Molecular Characterization of PARP Inhibitor Response Reveals Co-Targeting Strategies in Advanced Prostate Cancer

Round 1

Reviewer 1 Report

Comments and Suggestions for Authors

Major Concerns

1. The study relies heavily on a single cell line (C4-2B) for RNA-seq and most functional assays. Although the AbiR derivative is used for validation, it originates from the same parental lineage. In addition, C4-2B cells harbor specific homologous recombination repair (HRR) mutations, meaning that the findings reflect a single genetic background. To strengthen the study, the authors should either (a) validate key observations in at least one additional, genetically distinct CRPC cell line (e.g., 22Rv1, PC3, or DU145), or (b) clearly limit their conclusions to the C4-2B/LNCaP lineage and avoid broader generalizations to advanced prostate cancer.
2. PARPi activity is tightly linked to HRR deficiency, the exact mutations present, including affected genes and zygosity, should be clearly specified in Section 2.1 or in a supplementary table. Alternatively, the authors could experimentally confirm HRR status using an HDR/NHEJ reporter assay. This information is critical for interpreting the mechanistic basis of ATM inhibitor (ATMi) synergy.
3. Another major issue is the presentation of western blot data. All blots are shown as representative images without any densitometric quantification. As a result, statements such as “olaparib induced γH2AX… is enhanced by combination treatment” (lines 384–385) or “western blots confirm increased expression of SLUG and VIM” (lines 418–420) remain qualitative. At a minimum, densitometric analyses normalized to loading controls should be provided, along with statistical evaluation from independent experiments.
4. The RNA-seq analysis is performed exclusively in C4-2B cells, yet validation experiments in AbiR cells (e.g., western blots and viability assays) are interpreted as supporting the transcriptomic findings. This extrapolation is not fully justified, as AbiR cells are expected to have distinct transcriptional adaptations due to chronic abiraterone exposure. The authors should either include RNA-seq data for the AbiR model or clearly state that transcriptomic conclusions are specific to C4-2B, with AbiR results serving only as functional validation.
5. Regarding experimental design, RNA-seq was conducted with triplicate samples (n=3), which is the minimum acceptable standard. The authors should clarify that these represent true biological replicates (i.e., independent cultures from separate passages) rather than technical replicates from a single preparation.
6. In Figure 5E, SLUG knockdown combined with olaparib reduces cell viability. However, the conclusion that “PARPi-induced EMT may provide tolerance for cells to persist during treatment” appears overstated. The current data do not distinguish whether SLUG knockdown (a) inhibits EMT and thereby blocks adaptation, or (b) sensitizes cells through an EMT-independent mechanism. A rescue experiment restoring SLUG expression would be required to support a causal EMT-based interpretation.
7. There is also inconsistency in how viability is measured. Figure 4C uses a CCK-8 assay, whereas Figure 5E uses a Coulter counter. Using different platforms without cross-validation introduces potential bias. The authors should justify this choice and demonstrate that the two methods yield comparable results under equivalent conditions or include at least one experiment assessed by both approaches.
8. The tumoroid experiment (single patient, technical triplicates) is appropriately placed in the Supplementary section. However, it is cited in the Discussion (lines 514–516) as supporting the ATMi + PARPi strategy. Given that this represents only one biological sample without statistical power, it should not be presented as substantive evidence. The authors should either include additional patient samples or clearly describe this result as exploratory and hypothesis-generating.

 

 

Minor Comments

1. Section numbering skips from 3.2 to 3.4; Section 3.3 is missing and should be corrected.
2. The fatty acid metabolism analysis (lines 451–458) relies solely on RNA-seq data. Key enzymes involved in FAO and FAS should be validated at the protein or mRNA level prior to interpreting inhibitor studies.
3. For Figure 4D, the PI-based cell cycle protocol does not specify how long fixed cells were stored at 4°C. Extended storage (>2 weeks) can affect data quality. This should be clarified. Additionally, the sub-G1 (apoptotic) population is not reported despite evidence of apoptosis (c-PARP); this fraction should be quantified.
4. The olaparib concentrations used (1 µM and 5 µM) should be better justified. As 1 µM may be subtherapeutic, the authors should provide relevant pharmacokinetic context.
5. The proposed mechanism of ATMi-induced gap formation exploited by PARPi, discussed in lines 508–521, but not directly tested in this study. The language should be softened to reflect that this is a hypothesis rather than a demonstrated mechanism.
6. While C4-2B cells were authenticated using STR profiling, no such information is provided for AbiR cells. The authors should clarify whether independent authentication was performed.
7. RNA-seq methods should include RNA integrity number (RIN) thresholds, and values for all samples should be provided in a supplementary table.
8. The DEG cutoff of log2FC > 0.5 is relatively permissive. The authors should justify this choice and consider reporting DEG counts at a more stringent cutoff with log2FC > 1 as a sensitivity analysis.

Author Response

We thank Reviewer 1 for their thorough and critical assessment of our work. Please see the attached PDF with our detailed response to all comments. We are confident the study has substantially improved based on your recommendations, thank you.

Author Response File: Author Response.pdf

Reviewer 2 Report

Comments and Suggestions for Authors

This manuscript by Gonzalez BC et al., describes clearly and thoroughly molecular characterization of PARP inhibitor response using in vitro prostate cancer models and identified significant mechanisms of resistance. The investigators identified ATM inhibition to enhance Poly (ADP-ribose) polymerase (PARP) inhibitor (PARPi) utility and showed that targeting PARPi induced EMT and metabolic alterations may be strategies to combat adaptation. The work should capture the interest of the wide prostate cancer audience, and it is timely. The laboratory work seems well done and the conclusions appropriate. The study would have been enhanced by studies using relevant in vivo models, which was appropriately noted by the investigators as the major limitation of the work.

Author Response

We thank Reviewer 2 for their assessment of our work. Please see the attached PDF with our response.

Author Response File: Author Response.pdf

Reviewer 3 Report

Comments and Suggestions for Authors

PARP inhibition has shown significant clinical efficacy as a treatment strategy in homologous recombination deficient cancer cells by driving synergistic disruption of DNA repair.  Recently, PARPi monotherapy was approved for metastatic castration resistant prostate cancer, however, recurrence is common and treatment can yield only minor improvements in response.  To overcome these challenges, the authors sought to explore the mode of action of PARPi in prostate cancer to identify potential novel combinatorial targets to enhance efficacy.  Using transcriptomics, the authors identify early DNA damage/p53 dependent effects that synergizes with ATM inhibition, consistent with the classical hypothesis of PARPi cooperating with DNA damage and repair pathways.  More interestingly, the authors identify a potential long-term phenotype related to EMT that may provide a means of escape for cancer cells and potentially fatty-acid metabolism as a metabolic vulnerability. These findings are of significant interest in potential therapeutic treatments of cancers and provide novel insight into the modes of action involved in PARPi treatment. In most instances, authors provide strong evidence of mechanisms through multiple orthogonal approaches, however, there are some areas where we believe additional experiments are needed to fully validate some of the conclusions.

Major comments

1. While the authors highlighted the presence of cleaved PARP as a measure of cell death, it would be beneficial to have a secondary measure of cell death. Even a simple sub G1 analysis of the flow cytometry would strengthen this finding without necessarily requiring additional experiments to be performed.
2. Repeating some of the key experiments (synergy with ATM inhibition, EMT induction, and fatty acid metabolism synergy) in a p53 mutant or null cell line would significantly strengthen the findings as metastatic, castration resistant prostate cancer shows significant levels of p53 disruption (distinct from p53 wildtype LNCaP cells).
3. In Figure 5C, it appears that Slug and Vimentin were blotted from a parallel run of samples (potentially independent of the tubulin loading control). Authors should provide additional clarity on some of the blots given the cutting of blots and composites not showing the fully assembled blot.

 

Minor Comments

1.   In Figure 1B, authors show morphological changes with long-term PARPi.  This could be strengthened with a more quantitative measure of morphology.  Even as simple as a change in FSC/SSC by flow cytometry.  Additional, while it’s assumed the FOV is an identical size across images the authors could clarify this or include scale bars in all panels.
2. Rationale for selecting a relative low threshold cutoff for DEG analysis via RNA-seq would be beneficial. It’s unclear why a |log2 FC|>0.5 was selected rather then a more standard >1. Are any of the genes that fall within this range predicted or validated to be biologically relevant for the response?
3. Additional validation of select RNA-seq results by RT-PCR would also support the authors findings, though they do show increased expression of p21 (CDKN1A) by western blot. This may be most relevant in Figure 5 as authors simply re-use read counts for gene expression of EMT associated genes.
4. The composite raw western blots do not appear to match the figure blots, which appear to have a much lighter background. We’d suggest that authors simply crop the raw blots for the figures to avoid this issue as the overall bands appear the same.

Author Response

We thank Reviewer 3 for their assessment of our work. Please see the attached PDF with our responses.

Author Response File: Author Response.pdf

Round 2

Reviewer 1 Report

Comments and Suggestions for Authors

Thank you for addressing the comments and concerns satisfactorily.