Peer review of: Chronic activation of endothelial MAPK disrupts hematopoiesis via NFKB dependent (2020)

Reviewers' comments: 

Reviewer #1, expert in inflammatory signaling in hematopoiesis (Remarks to the Author): 

In their manuscript, Ramalingam et al. describe the consequences of deregulated MAPK signaling in 
the maintenance of endothelial niche. In particular, they suggest that defective MAPK signaling leads 
to activation of the canonical NF-KB pathway mediated inflammatory signals and that these signals are 
responsible for defective HSC functions and hematopoiesis in their mouse model. 
Overall, these studies are fairly well performed and there are some interesting observations reported 
in their manuscript. However, there are many serious (both conceptual and technical) concerns that 
need to be addressed. A few of them are highlighted below; 

1. The novelty and significance of their findings are unclear. As pointed out by the authors in pages 3 
& 4, NFKB and MAPK are well known candidates to control inflammatory responses in endothelial cells; 
a previous report (Poulos, Nature communications, 2016) from the same group established (through a 
loss of function approach) that Endothelial specific inhibition of NF-KB led to increased HSC functions 
due to a decrease in pro-inflammatory cytokines; and another report by the same group already 
demonstrated that endothelial MAPK activation drives myeloid-biased differentiation of HSCs, at the 
expense of self-renewal possibly due to inflammation. The current study essentially recapitulates all 
their previous findings, although with a slightly different approach and model system. 

2. The authors repeatedly discuss about BM niche/endothelial niche and HSC maintenance/functions, 
but surprisingly they do not show any documentation on the actual “BM/HSC niche status” in the 
CDH5-MAPK mice. They should perform sections on the BM and perform microscopy to demonstrate 
that the vascular niche and HSC interactions are disturbed in their model. 

3. The HSPC characterization in figure 1 is far from complete. It is surprising that they make large 
claims without providing the immunophenotype of the “true” HSCs. They show highly reduced HSCPs 
(LSK cells), but they have not provided data on distinct HSPC subsets; LT-HSC, ST-HSCS, MPP2, MPP3 
& MPP4. Are there specific changes on these distinct subsets ? are there changes in relative numbers 
vs. absolute numbers of these fractions. Without all these critical information, it is very difficult to 
make any claims on HSCs. 

4. The western blot data shown in Figure 2 are not convincing. Have they performed any densitometry 
quantifications of these images ? Is this statistically significant ? Also, it is quite difficult to conceive 
that only a modest increase of phospho-ERK caused all these changes. Do the authors believe that 
ERK is the only MAPK target in their model, have they looked at other MAPK members ? 

5. Similarly, the phospho- p65 data are not convincing. As mentioned above, no 
quantification/statistical data were given. Moreover, a critical analysis of p65 blots suggests that the 
phosphorylation of p65 may not be increased in CDH5-MAPK mice. This is because the total levels of 
pan-p65 were increased in the CDH5-MAPK mice (or even total protein levels were increased, as 
tubulin levels were slightly higher). Moreover, the authors make a strong claim that increased 
(canonical) NFKB activation was observed in their model. However, all they show to justify their claims 
was a simple western blot on p65, which is questionable. To substantiate their claim that canonical 
NFKB is hyperactivated, the authors should really show Phospho-IKB and IkB degradation assays and 
p65 translocation to the nucleus. Again, without the statistical data and with all these indicated 
caveats, it is impossible to make proper sense of these presented data. 

6. In figure 4a-d, the authors show data on ROS levels, quiescence and apoptosis. Again, all these 
experiments were performed with mixed bag of (LSK) cells. It is unclear if any of these inferences can 
be attributed to the “true” HSCs, especially in view of the fact that LT-HSCs are only ~10 % of LSK. 
Moreover, it is of a major concern that they show that ~ 90% of the LSK cells of control and IkB mice 
are in G0 phase. This is totally unacceptable and certainly there are some obvious technical issues 

associated with this analysis. According to the current understanding on HSC biology, on an average 
only 20-30% of the LSK cells will remain quiescent under steady state conditions (Wilson, Cell,2008). 
Among the LSK cells the true quiescent LT-HSCs (lin−Sca1+cKit+CD150+CD48−CD34− ) are the only 
fraction that remains quiescent (~ 70%), but this fraction is < 5 % of the LSK. So, their data on 
quiescence cannot be considered. 

7. The manuscript lacks any molecular insights. While they do provide many isolated observations on 
hematopoiesis, NFKB signals, hypoxia and the role of SCGF in the model. However, no attempt was 
made to connect all these observations and make sense of them. In particular, they talk about 
hypoxia but they have not provided insights on the role of hypoxia (if any) in the HSC phenotype. 
Does hypoxia affect any physiological properties of HSCs, in other words what are the functional 
consequences of hypoxia ? Moreover, what are the actual or proposed mechanisms through which 
SCGF influences the phenotype ? 

8. Along the lines mentioned above, the gating strategy for CMPs, GMPs and MEPs are inappropriate. 
The field has convincingly shown by many groups and different technologies, that true common 
myeloid progenitors cannot be sorted accurately by Akashi et al. 2000 Nature. The described CMP 
population is a mixture of pre-GMPs and pre-MEPs that are already restricted to GM or MekE. The 
authors should adopt the accepted immunophenotyping strategy (Pronk et al. Cell Stem Cell 2007 and 
Rieger et al. 2008 Brit J Haematol.). 

9. The authors performed their studies based on VE-Cadherin-Cre and Tie2-Cre mouse strains. Even 
though cre expression in these strains is largely specific to endothelial lineage cells, there are reports 
that both these strains may have “leakiness” in the hematopoietic lineage cells. It is unclear if the 
authors have taken these observations into consideration while interpreting their data. Are the authors 
convinced that the Cre deleters used in their studies are perfect? Did they cross their cre lines with 
Rosa26 reporter mice and study the deletion efficiencies in endothelial vs. hematopoietic lineages. In 
the absence of such data it is unclear if their phenotype is exclusively caused by HSC extrinsic 
mechanisms. The should have performed reciprocal BMT (injecting WT bone marrow cells into CDH5 
MAPK mice) studies to prove that the phenotype is exclusively mediated by endothelial cells. 

Reviewer #2, expert in HSC niche biology (Remarks to the Author): 

This is an interesting report from Ramalingam et al. in which the authors show that activation of MAPK 
signaling in BM ECs induces inflammatory pathway activation in the hematopoietic compartment and 
suppression of NFkB signaling in endothelial cells restores niche integrity and hematopoietic function. 
The authors further identify stem cell growth factor alpha as a soluble factor that suppresses BM 
inflammation and restores hematopoietic function. The manuscript includes some interesting findings 
that would be of interest to the field, but I have some concerns regarding the experimental approach 
and conclusions that, if addressed, can improve the manuscript: 

1. The authors utilized tamoxifen – impregnated feed to induce MAPK activation in endothelial cells 
and then describe the effects of this intervention on bone marrow cellularity, etc. Did the authors 
verify the increase in MAPK signaling in VEcadherin+ ECs? This should be shown. 

2. Figure 1. In the competitive repopulation assay, the cell doses in the donor and competitor grafts 
should be stated in the main text or figure legend. Was this a 1:1 dilution? Were secondary 
transplants performed to assess long-term HSC defects? 
In Figure 1e, the data appear to show the contribution of donor cells within each lineage population, 

as opposed to the absolute percentages of donor+myeloid cells, donor+ T cells, donor+ B cells, etc. in 
recipient mice. Is the myeloid biased engraftment also evident when the absolute percentages of 
donor lineage+ cells are compared? Also, if the CDH5-MAPK mouse produces myeloid – biased 
engraftment after transplantation, why don’t the CFCs from the BM of CDH5-MAPK mice (Figure 1c) 
show increased myeloid progenitor cells compared to littermate controls? 

Figure 1g. A p value of 0.0479 would appear to approximate p = 0.05 or non-significance. Does this 
mean that the difference in the limiting dilution analysis is relatively weak or requires more replicates 
to confirm a statistically significant difference? Usually, limiting dilution assays to estimate HSC 
frequency are evaluated using Poisson Statistical Analysis. Was this approach utilized here? 

Figure 1k. The immunofluorescent images of the BM vasculature suggest an impressive difference in 
response to enforced MAPK signaling in ECs. What is the time point of analysis of the mice following 
MAPK induction in ECs? Is this change in BM vascular appearance persistent over time or does it 
resolve or worsen over time? 

3. Figure 2. In Figure 2d, the authors describe crossing CDH5-MAPK mice with Tie2.IkB-SS mice to 
generate CDH5-MAPK::IkB mice to evaluate whether suppression of endothelial NF-kB signaling 
downstream of endothelial MAPK activation could temporize BM inflammation observed in CDH5-MAPK 
mice. Tie2 is expressed in the majority of hematopoietic cell lineages (Genesis 2010;48:563-7) so the 
Tie2.IkB-SS mice would suppress NF-kB signaling in Tie2+ hematopoietic cells and endothelial cells. 
How does this cross allow for specific conclusions to be drawn about suppression of endothelial-
specific NF-kB signaling suppression? 

4. Figure 3. As stated above, the authors should explain how the CDH5-MAPK mice show decreased 
myeloid colony formation, whereas CDH5-MAPK::IkB mice show restoration of myeloid colony 
formation (Figure 3c); following competitive transplantation, the opposite effect is observed, with 
increased myeloid repopulation in the recipients of CDH5-MAPK donor cells and restoration of normal 
lineage distribution in recipients of CDH5-MAPK::IkB mice (Figure 3e). These results appear to be at 
odds with each other. 

Figure 3i. The differences in hematologic parameters shown in this panel are interesting, but it would 
be helpful to know whether neutrophil counts are also significantly different in the CDH5-MAPK mice 
versus controls and corrected with CDH5-MAPK::IkB mice. This would be much more relevant than 
RBC counts which are largely irrelevant clinically. 

My larger concern, as stated above, relates to the Tie2 IkB mouse model and whether it can allow 
discrimination of effects on endothelial cells versus hematopoietic cell effects. Would it be possible to 
validate the findings from the CDH5-MAPK::IkB mice using an endothelial – specific model in which 
NFkB signaling is suppressed? 

5. Figure 4. Could the absence of differences in ROS levels in BM ECs be a function of the possibility 
that Tie2 – driven suppression of NFkB signaling is primarily occurring in hematopoietic cells, rather 
than in the vascular compartment in these mice? 

In Figure 4, the authors transition into analysis of BM stromal cells for evidence of alteration in ROS 
levels, cell cycling and apoptosis. It is unclear or not well justified or explained why the authors chose 
to focus additionally on BM stromal cells as well as endothelial cells and HSPCs. Do the authors 
postulate that suppression of NFkB signaling in ECs alters cross-talk between ECs and stromal cells 
such that BM stromal cell function is altered? Do the authors have any insight mechanistically as to 
how this communication between ECs and stromal cells is occurring? 

In Figure 4n-p, the authors show that expression of Il1b and Csf1 is decreased in CD45+ cells, but 
only Il1b is decreased in BM ECs and stromal cells. If Il1b and Csf1 are both involved in mediating the 

effects of MAPK activation in BM ECs on hematopoiesis, how do the authors explain these differences? 

6. Figure 5. The authors show that delivery of SCGF reverses the hematopoietic and BM vascular 
defects in CDH5-MAPK mice by suppression of BM inflammation driven by MAPK activation in BM ECs. 
Are the differences in gene expression of target genes shown in Figure 5i significant? Were these 
analyses repeated more than once to validate the original results? Significant differences should be 
indicated clearly in the Figure. 

It is unclear mechanistically exactly how SCGF suppresses BM inflammation driven by BM EC MAPK 
activation. How does increased NFkB signaling in ECs downregulate SCGF expression in BM stromal 
cells since BM stromal cells are the primary source of SCGF in the BM (extended Figure 7)? Does SCGF 
act directly on HSPCs and also directly on BM ECs and/or stromal cells or do indirect effects occur on 
these populations in response to SCGF infusion? 

7. Figure 6. Interesting results are shown to indicate that infusion of SCGF improves hematologic 
recovery following irradiation. Did SCGF accelerate recovery neutrophils in irradiated mice? This would 
be the most clinically interesting result, since neutrophil counts dictate need for hospitalization and 
risk of bacterial infections. 

If SCGF infusions do not increase numbers of phenotypic HSPCs in wild type mice following irradiation 
(6d), how do the authors explain the significant enhancement in recovery of cells capable of 
competitive repopulation as shown in Figure 6e? 

Minor Concern 
Page 14, bottom paragraph: Several other publications have characterized the effects of 
myelosuppressive injury on the BM vasculature and BM vascular function beyond Hooper et al., and 
these references should be appropriately cited. 

Reviewer #3, expert in HSC repoulation (Remarks to the Author): 

Endothelial MAPK activation disrupts hematopoiesis by including NFkappaB dependent inflammatory 
stress by Ramalingam et al. 
The role of chronic inflammatory signals in the bone marrow niche for hematopoiesis is still 
controversially discussed. The authors demonstrate that constitutive expression of MAPK in endothelial 
cells perturbs hematopoiesis. This correlates with an overall inflammatory signature in stroma as well 
as hematopoietic cells (NFkappaB) and inflammatory signatures. Genetic inhibition of NFkappaB 
signaling restores normal function in the model system. Mechanistically, that also restores hypoxia in 
the bone marrow to normal levels of hypoxia, but not ROS, as ROS is not induced by elevated MAPK in 
endothelial cells. The authors further identify SCGF as a target cytokine that mediates the negative 
effect of MAPK activation as well as myelosuppressive treatment in endothelial cells on hematopoiesis. 
This is an overall interesting study with a number of very novel findings including mechanisms that will 
contribute to the field. 

There are though a couple of concerns that should/need to be addressed: 
Major: 
The authors need to confirm the level of activation of MAPK in endothelial cells in their animal model 
system. That information is not provided. All cells? Level of activation etc.? 

The Tie2 promoter can be leaky and also be expressed in HSCs/hematopoietic cells. 
The authors need to test the level of expression of the transgene in hematopoietic cells and especially 
HSCs. It looks like that has not been tested yet, also not in the previous publications with that mouse. 
That needs to be provided, as worst case, the data would require a strong re-interpretation of the 

results. 

The link between activation of MAPK in endothelial cells and the overall strong inflammatory signature 
in the whole bone marrow, including hematopoietic cells, is not determined to a great extend. There 
should be more emphasis on that point, especially as 2d, e and g show very similar overall activation 
patterns. 

Minor: 
Hypoxia in bone marrow is notoriously difficult to determine. The authors need to provide gating 
information etc. on these analyses, especially as the data are central for the conclusions. 

The hematopoietic phenotype is complex, and due to the overall broad changes in the bone marrow, 
multiple cells type might be the target of the changes and contribute to the observed changes. For 
example, a 5 day treatment that results in such a large overall changes in hematopoiesis needs to 
target a broad range of distinct type of hematopoietic cells. That should be addressed/discussed in 
more detail. 

Page11: The data does not show that the defects in hematopoiesis are a direct effect of inflammation-
induced alterations in ROS and hypoxia. That is a correlation.