JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/1471-230X-9-84 (2009)

Reviewer's report
Title:Effects of esomeprazole treatment for gastroesophageal reflux disease on
quality of life in 12- to 17-year-old adolescents: an international health outcomes
study
Version: 1Date:30 June 2009
Reviewer: Marco Scarpa
Reviewer's report:
This is a well organized prospective assessment of the effect of esomeprazole on
quality of life of adolescent affected by GERD. The question posed by the author
is well defined and the methods are generally quite appropriate even if there are
some critcial points. The data arte sound and the manuscript adere to the
general stadard for reporting. The discussion and the conclusion are well
balanced and the limitation of the work is clearly stated as well the references.
The abstract and the title convey accurately what has been found and tye writing
is acceptable.
However there are some Major Compulsory Revisions that I feel necessary:
Was the QOLRAD questionnaire tested for comprehension in young adolescents
(12-13 years old boys or girls might not necessarily understand all the questions
posed). If the aim of the study was to validate the QOLRAD in young patients we
should be sure that they understand it (and in every language). I feel that this is a
major point of concern.
Moreover, this study was conducted in different countries. Were the cross
cultural differences taken in account in the analysis of quality of life?
Was the distribution of the data assessed? Was it normal? Why did the authors
not use nonparametric tests such as Wilcoxon paired test instead of paired t test
that should be used only in case of normal distribution?
If the data were not normal median and IQ range would be a more appropriate
way to present them.
Could the authors explain better and with more details why they considered
"differences in QOLRAD scores 0.5 or more as clinically significant"? Is it a
standard use in QOLRAD anayisis?
The last paragraph of the results section is unclear: could the authors rewrite it
more clearly?
Review for 10.1186/1471-230X-9-84 (2009)

Reviewer's report
Title:Effects of esomeprazole treatment for gastroesophageal reflux disease on
quality of life in 12- to 17-year-old adolescents: an international health outcomes
study
Version: 2Date:9 September 2009
Reviewer: Marco Scarpa
Reviewer's report:
I have carefully read the point by point reply of the authors and I think that they
aswered adequately and completely to all the questions. Therefore, I recommend
that the paper should be accepted without any further delay.
Review for 10.1186/1471-230X-9-83 (2009)

Reviewer's report
Title:Psychological stress decreased iron absorption in rats
Version: 1Date:10 June 2009
Reviewer: Phillip S Oates
Reviewer's report:
This is an interesting paper regarding the effect of psychological stresshas on
intestinal iron absorption. It involves providing rats 4-5 weeks of age(assumed
given the weight) with bursts of electrical shock at 30 sec intervals. I assume
ethical approval has been given for this protocol as I cannot see a statement to
this effect.
The results suggest that although dietary intake and therefore iron absorption
was the same, feacal iron absorption decreased with the length of PS and that
this was ferroportin/hepcidin dependent. Although this is the conclusion no data
is included here regarding hepcidin although a previous study indicates this
relationship.
Major issues with this study that need to be resolved:
Hepatic hepcidin expression needs to be included on these rats to confirm the
temporal pattern of iron absorption.
Spleen iron and ferroportin expression should be presented to demonstrate the
hypoferremia is not due to retention of iron by macrophages. It is likely
macrophages contribute significantly to the hypoferremia measured and be the
more potent factor than intestinal iron absorption.
Importantly, the nature of the intestinal iron measurements are indirect rather
than direct such as using isotopic measurements, the preferred method.
Moreover the experimental design also may be problematic, that is PS is likely to
increase intestinal transit. The fact that defacation was a response to PS
indicates loss of control of bowel movements. Since non haem iron absorption is
confined to the duodenum any rapid/uncontrolled gastric emptying will make iron
absorption inefficient and this may account for the decreased iron absorption
measured. This can be estimated by the period of the red coloration appearing in
the feaces (not included) but still this is not as good as measuring isotopic iron
absorption in duodenal situ gut sacs which is direct.
The way in which the protein was harvested from the duodenum appears
suboptimal. The lack of protease inhibitors in the buffers used to recover protein
from the duodenum is fraught with problems as the duodenum contains high
levels of pancreatic derived proteases which can rapidly degrade the protein.
In summary although interesting the data is not convincing in its demonstration of
PS affects on iron absorption via hepcidin/ferroportin.
Review for 10.1186/1471-230X-9-83 (2009)

Reviewer's report
Title:Psychological stress decreased iron absorption in rats
Version: 1Date:25 August 2009
Reviewer: Gaelle Boudry
Reviewer's report:
This short paper investigates the effect of different durations (1d, 3d and 7d) of
psychological stress (using the communication box model) on iron apparent
intestinal absorption and iron transporter expression in the duodenum of rats.
They observed an almost 50% decrease in iron apparent absorption after 3 days
of psychological stress as well as a down-regulation of ferroportin 1 expression,
up-regulation of ferritin and presence of iron in the apical poles of enterocytes.
The divalent metal transporter 1 expression was not affected by stress.
Major Compulsory Revisions
1- There are numerous misspellings and grammatical errors that will have to be
corrected.
2- The material and methods section is not complete and some precisions should
be given:
- the description of the stress protocol should be improved
- the way the hypothalamus and serum was collected and then stored should be
described
- the name of the companies for the ELISA kits for corticosterone, ACTH and
norepinephrine as well as the CV for each assay should be given.
- How was the duodenum fixed: formalin then embedded in paraffin or frozen?
- in the Western blot section, no details on the HEPES-EDTA buffer are given
(use of protease inhibitor, sucrose?). There are also no details on the
electrophoresis and transfer procedures.
3- The values for ACTH are enormous (300-400 ng/mL when the usual values
range between 10 and 100 pg/mL): is it a problem with the assay or a mistake in
the units?
4- In the discussion and conclusion, the authors use the results of one of their
recent paper to conclude on the role of hepcidin and IL-6 in the reduced iron
intestinal absorption they observed. However, they did not actually measure the
iron apparent absorption in rats treated with anti-IL6 antibody to draw firm
conclusion. I would therefore suggest being less affirmative in their conclusions
and discuss other possible mechanisms.
Minor Essential Revisions
1- Figure 1 B: are the iron intake in mg as written or mg/d?, Figure 1C: what is
the actual unit of fecal iron content: mg/g of faeces, mg excreted / d ? Figure 1D:
is it the percentage or the ratio?
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-9-83 (2009)

Reviewer's report
Title:Psychological stress decreased iron absorption in rats
Version: 1Date:27 August 2009
Reviewer: Chen Wei-Qiang
Reviewer's report:
Minor essential revisions:
1. the title was too confirmed about the effect of PS on iron absorption in rats.
Should it be “effect of PS on iron absorption in rats”.
2. page2 the 2nd line: “in rats” should be deleted.
3. page2 the 9th line: “that” should be deleted. Or the sentence should be altered
as “And we found that the iron apparent absorption and accumulation were
decreased in the apical poles of villous ------”.
4. add several keywords.
5.there are many “the”s in this manuscript, please confirm their necessary usage.
For example, page4 the 9th line: the control group and the PS group.
6. page8 “Results: PS induced changes in CORT, ACTH and NE”, and page 9
“PS induced changes in ferritin and FPN1 protein expressions”, “in” should be
replaced by “of”.
7. page9 “Perl’s staining”: the whole sentence has grammar mistakes.
8. page10 the last 5th line: “It was conclude that------” should be altered as “It
was concluded that”.
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-9-83 (2009)

Reviewer's report
Title:The effect of psychological stress on iron absorption in rats
Version: 2Date:15 October 2009
Reviewer: Phillip S Oates
Reviewer's report:
I have checked the paper, the response to my concerns have been addressed.
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-9-83 (2009)

Reviewer's report
Title:The effect of psychological stress on iron absorption in rats
Version: 2Date:16 October 2009
Reviewer: Gaelle Boudry
Reviewer's report:
The author's have significantly improved the manuscript with their corrections
and additional information. They have addressed most of my concerns. There
are still some mispelling and grammatical errors e.g.:
line 11-12 of the abstract chnage "expression of DMT1 had no change" to
"expression of DMTA did not change"
page 3 change "is being normal" by "is normal", change the sentence "However
the involved..." by "However, the molecular mechnanisms explaing how..."
page 4 change "demonstrated" by described, "weighting" by "weighing"
page 6 change "the diets changed" by "the diets were changed", "not include the
second" by "not including the second" and "shown" by "expressed"
page 8 change 'under condition 200 mA" by "under conditions of 200 mA during
120 min"
page 9 change "was considered statistically significant difference" by "was
considered as a statistically significant difference"
page 10 change "DMT1 expression" as for the abstract
page 11 change 'in present study" by "in the present study"
page 13 remove the "and" before interleukine (IL-6) can..., rewrite the sentence
"based onivestigations...iron absorption.", same for (In present study, the iron
intake....with other's studies"
Last comment, why are the CORT, ACTH and NE data avalaible only for PS 7d ?
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 I have no competing interets
Review for 10.1186/1471-230X-9-81 (2009)

Reviewer's report
Title:Liver fibrosis secondary to bile duct injury: correlation of Smad7 with TGF-b
(beta)and fibrotic proteins
Version: 2Date:5 May 2009
Reviewer: Ian Hines
Reviewer's report:
The manuscript entitled “Liver fibrosis secondary to bile duct injury: correlation of
Smad7 with TGF-b (beta) and fibrotic proteins” by Alatorre-Carranza et al
demonstrates the expression of key fibrotic and potentially anti-fibrotic proteins
within the livers of humans suffering from cholestatic liver disease and fibrosis.
The data essentially confirm experimental findings in animals showing
expression of TGFb, Platelet activating inhibitor-1, etc. within the fibrotic liver.
The studies also suggest a positive correlation of the expression of these factors
with the induction of Smad7 expression. Again these findings are similar to those
shown in animal models but does extend findings to the human condition which
is important. Several concerns were noted during review which should be
addressed.
Major Compulsory Revisions
1. While this paper provides some translational data to suggest that findings in
animal models are consistent with processes activated in humans, it falls short of
providing important information about the cellular source of certain factors,
specifically Smad7. The source of expression of TGF# and PAI-1 is less
important as these are soluble proteins however Smad7 is an intracellular
inhibitor of Smad signaling. In hepatocytes, Smad7 induction serves to inhibit
Smad2-3-4 signaling and likely inhibits apoptosis whereas its expression in
stellate cells limits collagen gene expression. It is likely that this protein is
expressed in both cell types however these data need to be shown.
Immunohistochemical localization of Smad7 would greatly strengthen the
findings and significance of this work.
Minor essential revisions
2. The patient population examined appears to be somewhat heterogeneous with
respect to the duration of the diagnosed disease. While it is recognized that
heterogeneity is inevidable when examining human samples, does this
heterogeneity potentially weaken the findings. Alternatively, are there two
populations within this study (short term disease vs. long-term disease) which
may show differences in the relative correlations among expression of the factors
examined. Please comment.
3. The image provided for Trichrome staining is not clear. While there is no doubt
fibrosis exists, other stains such as Picrosirius red should be considered as the
typical blue staining denoting collagen in Trichrome is not visible and such data
would be most helpful to readers not familiar with fibrosis-associated
histopathological changes. Also, given the heterogeneity of the patients, it should
be noted which patient sample was used for this image.
4. The manuscript suffers from substantial grammatical errors which must be
corrected prior to publication.
Quality of written English: Not suitable for publication unless extensively edited
Review for 10.1186/1471-230X-9-81 (2009)

Reviewer's report
Title:Liver fibrosis secondary to bile duct injury: correlation of Smad7 with TGF-b
(beta)and fibrotic proteins
Version: 3Date:28 July 2009
Reviewer: Ralf Weiskirchen
Reviewer's report:
Alatorre-Carranza and co-workers have addressed and comment on most of the
issues that were raised in my initial review. However, I have (still) two further
short comments that should be revised in the final version:
Discretionary Revisions
1. in the headline it must read “extracellular matrix proteins” instead of “matrix
extracellular proteins”
2. In the cover letter the authors state that “… there does not exist any reports in
the literature on polymorphisms in TGF-beta genes and serum levels within the
Mexican population”. However, it was previously shown that there is a potential
link of these polymorphisms to hepatic fibrosis in patients of Mexican ancestry
(see Armendáriz-Borunda et al. J Investig Med. 2008;56:944-953). Moreover the
precise frequencies of some of these polymorphisms can be found in the
HapMap database that also includes gene frequencies of a Mexican ancestry in
Los Angelos. The respective link is:
http://www.hapmap.org/cgi-perl/gbrowse/hapmap27_B36/. Therefore, I would ask
the authors for adding one short critical sentence highlighting the fact that these
results might partially be overlapped by TGF-beta gene polymorphisms that were
not analysed in this study.
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-9-81 (2009)

Reviewer's report
Title:Liver fibrosis secondary to bile duct injury: correlation of Smad7 with TGF-b
(beta)and fibrotic proteins
Version: 3Date:18 August 2009
Reviewer: Ian Hines
Reviewer's report:
While the authors verbally addressed my concerns, additional data was not
included. Cell localization of Smad7 expression as well as alternative approaches
to stain collagen would greatly strengthen the manuscript and increase its
impact. In the current form, this manuscript is very descriptive and falls
somewhat short of defining a role for Smad7 in cholestasis associated liver
fibrosis in humans.
Nevertheless, it is the first report to my knowledge to measure Smad7 expression
in human liver samples in this setting. It may provide a springboard for
subsequent studies to define a role for Smad7 in human liver fibrosis, a clinically
relevant problem and potential therapeutic target. For this reason, I find the
article acceptable in the current form for publication.
Review for 10.1186/1471-230X-9-82 (2009)

Reviewer's report
Title:A comparison of diagnostic tests for lactose malabsorption - which one is
the best?
Version: 1Date:13 July 2009
Reviewer: Antonio Tursi
Reviewer's report:
This is an interesting study comparing several common tests to diagnose lactose
malabsorption. The authors found that the combination H2+CH4 is the best test
to diagnose malabsorption.
I mean that this study needs of Major compulsory revisions.
The most weakness is that this report did not consider the statements about this
field recently published by the Rome Consensus Conference in APT (Gasbarrini
A et al. APT 2009;29(suppl. 1): 1-49). In particular, methodology of the text (e.g.
collecting samples, diet before testing, avoiding smoke, etc.) should be
performed according to these statements. Moreover, the results should be
discussed in light of these Consensus Conference statements. For example,
Consensus statement did not find measurement of CH4 currently recommended
to improve the diagnostic accuracy of the hydrogen breath test (level of evidence:
IIa, strength of recommendation: B). At the same time, It identify that it is useful
to evaluate the onset and the severity of symptoms during the tests and up to 8
hours after, to determine lactose intolerance test (level of evidence: IIb, strength
of recommendation: B). All the methodology should be therefore performed
according to these indications, and the results should be discussed according to
these new statements.
Moreover, could be interesting whether the authors discuss better some results
(e.g., higher MBI in not-LM subjects) that may influence the symptomatic
response, also in light of the different literature’s experiences (see Landau DA et
al. J Clin Gastroenterol 2008;42(8):903-9);
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 interest"
Review for 10.1186/1471-230X-9-82 (2009)

Reviewer's report
Title:A comparison of diagnostic tests for lactose malabsorption - which one is
the best?
Version: 1Date:28 July 2009
Reviewer: Piero Vernia
Reviewer's report:
The study, although of some interest, is not new. In 1975 Necomer et al
published in NEJM a paper addressing the same problem. The test for genetic
defect is here used (and in a subset of patients only) whereas Newcomer
measured lactase activity. In both papers the serum glucose levels after a
lactose load were compared to the H2 breath test. Glucose levels, however, are
not any more used in adults, being less reliable that other techniques for the
diagnosis of lactose malabsorption /intolerance.
One main problem resides in the overall number of patients, which is low. The
patient selection, based on perceived milk intolerance (which is utterly unreliable)
and/or “non specific abdominal discomfort” is vague and debatable. Better
defined inclusion criteria, a larger patient series, and , possibly, exploring the
genetic defect in all patients would add much to this study.
The most interesting point of the paper is the demonstration that the sum of H2
plus CH4 x 2 has slightly better diagnostic properties as compared to H2.
Theoretically this approach is sound, H2 plus CH4 x 2 expressing more precisely
than H2 alone the overall production/ excretion of hydrogen. Nonetheless the
clinical use of methane is difficult as its concentration is highly variable, both in
fasting condition and after meals. The problem, in my opinion should be
discussed in detail by the authors.
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-9-82 (2009)

Reviewer's report
Title:A comparison of diagnostic tests for lactose malabsorption - which one is
the best?
Version: 2Date:14 October 2009
Reviewer: Antonio Tursi
Reviewer's report:
The authors answered to all questions, and the paper may be now accepted.
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-9-82 (2009)

Reviewer's report
Title:A comparison of diagnostic tests for lactose malabsorption - which one is
the best?
Version: 2Date:19 October 2009
Reviewer: Piero Vernia
Reviewer's report:
the low number of cases , and the inclusion of some patients with organic
disease, the authors answered reasonably well to my comments and those of the
othe reviewer.
Although the overall idea is not new, some part of the paper provide new and
interesting data to this area.
The paper may be accepted.
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 daclare that I have no competing interests
Review for 10.1186/1471-230X-9-80 (2009)

Reviewer's report
Title:Cholecystectomy and sphincterotomy in patients with mild acute biliary
pancreatitis in Sweden 1988 - 2003: a nationwide register study
Version: 1Date:23 November 2008
Reviewer: Raffaele Pezzilli
Reviewer's report:
Overview
The authors report the effect of cholecystectomy/sphincterotomy within 30 days
of index admission, on readmission rate, total cholecystectomy rate at one year,
and mortality at 90 days in the Swedish population. The data were extracted from
nationwide hospital discharge and death certificate register. The conclusions are
that after an attack of mild acute biliary pancreatitis, 55% of patients in this audit
had cholecystectomy within one year of index admission but only 20% within one
month. Cholecystectomy during index stay slightly prolonged this stay, but
drastically reduced readmissions for biliary indications. The data are similar to
those already reported in other European and American countries and they do
not add any useful information on this topic.
Major compulsory resision
The main criticism of this study has been underlined by the same authors: even if
the authors have used nation-wide and validated register data based upon
personal identification numbers unique for each citizen, which makes it possible
to follow individuals over time and to record diagnoses and procedures during
each hospital stay they have limited information on patients’ clinical status. They
are not able to apply the Atlanta severity classification method to assess the mild
acute biliary pancretitis: this represents a bias for a study like this that would
assess the effect of cholecystectomy on mild acute biliary pancreatitis.
Discretionary revisions
1. In the results section the authors should report the mean age and the
respective range of the patients studied (see Table 1).
2. The four different MBAP groups studied should be reported in the methods
section
Level of interest: An article of limited interest
Quality of written English: Not suitable for publication unless extensively edited
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-9-80 (2009)

Reviewer's report
Title:Cholecystectomy and sphincterotomy in patients with mild acute biliary
pancreatitis in Sweden 1988 - 2003: a nationwide register study
Version: 1Date:4 December 2008
Reviewer: Hein Gooszen
Reviewer's report:
This is a review of the paper “Cholecystectomy and sphincterotomy in patients
with mild acute biliary pancreatitis in Sweden 1988 – 2003: a nationwide register
study” bij
Birger Sandzén et al.
Minor Essential Revisions (such as missing labels on figures, or the wrong use of
a term, which the author can be trusted to correct)
Introduction: “In UK guidelines” should be “In the UK guidelines”
Introduction: “Data from nationwide hospital discharge and death certificate
register were used” shoud read “Data from the nationwide….”
Results: 4 groups are described first here, please already describe them in the
methods section .
Results: please do not mention data with groups 1-4 in the text but rather use
tables.
Please ask a native speaker to check the full text of this paper. At numerous
points in the text words like “the” and “a” are missing
Major Compulsory Revisions
- Introduction:“The complication risk in predicted severe acute biliary pancreatitis,
but not in mild acute biliary pancreatitis (MABP), is reduced by early ERCP with
or without sphincterotomy [5]”. This statement is too strong according to recent
literature, such as Petrov et al, Ann Surg 2008.
- Explain how patients were divided into the four groups: institution policy,
docotor's preference, author's discretion?
- Discussion:
- explain potential biases, like in the subdivision into four groups, were age and
local preference and patient selection for the different approaches may hqave
played a major role by the type of treatment for the specific clinical and
radiological presentation; selection bias and its impact must be discussed here.
- “Thus, for patients with mild gallstone pancreatitis fit for surgery,
cholecystectomy at first admission, with intraoperative cholangiography and
concomitant bile duct exploration if necessary is an appropriate treatment”
Laparoscopic bile duct exploration is not a widely accepted technique and there
countries "in favor" and countries "against" at this point in time. Worldwide
acceptance is unlikely. Intraoperative cholangiography is more widely accepted
but still controversial, even in patients with relatively high risk of common bile
duct stones as most stones will pass spontaneously. Please revise these
paragraphs, using international guidelines +/- meta-analysis/reviews as
references.
- there is a difference in mortality between groups 1-2 and 3-4, please discuss
this difference. Is there another source of bias here, in the sense that the older
the patient, the more restrictive the surgical approach?
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.
Review for 10.1186/1471-230X-9-80 (2009)

Reviewer's report
Title:Cholecystectomy and sphincterotomy in patients with mild acute biliary
pancreatitis in Sweden 1988 - 2003: a nationwide register study
Version: 1Date:29 December 2008
Reviewer: Thomas P. Hüttl
Reviewer's report:
The paper from Sandzen et al. includes highly intreseting results of nationwide
database with clear statements.
The paper is helpful for surgeons as well for gastroenterologists and it is
worthwile to be published.
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-9-80 (2009)

Reviewer's report
Title:Cholecystectomy and sphincterotomy in patients with mild acute biliary
pancreatitis in Sweden 1988 - 2003: a nationwide register study
Version: 2Date:26 June 2009
Reviewer: Hein Gooszen
Reviewer's report:
The main findings are:
- high readmission rate in group 2
- higher CFR in groups 3 and 4
The high re-admission rate is inevitable because this is surgeon's/hospital policy
and it even needs further explanation why it is not 100% and, again, which were
the reasons for re-admission: was it for cholecystectomy only or was it for
complications of gallstone disease
The higher CFR is explained by a combination of age alone and most likely also
because of complications of the disease. This is, again, not sub-divided
Unfortunately, the manuscript has not improved as compared to the previous
version
Level of interest: An article whose findings are important to those with closely
related research interests
Quality of written English: Not suitable for publication unless extensively edited
Statistical review: No, the manuscript does not need to be seen by a
statistician.
Review for 10.1186/1471-230X-9-80 (2009)

Reviewer's report
Title:Cholecystectomy and sphincterotomy in patients with mild acute biliary
pancreatitis in Sweden 1988 - 2003: a nationwide register study
Version: 2Date:11 September 2009
Reviewer: Greger Lindberg
Reviewer's report:
In my modest opinion the manuscript does contain sufficient novel information to
merit publication. I have two minor suggestions.
1. Age should not be given as mean and SD since it is usually not a normally
distributed variable (Table 1). I would prefer median and range or interquartile
range.
2. I wonder if the contribution of age to the case fatality rate could be studied
using a multiple regression model (e.g Cox regression) with age, complications (if
these can be determined from available data), and group as covariates.
Review for 10.1186/1471-230X-9-79 (2009)

Reviewer's report
Title:Investigation of innate immunity genes CARD4, CARD8 and CARD15 as
germline susceptibility factors for colorectal cancer
Version: 1Date:11 May 2009
Reviewer: George E Theodoropoulos
Reviewer's report:
I read with pleasure the article by Möckelmann et al dealing with the germline
CARD/NOD polymorphisms on colorectal cancer susceptibility. This is an
exceptional paper offering valuable data on this interesting matter, since it refers
on the largest series of patients amongst studies focusing on a similar matter. It
is a well-written, concise paper that may require a brief overview for minor
grammatical errors. The methods used seem sound and appropriate and the
results are well presented and comprehensible by non-experts.
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-9-79 (2009)

Reviewer's report
Title:Investigation of innate immunity genes CARD4, CARD8 and CARD15 as
germline susceptibility factors for colorectal cancer
Version: 1Date:19 May 2009
Reviewer: Frank Grünhage
Reviewer's report:
The authors present a negative association study on different CARD SNPs and
colorectal cancer. The study is well done and although the result is negative it
provides important information for the scientific community. The methods are
sophisticated and the power of the study has been formally assessed. Thus I
have only minor comments that should be addressed in the discussion and may
be taken as suggestions for further studies:
1. Genetic sucsceptibility factors for whatever trait tend to lead to presentation of
affected patients at younger age. Thus, it would have been interesting to look at
a subgroup of patients with earlier manifestation of the CRC (e.g. below 50y).
2. The authors noticed that CRC syndromes are rare and a majority of CRC
cases are sporadic. However, there is also a group of patients (appr. 20%),
which is not well defined and who have a personal or family history of CRC that
does not fulfil HNPCC or FAP criteria but is suspicious of an underlying genetic
susceptibility factor. The likelihood to identify such factors in sporadic cases is
low. Hence, it would have been interesting to look at differences in
allele/genotype distribution between phenotypic extremes such as patients with
early CRC or late CRC
3. By including controls who were older than the cases, the authors excluded to
assign patients who might develop CRC in the future. However, this approach
does not exclude controls with undetected colorectal adenoma. Thus the ideal
controls are age matched with no personal or family history of colorectal
adenoma and a normal colonoscopy, so called hyper normal controls.
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-9-79 (2009)

Reviewer's report
Title:Investigation of innate immunity genes CARD4, CARD8 and CARD15 as
germline susceptibility factors for colorectal cancer
Version: 2Date:6 August 2009
Reviewer: Frank Grünhage
Reviewer's report:
All my concerns were addressed sufficiently in the revised version of the
manuscript. Thus I would recommend this paper for publication.
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-9-79 (2009)

Reviewer's report
Title:Investigation of innate immunity genes CARD4, CARD8 and CARD15 as
germline susceptibility factors for colorectal cancer
Version: 2Date:10 September 2009
Reviewer: RAJA MARRAKCHI
Reviewer's report:
This article is accepted
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 interest's
Review for 10.1186/1471-230X-9-77 (2009)

Reviewer's report
Title:The VEGF -634G>C promoter polymorphism is associated with risk of
gastric cancer
Version: 1Date:11 June 2009
Reviewer: Stefania Boccia
Reviewer's report:
The paper of Guan et al. reports the results of an hospital-based case- control
study conducted in US aimed to investigate the association between selected
SNP in TGFB1 and VEGF genes and risk of gastric cancer. Results suggest that
subjects heterozygous for the -634 CG genotype of VEGF gene have an
increased risk for gastric cancer. Haplotype analysis and stratified analyses did
not show significant associations.
Even though the study is methodologically well conducted, authors acknowledge
the fact that the genotype data of VEGF-634 among controls do nor respect the
Hardy-Weinberg equilibrium. This observation strongly affects their results, as
the p-value for the chi-square test (not reported in the results) is 5 x10 -13, which
is particularly high. Selection bias of the control is not likely to explain such a
large deviation of HWE, as authors claim. The most common reason for the
violation of the equilibrium is a genotyping error, and even though authors
acknowledge that for 10% of samples the assay was repeated with 100%
concordance, this cannot exclude that a genotyping error might affect the validity
of the results of the entire study. Additionally, if they exclude that a laboratory
error happened, they should have stratify the VEGF -634 CG results according to
ethnicity (e.g., by excluding non-white), as the second most probable reason for
violation of the HWE is population stratification.
As such, I find hard to accept the results of the manuscript in view of the
aforementioned observations.
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 have no competing interests.
Review for 10.1186/1471-230X-9-77 (2009)

Reviewer's report
Title:The VEGF -634G>C promoter polymorphism is associated with risk of
gastric cancer
Version: 1Date:23 June 2009
Reviewer: Maria Gazouli
Reviewer's report:
Minor Essential 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-9-77 (2009)

Reviewer's report
Title:The VEGF -634G>C promoter polymorphism is associated with risk of
gastric cancer
Version: 1Date:24 June 2009
Reviewer: Jing Shen
Reviewer's report:
A hospital-based case-control study was conducted to examine the association
between TGFB1 and VEGF genetic polymorphisms and gastric cancer risk.
Although the sample size is moderate (171 patients and 353 controls), one
positive result was observed that VEGF 634CG genotype and the combined
CG+CC genotype were associated with a significantly elevated risk of gastric
cancer. The study design is well, and the statistical methods are suitable. The
results were described correctly, and no over-interpretation. These results are
valuable for understanding the susceptibility of gastric cancer in Caucasian
although several studies have been done in Asian population.
Minor Essential Revisions
1) It is unclear how many gastric cancer cases are histological diagnosed
intestinal or diffuse types in the current study. It is important because different
subtypes may have different susceptibility.
2) Providing the information about the false-positive report probability (FPRP) for
the positive findings is necessary.
3) More discussions are also needed to evaluate the potential influence of the
SNP that is not in agreement with the Hardy–Weinberg equilibrium. Whether it
may bias the result?
4) What is the advantage of the current study or the feature that are different
from other previous studies in gastric cancer?
5) As mentioned by the authors that an obvious limitation of the current study
was the lack of information on the H. pylori infection status of the subjects, more
evidence that the observed positive results may be unlikely to be impacted by the
relatively lower H. pylori infectious rare in US population will strengthen the
discussion.
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-9-77 (2009)

Reviewer's report
Title:The VEGF -634G>C promoter polymorphism is associated with risk of
gastric cancer
Version: 1Date:26 June 2009
Reviewer: Annamaria Ruzzo
Reviewer's report:
The manuscript by Guan et al reports that exist an association between gastric
cancer and VEGF -634 G/C polymorphism.
There are some important points unclear:
1. Gastric cancer consists of two pathological variants, intestinal and diffuse: how
many patients in this study are intestinal? how many diffuse?
2. The association of Helicobacter Pylori(HP) and gastric cancer is well
established and Authors underlay this statement under “introduction”, but at the
same time they don’t mention if samples are or not infected by HP. HP is more
diffuse in Asians than Caucasians, but this is not a good reason for not reporting
this information among variables.
3. What the author mean with Non-Hispanic white? The term Caucasian race
(also Caucasoid or Europid) has been used to denote the general physical type
of some or all of the indigenous populations of Europe, North Africa, the Horn of
Africa, West Asia, Central Asia and South Asia (The Races of Europe by Carlton
Stevens Coon. From Chapter XI: ).
3. Authors report under “TGFB1 and VEGF genotypes and risk of gastric cancer”
that the SNPs were all in agreement with H-W equilibrium except for TGFB1 -509
C/T and VEGF -634 G/C. The VEGF -634 G/C is the only SNP associated with
gastric cancer. In my opinion the H-W disequilibrium for VEGF -634 can influence
the results reported and address researchers to wrong conclusions.
Level of interest: An article of outstanding merit and interest in its field
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
Review for 10.1186/1471-230X-9-77 (2009)

Reviewer's report
Title:The VEGF -634G>C promoter polymorphism is associated with risk of
gastric cancer
Version: 1Date:6 July 2009
Reviewer: Xinru Wang
Reviewer's report:
The authors studied correlation between genetic polymorphisms of TGF-ß1 and
VEGF genes and gastric cancer in a case-control study consisting of 171
patients with gastric cancer and 353 cancer-free controls. They found that
VEGF-634G>C SNP may contribute to the risk of developing gastric cancer.
General comments:
The experiment seems well performed and data are clearly exposed. The results
are of interest, although the sample sizes are rather small.
However, several points deserve great attention.
1. In table 3, the reason why the authors have chosen the age 57 years as the
cut-off value is not clear and should be explained.
2. The data show that the genotype frequencies of the VEGF -634CG
heterozygous was significantly higher in cases (42.1%) than the controls
(28.0%), and the authors got the conclusion that VEGF-634G>C SNP may be
associated with susceptibility to gastric cancer. Intuitively one would think that the
CC genotype may have a stronger association with the risk of gastric cancer.
However, from the table 2, it shows that VEGF -634CC genotype was less
frequent in the cases (17.5%) than in the controls (21.0%). This issue should be
discussed.
3. The interesting aspect of the alcohol use effects should be discussed more
intensively, and explain how the genetic effects was more profound in the never
drinkers.
Recommendation: Major Compulsory Revisions
Review for 10.1186/1471-230X-9-77 (2009)

Reviewer's report
Title:The VEGF -634G>C promoter polymorphism is associated with risk of
gastric cancer
Version: 2Date:22 August 2009
Reviewer: Stefania Boccia
Reviewer's report:
No revisoin required.
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:
No
Review for 10.1186/1471-230X-9-77 (2009)

Reviewer's report
Title:The VEGF -634G>C promoter polymorphism is associated with risk of
gastric cancer
Version: 2Date:25 August 2009
Reviewer: Annamaria Ruzzo
Reviewer's report:
Major Compulsory Revisions:
1.The association between Helicobacter Pilory (HP) and gastric cancer is well
established. HP infection is common in the United States. About 20 percent of
people under 40 years old and half of those over 60 years have it. It is very
important to know if patients and controls are infected. This paper still lacks this
important data.
Level of interest: An article of insufficient interest to warrant publication in a
scientific/medical journal
Quality of written English: Acceptable
Statistical review: Yes, but I do not feel adequately qualified to assess the
statistics.
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:24 May 2009
Reviewer: Jeroen J Kolkman
Reviewer's report:
Major Compulsory Revisions (which the author must respond to before a
decision on publication can be reached)
1. This study includes only pediatric CD patients. This should be stated in title,
abstract, discussion and conclusion.
2. at p 9. the Hopper study is wrongly references to nr 14 (should be 15).
("Recognizing the patchy nature of the disorder, Hopper et al further studied the
number and location of biopsies required to make a definitive diagnosis of celiac
disease [14]".)
3. This study mainly confirms previous, larger studies. Although I agree the
importance of confrimatory studies in daily practice, the conclusion is therefore,
in my view, "overstated"
.
"In conclusion, villous atrophy can be patchy in patients with celiac disease with
duodenal
bulb mucosa being the only area showing histological changes in some cases. "
should in my view be:
"this study confirms previous reports that villous atrophy can be patchy in
pediatric patients with celiac disease with duodenal
bulb mucosa being the only area showing histological changes in some cases"
The remaining of the conclusion is not supported by the paper, but by other,
larger studies (Bonamico 2008 for example involves 665 patients, in contrast to
these 35 patients)
I would like to suggest to add that the current guideline may lead to
false-negative diagnosis with large implications for the patient (which would also
relate to the initial question of the paper).
Minor Essential Revisions (such as missing labels on figures, or the wrong use of
a term, which the author can be trusted to correct)
1. In the methods section I would like to suggest to explain the Marsh
classification, including the threshold for IEL's (the reference does cover this but
it makes the paper more easy to read).
2. on p4 the authors state that there question involved the outcome in daily
practice. A more precise definition of waht this sentence menas would be
helpfull.
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'
Jeroen J Kolkman