JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-9-50 (2009)

Reviewer's report
Title:The galactose elimination capacity and mortality in 781 Danish patients
with newly-diagnosed liver cirrhosis: a cohort study
Version: 1Date:22 December 2008
Reviewer: Carlo Merkel
Reviewer's report:
The Authors assessed mortality in a large series of patients with a first diagnosis
of cirrhosis, in whom GEC was measured at the time of diagnosis. They
observed that short and long term mortality was related to GEC, particularly in
the low values.
The main strenght of this manuscript is the fact that this report is based on the
largest database of GEC in cirrhosis ever compiled. Amongf the weak points, I
would consider particularly the fact that the study is a retrospective analysis of of
data collected for different reasons, and therefore crtieria of inclusion are not
clearly established.
I would suggest the following comments for a possible improvement:
Major compulsory revisions:
1) Data should be reported with their confidence intervals
2) Survival in the various deciles of GEC should be reported as Kaplan-Meier
curves, since most readers are familiar with this way of reporting survival course
of patients.
Minor essential revisions:
1) Since the time of beginning of cirrhosis is difficult to define, as compensated
disease may last for 10 years, the principle of an inception cohort of patients
enrolled at the beginning of disease is hard to demonstrate. As the only definite
point in the natural history of cirrhosis is the time of the first decompensation, I
would suggest to make a further analysis considering as beginning of follow-up
the first decompensation (and GEC at the time of first decompensation).
2) I suggest to discuss in detail if it is reasonable to hypothesize that marginally
decreased values of GEC may be of value in predicting long-term outcome of a
compensated disease, of which the date of beginning is unknown, and the
remaining span of time in compensated disease ought to be predicted by this
test. At a first look at the results, it appears that when GEC is normal or
nearly-normal, 5-yr survival is the same for any value of GEC. This reinforce my
suggestion of assessing outcome from the first decompensation.
Discretionary revisions:
1) I would try to express clearly the concept that the relationship between liver
function and survival is more than a hypothesis, and that the real problems lay in
the way of evaluating derangement in liver function, and in the time-course of the
decrease in liver function, that may not be linear.
2) I would also discuss the fact that available literature is not concordant on the
additive value of GEC to the prognostic assessment obtained by conventional
liver function tests.
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-9-50 (2009)

Reviewer's report
Title:The galactose elimination capacity and mortality in 781 Danish patients
with newly-diagnosed liver cirrhosis: a cohort study
Version: 1Date:22 December 2008
Reviewer: Giulio Marchesini
Reviewer's report:
Jepsen et al report a large experience on GEC as predictive of short- and
long-term survival in newly-diagnosed cirrhosis. In their experience based on 781
cases having GEC determination within 90 days from diagnosis, GEC was
significantly associated with mortality, and the association does not change much
after correction for age and comorbidities.
There are however a few issues that should be discussed in more details.
Major compulsory revisions
1. The manuscript is extremely concise and lacks any statistical analysis. From
the figure the reader has the impression that there is a continuum between GEC
and survival, after lowess smoothing, but it is also evident that survival is
scarcely affected by GEC in the range above 1.5-1.75 mmol/L, if not at all. The
confidence interval of the regression line is not plotted, and I can hardly guess
that the line deviates from a horizontal line. This is clinically sound, and should
be tested by proper statistical methods.
2. Apparently, only all-cause mortality was considered. This is very robust
outcome, but GEC might be more predictive of liver-related mortality. Were this
piece of information available, it should be presented in the manuscript.
3. Charlson’s index provides a quantitative estimate of comorbidities, by
summing up the scores of diseases in different organs, having different scores. It
is not clear in the manuscript if the presence/absence of comorbidities was
considered (this is my impression), or data were adjusted for the final score. This
may make a large difference in the final outcome.
Minor essential revisions
1. Apparently, only all-cause mortality was considered. This is very robust
outcome, but GEC might be more predictive of liver-related mortality. Were this
piece of information available, it should be presented in the manuscript.
Discretionary revisions
1. The physiologic meaning and the clinical robustness of GEC are out of
discussion. Its limited use is not related to technical difficulties, but to the lack of
evidence of a clear-cut superiority when compared to standard liver tests. This
may be due to uncertainty in the measurement (Confidence Interval of the
regression line), as well as to the confounding effects of complications. From a
clinical point of view, we need to know whether GEC behaves significantly better
than routine tests (albumin, prothrombin) in clinical prediction. It is a pity that this
information is not presented in the manuscript. This limits the clinical significance
of the study, and should be tested or discussed.
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-9-50 (2009)

Reviewer's report
Title:The galactose elimination capacity and mortality in 781 Danish patients
with newly-diagnosed liver cirrhosis: a cohort study
Version: 2Date:27 March 2009
Reviewer: Teh-Ia Huo
Reviewer's report:
This paper has been improved a lot after revision.
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-9-50 (2009)

Reviewer's report
Title:The galactose elimination capacity and mortality in 781 Danish patients
with newly-diagnosed liver cirrhosis: a cohort study
Version: 2Date:31 March 2009
Reviewer: Carlo Merkel
Reviewer's report:
The manuscript is definitely improved.
The Authors corrected the text according to the suggestion as far as possible
(considering the kind of data that were available). The questions were answered
sufficiently in-depth. Discussion is now acceptable.
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-9-49 (2009)

Reviewer's report
Title:Increasing prevalence and high Incidence of celiac disease in elderly
people: A population-based study
Version: 1Date:23 February 2009
Reviewer: Detlef Schuppan
Reviewer's report:
Vilppula et al. studied prevalence and incidence of celiac disease in the elderly
by sequential serum screening for celiac disease antibodies. They found that the
prevalence of celiac disease in elderly people is high but the symptoms are only
minor. Furthermore, they show 5 cases that developed celiac disease within
three years after being seronegative in the first screening. Since little is known
about the development of celiac disease in elderly people these results are
interesting.
However, the major point of critique is that the first and major part of the study
was already published elsewhere (Vilppula et al; Dig Liver Dis.; 2008). Therefore
the only novel aspects the authors are presenting is the 5 newly detected cases
of celiac disease on follow up.
Minor points:
1. The study population is not well defined. The authors included all people over
55 years in their statistical analysis. It would make more sense to distinguish
groups between 55 and 65 years and over 65 years, and to calculate prevalence
and incidence separately for these groups.
2. The authors should state the number of biopsies that were taken per patient
and the histopathological appearance (MARSH criteria) of the diagnosed
patients. What does it mean when patients were only classified as celiacs based
on marginally elevated autoantibodies and a Marsh I histology?
3. Thus they should present the titers of the seropositive patients together with
the cut offs they used for diagnosis. Could the 5 newly detected celiacs be due to
some variability within the used anti-tTG assay which though showing excellent
reliability is not perfect?
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:
no conflicts of interest
Review for 10.1186/1471-230X-9-49 (2009)

Reviewer's report
Title:Increasing prevalence and high Incidence of celiac disease in elderly
people: A population-based study
Version: 1Date:2 March 2009
Reviewer: joseph murray
Reviewer's report:
This is a very important observation of the new development celiac disease in
older patients. it is of scientific and practical clinical importance.
Whilst there were new 5 elderly individuals identified with probable new onset
celiac disease, this is a small number whilst this is statistically significant in terms
of a change over prior. Could this change be due to variability in the testing
between the two time periods? This could be addressed by examining and
reporting the absolute values and arbitrary assay units between the two time
points. For example, were the earlier samples close to the threshold considered
abnormal for tissue transglutaminase antibody ? Repeating testing on both the
first and the subsequent sample at the same time for both tests to make sure this
truly was not simply variation around a threshold. The second issue is whether
there were any confounders occurring on the first time, such as the use of
steroids, be it topical or other immune modifiers.
2. Another second issue relates to the very high incidence of celiac disease in
this unique population. Is the population of Lahti particularly inbred or isolated? Is
there an especially high prevalence of homozygocity for DQ2, for example?
3. How would these results from this very isolated population relate to other
populations? Have the authors taken into account the possibilities that the
patients may have originally been seronegative celiac disease who then became
seropositive, but had celiac disease all along? Demonstration of the actual
histology would be convincing to this reviewer. Also, it would be worthwhile to
know what the prevalence of seronegative celiac disease or pre-celiac disease
could be in these individuals.
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-9-49 (2009)

Reviewer's report
Title:Increasing prevalence and high incidence of celiac disease in elderly
people: A population-based study
Version: 2Date:24 April 2009
Reviewer: joseph murray
Reviewer's report:
well done no need for firther changes
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-9-49 (2009)

Reviewer's report
Title:Increasing prevalence and high incidence of celiac disease in elderly
people: A population-based study
Version: 2Date:4 May 2009
Reviewer: Detlef Schuppan
Reviewer's report:
The authors partially responded to the issues that were raised in the first review.
However, our main point of critique (lack of novelty) remains.
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
Review for 10.1186/1471-230X-9-48 (2009)

Reviewer's report
Title:Assessment of safety and feasibility of a new technical variant of
gastropexy for percutaneous endoscopic gastrostomy: an experience with 453
cases
Version: 1Date:19 February 2009
Reviewer: Hugo Heij
Reviewer's report:
* Major compulsory revisions.
A (historical) control group is necessary to assess the value of this method in
comparison with either the pull-method or the Direct PEG method as described
by Shastri (ref 12) and by Hikki et al (J Am Coll Surg 2008; 207: 737-44). The
reasons to ask for a control group are a) to demonstrate the safety and feasibility,
as claimed by the authors, whereas several serious complications have occurred
with one death; b) the procedure described in the present manuscript appears to
require surgical skills, whereas the pull method can be performed by
non-surgeons.
* Minor essential revisions
- No abstract attached
- Can the authors inform the reader who performed these procedures?
Gastroenterologists or surgeons?
- What was the mean survival after PEG insertion, in relation to the risk of tumor
cell migration. In other words, how relevant is this risk in this patient category
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-9-48 (2009)

Reviewer's report
Title:Assessment of safety and feasibility of a new technical variant of
gastropexy for percutaneous endoscopic gastrostomy: an experience with 453
cases
Version: 1Date:27 February 2009
Reviewer: Arno J Dormann
Reviewer's report:
Dear Editor,
this article is a well written paper about PEG procedure with gastropexy.
The technical approach is well described and new.
The technical success rate is high and complication rate is low.
Local infection are on the same level and lower as described before.
I agree that by using introducer technique in all patients an anbiotic prophylaxis
might be not mandatory.
The authors should discuss the economic effect of this new approach because
the new systems are normally much more expensive than introducer PEG
systems (Germany 4 times more).
The only disadantage of all introducer systems is that they are not good in
patients with high BMI.
For the future the authors should discuss the option of a peal-off sheath instead
of their trocar system which does not seem to be very comfortable and easy to
use. Then the need of the dissection with scissors might be avoided.
They should fill in the total procedure time into the table and the way of intubation
during endoscopy.
They should state if their system could be used in patients which can not be
evaluated by endoscopy.
Level of interest: An article of outstanding merit and interest 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-9-48 (2009)

Reviewer's report
Title:Assessment of safety and feasibility of a new technical variant of
gastropexy for percutaneous endoscopic gastrostomy: an experience with 453
cases
Version: 2Date:11 May 2009
Reviewer: Hugo Heij
Reviewer's report:
I think the authors have addressed the comments well and have modified the text
of the manuscipt accordingly. Therefore, I see no objection to acceptance of the
manuscript for publication.
Review for 10.1186/1471-230X-9-47 (2009)

Reviewer's report
Title:Trends in esophageal cancer and body mass index by race and gender in
the state of Michigan
Version: 1Date:16 February 2009
Reviewer: Thomas Vaughan
Reviewer's report:
This is a well-written report examining the incidence of esophageal cancer in
Michigan State over time and in relation to BMI trends in the state.
Minor essential revisions:
1. (Background, 2nd para, 3rd sentence). The authors imply that the action of
BMI is through reflux. However this ignores recent data (e.g., Whiteman DC,
GUT, 2008;57) that strongly suggests that obesity and GERD may act
synergistically. This section should be revised to reflect conflicting information on
this topic. This also pertains to the 3rd paragraph of discussion, which does not
take into account recent case-control studies of esophageal adenocarcinoma and
Barrett’s.
2. (Background, 2nd para, 4th sentence). Three references (10-12) are given and
described as case-control studies, whereas all are cohort studies. Additional
recent case-controls studies would be good to add as well (e.g., Whiteman,
above).
3. (Background, 2nd para, last sentence). The fact that previous case-control
studies may have matched on race does not preclude the examination of
race-specific estimation of BMI associations. This should be corrected.
4. Regarding the analysis of incidence trends, it would be helpful to provide
estimates of annual % change in incidence to facilitate comparisons with other
studies. Also, a bit more detail on the analysis of change in slope would be of
interest. For example, how was 1999 chosen as a cutpoint?
5. The discussion should also include results from Jeon et al (Cancer Causes
Control; 2006;17) who conduct SEER-wide analyses of incidence along with a
brief look at obesity trends and their potential role.
Discretionary revisions:
6. (Discussion, 1st para, 3rd sentence). It is a bit odd to refer to Barrett’s as a risk
factor for esophageal adenocarcinoma, implying etiology. A precursor is perhaps
a better term.
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
Review for 10.1186/1471-230X-9-47 (2009)

Reviewer's report
Title:Trends in esophageal cancer and body mass index by race and gender in
the state of Michigan
Version: 1Date:2 April 2009
Reviewer: wyn lewis
Reviewer's report:
This is a well written paper on a topical and important area of both medicine and
surgery which deserves to be published.
I have only a few minor comments:
1.Abstract - adenocarcinomas should read adenocarcinoma. Quoting values for
the avergae BMIs would help with clarity regarding the overall message.
2.Methods and Results. Definitions of low, normal and high BMIs differ between
the WHO and other dietary societies. The defintion used for this study should be
included and whether or not it differed for males and females. Median (range)
values for the BMIs considered should be quoted.
3.There are arguably too many figures and the female incidence rate figures
could be ommitted without compromising on the message.
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-9-44 (2009)

Reviewer's report
Title:Gluten sensitivity enteropathy and recurrent aphthous stomatitis
Version: 3Date:22 November 2008
Reviewer: Luca Pastore
Reviewer's report:
Major Compulsory Revisions
1. page 4, lines 15-17 "Aphthae can be a presentation of [...] celiac disease. In
fact in 5% of CD patients, RAS can be the only presentation of disease"; page 8,
line 3-4 "it is clearly understood that RAS is at least among the fifth commonest
presentations of CD": the aim of the study is to verify the hypothesis of an
association between CD and RAS; authors should avoid affirming this hypothesis
making reference to other studies. Authors should assert: "Aphthae has been
reported as a presentation of [...] celiac disease"; "RAS has been reported as
one of the fifth commonest presentations of CD".
2. page 5, line 17: please specify what were the conventional drugs.
3. page 9, line 4: "was statistically higher"; no statistical comparation has been
performed.
Minor essential revisions
1. page 5, line 3: "aphthous" should be "aphthae";
2. page 5, line 4: "Riter" should be "Reiter";
3. page 5, line 9: "explained" should be "were explained";
4. page 7, line 9: "EMA and tTG test" should be "EMA and tTG tests";
5. page 7, line 10: "were underwent" should be "underwent".
Level of interest: An article of importance in its field
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-9-44 (2009)

Reviewer's report
Title:Gluten sensitivity enteropathy and recurrent aphthous stomatitis
Version: 3Date:26 November 2008
Reviewer: Julio C Bai
Reviewer's report:
The manuscript by Ramin Shakeri et al antitled: “Gluten sensitivity enteropathy
and recurrent aphthous stomatitis” is a very interesting piece of epidemiological
research evidencing an almost three folds greater prevalence of CD among
patients with oral aphthoid ulcerations than in the general population. The study
also confirms that the CD specific treatment solves the RAS problem.
The question of the authors is adequate and the methods employed are the
currently used. Results should be considered with the limitations reported below
The authors define cases as gluten sensitive enteropathy in place of CD mainly
due to the high prevalence of minor mucosal damage. Definition of enteropathy
according to Marsh´s criteria should be more explicit considering the prevalence
of minor changes among cases identified.
It is interesting consider that patients with minor mucosal damage may have a
lower prevalence of positive serology tests; therefore, the authors should be
more cautious in estimating the prevalence of GSE since that other RAS cases
could have similar changes but not detected by the serologic/histologic algorithm
employed.
The results section looks very short.
Level of interest: An article of importance in its field
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:
No competing interests
Review for 10.1186/1471-230X-9-44 (2009)

Reviewer's report
Title:Gluten sensitivity enteropathy and recurrent aphthous stomatitis
Version: 6Date:4 March 2009
Reviewer: Julio C Bai
Reviewer's report:
The manuscript has been improved including most of the changes suggested by
the reviwers. In my opinion, the response from the authors to my main concern
(the possibility of a higher prevalence of a seronegative gluten sensitive
enteropathy) seems to be pertinent. However, this does not exclude the fact that
seronegative enteropathy are also gluten sensitive. In such event, response
(clinical and histological) to the GFD sould be confirmatory. What´s about clinical
improvement with GFD despite no serological or histological evidences of glten
sensitivity. Please, remember that 1/3 of patients with DH neither histological
damage nor positive serology tests. The authors should postulate potential
factors explaining discrepancies in prevalence among studies. Therefore, I
believe the manuscript could be viable just adding comments about this topics in
the discussion section.
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 have no competing interest
Review for 10.1186/1471-230X-9-44 (2009)

Reviewer's report
Title:Gluten sensitivity enteropathy and recurrent aphthous stomatitis
Version: 6Date:12 March 2009
Reviewer: Luca Pastore
Reviewer's report:
Major Compulsory Revisions
- Authors assert that “GSE should be considered in RAS patients who are
refractory to conventional anti-aphthae treatment” since all the 7 patients with
GSE they observed had refractory RAS; to draw such a conclusion authors
should compare the prevalence of refractory and non-refractory RAS in patients
with and without GSE. Authors could draw the following conclusion: “GSE should
be considered in RAS patients; unresponsiveness to conventional anti-aphthae
treatment could be an additional risk indicator”.
- “All the GSE patients were unresponsive to previous trials of conventional
anti-aphthae drugs (e.g. tetracycline, diphenhydramine, and colchicine)”;
consider that the mainstay of therapy for mild RAS is topical corticosteroids.
Minor Essential Revisions
- Page 2: “in those who diagnosed” should be “in those who were diagnosed”.
- Page 4: “diagnosed because of new serological screening methods” should be
“diagnosed by screening with serological tests”.
- Page 5: “An inclusion criterion was suffering from oral aphthae at least three
times per year, and exclusion criteria were…” could be “Patients included in the
study had had at least three episodes of oral aphthae during the year; exclusion
criteria were…”.
- Page 8: “None of them complained from other symptoms of CD including
infertility, gastrointestinal or dermatologic problems” could be “None of them
complained from other typical or atypical signs and symptoms of CD”.
- Page 8: “GSE patients adhered to strict gluten free diet” should be “GSE
patients started a strict gluten free diet”.
- Page 8: “was decreased to” should be “decreased to”.
- Page 9: “a 2.83% prevalence of GSE was observed. This could be compared
with the prevalence of 0.9% of GSE in the general population” could be “a 2.83%
prevalence of GSE was observed, as compared with an estimated prevalence of
0.9% in the general population”.
- Page 10: “Prevalence of GSE was estimated 2.83% which was about 3-fold
higher than its prevalence in general population” could be “Prevalence of GSE in
patients with RAS was 2.83% , which is about 3-fold higher than that expected in
general population”.
- Page 10: “Four of our patients accepted to consider GFD” could be “Four
patients accepted to start GFD”.
Level of interest: An article of importance in its field
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-9-44 (2009)

Reviewer's report
Title:Gluten sensitivity enteropathy and recurrent aphthous stomatitis
Version: 8Date:18 May 2009
Reviewer: Luca Pastore
Reviewer's report:
The manuscript has been revised according to the suggestions
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-9-45 (2009)

Reviewer's report
Title:Endoscopic treatment of malignant gastric outlet obstruction with stents: A
systematic evaluation of the reported variables for clinical outcome
Version: 2Date:23 January 2009
Reviewer: Iruru Maetani
Reviewer's report:
Minor Essential Revisions
1. In the Methods section, the authors mention that the third evaluation
parameter of this study is “information on stent patency and survival”. However,
in the Results section, although explanation of stent patency and migration is
provided, there is no mention of its survival.
2. In the Methods section, the authors say, “When studies included identical
patients, the most recent study was included.” Although Ref#26 (2001-2004) and
Ref#41 (2001-2005) presumably included identical patients, both articles were
included as prospective studies. This needs to be confirmed.
3. Did your study include stent placement for esophagojejunostomy after total
gastrectomy (i.e. Ref#40)? If so, you should exclude these references from this
study, since stricture of esophagojejunostomy is not gastric outlet obstruction.
4. In the Results section, the authors mention that the numbers of prospective
studies are 10 with endoscopic/fluoroscopic method and 11 with fluoroscopic
method, totaling 21. According to Table 2, however, the number of prospective
study is 20. Please confirm the number of references.
5. The title of this paper is “endoscopic treatment….” However, this paper
includes some studies by radiologists making no use of endoscopy, and so the
title should be revised.
Discretionary Revisions
1. It seems favorable to display brief listing of all studies included in this study.
2. In the end of Discussion, the authors mention, “and it is ………….in all
subjects treated.” This was confirmed in a previous investigation (Maetani I, et al.
Hepato-Gastroenterology 2008;55:298-302). It is preferable to quote the
reference for this sentence.
Level of interest: An article of outstanding merit and interest 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-9-45 (2009)

Reviewer's report
Title:Endoscopic treatment of malignant gastric outlet obstruction with stents: A
systematic evaluation of the reported variables for clinical outcome
Version: 2Date:26 January 2009
Reviewer: Greger Lindberg
Reviewer's report:
The authors have reviewed some of the literature on stenting of gastric outlet
obstruction. The specific aim of their study was to find out if sufficient data were
given on clinical effects of stenting and whether or not quality of life had been
assessed. The review is well designed and the conclusions are probably valid.
However, there are a few points that need some explanation to render this
manuscript understandable to the reader.
Major Compulsory Revisions
1. The authors chose to include only studies with 15 or more subjects. What was
the rationale for this choice? Please specify why 15 and not 10 or 5 or any other
number of subjects was chosen as numerical limit for inclusion. For example, the
choice of 15 excluded the only RCT on this subject.
Minor Essential Revisions
2. It is possible that the majority of readers are familiar with the Karnofsky
performance scale, which measures physical impairment and not health related
quality of life, but I think this should be explained to the reader. It is perhaps not
necessary to cite the original paper, but at least the nature of this scale should be
mentioned.
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-9-45 (2009)

Reviewer's report
Title:Endoscopic treatment of malignant gastric outlet obstruction with stents: A
systematic evaluation of the reported variables for clinical outcome
Version: 2Date:28 January 2009
Reviewer: Todd Baron
Reviewer's report:
Minor essential revision. The authors state "there no Objective evaluation of
gastric/duodenal function after stenting is limited and no studies have performed
quantitative tests of gastric emptying". this is not true. there is one study: Maetani
I, Ukita T, Tada T, Ikeda M, Seike M, Terada H, Kohda E. Gastric emptying in
patients with palliative stenting for malignant gastric outlet obstruction.
Hepatogastroenterology. 2008 Jan-Feb;55(81):298-302. This needs to be
included in the paper even though it may not meet the criteria for 15 patients.
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-9-45 (2009)

Reviewer's report
Title:Treatment of malignant gastric outlet obstruction with stents: A systematic
evaluation of the reported variables for clinical outcome
Version: 4Date:21 April 2009
Reviewer: Greger Lindberg
Reviewer's report:
I have no further questions or comments regarding this manuscript.
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-9-46 (2009)

Reviewer's report
Title:Lipoprotein lipase activity and mass, apolipoprotein C-II mass and
polymorphisms of apolipoproteins E and A5 in subjects with prior acute
hypertriglyceridaemic pancreatitis
Version: 1Date:26 March 2009
Reviewer: John Brunzell
Reviewer's report:
Major:
1. The authors addressed whether biochemical or clinical differences could be
noted in severely hypertriglyceridemic patients who had and did not have
pancreatitis. Other than finding 5 patients with LPL deficiency, there were few
differences. A bordrline increase in apoA5 snp was noted in HTG with
pancreatitis. The first paragraph is not clear about this.
2. Results: Estimates of positive family history are probably underestimates
unless relatives were actually studied. This should be noted.
3. The measures of chylomicron lipids are estimates at best. This technique is
not able to distinguish between smaller chylomicrons and larger VLDL. Did they
measure apoB48 and apoB100? NMR has not been shown to differentiate
between these particles either. They should call their chylomicrons "estimated".
Minor:
1. Page 3, line 2: "1.3-3.5%" of what?
2. Page 4, line 6: Delete word "promising". This is still experimental.
3. Page 4, para 3: Change lipidaemic to lipaemic.
4. Page 6, para 3: Split last sentence with period after word "plasma". Start
second part of sentence with "One mU".
5. Results: Were fibrates started after the bouts of pancreatitis? This might lead
to further underestimation of triglyceride levels.
6. Put BMI into table, perhaps in place of weight.
7. Page 10, end of para 2: add "or by measuring postheparin plasma LPL
activity"
8. Page 11, delete last sentence in para 1. See major comment #3 above.
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-9-46 (2009)

Reviewer's report
Title:Lipoprotein lipase activity and mass, apolipoprotein C-II mass and
polymorphisms of apolipoproteins E and A5 in subjects with prior acute
hypertriglyceridaemic pancreatitis
Version: 2Date:5 June 2009
Reviewer: Emilio Ros
Reviewer's report:
Minor essential revisions:
The manuscript needs some language corrections,
Page 5. Because few relatives were available for lipid analyses, family history of
hyperlipidemia relied mainly in (should be “on”) patient’s recall.
Page 6. Where it says “Because our technique is not able to distinguish between
smaller chylomicrons and larger VLDL we call it chylomicron-like particles.” would
read better: “Because this technique cannot distinguish between smaller
chylomicrons and larger VLDL, the lipoprotein fraction obtained is named
chylomicron-like particles.”
From here on, chylomicrons should be named chylomicron-like particles
throughout the manuscript.
Page 8. “A positive family history for (should be “of”) hyperlipidaemia”
Page 10. Our patients with hypertriglyceridaemic pancreatitis due to LPL
deficiency were clinically different from “the others”... Substitute “others” for
“those with preserved LPL mass and activity…”
There are other parts in the additions in red or in the initial wording of the
manuscript where English can be improved (i.e., page 10, suggest using “onset”
instead of “debut”; page 11, inflammatory is misspelled as inflamatory).
Level of interest: An article of importance in its field
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 have no competing interests to declare.
Review for 10.1186/1471-230X-9-43 (2009)

Reviewer's report
Title:The clinicopathological observation, c-kit gene mutation and clonal status
of gastrointestinal stromal tumor in sacrum
Version: 2Date:5 January 2009
Reviewer: Tadashi Terada
Reviewer's report:
The manuscript of LiGong et a. is interesting, and merit publication after minor
revisionb in your journal.
However, some concerns exist as follows.
1. GIST may be converted into EGIST (extragastroentestinal stromal tumor)
2. The sources of antibodies should be written.
3. The relationship of testis should be written, because testicular germ cell
tumors frequently show KIT gene mutation.
Review for 10.1186/1471-230X-9-43 (2009)

Reviewer's report
Title:The clinicopathological observation, c-kit gene mutation and clonal status
of gastrointestinal stromal tumor in sacrum
Version: 4Date:31 March 2009
Reviewer: Giuliano Ramadori
Reviewer's report:
Comments to the Authors
The initial manuscript has been carefully revised, and it is now interesting to read
the details. We therefore consider the manuscript worth for publication.
We would however like to suggest the following corrections.
General comments:
The changes are marked in red.
The figures still have the wrong numbers on the images:
Figure 1 = Figure 1A
Figure 2 = Figure 1B
Figure 3 = Figure 1C
Figure 4 = Figure 2A
Figure 5 = Figure 2B
Figure 6 = Figure 3A
Figure 7 = Figure 3B
Figure 8 = Figure 4
Figure 9 = Figure 5
Figure 10 = Figure 6
The figures are correctly numbered within the text and in the figure legends.
“c-KIT” should be written in capital letters (instead of “c-kit”), whenever it is the
name of the gene itself, such as
Page 1, line 9;
Page 1, line 21;
Page 3, line 11;
Page 3, line 14;
Table 1.
In the other places it has been done correctly.
Abstract
Page 1, line 1f: “…occurs in the sacrum.”, instead of “…in sacrum.”
Page 1, line 20: “…found in the sacrum.”, instead of “…in sacrum.”
Background
Page 3, line 4: “…non-lymphatic,…”, instead of “non-lympha”
Page 3, line 12: “We suggest that GIST should be…”, instead of “First of all,…”
Methods
Page 4, line 14: “…, and to exclude melanoma HMB45”, please specify as this is
an antibody not known to every reader.
Page 5, line 12: “…was carried out…”, instead of “carried”.
Page 7, line 4: “…was the same as for the first round,…”, instead of “as the first
round”.
Page 7, line 11: “4#l”, instead of “ul”.
Results, instead of “Result”.
Page 9, line 1: “The resected irregular tissue was…”, instead of “tissues was”
Page 9, line 10: “SM-actin”, instead of “SC-actin”.
Page 9, line 19: “…was found at position 100”, instead of “at the location of 100”.
Page 10, line 8: “The results indicate that GIST is a clonal neoplastic lesion.”,
instead of “…indicated that GIST was a neoplastic hyperplasia”.
Discussion
Page 11, line 10f: “The diagnosis of GISTs mostly relies on histopathological
features and the immunohistochemical phenotype,…”, instead of “rely” and
“immunohistochemical…”.
Page 11, line 12: ”…feature is”, instead of “was”.
Page 11, line 13f: Please change to“…90-95% of GISTs express CD117, 60-70%
express CD34, 30-40% SM-actin and only 5% are positive for S-100 protein.”
Page 11, line 14: “Please delete: “Expression of vimentin was always positive.”
Page 11, line 19: “…and showed”, instead of “besides”.
Page 13, line 18: “…were similar”, please delete “coincided”.
Figure legends
Figure 2 and Figure 3: Please give the original magnification, such as “Original
magnification 200x”.
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 do have no competing interests.
Review for 10.1186/1471-230X-9-43 (2009)

Reviewer's report
Title:The clinicopathological observation, c-kit gene mutation and clonal status
of gastrointestinal stromal tumor in sacrum
Version: 4Date:3 April 2009
Reviewer: Tadashi Terada
Reviewer's report:
I carefully read the below manuscript, and think that the paper is now acceptable
in your journal.
Review for 10.1186/1471-230X-9-42 (2009)

Reviewer's report
Title:Intra-abdominal pressure alterations after large pancreatic pseudocyst
transcutaneous drainage
Version: 1Date:24 November 2008
Reviewer: William Brugge
Reviewer's report:
This is a 9 month prospective, single institution study of 27 patients with a
pancreatic pseudocyst. The authors sought to determine the effect of pseudocyst
drainage on the intra-abdominal pressure (as measured with a urinary bladder
catheter). The patients were divided into two groups: A (CT guided pseudocyst
drainage) and B (no drainage). The authors found that pseudocyst drainage was
associated with a decrease, but transient, in intra-abdominal pressure.
Comments to the authors
1. The authors should comment on the location of the pseudocysts and whether
the retroperitoneal location will effect intra-abdominal pressure
2. It would have been interesting to know the rate of reaccumulation of the
pseudocyst after drainage. Perhaps the rise in the IAP after drainage was a
result of reaccmulation of pseudocyst fluid.
3. How were the patients assigned to the groups?
4. The clinical significance in the elevated IAP is not clear
5. Please provide the characteristics of the pseudocyst fluid (protein
concentration, WBC count, amylase, and CEA)
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:
Consultant, Boston Scientific
Review for 10.1186/1471-230X-9-42 (2009)

Reviewer's report
Title:Intra-abdominal pressure alterations after large pancreatic pseudocyst
transcutaneous drainage
Version: 2Date:19 January 2009
Reviewer: Manu Malbrain
Reviewer's report:
I read with interest the revised paper by Theodossis et al. entitled “IAP alterations
after large pancreatic pseudocyst transcutaneous drainage”. The article is short
and to the point on a clinically relevant topic and what some even call a “sexy
subject”. We thank the authors for their point by point answers to all the
reviewers comments. The article has been substantially improved in its present
form and we only have minor comments.
I believe that The English still can be improved here and there.
Please state results with 1 digit after the comma so IAP was 5.1 instead of 5.07,
etc…
Give SD for each result
In abstract how can PRE-drainage IAP be higher in group A than group B (since
in group B no drainage was performed – this is a bit confusing???) – please
rephrase by stating that baseline IAP was higher in group A vs group B
Please state the pseudocyst volume also for group B
Omit Table 1 since it represents the same information as figure 1
I would add a Table with the patient demographics of group A and B: age;
gender, BMI, volume of pseudocyst, baseline IAP, hos stay,.. with p-value when
appropriate,
Please add in methods how Cabd was calculated and not in results: please
rephrase formula Cabd = volume of fluid drained/ (pre drainage IAP – post
drainage IAP)
How many patients had IAP > 12mmHg (or thus IAH)
I would suspect that these patients had a lower Cabd and thus a higher drop in
IAP for the same amount drained – can you provide some results on this and
please discuss this issue – even if you did not found any difference.
Also was Cabd lower in patients with high BMI?
In conclusion: this is a very interesting small study, congratulations. Please take
into account the comments above.
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:
No competing interest
Review for 10.1186/1471-230X-9-40 (2009)

Reviewer's report
Title:Afferent signalling from the acid-challenged rat stomach is inhibited and
gastric acid elimination is enhanced by lafutidine
Version: 1Date:16 March 2009
Reviewer: Koji Takeuchi
Reviewer's report:
The authors confirmed that the acid (0.25 M) challenge increased the expression
of c-Fos in the NTS with a minimal damage in the gastric mucosa. Lafutidine, a
histamine H2 antagonist with mucosal protective action mediated by
capsaicin-sensitive afferent neurons, reduced the acid-evoked c-Fos expression
in the NTS and elevated the luminal pH following the acid challenge. In addition,
the gastroprotective effect of lafutidine was found to be in parallel with facilitation
of gastric emptying and reduction of luminal acidity, and the effects of this drug
were only in part shared by cimetidine. They concluded that lafutidine inhibits
gastric acid-evoked vagal nociceptive signalling and that this drug protects the
gastric mucosa from acid injury independently of its ability to suppress acid
secretion due to H2 receptor blockade. The present study was well designed and
performed, and the data well supported the conclusion. However, there are
several points that should be addressed before consideration of its publication.
Major Compulsory Revisions
1. Lafutidine is known to exhibit gastroprotection mediated by capsaicin-sensitive
afferent neurons. The present study showed that lafutidine inhibited the
acid-evoked c- Fos expression in the NTS. This reviewer wonders if the
acid-evoked c-Fos expression is affected by capsaicin or ablation of
capsaicin-sensitive afferent neurons? Some comments on this point, including a
relation to the sensory neuronal activating property of lafutidine, should be made
in the text.
2. In this study, the effect of cimetidine was examined at 10 mg/kg, in comparison
with lafutidine at 30 mg/kg. The authors should give a rationale to use this dose
of cimetidine, ie., do the authors have some evidence showing that the potency
of the antisecretory action of cimetidine at 10 mg/kg is equivalent to that of
lafutidine at 30 mg/kg?
3. The authors speculated that endogenous acid plays some role in the
mechanism of the central c-Fos response to back-diffusion H+. Since lafutidine
inhibits endogenous acid secretion due to histamine H2 receptor blockade, this
action may somehow contributes to suppression of the c-Fos expression
following the acid challenge. This reviewer wonders if lafutidine inhibits the
acid-evoked c-Fos expression in the animals pretreated with omeprazole to
completely inhibit endogenous acid secretion. Does lafutidine suppress the c-Fos
response to exogenous acid challenge in the absence of endogenous acid
secretion? If it does, this action of lafutidine could be mimicked by cimetidine or
omeprazole? Such data would be helpful for further understanding of the
regulatory mechanism of c-Fos response to acid challenge.
Minor Essential Revisions
4. page 2, line 5 from the bottom and page 12, Discussion, line 3-4: The ability of
lafutidine to elevate intragastric acidity – this should be read “—to elevate
intragastric pH or to decrease intragatric acidity”