JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-022-02501-9 (2022)

Title: Clinical Characteristic and Pathogenesis of Tumor-Induced Acute Pancreatitis: A
Predictive Model
Version: 1 Date: 26 Jul 2022
Reviewer's report:
The authors carry out a prospective study to determine the clinical characteristics and
pathogenesis of tumor-induced acute pancreatitis, and to develop a reliable prediction model of
the clinical features to guide the diagnosis and treatment.
Congratulations to the authors for having be able to carry out this study that shows significant
differences between groups (tumor vs non-tumor) and predictive factors which may lead to
improve the clinical suspicion of these patients. This is an interesting a well-written manuscript.
It has a few minor issues and some points of clarity from the authors would be helpful. Can you
explain these points better?
1. "360 admissions were random selected from those AP patients with other etiologies as the
non-tumor group".  I think that you have explained this part, because it will be  a cause of bias.
Explain the election criteria.
2. "aggravated intense pain in the upper abdomen was special symptoms of 88 patients". If
this is a retrospective study, how was pain intensity measured in all patients? Do you have this
measurement in each patient's clinical history? Was the same scale used for all?
3. "median cost of the tumor group was more", What cost parameters were evaluated? hospital
stay? treatments? interventions? oncological surgery? only AP cost?
4. "The sensitivities of CT, US, MRCP, EUS and PET-CT were 97.7%(85/87), 84.1%(58/69),
95.7%(45/47), 100%(9/9) and 81.8%(9/11)". The sensitivity for the diagnosis of what? All
patients underwent to all diagnosis studies?  How did they find the sensitivity of diagnostic
studies?
5. There are studies said Acute Pancreatitis can be a early marker of pancreatic cancer, for this
reason, it is a disappointment not to have the stage of the tumors.
Review for 10.1186/s12876-022-02501-9 (2022)

Title: Clinical Characteristic and Pathogenesis of Tumor-Induced Acute Pancreatitis: A
Predictive Model
Version: 3 Date: 27 Aug 2022
Reviewer's report:
In the epidemiology section of the results, the incidence of tumor-related AP
increased significantly in 2020 and 2021 (0.81% in 2019, 3.83% in 2020, and 2.82% in
2021), the author's explanation is still not convincing, and it is hoped that the original data will
be independently re-reviewed by different authors.
Review for 10.1186/s12876-022-02489-2 (2022)

Title: Construction and validation of a predictive model for hepatocellular carcinoma based on
serum markers
Version: 2 Date: 03 Jul 2022
Reviewer:  Yutaka Midorikawa
Reviewer's report:
Comment on the manuscript 3a48cbe1-1130-4474-9bb5-524d64c19cb1 by Zheng, et al.
Despite of the development of imaging modalities and serum marker, it is still difficult to
detect HCC at early stage. Furthermore, prognosis of the HCC patients is still poor even after
curative resection, because of the dysfunction of the background liver. The authors established
a non-invasive predictive model which could predict the HCC onset and survival of patients
undergoing liver resection. The concept of the paper is intriguing, however, there are major
concerns that need to be addressed.
There are several questions and suggestions for corrections.
1) The aim of this study is unclear. In Introduction, the purpose of this study is to diagnosis a
small HCC, however, there is no description about the tumor status. The Changzhou cohort did
not really include advanced stage HCC?
2) In Figure 2, the predictive score was lower 9 months before diagnosis of HCC. If so, all
patients in this cohort was diagnosed not to have HCC at this point?
3) The predictive model included not only tumor marker but also liver function. Therefore, I
assume that this model is available for the prediction of survivals of patients after operation, but
not for diagnosis of small HCC.
4) Survival curves should be shown as validation using Wuxi cohort.
5) Given that etiology of HCC patients is not only HBV but also HCV, alcoholic, and NASH,
HBV as a characteristic for score model should be excluded in order to be available world-wide.
6) The first sentence in Conclusion of Abstract should be removed.
7) Limitations of the study should be in Discussion, not in Conclusions.
Review for 10.1186/s12876-022-02489-2 (2022)

Title: Construction and validation of a predictive model for hepatocellular carcinoma based on
serum markers
Version: 2 Date: 07 Jul 2022
Reviewer's report:
This article by Zheng et al. aimed to construct a predictive model based on baseline serum
markers to predict the early-stage onset and evaluate the prognosis in patients with HCC.
Although it is indeed an important and urgent matter to establish an effective model to diagnose
early-onset HCC and predict patient outcome. There are a few concerns that I need to raise
regarding the design of this investigation.
1. The baseline characteristics of this cohort are significantly different. Patients’ age, gender,
HBV and HCV status, ALP, ALB, GGT, TP, WBC, NEUT, AFP, AFP-L3, and PIVKAII
all show drastic difference. This indicates the two groups are imbalance and therefore not
comparable. I would suggest the authors perform propensity score matching (PSM) and repeat
the analysis to get a more convincing result;
2. One of the authors aim in this study was to construct a model that could predict early onset
of HCC, yet the patient cohort includes all stages of patients. It is therefore not possible to draw
conclusion that this model can predict early onset based on its current form. I would suggest the
authors separate patients of different stages and perform individual analysis;
3. Since this model is constructed by clinical parameters that is of easy access, the authors should
consider adding a validation group to examine the efficacy of this model;
4. Figure legends is missing from the manuscript, and the figures and tables should also be given
appropriate titles and annotations so that they could be understood as a single;
5. Language can be polished but is acceptable at its current form.
Review for 10.1186/s12876-022-02489-2 (2022)

Title: Construction and validation of a predictive model for hepatocellular carcinoma based on
serum markers
Version: 4 Date: 15 Aug 2022
Reviewer:  Yutaka Midorikawa
Reviewer's report:
Comment on the manuscript 3a48cbe1-1130-4474-9bb5-524d64c19cb1 by Zheng, et al.
The new version of the manuscript by Zheng, et al. has been considerably improved and I am
satisfied with the revisions.
Review for 10.1186/s12876-022-02499-0 (2022)

Title: Long-term prognosis of curative endoscopic submucosal dissection for early colorectal
cancer according to submucosal invasion: A multicenter cohort study
Version: 1 Date: 31 Jul 2022
Reviewer:  Katsumi Yamamoto
Reviewer's report:
Dear authors,
Thank you for reviewing a manuscript titled “Long-term prognosis of curative endoscopic
submucosal dissection for early colorectal cancer according to submucosal invasion: A
multicenter cohort study”
This manuscript seems to be a very valuable multicenter cohort study regarding long-term
prognosis of curative endoscopic submucosal dissection for early colorectal cancer. This study
includes a large number of colorectal ESD cases at Korean institutions and seems to reflect
the reality. I also agree with their conclusion. On the other hand, I am very interested in
your recurrent cases in curative resection. A distant or regional LN metastasis occurred in two
intramucosal cancer cases and two SM1 cancers. Besides, those three cases except piecemeal
resection were resected in en bloc and margin negative. In general, CT test following ESD is
not performed in case of intramucosal cancer. I have two suggestions as follows.
1. Immunostaining of D2-40 and VB are often performed for detection of lymphovascular
invasion, but there is no description in this manuscript. Lymphovascular invasion is a crucial
risk of metastasis, and it occurs not only submucosal cancer but also intramucosal cancer,
rarely though. At our and other institutions, immunostaining of D2-40 and VB is performed
in all cases of submucosal cancers, and a small number of intramucosal cancer in case that
lymphovascular invasions are suspected. Authors should discuss recurrent cases in more details
and the immunostaining of D2-40 and VB.
2. Secondly, the authors should describe the depth of submucosal dissection. Some endoscopists
dissect deep submucosal layers just above the muscle layer, but others dissect shallower layer. If
shallow submucosal layer was dissected, lymphovascular invasion could be missed. Therefore,
the depth of submucosal dissection is very important for precise histopathological examination.
In a Japanese report, more than 500µm of the distance between the deepest part of cancer
invasion and vertical margin is favorable, although it is controversial. Authors should investigate
the deepest part of cancer invasion and vertical margin in recurrent cases of submucosal cancers,
and discuss the depth of submucosal dissection.
I guess the discussion about those two problems are mandatory for the best treatment of
colorectal ESD. If those suggestions are properly dealt, this manuscript will be more valuable.
Review for 10.1186/s12876-022-02499-0 (2022)

Title: Long-term prognosis of curative endoscopic submucosal dissection for early colorectal
cancer according to submucosal invasion: A multicenter cohort study
Version: 1 Date: 02 Aug 2022
Reviewer's report:
Shin J et al. reported the results of multicenter retrospective study for long term prognosis of
early colorectal cancers treated by endoscopic submucosal dissection (ESD). They emphasized
good recurrence free survival rate in curative resection group. Almost previous reports of long
term prognosis were form single center, so this report seemed to be valuable. However, results
of them were as we predicted without remarkable knowledge. I will propose some suggestion
to improve manuscripts.
Major comments
1) In abstract, inclusion period was between 2003 and 2015. On the other hand, in method
section, it was between 2003 and 2013. Which period was correct?
2) In method, sub category surveillance after ESD, please describe about interval of CT and
tumor markers.
3) In results, they described all included cases were stage #. However, in UICC and JSCCR, Tis
N0 M0 was classified as Stage 0. Please re-confirm about them.
4) In results, they did not describe about morphology of included cases in main text and table
1. Morphology data seemed to be essential for investigation of colorectal ESD. Please add their
information.
5) They should insert figure 1 into result section. Moreover, please add information after non
curative resection such as additional surgery and recurrence.
6) In result section and table 1, type of recurrence such as local, regional and distant should
be presented separately. For readers, type of recurrence was important information comparing
with previous reports.
7) In figure 2 and 3, please add information of number at risk instead of number at event.
8) In discussion (page 13, line 260~262), contents of significant factors associated with
recurrence are different from original article of Oka S et al in AJG. Please re-confirm it.
Minor comments
1# In page 11, line 216, spell of discussion was misspelled.
2# In page 12, line 238, mm2 should be changed to mm2.
3# In reference, essential information of ref. 20 were lacked.
Review for 10.1186/s12876-022-02499-0 (2022)

Title: Long-term prognosis of curative endoscopic submucosal dissection for early colorectal
cancer according to submucosal invasion: A multicenter cohort study
Version: 3 Date: 05 Sep 2022
Reviewer:  Katsumi Yamamoto
Reviewer's report:
Dear authors,
You answered all queries appropriately.
I have no  further comments.
Review for 10.1186/s12876-022-02499-0 (2022)

Title: Long-term prognosis of curative endoscopic submucosal dissection for early colorectal
cancer according to submucosal invasion: A multicenter cohort study
Version: 3 Date: 05 Sep 2022
Reviewer's report:
Their revised manuscript was improved as reviewer's comments. Therefore, I have no additional
comment to the revised version.
Review for 10.1186/s12876-022-02494-5 (2022)

Title: Stenting of the pancreatic duct in the early phase of acute pancreatitis: a retrospective
study
Version: 0 Date: 03 Jul 2022
Reviewer's report:
The authors carry out a retrospective cohort study in 131 patients in which they determine
the efficacy and safety of early pancreatic duct setting for acute pancreatitis. The authors
demonstrate that pancreatic duct stunting has the potencial to reduce pain relief time, oral
refeeding time and hospital stay time.
Congratulations to the authors for having been able to carry out this study about very
controversial subject.
It has various  issues and some points of clarity from the authors would be helpful.
The first questions are philosophical in nature: how do the authors explain the differences they
have found between the two groups of patients analyzed in the study? One of the reasons given
in the introductions that “PD stent placement can reduce ongoing pancreatic injury by providing
adequate drainage of pancreatic fluids”.
1. If the IAP/APA and AGA guidelines consider that ERCP is not indicated due to the high
risk of complications in patients with AP and worse prognosis for these patients . It is only
recommended in patients with cholangitis (GRADE 1A). In this context, it is difficult to
understand the indication for an ERCP.
2. The authors describe few complications in performing ERCP thanks to their expertise, but
without ERCP procedure, perhaps the evolution  that they find is the natural evolution of AP
in each of the cases.
3. They describe that the treatment used is described in the guidelines. Nonetheless, in recent
years, there is well-established evidence that in patients with mild AP, an early oral diet can be
started immediately with good results and prognosis.
Considering that more than 90% are mild AP, perhaps only optimized medical treatment and an
early diet are sufficient for the clinical improvement of the patient and the reduction of hospital
stays, admissions and stay in the ICU, severity and improvement of pain. Factors that the authors
consider to be improved by the stent (?).
4. The analysis of lipase and amylase is not clear to me,  it is known that both lipase and amylase
lack the capacity to determine the severity and etiology of acute pancreatitis. The joint ordering
of both tests has shown little or no increase in diagnostic sensitivity and specificity.
5. I do not understand how, based on a retrospective study, few patients and cases and controls
study can find risk factors  of severity. Factors in which the lipase and amylase are included.
Understanding the statistical analysis performed and perhaps it is adequate but the discussion
is a little deeper.
6. Placing a stent with such a high risk of complications may not be necessary in a high-risk
patient. Perhaps the optimization of preserved management alone will help these patients to do
well and reduce all the results described by the authors with the placement of a stent.
Review for 10.1186/s12876-022-02494-5 (2022)

Title: Stenting of the pancreatic duct in the early phase of acute pancreatitis: a retrospective
study
Version: 0 Date: 05 Jul 2022
Reviewer's report:
I would congratulate the authors for providing very important information regarding surgery
for acute cholecystsitis in severe systemic disease from national registry data. Please find my
comments.
1. The issue with registry-based data being heterogeneity and discretion of physician for
cholecystectomy. If a surgeon feels a patient deemed non-suitable for emergency surgery, patient
will be managed conservatively and undergo elective surgery. This is also reflected in the data
provided as patients managed non-operatively were older and sicker. So among ASA III only
those patients underwent emergency surgery who were relatively stable. This issue needs to be
discussed.
2. In the abstract the authors should remove “complicating risk benefit analysis” from the
conclusion as this is not a part of this study.
3. Since ASA groups differ significantly in age, a subgroup analysis of mild and severe
complication on the basis of age (< 65-70 and >65-70) among different ASA group should be
done.
Review for 10.1186/s12876-022-02494-5 (2022)

Title: Stenting of the pancreatic duct in the early phase of acute pancreatitis: a retrospective
study
Version: 0 Date: 27 Jul 2022
Reviewer:  Áron Vincze
Reviewer's report:
This is a retrospective cohort study involving 131 acute pancreatitis patients. Group of patients
had ERCP with PD stent within 48 hours after admission (study group, n=46), while the rest
of the patients did not receive pancreatic stent (control group). The primary endpoints were the
complications (ERCP related, new onset organ failure, new systemic and local complications,
outcome at 2 months). There was no significant differences between the two groups. Favorable
differences were found in the secondary endpoints (time of pain relief, time of oral refeeding,
length of hospital stay, length of ICU stay in the study group.
Major concerns:
1) The etiology of the pancreatitis not detailed in the two groups, however significantly more
cases of biliary pancreatitis were in the study group, as it shown in Table 1.
2) The exact indication of ERCP is not clearly explained.
3) How many patients had ERCP without pancreatic duct stenting in the two groups?
4) What was the biliary cannulation failure rate, pancreatic stenting failure rate during the
ERCPs?
5) Were there any advanced cannulation techniques applied during the ERCPs?
6) Why were different stent types used in the study? Only prophylactic (5 Fr), short stents might
be indicated in selected cases during ERCP in patients without chronic pacreatitis. Chronic
pancreatitis patients were excluded from the study. What was the indication of larger calibre,
longer pancreatic stents?
7) Because all of these concerns, the study group itself is very heterogeneous, the study and the
control group is not really comparable.
Minor concers:
1) The English language should be improved, lots of imprecise sentences along the manuscript
2) The case load of endoscopists who performed the ERCPs in the study requires some
explanation. It is stated that the endoscopists performed more than 500 ERCP and more than
500 pancreatic cannulation yearly. The latter is unusually high number, since the majority of
ERCPs have biliary indications, when pancreatic cannulation is not required.
3) What is the indication of preprocedural intramusculars phloroglucinol?
4) Were there any prophylactic measures (i.e., NSAID, iv hydrations) applied to prevent post-
ERCP pancreatitis, other than pancreatic stenting?
5) Data cleaning and processing in the Methods part are not clear. What happened with the
missing values?
6) Reference 13 and 24 are the same
7) Reference 28 author list is not correct
Review for 10.1186/s12876-022-02498-1 (2022)

Title: A nationwide cohort study suggests clarithromycin-based therapy for Helicobacter pylori
eradication is safe in patients with stable coronary heart disease and subsequent peptic ulcer
disease
Version: 1 Date: 29 May 2022
Reviewer:  giuseppe losurdo
Reviewer's report:
In this retrospective cohort Taiwanese study, Chen et al showed that use of clarithromycin for
H. pylori therapy did not affect overall mortality and cardiovascular mortality and morbidity.
Main comments:
1) Authors did not specify the dose of clarithromycin, nor the duration of eradications therapy
(10 days in all cases?). These could be confounders as well.
2) Clarithromycin may prolong QT interval. However, in the analysis it was not discriminated
morbidity or mortality due to arrhythmia rather than ischemic disease. This sub-analysis should
be added to shed a new light on the study.
3) H. pylori has been linked to atherosclerosis as well and even to ischemic heart disease (see
Ribaldone DG et al, Minerva Gastroenterol Dietol 2016), and this aspect should be discussed.
4) H. pylori should be always italicized.
Review for 10.1186/s12876-022-02491-8 (2022)

Title: Impact of bowel preparation on elective colectomies for diverticulitis: analysis of the
NSQIP database
Version: 3 Date: 03 Jul 2022
Reviewer's report:
Nice work, interesting subject which is being debated now (bowel prep or not). In general it
would be nice to know a little more about the NSQUIP data base, has it been validated? How
reliable is the data? Some concerns were addressed in limitations which is good.
It should be stated that what kind of study this is (retrospective cohort national cohort study)
in methods.
Reference no 14 is very old, are there no more recent studies comparing this?
In Table 1, are any colectomies clean? Shouldn't they at least be clean-contaminated?
Is possible to know if all antibiotics given were parenteral or could there be oral as well?
Review for 10.1186/s12876-022-02491-8 (2022)

Title: Impact of bowel preparation on elective colectomies for diverticulitis: analysis of the
NSQIP database
Version: 3 Date: 08 Jul 2022
Reviewer's report:
Clearly written manuscript and well-designed study.
Table 1: it would be more helpful to know the proportion of each sub-group who had had
prep/type of prep vs no prep/another type of prep rather than the proportion of each sub-group
represented in a prep status. E.g. what proportion of each ethnicity had bowel prep vs no bowel
prep rather than what is the ethnicity breakdown within the bowel prep group. This would give a
better idea of the potential disparaties by sociodemographic categories rather than the proportion
of each subgroup in the study cohort.
General comments:
-Are there regional variations in clinical practice that the authors could comment on? or a 'gold
standard' or best practice guideline with regards to prep. This would be useful information to
have in either the introduction or discussion.
-If the proportions recommended in my comments regarding Table 1 do contain disparities/
inequities by sociodemographic group, this should be commented on.
Review for 10.1186/s12876-022-02488-3 (2022)

Title: Association between dietary antioxidant index and risk of Helicobacter pylori infection
among adults: a case–control study
Version: 2 Date: 12 Jun 2022
Reviewer:  Hong Cheng
Reviewer's report:
Helicobacter pylori infection is closely related to a variety of gastrointestinal diseases and is an
important risk factor for gastric cancer. Exploring the protective factors against Helicobacter
pylori is helpful to the prevention and control of Helicobacter pylori infection. In this case-
control study, the authors investigated the association between dietary antioxidant index and
risk of Helicobacter pylori infection among adults. They found appropriate intake of nutrient
antioxidants may have a role in decreasing the likelihood of Helicobacter pylori infection risk.
There are some problems:
For the healthy control group, when judging that there was no Helicobacter pylori infection, the
patients who had been infected in the past should be excluded.
For those who are judged to have no Helicobacter pylori infection, whether to use any negative
test method to judge that they have no Helicobacter pylori infection, or to use some negative
test methods to judge that they have no Helicobacter pylori infection? For example, if the serum
antibody test and urea breath test are negative, it is judged that the patient has no Helicobacter
pylori infection. Please describe in detail in the article how to judge that the patient has no
Helicobacter pylori infection.
Review for 10.1186/s12876-022-02488-3 (2022)

Title: Association between dietary antioxidant index and risk of Helicobacter pylori infection
among adults: a case–control study
Version: 2 Date: 09 Jul 2022
Reviewer:  Felipe Mazzoleni
Reviewer's report:
Assessing the role of diet in H. pylori infection can help develop strategies to treat it.
Main comments:
1. H. pylori detection was made by different methods. Since the selection of patients was
determined by the presence or absence of H. pylori, it is better to use only one method, preferably
the gold standard, the anatomopathological. Without that,  describe which tests were used, and
their percentage, in each group, and assess whether there is significant differences.
2. Although patients were compared according to age, in baseline data, there was a significant
age difference between groups, which can generate a significant bias for this study, since age
influences H. pylori prevalence.
3. Many variables interfere with the prevalence of H. pylori, making it extremely important to
add in the multivariate analysis, for example, years of education.
4. Positive points: the author described the study limitations and the conclusion is consistent
with the results (although the title suggests a risk association). All the study tools to evaluate
the data are adequate, with validated questionnaires and index (DAI), which is mandatory for
studies that assess diet habits.
Minor comments:
1. I suggest a specialized translator in English medical articles translate the article.
2. H. pylori should be written in italics.
Review for 10.1186/s12876-022-02492-7 (2022)

Title: Poorly Differentiated Cluster Grade-A Vital Predictor for Lymph Node Metastasis and
Oncological Outcomes in Patients with T1 Colorectal Cancer: A Retrospective Study
Version: 2 Date: 13 Jun 2022
Reviewer's report:
Xiaolin Ji et al. investigated the PDC as a predictor for LNM and prognosis in T1 CRCs. They
concluded the PDC was an independent risk factors for LNM and indicated shorter OS and DFS.
Although this paper needs some revisions, it is well-structured. To improve the quality of this
paper, my comments were as follows.
Major comments:
1. Please provide a breakdown of the number of cases of primary surgical resection and
secondary surgical resection followed by initial endoscopic resection in the methods section.
This is because the role of PDC as a risk factor for lymph node metastasis is essentially fulfilled
for cases treated with initial endoscopic resection.
2. How about the interobserver agreement for PDC grading among pathologists in this study?
Interobserver agreement in other predictors for LNM such as LVI or tumor grade were reported
to be low. The authors had better present the concordance for PDC grading even for 20-30 T1
cases between two pathologists participating in this study to validate the effectiveness of PDC
as a predictor.
3. A sufficient lymph node yield is important for a robust ground truth of lymph node status.
Please provide the mean number of LNs per patient in this dataset.
4. In a first paragraph in the results, please re-check the number in the following sentences. One
patient was missing. “The percentages of patients with different PDC grades were G1, 71.2%
(131/184); G2, 19.6% (36/184); and G3, 8.7% (16/184).”
5. This study included only surgical resection cases, which was one of the limitations the authors
should mention in the discussion section. This is because the endoscopic resection alone cohort
was essentially part of the true target.
6. Please provide clinical information such as patients age and sex, and tumor size, etc. in Table 1.
Minor comments:
1. Please add the reference of PMID 34942683, which is closely related to the issue of treatment
strategy of T1 CRC, in the same place as ref 18 in the introduction.
Review for 10.1186/s12876-022-02492-7 (2022)

Title: Poorly Differentiated Cluster Grade-A Vital Predictor for Lymph Node Metastasis and
Oncological Outcomes in Patients with T1 Colorectal Cancer: A Retrospective Study
Version: 2 Date: 30 Jun 2022
Reviewer's report:
This study shows that PDC grade is a factor that strongly reflects LNM and oncological outcome
in T1 colorectal cancer. This finding may be a criterion for deciding whether or not to perform
an additional bowel resection in patients undergoing endoscopic resection. However, I would
like to ask a few questions.
1. Although the report describes radical surgery, it does not indicate the extent to which lymph
node dissection is performed. For example, (1) How much of the intestinal tract was resected,
(2) Was lymph node dissection performed to the center with or without (CVL), (3) Is TME
performed for rectal lesions, etc.?
2.  How many patients received postoperative adjuvant chemotherapy?
3.  The type of distant metastasis is not mentioned.
4.  Whether the combination of risk factors mentioned is evaluated.
Review for 10.1186/s12876-022-02492-7 (2022)

Title: Poorly Differentiated Cluster Grade-A Vital Predictor for Lymph Node Metastasis and
Oncological Outcomes in Patients with T1 Colorectal Cancer: A Retrospective Study
Version: 4 Date: 17 Aug 2022
Reviewer's report:
The authors have satisfyingly answered to all the raised concerns and increased quality of the
manuscript.
I have one further minor comment.
#Please correct the  following last sentence in the introduction: "Additionally, strong
interobserver agreement was also found in our PDC grading." It should be changed to an
objective, not a result.
Review for 10.1186/s12876-022-02492-7 (2022)

Title: Poorly Differentiated Cluster Grade-A Vital Predictor for Lymph Node Metastasis and
Oncological Outcomes in Patients with T1 Colorectal Cancer: A Retrospective Study
Version: 5 Date: 31 Aug 2022
Reviewer's report:
Congratulations.
Review for 10.1186/s12876-022-02446-z (2022)

Title: Elevated Serum Ferritin Levels are Associated with Severity and Prognosis of Severe
Acute Pancreatitis: A Preliminary Cohort Study
Version: 1 Date: 17 May 2022
Reviewer's report:
Wang et al have, in a retrospective single center cohort study, investigated whether the levels of
serum ferritin might be correlated with disease severity in AP.
I find this study very interesting, involving reliable statistic methods and novel findings in the
field of AP.
However, the manuscript needs revision.
General comments
The manuscript is great in need of English language revision and general writing corrections.
Abstract
It would be interesting if the authors could present specific data and numbers also in the abstract
regarding the “significant increase in the proportion of patients with severe AP and a higher
proportion of SIRS in comparison…”
Introduction
Is it possible to present, in a more profound way, more about the physio-pathological scenario
regarding SF and different inflammatory diseases? Is there any data on sepsis for example?
Methods
# Why were patients > 80 years excluded? And patients with pancreatic tumors? Please explain
thus further in the manuscript
# What does it mean that a SF-level of >275 is ‘positive’?
# In the logistic regression analysis – did the authors adjust for any variable such as age, sex etc?
# Have the authors investigated a possible association between specific organ failures and SF
levels?
Results
# Which are the systemic complications in Fig 1H? Please specify
# Figure 1 presents median levels of SF in different scenarios. However in the manuscript the
authors write that the levels are ‘positively correlated’… However, THIS figure doesn’t show
the results of a correlation test? Compared to Fig 2
# Please describe, in more detail, the complications investigated regarding SF levels
# The authors claim that ‘logistic regression analysis indicated that serum SF was an independent
risk factor for SAP and organ failure….’ However what the authors have demonstrated is an
association between SF and SAP and SF OF, no investigation of risk factors has been performed.
Discussion
# were the positive correlations found between SF and ALT, AST etc expected?
# Although the authors found an association between SF levels and SAP and organ failure this
relationship is very weak when considering the odds ratios which need to be highlighted in the
manuscript
# The authors claim in the Discussion section that AP is a non-infectious disease, however this
not really the truth depending on which phase of the disease that’s in focus.
# Have the results from this study been confirmed in previous studies?
# The authors claim that SF ‘can be used as an ideal biomarker to predict the severity of AP’ – this
seems too much as an exaggeration, and not a result that can be concluded from a retrospective
study with unvalidated results.
# Can the authors specify in the text which inflammatory mediators they are referring to
regarding the involvement in the iron metabolism?
Review for 10.1186/s12876-022-02446-z (2022)

Title: Elevated Serum Ferritin Levels are Associated with Severity and Prognosis of Severe
Acute Pancreatitis: A Preliminary Cohort Study
Version: 3 Date: 19 Jul 2022
Reviewer's report:
I have read the revised version and the comments for reviewers from Wang et al investigating
elevated levels of serum Ferritin in patients with severe AP.
The manuscript has been carefully revised and reviewers comments adequately responded.
Therefore, in my opinion, the manuscript can proceed to publication.
Review for 10.1186/s12876-022-02490-9 (2022)

Title: Identification of Early Predictors for Infected Necrosis in Acute Pancreatitis
Version: 1 Date: 06 Apr 2022
Reviewer's report:
Mats L. Wiese report a much needed study on early predictor of infected necrosis in acute
pancreatitis. This study was analysed and written well even though the data were retrospective
and
nondynamic in nature. However, a few data were missing in the result and discussion section.
1) In the study it was reported that 89 patients had either EUS-FNA or drainage. It would have
been better if you distribute the values between EUS-FNA and Drainage. How many patients
had undergone EUS-FNA only without drainage?
2) In the study it was not mention about the time of organ failure and intervention. As early
infection is associated with increased mortality. ( Additional reference PMID:34774414)
3) It was reported that out of 89 patients, 50 patients had microbiologically confirmed
infection. However, data regarding nature of infection and type of organism was not
mention.
4) Prospective study will give us further direction regarding the validity of the model.
Review for 10.1186/s12876-022-02490-9 (2022)

Title: Identification of Early Predictors for Infected Necrosis in Acute Pancreatitis
Version: 1 Date: 16 May 2022
Reviewer's report:
The authors have tried to address an important research question: “prediction of infected necrosis
in patient with necrotizing pancreatitis”. Please find my comments.
Major Comments
1. The authors took a heterogeneous population for analysis. The study population was
patient with necrotizing pancreatitis requiring intervention such as aspiration and drainage. A
substantial proportion of patients with infected necrosis improve with antibiotics only (PMID
20417724) which were not included. Patients with acute on chronic pancreatitis also included.
2. Patients were classified to have infected necrosis on the basis of positive report on gram
stain or culture. However if a patient had undergone multiple interventions, any one positive
culture was classified as infected necrosis. Thus patients with initial sterile collection which got
infected after intervention also included erroneously. Patients with suspected infected necrosis
i.e. ongoing sepsis and/or worsening organ failure in a patient with necrotizing pancreatitis were
not included.
3. Though the authors have tried to include all plausible factors for prediction of infection in
necrotizing pancreatitis following important factors were missing:
a. Presence of organ failure in the first two weeks of illness (It is different from organ failure
developing after infection has set in. This parameter simply denotes severity of initial systemic
inflammation which may be reciprocated by an equally severe compensated anti-inflammatory
response resulting in infection of necrotic bed)
b. Extent of necrosis
It was not clear whether the lab parameters included in analysis were prior to infection or
after that. Since the factors which came out to be significant like CRP, albumin, creatinine can
be deranged in a patient with ongoing infection. The readers will be more interested in these
parameters at the baseline i.e. within first two weeks of illness prior to initiation of infective
cascade.
Minor comments
1. The sample size is small to predict a model
2. Usually 2/3rd of all necrotizing pancreatitis is sterile and 1/3rd get infected. However the
study shows 59 infected and 30 sterile pancreatitis which may be due to selection of patients
who have undergone intervention only. This should be highlighted in the discussion.
Review for 10.1186/s12876-022-02481-w (2022)

Title: Construction of a prognostic risk model based on apoptosis-related genes to assess tumor
immune microenvironment and predict prognosis in hepatocellular carcinoma
Version: 1 Date: 10 Jul 2022
Reviewer:  Yutaka Midorikawa
Reviewer's report:
Comment on the manuscript a5bc75ba-fdc4-4ca5-b984-7c52c11a7f0e by Wang, et al.
Despite of curative resection, HCC often relapse because of high grade of malignancy. This
paper established the risk score using 9 apoptosis-related genes from the TCGA data, which
could predict the patient survivals. The concept of the paper in intriguing, however, there are
major concerns that need to be addressed.
There are several questions and suggestions for corrections:
1) Study design is confusing. Nine apoptosis-related genes with expression aberration between
cluster A and B were selected. Using these predictor genes, the authors constructed risk score
and divided HCC patients into the high and low risk groups based on survival data. However,
I assume that it is a matter of course because these predictor genes were selected and validated
from the same TCGA cohort; 9 ARGs in high risk group were selected from Cluster A and those
in low risk group from Cluster B. Survival curves in Figure 3E should have been validated using
the independent cohort such as ICGC.
2) Similarly, nomogram in Figure 6A should have been validated using another cohort, not
TCGA.
3) It is not clear that only the apoptosis-related genes were focused for construction of risk score.
How about the expression of genes in the other categories?
4) Discussion about Figure 4F is insufficient.
5) The last sentence of Introduction should be removed because it is one of conclusions.
6) The word “gene signature” in the title or Figure 3 is inadequate because there is no data about
gene signature in this report.
Review for 10.1186/s12876-022-02481-w (2022)

Title: Construction of a prognostic risk model based on apoptosis-related genes to assess tumor
immune microenvironment and predict prognosis in hepatocellular carcinoma
Version: 1 Date: 11 Jul 2022
Reviewer's report:
This article by Wang and Ji aimed to establish a prognosis model based on apoptosis-related
genes (ARGs) to predict the outcome of HCC patients. Although it is indeed an urgent and
important matter to find an effective biomarker for the diagnosis and prognosis of HCC, this
topic has been investigated in several reports. The novelty is therefore limited. The following
are some suggestions that might help improve the manuscript.
1. Emphasize the novelty of this study. How is it different from previous results? What is its
value?
2. Compare the efficacy of this prognosis model to current clinical biomarkers, such as AFP.
3. Contrast and compare the results of previous reports that has also used ARGs as prognosis
biomarkers to your results.
4. Editing from a native speaker is required.
Review for 10.1186/s12876-022-02481-w (2022)

Title: Construction of a prognostic risk model based on apoptosis-related genes to assess tumor
immune microenvironment and predict prognosis in hepatocellular carcinoma
Version: 3 Date: 16 Aug 2022
Reviewer:  Yutaka Midorikawa
Reviewer's report:
Comment on the manuscript a5bc75ba-fdc4-4ca5-b984-7c52c11a7f0e by Wang et al.
The authors have satisfactorily addressed all my questions. The new version of the manuscript
by Wang et al. has been considerably improved by the addition of important data analyses that
were missing in the first version.
Review for 10.1186/s12876-022-02482-9 (2022)

Title: Systemic immune-inflammation index within the first postoperative hour as a predictor of
severe postoperative complications in upper abdominal surgery: A retrospective single-center
study
Version: 1 Date: 11 Jul 2022
Reviewer's report:
Dear editor
Thank you for giving me the opportunity to evaluate this work.
In this study,  310 patients who underwent upper GIS surgery were evaluated, the success of the
SII in predicting postoperative complications was studied.
The study is generally well designed and well written. I have a few comments to the authors;
1- Those with active infection (total lymphocyte count > 10 9/l) who were included in the
exclusion criteria from the study should be more clearly stated.
2- Was the ethics committee approval for the study or was it only IRB approval? Was an author
from the surgical specialty included in this study?
3- Is it routine to get a hemogram and biochemistry at the postoperative 1st hour from patients
who have had all upper GIS operations in your hospital? For example, what would be the clinical
benefit of checking albumin routinely in the 1st postoperative hour?
4- As a practice in our center, patients at risk of delayed extubation after UAS would be
transferred to the anesthesia intensive care unit (AICU) for further observation
What are the criteria for "delayed extubation"? Is there information about the complication rates
in patients followed in the general surgery intensive care unit?
5- The exclusion criteria were patients with incomplete medical records, who underwent
complex surgical procedures, with severe anemia, active bleeding, neutropenia and/or active
infection (total lymphocyte count >109/L).
-----it is recommended that the authors do a flow-chart showing how many patients were
excluded from these criteria.
6- How the oxygenation index is calculated should be stated in the method section.
Review for 10.1186/s12876-022-02482-9 (2022)

Title: Systemic immune-inflammation index within the first postoperative hour as a predictor of
severe postoperative complications in upper abdominal surgery: A retrospective single-center
study
Version: 1 Date: 18 Jul 2022
Reviewer's report:
The paper seems technically sound however, the claims are not fully supported by the data.
Please see the comments below.
Statistical analysis of the data is sound.
The primary outcome as the incidence of postoperative complications in a well-defined and
researched elective population does not seem novel.
What is novel is the exploration of the prognostic value of  SII in this patient population.
Table 4: I am having trouble understanding how an OR of 1.0  for SII is a significant predictor
of postoperative complications.
Table 6:
please indicate what the actual cut of value is
please indicate how many had SII # 754.6×109/L  and how many <754.6×109/L
Page 4 line 22: the word "with" is repeated twice
Page 5 line 15: "cholecystectomy in 117 patients, cholecystectomy in 10 patients" - is there a
difference in these patient groups? I think its suppose to be "liver resections"
Page 7 lines 24-26: Can you suggest a potential correlation when you prior to that conclude that
no significant difference was detected in this study?
Page 7 lines 28-33: Please elaborate why there is a need for yet another variable to predict PPC
when we have - as you write - lactate, CRP, age, etc already?
Page 7 line 38: "Finally, we did not detect SII level change over time during the follow-up
visits." Nowhere in the method section is it indicated a follow-up visit. This sentence comes up
out of the blue.
Page 8 Line 2: Please specify, is it the 1-h SII altogether or the cutoff value of SII.
Thank you.
Review for 10.1186/s12876-022-02482-9 (2022)

Title: Systemic immune-inflammation index within the first postoperative hour as a predictor of
severe postoperative complications in upper abdominal surgery: A retrospective single-center
study
Version: 2 Date: 12 Aug 2022
Reviewer's report:
All of my suggestions have been made. The article can be published as it is.
Review for 10.1186/s12876-022-02469-6 (2022)

Title: PNPLA3 and TM6SF2 genetic variants and hepatic fibrosis and cirrhosis in Pakistani
chronic hepatitis C patients: a genetic association study
Version: 0 Date: 07 Jun 2022
Reviewer's report:
This study by Rauff et al. “PNPLA3 and TM6SF2 genetic variants and hepatic fibrosis and
cirrhosis in Pakistani chronic hepatitis C patients: a genetic association study” investigates the
association of two major genetic risk variants with fibrosis and cirrhosis in Pakistani chronic
hepatitis C patients. The role of both variants for fibrosis/cirrhosis risk in patient with chronic
hepatitis C is debated. The current study is well written and provides important and detailed
information on this issue. The tested PNPLA3 and TM6SF2 polymorphisms were not identified
as major determinants of liver fibrosis/cirrhosis in Pakistani patients with CHC. One limitation
of this study is the limited power to detect true associations with modest effect sizes (OR ~1.3)
for cirrhosis.  However, this limitation is already stated by the authors.
Association results for rs738409 and rs58542926 allelic, recessive and genotypic unadjusted
analysis are clearly presented.
Multivariate regression analysis
1. Association results for rs738409 and rs58542926 from the multivariate regression analysis
are not provided.
Provide odds ratios and p values for rs738409 and rs58542926 from  multivariate regression
analysis for advanced hepatic fibrosis and hepatic cirrhosis to Table 5. Statistical models should
include the SNP (rs738409 or rs58542926) age, sex, body mass index and HCV viral load.
Models should not include liver enzymes. Variants PNPLA3 rs738409 and TM6SF2 rs58542926
are associated with increased ALT and AST (PMID: 34315874). Both enzymes are known
surrogate measures of liver fibrosis. Including liver enzymes in the model weakens the effect
for PNPLA3 and TM6SF2.
Correct the statement accordingly: “The same trend of no association with hepatic fibrosis or
cirrhosis persisted in the multivariate logistic regression models adjusting for age, gender, body
mass index, HCV viral load and liver enzymes (p = >0.05).
2. Diabetes mellitus is a significant risk factor for the development of liver cirrhosis in chronic
hepatitis C patients (PMID: 28831144). This is also acknowledged in the manuscript. “Indeed,
presence of hepatic steatosis and features of metabolic syndrome (including obesity and diabetes
mellitus) have been shown to exacerbate progression of hepatic fibrosis and cirrhosis in CHC
settings”.
But information on type 2 diabetes status is not provided.  Regression models were not adjusted
for diabetes status. If available, provide diabetes information in Table 1 and include diabetes in
the multivariate regression models. If not available, indicate absence of diabetes status in the
limitation sections of your manuscript.
Review for 10.1186/s12876-022-02469-6 (2022)

Title: PNPLA3 and TM6SF2 genetic variants and hepatic fibrosis and cirrhosis in Pakistani
chronic hepatitis C patients: a genetic association study
Version: 2 Date: 31 Jul 2022
Reviewer's report:
The authors implemented the reviewer’s suggestions in this revised version of the manuscript,
with significant improvements.
Minor comment:
Please correct the title of the Table from the additional file 3 regarding the term severe hepatic
fibrosis.