Pharmacological CDK4/6 inhibition reveals a p53‐dependent senescent state with restricted toxicity

Abstract Cellular senescence is a state of stable growth arrest and a desired outcome of tumor suppressive interventions. Treatment with many anti‐cancer drugs can cause premature senescence of non‐malignant cells. These therapy‐induced senescent cells can have pro‐tumorigenic and pro‐disease functions via activation of an inflammatory secretory phenotype (SASP). Inhibitors of cyclin‐dependent kinases 4/6 (CDK4/6i) have recently proven to restrain tumor growth by activating a senescence‐like program in cancer cells. However, the physiological consequence of exposing the whole organism to pharmacological CDK4/6i remains poorly characterized. Here, we show that exposure to CDK4/6i induces non‐malignant cells to enter a premature state of senescence dependent on p53. We observe in mice and breast cancer patients that the CDK4/6i‐induced senescent program activates only a partial SASP enriched in p53 targets but lacking pro‐inflammatory and NF‐κB‐driven components. We find that CDK4/6i‐induced senescent cells do not acquire pro‐tumorigenic and detrimental properties but retain the ability to promote paracrine senescence and undergo clearance. Our results demonstrate that SASP composition is exquisitely stress‐dependent and a predictor for the biological functions of different senescence subsets.


5th Aug 2021 1st Editorial Decision
Thank you again for your patience during our arbitrating review of your transferred manuscript on p53-dependent senescence programs upon CDK4/6 inhibition. I have now heard back from two experts, who looked into the study as well as into the transferred previous referee reports and your response to them. Given their overall interest and generally supportive comments, we would be happy to pursue this work further for EMBO Journal publication, pending revision along the lines suggested in your tentative response letter and also taking the additional thoughts of our arbitrating referees on board.
To recapitulate what the key points would be: Since it is our policy to consider only a single round of major revision, it will be important to comprehensively answer to all the points raised at the time of resubmission; I would be happy to discuss the time line for the revision work with me once you had the time to consider this letter. I can also remind of our 'scooping protection', which will allow you to finish dedicated revision experiments without the danger of losing novelty upon publication of related/competing work here or elsewhere.
Further information on preparing and uploading a revised manuscript can be found below and in our Guide to Authors. Thank you again for the opportunity to consider this work for The EMBO Journal, and I look forward to your revision.
2. Some of the points raised by Rev 2 are valid and should be addressed in the revision. In addition to what the authors suggested to do, which is mostly fine, I'd suggest a few simple experiments that would address the concern of this reviewer: For point 1 -I suggest doing a concentration curve from 200 nM to 1uM and check which dose induces irreversible arrest following 8 days of treatment.
For point 6 -the authors already suggested that they will do the experiment. It is important to look at cells from different tissues in this experiment to see the real picture. This experiment will prove (or not) the relevance of the finding in vivo. I suggest authors focus on this and provide comprehensive information on this point.
For the other points raised by the reviewer, I suggest the authors downtone some of their conclusions instead of arguing with the reviewer.
Arbitrating Referee #2: CDK4/6i (or p16)-induced senescence is a unique type, lacking a typical inflammatory sasp and persistent DNA damage response (two major effectors in senescence). In this study, Wang and colleagues identify and characterise p53-dependent sasp in such senescence in (non-cancer cells). this seems to be a subset of typical sasp. rather unexpectedly, these 'coldsenescence' still appears to get cleared in vivo.
The authors have addressed most of the reviewers' questions. one outstanding one is how CDK4/6i activates p53 without DDR. This is certainly an interesting but challenging question. The authors appear more concerned with the functional relevance, which is also very important. General and tumorigenic side effects of CDK4/6i-induced senescence appear to be lower than genotoxic chemotherapies, reinforcing the potential advantage of this therapeutic strategy in cancer. In this context, I would be very curious how CDK4/6i-senescent cells are cleared. Is this immune-mediated, or   AUTHORS: We agree that certain cancer cell lines seem to respond to lower concentrations of CDK4/6 inhibitors, but also that in many studies a significant cytostatic effect is reached only at high concentrations (2-5 uM). It is important to note that the mean concentration of the active metabolites of abemaciclib achieved in patient plasma is approximately 1 uM (Ref: https://www.cell.com/cancer-cell/fulltext/S1535-6108(17)30509-3). To add to the selection of 1 uM as our working concentration, we have studied a titration of abemaciclib on irreversible growth arrest. We treated BJ cells with 250nM, 500nM or 1uM abemaciclib for 8 times 24 hours, and then replated the cells for colony formation assays. As shown below, partial effects on proliferation were observed at 250 and 500 nM, while strong effects were achieved at 1uM. These data are now included in Fig   It is insufficient in a molecularly, mechanism-oriented, manuscript to report it without providing an understanding of it. Perhaps you change the nature of the p53 response, but again the data is somewhat deficient for this. One example, is in your figure 1 you score p53 binding to target loci, but you do not compare this binding to that of a clearly dependent DNA damage p53 response here, but when reading other outputs, such as transcription in figure 3 you do that control. Such "cherry-picking" of data does not make for a persuasive argument that p53 is even involved.

AUTHORS:
We have now performed analysis of mitochondrial ROS, and observed upregulation in cells treated with abemaciclib ( Fig EV4A). However, this is not sufficient to induce a significant DDR, thus the absence of NFkB signaling. These data were already shown in the original submission as Fig 3A-B. In addition to the ROS data, we have also measured the level of nuclear p53, showing an increase in cells treated with abemaciclib ( Figure EV1P).
In order to compare p53 binding to target loci in DNA damage models, we have performed a ChIP experiment including doxorubicin-treated cells. As we show in Figure, the increase in p53-binding activity is similar between abemaciclib and doxorubicin treatment.

orig. ref 2/pt 6. Rather than look indirectly for cytokines in serum, why don't you treat mice with cdk4/6 inhibitors and look at the stromal cells for evidence of this event, perhaps the proliferating epithelial cells in the gut, or the mesenchymal cells during wound repair.
Maybe you could isolate them and use single cell seq to define the phenotype and its relation to a p53-dependent non-inflammatory phenotype in cultured cells. Alternatively, you might come up with a way to show that a cell has "stable arrest induced by cdk4/6 inhibitor" by creative use of fluorescent indicators that monitor the expression programs and DNA replication after drug withdrawal.
AUTHORS: In order to address SASP expression directly in vivo, we treated the p16-3MR mice with vehicle, doxorubicin or abemaciclib and sorted the RFP+ (p16+) cells from the kidney cortex. RNA was isolated and qPCR targeting pro-inflammatory SASP was performed. Data indicate a high expression of pro-inflammatory SASP factors in cells isolated from doxorubicin-treated but not from abemaciclib-treated mice. These data re now in Fig 3K and EV4E. Thank you again for submitting your revised manuscript for our consideration, and apologies for the delayed re-review, during which both arbitrating referees have now assessed the data added subsequent to your earlier tentative response to the previous reviews, as well as your answers to the points they had emphasized. As you will see from the comments copied below, arbitrator 1 was not satisfied with all revisions, necessitating careful further consultations both within our team and with arbitrator 2.
The first issue raised by arbitrator 1 concerns the inhibitor concentration, which the reviewer considers too high to be clinically significant. Arbitrator 2 has now taken a detailed second look at this (see additional comments below), and while appreciating the reason for the concern, feels that the new data would still support senescence induction in a physiological range.
The second criticism of arbitrator 1 concerns the new senescent cell isolation experiments (Fig 3K and EV4E), as they have only been done from kidney but not other tissues. I appreciate that the initial revision proposal had not clearly specified which tissues exactly you were planning to analyze, and the referees had not explicitly excluded kidney as a relevant tissue to use either. Nevertheless, given that also arbitrator 2 agrees that the study would be strengthened by inclusion of data from additional tissues, I would strongly encourage you to add any such data that you may already have.
Finally, I appreciate your evidence for PASP being directly due to p53 transcriptional activity, and p53 activation not being due to DNA damage or ROS. But I still miss any thoughts on what else might then be mediating p53 activation upstream of the PASP? I.e., an (even if speculative) answer to original referee 2's question "How do you get a p53 response?" => even if this may already be the topic of follow-up work, please do add some concrete thoughts on how CDK4/6 inhibition might cause p53 activation (as asked in my previous decision letter) to the discussion.
In conclusion, we decided that pending adequate re-revision, we would consider the study further for eventual publication in The EMBO Journal. In addition to paying attention to the above points, this final version should also incorporate the following editorial points: I acknowledge that the authors perform some of the suggested experiments in regard to points 1 and 6 of rev2 that I asked to address in my previous review. Below is the analysis of the results I see. Regarding point 1: A concern is that the concentration used (1 uM) is way above what happens in patients and therefore observed results might not be relevant to the patients. The authors perform the experiment with lower concentrations of the drug and the results show that these concentrations do not induce senescence as the arrest is reversible. The authors originally cited a paper in Cancer Cell and suggested that this paper shows that 1uM is the concentration in patients. I've looked at this paper and surprisingly found that there were no measurements of plasma concentration of the drug in patients in this paper. The citation of this paper was, apparently, misleading. The studies with patients (https://cancerdiscovery.aacrjournals.org/content/6/7/740 ; https://clincancerres.aacrjournals.org/content/26/20/5310 ) clearly show that the concentration in the plasma and other internal body fluids is indeed 100nm and can reach up to 500nM only at the maximum tolerated dose, which is rarely used. The new results presented by the authors show that even at 500nM the cells resume proliferation after removal of the drugmeans they are not senescent and thus strikingly different from the cells treated with 1uM. Unfortunately, all the above shows that the concern of the reviewer was valid and the concentration used in the study is not clinically relevant. Therefore, all the conclusions regarding relevance to the patients do not stand.

Regarding point 6:
The question was if there is an increase in senescent cells with the described properties in different tissues following the drug treatment. The authors continue to focus on one tissue -the kidney. The kidney is an important metabolic organ and is responsible for the removal of all the metabolites of the drug and partially the drug itself. Therefore, concentrating at the kidney provides only a limited picture. The authors themselves suggested that they will isolate cells from different tissues. Apparently, the result of such experiments is not shown and thus raises the concern of the appearance of the relevant cells in tissues even higher.
Arbitrating Referee #2: The authors have added new data addressing the remaining issues.
ADDITIONAL CROSS-COMMENTS on Arbitrator 1: The first point seems to come down to the question about 'active metabolites of abemaciclib' vs 'parent abemaciclib'.
Gong et al (the paper cited by the authors) describe that Abemaciclib mean steady-state plasma concentrations range from 0.4 to 0.6 μM. This is based on Patnaik et al., 2016 (cited by reviewer 1). I have to say it was not easy to find the exact numbers in this paper (at least to me). But let's say it is correct, this seems to represent the 'abemaciclib' parent drug, and Gong et al doubled the concentration to reflect the 'abemaciclib' parent drug + active metabolites, leading to 1uM as an 'upper threshold' for their in vitro (cell lines) screens. Thus, based on this argument, 1uM in vitro is high but may not be too far from the physiological level. However, it is true that the other paper, which was cited by reviewer 1, estimates plasma concentration of 'active metabolites' a bit lower. It is hard to directly compare between total active metabolites/parent drug in the plasma and parent drug in culture media.
Having said this, their new colony formation assay data using lower doses show substantial differences, thus lower doses do induce senescence (although not 100%). Additionally, the authors might argue that they do find senescence in mice using the tolerable concentration (50mg/kg). I find the second point (they only used kidneys) is more problematic. Sorry, I didn't pick this up. But I would think they must have data from other issues already. It should be easy for them to add those data.
The first issue raised by arbitrator 1 concerns the inhibitor concentration, which the reviewer considers too high to be clinically significant. Arbitrator 2 has now taken a detailed second look at this (see additional comments below), and while appreciating the reason for the concern, feels that the new data would still support senescence induction in a physiological range.
AUTHORS: we agree that the debate about abemaciclib concentration remains open and important. However, as we have mentioned in the manuscript, we have tried to mimic a clinically-relevant situation, even if the concentration used for each dosage is in the high-end of the spectrum. On this point, we would also like to add that human patients are treated for much longer periods of time than 7 days (in the clinical trial MonarchE patients were treated up to 2 yearssee https://ascopubs.org/doi/10.1200/JCO.20.02514).
The second criticism of arbitrator 1 concerns the new senescent cell isolation experiments (Fig 3K and EV4E), as they have only been done from kidney but not other tissues. I appreciate that the initial revision proposal had not clearly specified which tissues exactly you were planning to analyze, and the referees had not explicitly excluded kidney as a relevant tissue to use either. Nevertheless, given that also arbitrator 2 agrees that the study would be strengthened by inclusion of data from additional tissues, I would strongly encourage you to add any such data that you may already have.
AUTHORS: during the first round of revision we did not indeed mention any particular tissue. The sorting of RFP+ (p16+) cells from tissues is technically challenging and we can process only one tissue/mouse. The decision to sort from kidneys is due to our previous studies (Demaria M et al, Cancer Discovery, 2017; Van Vliet et al, Mol Cell, 2021) which indicated the kidney being a tissue accumulating premature senescence and SASP in response to exposure to genotoxic chemotherapy. Analysis of another tissue would require a new cohort of mice requiring additional resources and raising several ethical concerns. Thus, it is not possible for us at this stage to add more data to this point.
Finally, I appreciate your evidence for PASP being directly due to p53 transcriptional activity, and p53 activation not being due to DNA damage or ROS. But I still miss any thoughts on what else might then be mediating p53 activation upstream of the PASP? I.e., an (even if speculative) answer to original referee 2's question "How do you get a p53 response?" => even if this may already be the topic of follow-up work, please do add some concrete thoughts on how CDK4/6 inhibition might cause p53 activation (as asked in my previous decision letter) to the discussion. AUTHORS: we have now added this point to the discussion part. In particular, we are suggesting that future studies should aim at understanding how p53 is activated, but also at the role of epigenetics and accessibility to p53 target genes. Do the data meet the assumptions of the tests (e.g., normal distribution)? Describe any methods used to assess it.
Is there an estimate of variation within each group of data?
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We estimate the sample size for the animal studies based on former studies and publications.
Exclusion criteria was pre-established for the animals studies (i.e. sick animals or animals with significant weight difference will be excluded). But in this study, no animal was excluded when the experiments were done.
Randomization was applied in most of the animal experiments (drug treatments for healthspan and SASP analysis). For tumor-bearing experiments, the mice were divided into different groups based on the tumor sizes to make a even distribution, before the treatments started.

Manuscript Number: EMBOJ-2021-108946
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Randomization was used in this study.
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