JerMa88/BMC_Gastroenterology_Peer_Reviews huggingface dataset:
Review for 10.1186/s12876-023-02795-3 (2023)

Title: The Risk for Celiac Disease after Covid-19 Infection
Version: 3 Date: 20 Mar 2023
Reviewer's report:
The work by J. Lexner et al. assess the risk for celiac disease after COVID-19 infection. The
work is well written as there are no big gramatical or language mistakes. The strenght of this
work is a complementary disscussion. Most of my concers were adressed there.  However there
are several issues to be addressed.
In Abstract:
line 8 - potential association between CD and COVID-19 were already studied. Please delete
or rewrite that sentence.
In Introduction:
page 3, line 28 - please provide also the abbreviation for respiratory syncytial virus as its more
commonly used.
In Patients and methods:
page 4, line 23/24 - you wrote that PIN number is "given at birth or immigration". I think
you should changed it to "given at birth or during naturalization" or "given at birth and to the
immigrants" to make it more clear.
page 5, line 7/8 - you used the biopsy's arrival date as the date of CD diagnosis. Why didn't you
use the exact date of diagnosis?
page 5, lines 24-34 and page 6, line 1-19  - very detailed description of COVID 19 and tTG-ab
detection techniques are provide. I think it is uneccessary to have that information as your study
used the data derived from registeries. This information should be deleted from your manuscript.
In Results:
page 9, Figure 2 - In your manuscript you wrote that the time between COVID-19 and CD was
evenly distributed and there is a reference to Figure 2. I think that this figure at first sight is not
very informative as I really cannot say how many point there are in left and right part of the
figure. You could delete that figure or try to make it more clear.
page 9, figure 2 - title of the figure should be changed to "Days from Covid-19 to celiac disease
diagnosis"
In Discussion:
page 10, line 14/15 - The content of last sentence is repeated. Please delate that sentence.
Review for 10.1186/s12876-023-02795-3 (2023)

Title: The Risk for Celiac Disease after Covid-19 Infection
Version: 6 Date: 21 Apr 2023
Reviewer's report:
thanks for resubmitting your amended pare and thanks for addressing my comments. I think the
paper reads well
a couple of comments / amendments required.
Page 4 line 26, instead of  and to the immigrants, suggest reword as 'and immigrants to the
country' or 'and to immigrants to Sweden'. only a minor change.
Second comment, Page 6 line 7, should be ESPGHAN.
best wishes
Review for 10.1186/s12876-023-02787-3 (2023)

Title: Phosphodiesterase 5 (PDE-5) inhibitors (sildenafil, tadalafil, and vardenafil) effects on
esophageal motility: a systematic review
Version: 3 Date: 18 Dec 2022
Reviewer's report:
Phosphodiesterase 5 (PDE 5) inhibitors (sildenafil, tadalafil, and vardenafil) in patients with
esophageal motility disorders: a systematic literature review
The authors have done review of the literature on PDE5 inhibitors in various motility disorders.
This is a gray area and rightly so needs evidence.
The study is good but needs better framing for a meaningful paper for readers.
Lower esophageal tone and contraction wave amplitude were reported to be decreased after
using PDE5 inhibitors in how many studies?
What were the main outcomes of the study? Enumerate in methods
How was the quality assessment done for the included studies? This has to be mentioned in
methods and the outcomes of assessment in results.
If there were a good number of trials, can the case reports be excluded or compiled in a separate
table? Better to focus on the outcomes of clinical trials.
In PRISMA, there are 3 studies from other sources. How were these three additional studies
obtained ?
Could you summarize your results according to the diseases?
The adverse events profile and drug discontinuation results should be summarized separately
in results
Discussion needs to focus on limitations of drug therapy in motility disorders, manometric
alteration produced by PDE5 inhibitors and various mechanisms of PDE5 inhibitors. What are
the conditions where PDE5 inhibitors could be started and where it lacks evidence?
Review for 10.1186/s12876-023-02787-3 (2023)

Title: Phosphodiesterase 5 (PDE-5) inhibitors (sildenafil, tadalafil, and vardenafil) effects on
esophageal motility: a systematic review
Version: 3 Date: 09 Jan 2023
Reviewer:  Praveen Kumar-m
Reviewer's report:
The authors should provide a detailed explanation of the outcomes and adverse events that were
examined in the study.
They should also conduct a risk of bias assessment and include the relevant details in the
methodology and results sections.
The PDE-5 inhibitors that were studied should be listed.
It would be helpful to separate the studies that included healthy subjects from those that included
patients with esophageal disorders.
There are grammatical errors in the manuscript, such as "mgs" instead of "mg".
The outcomes, such as lower esophageal sphincter tone, contraction wave amplitude, and
residual pressure, should be explained in the methodology section.
Review for 10.1186/s12876-023-02787-3 (2023)

Title: Phosphodiesterase 5 (PDE-5) inhibitors (sildenafil, tadalafil, and vardenafil) effects on
esophageal motility: a systematic review
Version: 5 Date: 27 Feb 2023
Reviewer's report:
The paper still lacks a structured format for easy readability. The results are confusing.
The outcome and results are confusing whether they are dealing with normal esophageal function
or motility disorder. The study by Kim HS et al also includes GERD. The results should be
shown separately for normal esophagus and for other diseases excluding GERD subset.
When you already are able to do meta-analysis of studies, case reports better be excluded. The
results of the qualitative section have to be organized and cut short in a better way.
And the other problem is a study of two case reports (Fox et al) was not included in either table
1 or 2.  To add to this confusion, the study by Fox et al has been cited twice in references (Ref
17 and Ref 29).
Please add the quality of studies as good or fair in assessment in the results section. JBI case
report appraisal suggests the use of include or exclude or seek further info as overall appraisal.
Review for 10.1186/s12876-023-02787-3 (2023)

Title: Phosphodiesterase 5 (PDE-5) inhibitors (sildenafil, tadalafil, and vardenafil) effects on
esophageal motility: a systematic review
Version: 5 Date: 20 Mar 2023
Reviewer:  Praveen Kumar-m
Reviewer's report:
All my comments have been addressed.
Review for 10.1186/s12876-023-02787-3 (2023)

Title: Phosphodiesterase 5 (PDE-5) inhibitors (sildenafil, tadalafil, and vardenafil) effects on
esophageal motility: a systematic review
Version: 6 Date: 11 Apr 2023
Reviewer's report:
The authors have revised the manuscript well
Review for 10.1186/s12876-023-02806-3 (2023)

Title: Value of transrectal ultrasound guided biopsy in endoscopy negative biopsy patients with
rectal lesions
Version: 1 Date: 15 Feb 2023
Reviewer:  Thomas Togliani
Reviewer's report:
This is an interesting and original work about ultrasound-guided needle biopsies of rectal lesions
after an unrevealing endoscopic biopsy.
My remarks are:
1) the english language is a bit poor:
page 4: need (be needed)
page 4: has use (is used)
page 5: patients divided (patients were divided)
page 7: take (taking)
page 8: endoscopic (endoscopy)
2) the methods are questionable: I don't understand why the choice of using the contrast or not
depends on the conditions and the willing of the patient; I would have preferred a randomization
3) in the discussion lacks any mention or comparison to studies about the gold standards
after negative endoscopic biopsies, which are the repetition of endoscopic biopsies (in case of
epithelial lesions) or EUS-guided needle biopsies (is case of subepithelial lesions)
Review for 10.1186/s12876-023-02806-3 (2023)

Title: Value of transrectal ultrasound guided biopsy in endoscopy negative biopsy patients with
rectal lesions
Version: 1 Date: 15 Apr 2023
Reviewer:  Andreas Polydorou
Reviewer's report:
This study is very good and helps in better histological diagnosis of rectal tumors especially
those that are not accompanied by mucosal damage. A few points need to be clarified:
1. Selection criteria number 3 states that patients had normal preoperative examinations. This
means that they had undergone a rectal CT scan or MRI with no pathological findings or not.
2. Details of endoscopic imaging and biopsies should be reported, eg in how many patients there
was visible mucosal damage and how many biopsies were taken each time.
It is mentioned in the results that the median size of the lesions was 4.5 cm, but it is not mentioned
with which examination it was measured, eg endoscopy, CT, MRI?
3. It would be interesting to add to table 3 in separate columns the clinical diagnoses from CT,
MRI and endoscopy and maybe understand the reason for failure of CE-TRUS or TRUS.
4. A comment should be added regarding the training and experience of the physician performing
the TRUS or CE-TRUS biopsies.
Review for 10.1186/s12876-023-02738-y (2023)

Title: The contribution of lysophosphatidic acid receptors in the response of human lower
esophageal sphincter under the electrical field stimulation
Version: 1 Date: 20 Jan 2023
Reviewer's report:
Feng et al. present an experimental  study with ex-vivo fragments of human esophagi to evaluate
the role of lysophosphatidic acid receptors  in the regulation of the lower esophageal sphincter
motility.
The idea is interesting and it is a follow up of previous experiemnts by the group.  The
manuscript; however, needs some clarification and perhaps another set of experiments to
adequate the methodology.
1) why this is called a "randomized comtrolled  study"?
2) I am familiar with the methodology but most readers will not be. A figure of the organ bath
would be contributory
3) Figures presented are not  comprehensible per se.  They represent a single result and not the
average for the n=28 as I understood. Tables would be more adequate.
4) In regards to the methodology, 2 points are lacking. First, how the specimens were preserved
until the experiment? How long between the operation retrieval and  the experiment? If this
was variable, vitality of the samples could be compromized and the second and most important
criticism is that there is no control group. How do I know that there was no effect of the frug or
that the muscle was simpling dying or weaking with time?
Review for 10.1186/s12876-023-02738-y (2023)

Title: The contribution of lysophosphatidic acid receptors in the response of human lower
esophageal sphincter under the electrical field stimulation
Version: 1 Date: 24 Jan 2023
Reviewer's report:
This investigation is based on the fact that in the past, lysophosphatidic acid receptor agonists
have been shown to cause contraction in clasp and sling fibers. The researchers’ previous studies
found that 10-5mol/L selective LPA1, LPA2 receptor agonists, and selective LPA3 receptor
agonists can induce the maximum contraction effect of clasp and sling fiber muscle strips. In
addition, they found that non-specific antagonists’ have been shown to block this effect in human
clasp and sling. (reference 21).
Therefore, it appears that they set out to determine which specific lysophosphatidic acid receptor
antagonists were involved in blocking the contractile and relaxation responses. Combined with
the above research results, the investigators compared the response of human LES induced
by EFS, before and after the application of 10-5mol / L selective LPA1 and LPA3 receptor
antagonists, to clarify the role of LPA1 and LPA3 receptors in EFS. They found that there was
no significant difference in contractile or relaxation response to these two antagonists. However,
the authors don’t comment on why they didn’t try a selective LPA2 receptor antagonist. At a
minimum, I would suggest that the authors explain why this wasn’t done. Is it because there is no
LPA2 antagonist available? However, if an LPA2 receptor antagonist is available, the authors
should run those experiments to determine the effect, especially since the nonspecific antagonist
blocks the effect. Alternatively, if there is no selective LPA2 antagonist they could explain that
blocking the LPA1 and LPA3 receptors with selective antagonists has no effect, yet using a
nonspecific antagonist blocks the response. Therefore, the LP3 receptors must be responsible
for blocking the response. The investigators should have the paper reviewed for grammar and
syntax.
Review for 10.1186/s12876-023-02738-y (2023)

Title: The contribution of lysophosphatidic acid receptors in the response of human lower
esophageal sphincter under the electrical field stimulation
Version: 4 Date: 19 Mar 2023
Reviewer's report:
I would include the possibility of LP2 receptors having an effect on the clasp and sling fibers in
the abstract. Otherwise I think that the paper can be published.
Review for 10.1186/s12876-023-02810-7 (2023)

Title: A Postsurgical Prognostic Nomogram for Patients with Lymph Node Positive
Rectosigmoid Junction Adenocarcinoma
Version: 2 Date: 27 Jan 2023
Reviewer's report:
Authors established a nomogram model for PLN-RSJCs, intending to support
clinicians in the treatment and follow-up of patients. However, the study lacks external
validation and therefore the nomogram application is doubted. The paper may provide sufficient
information if authors could provide validation using their own cohort.
Review for 10.1186/s12876-023-02810-7 (2023)

Title: A Postsurgical Prognostic Nomogram for Patients with Lymph Node Positive
Rectosigmoid Junction Adenocarcinoma
Version: 2 Date: 09 Feb 2023
Reviewer's report:
In the current manuscript the authors aimed to generate a reliable RSJC risk prediction model
that supports the prediction of the prognosis of PLN-RSJCs after surgery. They established a
nomogram model using independent risk predictors such as age, marital in a development cohort,
and validated its accuracy in a validation cohort. As an original research article, this paper is
well written, and provides a method for prognosis of PLN-RSJC patients. It can be considered
to minor revision. However, I have concerns with some questions as follows.
1. To explore and validate your model, the ratio of patients is 7:3 but not some other ratio. Please
explain it in the discussion.
2. There is a spelling mistake in the sentence " we extracted 3384 patients with PLN-RSJCs and
randomly divided them into development (n=2344) and validation (n=1004) cohorts at a radio
of 7:3" in your abstract. Please correct it in your revision.
3. There is a grammatical errors in the sentence “Kaplan-Meier survival curves showed
significant different in OS between the two groups in your result”. Please correct it in your
revision.
4. How do you know that there is no difference in results such as c-index or AUC values between
the development cohort and the validation cohort?  Please explain it.
Review for 10.1186/s12876-023-02810-7 (2023)

Title: A Postsurgical Prognostic Nomogram for Patients with Lymph Node Positive
Rectosigmoid Junction Adenocarcinoma
Version: 4 Date: 21 Apr 2023
Reviewer's report:
"PEER REVIEWER ASSESSMENTS:
OBJECTIVE - Full research articles: is there a clear objective that addresses one or several
testable research questions? (Brief or other article types: is there a clear objective?)
Yes - there is a clear objective
DESIGN - Is the current approach (including controls and analysis protocols) appropriate for
the objective?
Yes - the approach is appropriate
EXECUTION - Are the experiments and analyses performed with sufficient technical rigor to
allow confidence in the results?
Yes - experiments and analyses were performed appropriately
STATISTICS - Is the use of statistics in the manuscript appropriate?
Yes - appropriate statistical analyses have been used in the study
INTERPRETATION - Is the current interpretation/discussion of the results reasonable and not
overstated?
Yes - the author's interpretation is reasonable
OVERALL MANUSCRIPT POTENTIAL - Has the author addressed your concerns sufficiently
for you to now recommend the work as a technically sound contribution? If not, can further
revisions be made to make the work technically sound?
Yes - current version is technically sound
PEER REVIEWER COMMENTS:
GENERAL COMMENTS: I was not a previous reviewer. I read the responses to the prior
reviewers, but I did not actually have the prior reviews. Unfortunately, the authors did not copy
the prior comments into their response letter. However, the responses suggest the prior comments
were relatively minor. The authors used standard of care methods, including a nomogram,
concordance indices, receiver operating characteristic (ROC) curves, calibration curves, and an
internal validation cohort. The methods adhere to the typical nomogram development paradigm.
Based on the paper and the responses, I think the paper has been improved.
ADDITIONAL REQUESTS/SUGGESTIONS:
Minor comment: The authors could define the “All” and “None” labels in Figure 5, perhaps in
the figure caption (DCA curve)."
Review for 10.1186/s12876-023-02791-7 (2023)

Title: Assessing the Relationship Between Gut Microbiota and Irritable bowel syndrome: a
Two- Sample Mendelian Randomization Analysis
Version: 0 Date: 28 Mar 2023
Reviewer's report:
I read with great interest the manuscript by Liu et al., a Mendelian Randomization study designed
to examine the casual association between gut microbiome and irritable bowel syndrome. The
manuscript is well written and here are some comments for revision.
Experimental design and methods
The method section  lacks sufficient details in certain aspects, which may affect the readability
of the article as well as the reproducibility of the experimental results. For example,
1. The formulae used to calculate the proportion of variation explained (R2) and F-statistics:
a) What are the meanings of the parameters "MAF", "n" and "k" in the two equations and how
to obtain them?
b) When excluding the SNPs, it would be good to calculate the F-value again.
2. The beta values obtained from the results are relatively small. This could potentially be due
to the calculation unit used in the Mibiogen database.
3. For the MR design, Outcome Data Sources, Selection of Instrumental Variables and statistical
analyses, authors should justified their rationales behind the selection of each method used. For
example,
a) The Mibiogen database includes approximately 4,000 individuals who do not have European
ancestry. It would be worthwhile to investigate whether this non-European population has any
impact on the findings. A previous study has figured out this problem (PMID: 36380372).
b) I suggest to provide an explanation of the reasons behind selecting a specific method. This
will help readers understand the rationale for the approaches.
Validity of the findings.
In the discussion, the authors mentioned that "a decrease of phylum Actinobacteria was found in
patients with IBS compared to healthy controls"; however, phylum Actinobacteria was identified
as a risk factor in this study (odds ratio (OR): 1.08; 95% confidence interval (CI): 1.02, 1.15; P
= 0.011). This elaboration may be contradictory.
Considering the modest #-value and nominal p-value, the biological interpretation of the results
should be elaborated.
Additional Comments
Line 65: some unexpected spaces at the end of paragraph;
Attention should be paid to the font used for writing Latin.
Table 4: OR calculated via MR-Egger method was very large.
Review for 10.1186/s12876-023-02791-7 (2023)

Title: Assessing the Relationship Between Gut Microbiota and Irritable bowel syndrome: a
Two- Sample Mendelian Randomization Analysis
Version: 0 Date: 29 Mar 2023
Reviewer's report:
Thank you for sharing your research with us! You chose an interesting topic
Here are some ideas, which might improve your manuscript and make it more precise:
"p" is typically written in small letters.
Page 5, line 107: “‘TwoSampleMR” please correct
Page 5, line 109 “2,699” the comma should be removed
Review for 10.1186/s12876-023-02710-w (2023)

Title: CIRRHOSIS IN INTRAHEPATIC CHOLANGIOCARCINOMA: PROGNOSTIC
IMPORTANCE AND IMPACT ON SURVIVAL
Version: 3 Date: 16 Jun 2022
Reviewer's report:
This manuscript reported cirrhosis is associated with worse overall survival (OS) in patients
with iCCA using National Cancer Database (NCDB). The study showed that significant
differences were found for grade, pathologic stage, and tumor size across cirrhosis status, and
highlighted that cirrhosis was an independent factor for poor prognosis in iCCA patients. The
manuscript showed a potential role of cirrhosis in iCCA treatment and clinically practicality for
predicting the outcome of iCCA paitents. However, multiple weaknesses are noted, including
overinterpretation of the data and lack of innovation to support the conclusion of the manuscript.
Specific comments:
1. The role of cirrhosis in the treatment and prognosis of intrahepatic cholangiocarcinoma has
been reported before, and in 8th AJCC Tumor-Node-Metastasis (TNM) staging system, the
cirrhosis has been mentioned as an additional prognostic factor in iCCA patients. The authors
should highlight the innovation and particularity of this study compared with previous studies.
2. In table 5, the authors showed that after adjusting for sex, insurance, median income, race,
ethnicity, Charleson-Devo comorbidity score and timing of first course treatment, the presence
of cirrhosis among iCCA patients was associated with a reduced likelihood of both short-
term survival (OR=0.72, p=0.009) and long-term (OR= 0.77, p=0.031) survival, the authors
need to explain why these socio-demographic variables were selected for multivariable logistic
regression instead of the usual clinical variables, because the influence of socio-demographic
parameters on the prognosis of tumor patients remains to be further explored
3. In table 2, the author mainly mentioned tumor size and distant metastasis. However, lymph
node metastasis, vascular invasion and other important clinical parameters were not mentioned.
Relevant data or explanations need to be supplemented.
Review for 10.1186/s12876-023-02710-w (2023)

Title: CIRRHOSIS IN INTRAHEPATIC CHOLANGIOCARCINOMA: PROGNOSTIC
IMPORTANCE AND IMPACT ON SURVIVAL
Version: 6 Date: 10 Sep 2022
Reviewer's report:
Existing evidence suggests that cirrhosis is one of the major risk factors for intrahepatic
cholangiocarcinoma (CCA). Unfortunately, the presence of cirrhosis can be a relative
contraindication for curative surgical resection depending on the degree of underlying liver
synthetic dysfunction. Whether or not cirrhosis is truly prognostic of oncologic outcomes
remains controversial based on existing studies, with some studies suggesting that cirrhosis is
associated with worse outcomes. In this study, the authors conclude that there is no statistically
significant difference in long-term (5-year) survival among patients with iCCA based on
cirrhosis status after adjusting for clinical and tumor characteristics.
Minor comments:
Abstract: When reporting the number of people with iCCA as 33,160, the percentage
(63.4%) that is reported is a bit confusing. I’m assuming they mean that of all the cases of
cholangiocarcinoma, 63.4% were iCCA? This should be stated more clearly.
Lines 133-135: This sentence seems like it was duplicated by mistake
Line 144: I thought a total of 33,160 patients with iCCA were identified and only 3,644 had
a liver biopsy.
Table 1: The cutoff for elderly and non-elderly should be stated. Would list the age ranges for
the age categories.
Table 5: Duplicated. One of the tables should be removed.
Review for 10.1186/s12876-023-02710-w (2023)

Title: CIRRHOSIS IN INTRAHEPATIC CHOLANGIOCARCINOMA: PROGNOSTIC
IMPORTANCE AND IMPACT ON SURVIVAL
Version: 6 Date: 24 Sep 2022
Reviewer's report:
1. I think more details about all factors in the NCDB and why the authors chose current factors
are needed.
2. This study could add a flow chart to describe the included patients more concisely.
3. Compared with other studies about the same topic, are there some different factors that may
result in different conclusions?
4. There are two"AASLD" in lines 291 and 292.
Review for 10.1186/s12876-023-02710-w (2023)

Title: CIRRHOSIS IN INTRAHEPATIC CHOLANGIOCARCINOMA: PROGNOSTIC
IMPORTANCE AND IMPACT ON SURVIVAL
Version: 10 Date: 13 Nov 2022
Reviewer's report:
The study period and study population need to be described more clearly. The initial draft of the
manuscript reported that during the study period of 2010-2017, there were 53,054 patients with
CCA of whom 33,160 had intrahepatic CCA and 3,644 of the patients with iCCA underwent
a liver biopsy. In the current paper, the study period is reported to be from 2004-2017 but the
number of patients are the same despite expanding the study period. I’m assuming this was a
typo but just wanted to double check. Second, the study population and the patient flow figure
should be edited to enhance clarity. In the results section of the abstract (lines 52-53), the authors
report that there were 33,160 people with CCA, of whom 3,644 had intrahepatic CCA. In the
results section of the manuscript (line 142), they again state that 3,644 represents the number of
people with iCCA. In the limitations section (lines 309-310), they suggest that 33,160 represents
the number of people with iCCA and 3,644 represents the number of individuals that underwent
a liver biopsy. The patient flow diagram is a nice addition to the paper but should be revised to
enhance clarity and should include the study period. For example, “33,160 patients with iCCA
in NCDB (2004-2017) -> 3,644 patients with iCCA that underwent a liver biopsy -> 1,052 with
cirrhosis” etc.
The results section is redundant, with much of the information in the tables being reported in
the results section, and could be condensed.
There should be mention of the fact that only 3,030 patients had survival data available for
analysis and what proportion died during the study period. While the authors state this at the end
of their limitations section, it should be mentioned in the results section for greater transparency.
Lastly, the authors should state which variables were included in the final model and why.
Review for 10.1186/s12876-023-02710-w (2023)

Title: CIRRHOSIS IN INTRAHEPATIC CHOLANGIOCARCINOMA: PROGNOSTIC
IMPORTANCE AND IMPACT ON SURVIVAL
Version: 11 Date: 02 Mar 2023
Reviewer's report:
The paper discussed the significance of cirrhosis in the survival of  intrahepatic
cholangiocarcinoma. The results indicated that the presence of cirrhosis is not an independent
prognostic factor for survival in ICC patients. The authors well addressed the reviewer's
problems and the revised version of paper is qualified for publication.
Review for 10.1186/s12876-023-02777-5 (2023)

Title: Establishing Minimal Clinically Important Differences for the Quality of Life Instrument
of Chronic Gastritis QLICD-CG(V2.0) Based on Distribution-Based Methods
Version: 2 Date: 07 Jan 2023
Reviewer:  Edison Vitório De Souza Júnior
Reviewer's report:
Prezados autores e editores, agradeço-lhes por essa excelente oportunidade de avaliar vosso
trabalho que se mostra com grande relevância
1) Na introdução, senti falta da definição de qualidade de vida que os autores julgam relevante
para o estudo, bem como a citação de algum referencial teórico sobre o tema. Seria interessante,
também, trazer um tópico definindo e exemplificando os termos “Qualidade de Vida” e
Qualidade de Vida Relacionada à Saúde”, dois termos distintos, com aplicações diferentes
na prática e na teoria. Por fim, gostaria que os autores enfatizassem, ainda na introdução,
qual qualidade de vida foi adotada no estudo. No decorrer do texto está muito claro que a
definição adotada foi a Qualidade de Vida Relacionada à Saúde, pois os autores utilizaram dois
instrumentos específicos (SF-36 e o QLICD-CG), mas essa informação deve ser dada ainda na
introdução.
2) Não houve a realização prévia de cálculo amostral baseado em informações da literatura?
Caso contrário, é importante descrever que a amostra coletada é fruto de uma “amostragem por
conveniência”, ou “amostragem não probabilística do tipo consecutiva”. Essa informação deve
estar na seção “Settings and Participants”.
3) No item “Investigation Tools”, colocar as propriedades psicométricas dos instrumentos
utilizados conforme os estudos de validação.
CONCLUSÃO:
Diante da robustez metodológica do estudo, acredito que o mesmo é apto a ser aprovado por
esse periódico após sua adequação aos aspectos mencionados. Ressalto que a discussão está bem
fundamentada, a conclusão responde ao objetivo e as referências são específicas e pertinentes
ao tema. Agradeço aos autores e ao periódico pela oportunidade.
Review for 10.1186/s12876-023-02777-5 (2023)

Title: Establishing Minimal Clinically Important Differences for the Quality of Life Instrument
of Chronic Gastritis QLICD-CG(V2.0) Based on Distribution-Based Methods
Version: 6 Date: 12 Apr 2023
Reviewer's report:
The ammendments in the manuscript that I asked were all done by the authors.  I accept the
final version as it is.
Review for 10.1186/s12876-023-02812-5 (2023)

Title: The expression of interleukin-1# in patients with chronic hepatitis B treated with
Pegylated-interferon-# combined with tenofovir and monotherapy: analysis of 162 cases from
a single center
Version: 1 Date: 02 Mar 2023
Reviewer:  Li-Kun Wang
Reviewer's report:
The manuscript (entitled “The expression of interleukin-1# in patients with chronic hepatitis
B treated with pegylated interferon-# combined with tenofovir and monotherapy: analysis of
162 cases from a single center”) aimed to investigate the expression of IL-1# in patients with
CHB treated with Peg-IFN# combined with tenofovir (TDF) and monotherapy. The results
showed that TDF combination with Peg-IFN# expressed higher IL-1# and inhibited HBV more
effectively than monotherapy in vitro. The increase of serum IL-1# level may improve the
antiviral efficacy of NAs combination with Peg-IFN-#. This may provide a new therapeutic
tactic for patients with CHB, especially for those patients who can not respond well to antiviral
therapy.
Question:
There are several lexical repetition and grammatical mistakes in the text. Please revise and
correct them carefully.
Review for 10.1186/s12876-023-02812-5 (2023)

Title: The expression of interleukin-1# in patients with chronic hepatitis B treated with
Pegylated-interferon-# combined with tenofovir and monotherapy: analysis of 162 cases from
a single center
Version: 1 Date: 09 Mar 2023
Reviewer's report:
1.The language used in this article requires refinement.
2.The article needs to provide a clear explanation of the diagnostic criteria for patients with CHB.
3.Regarding the expression of IL-1# in Result 1, it is insufficient to rely solely on detecting
mRNA content. This is because an increase in mRNA level does not always translate to a
corresponding increase in protein level. Therefore, it is necessary to supplement with ELISA
assay to detect protein content in the cell supernatant.
4.To enhance the logical coherence of the article, the author should include an explanation of
the changes in HBV protein levels following treatment of HBV-infected liver cells with IL-1#,
in order to illustrate the potential antiviral activity of IL-1#.
Review for 10.1186/s12876-023-02804-5 (2023)

Title: Combination of Neutrophil/Lymphocyte Ratio and Albumin/Bilirubin Grade as a
Prognostic Predictor for Hepatocellular Carcinoma Patients Undergoing Curative Hepatectomy
Version: 2 Date: 02 Mar 2023
Reviewer:  Takayuki Shimizu
Reviewer's report:
The authors developed new prognostic score for patients with HCC. This prognostic score
combined tumor behavior with liver functional assessment. This score clearly stratified survival
curve in patients with HCC. Multivariate Cox regression analysis revealed this score was
independent prognostic variable. However, the result section had unnecessary sentences and
Tables, and the discussion section should be revised because your consideration and discussion
is not enough.
In method section, Graphpad software is not the production from IBM.
In result section, Table1, Table2 and Table3 is not necessary because I think the authors show
only the association of NLR-ALBI score with clinicopathological features in HCC patients.
The authors should delete the sentences of “The association of the per-operative NLR with the
clinicopathological features of HCC.” and “The association of the per-operative ALBI with the
clinicopathological features of HCC.”, Table 1, Table 2 and Table 3.
In first paragraph of discussion section, I have no idea why the authors mentioned about
diagnosis and economic burden of HCC. These contents should be written in Introduction
section. Is there any association of HCC diagnosis and economic burden with NLR-ALBI score?
Anyway, the authors delete this first paragraph. The authors should mention the brief summary
of result in first paragraph of discussion section.
In third paragraph of discussion section, the author should refer to the reference as following
sentence; In a systemic review that included 20 studies with 11365 patients, Geng and his
colleagues concluded that higher ALBI was associated with poorer OS.
In forth paragraph of discussion section, the authors revise the following term from “per-
operative” to “pre-operative”.
Do you think how does your new prognostic NLR-ALBI score apply to clinical practice? Is this
new score useful for early intervention of adjuvant therapy or nutritional therapy, evacuation of
invasive surgery? You should consider how does NLR-ALBI score apply to clinical practice in
order to improve patients outcome, and mention your consideration in discussion section.
Review for 10.1186/s12876-023-02804-5 (2023)

Title: Combination of Neutrophil/Lymphocyte Ratio and Albumin/Bilirubin Grade as a
Prognostic Predictor for Hepatocellular Carcinoma Patients Undergoing Curative Hepatectomy
Version: 2 Date: 07 Mar 2023
Reviewer's report:
The authors explored some common inflammation-related markers vut there are also other
markers, for example lymphocyte/monocyte ratio. Could the authors comment on this?
How did the authors validated the model? The authors could try an internal validation (the
authors could at least comment and cite an example of this validation like in the paper PMID:
27005802)
How the cut-off for these values were chosen?
Review for 10.1186/s12876-023-02804-5 (2023)

Title: Combination of Neutrophil/Lymphocyte Ratio and Albumin/Bilirubin Grade as a
Prognostic Predictor for Hepatocellular Carcinoma Patients Undergoing Curative Hepatectomy
Version: 4 Date: 23 Apr 2023
Reviewer's report:
The revised version is OK. Thank you!
Review for 10.1186/s12876-023-02794-4 (2023)

Title: Clinical Characteristics and Management of Patients with Nonalcoholic Steatohepatitis
in a Real-World Setting: Analysis of the Ipsos NASH Therapy Monitor Database
Version: 2 Date: 13 Jan 2023
Reviewer:  Harishankar Gopakumar
Reviewer's report:
Dear Authors,
It was a pleasure to read your work titled “Clinical Characteristics and Management of Patients
with Nonalcoholic Steatohepatitis in the Real-World Setting: Analysis of the Ipsos NASH
Therapy Monitor Database"
This is overall a well written study and I commend the authors on their very relevant work in the
field of NASH and NAFLD that is increasing prevalence globally. There is need for awareness
and ongoing education on the latest recommendations of diagnosis and management of NAFLD/
NASH in non-academic community practice and this study highlights this.
There are a few concerns that I have outlined below.
# 1
The authors find that the biopsy rates were broadly similar among PCPs, endocrinologists,
gastroenterologists, and hepatologists (72%-74% across all four diagnosing physician
specialties). This I find to be very different from what is "real-world". It is much more likely
that a primary care physician or endocrinologist would refer a patient to a gastroenterologist
or hepatologist for evaluation rather than ordering the liver biopsy themselves. As the authors
have mentioned, the liver biopsy rates in this study are also higher than what is usually reported.
The results of this study hence seem to not actually be a representation of real-world practice
of these specialists.
# 2
This study seems to reflect practice of physicians who manage NASH regularly given the high
percentage of liver biopsies and use of Vitamin E and Pioglitazone which are the two medications
that have been shown to reverse steatohepatitis (PIVENS Trial).
# 3
In sentence 287, the authors mention that vitamin E is the only drug "shown to have
any histological efficacy in randomized clinical trials". This is an inaccurate statement as
Pioglitazone was also shown to have histological efficacy with reduction in lobular inflammation
and steatosis as in PIVENS trial although it did not meet the primary endpoint.
# 4
In keeping with the above, the readers, I believe would be curious to know what constitutes the
Ipsos NASH database and what patients/hospitals/physicians contribute to it.
# 5 The authors of this study conclude that physicians prescribed statins and vitamin E primarily
for weight loss. Statins have been in use for many decades now and its indications are well known
to most physicians. Patients with NAFLD and NASH frequently have coexisting metabolic
syndrome including hypercholesterolemia for which statins are often prescribed. Hence it will
be very important to clarify how this was ascertained that statins were prescribed primarily for
weight loss.
# 6
I am afraid this study also suffers from lack of novelty as the subject of knowledge gap and
the divergence of community practice from guidelines in NAFLD/NASH are previously studied
and published.
Review for 10.1186/s12876-023-02816-1 (2023)

Title: Diagnostic performance of the normal range of gastrin calculated using strict criteria
based on a combination of serum markers and pathological evaluation for detecting gastritis: a
retrospective study
Version: 0 Date: 06 Nov 2022
Reviewer's report:
This is a study investigating normal range of serum gastrin based on the strict criteria of
non-gastritis normal subjects. The study design, methods, results, and interpretation are good.
However, the presentation is not good. Abstract is also bad.
Major points
1. Tables 3 and 4 are inserted in the manuscript, but Tables 1 and 2 are added at the end of the
manuscript. In addition, Tables should be uploaded in comfortable format for readers because
the presented tables are not comfortable to see.
2. The purpose of the study is not described well in Introduction and the readers cannot
understand the purpose until later. On the other hand, the readers finally understand the purpose
of the study when they read Discussion. Authors should move a lot of sentences in Discussion
to Introduction.
3. Abstract should be completely changed because it is very hard to understand the study.
4. Line 26-18: The meanings of the sentences are hard to understand.
5. Line 32: “populations” may be better changed to “groups”.
6. Line 169-170: “no gastritis in endoscopy” is not included in the table.
7. Line 226-228: This sentence is for endoscopy group, but the description is complicated. The
readers may misunderstand.
8. Line 232-233: there are no data about this sentence.
9. Line 233-234: PG I and II may be mistaken by each other.
10. Line 273: is “atrophic” necessary?
11. Line 309: “specificity” may be “sensitivity”.
12. Table 1: (G0/G1-3) should be explained.
13. Table 4: what is the cut-off value between high and low gastrin?
14. Supplementary figure 1: This figure is very hard to understand. Presentation should be
improved.
Review for 10.1186/s12876-023-02816-1 (2023)

Title: Diagnostic performance of the normal range of gastrin calculated using strict criteria
based on a combination of serum markers and pathological evaluation for detecting gastritis: a
retrospective study
Version: 0 Date: 08 Nov 2022
Reviewer's report:
I read with interest the paper on the diagnostic  performance of gastrin combined with other
serum markers for gastritis. The paper il well conducted on an impressive number of patients.
and clearly written.
I would suggest to included STARD guidelines in the Methods section.
No further comments.
Review for 10.1186/s12876-023-02816-1 (2023)

Title: Diagnostic performance of the normal range of gastrin calculated using strict criteria
based on a combination of serum markers and pathological evaluation for detecting gastritis: a
retrospective study
Version: 1 Date: 29 Nov 2022
Reviewer's report:
This is a study investigating normal range of serum gastrin based on the strict criteria of
non-gastritis normal subjects. The study design, methods, results, and interpretation are good.
Authors revised the manuscript as I pointed out at the previous review. Unfortunately, Englich
sentences, word selection and grammar are not good. The sentences are too complicated to
understand, and redundant. Simple is the best. Shorter is better. You should make simple
sentences in shorter manuscript for scientific paper. I recommend you ask an English editing
service to improve the sentences. You should read the manuscript again and again, and improve
the manuscript before re-submission.
Points for revision (Just examples)
1. Discussion looks better. On the other hand, Introduction is still bad. Sentences are not simple.
The sentences in the other parts are also bad. Authors should ask an English editing service
to improve the whole manuscript including the Figures. The sentences in the boxes in the
Supplementary figure are also bad.
2. Example, Line 78-83: Sentences are so complicated. I do not want to read such difficult
sentences. I would propose an example for the sentences: “When group A subjects were
endoscopically divided into two groups, the true-A group without endoscopic atrophy showed
extremely low carcinogenicity whereas the pseudo-A group with endoscopic atrophy showed
high carcinogenicity. So, it is important to take endoscopic findings into account in ABC
methods to discriminate true-A subjects from pseudo-A subjects in the assessment of gastric
cancer risk.”
3. I would delete most of the sentences in the line 84-93.
4. Line 94: What is GastroPanel? Authors should explain what it is.
5. The sentences in line 99-102 would be better deleted.
6. Line 135: ‘level’ is not adequate, I think. ‘concentration’ is better.
7. Line 140: ‘level’ is not needed. Unit has already been written.
8. Line 146-148: Explanation of ABC method should be written in Introduction because authors
have already described about ABC method in Introduction.
9. Line 187-194. There are a lot of uncomfortable words and sentences. These sentences should
be revised by English editing services. G0 should not be used in the manuscript. Grade 0 is
comfortable.
10. Above list is just an example. There are still a lot of uncomfortable parts.
Review for 10.1186/s12876-023-02816-1 (2023)

Title: Diagnostic performance of the normal range of gastrin calculated using strict criteria
based on a combination of serum markers and pathological evaluation for detecting gastritis: a
retrospective study
Version: 5 Date: 18 Feb 2023
Reviewer's report:
This is a study investigating normal range of serum gastrin based on the strict criteria of non-
gastritis normal subjects. The study design and methods are good. Authors revised manuscript
according to the advice of the reviewer, and the revised manuscript has much improved. It looks
perfect, but I think it needs some more revisions.
Points for revision
1. Authors raised a problem of the ABC method in which group A includes pseudo-A subjects. Is
the new cut-off value of gastrin possible to differentiate pseudo-A subjects from true-A subjects?
Authors may need some additional data to answer the problem, or make some more discussions
and revise the conclusions.
2. Authors only described good data (specificity and PPV) in the abstract. Sensitivity and other
indices should also be described.
3. Is ‘non-gastritis’ adequate? I think ‘normal stomach’ may be better, because ‘non-gastritis’
include some other pathological findings than gastritis, such as intestinal metaplasia and atrophy.
4. Supplementary table 2: What is ‘negative’ or ‘positive’ in the second line of the table? For
example, ‘normal’ and ‘non-normal’ may be better. The title of the table should also be changed
adequately.
5. This study also raised the normal values of pepsinogens. Authors can describe them or make
one more article.
6. Line 137: Supplementary Fig. 1 should be described. ‘Additional file’ may not be needed.
7. Figures and tables need adequate margins so that they could be printed completely.
8. A blank line should be added before ‘References’.
Review for 10.1186/s12876-023-02816-1 (2023)

Title: Diagnostic performance of the normal range of gastrin calculated using strict criteria
based on a combination of serum markers and pathological evaluation for detecting gastritis: a
retrospective study
Version: 6 Date: 01 Apr 2023
Reviewer's report:
This is a study investigating normal range of serum gastrin based on the strict criteria of non-
gastritis normal subjects. The study design and methods are good. Authors revised manuscript
according to the advice of the reviewer, and the revised manuscript has much improved again.
But I think it needs some more revisions again (I am very sad. I wanted to be freed.).
Points for revision
1. Line 181: C-0 was not described in the original Kimura-Takemoto’s paper. “Updated Kimura-
Takemoto classification” should be indicated in this manuscript and the reference should be
changed to the paper of Nakajima, et al. Dig Endosc 2021; 33: 125-132, which describes both
C-0 and C-1.
2. Line 278, 282 and others: ‘low gastrin’ is not adequate, but ‘normal gastrin’ is adequate. And
‘high proportion of true A patients’ is better changed to ‘higher proportion of true A patients
than high gastrin group’.
3. Line 296 and 53: ‘low’ to ‘normal’.
4. Line 335: ‘do have low’ to ‘do not have high’.
5. Table 4: ‘Low gastrin group’ to ‘normal gastrin group’.
6. All figures are too small if I printed. It is not comfortable for reviewers and readers. Authors
should change the layout of the figures according to the paper. For example, you can put the
paper from longitudinal to horizontal position, so that the figures and the words can be enlarged.
Authors should always consider reviewers when submission, so that the reviewers do not feel
uncomfortable to see the figures and tables when printing (I used a magnifying glass this time).
I pointed out many times about the presentation of figures and tables to you, but you did not.
7. Line 506: Title of the figure should be changed to ‘Number of subjects in the pathologically-
evaluated normal stomach group.’
8. Line 515: Before (b), a sentence should be inserted “The horizontal line indicates the cut-
off value, 126.03 pg/mL, which is the upper limit of the 95th percentile of the normal range of
serum gastrin concentrations calculated in the pathologically…”. Instead, the sentence of the
line 518-519 is deleted. And then, the legend of (b) is better changed to ‘Receiver operating
characteristic (ROC) curve with the cut-off value for detecting …’.
Review for 10.1186/s12876-023-02782-8 (2023)

Title: Severe Combined Immunodeficiency: Improved survival leading to detection of
underlying liver disease
Version: 3 Date: 20 Dec 2022
Reviewer's report:
- The title should be softened
- In abstract ULN should be referred to enzymes. The acronymus FIB-4 and NAFLD in the
abstract should be explained.
- In table 3 a coulumn indicating the indication should be added.
- Methods: hepatic panel: what does it include?
- Has enzyme replacement therapy never be correlated with increased liver enzymes?
- Maybe the correlation of the increase of enzymes with BMI could explain better than diagnosis
of ADA  the hepatic injury. It should be underlined in the discussion.
- DILI: for what drug? When? Features?
- Considered that the wide spectrum of the ADA deficiency phenotype is largely related to
the variability in genetic mutations and the amount of residual ADA enzyme activity, have the
authors analyzed a possble correlation with liver injury'