Peer review of: Caveolin-1-mediated sphingolipid oncometabolism underlies a metabolic vulnerability of (2020)

Reviewers' comments: 

 

Reviewer #1 (Remarks to the Author): 

 

This manuscript reports the association between plasma sphingolipid profile and disease progression 
in low risk localized prostate cancer, and attempts to link this observation to a targetable biology in 
the cancer cells involving scavenging and metabolism of extracellular sphingolipids. The manuscript 
features some interesting lipidomic profiling and sphingolipid biochemistry, but is ultimately limited 
by several experimental concerns and the use of laboratory models that poorly recapitulate clinical 
disease, particularly for early stage localized prostate cancer which is the relevant patient group in 
active surveillance cohorts. 

 

The cell line models used in this manuscript are not typical of active surveillance patients or indeed 
most clinical prostate tumors. The only lines that express CAV1 are PC-3, RM9 and DU145, all of 
which are androgen receptor negative and reflect a very small proportion of very advanced or 
neuroendocrine prostate tumors. Virtually all early stage and low risk primary tumors express the 
androgen receptor and all of the AR-positive cell lines here (and seemingly most clinical tumor 
epithelium on Protein atlas) appear to express little to no CAV1, which casts some doubt on the 
mechanistic links being drawn by the authors between the plasma and cancer cell data. 

 

Major comments: 

 

1. Lipidomics data is not quantitative in this manuscript but rather expressed as HRs relative to 
historical plasma values- this is not explained. Can the authors please provide further information 
about how specific metabolites/lipids were identified and which standards were used? Was any 
interference from the presence of EDTA and/or age of the plasma samples evident in the samples 
detected for metabolomics? Were the plasma samples from fasted individuals? 

 

2. I have a concern over some of the clinical terminology used in the manuscript- when considering 
upgrading in an active surveillance cohort, this should not be described as aggressive versus indolent 
prostate cancer. There is a wealth of evidence that the vast majority of even those men experiencing 
upgrading or other measures of disease progression will not ultimately develop clinical metastases 
or die from prostate cancer. Even biochemical relapse following prostatectomy has been shown to 
be a poor surrogate for overall survival. This aspect of the manuscript and its title needs to be 
described more accurately, and the results interpreted with this in mind- the signatures found are 
really prognostic for disease progression at best, not aggressive disease. 

 

3. Please justify the 25%:75% cutpoint for the Kaplan-Meier survival curve in Figure 1B. Importantly, 
when considering an active surveillance cohort, “Survival probability” in this context (Y-axis) is 
misleading and should more clearly relate to disease progression or upgrading. Figure 1C is not well 
explained in the text and it is not evident why pathways involved in sphingolipid metabolism were 
not included considering the focus of the rest of Figure 1. Can the authors please also include a 
figure presenting the absolute expression data for CAV1 in the TCGA samples rather than relative 
levels? Alternatively IHC staining data from their own cohorts. This is critical to support the link 
between the plasma data and the mechanistic data in the rest of the manuscript. My quick 
impression is that the abundance is rather low in most localized tumor samples. 

 

4. For all of the CAV1 overexpression (LNCaP) and knockdown (PC-3) data in the manuscript, the 
degree of overexpression or knockdown is not shown anywhere in the manuscript, figures, legends 
or Supplemental data. This is unacceptable and needs to be included for all major experiments. 

 

5. Figure 2E lacks clarity and could be annotated to emphasize the main points regarding the 
biochemical pathways being highlighted by the authors. 

 

6. Figure 3: CAV1 staining should be included in all of these experiments to show the extent and 
efficiency of knockdown in the cell populations shown- particularly important when highlighting 
individual cells. This may also underpin the fact that there appear to be differences in the 
appearance of the mitochondria in the PC-3M cells in panel A versus Panel C. 

 

7. Figure 4: How does the total number of EVs change in response to altering CAV1 levels? 

 

8. Figure 6: There is no information in the manuscript or figure legends regarding the numbers of 
mice used in the experiments. The IHC data on single tumors is inadequate in the absence of any 
quantitative data on the remainder of the mice in the study. It is not evident whether the effects of 
eliglustat on tumor growth are due to systemic effects versus a targeted effect on the tumors- was 
any toxicity noted? A parallel experiment to confirm this using stable knockdown of CAV1 in the RM9 
cells would help distinguish between these two mechanisms. 

 

Minor comments: 

 

1. Certain figures within the manuscript lack clarity or are illegible. Please consider increasing font 
sizes and image quality for Fig 1B, 2E, 5B at a minimum. 

 

 

 

Reviewer #2 (Remarks to the Author): 

 

The authors of the manuscript entitled “Cav-1-Mediated Sphingolipid Oncometabolism Underlies a 
Metabolic Vulnerability of Aggressive Prostate Cancer” report on caveolin-1-dependent effects on 
the metabolome in prostate cancer by plasma from two independent cohorts of impressive size. 
Moreover, CCLE and TCGA transcriptomic data are incorporated throughout the study partially 
supporting findings. Mechanistically, three standard prostate cancer cell lines are applied 
throughout the study using transient silencing and overexpression of Cav-1 as well as inhibitors/ Cav-
1 specific antibody. The investigation of metabolic rewiring in prostate cancer seems to be novel. 
The manuscript is well written, however, there are quite a few major points (especially in regards to 
investigations in potential mechanisms) which require a more detailed determination for current 
conclusions made by the authors. 

 

1. In regards to the volcano plot shown in Figure 1B, there seems to be a general trend towards 
higher HR in “early disease progression” indicating that there is no single metabolite detected 
suggesting a smaller risk. Is this the correct interpretation and if yes, does it mean there is a 
generally higher abundance of detected metabolites in the DP group? 

 

2. The authors utilize a “sphingolipid signature” to determine the prediction power for progression-
free survival separating the cohort into top 25th percentile versus bottom 75th percentile, 
unfortunately, without providing detailed information how this arbitrary threshold was selected. 
Beside further information needed and without knowing the rational for an optimal threshold, it is 
suggested to split the entire cohort into quartiles which might reflect prediction power closer to 
what has been shown in the manuscript. How does a quartile split look like? 

 

3. The authors have accessed the TCGA prostate cancer transcriptomic data to provide further 
evidence of CAV-1 in prostate cancer and to study the relationship to lipid metabolism. Here, 
clinicopathological data accompanied with the data sets should be thoroughly investigated in 
regards to CAV-1/ gene sets. Has this been done? Neither the results nor the figure legends provide 
details on the generation of “iCluster-1 to 3”. An appropriate dendrogram on the patients and 
possible prostate cancer subgrouping (if there are any) might be of benefit. 

 

4. The Western blot Figure 2B (bottom of the images) has to be improved. Here, at least a repetitive 
Western blot with reference protein should be shown for all three cell lines together. In addition, an 
appropriate quantification should be done on the images. Stating “…exhibited substantially higher 
fluorescence accumulation” is insufficient. In addition, the scale bar in cell culture images is missing. 

 

5. There is no clear evidence that neither overexpression or silencing of Cav-1 in selected cell lines is 
functional. The Cav-1 antibody seems to work well in Western blot (Figure 2A). Thus, the 
overexpression and silencing could be easily demonstrated in all cell lines used throughout this 
study. 

 

6. CAV1-dependent investigation of the CCLE and TCGA in Figure 2 has been done in order to study 
the possible association of CAV1 and metabolite enzyme-encoding gene expression. Here, the 
description in the text (row 189 to 196) is not obvious in the related figures. It might be true for 
glycosphingolipids, but not for ceramides. A more sophisticated analysis should be done. Moreover, 
the stratification into high or low CAV1 is insufficiently explained. Why were only the highest and 
lowest quartiles chosen? What are the remaining patient numbers in both groups? Is this statistically 
tested? 

 

7. The authors utilize LC-MS for tracing uptake of extracellular sphingomyelins and subsequent 
synthesis of ceramides and glycosphingolipids in the three prostate cancer cell lines. Drawing 
conclusions from the cell lines based on their endogenous Cav-1 expression doesn’t seem to be 
appropriate. Thus, the authors should show in at least 2 cell lines that their results are Cav-1 (in-
)dependent by either silencing or overexpressing Cav-1. In general, comparing cell lines based on 
their Cav-1 expression only, does not adequately allow to address the function of Cav-1 as 
differences might be unrelated to the protein. Here, additional functional tests as already performed 
at the beginning should be consequently applied in almost all the experiments. 

 

8. For entire figure 3, scale bar is missing and statistical evaluation is needed. The number of 
experiments is neither stated in the results nor figure legend. 

 

9. “Selective” inhibitors of glucosylceramide synthase (UGCG) were applied to test a targetable 
metabolic vulnerability. The literature on the specificity of UGCG inhibitors is not straightforward, 
especially in regards to the two inhibitors used. However, it is quite evident that inhibition of UGCG 
does not reduce all glucosylceramide-related glycosphingolipids. Also, studies focused on UGCG are 
quite controversial. The authors found cytotoxicity with accompanied alteration of metabolites in 2 
cell lines. Again, other non-glycosphingolipid related drugs might cause the same effect. Have other 
drugs been tested with focusing on identical readout? Are PPMP and PDPM working the same way 

as shown for eliglustat? Does Cav-1 overexpression (e.g. LNCaP) result in enhanced resistance to 
eliglustat? 

 

10. It is not clear where “… and acute (6hr) accumulation of intracellular ceramides…” (statement 
row 282-285) is demonstrated. There are no data on detailed expression of metabolites as stated. 

 

11. The colors for treatment (eligustat, PDMP, PDMP, vehicle) in figure 5B should be identical. 

 

11. Different series of glycosphingolipids play various roles in cancer. The limited number of 
glycosphingolipids investigated does not allow drawing conclusions for glycosphingolipids in general 
taken the heterogeneity of this class of biomolecules. Thus, it would be of benefit to reflect findings 
reported with the literature on glycosphingolipids in the context of cancer in the discussion. 

 

 

Reviewer #3 (Remarks to the Author): 

 

In this study, Vykoukal et al identify a Cav-1 and sphingolipid/glycosphingolipids and sphingomyelin) 
that is prognostic of prostate cancer disease progression and present a potentially interesting 
mechanism whereby prostate cancer cells utilize Cav-1 and increased ceramide to glycosphingo 
conversion to mitigate mito-toxicity potentially via increased clearance of ceramides. In addition 
they replicate the plasma signature of patients in tumor bearing mice. 

 

I found the data to be quite interesting. The paper covers a lot of ground and proposes a fairly 
detailed mechanism. Various technical points need to be addressed, and the mechanism could be 
refined a bit more. Altogether this is a good mixture of clinical and basic studies. Comments are on 
the heavy side, but this has as much to do with our interest as it does with science. 

 

Major comments: 

1. I am somewhat confused by their overarching mechanism: The authors demonstrate nicely that 
tumor cells upregulate ceramide synthesis from SM, but cells must then deal with (ceramide 
induced) mitochondrial toxicity by shuttling out glycosphingolipids. The mechanism (as written) 
doesn’t make sense to me, as it is a futile cycle with large bioenergetic/biosynthetic costs. If the 
ceramide toxicity point is important to the authors, they should test this with rescue studies 
(perhaps with inhibitors?). There are various other reasons why mitochondria are damaged, so I 

think they can work around it. Along these lines, are mitophagy markers generally upregulated in 
Cav1 KD cells? 

 

2. Figure 2G must include the abundance of total (labeled and unlabeled) species to make any claim 
about fluxes. The LnCAPs could have a much larger pool size (though I think results will hold). The 
10-fold abundance claim about d9-ceramide is misleading without this information. 

 

3. This important and elegant experiment would be better tested in isogenic Cav1 +/- cells (as in Fig 
2C/D). As currently shown, the Cav1 expression is correlative with their flux findings. These 3 cell 
lines are as different as 3 PCa patients – different genetic backgrounds, etc. 

 

4. The impact of Cav1 modulation on cell growth should be shown. This also puts the flux and 
metabolomics data in better context. Is this dependent on lipids in the medium? It would provide 
the reader with more confidence in their mechanism and data in Figure 3. I like the mitochondria 
efflux concept, but this is not supported enough by the data provided. 

 

5. Are significant amounts of mitochondrial DNA or protein present in EVs? Not +/- Cav1 (this will 
certainly be the case), instead the authors should compare vesicular mitochondrial pools to total to 
determine whether this flux is appreciable. 

 

6. If Cav-1 protects against mito toxicity, is overall mito function altered with Cav-1 KD such as 
oxygen consumption etc.? 

 

7. The clinical data is impactful, but none of the metabolites in question were statistically significant 
in their initial analysis (as the authors note). I am fine with the subsequent grouping/signature that 
focuses on ceramide metabolism, but these trends should be considered in the context of other 
clinical parameters. Could obesity or BMI be a driver of the dyslipidemia? Most plasma lipids are on 
liver-derived vLDL particles and thus reflects hepatic metabolism more than the tumor. On that 
front, it would be helpful to quantify the amount of sphingolipids in patient EVs vs vLDLs to know 
what they are observing in the clinical samples. 

 

 

Minor points: 

1. It’s not my area (making it all the more important), but the FL image results weren’t clear to me 
initially. I understand the point from the text and see the image, but it could be presented better. 
Some quantitation of FL imaging would allow the authors to show the highlight the difference to the 
reader more clearly. 

 

2. How was the lipid abundance in figure s3, 2c-d, 2g normalized, was this to cell number or protein? 

 

3. Authors note “Cav-1-mediated clearance of ‘damaged’ mitochondria”, then would you expect less 
LC3BII with eliglustat? 

 

4. Please add a scale bar to 6f images 

 

5. Please plot individual values on 6 b-c so that the biological variation is clear.