JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-9-78 (2009)

Reviewer's report
Title:Importance of Duodenal Bulb Biopsies in the Diagnosis of Celiac Disease
in Clinical Practice
Version: 1Date:15 June 2009
Reviewer: David Sanders
Reviewer's report:
Minor Essential
1. The authors do not clarify if the study has been performed solely by a single
endoscopist? I suspect this is the case but it needs to be more explicitly stated in
the methods.
2. Was the endoscopist aware of the positive TTG result? Again I would imagine
yes but needs to be stated.
3. With regards to the pathologists – the authors are right to say this is real
clinical practice with multiple pathologists reporting. However, was there any
internal validation check? For example, did the pathologists as a group re-assess
any of the cases to ensure that the initial reports were accurate? If so did they do
this for the whole cohort?
4. Table 1 is not particularly valuable. I would recommend deleting it and instead
providing a table with all 35 patients. This allows the readers to see all cases.
This is important because although the authors comment on discordant cases
between bulb and distal duodenum – they do not comment on concordance for
severity. In other words for the 29 concordant cases was the degree of villous
atrophy the same?
5. Within this table they should also give a TTG level that is quantitative (along
with a normal range). Symptoms allow the reader ascertain whether there may
be a relationship between severity of symptoms and likelihood of having only D1
involved or any other pattern which may immerge.
6. The authors should provide statistics – this should be between concordant and
discordant results. This is likely to be a chi-square and likely to be negative but
that is ok – the information should still be presented.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-9-78 (2009)

Reviewer's report
Title:Importance of Duodenal Bulb Biopsies in the Diagnosis of Celiac Disease
in Clinical Practice
Version: 1Date:6 July 2009
Reviewer: Peter Green
Reviewer's report:
major revisions
The aim of this paper is to document that biopsy of the duodenal bulb increases
the yield of celiac disease diagnosis in patients in whom the diagnosis is
considered.
1. The study is a retrospective review of biopsy reports, performed without the
aid of a pathologist. This must be stated.
2. Discussion
The authors accept that there may be differences in villous height in the
duodenal bulb. Why is that? This must be referenced.
3. Page 6, second paragraph. Were the patients with Marsh I and II lesions
diagnosed as celiac disease and commenced on a GF diet. This is somewhat
controversial as villous atrophy is usually required for a dx of celiac disease Why
were these patients diagnosed with celiac disease.
Discretionary revisions
There are many issues raised by gastroenterologists when one talks about
biopsy of the duodenal bulb because we are taught NOT to biopsy the bulb.
European studies have shown what the authors have shown. There is no new
data presented in this paper.
Specific points
Results
There is insufficient pathological data presented
How many biopsy pieces were sufficiently oriented for assessment of villous
atrophy?
There is no data as to the presence or absence of Brunner’s glands, and whether
they were in the mucosa or submucosa and if they interfered with the villous
architecture interpretation.
Was gastric metaplasia present? Did that interfere with the interpretation of
villous atrophy.
These are all factors that are used to argue against taking duodenal bulbar
biopsies.
A pathologist should review the slides to record this data
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-9-76 (2009)

Reviewer's report
Title:Genetic risk factors for intestinal metaplasia in a high risk
Singapore-Chinese population: a cohort study
Version: 1Date:9 July 2009
Reviewer: Nobuyuki Hamajima
Reviewer's report:
This study provides useful information on genetic traits for intestinal metaplasia
(IM) among Singapore-Chinese. To record full information, the below points are
recommended.
Major compulsory revisions
1. Since genotype/allele frequencies themselves are usuful information for other
studies, the genotype frequencies should be listed in the three categories (major
homo, hetero, and minor homo), not two categroies listed in Table 3.
Minor essential revisions
2. HWE should be examined for all subjects, but not necessary for the HP- group
and HP+ group, because the condition may be associated with the genotypes. It
is not clear whether the sentence "All polymophisms were in Hardy-Weinberg
equilibrium (HWE), except .." means that the examination was done for all
subjects. The p-value from HWE tests should be described in text or in Table 3.
3. Even if HP-, those with IM are regarded as being infected in the past. Since
those with IM were relatively common in the study subjects, the subgroup
analysis for IM among the infected subjects (HP+ or IM) would be informative. If
IM develops without HP infection among Singapore-Chinase as described in
"However, its association with increased risk of IM in HP negative individuals
suggests it may play a role independently of this factor" in the last sentence of
Discussion, the subgroup analysis is not needed.
4. The authors showed the percentages of those aged more than 60 years in
Table 2. The description of age distribution according to 5 or 10 year age-group
would be more informative.
5. "PTPN11 rs2301756 GA/AA" would be better than "PTPN11 SNP" in the first
line of page 7.
6. Reference 21 reported that the reduced risk of gastric atrophy was observed
only for AA genotype, not for GA/AA. The report on the OR for AA will be
recommended.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-76 (2009)

Reviewer's report
Title:Genetic risk factors for intestinal metaplasia in a high risk
Singapore-Chinese population: a cohort study
Version: 1Date:16 July 2009
Reviewer: Carlo-Federico Zambon
Reviewer's report:
Major Compulsory Revisions:
1. Patients characteristics should be more detailed (e.g. mean age and range,
definition of family history of gastric cancer, of drinking and smoking conditions,
eventual previous eradication therapy for H. pylori).
2. Since biopsy specimens were available for IM assessment was H. pylori
infection diagnosis performed also by mean of histology (gold standard)? Was it
possible to correlate it with the serological findings?
3. Was serum PGA/PGC ratio considered in screening of high GC risk
populations in combination with genetics and H pylori serological diagnosis?
4. When possible (IL-10 and STCH genes) haplotype analysis of SNPs might be
relevant.
5. Data recently reported by from Hishida and colleagues (BMC Gastroenterol
2009 Jul 9) on PTPN11 polymorphism and GC risk in a numerous Japanese
population should be discussed.
Minor Essential Revisions:
1. It appears that Authors have studied 18 polymorphisms (17 SNPs plus IL-1RN
VNTR) in 14 candidate gene not 17 polymorphisms in 13 genes as stated in
several occasion.
2. “.. Carriers of the NQO1 609CT/TT genotype showed ...” should be changed to
“carriers of the NQO1 609 T allele” or “carriers of the NQO1 C/T or T/T
genotypes…”. This applies throughout the paper to all genes considered.
3. Table 3: IL1RN VNTR genotypes do not include allele 1. Is it absent from the
Chinese studied population?
4. In background section relevant references should be cited for candidate genes
with respect to their association with gastric cancer risk.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-76 (2009)

Reviewer's report
Title:Genetic risk factors for intestinal metaplasia in a high risk
Singapore-Chinese population: a cohort study
Version: 2Date:21 August 2009
Reviewer: Nobuyuki Hamajima
Reviewer's report:
I understand the responses except the below two points.
Major Compulsory Revisions
1. The authors responsed that the p-value of HWE was >0.05, but it is 0.015 for
IL10 -819T/C (186, 124, and 38), and <0.001 for NQO1 609C/T, based on the
figures in Table 3. Both showed a significant finding. Are the authors sure that
the genotyping was correct?
2. As the authors stated "there is a high probability that IM+ subjects had HP
infection at some stage", the analysis for the infected (IM+ or HP+) is also
requested.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-76 (2009)

Reviewer's report
Title:Genetic risk factors for intestinal metaplasia in a high risk
Singapore-Chinese population: a cohort study
Version: 2Date:24 August 2009
Reviewer: Carlo-Federico Zambon
Reviewer's report:
no revision needed
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-76 (2009)

Reviewer's report
Title:Genetic risk factors for intestinal metaplasia in a high risk
Singapore-Chinese population: a cohort study
Version: 2Date:24 August 2009
Reviewer: charles S rabkin
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
We declare that we have no competing interests.
Review for 10.1186/1471-230X-9-76 (2009)

Reviewer's report
Title:Genetic risk factors for intestinal metaplasia in a high risk
Singapore-Chinese population: a cohort study
Version: 3Date:20 September 2009
Reviewer: Nobuyuki Hamajima
Reviewer's report:
None.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-74 (2009)

Reviewer's report
Title:Vitamin C supplement use may protect against gallstones: an
observational study on a randomly selected population
Version: 3Date:7 July 2009
Reviewer: Silvana Zanlungo
Reviewer's report:
Although the study is interesting, the association between gallstones and vitamin
C is known since several decades.
The work is well written. The major problem is the small number of cases for the
reliability of the statistical analysis. I strongly suggest that the manuscript needs
to be seen by a statistician.
1. Is the question posed by the authors well defined?
Yes
2. Are the methods appropriate and well described?
Yes
3. Are the data sound?
Yes
4. Does the manuscript adhere to the relevant standards for reporting and data
deposition?
Yes
5. Are the discussion and conclusions well balanced and adequately supported
by the data?
Yes
6. Are limitations of the work clearly stated?
Yes
7. Do the authors clearly acknowledge any work upon which they are building,
both published and unpublished?
Yes
8. Do the title and abstract accurately convey what has been found?
Yes
9. Is the writing acceptable?
Yes
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
'I declare that I have no competing interests'
Review for 10.1186/1471-230X-9-74 (2009)

Reviewer's report
Title:Vitamin C supplement use may protect against gallstones: an
observational study on a randomly selected population
Version: 3Date:14 July 2009
Reviewer: Chung-Jyi Tsai
Reviewer's report:
This is a population-based study investigating the association between vitamin C
supplementation and prevalence of gallstones using abdominal ultrasound
examination as the tool of diagnosis. The report indicated that there was an
inverse association between supplementation of vitamin C and gallstone
prevalence. The strength of the report is the large sample size in a retrospective
study.
1. In the Abstract: “ To assess the possible influence………..” would be most
appropriate as Aim or Purpose rather than Background.
2. In the Results of Abstract: “…….Female gender, hereditary
predisposition……were associated with risk of gallstone formation” This is a
cross-sectional retrospective analysis rather than a prospective study, so it would
be more appropriate to report as association with prevalence of gallstones
instead of risk of gallstone formation. For same reason, it would not be
appropriate to report a “protective effect” because this is not a clinical trial or
prospective study.
3. In the Conclusions, for the same reason it would not be appropriate to
conclude that “………a protective effect on the development of gallstones”
4. In the statistical model there is a covariate of inflammatory bowel disease,
presumed as personal history, but it is was not reported in the tables.
5. In the results the authors reported regular vitamin C use and duration, but
there was no dosage information and its analysis. For example, one tablet daily
for one year vs. two tablets daily for six months may differ in the associations.
6. Because all the results were reported as odds rather than relative risk as this
is a cross-sectional retrospective analysis, it would be better to use risk of
gallstones in the manuscript.
7. What are the associations between vitamin C supplement and gallstone
prevalence among participants with vs. without diabetes and others such as low
vs high physical activity, obese vs. normal weight in BMI, males vs females, etc.
8. There is no validation study on the use of vitamin C for the data collected in
the questionnaire.
9. It would be better to address the issue of misclassification in the assessment
of exposures.
Review for 10.1186/1471-230X-9-74 (2009)

Reviewer's report
Title:Vitamin C supplement use may protect against gallstones: an
observational study on a randomly selected population
Version: 4Date:28 August 2009
Reviewer: Henning Wittenburg
Reviewer's report:
I reviewed the revised version of the manuscript entitled "Vitamin C supplement
use may protect against gallstones: an observational study on a randomly
selected population" and the authors' response to my critisisms of the previous
version of the manuscript. The answers to my original criticisms have been are
completely satisfactory and the authors have revised the manuscript accordingly.
Due to the importance of this article in the field I therefore recommend
publication of the manuscript without further revisions.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-74 (2009)

Reviewer's report
Title:Vitamin C supplement use may protect against gallstones: an
observational study on a randomly selected population
Version: 4Date:18 September 2009
Reviewer: Chung-Jyi Tsai
Reviewer's report:
The concerns of the submitted manuscript are still unresolved (please see the
initial comments/review. This reviewer suggested rejection)
Review for 10.1186/1471-230X-9-73 (2009)

Reviewer's report
Title:Hepatitis B Virus Inhibition in Mice by Lentiviral Vector Mediated Small
Interference RNA
Version: 1Date:13 May 2009
Reviewer: Patrick Arbuthnot
Reviewer's report:
The authors describe an assessment of the efficacy of lentiviral vectors encoding
RNAi activators that target 2 sites within the HBV genome and demonstrate
silencing of markers of viral replication in a hydrodynamic model of HBV
infection. The investigation of the usefulness of lentiviral vectors for silencing of
HBV infection is important as the ideal vector for RNAi-based treatment of HBV is
yet to be established. Utilising lentiviral vectors may well have some advantages.
There are however points about the reported investigation that need to be
addressed before a clear understanding of lentiviral vector utility can be
established.
Major Compulsory Revisions
1 In the introduction, mention is made that RNAi is a surveillance mechanism.
Although this may be true RNAi is most important for the processing of primary
miRs, which have important functions for regulation of gene expression.
2 Exclusion of non specific effects to account for the observations is important.
This includes providing evidence that the vectors generate generate exogenous
antiHBV activators of RNAi.
3 The method employed to deliver the lentiviral vectors, hydrodynamic injection,
is an unconventional way of administering a vector. Low pressure injection would
give a clearer insight into the efficiency of lentiviruses as vectors for HBV
treatment.
4 It is assumed that there is integration of the vector provirus into the mouse
genome, but the evidence for this (e.g. using Southern blot hybridisation) is not
provided.
5 The discussion of the drawbacks of using lentiviral vectors that express U6
shRNA cassettes for therapeutic application needs expansion. For example,
overexpression of hairpins from a U6 promoter within AAV vectors has been
shown to be toxic. Stable integration of similar cassettes, such as are used in this
study, potentially has profound undesirable effects.
6 Surely the lenti vectors deliver an expression cassette that produce shRNAs
and not siRNA. siRNAs are a product of Dicer processing of the hairpins.
Level of interest: An article of limited interest
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-73 (2009)

Reviewer's report
Title:Hepatitis B Virus Inhibition in Mice by Lentiviral Vector Mediated Small
Interference RNA
Version: 2Date:28 July 2009
Reviewer: Patrick Arbuthnot
Reviewer's report:
Acceptable
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-73 (2009)

Reviewer's report
Title:Hepatitis B Virus Inhibition in Mice by Lentiviral Vector Mediated Small
Interference RNA
Version: 2Date:17 August 2009
Reviewer: Anja Ehrhardt
Reviewer's report:
The authors made several changes to the manuscript and included a figure
showing GFP expression in liver tissue after injection of lentiviral vectors. They
also explained the rational for using hydrodynamic delivery of lentiviral vectors.
Overall, they improved the manuscript and I would support publication. There is
only one minor issue which needs further clarification:
The author show that they detected GFP expression in murine liver after
lentivirus injection. Maybe I missed that information but I am assuming that Deng
et al. used hydrodynamic delivery of lentiviral vectors for experiments shown in
Fig 2. This should be clearly stated in the Materials and Methods section and in
the respective figure legend.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-72 (2009)

Reviewer's report
Title:Child-Pugh score is superior to model for end-stage liver disease score
(MELD) in predicting survival on and need for removal from waiting list in patients
awaiting liver transplantation
Version: 1Date:9 May 2009
Reviewer: Teh-Ia Huo
Reviewer's report:
The authors investigated the predictive accuracy for the outcome between the
CTP and MELD system. They concluded that CTP is superior to the MELD for
outcome prediction. There have been abundant studies in this regard during the
past 6-7 years. This study does not provide new or novel information.
The MELD has been chosen by the UNOS since 2002 in the US as the major
reference system for organ allocation in liver transplantation. The authors prvided
data to argue against this strategy. However, the case number in this study was
relatively small (n=268). More importantly, the authors did not report the AUC
values for CTP and MELD, and the p value for the statistical difference (Fig. 2),
which I suppose there is no statistical difference between CTP and MELD.
Therefore, their findings do not justify the conclusion.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-72 (2009)

Reviewer's report
Title:Child-Pugh score is superior to model for end-stage liver disease score
(MELD) in predicting survival on and need for removal from waiting list in patients
awaiting liver transplantation
Version: 1Date:25 May 2009
Reviewer: Ilka Boin
Reviewer's report:
Minor essencial revisions about reference, table titles and put the confidence
intervals results
Level of interest: An article of outstanding merit and interest in its field
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, and I have assessed the statistics in my report.
Review for 10.1186/1471-230X-9-72 (2009)

Reviewer's report
Title:Child-Pugh score is superior to model for end-stage liver disease score
(MELD) in predicting survival on and need for removal from waiting list in patients
awaiting liver transplantation
Version: 1Date:28 May 2009
Reviewer: Michael A Fink
Reviewer's report:
Major compulsory revisions:
1. The crux of the paper is the comparison of CTP and MELD score with respect
to prediction of waiting list mortality. The paper asserts that CTP is superior in
this regard. However, statistical analysis to support this is not presented. I think
that it is essential that the C-statistic for CTP and MELD are given and a P value
for the comparison be given.
2. Optimal cut-offs for CTP and MELD are given, but the method of determining
these is not described. This should be corrected.
3. The first 2 paragraphs of the discussion reproduce information contained in the
introduction. These should be removed from the paper. They could be replaced
by a very brief summary of the introduction.
4. Tables 5a and 5b do not contribute any substantial additional information and
are not further considered in the paper. They should be removed.
Minor essential revisions:
1. There are some minor grammatical issues that need to be corrected. For
example, Results page 1, last paragraph: "Of 29 patients died or removed..."
should read "Of 29 patients who died or were removed..."
2. Discussion page 1, 3rd paragraph: "In our study that compromised ..." should
read "In our study that comprised ..."
2. Discussion, page 2, 1st paragraph: "indicating, that patient with compensated
cirrhosis" should read "indicating that patients with compensated cirrhosis"
Discretionary revisions:
1. The mean MELD score of all patients in the study was 14.2. This seems
relatively low. It has previously been demonstrated that below a MELD score of
15, patients have a higher risk of death from transplantation than waiting list
death (Merion et al Am J Transpl 2005;5:307-13). This issue deserves some
consideration in the discussion.
2. The authors assert that other studies evaluating MELD and CTP "did not take
into account patients removed from the waiting list due to poor condition". In fact,
in one paper evaluating risk factors, including CTP and MELD, for waiting list
mortality, patients who were listed for transplantation and were removed from the
waiting list due to poor condition and subsequently died were included in the
waiting list mortality group (Fink et al. J Gastroenterol Hepatol. 2007;22:119-24)
Level of interest: An article of importance in its field
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-72 (2009)

Reviewer's report
Title:Child-Pugh score is superior to model for end-stage liver disease score
(MELD) in predicting survival on and need for removal from waiting list in patients
awaiting liver transplantation
Version: 1Date:30 May 2009
Reviewer: Ben-Hur Ferraz-Neto
Reviewer's report:
The article wrote is showing an interesting point, once we are seeing the world
accepting MELD score as the best method for liver graft allocation. Regarding to
this issue, the autors shown a better correlation with Child-Pugh in predicting
survival on and need for removal from waiting list in patients awaiting liver
transplantation.
We do know that MELD score has faild in some cases and we do have to
improve our methods to predicting survival on the waiting liver transplant lists.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-72 (2009)

Reviewer's report
Title:Limitations of the MELD score in predicting mortality or need for removal
from waiting list in patients awaiting liver transplantation
Version: 2Date:22 July 2009
Reviewer: Teh-Ia Huo
Reviewer's report:
There is significant improvement in this revised paper and may be accepted as it
is now.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-72 (2009)

Reviewer's report
Title:Limitations of the MELD score in predicting mortality or need for removal
from waiting list in patients awaiting liver transplantation
Version: 2Date:3 August 2009
Reviewer: Michael A Fink
Reviewer's report:
The authors have addressed most of my concerns and those of the other
reviewers. I note, however, that a major error persists in the current version.
Table 4 identifies the sensitivity and specificity of CTP as 68.9% and 70.1%,
respectively and the sensitivity and specificity of MELD as 62.0% and 72.6%,
respectively. Derived from the table, the correct figures are: 69.0% and 70.5% for
CTP and 62.1% and 72.7% for MELD. In the abstract and the results section, the
sensitivity and specificity figures are reversed: "The sensitivity and specificity to
identify mortality or severe deterioration for CTP was 70.1% and 68.9%,
respectively; for MELD, it was 72.6% and 62.0%, respectively. "
In terms of determining the ideal cut-off for each of the measurements, this would
usually be derived from the ROC analysis. The authors report that the cut-offs
were "determined by minimizing the false positive and false negative results of
each score". It is not clear to me exactly how this was done and I think that the
appropriateness of this technique needs to be confirmed by a statistician.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-71 (2009)

Reviewer's report
Title:What are the risk factors of colonoscopic perforation?
Version: 2Date:13 June 2009
Reviewer: Anthony Teoh
Reviewer's report:
Major Compulsory Revisions
Results section
- A no. of other risk factors for analysis could be included for analysis: Previous
operations, pelvic operations, pelvic inflammatory diseases, pelvic radiotherapy,
diverticular disease, sigmoid volvulus, peritoneal dialysis, pseudoobstruction,
presence of intra-abdominal adhesions, presence of colonic malignancy and
co-morbidities
Discussion
- It is a bit alarming that the overall perforation rate has increased significantly in
this study as compared to your last review. How does the outcomes of this study
compare to your last study? Any potential contributing factors to increased
perforations? Can you discuss in the discussion section
Minor Essential Revisions
Methods section
- What is the definition of emergency endoscopy? Do you give bowel prep to
these patients?
- For the sedation group, only propofol and fentanyl was used. Did any patients
received other sedatives e.g. benzodiazepams. Do you think that the choice of
drugs for sedation affects the endoscopist’s perception of pain experienced by
the patient?
- Further, was propofol during your last review from 1999 to 2007? Do you think
this could possible have affected the overall perforation rates?
- 2L of PEG as bowel preparation may not be adequate in some patient. Was
there documentation of the quality of bowel prep? Is this different between the
perforated and non-perforated groups?
Results section
- 6/15 perforations due to trainees that is quite a high percentage, is there any
explanation? Your no. in colonoscopies seems to have grown throughout the
pass few yrs. Are more colonoscopies being performed by trainees?
- What is the proportion of perforations that are sustained from diagnostics and
therapeutic colonoscopies. Is the difference significant?
- Some suggestions to table 1, the endoscopic procedure should be grouped into
whether it is diagnostic or therapeutic and the possible mechanism of perforation
is probably better grouped according to whether it is mechanical or due to a
procedure (hot/cold biopsy, polypectomy).
- What are the P values and odds ratio of the factors on multivariate analysis, pls
list out in table
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: Yes, and I have assessed the statistics in my report.
Declaration of competing interests:
I have no disclosures to make.
Review for 10.1186/1471-230X-9-71 (2009)

Reviewer's report
Title:What are the risk factors of colonoscopic perforation?
Version: 2Date:21 June 2009
Reviewer: Gregorios Paspatis
Reviewer's report:
General comments
This is a well designed study. The data were collected prospectively and they
were analyzed retrospectively (hisrorical cohort). Indded the existed data in the
literature regarding peforations in colonoscopy are adequate.However data
regarding the risk factors associated to colonic prforations are valuable.The
paper is well written.
Specific comments
1.Colonoscopic perforation occur more often in women. The authors should
mention this point in the Discussion
2. It would be interesting to present the number of snare polypectomies and
endoscopic mucosal resection
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-71 (2009)

Reviewer's report
Title:What are the risk factors of colonoscopic perforation?
Version: 2Date:24 June 2009
Reviewer: David Farley
Reviewer's report:
A few grammatical mistakes, but overall, fairly well written.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-71 (2009)

Reviewer's report
Title:What are the risk factors of colonoscopic perforation?
Version: 3Date:13 September 2009
Reviewer: Anthony Teoh
Reviewer's report:
The authors have adequately revised the manuscript.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-70 (2009)

Reviewer's report
Title:The roles of tumor necrosis factor-alpha in colon tight junction protein
expression and intestinal mucosa structure in a mouse model of acute liver
failure
Version: 4Date:25 May 2009
Reviewer: Salvatore Cuzzocrea
Reviewer's report:
In this paper the authors show that TNF-# affects the structure of the intestinal
mucosa, decreases expression of ZO-1, and affects the morphology of the colon
in a mouse model of acute liver failure, by the use of anti-TNF-# IgG antibody or
anti-TNF-# R1 antibody. The work is well thought-out and well executed, and the
data support the author conclusions, but there are some questions that need to
be addressed:
Major Compulsory Revision
1. TNF-# increases intestinal epithelial tight junction permeability. Moreover it has
been demonstrated that TNF-#-induced increase in Caco-2 cell TJ permeability
was mediated by NF-kappa B activation. What is the role of TNF-# on NF-kappa
B activation in this model?
2. There are data with knockout mice about the role of TNF-# in model of acute
liver failure?
Minor essential revisions
1. The manuscript needs to be carefully revised
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests'
Review for 10.1186/1471-230X-9-70 (2009)

Reviewer's report
Title:The roles of tumor necrosis factor-alpha in colon tight junction protein
expression and intestinal mucosa structure in a mouse model of acute liver
failure
Version: 4Date:2 July 2009
Reviewer: Hiroyasu Ito
Reviewer's report:
Comments;
In this manuscript, the authors have investigated the effects of TNF-# on the
ultrastructure of the intestinal mucosa using acute liver failure murine model.
They demonstrated that TNF-# damages TJs and affects the expression of ZO-1
protein in vivo, and may participate in the pathological mechanism of SBP
complicated to ALF. Although the present data are potentially easily
understandable and very interesting, there are several issues that should be
addressed as noted below.
Major;
1, Authors demonstrated that TNF-# damages TJs and decreases the expression
of ZO-1 protein in vivo. However, in the group in which only mice was
administrated with recombinant TNF-#, there was no damage on TJs and the
expression of ZO-1 was not decrease. If high dose of recombinant TNF-# was
injected to mice, is it observed the damage of TJs and the decrease of the
expression of ZO-1?
Authors should discuss on these issues.
2, In Western blot analysis of tissue ZO-1 content, the author should show the
internal control protein expression (e.g. #-actin, GAPDH etc.) to normalize for
protein loading. (Fig. 5)
3, In Fig.1, the concentration of TNF-# level was elevated at 9 hour after
GalN/LPS injection again. Why are observed these bimodal peaks of the
concentration of TNF-# level after GalN/LPS injection?
Authors should address this issues in Discussion.
Minor;
1, In Table 1, number of mice in the groups of anti-TNF-#-IgG+GalN/LPS and
anti-TNF-#R-IgG+GalN/LPS might be wrong.
2, The description `TNF-a` at line 32 in Discussion might be wrong.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-70 (2009)

Reviewer's report
Title:The roles of tumor necrosis factor-alpha in colon tight junction protein
expression and intestinal mucosa structure in a mouse model of acute liver
failure
Version: 4Date:2 July 2009
Reviewer: Damien Masson
Reviewer's report:
The manuscript “The roles of tumor necrosis factor–alpha in colon tight junction
protein expression and intestinal mucosa structure in a mouse model of acute
liver failure” by Hong-li Song et al. demonstrate with a mouse model of acute liver
failure that the TNFa induces an intestinal epithelial barrier disruption and a
bacterial peritonitis.
- This study with eight groups of mice (n=8 mice per group) is well designed.
- The choice of the target ZO-1 gene used is pertinent.
- The authors investigate strong histopathological parameters of this acute liver
failure mouse model.
- The time points of 2h, 6h, 9h for the histological and transcriptional analysis are
justified.
Minor Essential Revisions
The manuscript and particularly the experimental design on mouse model is well
written, and this study has exciting implication for early pharmacological
intervention by targeting TNF or TNFR1. Indeed, the efficiency and protective
effects of 2 mAb (anti-TNFa and anti-TNFa-R1) were demonstrated. This last
point could be discussed
The authors suggest that TNFa induces tight junction disruption and ZO-1
expression down-regulation. However, the chronology of events could be
discussed. The first TNFa peak 2h post injection may induced the ZO-1 down
expression and the tight junction disruption observed at 9h. Effectively, only the
GalN/LPS treatment induces an high serum TNFa level increased and they found
that major alteration of the intestinal epithelial barrier occurred 9h after GalN/LPS
treatment. In fact, at 9h post treatment, the multi-visceral decompensation was
evident (liver necrosis, intestinal epithelial barrier disruption …) and the second
TNFa peak 9h post injection was perhaps the result of the bacterial invasion.
This last point could be discussed
The reference following the sentence “ Among the pro-inflammatory mediators,
the TNFa and TNFaR1 systems …” 24 is not appropriate and could be replaced
by the references 25 and 26.
In the legend (Figure 2) : “Transmission electron microscopy of mousse …., the
GalN/LPS group (D, E and F), and groups …” must be corrected by
“Transmission electron microscopy of mousse …., the GalN/LPS group (D), and
groups …” (E) and (F) are respectively LPS control group and galN control
group.
The figure 3 legend could be more concise without repetition.
A good correlation was found between mRNA and protein ZO-1 expression at 2h,
6h, 9h after GalN/LPS treatment. So The figures 5 and 6 could be associated.
However The membranes could be reprobed with anti b-actin antibodies to
control the protein electrophoresed amount.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests
Review for 10.1186/1471-230X-9-70 (2009)

Reviewer's report
Title:The roles of tumor necrosis factor-alpha in colon tight junction protein
expression and intestinal mucosa structure in a mouse model of acute liver
failure
Version: 6Date:7 August 2009
Reviewer: Hiroyasu Ito
Reviewer's report:
Minor Essential Revisions
This manuscript should be checked by a native speaker.
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Review for 10.1186/1471-230X-9-69 (2009)

Reviewer's report
Title:Phosphodiesterase-5 inhibitors have distinct effects on the hemodynamics
of the liver
Version: 1Date:15 May 2009
Reviewer: Martin Hennenberg
Reviewer's report:
In the current manuscript, Halverscheid et al. tested the effects of PDE5
inhibitors on intrahepatic microcirculation of normal rats. Hepatic blood flow
regulation is of particular importance for portal hypertension in liver cirrhosis. Due
to the lack of sufficient therapeutic options, complications of portal hypertension
are still frequent and highly life-threatening in patients with cirrhosis. Therefore,
new therapies are urgently required. The authors assume that their current
results obtained from non-cirrhotic rats may provide the basis for subsequent
investigations in animal models of cirrhosis with portal hypertension.
To my opionion, the current manuscript of Halverscheid et al. should absolutely
not be regarded for publication in ?BMC Gastroenterology?.
Major points:
There are already at least 2 publications describing the effects of sildenafil in rats
with experimentally-induced cirrhosis (Ghali-Ghoul et al 2007;
Tahseldar-Roumieh et al 2006) ! These authors concluded that PDE5 inhibitors
are unsuitable for therapies in cirrhosis (e.g. for portal hypertension), since they
severely aggravate extrahepatic vasodilation ! Even 3 authors (Clemmesen et al
2008; Lee et al 2008;Thiesson et al 2005) investigated the hemodynamic effects
of sildenafil in patients with cirrhosis. These studies confirmed the aggravation of
extrahepatic vasodilation for the human setting, and did not reveal any beneficial
porto-hypotensive effect. However, only one of these studies is cited and
discussed in the current manuscript. With this background, the current
manuscript appears totally superfluous, as different studies already suggested
that the use of PDE5 inhibitors in cirrhotic patients and animals may be
disappointing.
Although the NO/cGMP system is investigated as a mediator and possible
therapeutic target in portal hypertension since almost 2 decades, absolutely none
NO/cGMP-based or ?targeting therapies emerged to the clinical use to date ! To
my opinion, any NO/cGMP-research in the context of portal hypertension is
therefore superfluous, and only led to success with regard to the carreers of
clinical scientist so far but not to new therapies. As currently available therapies
for complications of portal hypertension target vasoconstrictors and their direct
effectors, research should to my opinion concentrate on vasoconstrictor systems
in cirrhosis instead on NO/cGMP if promising results and new therapies are
desired in future.
From another point of view, it remains unclear to me, why the authors conclude
the need of studies in animal models of cirrhosis, but do not provide them. As
stated by the authors, their results can not answer the important questions
associated with their work (p. 15). In such a case, they should prepare and
submit a manuscript when having finished their studies.
Review for 10.1186/1471-230X-9-69 (2009)

Reviewer's report
Title:Phosphodiesterase-5 inhibitors have distinct effects on the hemodynamics
of the liver
Version: 1Date:21 May 2009
Reviewer: Han-Chieh Lin
Reviewer's report:
Major points
1. -Recently, phosphodiesterase-5 (PDE-5) inhibitor has been studied by
different investigators to improve pulmonary hypertension in cirrhotic patients
with primary pulmonary hypertension and to decrease portal pressure in cirrhotic
patients with portal hypertension. A dys-regulation of hepatic NO-cGMP system
due to over-expression of hepatic PDE-5 has been observed in cirrhotic patients
and animals. Thus, the hemodynamic effects of PDE-5 inhibitors should be
explored in cirrhotic animals. However, the current study only performed in
non-cirrhotic rats. Moreover, it is more important to explore the mechanistic
details of PDE-5 inhibitors in portal hypertension. Unfortunately, this study failed
to do so. In fact, both acute and chronic hemodynamic and mechanism of
different PDE-5 inhibitors had already been explored in the past [Aliment
Pharmacol Ther 2005;23:121-8; Liver Int 2004;24:63-8; Eur J Pharmacol
2007;572:49-56]. Accordingly, the current study lacks of originality.
2 Regarding methodology
-How were the doses of sildenafil and vardenafil chosen?
-How can authors measure the portal venous pressure (by cannulation of portal
vein) and portal venous blood flow (by ultrasound flow probes) at the same time?
In general, the cannulation of portal vein may interfere with the measurement of
blood flow with ultrasound flow probes at the same location.
Minor points
-The formula to calculate fractional liver flow (portal venous + hepatic arterial
blood flow/cardiac output = proportion of cardiac output passing through the liver)
should move to “Method”.
-The sentence “These data support the interpretation that PDE-5 inhibitors at low
concentration have distinct effects on the hemodynamics of the liver” is not clear.
-Most of the description in discussion is focusing on the role of PDE-5 inhibitor in
cirrhosis and portal hypertension. Nonetheless, the current study was only
performed in normal rats.
-Duplicated references: reference 34 & reference 50 are the same paper
Level of interest: An article of limited interest
Quality of written English: Needs some language corrections before being
published
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests.
Review for 10.1186/1471-230X-9-69 (2009)

Reviewer's report
Title:Phosphodiesterase-5 inhibitors have distinct effects on the hemodynamics
of the liver
Version: 3Date:29 July 2009
Reviewer: Toshishige Shibamoto
Reviewer's report:
No comments. This paper becomes accepted for purblication.
Level of interest: An article of importance in its field
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Review for 10.1186/1471-230X-9-69 (2009)

Reviewer's report
Title:Phosphodiesterase-5 inhibitors have distinct effects on the hemodynamics
of the liver
Version: 3Date:7 August 2009
Reviewer: Han-Chieh Lin
Reviewer's report:
Although the authors have made certain revision of this manuscript, the value of
this study is greatly hampered by the lack of cirrhotic group. It is well known that
vasoactive agents may provide different effects between those with and without
cirrhosis. For example; compared to normal rats, the activity of eNOS was
decreased and the bioavailability of NO was impaired in cirrhotic liver. Extensive
discussion of the hemodynamic effects of PDE-5 inhibitors in normal animals
does not provide much novel information regarding the potential therapeutic
effect and pathophysiological aspects in cirrhosis.
Level of interest: An article of limited interest
Quality of written English: Acceptable
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Declaration of competing interests:
I declare that I have no competing interests