conclusion. A bit more succinct what are key area s are failed to assess, so that it is
clearer, otherwise . It is very well written article.
Review for 10.1186/s12876-023-02935-9 (2023)

Title: Patient-Reported Outcome Measures in Functional Dyspepsia: A Systematic Review and
COSMIN Analysis
Version: 3 Date: 04 May 2023
Reviewer's report:
The review of patient reported outcome measures (PROMs) by Wang et al is a very thorough and
useful piece of work for researchers contemplating patient outcomes in functional dyspepsia.
The review covers key areas including content, psychometric properties and feasibility. Overall
I feel this to be an important contribution to the literature. There are however a small number
of issues that could be addressed by the authors.
1. Inclusion criteria: While it is commendable that the authors have been thorough, I wonder if
they have cast their net too wide. I am not personally familiar with all of the instruments reported
but am aware that not all of them are designed to be functional dyspepsia (FD)-specific, for
example the GSRS and SAGIS. From one perspective I guess it is okay to evaluate the relevance
of these instruments to FD but I also question whether it is reasonable to evaluate them using the
same criteria as a disease-specific instrument. At least I believe the authors should categorise
instruments as FD-specific vs general gastrointestinal symptom burden measures and interpret
their findings in that context.
2. The range of characteristics evaluated in this review is thorough and I applaud the authors for
that. However while Table 3 provides the authors summary of psychometric properties I would
have liked to see the "raw" data provided as an appendix. I think this is important since the
categorisations made by the authors seem to involve some judgement and I think readers should
be able to make that judgement themselves.
Review for 10.1186/s12876-023-02935-9 (2023)

Title: Patient-Reported Outcome Measures in Functional Dyspepsia: A Systematic Review and
COSMIN Analysis
Version: 6 Date: 04 Aug 2023
Reviewer:  Nicholas J. Talley
Reviewer's report:
The paper is improved and the authors have addressed most points.
There is one error: it is reported in the paper that the Nepean Dyspepsia Index (NDI) did NOT
establish internal consistency. This is incorrect. See for example table 4 of the initial validation
report on the NDI:  Aliment Pharmacol Ther 1999; 13: 225±235. This may change the author
conclusions in the discussion and abstract.
Table 4. Internal consistency of domains identified by factor analysis
Domain No. items                                                   Cronbach's a*                     Cronbach's a-w
Interference dailyactivities/work 13                 0.96                                              0.94
Knowledge/control  7                                                     0.90                                              0.92
Eating/drinking  3                                                               0.81                                               0.91
Sleep  2                                                                                          0.92                                             0.96
*Using unweighted responses.
 Using importance-weighted responses
Review for 10.1186/s12876-023-02965-3 (2023)

Title: A single-center prospective study on pain alleviation during peroral upper endoscopy with
an ultrathin endoscope
Version: 0 Date: 05 Jul 2023
Reviewer's report:
This paper innovatively starts from pain alleviation of ultrathin endoscope, and discusses
through prospective research that ultrathin endoscope can relieve the pain of patients compared
with ordinary endoscopy, which has certain innovative and clinical guiding significance.
Preliminary comments are as follows:
1.The study was a single-center prospective study in people that had undergone general
endoscopy 1 year ago, and the evaluation indicators were highly subjective and may have recall
bias.
2.The method can be drawn as a flow chart, which makes the experimental design and
implementation path more intuitive.
3.The evaluation index of the study is highly subjective, and the subjects signed an informed
consent form before participating in the trial, and have relevant understanding of the trial
situation, which may affect the trial results due to psychological suggestion.
4.The comparison of ultrathin endoscope with conventional endoscopy may make the study
more clinically significant.a
Review for 10.1186/s12876-023-02965-3 (2023)

Title: A single-center prospective study on pain alleviation during peroral upper endoscopy with
an ultrathin endoscope
Version: 0 Date: 09 Jul 2023
Reviewer's report:
We appreciate the opportunity for peer review. The authors demonstrated that oral insertion of an
ultrathin endoscope reduces the patient's pain and increases satisfaction during the examination
compared to an conventional endoscope. This is a very useful point of view in clinical practice.
However, in order to accept the paper, we would like to make the following comments.
1. As the author describes in the limitations section, it is important to consider how patients who
experience pain during conventional endoscopy will subsequently accept endoscopy. Since these
patients were excluded from the study, it seems difficult to conclude that ultrathin endoscopy
really reduces pain.
2. In the patient satisfaction assessment, 20 were not satisfied. What were the reasons?
3. The distribution of pain scores shows that some patients have a score of 7, even with the
ultrathin endoscope. For example, if you focus on patients who had a relatively worse pain score
of 5 or higher in the previous examination, we would like to know how much the score changed
(improved) in the current examination. If you can provide this information, we will have a better
understanding of the advantages of the ultrathin endoscope.
4. The author described the physician side as 77.6% satisfied, but was there a definition of
satisfaction stated?