All reviews of published articles are made public. This includes manuscript files, peer review comments, author rebuttals and revised materials. Note: This was optional for articles submitted before 13 February 2023.
Peer reviewers are encouraged (but not required) to provide their names to the authors when submitting their peer review. If they agree to provide their name, then their personal profile page will reflect a public acknowledgment that they performed a review (even if the article is rejected). If the article is accepted, then reviewers who provided their name will be associated with the article itself.
Thanks for addressing the remaining concern. I am happy to now proceed.
[# PeerJ Staff Note - this decision was reviewed and approved by Vladimir Uversky, a PeerJ Section Editor covering this Section #]
Neither the reviewer or I are convinced by your rebuttal. I also note that key data is not presented for inspection.
I will allow you one further attempt to deal with these comments fully, transparently and as specified. Should you not do this, then the paper must be rejected.
"After calculating the IC50 values, we found that the IC50 values of Dihydrotanshinone I were lower in HCC cells than in normal liver cells, which implies that Dihydrotanshinone I produces stronger toxicity in HCC cells (Fig. S1)."
Authors mention a Fig. S1 here. There's no such figure in the uploaded files and there's no graphic for IC50 values in any of the uploaded figures.
No comment.
There were 2 concerns of mine in my previous review on this manuscript. One of these concerns was that the cytotoxic effect of Dihydrotanshinone I on healthy cells were ignored and unmentioned in the manuscript. That problem is fairly solved by the authors. Authors indicated these results in the Results section. But, I believe it could be mentioned in the discussion as well.
However, my second concern is still unsolved. Authors performed cell viability assays with Huh-7, Hepg2 and MIHA cells using different concentrations of Dihydrotanshinone I. Then, they compared the viability rates of the experimental groups with different concentrations to the control group of the same cell line and presented significant differences. By doing this, we can see the differing results of various concentrations in SAME CELL LINE.
Authors claimed that:
"However, the survival rate of MIHA cells was higher than that of HCC cells after treatment with high concentrations of Dihydrotanshinone"
However, there's no statistical alalyses to back that statement! To say that, authors have to compare the results of MIHA cells with other cancer cell lines!
We only see if, for ex.1.5 micromolar drug application on Huh7 cells is significantly different than the control group of Huh7 cells. Authors performed same statistical tests for MIHA cells as well. Seeing if the drug is giving significantly different results in MIHA cells when used in different concentrations is not the case we're doing this experiment. We have to see if the results of MIHA cells in one concentration is different than the results of Hepg2 and Huh7 cells in same concentration. For ex. we should bee seeing a comparison between results of 6.25 in MIHA cells vs results of 6.25 in Hepg2 cells vs results of 6.25 in Huh7 cells.
If you only make t tests to compare a dose with the control of the same cell line you cannot scientifically say that it was safer in MIHA cells. To say that, you should present a comparison between MIHA cells and the other two cancer cells for the same dose. Authors should perform multiple comparisons tests for each concentration between 3 used cell lines and should determine, in which doses the cell viability rates were significanltly higher in MIHA cells. Only after that, authors may claim that these doses were effective for killing cancer cells and had lesser cytotoxic effects on healthy cells.
No comment.
Thank you for responding to the comments of all three reviewers. As you will see two of the reviewers are satisfied with your responses and no further action is required. However one reviewer still has some concerns which I think you should address. I have indicated this as a major revision largely because I think more detailed statistical analysis for comparing different experimental groups is required. Because it is difficult to predict the outcome of this analysis I have chosen to use major revisions at this point.
Could you please address all of the concerns raised by this reviewer and explain in a detailed rebuttal letter what changes you have made to both the analysis the conclusions and the text of the manuscript in response to this.
Depending on the outcome of these further studies it may not be necessary to send this out for further review and I may be able to make a decision quickly; however until I see the changes I cannot be certain of this. I hope you will be able to undertake this further analysis and look forward to seeing the revised version.
Authors have now satisfactorily answered all my queries and added required improvement to the manuscript. I commend authors for performing additional data analysis and adding additional data in the supplementary information. This would help the readers understand this work more intuitively. I have no more pending issues.
.
.
.
I'd like to thank authors for answering all the inquiries and responding in a positive manner and adding few more studies to increase the value of their work.
I suggest authors to review the revised parts for the english language and the used terminology.
Authors are suggested to revise their descriptions for primary antibodies in materails methods section. I proposed a template for authors as a side note in my annotated pdf file.
Authors had added a few extra studies. Although they mentioned the results of these new experiments, we cannot see them in the materials and methods section. Authors must revise their materials and methods secion by adding these studies in the relevant sub-sections.
Authors used same concentrations of the drug on a healthy cell line (MIHA) too and presented the cell viability results for these cells as well. When we checked their results, both Hepg2 and huh7 cells seem to have much less viability starting from 6.25 micromolar of drug, compared to MIHA cells. However, this was not mentioned in neither results nor discussion. Authors just mention that "MIHA cells was significantly much higher" (which is grammatically incorrect as well) in the results; and "Dihydrotanshinone I showed a certain safety in normal hepatocytes" in the discussion. First of all, I cannot see a multiple comparisons test for the results of same concentration between different cell lines to say that. Yes, we can see their bars are looking much higher in the figures, but they're both having same statistical significance range (***) for both MIHA, Hepg2 and Huh7 cells in 6.25 and 12.5 micromolar concentrations compared to control. A multiple comparison should be made for these results. Plus, these results should be given in a more detailed manner in the results section, and should be discussed by mentioning dose-dependant differences between MIHA and other cells. Secondly, all the cell lines used in cell viability assay showed significantly different results starting with 1.5625 micromolar concentration when compared to control samples. Doesn't that mean that this dose was cytotoxic for MIHA cells too? I believe this should be mentioned in the manuscript that these doses were all cytotoxic for healthy cells and cancer cells but the cytotoxic effect of the drug were much higher against cancer cells in higher concentrations, after making multiple compasrisons of course.
This question does not require an answer in the manuscript:
I wonder why authors had chosen 2 cell lines (huh7 and hepg2) with absolutely same characteristics in their study? The results are same for both cell lines, so why you used 2 different cell-lines? It was obvious that you were going to have similar results since they are both derived from same cancer type, they have same culture characteristics, they're both taken from male patients, they're both from same specie, etc. So, I did not understand the logic behind using these two cell lines at the same time. Could you explain the reason?
Dear authors,
Thank you for your improvements in the manuscript. Despite your great effort on adressing the inquiries of the reviewers, unfortunately I have further questions related with your new cell viability results. This was the reason I was asking you to test the drug on the healthy cells as well. We see that used concentrations were cytotoxic for healthy cells as well, but the cytotoxic effects on cancer cells seem greater than it is on the healthy cells. However, this has to be plainly written in the manuscript, and in order to tell that the cytotoxic effects were greater in higher doses for the cancer cells compared to MIHA cells, a multiple comparison has to be made.
Best regards.
The manuscript “Dihydrotanshinone I inhibits hepatocellular carcinoma cells
proliferation through DNA damage and EGFR pathway” by Linjun Wang and colleagues is recommended for publication after the response to the mentioned suggestion has been met.
Authors are suggested to add RMSF spectra of control (Dihydrotanshinone) I in Fig. 5 D. It is questionable to justify your results without control.
The validity of the findings is novel. Conclusions are stated well and the structure of the article is well-designed.
Some revisions are needed which are detailed and extensive, and focus a lot on the English and presentation of your paper. Please take great care to address all points listed in the revision and address all concerns with rigour.
Table 1 should be removed and incorporated into the text.
Please specify for EVERY figure how many technical and biological replicates were performed.
For the figure with immunoblots, you must upload all three replicates of each imunoblot as supporting information. You must upload as supporting information data from each individual experiment of the replicates you discuss.
[# PeerJ Staff Note: Please ensure that all review and editorial comments are addressed in a response letter and any edits or clarifications mentioned in the letter are also inserted into the revised manuscript where appropriate. #]
[# PeerJ Staff Note: It is PeerJ policy that additional references suggested during the peer-review process should only be included if the authors are in agreement that they are relevant and useful #]
The English language needs improvement at multiple locations in the article. Literature references are missing at certain places. Major locations are highlighted in the attached annotated version.
Introduction can really use some more information about Dihydrotanshinone I and what is known about it with regards to cancer. Article structure is fine and raw data is shared. However, raw data needs some additions such as replicate information, error values etc.
Research is conducted rationally. Research question is well defined, but the conclusion stating that EGFR is the target for Dihydrotanshinone I does not seem convincing enough in the current version of the article. Providing more details in the methods and result section can help alleviate the former to some extent. See my additional comments for suggestions.
Statistical details about the methods are missing. A section should be added in the methods describing the statistical approaches used. Conclusions are satisfactory.
Additional Comments:
In this study, authors assessed the proliferation of hepatoma cell lines in response to Dihydrotanshinone I introduction. Through combination of immunofluorescence, flow cytometry and bioinformatic approaches, authors surmised that Dihydrotanshinone 1 inhibits the proliferation of the cell lines under study. Additionally, authors observed that this drug induces DNA damage and apoptosis in these cells. Finally, through computational network analysis, authors concluded that EGFR could be a potential candidate for Dihydrotanshinone mode of action.
Overall, the study seems to be performed rationally with a comprehensible flow. However, based on the results presented, I am not fully convinced that EGFR is a target for Dihydrotanshinone I. Still, barring a few missing details in the methods and results, the work seems acceptable to me. Please see my additional comments below.
1. Introduction: It could be useful to the reader if authors could add a few sentences about the chemical basis of Dihydrotanshinone I selection (with suitable references). What is the molecular structure of this drug? What made authors decide to test this specific compound? Current description about the selection of Dihydrotanshinone I for this study is not convincing enough.
2. Methods:
• Construction of PPI network:
- Please mention how many potential Dihydrotanshinone I targets were identified by Pharmapper tool.
- Provide parameters for maximum neighborhood method which was employed for identifying top 10 genes. Also, show the genes which did not make it to the top 10 list. This will help reader get a better understanding of the filtering approach utilized here.
• KEGG analysis:
- Provide details about the specific modules utilized to generate plots in R (e.g., ggplots etc.). Also, DAVID tool needs a reference.
3. Results:
• Figures 1B, C: The plots talk about cell viability. How is cell viability connected to proliferation? Authors mention in lines 161-162 that Dihydrotanshinone I significantly inhibits proliferation of HCC cells. It is not clear how cell viability can be directly connected to proliferation.
• Figure 1 bar plot y-axis should go to 100% max. 120% does not make sense to show.
• Why colony formation assay results in Figure 1D, E, F show significantly stronger inhibition by Dihydrotanshinone I compared to MTT assay in Figure 1B, C? Is there a sensitivity effect that impacts the observed result by these 2 methods? If yes, please mention the associated sensitivity and specificity.
• Figure 2: Please describe what is 53BP1 foci, either in results or in methods. I do not think it is very well known.
• Figure 2A: Why does control show 53BP1 foci? How was that normalized to calculate Dihydrotanshinone effect?
• Figure 3B: Please explain how flow cytometry analysis with Annexin served as a measure of apoptosis? This method is not described in sufficient detail anywhere.
• Figure 4A: Authors should provide a table with 422 liver cancer targets and 218 drug targets used to shortlist 35 intersecting genes (label the genes based on where they are obtained from - pharmapper, DigGeNET).
• Figure 4C: After authors identified hub targets in Figure 4C, it is not clear how they ended up with EGFR as the most promising candidate. Authors mention in lines 201-204, KEGG analysis shows enrichment for EGFR resistance for 35 targets. It is not clear what this means? Since this is an important pivot point for the next part of this study, it is important to clearly show as additional figure how EGFR was shortlisted at this stage?
• Figure 5: I think this part of the analysis is performed nicely. As a control validation, authors can perform similar docking and MD simulation of Dihydrotanshinone I with 2-3 additional protein molecules from the list of their hub targets in Figure 4. Theoretically, dihydrotanshinone I should show significantly weaker binding to these proteins when compared to its binding with EGFR in Figure 5.
• Figure 5D, E: The western blot for p-EGFR does not look convincing enough. A better blot clearly showing inhibition of EGFR upon Dihydrotanshinone I incorporation should be substituted here. Also, authors could quantify the blot intensity and show that next to the blot as bar plots (control + 2 Dihydrotanshinone I concentrations).
Minor:
- All the raw data files should contain information about the replicates and the values for each data point from the replicate experiments. The errors should also be added to the raw data files. Finally, please mention how many replicates were utilized for each experiment in the method section.
- Add another section about the statistical analysis in the methods. Which tests were performed to obtain p-values? How were the error bars obtain for the bar plots?
1- A language editing is suggested.
2- Authors had presented some statistical differences for their analyses, yet we can not see the used statistical tests. Please create a “statistics” section within the materials and methods by mentioning sample sizes, used statistical tests and the used significance format.
3- Please indicate the p values for statistical references in the results section for the presented differences.
1- Why do authors decided to use 2 different human liver cancer lines with similar characteristics, same gender and pathology? Also, please mention that in the discussion section.
2- Is it possible for authors to test the drug with non-cancer cell lines like liver ephitelial cell lines or fibroblast cell lines with same concentrations? By doing this authors can prove that the drug is non-toxic for the healthy cells and claim the drug as anti-tumorigenic.
3- Is it possible for authors to make any other quantitative analysis in order to determine effected and/or involved pathways for the drug's action like qPCR, flow cytometry, etc. for markers like caspase-3, Bcl/Bax, p53, etc to gain a better grasp of the drug's apoptotic action and the involved pathways?
4- Please mention the calculation of OD values for MTT results an place a citation for the used methodology.
5- Please indicate that if you rinsed the excessive stain after the crystal violet staining and please place a citation for the quantification method.
6- Please check the catalog number for anti-53BP1 antibody. I was unable to find the product with the given catalog number.
7- Please indicate the primary antibodies used in WB and share their catalog numbers with the used dilutions. And, mention the information for secondary antibody used in WB as well
1- There are several studies on Dihydrotanshinone, demonstrating its angiogenesis inhibiting effects, anti-cancer effects etc. pls use these previous studies on your discussion. We should see what drove you to use this agent for this study.
2- There are numerous studies both in vivo and in vitro, evaluating same drug in iver cancer, using same cell lines and there are studies which made further analyses to underline the molecular system beneath the effect by addressing which pathways are involved. What’s the original side of this manuscript? Is there a different approach in this study? Did you see any kind of different results? What is new provided by you for the drug or its effects? Please, indicate similarities and differences of your results in the discussion section and tell the readers what’s unique about the study. There is a lot of results can be compared to other studies in the manuscript. Please be sure to discuss your results with the previous research in the field in depth and specifically, please indicate what makes your study original since there are lots of research with the same drug on same type of cells with very similar methodologies. Here are a few examples that I had found in a short notice, I believe authors could find more studies very similar to their work and build a much better discussion:
https://www.sciencedirect.com/science/article/abs/pii/S0168365922003285
https://www.sciencedirect.com/science/article/abs/pii/S0024320513003949
https://www.sciencedirect.com/science/article/abs/pii/S0944711315002548
The manuscript “Dihydrotanshinone I inhibits hepatocellular carcinoma cells
proliferation through DNA damage and EGFR pathway” by Linjun Wang and colleagues proposes that Dihydrotanshinone I effectively inhibited the proliferation of Huh-7 and HepG2 hepatoma cells and EGFR might be potential therapeutic targets of Dihydrotanshinone I in HCC. The results suggest that Dihydrotanshinone I is a novel candidate therapeutic agent for the treatment of Hepatocellular carcinoma.
Huh-7 and HepG2 hepatoma cells poliferation was evaluated using MTT and clone formation assays. Immunofluorescence (IF) experiment and
flow cytometry analysis detect DNA damage and cell apoptosis. Computational analysis shows possible therapeutic targets and pathway using Dihydrotanshinone I.
In general, the finding is potentially interesting and important in the context of DNA damage and cancer drug targeting strategies. However, the manuscript can be considerably improved. I can recommend it for publishing with a few questions outlined.
1. Author in the manuscript have investigated 2.5 and 5 uM concentration of Dihydrotanshinone I for colony formation assay rather then choosing concentrations that match with MTT assay. Why the concentration of the drug is different?
2. Authors are suggested to check the off target effects of Dihydrotanshinone I.
3. MD simulation results not clearly explained. “The MD simulation revealed that the root means square distance (RMSD) of the protein backbone of EGFR, was converged after 4ns of simulation and it was stable for the complete simulation run (Fig. 5C)’ in this text it is unclear whether these RMSD results are in absence or in presence of Dihydrotanshinone I. Also if these results are in presence of Dihydrotanshinone I, what author want to say from this sentence? Generally, the RMSD analysis gives an idea about the structural fluctuation of protein with time and in order to find out the effect of ligand binding on protein, RMSD analysis is performed in absence and presence of ligand. In this study authors did not performed MD simulation in absence of Dihydrotanshinone I. Without comparing the MD simulation, results of EGFR in presence of Dihydrotanshinone I with control (in absence of Dihydrotanshinone I). How authors justify their results ?
4. Authors are suggested to calculate RMSF to determine the specific binding region of EGFR involved in binding with Dihydrotanshinone I.
5. In figure 2A authors show more foci formed with treatment of drug compared to the WT, but the average representation in plot 2C is low at 2.5uM. please check the formation of foci represented.
The validity of the findings is novel. Conclusions are stated well and the structure of the article is well designed. However few question posted are essential for clarity of concepts for readers.
1. Authors are suggested to correct the grammatical error.
2. Fig. 2 A, legends huh 7 is missing, authors are suggested to label it.
3. Correct the repeated sentence in line 132-133.
4. More recent literature related to effect of Dihydrotanshinone I on Hepatocellular carcinoma should be added in discussion section (eg. https://doi.org/10.3389/fphar.2021.654986).
5. Correct the spelling of pharmapper to “PharmMapper” in line 115.
6. Authors are suggested to increase the resolution of fig 3 B.
7. Authors are suggested to correct the format of references (journal abbreviations and page no.
All text and materials provided via this peer-review history page are made available under a Creative Commons Attribution License, which permits unrestricted use, distribution, and reproduction in any medium, provided the original author and source are credited.