Sulforaphane Enhances Cytotoxic Effects of Non-Thermal Plasma and Tirapazamine Combination Therapy in Pancreatic Adenocarcinoma Cells

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

The authors in the present manuscript investigates the biological effects of a so-called “novel thermal plasma” approach and its impact on cellular behavior. The manuscript suffers from overstated novelty, insufficient mechanistic depth, weak eperimental setup, and unclear conclusions that are not adequately supported by the data.

1.) The authors repeatedly describe their approach as a “novel thermal plasma” technique. However, TP generation is a well-established field with extensive prior literature. The manuscript does not clearly demonstrate a fundamentally new plasma generation mechanism, physical regime, or engineering principle that would justify the claim of novelty. The use of “novel” in the title is therefore misleading and should be removed or rigorously justified with direct comparison to previously published studies.

2.) The title of the manuscript is plagiarized or exactly similar to their own abstract published in a different journal. This will raise a potential conflict of interest in future between both the journals if the study is published with similar titles.

3.) I dont understand the relevance of figure 1. Is it really needed or should be depicted in form of a table.

4.) Again the relevance of figure 2A is not justified. Researchers working on this technique knows it very well. Is it developed by the authors? 

5.) Again the relevance of figure 3 is in doubt. A quick google search can be used to see how BxPC-3 cell line & AsPC–1 cell line looks like in a phase contrast microscope. Dose the figure 1-3 were included to increase the number of figures?

 6.) The entire manuscript comprises of 17 number of figures which looks like a master student thesis. Although there is no limitation of number of figures in MDPI publishing group of journals. But, such a high number of figures raises concerns of non-scientific & mis managed data.

7.) What doe N/T means in figure 7? In figure 7B, TPZ alone exhibit 95% inhibition in cell viability. Than could the authors justify the need for combination of NTP + TPZ in figure 7B?

8.) According to the study, Is the overall effect an additive effect? or synergistic? or anatagonistic? Please use The Chou-Talalay method to answer this question.

9.) The western blot shown in Figure-8 is not at all informative. The authors have not stated how many times the blot was replicated. There is no bar graph analysis & statistics for this figure-8.

10.) There is a research integrity question raised by the Proofig AI software used by the journal's editorial team. The pannel A & E of figure 11 are similar. Additionally, the entire figure 11 is in dark contrast & nothing could be inferred from it. Please perform tunnel assay to assess apoptotic cell death.

11.) The western blot shown in Figure-12 is not at all informative. The authors have not stated how many times the blot was replicated. There is no bar graph analysis & statistics for this figure-12.

12. Where are the western blot images for figure-13 & 14?

13.)again there is no analysis for western blot shown in figure 15?

14. The study is largely descriptive and does not establish causality, as No clear distinction between thermal effects and plasma-specific effects is provided. The authors suggested Key molecular pathways but none of them is experimentally validated. In depth investigation needed.

15.) Heat-only and sham exposure controls are missing or inadequately described. plasma dose–response and time-course experiments are limited.

16.) There is an overinterpretation of biological effects. Conclusions extend beyond the presented data. Observations are correlative but discussed as mechanistic.

17.) Overstated translational relevance. Tone down clinical claims or provide supporting preclinical data using in vivo  models & better in vtro controls.

18.) In the discussion section, it is not clearly stated how it advances beyond existing plasma-biology work.

Author Response

Reviewers’ Comments

Reviewer #1

Comments and Suggestions for Authors

The authors in the present manuscript investigates the biological effects of a so-called “novel thermal plasma” approach and its impact on cellular behavior. The manuscript suffers from overstated novelty, insufficient mechanistic depth, weak eperimental setup, and unclear conclusions that are not adequately supported by the data.

We thank Reviewer 1 for their detailed and thorough review. We have carefully considered each comment and have addressed them point by point below, revising the manuscript where appropriate and providing scientific justification where we respectfully disagree. We hope our responses demonstrate the merit of this work and that the reviewer finds the revised manuscript satisfactory for publication.

1.) The authors repeatedly describe their approach as a “novel thermal plasma” technique. However, TP generation is a well-established field with extensive prior literature. The manuscript does not clearly demonstrate a fundamentally new plasma generation mechanism, physical regime, or engineering principle that would justify the claim of novelty. The use of “novel” in the title is therefore misleading and should be removed or rigorously justified with direct comparison to previously published studies.

We thank the reviewer for this comment and would like to respectfully clarify that our study investigates non-thermal plasma (NTP), not "thermal plasma" as characterized in this review. These are physically and mechanistically distinct phenomena, as non-thermal plasma operates at near-ambient temperatures and exerts its biological effects through the generation of reactive oxygen and nitrogen species rather than thermal effects. Regarding novelty, we agree that NTP as a technology is established and we do not claim a new plasma generation mechanism. The novelty in our title referred specifically to the NTP+TPZ combination therapeutic strategy, which is protected under US Patent 9,586,056 disclosed in our Conflicts of Interest section, affirming its recognized novelty. That said, we understand that "novel" in the title without this context could be confusing and lead people to think NTP or TPZ are novel and not the combination treatment, and we have removed it in the revised manuscript.

2.) The title of the manuscript is plagiarized or exactly similar to their own abstract published in a different journal. This will raise a potential conflict of interest in future between both the journals if the study is published with similar titles.

We thank the reviewer for raising this concern. The abstract referenced was submitted to the AACR 2025 annual meeting as a preliminary presentation of this ongoing work while the full study was still in progress. It is entirely expected and appropriate that a conference abstract and its resulting full manuscript share a similar title, as this is standard academic practice since titles are not copyrightable and it’s our own preliminary work. Also, the title has been now revised to remove “novel.” A conference abstract is not a reviewed publication, does not contain the full dataset or conclusions presented here, and does not constitute duplicate submission. AACR and MDPI both explicitly permit prior conference presentation of preliminary findings, provided the full manuscript represents a substantial expansion, which ours clearly does. We are happy to provide documentation of the AACR submission upon request.

3.) I don’t understand the relevance of figure 1. Is it really needed or should be depicted in form of a table.

We thank the reviewer for this feedback. We would like to note that Figure 1 was originally presented as a table and was converted to a schematic at the suggestion of the MDPI editorial team. The relevance of the figure was to provide a visual of how the plates were set up for reproducibility. In response to this comment and consistent with editorial feedback recommending streamlining of the manuscript, we have removed Figure 1 from the revised manuscript.

4.) Again the relevance of figure 2A is not justified. Researchers working on this technique knows it very well. Is it developed by the authors? 

We thank the reviewer for this question. The specific plasma device depicted in Figure 2A was indeed developed by our research group, originally described in Zirnheld et al., IEEE Transactions on Plasma Science, vol. 38, no. 4, 2010, on which our corresponding author Dr. Shoshanna N. Zucker was a contributor. In response to this comment and consistent with editorial feedback recommending streamlining of the manuscript, we have removed Figure 2A from the revised manuscript. All subsequent figure numbers have been updated accordingly.

5.) Again the relevance of figure 3 is in doubt. A quick google search can be used to see how BxPC-3 cell line & AsPC–1 cell line looks like in a phase contrast microscope. Dose the figure 1-3 were included to increase the number of figures?

We thank the reviewer for this feedback. While we initially maintained Figure 3 on the grounds that cell morphology can vary depending on passage number and culture conditions, and that including our own images supports reproducibility, we have removed it from the revised manuscript in response to this comment and consistent with editorial feedback recommending figure reduction. Figures 1, 2, and 3 were not included to inflate the figure count but rather to build a complete and accessible narrative. We have made substantial reductions to the overall figure count in the revised manuscript, reducing from 17 figures to 9.

 6.) The entire manuscript comprises of 17 number of figures which looks like a master student thesis. Although there is no limitation of number of figures in MDPI publishing group of journals. But, such a high number of figures raises concerns of non-scientific & mis managed data.

Response: We thank the reviewer for this comment and take the concern seriously. In response to this feedback and editorial guidance recommending figure reduction, we have substantially streamlined the manuscript. Several figures have been removed entirely and remaining figures have been combined into multi-panel figures, reducing the total figure count from 17 to 7. We are confident that each remaining figure serves a distinct and necessary scientific purpose, and we believe the revised manuscript presents the data in a more organized and accessible format.

7.) What doe N/T means in figure 7? In figure 7B, TPZ alone exhibit 95% inhibition in cell viability. Than could the authors justify the need for combination of NTP + TPZ in figure 7B?

We thank the reviewer for pointing this out. N/T refers to the NTP+TPZ combination treatment condition, which was not explicitly defined on first use. We have added a parenthetical clarification throughout the manuscript. Yes, we can justify the need for the combination. TPZ is a bioreductive prodrug activated under hypoxic conditions, and NTP generates reactive oxygen and nitrogen species that may contribute to enhanced TPZ activation through modulation of the cellular redox environment, allowing for more targeted prodrug activation at the site of plasma delivery, which is an important mechanistic distinction from TPZ alone. While TPZ alone achieved approximately 95% inhibition in AsPC-1 cells, the addition of NTP further enhanced this to 99.5%, a statistically significant improvement. Critically, in BxPC-3 cells where TPZ alone achieved only 40% inhibition, the combination was essential to achieving the 87% reduction observed, demonstrating clear value the NTP environment creates. This combination approach builds on prior published work from our laboratory in melanoma models, for which we subsequently progressed to three-dimensional spheroid models following establishment of preliminary in vitro data, which is the same trajectory we intend to follow for this pancreatic cancer work.

8.) According to the study, Is the overall effect an additive effect? or synergistic? or anatagonistic? Please use The Chou-Talalay method to answer this question.

We sincerely thank the reviewer for this comment, which prompted us to carefully read the Chou-Talalay paper in full. We fully agree that terms such as synergy, additivity, and antagonism should be operationally defined rather than used loosely, and we have revised the manuscript throughout to more precisely describe these interactions. Bliss independence analysis was performed to formally assess drug interactions, with results reported in Tables 2 and 3. The N/T row in each table represents the Bliss calculation for the NTP+TPZ combination, where predicted inhibition is calculated from single agent data and compared to observed inhibition. Applying this framework, NTP+TPZ demonstrated approximately additive effects in BxPC-3 cells (Δ +1.4%) and moderate synergy in AsPC-1 cells (Δ +12.9%), and we have revised all synergy claims throughout the manuscript accordingly.

Regarding the Chou-Talalay method, we appreciate this recommendation but respectfully note that it requires multiple dose points in a fixed ratio and is designed specifically for titratable chemical compounds. NTP is a physical modality applied at fixed parameters (20V, 90.4 kHz, 4.29 L/min helium flow rate, 30 second exposure) and cannot be titrated like a drug. Varying NTP parameters would alter the composition of reactive oxygen and nitrogen species generated, introducing confounding variables that would make combination index calculations unreliable and scientifically inappropriate. There is therefore no NTP dose parameter that could be meaningfully entered into CompuSyn to generate a valid combination index. For the SF combinations specifically, Bliss independence was similarly selected as the appropriate unified model given that NTP is present as a component in several combination conditions, making it more appropriate to apply a consistent analytical framework across all conditions than to use different methods for different subsets of the data. We acknowledge that Bliss independence assumes mutually nonexclusive drug effects and provides a conservative estimate of additivity, but it remains a widely used and appropriate analytical choice for preliminary in vitro combination studies involving physical treatment modalities, and thus are confident it is the correct methodological choice for our experimental design.

9.) The western blot shown in Figure-8 is not at all informative. The authors have not stated how many times the blot was replicated. There is no bar graph analysis & statistics for this figure-8.

We thank the reviewer for this feedback. Regarding replication, western blot experiments were performed as two fully independent experiments using separate cell passages, and this has now been explicitly stated in the Methods section. Regarding bar graph analysis, Figure 8 was designed specifically to assess the presence or absence of EMT marker proteins across treatment conditions rather than to make quantitative claims about expression levels. The scientific questions being asked are qualitative in nature: whether N-cadherin induction occurs, whether vimentin becomes induced, whether E-cadherin disappears, and band presence or absence directly answers these questions without requiring densitometric quantification. We have revised all references to this figure to ensure they are framed strictly in terms of band presence and absence with no quantitative conclusions drawn. Quantitative densitometric analysis with full statistical comparisons was performed for the western blots examining dose-dependent and treatment-dependent expression changes, which are presented as bar graphs with statistics in the subsequent figures. We believe this approach appropriately matches the analytical method to the scientific question being asked in each figure and is consistent with standard practice in the field.

10.) There is a research integrity question raised by the Proofig AI software used by the journal's editorial team. The pannel A & E of figure 11 are similar. Additionally, the entire figure 11 is in dark contrast & nothing could be inferred from it. Please perform tunnel assay to assess apoptotic cell death.

Response: We thank the reviewer for raising this concern and want to address the research integrity question directly. Panels A and E of Figure 11 represented the control condition without sulforaphane and the control condition with sulforaphane respectively, both in untreated cells of the same line grown under identical conditions. These were independent images taken from separate experimental wells and were not duplicated or manipulated in any way. The visual similarity flagged by the AI software reflects the biological reality that untreated cells of the same line will exhibit similar morphology, which is not evidence of image duplication. We would like to emphasize that no image manipulation occurred in this study. That said, in response to feedback from multiple reviewers regarding figure clarity and necessity (since it was just pictures of treated cells), we have removed Figure 11 from the revised manuscript entirely, which we believe also resolves the Proofig flag.

Regarding the TUNEL assay request, cell viability data obtained via PrestoBlue already provides robust evidence of cytotoxicity across all treatment conditions with statistically significant reductions confirmed by one-way ANOVA. Furthermore, the apoptotic mechanisms of both NTP and TPZ are well established in the literature including our own published melanoma work. We respectfully consider TUNEL analysis to be beyond the scope of this preliminary study and a valuable direction for future work as we progress into more advanced model systems.

11.) The western blot shown in Figure-12 is not at all informative. The authors have not stated how many times the blot was replicated. There is no bar graph analysis & statistics for this figure-12.

Response: We thank the reviewer for this comment and would like to respectfully clarify that quantitative bar graph analysis and statistical data accompanying the western blot shown in Figure 12 are present in the manuscript immediately following the figure. The dose-dependent effects of sulforaphane on vimentin and E-cadherin expression are presented as bar graphs with statistical significance markers, and a comprehensive summary of expression ratios, SEM values, and adjusted p-values across all sulforaphane concentrations is provided in Table 4, which includes one-way ANOVA with Dunnett's multiple comparisons test results. We would kindly encourage the reviewer to refer to these figures and Table 4, which together provide the full quantitative and statistical analysis accompanying Figure 12.

Regarding replication, as clarified in the revised Methods section, western blot experiments were performed in biological duplicate using independent cell passages with consistent results observed across replicates. Our study was originally designed based on prior published data suggesting that sulforaphane upregulates Cx43 expression in AsPC-1 cells. The consistent absence of Cx43 in AsPC-1 cells across both replicates, while Cx43 remained clearly expressed in BxPC-3 controls, was an unexpected finding that we believe is scientifically meaningful and worth reporting. A reproducible null result obtained across independent biological replicates is a valid scientific finding. We discuss potential explanations for this discrepancy in the Discussion, including promoter hypermethylation, variations in cell passage number, and differences in experimental conditions, and we acknowledge that additional factors not captured in the current study may have contributed to this outcome and warrant future investigation. Importantly, sulforaphane produced significant and reproducible effects on other markers examined in this study, including dose-dependent modulation of vimentin and E-cadherin expression as shown in the figures and Table 4, and substantially enhanced cytotoxicity across all treatment conditions in both cell lines, which represents the most significant and expandable takeaway from this work. Taken together, these findings provide a coherent and publishable scientific narrative that advances our understanding of sulforaphane's effects in this context, even in the absence of Cx43 restoration.

12. Where are the western blot images for figure-13 & 14?

We thank the reviewer for this question. In the revised manuscript these have been combined into a single multi-panel figure, with the western blot image as panel A and the vimentin and E-cadherin bar graphs as panels B and C respectively. We hope this combined presentation makes the relationship between the blot image and its quantification more immediately clear.

13.)again there is no analysis for western blot shown in figure 15?

We thank the reviewer for this comment. In the revised manuscript these have been combined into a single multi-panel figure, with the western blot image as panel A and the graphs as panels B and C respectively, which we hope makes the relationship between the blot and its quantification immediately clear.

14. The study is largely descriptive and does not establish causality, as No clear distinction between thermal effects and plasma-specific effects is provided. The authors suggested Key molecular pathways but none of them is experimentally validated. In depth investigation needed.

Response: We thank the reviewer for this comment and would like to respectfully clarify that this study was designed as a preliminary descriptive investigation. The claim made in the title is observational and descriptive by nature, specifically that sulforaphane enhances cytotoxic effects, and no specific causal mechanism is claimed in the title or conclusions. The mechanistic pathways discussed are intentionally framed as candidate hypotheses situated within the broader literature rather than established conclusions, and deeper mechanistic validation is explicitly identified as a future direction. Correlational and descriptive studies that document novel observations and lay the groundwork for future investigation are routinely published and represent a valuable step in the scientific process. The present study provides original experimental data, statistical analysis, and reproducible findings that demonstrate this combination approach is worth investigating further and provide a foundation for future mechanistic work. Regarding thermal effects, we would like to clarify that our study uses non-thermal plasma, which by definition operates at near-ambient temperatures and does not generate significant heat, making a distinction between thermal and plasma-specific effects not applicable to our experimental system.

15.) Heat-only and sham exposure controls are missing or inadequately described. plasma dose–response and time-course experiments are limited.

Response: We thank the reviewer for this comment. Regarding heat-only controls, our study utilizes non-thermal plasma, which by definition operates at near-ambient temperatures and does not generate significant heat, making a heat-only control not applicable to our experimental system. Regarding sham controls, untreated cells served as the negative control across all experiments, which is the appropriate comparator in this context, as a sham NTP exposure would be methodologically indistinguishable from an untreated control given that NTP generates no meaningful physical output in the absence of plasma activation. Regarding dose-response and time-course experiments, we agree these represent valuable future directions and have noted this in our limitations section. This study was designed to establish preliminary proof of concept using fixed treatment parameters consistent with our previously published melanoma work, and more extensive parametric optimization is planned as we progress into more advanced model systems including three-dimensional spheroid cultures and in vivo mouse models, consistent with our laboratory's established research trajectory for this combination therapy.

16.) There is an overinterpretation of biological effects. Conclusions extend beyond the presented data. Observations are correlative but discussed as mechanistic.

17.) Overstated translational relevance. Tone down clinical claims or provide supporting preclinical data using in vivo  models & better in vtro controls.

18.) In the discussion section, it is not clearly stated how it advances beyond existing plasma-biology work.

16-18 combined Response: We thank the reviewer for these comments and have addressed them together as they relate to the overall framing and scope of the manuscript. We acknowledge that certain passages in the Discussion contained language that could be interpreted as making mechanistic claims beyond what the data directly support, and we appreciate the reviewer bringing this to our attention. The Discussion was intended to situate our findings within the broader literature and propose candidate mechanisms based on established research, not to assert causal conclusions from our in vitro data. In response we have revised language throughout the manuscript to ensure all conclusions are appropriately scoped, replacing causal phrasing with appropriately hedged language and framing proposed mechanisms explicitly as hypotheses for future investigation. Regarding translational relevance, the conclusion has been revised to state that this work may inform the development of novel therapeutic strategies rather than making direct clinical claims, supported by sulforaphane's established human safety profile, tirapazamine's prior clinical trial history, and our laboratory's existing in vivo experience with the NTP device in melanoma models. Regarding advancement beyond existing plasma-biology work, while NTP-treated solutions have been examined in pancreatic cancer models previously, the present study is the first to evaluate the patented NTP+TPZ combination in pancreatic adenocarcinoma, the first to investigate sulforaphane as a sensitizing adjunct to NTP-based combination therapy in any cancer model, and contributes a meaningful null result regarding Cx43 restoration that adds nuance to prior findings in this cell line. We have added a clarifying statement to the Discussion to make these contributions.

Reviewer 2 Report

Comments and Suggestions for Authors

The manuscript presents a well-organized and meaningful study addressing the biological effects of the proposed therapeutic/material strategy. The experimental workflow is generally logical, and the combination of in vitro and mechanistic analyses provides a reasonably comprehensive evaluation of the system. Overall, the results support the main conclusions, and the topic is relevant to the field. However, the following issues should be addressed before the acceptance of this paper.

1) The overall figure quality and resolution should be improved to ensure that morphological and quantitative differences can be clearly evaluated.

2) Statistical significance markers should follow a unified style throughout the manuscript (e.g., *, **, ***).

3) Some mechanistic statements appear somewhat over-interpreted based on the current data and should be revised with more cautious wording.

4) Several material or assay parameters (e.g., physicochemical measurements, characterization tests, or calculation methods) should be accompanied by a clearer description of how these data were obtained, including standards or instruments when applicable.

5) The description of certain experimental procedures would benefit from additional detail to ensure reproducibility (e.g., incubation conditions, replicates, or normalization methods).

6) More recent references related to cancer therapy should be cited: Nano Today 2022, 44, 101459; Advanced Materials 2024, 36 (11), 2310456; Advanced Materials, 2026 https://doi.org/10.1002/adma.202522016.

Author Response

Reviewers’ Comments

Reviewer #2

Yes	Can be improved	Must be improved	Not applicable
Does the introduction provide sufficient background and include all relevant references?	(x)	( )	( )	( )
Is the research design appropriate?	(x)	( )	( )	( )
Are the methods adequately described?	(x)	( )	( )	( )
Are the results clearly presented?	(x)	( )	( )	( )
Are the conclusions supported by the results?	(x)	( )	( )	( )
Are all figures and tables clear and well-presented?	(x)	( )	( )	( )

Comments and Suggestions for Authors

The manuscript presents a well-organized and meaningful study addressing the biological effects of the proposed therapeutic/material strategy. The experimental workflow is generally logical, and the combination of in vitro and mechanistic analyses provides a reasonably comprehensive evaluation of the system. Overall, the results support the main conclusions, and the topic is relevant to the field. However, the following issues should be addressed before the acceptance of this paper.

We thank Reviewer 2 for their careful and constructive evaluation of our manuscript. We appreciate the positive assessment of the study's organization and experimental logic, and we have addressed each comment below.

1) The overall figure quality and resolution should be improved to ensure that morphological and quantitative differences can be clearly evaluated.

Response: We thank the reviewer for this feedback. We wish to clarify that all western blot images were captured and exported at 300 DPI, which meets the minimum resolution requirement specified by MDPI's figure guidelines. Following necessary cropping to remove excess white space and format figures appropriately, this is the maximum resolution available from our current image files. We acknowledge that this may limit the clarity in some panels but does not detract from the overall understanding of the information. We would also note that in response to feedback from other reviewers regarding figure necessity and clarity, we have removed several cell morphology images that were noted as either unnecessary or insufficiently clear. We believe these removals, combined with the standardized 300 DPI resolution across remaining figures, collectively address concerns regarding figure quality to the extent possible within the constraints of our existing data.

2) Statistical significance markers should follow a unified style throughout the manuscript (e.g., *, **, ***).

Response: We thank the reviewer for noting this. We standardized all statistical significance markers throughout the manuscript to follow a unified convention: *p < 0.05, **p < 0.01, ***p < 0.001, ****p < 0.0001, consistent with GraphPad Prism notation used for our analyses. This has been applied uniformly across all figures and tables. If there are any specific further discrepancies, please let us know so we can address.

3) Some mechanistic statements appear somewhat over-interpreted based on the current data and should be revised with more cautious wording.

Response: We thank the reviewer for this observation and fully agree. Upon careful re-reading, we acknowledged that certain passages in the Discussion contained language that could be interpreted as making mechanistic claims beyond what our current data directly support. This was not the intention of the authors. The Discussion was designed to situate our findings within the broader literature, propose candidate mechanisms based on established research in related models, and contextualize our observations rather than assert causal conclusions from our in vitro data alone. In response we have revised language throughout the Discussion to ensure proposed mechanisms are framed as candidate hypotheses for future experimental validation and that observational findings are described with appropriately cautious wording reflecting the preliminary and descriptive nature of this study.

4) Several material or assay parameters (e.g., physicochemical measurements, characterization tests, or calculation methods) should be accompanied by a clearer description of how these data were obtained, including standards or instruments when applicable.

We thank the reviewer for this suggestion. In response to this comment we have added the Bliss independence formula to Section 2.4: E(A+B) = E(A) + E(B) − E(A) × E(B), where E(A) and E(B) represent the fractional inhibition of each single agent, with synergy, additivity, and antagonism defined as observed inhibition greater than, equal to, or less than predicted inhibition respectively. Densitometric quantification using ImageJ software (NIH, Bethesda, MD, USA) has also been explicitly added to Sections 2.3 and 2.5. We would also like to highlight that several instrument and parameter specifications were already present in the original manuscript, including the hypoxic chamber (Biospherix Model#E702m, 0.1% O2), plate reader (BioTek Synergy HT, 530 nm excitation, 590 nm emission), and NTP treatment parameters (20V, 90.4 kHz, 4.29 L/min helium flow rate, 30 second exposure). Together with the additions described above, we believe the Methods section now provides sufficient details needed for replication.

5) The description of certain experimental procedures would benefit from additional detail to ensure reproducibility (e.g., incubation conditions, replicates, or normalization methods).

Response: We thank the reviewer for this helpful suggestion. In response to this comment we have added the following to the Methods section: western blot experiments (Sections 2.3 and 2.5) now explicitly state that experiments were performed in biological duplicate using independent cell passages with consistent results across replicates, and protein expression normalization to GAPDH as a loading control using ImageJ is now explicitly stated in both sections. We would also like to highlight that several of the details noted by the reviewer were already present in the original manuscript, including incubation conditions (37°C, 5% CO2, 0.1% O2), drug treatment timepoints, plate reader settings (530 nm excitation, 590 nm emission), and antibody dilutions (1:1000 primary in 3% BSA TBS-T, 1:5000 secondary in dry milk TBS-T). Together with the additions described above, we believe the Methods section now provides the detail needed to ensure reproducibility of the reported experiments.

6) More recent references related to cancer therapy should be cited: Nano Today 2022, 44, 101459; Advanced Materials 2024, 36 (11), 2310456; Advanced Materials, 2026 https://doi.org/10.1002/adma.202522016.

Response: We thank the reviewer for these suggestions and have carefully reviewed all three references. We have incorporated the Advanced Materials 2024 reference (Yu et al.) into the Introduction where we discuss the need for novel combinatorial strategies to overcome resistance mechanisms in pancreatic adenocarcinoma, as this work represents a relevant example of emerging combination approaches in PDAC. The remaining two references are about addressing ferroptosis in platinum-resistant ovarian cancer and a hydrogel-based chemo-immunotherapy platform in breast cancer, which are mechanistically and contextually distinct from our plasma-based and phytochemical approach in pancreatic cancer, and we determined that their inclusion would not strengthen the scientific narrative of the current manuscript. However, we had incorporated the “Platinum Prodrug Nanoparticles with COX-2 Inhibition Amplify Pyroptosis for Enhanced Chemotherapy and Immune Activation of Pancreatic Cancer” as reference [6] in the Introduction where we discuss novel combinatorial strategies for PDAC since we feel it is relevant to our discussion. 

 

Reviewer 3 Report

Comments and Suggestions for Authors

Ishfar Shaan et al.'s study investigates a combinatorial approach targeting pre-metastatic and metastatic pancreatic cancer, a major therapeutic challenge. In vitro cytotoxicity data supports the use of non-thermal plasma and the hypoxia-activated prodrug tirapazamine combined, indicating synergy among diverse pancreatic cancer cell lines. One of its best features is sulforaphane adjuvant. This improves treatment without making people more aggressive or invasive, reducing concerns about aggression. Bliss independence analysis quantifies synergistic and additive interactions, help us understand their mechanisms. For the study, sulforaphane's mechanisms of NTP+TPZ activity enhancement, beyond connexin 43 and EMT indicators, should be better understood. Translational relevance would also improve with validation in physiologically relevant models like 3D cultures or in vivo systems. The researchers found a promising new way to combine pancreatic cancer treatments. This manuscript can be accepted in its present form 

Author Response

Reviewers’ Comments Reviewer #3 Yes	Can be improved	Must be improved	Not applicable
Does the introduction provide sufficient background and include all relevant references?	(x)	( )	( )	( )
Is the research design appropriate?	(x)	( )	( )	( )
Are the methods adequately described?	(x)	( )	( )	( )
Are the results clearly presented?	(x)	( )	( )	( )
Are the conclusions supported by the results?	(x)	( )	( )	( )
Are all figures and tables clear and well-presented?	(x)	( )	( )	( )

Comments and Suggestions for Authors

Ishfar Shaan et al.'s study investigates a combinatorial approach targeting pre-metastatic and metastatic pancreatic cancer, a major therapeutic challenge. In vitro cytotoxicity data supports the use of non-thermal plasma and the hypoxia-activated prodrug tirapazamine combined, indicating synergy among diverse pancreatic cancer cell lines. One of its best features is sulforaphane adjuvant. This improves treatment without making people more aggressive or invasive, reducing concerns about aggression. Bliss independence analysis quantifies synergistic and additive interactions, help us understand their mechanisms. For the study, sulforaphane's mechanisms of NTP+TPZ activity enhancement, beyond connexin 43 and EMT indicators, should be better understood. Translational relevance would also improve with validation in physiologically relevant models like 3D cultures or in vivo systems. The researchers found a promising new way to combine pancreatic cancer treatments. This manuscript can be accepted in its present form 

We sincerely thank Reviewer 3 for their thorough and encouraging assessment of our manuscript. We are pleased that the reviewer found our combinatorial approach, sulforaphane adjuvant strategy, and Bliss independence analysis to be strengths of the work, and we genuinely appreciate the recognition of this study's significance as preliminary work justifying further investigation of this combined therapy. Regarding the suggestion that sulforaphane's mechanisms of NTP+TPZ activity enhancement should be better understood, we agree and would like to highlight that Section 4.3 discusses several candidate pathways through which sulforaphane may enhance cytotoxicity, including Nrf2/phase II enzyme activation, modulation of cellular redox balance, NF-κB suppression, caspase-mediated apoptosis sensitization, and HIF-1α inhibition. Deeper mechanistic dissection falls beyond the scope of this initial report but is explicitly identified as a planned next step in our ongoing research program. Regarding validation in physiologically relevant models, we fully agree this is an important future direction. Our laboratory has prior experience with SCC7 spheroid cultures and rat models in related NTP combination therapy work, and should these findings continue to show promise, we plan to progress into similarly complex model systems for this pancreatic cancer work. We would also like to note that in response to the other reviewers' comments, we have made targeted revisions including methodological clarifications, figure consolidation, and refinements to mechanistic language that we believe have only strengthened the manuscript. We are truly grateful for the reviewer's encouraging words and their recognition of the significance of this work, and we look forward to sharing future developments as this research progresses.

 

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

The authors have successfully addressed all my comments except for the western blots, which are performed in two replicates rather than the standard practice of three. Since the authors have mentioned this in the method section so, it looks fine to me. But I think the guest editors can take a final decision on this issue. I do not have any other concern or comment.