Senescent Stroma-Derived Glutamine: A Driver of Aggressiveness in Prostate and Ovarian Cancer Cells

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Review of Senescent Stroma-Derived Glutamine: a Driver of Aggressiveness in Prostate and Ovarian Cancer Cells

 

Overall comments:

The authors show that Glutamine from fibroblast treated with platinum-based drugs make tumors more invasive make cancer cells more invasive, “stem cellish”, activating EMT and protective of ROS through GSH/GSSG.

In their in-vitro model this may be true but as the authors point out it needs to be validated at least in co-culture experiments and in preclinical models to bring it to the next level.

Specific comments:

All figure legends are too long. Please move parts of it to the methods and/or result sections. The panels containing crystal violet and immune fluorescence staining are hard to make out. Better increase them and maybe put them in the supplement if too large.

Fig1: Panel F please also add a bar graph with the absolute expression levels, so the reader can evaluate the difference between each metabolite.

Fig2: Panel B,C It is hard to make out the spheroids, especially when BPTES and Gln withdrawal. Please increase picture magnification, also it would be better if the BPTES panels are below the BPTES bar graphs.

Figure 5: The legend is hard to read, please increase the resolution. I would expand this with all the findings and use it as a summary model/graphical abstract figure.

Suppl. Fig 1A: please show the absolute levels of Gln after ASNase treatment.

Methods:

What is the recipe of the starvation medium?

What is the method for boiling the CM? How long boil, any centrifugation step to remove the precipitated proteins?

 

Author Response

POINT TO POINT

Reviewer 1

 

Overall comments:

The authors show that Glutamine from fibroblast treated with platinum-based drugs make tumors more invasive make cancer cells more invasive, “stem cellish”, activating EMT and protective of ROS through GSH/GSSG.

In their in-vitro model this may be true but as the authors point out it needs to be validated at least in co-culture experiments and in preclinical models to bring it to the next level.

 

We thank the Reviewer for this insightful comment and for highlighting the importance of further validation. We fully agree that extending our findings beyond the current in vitro model represents a crucial next step. In particular, our primary future focus will be the implementation of co-culture systems to better recapitulate the tumor microenvironment and to investigate potential contact-dependent signaling mechanisms between fibroblasts and cancer cells. To this end, we have recently established access to a fluidic platform (https://www.ivtech.it), which will allow us to perform more advanced and physiologically relevant co-culture experiments. These studies are currently planned and will be the subject of future work, allowing us to further validate and expand our findings in a more complex and dynamic setting, with the goal of progressing toward preclinical models. In the Discussion of the revised version of the manuscript, we have specified that our investigation will be focused on preclinical co-culture or in vivo models (Lines 717-719).  

 

Specific comments:

All figure legends are too long. Please move parts of it to the methods and/or result sections. The panels containing crystal violet and immune fluorescence staining are hard to make out. Better increase them and maybe put them in the supplement if too large.

We thank the reviewer for this suggestion. However, we noticed that reviewer 2 requested more detailed figure legends (“I recommend explaining the figures and tables more fully”), evidently, the current references did not fully satisfy both reviewers. To address both reviewers’ comments, we have revised the figure legends by removing redundant information, moving excessively technical details to the Methods section, and retaining essential descriptions to clearly show how the experiments were performed and how statistical analyses were conducted. Details of the statistical analyses for each panel are reported collectively at the end of the corresponding figure legend to avoid unnecessary repetition. We believe these changes improve clarity while ensuring reproducibility.

In addition, the panels showing crystal violet and immunofluorescence staining have been enlarged to improve their readability (Fig 1C-E; 2A-E; 4C and 5G).

 

Fig1: Panel F please also add a bar graph with the absolute expression levels, so the reader can evaluate the difference between each metabolite.

Accordingly, we have included, as a Supplementary Figure 2, a bar graph reporting the metabolite levels expressed as normalized peak area per cell number. This addition allows a more direct comparison between metabolites and provides the reader with a clearer evaluation of their relative differences.

 

Fig2: Panel B,C It is hard to make out the spheroids, especially when BPTES and Gln withdrawal. Please increase picture magnification, also it would be better if the BPTES panels are below the BPTES bar graphs.

We have replaced the panels with higher-quality versions, and their magnification has been increased to improve the visualization of the spheroids, particularly under BPTES treatment and glutamine deprivation conditions, which are associated with the formation of very small spheroids (Fig 3B-C).

In addition, we have reorganized the figure layout by placing the BPTES image panels below the corresponding bar graphs, as suggested, to improve clarity and consistency (Fig 3B).

 

Figure 5: The legend is hard to read, please increase the resolution. I would expand this with all the findings and use it as a summary model/graphical abstract figure.

We thank the Reviewer for this helpful suggestion. We have improved the resolution of Figure 5 to enhance the readability of the legend.

In addition, we have expanded the figure to incorporate the key mechanistic insights from our study,  thereby presenting it as a comprehensive summary model that also serves as a graphical abstract of our findings.

 

Suppl. Fig 1A: please show the absolute levels of Gln after ASNase treatment.

We thank the Reviewer for this suggestion. Accordingly, we have replaced the data in Supplementary Fig 3 with the absolute levels of glutamine after ASNase, now showing the molar concentration of glutamine and ammonium. We have also added the corresponding figure legend.

 

Methods:

What is the recipe of the starvation medium?

What is the method for boiling the CM? How long boil, any centrifugation step to remove the precipitated proteins?

We apologize for the omission of these methodological details in the previous version of the manuscript. We have now specified the composition of the starvation medium (Lines 134-135) and provided a detailed description of the procedure used for boiling the conditioned medium, including boiling time and any subsequent centrifugation steps to remove precipitated proteins (Lines 138-140).

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript is not fully balanced at present, because several conclusions are stated more strongly than the available evidence supports. In particular, mechanistic and translational claims should be phrased more cautiously unless additional validation is added. Please see the attached document. 

Comments for author File: Comments.pdf

Author Response

Please see the attachment

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

Thanks for the corrections

Author Response

We thank the reviewer for considering the manuscript suitable for publication.

Reviewer 2 Report

Comments and Suggestions for Authors

In my opinion, the revised manuscript is improved, but it is still not ready for publication and requires major revision. The authors addressed some concerns at the level of wording, statistics, and limitations, but the main scientific weaknesses remain only partly resolved.
Most importantly, the NRF2/ETS1 pathway is still discussed too strongly, although the authors themselves admit that it is supported only by correlative evidence and not by direct causal proof.
The oxidative stress model is clearer than before, but the connection between ROS, glutamine buffering, NRF2 activation, and invasion is still interpretative rather than firmly demonstrated.
The boiled conditioned-medium experiments are also not sufficient to conclude that metabolites alone explain the remaining biological effect. In fact, the authors’ own response indicates that boiling reduced total protein content by only about 50%, so residual protein contribution cannot be excluded. A major unresolved issue is the western blot evidence although the manuscript states that representative blots come from at least three independent experiments and that densitometric analyses are included, the raw material provided does not clearly document three independent replicates for the key signaling bands. For this reason, the blot data are not sufficiently documented and are not strong enough to support the mechanistic claims in their current form.
Overall, I would recommend major revision.

Author Response

In my opinion, the revised manuscript is improved, but it is still not ready for publication and requires major revision. The authors addressed some concerns at the level of wording, statistics, and limitations, but the main scientific weaknesses remain only partly resolved. Most importantly, the NRF2/ETS1 pathway is still discussed too strongly, although the authors themselves admit that it is supported only by correlative evidence and not by direct causal proof.

We are grateful to Reviewer 2 for acknowledging the improvements made in the revised version, particularly regarding clarity, statistical analysis, and presentation of limitations. We also thank Reviewer 2 for the important comment regarding the mechanistic interpretation of our findings. 

We agree that the involvement of the NRF2/ETS1 pathway in our study is primarily proposed by correlative evidence rather than direct causal demonstration. In response to this concern, we have further softened the interpretation, and we rephrased the relative sentences, both in Results and Discussion, to present the NRF2/ETS1 axis as a putative mechanism, rather than a definitively established pathway (Lines 465-472; 639-653). We have also ensured that the correlative nature of this association is explicitly stated and that no causal inference is implied. We now believe that these changes clearly avoid to misinterpretation of our results and clearly assess the correlative link of the proposed model. 

The oxidative stress model is clearer than before, but the connection between ROS, glutamine buffering, NRF2 activation, and invasion is still interpretative rather than firmly demonstrated.

We thank the Reviewer for this comment on the improvements we made. Generally, we agree that the proposed oxidative stress model should be interpreted with appropriate caution. Our intention is not to provide an unequivocal mechanistic demonstration of the connection between ROS, glutamine buffering, NRF2 activation, and invasion. Rather, our aim is to offer a plausible interpretation of our findings based on the experimental data generated in this study and in the context of previously reported evidence in the literature. Accordingly, we have revised the manuscript to further emphasize the correlative nature of our observations and to avoid any overinterpretation of the mechanistic links proposed (Lines 647-653).

The boiled conditioned-medium experiments are also not sufficient to conclude that metabolites alone explain the remaining biological effect. In fact, the authors’ own response indicates that boiling reduced total protein content by only about 50%, so residual protein contribution cannot be excluded.

We apologize if our previous description of the “boiling” experiment in the first rebuttal letter may have led to any misunderstandings. As also clarified in our previous response letter, the apparent ~50% reduction in total protein content is likely underestimated due to the intrinsic limitations of the BCA assay which may also detect partially degraded or modified protein products generated during boiling. We would like to emphasize that boiling (for 20 minutes) is well established to induce extensive protein denaturation, and we may therefore reasonably assume a substantial loss of functional protein activity. Really, only few proteins are known to be stable even at the boiling temperature of water (https://doi.org/10.1021/bi001441y). In this context, the phenotypic effects observed after boiling are more likely attributable to non-protein components, although we acknowledge that this cannot be stated in absolute terms. Accordingly, we have softened the wording throughout the manuscript to avoid over-interpretation of this experiment as definitive evidence (Lines 39; 354-362). However, importantly, our conclusions are not based solely on the boiling experiment: additional independent approaches modulating glutamine availability and metabolism (including ASNase treatment, glutamine supplementation, Gln synthetase silencing, and BPTES inhibition) consistently support the hypothesis that a non-protein component, Glutamine, may play a relevant role in the observed effects.

A major unresolved issue is the western blot evidence although the manuscript states that representative blots come from at least three independent experiments and that densitometric analyses are included, the raw material provided does not clearly document three independent replicates for the key signaling bands. For this reason, the blot data are not sufficiently documented and are not strong enough to support the mechanistic claims in their current form. Overall, I would recommend major revision.

We thank the Reviewer for this her/his comment and we apologize for the lack of clarity in the presentation of the file with the original western blot data. We acknowledge that original organization of the blots may have made it difficult to clearly identify the corresponding samples and independent replicates. In the present revised version, we have reorganized and resubmitted all the western blot data in a clearer and more structured format, allowing the number of biological replicates to be appreciated. The boxed regions indicate the representative bands shown in the manuscript figures. In addition, the original triplicate western blots are now presented alongside the corresponding bar graphs, which display mean values of the quantifications of the three replicates. We believe that these revisions improve the transparency and clarity of data presentation and more effectively support the robustness of our results.

 

 

 

Round 3

Reviewer 2 Report

Comments and Suggestions for Authors

This revised manuscript is clearly improved, but I still believe it requires major revision before it can be considered for publication. The study is interesting and potentially valuable, yet several conclusions are still expressed too strongly in relation to the actual strength of the data. In particular, the proposed NRF2/ETS1 mechanism remains suggestive rather than fully demonstrated, so the manuscript should distinguish more carefully between association and causation. The conditioned-medium experiments are also not sufficiently rigorous to support a specific metabolite-only interpretation, and this part needs either stronger controls or a more cautious discussion. In addition, the statistical reporting and presentation of replicates should be made more explicit throughout the figures and legends to improve transparency and reproducibility. Importantly, the authors still have not provided complete raw western blot data for all experiments in three biological replicates, which remains a significant issue for data transparency and proper evaluation of the reported protein analyses.

Author Response

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Author Response File: Author Response.pdf