Oxidative Stress Pathways Linked to Apoptosis Induction by Low-Temperature Plasma Jet Activated Media in Bladder Cancer Cells: An In Vitro and In Vivo Study

Round 1

Reviewer 1 Report

Author Response

Dear Editor

We thank the Reviewer’s for providing useful comments to help improve the quality of our manuscript. We have addressed each of their comments as indicated below.

Reviewer 1: Dear Authors, first of all I would like to congratulate You on your work. The topic Is of great clinical relevance. I would only just suggest to insert in the section conclusion the limits of present study.

We would like to thank the Reviewer for supportive comments and noting the clinical importance of our study. We agree that there are limitations for any study and we have provided discussion of this in the conclusion section, which we have renamed Conclusion and Future Directions.

“However, plasma activated solutions in bladder cancer treatment might help avoid common clinical problems associated with BCG such as atrophic bladder, infection, Reiter syndrome and interstitial pneumonia. Future research should investigate overcoming these challenges including longer term survival rates and a rigorous safety assessment in preclinical models to ensure the new therapy can be effectively and safely translated into clinical trials.”

Reviewer 2 Report

This manuscript showed the effect of plasma activated media in bladder cancer.
The authors demonstrate the plasma-activated media treatment effects the oxidative stress, cell cycle arrest, and apoptosis in bladder cancer cell lines.
They conclude that plasma-activated media treatment induces anti-cancer activities in vitro and in vivo, and it has the potential to be a new adjuvant therapy.
However, there are severe concerns in the presented study.

Comments
1. The reviewer wonders that the control condition is correct for the elucidation of ROS activities in plasma-activated media. 
Plasma-activated media is produced by high-voltage pulse with He gas. The reviewer think that it probably be appreciate condition to culture in the media including He gas without high-voltage media.
Or the condition with ROS reduction from the plasma-activated media is needed.

2. The authors should clarity the benefit of "plasma-activated media" treatment. If these effects are caused by ROS activities, it does not have to be treatment by plasma-activated media.
For example, is hydrogen peroxide sufficient?

3. In Figure 3, western blot lacks the internal control. In addition, there are several unclear bands.
Reexamination of western blotting should be performed.

4. In general, ROS induces the mutagenesis in the normal cells. In the manuscript, there is no evidence of plasma-activated media effect in normal cells.
The authors should show the effect of plasma-activated media in normal cells in vitro and in vivo.
Especially, in vivo experiment, the mice are incubated in plasma-activated media bath.
The authors should show the effects in other tissues.

5.　In Figure 5, it is an overstatement. The presented results are insufficient for the elucidation of scheme.
The further experiment, e.g. the validation of increase ROS in treated cancer cells, and the inhibitors treatment of ROS signal pathway should be performed.
In addition, the results are insufficient to prove their hypothesis. 

Author Response

We thank the Reviewer’s for providing useful comments to help improve the quality of our manuscript. We have addressed each of their comments as indicated below.

Reviewer 2: This manuscript showed the effect of plasma activated media in bladder cancer.

The authors demonstrate the plasma-activated media treatment effects the oxidative stress, cell cycle arrest, and apoptosis in bladder cancer cell lines.

They conclude that plasma-activated media treatment induces anti-cancer activities in vitro and in vivo, and it has the potential to be a new adjuvant therapy.

However, there are severe concerns in the presented study.

We thank the Reviewer for the above comments and we have addressed the Reviewer’s comments below.

Comments

1. The reviewer wonders that the control condition is correct for the elucidation of ROS activities in plasma-activated media.

Plasma-activated media is produced by high-voltage pulse with He gas. The reviewer think that it probably be appreciate condition to culture in the media including He gas without high-voltage media.

Or the condition with ROS reduction from the plasma-activated media is needed.

We have revised Figure 1e to include three control samples: (1) untreated media, (2) media with addition of luminol, and (3) media with luminol following helium gas treatment.

2. The authors should clarity the benefit of "plasma-activated media" treatment. If these effects are caused by ROS activities, it does not have to be treatment by plasma-activated media.

For example, is hydrogen peroxide sufficient?

This was not the purpose and is beyond the scope of the present study. The present study focussed on the overall oxidative effects of PAM in bladder cancer therapy. We agree with the Reviewer that this is an important point to address in future studies. A recent study has shown that even PAM prepared with very low concentrations of hydrogen peroxide below 10 µM can induce beneficial anticancer effects (Guo B et al Proc Natl Acad Sci U S A. 2021 Dec 21;118(51):e2107220118). Therefore, it is likely to be the unique composition of all the ROS created by plasma in PAM and their synergistic action that produces the anticancer effects.

3. In Figure 3, western blot lacks the internal control. In addition, there are several unclear bands.

Reexamination of western blotting should be performed.

We have re-examined the western blot to improve the resolution of the bands and included the internal control GAPDH.

4. In general, ROS induces the mutagenesis in the normal cells. In the manuscript, there is no evidence of plasma-activated media effect in normal cells.

The authors should show the effect of plasma-activated media in normal cells in vitro and in vivo.

Especially, in vivo experiment, the mice are incubated in plasma-activated media bath.

The authors should show the effects in other tissues.

We have investigated the effect of PAM on two normal bladder cell lines HBEC-A and HBEC-D (shown in revised Figure 1f and 1g). The results show that PAM selectively reduces cell viability in the cancer cell lines as opposed to the normal cells. The in vitro result could be translated into the preclinical bladder cancer tumour in Figure 4c where the PAM selectively induces apoptosis and reduces cell proliferation in the tumour region as opposed to the healthy surrounding tissue.

5.　In Figure 5, it is an overstatement. The presented results are insufficient for the elucidation of scheme.

The further experiment, e.g. the validation of increase ROS in treated cancer cells, and the inhibitors treatment of ROS signal pathway should be performed.

In addition, the results are insufficient to prove their hypothesis.

We disagree this with comment. Figure 2i and 2j shows the elevation in mitochondrial ROS stress in the PAM treated 253JB-V and T24 bladder cancer cells. This correlates to caspase 3 and cytochrome c release as shown in Figure 2g and 2h, which leads to apoptosis in Figure 2a-f. This correlates to cell cycle arrest shown in Figure 3a-d, which is associated with downregulation of the cell cycle regulatory factors cyclin D and CDK 4 and up-regulation of p21 as shown in Figure 3e. To highlight these points better we have included references to the relevant Figures within Figure 5.

Round 2

Reviewer 2 Report

This manuscript showed the effect of plasma activated media in bladder cancer.
The authors demonstrate the plasma-activated media treatment effects the oxidative stress, cell cycle arrest, and apoptosis in bladder cancer cell lines.
They conclude that plasma-activated media treatment induces anti-cancer activities in vitro and in vivo, and it has the potential to be a new adjuvant therapy. The authors revised the manuscript following my concerns. Despite this effort, little improvements have been made, and the following concerns remain unaddressed. 

Comments
1. As previous my comment 1, the reviewer can not judge the results, it is because the presented manuscript file (pdf file) lacks a part of figure 1. The authors should present a clear manuscript. Luminol condition is good as a control sample. The reviewer thinks that the reduction condition (as an inhibition) in Figure 2-4 can help to prove their hypothesis. The manuscript could profit from a careful response to these points.

2. As previous my comment 3, the authors reexamine the WB analysis. GAPDH is acceptable as an internal control. However, Cyclin D in T24 cells and CDK4 in 253JB-V cells are not decreased by PAM treatment. These alterations are very small. The authors' interpretations are not fair. It does not support their conclusions and hypothesis.

3. As previous my comment 4, the reviewer concerns "mutagenesis" in the normal cells. The authors showed the cell viabilities of normal cell; however, these results does not address my concerns. Mutagenesis by ROS causes cell death via p53 or contributes to tumorigenesis. The authors commented, " The in vitro result could be translated into the preclinical bladder cancer tumour in Figure 4c where the PAM selectively induces apoptosis and reduces cell proliferation in the tumour region as opposed to the healthy surrounding tissue.". This is unsubstantiated speculation. In vitro and in vivo results do not necessarily match. The reviewer previously asked the effect in "other tissues". Please provide the evidence.
Next, in Figure 1f and 1g, the reviewer can see that PAM treatment effects the normal cells. In addition, the reviewer wonders that cell viabilities in control condition exceeds 100%. There is doubt about the method. The authors should discuss the usefulness of PAM treatment, considering its toxicity to the normal cells.

4. As previous my comment 5, in general signal pathway analysis, knockdown, or inhibition of signal transmediators reveals the signal cascade and causal relationships. The authors comments the "correlates", the reviewer agree this. It is just a correlation, it is not signal pathway. The authors showed only the correlations, it is insufficient to prove the cascade of the pathway.
In addition, this study's design does not exclude the possibility of other signal pathways. Again, it is insufficient as a signal transduction study.

In general, the other ROS signaling, for example
a) p53 is a major regulator in cell cycle and mitochondrial regulation in apoptotic signaling. The alteration of p53 induces apoptosis via mitochondria.
b) ASK1 and JNK are famous kinases in ROS pathway. These kinases are activated by ROS, and induces the Caspase-3 activation via mitochondria. 
In addition, in Figure 3, the alterations of cell cycle genes are varied in the used cell lines. 
Despite the presented study does not exclude the contribution from other ROS pathway, the authors concluded the ROS pathway in PAM treatment.
Again, it is an overstatement. These results are insufficient to prove the ROS pathway in PAM treatment.

5, Whole of the manuscript, the revised regions are not highlighted. Therefore, it is difficult the revised point in the manuscript. As also mentioned in comment 1, the manuscript is well not prepared to review. 

The reviewer's expertise: cell biology, signal transduction, oncogene, cancer metastasis

Author Response

We would like to Reviewer for the second review of our manuscript. Whilst the Reviewer raises useful suggestions we are not able to address all of the Reviewer’s points (e.g. sampling other tissues); because, whilst important we do not think this extra information is essential at this stage of the research and we would unlikely receive further ethical approval to conduct these animal experiments at this stage. We agree with the Reviewer that we were perhaps a little optimistic about our cellular pathway claims and do not disagree that other pathways can be involved in explaining the anticancer in this study. Therefore, we have revised the manuscript accordingly to reflect these possibilities and have toned down our claims on the molecular pathways. This includes a revision a of the title and throughout the entire manuscript. Our changes are highlighted in blue.

Comments

1. As previous my comment 1, the reviewer can not judge the results, it is because the presented manuscript file (pdf file) lacks a part of figure 1. The authors should present a clear manuscript. Luminol condition is good as a control sample. The reviewer thinks that the reduction condition (as an inhibition) in Figure 2-4 can help to prove their hypothesis. The manuscript could profit from a careful response to these points.

We have added the control luminol formulations into the revised Figure 1e and described these in the Figure caption. We have removed some of earlier claims particularly related to the cell cycle regulatory factors and we believe that the negative controls provide enough evidence to support our revised discussion.

2. As previous my comment 3, the authors reexamine the WB analysis. GAPDH is acceptable as an internal control. However, Cyclin D in T24 cells and CDK4 in 253JB-V cells are not decreased by PAM treatment. These alterations are very small. The authors’ interpretations are not fair. It does not support their conclusions and hypothesis.

We agree with this comment and we have revised the manuscript throughout (all changes highlighted in blue) to reflect this. This includes modification of Figure 5.

3. As previous my comment 4, the reviewer concerns "mutagenesis" in the normal cells. The authors showed the cell viabilities of normal cell; however, these results does not address my concerns. Mutagenesis by ROS causes cell death via p53 or contributes to tumorigenesis. The authors commented, " The in vitro result could be translated into the preclinical bladder cancer tumour in Figure 4c where the PAM selectively induces apoptosis and reduces cell proliferation in the tumour region as opposed to the healthy surrounding tissue.". This is unsubstantiated speculation. In vitro and in vivo results do not necessarily match. The reviewer previously asked the effect in "other tissues". Please provide the evidence.

Next, in Figure 1f and 1g, the reviewer can see that PAM treatment effects the normal cells. In addition, the reviewer wonders that cell viabilities in control condition exceeds 100%. There is doubt about the method. The authors should discuss the usefulness of PAM treatment, considering its toxicity to the normal cells.

We did not study the potential systemic effect of PAM as this was not the motivation of our study. However, as previously mentioned, since PAM did not affect the immediate surrounding tissue or healthy cells to the same level of the bladder cancer cells in vitro and the cancer tumour in vivo, it indicates the potential selectivity of PAM in killing bladder cancer cells. We agree that a detailed safety assessment of PAM including off-target effects in other tissues is essential knowledge in progressing the technology to clinical trials. We included this point into the future directions of the research.

4. As previous my comment 5, in general signal pathway analysis, knockdown, or inhibition of signal transmediators reveals the signal cascade and causal relationships. The authors comments the "correlates", the reviewer agree this. It is just a correlation, it is not signal pathway. The authors showed only the correlations, it is insufficient to prove the cascade of the pathway.

In addition, this study's design does not exclude the possibility of other signal pathways. Again, it is insufficient as a signal transduction study.

In general, the other ROS signaling, for example

1. a) p53 is a major regulator in cell cycle and mitochondrial regulation in apoptotic signaling. The alteration of p53 induces apoptosis via mitochondria.
2. b) ASK1 and JNK are famous kinases in ROS pathway. These kinases are activated by ROS, and induces the Caspase-3 activation via mitochondria.

In addition, in Figure 3, the alterations of cell cycle genes are varied in the used cell lines.

Despite the presented study does not exclude the contribution from other ROS pathway, the authors concluded the ROS pathway in PAM treatment.

Again, it is an overstatement. These results are insufficient to prove the ROS pathway in PAM treatment.

We agree that including the cell cycle regulatory factors into Figure 5 may be an overstatement. We have revised Figure 5 accordingly to create illustrate “proposed” molecular pathways of how PAM might be inducing apoptosis in the bladder cancer cells.

5, Whole of the manuscript, the revised regions are not highlighted. Therefore, it is difficult the revised point in the manuscript. As also mentioned in comment 1, the manuscript is well not prepared to review.

All our changes are highlighted in blue.