Reviewer's report
Title:TNF-alpha-induced up-regulation of pro-inflammatory cytokines is delayed
by phosphatidylcholine in intestinal epithelial cells
Version: 3Date:26 August 2008
Reviewer: Alexandr Parlesak
Reviewer's report:
This is an interesting study dealing with the mechanism leading to
down-regulation of intestinal inflammation by phosphatidylcholine (PC). The
authors applied PC with different fatty acids (FA) to two different cell lines. In
non-differentiated Caco-2 cells, they proved that PC – depending on FA
composition and pre-treatment time – delayed TNF-a-induced transcription of
genes for IL-8, ICAM-1, IP-10, MCP-1, TNF-a, and MMP1. They showed that this
effect depended on NFkB activity and that it was not due to inhibition of TNF-a
binding to its receptor. PC was also effective when applied to the apical side of
polarized Caco-2 cultures if cells were stimulated from the basolateral side.
Major compulsory revisions:
1) An important flaw of the study is that it is not clear at all which differences are
significant and which not. Therefore, the reader does not know whether PC had
an effect (meaning the PC treatment reduced production of the corresponding
mRNA or not) – despite that the authors are claiming that. Hence, all statements
on effects of PC in the Result section and the Discussion section are not
substantiated. The authors state that they tested differences with the test of
Kruskal-Wallis; however, this is a non-parametrical test indicating only
inhogeneity among more than two samples, meaning that the authors are not
able to say e. g. whether the MCP-1 mRNA production after 60 min is lower with
compared to without PC. Especially, if the authors include the negative controls
in their Kruskal-Wallis-test, Kruskal-Wallis indicates the significance of difference
between with and without TNF-a, but not that with and without PC!
If the authors wish to make such statements, they need to apply a post-hoc test
(e.g. that of Nemenyi), if they really want to apply this conservative
(non-parametric) way of evaluation, indicating clearly which differences are
significant (with P-values) and which one not. However, I would consider also the
application of a parametrical 2-way ANOVA for data (eventually after
log-transformation) from Figs. 5, 6, and 8 (time × PC vs. outcome) and Fig. 7
(orientation × PC vs. outcome) with an appropriate post-hoc test (e.g. Tukey) –
even considering the type of reading.
2) The Introduction lacks the working hypothesis of the current work.
3) The biological relevance needs to be pointed out more clearly: in some cases
the difference induced by PC after TNF-a challenge is only 20 transcripts/µl (e.g.
Fig. 8, MCP-1 after 60 min.), which is close to nothing and it is more than
questionable whether this has any biological significance.
4) Frequently there’s a difference between the effect of compounds on mRNA
formation and the release of the biologically effective protein. Therefore, an
ELISA should be performed showing for at least 2 of the cytokines/chemokines
the mRNA concentration of which was measured the same effect at protein level
(e. g. IL-8 and IP 10).
5) The authors are not stringent in their way of argumentation. In both the
Abstract and the Introduction, they state that PC might be effective as part of the
mucus and the PC-enhancing barrier function in preventing translocation of
inflammation-triggering compounds. This aspect is not regarded at all in the
Discussion, despite the fact that it was shown that PC also reduces
trans-epithelial activation of leukocytes without being able to reduce directly
bacteria-induced activation of human mononuclear leukocytes (sorry to bring in
here work from our group: Parlesak et al., Crit Care Med. 2007;35:2367-74).
Furthermore, the authors should comment on the finding that direct treatment of
bacteria-challenged mononuclear leukocytes with phosphatidylcholine does not
result in diminished TNF-a production (same publication).
6) Composition of the membrane can be crucial for activity of membrane-bound
kinases (Sando et al. Biochem J. 1996;317:583-8; Switzer et al. Lipids.
2004;39:1163-70; Siddiqui et al. Nutr Clin Pract. 2007;22:74-88). The important
aspect of microdomain modification in the cellular membrane and its implication
for TNFa-receptor signalling by PC should be regarded in the Discussion.
7) It does not become clear whether the authors think that PC is directly
interacting with NFkB (a presumption they have no proof for) or whether PC’s
effect occurs upstream of NFkB. The involvement of NFkB per se is not
surprising as TNF-a signals also by NFkB. Hence, if e.g. incorporation of PC into
the cellular membrane affects down-stream signalling of the TNF-a receptor
(without changing affinity to its ligand), this would also reduce NFkB activation
without direct PC-NFkB interaction. Hence, the authors need to be clearer about
what they mean with “… the inhibitory effect of PC seems to be regulated via the
NFkB-pathway”.
Minor essential revisions:
8) Too many references were regarded in the introduction. E.g., it is sufficient to
give 2 instead of 4 refs. on the genetic susceptibility in IBD (refs. 3-6), 2-3
references on the role of chemokines in IBD instead of 9 (refs. 15-23), one
instead of 3 on the role of TNF-a in IBD (26-28).
9) Too many charts are regarded in the figures; it would be good to omit those
where no significant difference occurs (e.g. those in Figure 5b, presumably also
those in Fig. 6 for ICAM-1 and IP-10).
10) It is not clear how the authors obtained radiolabeled PC.
11) As cDNA is not a liquid, its unit should not be given in µl.
12) Explanations for the following abbreviation “PE” is missing.
13) Occasionally, the authors used the word ’like’ instead of ‘such as’ (e.g.
legend of Figure 5) and, occasionally, subjects and verbs are not fitting together
(singular/plural mismatch). This should be changed. In general, the manuscript
needs some language corrections before being published.
Declaration of competing interests:
I declare that I have no competing interests.
Reviewer's report
Title:TNF-alpha-induced up-regulation of pro-inflammatory cytokines is delayed
by phosphatidylcholine in intestinal epithelial cells
Version: 3Date:26 August 2008
Reviewer: Alexandr Parlesak
Reviewer's report:
This is an interesting study dealing with the mechanism leading to
down-regulation of intestinal inflammation by phosphatidylcholine (PC). The
authors applied PC with different fatty acids (FA) to two different cell lines. In
non-differentiated Caco-2 cells, they proved that PC – depending on FA
composition and pre-treatment time – delayed TNF-a-induced transcription of
genes for IL-8, ICAM-1, IP-10, MCP-1, TNF-a, and MMP1. They showed that this
effect depended on NFkB activity and that it was not due to inhibition of TNF-a
binding to its receptor. PC was also effective when applied to the apical side of
polarized Caco-2 cultures if cells were stimulated from the basolateral side.
Major compulsory revisions:
1) An important flaw of the study is that it is not clear at all which differences are
significant and which not. Therefore, the reader does not know whether PC had
an effect (meaning the PC treatment reduced production of the corresponding
mRNA or not) – despite that the authors are claiming that. Hence, all statements
on effects of PC in the Result section and the Discussion section are not
substantiated. The authors state that they tested differences with the test of
Kruskal-Wallis; however, this is a non-parametrical test indicating only
inhogeneity among more than two samples, meaning that the authors are not
able to say e. g. whether the MCP-1 mRNA production after 60 min is lower with
compared to without PC. Especially, if the authors include the negative controls
in their Kruskal-Wallis-test, Kruskal-Wallis indicates the significance of difference
between with and without TNF-a, but not that with and without PC!
If the authors wish to make such statements, they need to apply a post-hoc test
(e.g. that of Nemenyi), if they really want to apply this conservative
(non-parametric) way of evaluation, indicating clearly which differences are
significant (with P-values) and which one not. However, I would consider also the
application of a parametrical 2-way ANOVA for data (eventually after
log-transformation) from Figs. 5, 6, and 8 (time × PC vs. outcome) and Fig. 7
(orientation × PC vs. outcome) with an appropriate post-hoc test (e.g. Tukey) –
even considering the type of reading.
2) The Introduction lacks the working hypothesis of the current work.
3) The biological relevance needs to be pointed out more clearly: in some cases
the difference induced by PC after TNF-a challenge is only 20 transcripts/µl (e.g.
Fig. 8, MCP-1 after 60 min.), which is close to nothing and it is more than
questionable whether this has any biological significance.
4) Frequently there’s a difference between the effect of compounds on mRNA
formation and the release of the biologically effective protein. Therefore, an
ELISA should be performed showing for at least 2 of the cytokines/chemokines
the mRNA concentration of which was measured the same effect at protein level
(e. g. IL-8 and IP 10).
5) The authors are not stringent in their way of argumentation. In both the
Abstract and the Introduction, they state that PC might be effective as part of the
mucus and the PC-enhancing barrier function in preventing translocation of
inflammation-triggering compounds. This aspect is not regarded at all in the
Discussion, despite the fact that it was shown that PC also reduces
trans-epithelial activation of leukocytes without being able to reduce directly
bacteria-induced activation of human mononuclear leukocytes (sorry to bring in
here work from our group: Parlesak et al., Crit Care Med. 2007;35:2367-74).
Furthermore, the authors should comment on the finding that direct treatment of
bacteria-challenged mononuclear leukocytes with phosphatidylcholine does not
result in diminished TNF-a production (same publication).
6) Composition of the membrane can be crucial for activity of membrane-bound
kinases (Sando et al. Biochem J. 1996;317:583-8; Switzer et al. Lipids.
2004;39:1163-70; Siddiqui et al. Nutr Clin Pract. 2007;22:74-88). The important
aspect of microdomain modification in the cellular membrane and its implication
for TNFa-receptor signalling by PC should be regarded in the Discussion.
7) It does not become clear whether the authors think that PC is directly
interacting with NFkB (a presumption they have no proof for) or whether PC’s
effect occurs upstream of NFkB. The involvement of NFkB per se is not
surprising as TNF-a signals also by NFkB. Hence, if e.g. incorporation of PC into
the cellular membrane affects down-stream signalling of the TNF-a receptor
(without changing affinity to its ligand), this would also reduce NFkB activation
without direct PC-NFkB interaction. Hence, the authors need to be clearer about
what they mean with “… the inhibitory effect of PC seems to be regulated via the
NFkB-pathway”.
Minor essential revisions:
8) Too many references were regarded in the introduction. E.g., it is sufficient to
give 2 instead of 4 refs. on the genetic susceptibility in IBD (refs. 3-6), 2-3
references on the role of chemokines in IBD instead of 9 (refs. 15-23), one
instead of 3 on the role of TNF-a in IBD (26-28).
9) Too many charts are regarded in the figures; it would be good to omit those
where no significant difference occurs (e.g. those in Figure 5b, presumably also
those in Fig. 6 for ICAM-1 and IP-10).
10) It is not clear how the authors obtained radiolabeled PC.
11) As cDNA is not a liquid, its unit should not be given in µl.
12) Explanations for the following abbreviation “PE” is missing.
13) Occasionally, the authors used the word ’like’ instead of ‘such as’ (e.g.
legend of Figure 5) and, occasionally, subjects and verbs are not fitting together
(singular/plural mismatch). This should be changed. In general, the manuscript
needs some language corrections before being published.
Declaration of competing interests:
I declare that I have no competing interests.
Please review this paper.
user
Reviewer's report
Title:TNF-alpha-induced up-regulation of pro-inflammatory cytokines is delayed
by phosphatidylcholine in intestinal epithelial cells
Version: 3Date:26 August 2008
Reviewer: Alexandr Parlesak
Reviewer's report:
This is an interesting study dealing with the mechanism leading to
down-regulation of intestinal inflammation by phosphatidylcholine (PC). The
authors applied PC with different fatty acids (FA) to two different cell lines. In
non-differentiated Caco-2 cells, they proved that PC – depending on FA
composition and pre-treatment time – delayed TNF-a-induced transcription of
genes for IL-8, ICAM-1, IP-10, MCP-1, TNF-a, and MMP1. They showed that this
effect depended on NFkB activity and that it was not due to inhibition of TNF-a
binding to its receptor. PC was also effective when applied to the apical side of
polarized Caco-2 cultures if cells were stimulated from the basolateral side.
Major compulsory revisions:
1) An important flaw of the study is that it is not clear at all which differences are
significant and which not. Therefore, the reader does not know whether PC had
an effect (meaning the PC treatment reduced production of the corresponding
mRNA or not) – despite that the authors are claiming that. Hence, all statements
on effects of PC in the Result section and the Discussion section are not
substantiated. The authors state that they tested differences with the test of
Kruskal-Wallis; however, this is a non-parametrical test indicating only
inhogeneity among more than two samples, meaning that the authors are not
able to say e. g. whether the MCP-1 mRNA production after 60 min is lower with
compared to without PC. Especially, if the authors include the negative controls
in their Kruskal-Wallis-test, Kruskal-Wallis indicates the significance of difference
between with and without TNF-a, but not that with and without PC!
If the authors wish to make such statements, they need to apply a post-hoc test
(e.g. that of Nemenyi), if they really want to apply this conservative
(non-parametric) way of evaluation, indicating clearly which differences are
significant (with P-values) and which one not. However, I would consider also the
application of a parametrical 2-way ANOVA for data (eventually after
log-transformation) from Figs. 5, 6, and 8 (time × PC vs. outcome) and Fig. 7
(orientation × PC vs. outcome) with an appropriate post-hoc test (e.g. Tukey) –
even considering the type of reading.
2) The Introduction lacks the working hypothesis of the current work.
3) The biological relevance needs to be pointed out more clearly: in some cases
the difference induced by PC after TNF-a challenge is only 20 transcripts/µl (e.g.
Fig. 8, MCP-1 after 60 min.), which is close to nothing and it is more than
questionable whether this has any biological significance.
4) Frequently there’s a difference between the effect of compounds on mRNA
formation and the release of the biologically effective protein. Therefore, an
ELISA should be performed showing for at least 2 of the cytokines/chemokines
the mRNA concentration of which was measured the same effect at protein level
(e. g. IL-8 and IP 10).
5) The authors are not stringent in their way of argumentation. In both the
Abstract and the Introduction, they state that PC might be effective as part of the
mucus and the PC-enhancing barrier function in preventing translocation of
inflammation-triggering compounds. This aspect is not regarded at all in the
Discussion, despite the fact that it was shown that PC also reduces
trans-epithelial activation of leukocytes without being able to reduce directly
bacteria-induced activation of human mononuclear leukocytes (sorry to bring in
here work from our group: Parlesak et al., Crit Care Med. 2007;35:2367-74).
Furthermore, the authors should comment on the finding that direct treatment of
bacteria-challenged mononuclear leukocytes with phosphatidylcholine does not
result in diminished TNF-a production (same publication).
6) Composition of the membrane can be crucial for activity of membrane-bound
kinases (Sando et al. Biochem J. 1996;317:583-8; Switzer et al. Lipids.
2004;39:1163-70; Siddiqui et al. Nutr Clin Pract. 2007;22:74-88). The important
aspect of microdomain modification in the cellular membrane and its implication
for TNFa-receptor signalling by PC should be regarded in the Discussion.
7) It does not become clear whether the authors think that PC is directly
interacting with NFkB (a presumption they have no proof for) or whether PC’s
effect occurs upstream of NFkB. The involvement of NFkB per se is not
surprising as TNF-a signals also by NFkB. Hence, if e.g. incorporation of PC into
the cellular membrane affects down-stream signalling of the TNF-a receptor
(without changing affinity to its ligand), this would also reduce NFkB activation
without direct PC-NFkB interaction. Hence, the authors need to be clearer about
what they mean with “… the inhibitory effect of PC seems to be regulated via the
NFkB-pathway”.
Minor essential revisions:
8) Too many references were regarded in the introduction. E.g., it is sufficient to
give 2 instead of 4 refs. on the genetic susceptibility in IBD (refs. 3-6), 2-3
references on the role of chemokines in IBD instead of 9 (refs. 15-23), one
instead of 3 on the role of TNF-a in IBD (26-28).
9) Too many charts are regarded in the figures; it would be good to omit those
where no significant difference occurs (e.g. those in Figure 5b, presumably also
those in Fig. 6 for ICAM-1 and IP-10).
10) It is not clear how the authors obtained radiolabeled PC.
11) As cDNA is not a liquid, its unit should not be given in µl.
12) Explanations for the following abbreviation “PE” is missing.
13) Occasionally, the authors used the word ’like’ instead of ‘such as’ (e.g.
legend of Figure 5) and, occasionally, subjects and verbs are not fitting together
(singular/plural mismatch). This should be changed. In general, the manuscript
needs some language corrections before being published.
Declaration of competing interests:
I declare that I have no competing interests.
assistant